ELUSIVE CURES

Elusive Cures WHY NEUROSCIENCE HASN’T SOLVED BRAIN DISORDERS—AND HOW WE CAN CHANGE THAT

Nicole C. Rust

PRINCETON UNIVERSITY PRESS

PRINCETON & OXFORD

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Library of Congress Cataloging-in-Publication Data

Names: Rust, Nicole C, 1975– author.

Title: Elusive cures : why neuroscience hasn't solved brain disorders—and how we can change that / Nicole C Rust.

Other titles: Why neuroscience hasn't solved brain disorders—and how we can change that

Description: Princeton : Princeton University Press, [2025] | Includes bibliographical references and index.

Identifiers: LCCN 2024040039 (print) | LCCN 2024040040 (ebook) | ISBN 9780691243054 (hardback) | ISBN 9780691243078 (ebook)

Subjects: LCSH: Brain—Diseases. | Neurology—Research. | BISAC: SCIENCE / Life Sciences / Neuroscience | HEALTH & FITNESS / Diseases & Conditions / Nervous System (incl. Brain)

Classification: LCC RC346 .R87 2025 (print) | LCC RC346 (ebook) | DDC 616.8—dc23/eng/20250115

LC record available at https://lccn.loc.gov/2024040039

LC ebook record available at https://lccn.loc.gov/2024040040

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For Klara and Hendrik

AUTHOR’S NOTE

I was inspired to write this book to help individuals who are afflicted with some type of brain or mental dysfunction, or have a loved one who is. I am among you, and I am empathetic. I acknowledge that there are complexities around whether and when we should consider some conditions as “dysfunction” as opposed to a type of neurodiversity that society has wrongly become intolerant to—cases of autism, attention deficit hyperactivity disorder, and depression are all examples. That said, for each of these conditions, a subset of diagnosed individuals suffer in ways that can benefit from treatment. For those individuals, when our existing treatments fall short, we need better ways to help them. With this empathetic spirit, I use the terms “dysfunction” and “disorder” to refer to the conditions of individuals who need better solutions than the ones we can offer them today.

I approached this book with some trepidation about the voice with which to write it. Scientific progress does not follow from individual authors offering up their independent genius ideas. Instead, progress follows from communities that work and move somewhat independently but also together, like a flock. In brain research today, that community includes tens of thousands of individuals, all contributing. Among them, no individual researcher holds the special key to unlocking insights into what type of thing the brain is, how it breaks, and what to do about it when it does. The questions we need to answer about the brain are vast, and they are much too big for any one of us to take on; it is up to a community (not a few individuals) to figure these things out.

In that light, as this book’s author, I regard my role first and foremost as a curator. My job here is to sift through an immense amount of material about the brain and mind to extract what’s most valuable (leaving behind what’s not) and, in doing so, enhance what brain researchers like to call the “SNR” (signal-to-noise ratio). My task is to channel the ethos of this era to spell out the emerging intellectual framework driving brain research forward. I regard this as an extremely important task and take it very seriously. As a brain researcher with decades of experience in many flavors of it—from molecular to systems, from experimental to computational, from the nuts-and-bolts foundational work to the early stages of exploring a new therapy—I believe I’m reasonably well equipped for the role (or at least as well equipped as anyone in a community that fosters specialists). But as you read, please know that these aren’t my genius ideas; they are the curated genius of a large community of which I am but one member.

I’ve agonized a lot about how to best convey these ideas in a broadly accessible and compelling way, weighing the factors that scientists tend to prioritize (like attribution) versus (yes, I’ll say it) the pragmatic tedium of reading traditional scientific prose. I’ve concluded that everything has its place, and when both scientists and nonscientists alike take the time to read a nonfiction book, they want to focus on ideas. This is why, for the most part, I will describe the scientists involved generically as the researchers. In some cases, the researchers are part of the narrative; in those cases, I name them. But when the focus is on the ideas themselves, I do not. Please know that when I refer to the researchers, I refer to the devoted and passionate work of real individuals. I apologize to those individuals when I cannot fully acknowledge their contributions in this context (I hope they understand). Anyone who would like to learn more about these terrific researchers (and I encourage you to), please follow up on the notes at the end of the book.

CHAPTER 1 The Grand Plan

No one had ever suggested it could be hereditary, it was just seen as a terrible coincidence. But on my little A5-size Basildon Bond paper, I drew the family tree. There were my grandma and grandad, both of whom I suspected had Alzheimer’s, and in the next line I put their 10 children and marked the three who had been diagnosed. In the letter I said we’d love to take part in any research. I wasn’t necessarily thinking they would find a missing link, but that if they could give us any information, any idea about how to treat it, it would be worth it.

CAROL JENNINGS, 1999

The first signs of Alzheimer’s include forgetting little things here and there—symptoms that are difficult to distinguish from the consequences of fatigue, the hormonal changes that accompany menopause, and normal age-related cognitive decline. As the disease progresses, it causes more severe memory problems, and individuals increasingly become unable to do everyday tasks. Alzheimer’s is a heartbreaking, slowly progressing neurodegenerative disease that typically escalates over ~4–8 years (but sometimes as many as 20) until complications from it (like choking or pneumonia) lead to death. It is responsible for approximately 70% of all cases of dementia and afflicts 10% of individuals 65 and older. Worldwide, more than 35 million individuals are currently suffering from it. The disease inevitably brings tragedy to those who suffer and to their families. But the biggest tragedy of all is that we do not have any highly effective cures or treatments.

Alzheimer’s is not a new disorder—we’ve known about it for more than a century. Dr. Alois Alzheimer was the first to report clumps in the brain of one of his dementia patients in 1906, following her death. He described the clumps as a “deposition of a peculiar substance in the cortex.” We now know these clumps as the plaques typically associated with Alzheimer’s.

In the 1970s and 1980s, the causes of Alzheimer’s were not thought to be genetic. Viruses, aluminum exposure, and other environmental toxins were all suspected. However, when Carol Jennings’s father and two of his siblings were all diagnosed with the disease at the atypically young ages of 54–59, Carol suspected her family carried a genetic form of the disorder. She began writing letters to Alzheimer’s researchers asking whether her family could contribute to some type of study. She wrote one of those letters to Dr. John Hardy at St. Mary’s Hospital in London in response to an ad he had placed in the Alzheimer’s Society Newsletter. In Carol’s letter, she described her family tree, highlighting the individuals with Alzheimer’s and the inheritance pattern. That letter triggered a cascade of events that changed the course of Alzheimer’s research for over 30 years.

The genetics of Alzheimer’s are complex, involving many genes. Most of these genes, if inherited, increase the risk that an individual will acquire the disease but do not ensure it. But if an individual inherits one of a few rare genes (accounting for <1% of all cases of the disease), there is an exceedingly high probability that they will develop Alzheimer’s. Likewise, if an individual’s parent is afflicted but does not pass on the gene to them, their own offspring are not at increased risk. Carol’s family carries that type of autosomal dominant Alzheimer’s gene. Because her father was afflicted, Carol herself had a 50% chance of developing the disease, and if she was a carrier, so did her two children.

Upon receiving Carol’s letter, Hardy’s team responded, eager to learn more about her family. Based on previous work, they suspected that the family’s mutation would be somewhere on the long arm of chromosome 21, but it was unclear which gene would be involved. Carol rallied her family to contribute blood samples and participate in clinical tests.

With the genetic material from Carol’s family, Hardy’s team proceeded to do the laborious work of finding the mutation. It took 4 years. The culprit turned out to be a mutation in a single DNA base pair in a gene called APP—a “C” changed into a “T.” That mutation led to a swap of a single amino acid (an isoleucine instead of a valine) in the protein amyloid-beta. The researchers confirmed the same mutation in a second afflicted family.

Many lauded the discovery as a “breakthrough.” The New York Times reported, “Gene mutation that causes Alzheimer’s is found.” The junior researcher who made the discovery, Alison Goate, remembers thinking, “Sometimes in science, you generate the data gradually. This was like, boom, a eureka moment.” Hardy recalls the discovery similarly, “I felt we’d cracked Alzheimer’s. I felt we’d done something that had made a real difference.” One researcher speculated, “I would bet you a great deal of money that if you could prevent the accumulation of amyloid, you could stop dementia.”

With this knowledge in hand, Hardy and other researchers went on to develop the “amyloid hypothesis.” They already knew that the plaques Alois Alzheimer first identified were composed of amyloid-beta. The fact that a mutation in the gene for this protein caused Alzheimer’s in Carol’s family and others suggested that the plaques might be a cause (not a consequence) of the disorder. The gist of the amyloid hypothesis is that mutations in APP (and other factors) lead to the accumulation of amyloid into plaques, and because these are toxic, they trigger a cascade of events that leads to neurodegeneration; in turn, this leads to cognitive decline. This hypothesis quickly became the dominant focus of Alzheimer’s research.

Launching from it, researchers set out to discover how to clear amyloid plaques from the brain. After a number of false starts, brain researchers successfully produced a drug to do just that, and the FDA approved the first amyloid-clearing drug, aducanumab, in 2021 and then a second, similar drug, lecanemab, in 2023. These drugs are both antibodies that bind to amyloid-beta, triggering the body to clear plaques from the brain. They both do that job quite well, and that in and of itself is remarkable.

Up to this point, everything about the story of Alzheimer’s is so incredible that it breaks my heart to tell you the twist. There was so much hope that these amyloid-clearing drugs would stop Alzheimer’s, but clinical trials have demonstrated only modest effects in slowing cognitive decline. Of the two drugs, the lecanemab clinical trials were the most promising, showing a modest slowing projected to extend the course of the disease by ~9 months. Unfortunately, the drug also has side effects, like an increased risk of brain swelling. It helps; it’s a crucial step, but sadly, it’s not the final solution.

Why hasn’t the amyloid-clearing approach worked better? That’s unclear. There’s still hope that these drugs do work well, but they weren’t given early enough in the course of the disease to prevent neurodegeneration. Evidence from families with autosomal dominant genetic mutations (like Carol’s family) suggests that the biomarkers for Alzheimer’s probably begin to appear more than 15 years before the onset of cognitive symptoms; in the clinical trials, however, the drugs were administered much later in the course of the disease. Clinical trials are underway to determine whether earlier administration of the drugs will yield better results, and everyone has their fingers crossed. In parallel, some suspect that the amyloid hypothesis, as stated, may not be quite right or may be incomplete. Hardy has taken this position: “Although [the amyloid hypothesis] almost certainly has some elements of truth to it … it clearly does not capture the complexity of the disease process in several ways.” Still others speculate about alternative triggering causes, such as the accumulation of another protein inside neurons, tau, as well as viruses and environmental toxins. At this point, no one knows for sure.

The unfinished story of Alzheimer’s is a remarkable account of scientific achievement but one that does not have a happy ending, at least not yet. Carol spent the 30 years following the discovery of the APP mutation as a patient advocate for the disorder, sharing the story of her family and inspiring connections between individuals afflicted with Alzheimer’s and researchers searching for a cure. Absent that cure, she refused to get a genetic test to determine if she was a carrier herself. Sadly, she was diagnosed with the disease in 2012 and we had no way to help her. After experiencing all stages of Alzheimer’s, she died from it in March 2024. Let’s pause to reflect on this timeline: more than 30 years have passed since Carol wrote her letter and Hardy’s group identified APP, and we still do not have a highly effective treatment or cure for Alzheimer’s, even for families like Carol’s where we can trace it to a genetic mutation. As Carol’s devoted husband, Stuart, says, “It’s the kids we’re fighting for now.”

So, what’s holding back a cure for Alzheimer’s? Tragically, we can ask the same question for so many other brain disorders, including Huntington’s, Parkinson’s, multiple sclerosis, epilepsy, depression, schizophrenia, and so many more. Though we have ways of mitigating some of the effects of these disorders, we cannot cure any of them. Worldwide, the numbers are staggering. For the 8.5 million individuals afflicted with Parkinson’s, we have treatments to help mitigate the symptoms but no way to slow down the neurodegeneration associated with it. A striking 970 million people around the world are living with a mental disorder such as depression, anxiety, or psychosis, and for approximately one-third of those (323 million), their symptoms are resistant to existing treatments. A remarkable 1.2 billion individuals suffer from chronic pain, and while the most extreme cases can be treated with opioids, those drugs can lead to both cognitive impairment and addiction. These are just a few examples. In 2010 brain disorders cost the European Union (EU) €800 billion per year—an amount larger than the entire gross domestic product of the Netherlands and more than cancer, cardiovascular disease, and diabetes together. Similar estimates for the United States in 2016 suggest a cost of $1.5 trillion, or 9% of its gross domestic product.

Humanity can do so many amazing things. We can fly to the moon; we can battle many types of cancers into remission. So, what’s holding us back from curing brain dysfunction? Or, in the absence of cures, what’s holding back more effective treatments?

I am a neuroscientist, and I have been engaged in brain research for over two decades. For a long time, I’ve been convinced that I have the best of all possible jobs: I get paid to think up new questions about how the brain works and answer them. A large part of what inspires my research is my intense curiosity about how the brain gives rise to the mind, and to ourselves. To answer these questions, I focus on memory. I investigate questions like: When we have the experience of remembering that we’ve seen something before, what is happening in our brains? How do our brains manage to remember so much? And how do our brains curate what we remember and forget?

My work is not driven just by curiosity; I believe that a foundational understanding of how memory works will contribute to future treatments and cures for memory dysfunction, including age-related dementias such as Alzheimer’s. In fact, part of my research program focuses on transforming what we’ve learned about memory into the earliest stages of developing a new treatment for memory impairment. Ours is but one example of what is known as the bench to bedside approach, where fundamental research discoveries are the first step toward developing new clinical treatments.

The bench to bedside narrative is so deeply ingrained in brain research that it’s not typically questioned or even discussed. Brain researchers all have their own analogs of the things that I state in all my research grants: “The goal of this proposal is to understand how the brain stores memories. These results could inform new treatments for deficits in memory such as age-related dementia.” After all, to fix something it’s helpful to understand it, right? Obviously.

But are we learning the right types of things? In the past few years, I have started to question the broader bench to bedside narrative when it comes to brain research. Simply put, when it comes to brain disorders, the orderly progression of discovery in brain research has not led to an orderly progression of new treatments and cures for brain dysfunction. In other words, there has been a lot of perceived success on the bench and very little on the bedside, at least so far. There are exceptions—very important ones. But the bedside has been dominated by frustrations, variations of the frustrations encountered with Alzheimer’s.

Around 2011 something alarming happened: six of the world’s largest pharmaceutical companies decided to pull back their brain drug development efforts following years of failed and expensive attempts to bring drugs through clinical trials. Together, they had invested several billion dollars in developing new drugs, including $18 billion in Alzheimer’s alone, and they had very little progress to show for the venture. What was going wrong? Reports suggest that, en masse, these companies concluded that we do not yet know enough about the brain to create new drug therapies for its dysfunction; it simply is not a good investment. In other words, progress at the bedside would be limited unless and until we make more progress at the bench.

In the grand scheme, not much has changed since 2011. We still do not understand the causes of most brain disorders. For Alzheimer’s and Huntington’s disease, we still lack any highly effective treatments. For disorders like depression and schizophrenia, existing treatments work for some individuals but not for many others. That isn’t to say nothing has been happening—it has! Progress in the nuts-and-bolts arm of brain research is exploding in any way you measure it: papers published (fig. 1a; a proxy for facts collected), or even the number of pages in neuroscience textbooks. And it has been for several decades. However, progress in developing new treatments has not followed as expected: the number of new brain drugs introduced annually has been steady for the past 30 years (fig. 1b). So work at the bench has been progressing, but for some reason it has not translated efficiently to the bedside. The big question we need to answer is: What’s been missing?

Unless you are really (really!) in the know, the arc from discovery to treatments in brain research—the bench to the bedside—probably is not happening as you suspect. At least that was true in my case. Even after working for decades in the field, I misunderstood how new treatments for brain dysfunction are developed. To drive this home, consider that in 2019 Joshua Gordon, director of the National Institute of Mental Health (NIMH) from 2016 to 2024, lauded the approval of a new drug to treat postpartum depression (brexanolone) as “a cause for celebration for psychiatric neuroscience, as it represents a true bench to bedside success for our field. The promise of basic neuroscience to provide truly novel and effective treatments for psychiatric disorders has for a long time been only that, a promise. But not anymore.” Note that brexanolone was one of the first realizations of the bench to bedside narrative leading to a genuinely novel treatment for a psychiatric disorder. It didn’t come until 2019, and it was one success in a rich and varied history in which successes were few and far between.

FIGURE 1. The disconnect between papers published about the brain and the introduction of new brain drugs. a) Total number of papers published per year 1990–2023, indexed on the search engine PubMed.gov with “brain” in the title, keywords, or abstract. b) Total number of new brain drugs introduced per year across the same 33-year period, computed via a 10-year running average.

You might wonder: How can this possibly be true? After all, we have plenty of drugs to treat depression, anxiety, psychosis, and many other psychiatric disorders. Well, while these existing drugs work for some individuals, they fail to work for many others. And further, we don’t have a complete understanding of how these drugs work. It turns out that many of these drugs were not developed based on understanding how the brain operates, but rather during a time when we did not understand much about the brain at all. In fact, when these drugs were developed, the field hadn’t even reached a consensus that neurons in the brain use neurotransmitters to communicate. Instead, many of these brain drugs were discovered either serendipitously or by a process I’ll call “try it and see what happens.” The first antidepressant (iproniazid) was created in 1952 while researchers were looking for a treatment for tuberculosis. The first drug to treat anxiety (meprobamate) was created in 1945 while they were looking for a treatment for penicillin-resistant bacteria. Ritalin, one of the first drugs for attention deficit hyperactivity disorder (ADHD), was created in 1944 via “try it and see.” A nontrivial fraction of the drugs that we have today are actually not new drugs, but rather refinements of old drugs created before 1960. And, while we now better understand how the old (and new) drugs work, many of the newer drugs operate in the same ways as the original ones.

One of the most powerful statements of frustration comes from Thomas Insel, the director of NIMH who preceded Gordon and served from 2002 to 2015:

I spent 13 years at NIMH really pushing on the neuroscience and genetics of mental disorders, and when I look back on that, I realize that while I think I succeeded at getting lots of really cool papers published by cool scientists at fairly large costs—I think $20 billion—I don’t think we moved the needle in reducing suicide, reducing hospitalizations, improving recovery for the tens of millions of people who have mental illness. I hold myself accountable for that.

Twenty billion dollars spent across 13 years did not move the needle. What will it take?

During his tenure at NIMH, Insel was a tremendous and effective force in directing mental health research toward investigations of brain dysfunction. One of the explicit goals during that era was to redefine “mental disorders” as “brain circuit disorders” to focus the search for new therapeutics on the brain. Since leaving his position a decade ago, Insel has redirected his efforts toward facilitating access to treatments that already exist. As he explains, “I still believe we need better science and a deeper understanding of the biology, the psychology, and the environmental factors underlying mental illness.… But there are pioneers who have taken a broader view of the problem … they are finding faster ways to put out the fire.” While I admire this move tremendously, the fact that one of the once biggest and most influential proponents of brain research is now questioning the efficacy of the enterprise should prompt us all to pause and reflect, to say the least.

When thinking about these issues, it’s natural to ask: Won’t new treatments naturally emerge once we fully understand the brain? Perhaps, but there are two complications to this question. The first is that what’s happening in the brain is not the only thing we need to consider when trying to understand brain dysfunction and develop treatments. Social, economic, and environmental factors and trauma can cause brain disorders; behavioral interventions, as well as social support, are important routes to treatment. In other words, it’s not just the brain that we need to understand—we also need to understand how brains are influenced by (and interact with) the world. The second is that we are far from understanding everything about the brain. In the case of drugs and other brain-based therapies (like brain stimulation), interventions typically lag scientific discoveries by decades. To ensure that the intervention is effective and safe, an intervention must first be created and then tested in multiple stages of clinical trials. For instance, a new generation of game-changing drugs designed to treat and prevent migraine that were first approved in 2018 evolved from discoveries about a specific neurotransmitter pathway (CGRP) that happened more than 30 years prior, in the early 1980s. Patients with neurological and psychiatric disorders need solutions now. So the question we need to answer is: How do we expedite learning the things about the brain that we need to know to treat brain dysfunction?

I’ve looked, and the information needed to answer this question is hard to find and synthesize, even if you are an expert. So I decided to write a book to try to answer it. I wanted to understand the challenges blocking progress to new treatments for all types of brain dysfunction, including mental illness. Neuroscience has seen so much progress in the past 30 years—we’ve seen multiple forms of technology revolutionize the field, including CRISPR, genome-wide association studies (GWAS), connectomics, optogenetics, large-scale neural recording, machine learning, and artificial intelligence. We’ve invested tremendous resources to pursue brain research globally, including the US BRAIN Initiative and similar efforts in Australia, Canada, China, the EU, Japan, and South Korea. And we’ve learned a lot about the brain through these efforts. So why have we struggled so much to translate the exploding number of discoveries that are happening at the bench to the bedside? How can we get better at understanding and treating neurological and mental health? What does the path from where we are now to successful treatments look like?

This book began as my own personal journey, as a brain researcher, trying to answer these questions for myself. In all honesty, I began the journey quite pessimistically, as I realized that I could not describe the current “grand plan” for the field—a description, in broad strokes, of how neuroscience plans to discover the things it needs to know about the brain to develop new treatments and cures for brain disorders. I suspected the same was true for most of my colleagues. If we cannot even articulate the field’s current plan, how can we identify why or how it is going wrong?

I thus became compelled to spell out a Grand Plan for brain research that I could believe in. And so I spent the better part of a few years sifting through neuroscience and medicine well outside my typical wheelhouse, as well as history and philosophy. By the end, I realized that a new path forward is emerging in brain research just where we need it, one that I am optimistic will lead to more and better treatments. Some researchers are already on this path, and it is exciting to think about where it will bring us. It’s a significant shift, however, relative to how we’ve been thinking about the brain up to this point, and it requires us to rethink how we approach treatments entirely. Before we can think about this new path, we need to understand the Grand Plan as it has existed in neuroscience to date. In a nutshell, we’ve been oversimplifying our ideas about what type of thing the brain is and how it breaks. It’s not that simplification in and of itself is bad; in fact, simplification is inevitable. As the saying goes, “All models are wrong, but some are useful.” In that famous phrase, “wrong” refers to the fact that any model, by design, is a simplification that captures some aspects of reality while disregarding others. The problem in brain research is that we’ve oversimplified how we think about the brain in ways that aren’t just wrong but also aren’t useful for treating brain dysfunction because they fall short of what we need to know. The Grand Plan up to this point has rested on these oversimplifications.

What’s the current Grand Plan?

One of the biggest slices of the Grand Plan is so central to the modern research agenda that it appears in the popular undergraduate introductory textbook Neuroscience: Exploring the Brain. It’s called molecular medicine. The first step involves identifying a gene whose mutation is responsible for the disorder of interest. Next, researchers create an animal model of the disease by mutating that gene in a mouse, and they use it to determine what is going wrong in the brain. The mutation might lead to the absence of something the brain needs to function. Or it might lead the brain to produce something toxic. Whatever is happening, once it’s understood, researchers create a drug to fix it.

The rationale here is that the mouse brain serves as a proxy for the human brain. While we cannot perform invasive experiments in humans, we can (with much thought, care, and compliance with ethical and regulatory guidelines) purposefully recapitulate a mutation in a mouse. If that gene has a similar function in mice and humans, learning what happens when it is mutated in a mouse can help us develop a potential treatment. And once we have a treatment that works in mice, we can then test it in humans. Finally, if the drug makes its way through clinical trials, voilà, we have a new treatment! Molecular medicine had tremendous optimism behind it as recently as a few decades ago. Today, the plan—at least stated in this simple way—is regarded as naive. Among the many reasons is that we’ve learned most brain disorders cannot be linked to individual genes or even a handful of them. So why did we initially think that they could be?

Molecular medicine followed tremendous discoveries in genetics and molecular biology in the 1950s–1990s, including the discovery of the genetic code (loosely: DNA base pair triplets code for amino acids and amino acid sequences are configured into proteins, the building blocks of the body and brain). The excitement surrounding these discoveries spilled over into brain research and was described by the psychiatrist and Nobel laureate Eric Kandel in a brilliant paper in 1998 titled “A new intellectual framework for psychiatry.” In this paper, Kandel described the new, emerging way to think about psychiatric disorders as tied to physical changes in the brain. He was tapping into the same ethos that Insel was channeling during his tenure at NIMH when he sought to redefine “mental disorders” as “brain circuit disorders”; it was the same ethos that led to the description of molecular medicine that is reflected in today’s textbooks. Because it reflects the ideas of not just one individual but an entire era, I’ll refer to it throughout the book as the molecular neuroscience framework.

This way of thinking was a notable shift away from how mental disorders were regarded in the 1960s, where only a few such disorders were regarded as “organic” (brain) disorders. The majority were regarded as “functional” (mental) disorders with unspecified causes that need not be tied to the brain in any way and were most often treated through psychodynamic therapy. If, as Kandel proposed, all psychiatric disorders arose from the brain, then perhaps we could understand them by understanding the brain.

The first two principles, the core of the framework as Kandel described it, conceptualize psychiatric illness as the end of a domino chain: genes code for mRNA, which codes for proteins; proteins create neurons; neurons combine into neural circuits; and activation of the brain’s neural circuits leads to all mental and behavioral function and dysfunction (fig. 2). Consequently, all psychiatric illness is a disturbance of brain function. Even in cases where the causes of disease are environmental, brain function is still implicated because the environment is causing changes in the brain that lead to the illness.

Kandel’s third and fourth principles acknowledged that genes alone do not determine mental illness. Rather, social and developmental factors also play a crucial role. Together, these two principles specified a mechanism by which this happens: behavior and social factors feed back to modify genetic expression, leading to changes in how neurons function and how neural circuits are wired (in other words, “learning”). As a consequence of this feedback loop, Kandel proposed that “all of ‘nurture’ is ultimately expressed as ‘nature.’ ” Conceptually, this was a big step forward for the field.

Finally, the fifth principle captured the idea that the long-term effects of psychotherapy and counseling operate via this same mechanism: by learning. Therapy changes gene expression and, in turn, reshapes neural circuits. In this framework, both psychotherapy and brain drugs operate via a common pathway.

FIGURE 2. The molecular neuroscience framework. Genes code for mRNA, which codes for proteins; proteins create neurons; neurons combine into neural circuits; and activation of the brain’s neural circuits leads to all mental and behavioral function and dysfunction. Influences from the environment happen via a feedback loop to the brain to influence gene expression. In this framework, dysfunction is presumed to happen following deficits at one (or more) of these four stages.

In sum, the molecular neuroscience framework is largely set up as a domino chain where changes in genetic expression ultimately change brain activity and brain function. It allows for a singular feedback loop whereby information from the environment can be fed back to the brain (to influence gene expression; fig. 2). Crucially, this framework is not limited to descriptions at the molecular level, but it does emphasize gene expression as a crucial node through which everything must pass. In the case of neurological disorders, the presumption is that changes in something about the brain lead to neurological dysfunction. Take Alzheimer’s, for instance. The amyloid hypothesis fits within this framework, with its emphasis on a domino-chain cascade of events that begins with a mutated gene that produces a protein and ends in cognitive impairment; in the case of Carol’s family, that gene is APP, and the protein is amyloid-beta.

I am not arguing that the molecular neuroscience framework, with its emphasis on domino-chain causality, is exclusively how researchers have been thinking about the brain—there are plenty of examples of brain researchers thinking in other ways. Instead, my argument is that it has implicitly been the predominant way of thinking about the brain in the past few decades of brain research and has, therefore, guided how we have thought about treatments for brain disorders. The framework has led us to several important discoveries, including some that are recognized by Nobel prizes, and it has also led to transformative new therapies to treat brain disorders. At the same time, we can now see how it’s problematic, and why it’s time to evolve beyond it.

Three problems with the molecular neuroscience framework

Now that more than 25 years have passed, the problems with the molecular neuroscience framework are apparent. The biggest problem is that the framework sets brain researchers off along the wrong path regarding how the causes of brain dysfunction will manifest. Domino chains are devilishly tempting because they are among the simplest and most satisfying accounts of how a system works: you set up the dominos in a row, you knock the first one down, and they all fall in turn. But thinking about the brain this way presumes that brain dysfunction follows from an aberrant domino; it leads researchers to focus on pinpointing that one domino (such as a genetic mutation or the reduced vigor of activity in a brain area). Once a cause for a disorder is pinpointed, the thinking goes, researchers can develop treatments for it either by targeting that domino directly or by compensating for the broken domino somewhere downstream. In other words, the framework can be summarized by the phrase, “find the broken domino and fix it.”

Why is this a problem? Because the brain is not a domino-like system. It is instead a system that is designed to adapt to changing conditions. A changing brain means that many dominos and their interactions might change over time, and we may not be able to reliably point to a single domino as a culprit. One well-understood example is blood pressure. Our blood pressure is regulated by our brain: brain mechanisms compare what our blood pressure is with what it should be, and when it’s off target, our brain sends signals to our body to adjust it. When our blood pressure chronically deviates from what is healthy for us, the specific cause is most often unknown. Instead of thinking about blood pressure as a chain with a broken domino, we think about it as a system that is constantly incorporating feedback but is set to the wrong point. To fix unhealthy blood pressure, we focus on recalibrating the system (for instance, with drugs that change the dilation of blood vessels) as opposed to finding and fixing one broken piece of it. This is an entirely different way to conceptualize how dysfunction manifests. We’ll elaborate on what kind of system the brain is later on, but for now, the upshot is that we need to seriously consider whether the reason we still do not understand the causes of many brain disorders is that we’ve been primarily focused on pinpointing broken dominos, and this is just not how the brain works.

The second problem with the molecular neuroscience framework is closely aligned with the first. Our focus on broken dominos not only has led researchers to search for the causes of dysfunction in individual dominos, it has also led to a laser focus on creating treatments that target those individual dominos with exquisite selectivity. When those treatments are drugs, the approach is called rational drug design, and it’s captured with the phrase “one gene, one drug, one disease.” In 2011, when pharmaceutical companies abandoned brain drug development efforts en masse, some researchers pointed to this type of oversimplification as the problem—a drug targeting a single domino can fail when that domino interacts with other dominos.

One example of this from cancer research is drug resistance. It happens when a drug that is initially effective at treating an individual’s cancer stops working, leading to cancer relapse. Cancer drugs are often designed to target specific elements of a genetic network (dominos), and the reason drug resistance happens is that the genetic networks that lead to cancer are set up not as domino chains, but instead as complex networks in which there are multiple pathways that lead to a cancerous state—when one route is blocked, the cancer cells adapt and find another path. Consequently, when developing effective treatments for cancer, researchers consider full genetic networks, not just individual genes, and oncologists will often administer combination therapies designed to block multiple paths to cancer, not just one. Given that the brain’s components (like genes) are more often than not components of complex networks, we need to seriously consider whether the reason that attempts to treat brain dysfunction have not worked is that, as with cancer, targeting singular dominos is often the wrong approach.

The third problem with the molecular neuroscience framework is that it is incomplete. When Kandel first described it, he intentionally left details about how the brain gives rise to the mind and behavior unspecified, explaining that “the great challenge for biology and psychiatry at this point is to delineate that relationship in terms that are satisfying to both the biologist of the brain and the psychiatrist of the mind.” Thus, this framework not only leaves out missing facts (like details about specific genes and genetic expression) but is missing concepts about how we should think about the link between the brain and the mind. How can we possibly understand how changes in the brain lead to mental dysfunction in the absence of solid ideas about how they connect together?

I don’t expect that my call to rethink how brain researchers have been approaching things will be controversial. It captures the pulse of what’s happening in the field right now. Brain researchers in all divisions of the field are sounding the alarms, and funding agencies are listening. There’s a growing sense that we’ve been oversimplifying the brain, and it’s time to evolve the current Grand Plan as it’s described in textbooks. What’s much less clear is what comes next. What should we replace the existing Grand Plan with?

How do we move forward?

A fable written in 1963 titled “Chaos in the Brickyard” likens the scientific enterprise to building large, imposing edifices, and the facts that scientists acquire via their experiments to bricks. The tale begins by describing science as a type of thoughtful construction that relies on producing bespoke bricks, as needed, to build solid and sound structures while also avoiding waste. It then transitions into the misguided notion that “bricks are the goal,” with bricks collected into large piles with great pride—ultimately at the cost of actually building anything, because the builders can’t find the right bricks in the big mess. The fable ends with the warning, “Saddest of all, sometimes no effort was made to maintain the distinction between a pile of bricks and a true edifice.”

It’s time for us all to consider whether we have arrived at our own form of chaos in the brickyard of brain research. Have we transitioned into piling up bricks (data)? To be clear, I am not questioning the value of nuts-and-bolts, curiosity-driven research. The history of biomedical research offers up many examples of why this type of research is so essential: investigations of retroviruses before the discovery of HIV; investigations of the light-sensitive proteins in algae before they became the foundation of optogenetic biotechnology; investigations of the chemicals released by parasitic snails before anyone suspected that they might be useful to treat pain. Curiosity-driven or “basic” research is crucial for laying the foundation for treating brain dysfunction. Moreover, understanding the brain because we are curious about it—to gain insights into ourselves and how we work—is a worthy and impactful goal in and of itself.

It’s time, however, to reconsider the edifices we’ve presumably been building as we mass-produce bricks. In other words, it’s time to evolve curiosity-driven research beyond the molecular neuroscience framework and its domino-chain ethos because it’s both wrong and too simple. As I’ve mentioned, different and more complex ways of thinking about the brain have already been suggested. All reflect a shift away from simple domino-chain descriptions that emphasize things like candidate genes and proteins or which brain areas are activated in human fMRI studies, and a shift toward examining brain systems more holistically. In place of domino chains, these approaches appreciate that the whole may not easily be predicted by understanding how the brain’s parts operate when studied in isolation. None of these new ways of thinking have reached a broad consensus, however, and more consensus is what we need if we are going to move the needle on more successfully treating the brain and its dysfunction.

Let’s take another look at Alzheimer’s disease, this time to understand what kinds of new ways of thinking about the brain have been proposed. The amyloid hypothesis that John Hardy championed in 1991 and its focus on the accumulation of the protein amyloid-beta as the triggering cause for Alzheimer’s fit squarely into the molecular neuroscience ethos. In 2023 Hardy and his colleagues began advocating for a different approach to Alzheimer’s in which we stop assuming that the events causing Alzheimer’s are reflected as domino chains, and we begin to embrace more of the system’s complexity. Hardy now advocates for modeling the brain systems associated with Alzheimer’s as a nonlinear dynamical system; in these systems, typically the whole (like cognitive function and dysfunction) is not easily predicted from the operation of its parts (like proteins). Calling this a shift in perspective doesn’t begin to describe it: “For non-linear systems, correlation does not imply causation, causation does not imply a correlation, and even the concept of cause-effect can be difficult to define when multiple interactions, feedbacks, and time delays are involved.” Indeed, these types of systems are far from intuitive. They can be understood; they just require different approaches, including mathematical models. Suppose the parts of the brain that go awry in Alzheimer’s operate as a nonlinear dynamical system (which, as we will discuss, is likely). In that case, Hardy is right—tackling the problem through the lens of such systems may be the only path to a cure for Alzheimer’s.

This is just one example of what’s happening at the cutting edge of brain research today, and we will discuss many more examples throughout this book. As we will see, researchers are beginning to shift their perspectives of the brain away from the domino-chain ethos of the molecular neuroscience framework to ways that better capture its complexity. But navigating the path forward is exceedingly tricky. To embrace more complexity, we can shift our perspectives about the brain in a multitude of ways. What ideas about the brain will be vital to making impactful progress toward treating—or even curing—brain dysfunction?

In this book, I will take you along a streamlined version of the same path I traversed to ask and answer the hard questions I’ve posed in this introduction. We’ll begin in part 1 by exploring how we arrived where we are today, launching with the history (which even many brain researchers don’t know) of how we’ve developed the treatments that we have thus far. To explore the relationship between understanding the brain and fixing it, we’ll trace the discovery stories behind the treatments for disorders such as psychosis, depression, and extreme paralysis, pinpointing the scientific breakthroughs that led to them. As a spoiler, unless you are really in the know, it probably hasn’t worked quite like you think (and the phrase bench to bedside certainly is not a good account of it).

In part 2 we’ll explore how brain researchers are elaborating the molecular neuroscience framework to address its three big problems. The first elaboration seeks to fill in the gap between the brain and the mind by treating the brain as a type of “computer”: an information-processing machine that receives sensory input and performs computations to determine how it should behave. While this approach holds much promise for designing new drugs (and has facilitated impactful developments in artificial intelligence, or AI), it gets us only partway to where we need to go because it continues to oversimplify the brain, treating it as a domino chain. The second elaboration proposes that we think about the brain not as a domino chain, but as something that regulates its stability and flexibility in ways that require feedback. It regards the brain as a complex adaptive system that processes information while regulating itself, thereby maximizing its fitness. We’ll see how this approach is much more promising.

In part 3 we will explore how this newfound appreciation of the brain’s complexity changes how brain researchers go about finding the causes of brain dysfunction and how to treat it. I’ll lay out in broad strokes the next steps for brain research that will be required to unlock the brain’s biggest mysteries and lead to new treatments to help the billions of individuals who are suffering. In the final chapter I’ll describe the reasons that I’m so optimistic that the next few decades in brain research will be more impactful than the last.

This book was inspired by my growing pessimism about the path forward for brain research. On the other side of writing it, I’m unequivocally optimistic. This new ethos will have a profound impact on how I approach research at the “bench,” but I’m ready to embrace these changes wholeheartedly. Brain research is on the cusp of a new era. Now that I can see how things are transforming, I’m excited to share that vision with you.

Before we dive in, a quick note on the level at which this book is written. I firmly believe that brain research will benefit from a combination of clear-headed thinking and straightforward explanations accessible to nearly anyone. While the brain is complicated and brain research is technical, it is our good fortune that these issues are conceptual, and the concepts themselves are pretty straightforward. Ideas about the path forward for brain research are important for experts engaged in brain research, but not just for researchers; they are also important for anyone who is affected by some type of brain dysfunction or has a loved one who is, as well as for policymakers, journalists, and anyone who wants to better understand the brain. Understanding the brain concerns all of us. It makes sense that we should all be privy to the solutions.

PART I How did we get here?

In the first part of this book, we’ll dive into the history of neuroscience and drug discovery to understand how we’ve developed the treatments that we currently use to treat brain disorders. In neuroscience, as in any scientific field, there are several big research questions whose answers are difficult to find and sometimes remain elusive for centuries. These questions are a persistent backdrop for the researchers who are trying to solve any problem in the field—whether it’s understanding how a memory is formed or trying to figure out how to alleviate a treatment-resistant form of depression. So, if we want to understand how we’ve gotten where we are today, we need to understand something about these big questions. I’ll start by introducing one of these questions, which will (as it has for researchers) serve as a backdrop for the first two chapters.

What is the best way to understand something as complicated as the brain?

Brain research is shaped around the reasonable presumption that understanding the right things about the brain will lead us to new treatments for its dysfunction. Achieving this goal begins with a model or theory of a brain function, like mood, or a disorder, like depression. But how do we create an illuminating model or theory? Given that there are many levels to something as complex as a brain (such as neurons, circuits, brain systems, and behavior), how can we possibly know where to start? The answer is not as straightforward as you might think—even brain researchers do not all agree among themselves.

One strategy is methodological reductionism, the notion that you should begin by breaking the problem down into simpler ones. Here, the idea is that we can understand the brain and the mind by understanding first how its parts (like neurons) operate in isolation and then how they interact. It’s an approach that begins at the bottom, with the parts, and works its way up. For some problems in brain research, reductionism has been tremendously successful—among them, understanding the molecular pathways that support learning, first in sea slugs and then in mice. Reductionism lies at the heart of the molecular neuroscience ethos. It has both fans and critics.

Reductionism is often pitted against emergence, the idea that the behavior of a complex system is hard to predict from its parts alone, because that behavior emerges in surprising ways from how those parts interact. But reductionism and emergence are not actually at odds with each other. In principle, researchers could use reductionism to figure out a complex system in which a behavior is emergent. They could study the system’s parts alone and then investigate how those parts interact (and this indeed is the explicit plan that reductionists hold in mind). The real problem is that “in practice,” exhaustively studying those interactions is typically infeasible because the number of things that exist and interact is too massive. We will not figure out the brain by exhaustively studying all the possible ways in which its 86 billion neurons can interact, and, from those principles, infer our mental abilities.

Instead, when dealing with a complex system, it can help to approach the problem from the top down, first establishing the phenomenon that needs to be accounted for (like depression) and then searching for the mechanisms that give rise to it—like the operation of its parts and the interactions between them. This top-down approach is one alternative to bottom-up reductionism. It’s an approach that ensures you keep your eyes on the prize; it retains the element that the reductionist ethos can easily overlook. While that’s easily said, it’s also important to note that a top-down approach is not a magic bullet—simply keeping in mind that you want to “understand depression” doesn’t magically lead you to a solution, and herein lies the big challenge. We can’t tackle everything, everywhere, all at once. The rationale behind bottom-up approaches is to begin by starting with the parts. The rationale behind top-down approaches is to focus on understanding the things that we most want to explain.

The tension between bottom-up and top-down approaches naturally leads to debates about the brain versus the mind. Does the brain cause all mental function? Does mental anguish like depression stem entirely from the physical brain? Even if it does, is it actually helpful to think about it that way? Debate around this question began centuries ago and continues today. As the anthropologist Tanya Luhrmann describes contemporary psychiatrists:

Sometimes they talk about mental anguish as if it were cardiac disease: you treat it with medication, rest, and advice about the right way to eat and live. A person who has had a heart attack will never be the same—he will be always a person who has been very seriously ill—but he is not his heart attack. His heart attack is in the body, not the mind. When psychiatrists talk in this manner, psychosis and depression become likewise written on the body.… Sometimes, though, psychiatrists talk about distress as something much more complicated, something that involves the kind of person you are: your intentions, your loves and hates, your messy, complicated past.… From this vantage point, mental illness is in your mind and in your emotional reactions to other people. It is your “you.”

The struggle that psychiatrists face in understanding the causes of mental disorders translates into a battle about how to treat them: Do we treat the brain (with drugs or brain stimulation), or do we treat the mind (with behavioral and talk therapy)? Neurologists don’t struggle in the same way. If someone suffers from migraine headaches, their doctor will encourage them to figure out whether certain foods, stress, lack of sleep, or substances (like alcohol or nicotine) trigger it and advise them to stay away from those things whenever possible. But neurologists won’t struggle to figure out whether it’s the brain or mind that needs treatment, and they won’t hesitate to offer medication to help the person through migraine episodes. What, if anything, makes episodes of depression, anxiety, or psychosis different?

While some individuals might go to behavioral or talk therapy to deal with the emotional fallout from a disorder like diabetes or cancer, that therapy isn’t meant to treat the cause of the disease. In contrast, for mental disorders, interventions that target the mind, like cognitive behavioral therapy (CBT), can be as effective as brain-based treatments (like medication). The idea behind CBT is that feelings, thoughts, and actions all interact reciprocally. In the case of depression and anxiety, depressed and anxious feelings arise from our thoughts about our circumstances, and this can lead to behaviors that reinforce those feelings: something at work happened that led me to think my work isn’t great, which led me to feel sad and unmotivated to do work tomorrow, and it all spirals downward. The focus of cognitive behavioral therapy is to break this feedback cycle at the stage of thoughts, over which we have control. The notion is that how we perceive situations can become exaggerated, distorted, or mistaken relative to reality, and fixing those automatic thoughts is the key to redirecting the reinforcing feedback loop toward more positive feelings and behaviors.

The way that CBT works is not inconsistent with the presumption that the brain mediates the mind. CBT could very well work via plasticity—by changing the physical brain. Thinking about what the brain is doing may not be very useful, however, because it’s a level that contains too much detail for us to see the forest for the trees. To put it another way, when we think about how neurons work, we don’t think about subatomic particles like quarks; quarks exist at a too fine-grained level for thinking about neurons (but quarks are still configured to give rise to them). Likewise, the brain might very well produce the effects of CBT, but the brain may be too fine a level to think about the problem.

Today, the effectiveness of CBT and other approaches like it is underappreciated. That said, they don’t work for everyone. But neither do brain-based therapies (like antidepressants). The big question is: What type of treatments should we employ for an individual? Ones that target the brain? The mind? Or both, simultaneously? Likewise, where should researchers look for new treatments? It’s a centuries-old debate.

These big, unresolved challenges set the stage for our dive into how we came to know what we know, and what remains unknown. What types of dysfunction can we treat, how do those treatments work, and how were those treatments developed?

CHAPTER 2 From bench to bedside

If you ask a brain researcher to describe how new treatments for brain dysfunction are created, they will likely respond with some version of the bench to bedside narrative. The idea is that discoveries about the brain at the research bench lead to treatments at the bedside, where they help actual patients in a clinical setting. Once researchers at the bench learned that the uncontrollable movements associated with Parkinson’s disease involve the depletion of dopamine, they sought to restore dopamine levels. Likewise, once they learned that the grueling sensation of pain involves pain signals traveling through the spinal cord, they sought to block those signals. The bench to bedside narrative is pervasive not just in brain research, but in biomedical research of all types: cancer, cardiology, infectious disease—you name it. The narrative captures the straightforward notion that if we want to fix the brain, we need to understand it.

In brain research, the bench to bedside narrative leads us to the following puzzle: If new understanding leads to new treatments, why hasn’t the accelerating pace of discoveries about the brain led to an acceleration in the introduction of new therapies? The answer cannot be that there is a simple delay in the time required for discoveries to be transformed into treatments; something else is happening.

Sometimes, it’s helpful to give away a punchline before explaining the details, and this is one such case. The prototypical arc of bench to bedside discovery does happen in brain research, but not as often as you might think. When it does happen, the discovery story is typically epic. But thus far it’s been more of an aspiration than a realization. Instead of starting at the bench and ending at the bedside, new treatments typically have emerged serendipitously—scientists stumbling on a treatment for one disorder while looking for another—or via “let’s just try this therapy and see what happens.” That, coupled with minor tweaks to older therapies (primarily drugs), accounts for the majority of the treatments that we have today. Historically, when bench to bedside research has worked, it’s worked well: once brain researchers have pinpointed causes, they’ve usually been pretty amazing at developing treatments. Unfortunately, we’ve been unable to pinpoint the causes of many types of brain dysfunction, and this is the central factor that led so many pharmaceutical companies to abandon the drug development effort around 2011: the absence of good leads to chase.

Ultimately, the most significant thing holding back new treatments is that, for the most part, we have not yet learned the right things about the brain, and consequently, we still do not know what causes brain dysfunction. While we might wish for research to progress along an orderly track from the bench to the bedside, it just doesn’t. The reality is more complex. A revised appreciation of how brain research happened historically naturally leads to the question: What does the future hold? One welcome new wrinkle to our forward-looking narrative is the introduction of powerful tools from AI, which provide us with a new way to circumvent understanding (at least how we think about understanding in the classic sense).

With that multipronged punchline in mind, let’s have a closer look at the details.

Bench to bedside research does happen, sometimes

When bench to bedside brain research happens, the discovery story behind the newly created therapy is epic in terms of human effort, time, and money, particularly in modern times. The first step, the bench, typically involves several different academic research groups that build on the work of one another iteratively across decades. The second step, the to, involves the transformation of those fundamental research discoveries into a new therapy (such as a drug). This step can include screening millions of chemical compounds for a promising candidate and synthesizing and screening more variants to create the right one. The final step, the bedside, includes the clinical trials required to establish that the drug is effective and safe. This last step is expensive and fraught: the average cost of clinical trials for a single brain drug is estimated to be around US$1 billion and take approximately 10 years. Once a brain drug enters clinical trials, the probability that it makes it through and to the market is less than 5%.

When bench to bedside development stories happen, we can and should celebrate. It’s worth looking at a few examples to appreciate the complexity of what’s involved.

Blocking the molecules that keep us awake

Around 30% of all adults experience occasional or chronic insomnia. It’s associated with menopause and normal aging, as well as disorders such as Parkinson’s disease, Alzheimer’s disease, and chronic pain. Loss of sleep can, in turn, lead to a host of problems, such as brain fog, depression, and poor physical health. Behavior-based interventions like cognitive behavioral therapy can help many people with insomnia, but they don’t work for everyone. Drugs are another option, but they can be addictive and have side effects. One popular insomnia drug, zolpidem (Ambien, approved in 1992), operates by modifying activity in a specific neurotransmitter pathway—in this case, the pathway of the inhibitory neurotransmitter GABA. Zolpidem enhances the amount of inhibition that normally follows when GABA binds to GABA receptors, triggering a cascade of events that leads to sleep. But zolpidem is associated with rare but infamous and bizarre nocturnal behaviors, such as driving while not fully awake—typically with no memory of the event afterward. Side effects like this have inspired the pharmaceutical industry to search for alternatives to GABA-acting drugs. The newly developed suvorexant (Belsomra) operates via a different and more recently discovered neuropeptide pathway, orexin. Neuropeptides work like neurotransmitters to facilitate chemical communication between neurons, but neurotransmitters are smaller molecules whereas neuropeptides are larger, built from amino acid sequences.

The basic research leading up to the sleep drug suvorexant began with dogs that were experiencing not insomnia but narcolepsy. Like humans, dogs with narcolepsy are excessively sleepy during the day and can suddenly lose muscle tone when excited. In the 1970s researchers at Stanford began studying dogs with a naturally occurring genetic form of the disorder. They eventually turned to identifying the genetic mutation responsible, in hopes that determining the cause of the disorder in dogs would help inform treatment in humans. Because the dog genome had yet to be sequenced, this work was slow, and the effort took about a decade.

In parallel, researchers discovered the orexin neuropeptides and their receptors in 1998 as part of efforts to better understand the hypothalamus, a region of the brain that controls many everyday functions, including eating, circadian rhythms, reproduction, and sleep. At the time of their discovery, the orexins were thought to be involved in eating (rather than sleep). The Stanford researchers linked them to sleep by showing that the genetic mutation responsible for dog narcolepsy was in fact an orexin receptor. It was still unclear, however, whether orexin would also be involved in human narcolepsy. Unlike in dogs, narcolepsy in humans is rarely passed on through families via genetic inheritance.

A few years later, a research group at UCLA linked the orexin pathway to human narcolepsy. In 2000 they discovered that orexin-releasing neurons were degenerated in the brains of individuals with narcolepsy following their death. The Stanford group followed this with a report showing that humans with narcolepsy have lower levels of orexin in their cerebral spinal fluid (as opposed to mutated orexin receptors, like the dogs). While the cause of orexin neuron degeneration in human narcolepsy remains unknown, it is suspected to be a degenerative process that involves the immune system attacking and destroying orexin-releasing neurons.

The existence of the orexins changed the way that brain researchers think about sleep. Researchers had long appreciated that hormones like melatonin play a role in making us fall asleep. From that knowledge alone, it’s easy to imagine wakefulness as the brain’s default mode, which happens when the brain holds back its sleep hormones. But the work on orexin suggests that the brain also requires at least one element, orexin, to keep it awake (fig. 3a). Consequently, orexin research created a flurry of interest from several different pharmaceutical companies into new drugs to treat insomnia. Building on the finding that individuals with narcolepsy are sleepy in the absence of orexin (fig. 3b), pharmaceutical researchers set out to create insomnia drugs to block the action of orexin in the brain. With the logic that wakefulness happens following orexin binding to orexin receptors, the researchers set out to create sleep drugs that would block those receptors, orexin receptor antagonists (fig. 3c). More than fifty patent applications for orexin receptor antagonists were filed in the years 1999–2007. Of those, suvorexant was the first to be approved by the FDA, developed by researchers at Merck.

FIGURE 3. The orexin pathway and suvorexant. a) In a healthy brain during daytime, orexin neuropeptides are released, bind to orexin receptors, and trigger a cascade of events that leads to wakefulness. b) In the brain of an individual with narcolepsy, the orexin-releasing neurons are degenerated, and orexins are not released. Sleep results because the cascade leading to wakefulness is not triggered. c) To treat insomnia, suvorexant works by blocking the activation of the orexin receptors and thus the cascade that leads to wakefulness. Adapted from Han, Y., Yuan, K., Zheng, Y., & Lu, L. Orexin receptor antagonists as emerging treatments for psychiatric disorders. Neurosci. Bull. 36, 432–448 (2020).

In the early 2000s Merck had invested heavily in the infrastructure required to explore insomnia drugs in a high-throughput way, meaning that they were set up to explore exceedingly large numbers of drugs in their pursuit of finding just the right one. The first step in the development of suvorexant involved a high-throughput screen of compounds for their ability to block orexin signaling, in 2005. While the number of compounds screened—2 million!—was large, because the process was automated and robotic, it only took 3 weeks. To perform the screen, they organized the chemicals on small plates, each 3 by 5 inches, in wells of around 1,500 chemicals per plate. By design, when orexin bound to the orexin receptors, an agent glowed, and when orexin binding was blocked, the agent failed to glow. Promising candidates (labeled “hits” in the pharmaceutical field) were those that prevented glowing. Merck researchers then screened hits for other chemical and physiological properties that would impact efficacy, safety, and the likelihood of side effects. Once they identified a promising candidate, they then created a number of chemical variants of it and screened them again in the same way. Finally, they selected one compound, suvorexant, for clinical trials.

At the same time that Merck was developing suvorexant, the Swiss pharmaceutical company Actelion was developing a competitive insomnia drug—also an orexin receptor blocker. In fact, when Merck’s clinical trials for suvorexant were just beginning in 2007, Actelion’s were ahead in the process. However, Actelion halted clinical trials in 2011 over concerns about liver safety. In contrast, Merck’s drug passed through all three phases of clinical trials in 7 years, and the FDA approved suvorexant in 2014. Five years later, in 2019, a second orexin receptor antagonist to treat insomnia, lemborexant (Dayvigo), was approved, developed by the Japanese pharmaceutical company Eisai.

To recap, the bench to bedside discovery story behind suvorexant begins with decades of basic academic research, including the discovery of the orexin pathway and the discovery that dysfunction in this pathway leads to narcolepsy. More than a decade of drug development by the pharmaceutical industry followed this basic research, including a screen of over 2 million chemicals to find ones that block orexin receptors, with minimal side effects. Next, researchers created several chemical variants to find just the right one. Finally, the compound suvorexant made its way through clinical trials. An epic tale, for sure.

Interfacing with the brain to restore movement

Drugs are not the only type of brain-based treatments for brain dysfunction. Another type of therapy, “neuroelectronics,” involves treatments that interface with brain activity more directly, either invasively with electrodes placed beneath the skull or noninvasively with electrical or magnetic current delivered through the skull. Neuroelectronic therapy can treat patients in cases where drugs exist but are ineffective, which is the case for a subset of patients with disorders like depression, schizophrenia, and epilepsy. It can also be used in cases where drugs are simply the wrong type of therapy, such as the paralysis that follows from a severed spinal cord (where no drug can recover lost function). One big advantage of neuroelectronic therapy over drugs is that it can be delivered in a localized way, to a specific part of the brain. A tremendous amount of excitement exists around neuroelectronic therapy as the next-generation of treatment for brain disorders. Many predict that this is where the majority of major brain research breakthroughs will happen, at least in the next few decades. Some neuroelectronic therapies have been developed through bench to bedside research. Let’s take a look at one such case.

Amyotrophic lateral sclerosis (ALS) is a rare and tragic neurodegenerative disorder that leads to the death of the motor neurons used for voluntary movement like walking and talking. Later stages of the disorder lead to the nightmare scenario of locked-in syndrome, where a patient has normal awareness and cognitive function but paralysis of all voluntary muscles—sometimes with the exception of the ones that move the eyes. It is the disorder that afflicted Stephen Hawking, as well as the baseball player Lou Gehrig (and it’s often called Lou Gehrig’s disease). A number of devices exist to allow patients to communicate through residual muscular function like Hawking’s system with its famous voice, but those modes of communication are pretty slow.

To treat extreme paralysis, researchers are working on a type of neuroelectronic therapy known as the brain-computer interface. It works by measuring electrical activity in the brain and decoding from it what a patient wants to happen, and then controlling a robotic device (or stimulating a person’s muscles) to see it realized. The more invasive brain-computer interfaces that require implantation of electrodes into the brain are still in clinical trials, but, like suvorexant, they are epic tales of discovery.

One example is BrainGate, a brain-computer interface that enables paralyzed patients to communicate and to move. To date, BrainGate has successfully worked in a handful of patients, including one 60-year-old man who was paralyzed from the neck down following an accident. In this patient, researchers surgically implanted an array of electrodes into the region of premotor cortex that controls hand movement. The patient then imagined writing letters with a pencil on a piece of paper, and these imagined movements caused changes in brain activity in this region that were interpreted by a computer program developed for this purpose. As he imagined characters, they would appear on the computer screen after a short delay of about half a second. Ultimately, he was able to type at a speed and accuracy comparable to texting in his age group: ~90 characters per minute with 94% accuracy. Remarkable!

The research leading up to the success of BrainGate spans decades and includes not only scientific discoveries but also the development of multiple types of technology to record brain activity. This technology has to be biocompatible, with minimal damage to the brain, and it must also be capable of recording the same brain signals for long periods of time. Several electrodes are required to measure brain activity, as one location alone is not enough—and the more the better. They also need power—these are electronics, after all. But the system can’t get too hot or it will damage the brain. Over several decades engineers have developed and refined all this technology, which continues to be developed today.

BrainGate also relies on knowledge about where in the brain to place the recording electrodes. In the 1940s Wilder Penfield identified the brain regions responsible for movement during surgeries to treat epilepsy using electrical stimulation. Following Penfield’s work, researchers mapped those premotor and motor regions with increasing levels of detail in humans and nonhuman primates using stimulation, noninvasive brain imaging (such as functional MRI), and electrical recording techniques.

BrainGate would not work if premotor cortex were not activated in a paralyzed patient as they imagine movements, and it’s fortunate that this happens. Researchers also need to be able to decipher which letter a patient is imagining based on patterns of neural activity. They developed a new way to do this using machine learning to train a recurrent neural network. The researchers began by collecting data to train the decoder, asking the patient to imagine writing each letter several times while recording neural activity. They then used this data to train the network to transform the neural activity during imagined handwriting into actual letters.

One big milestone in the development of BrainGate came in 2004 with the first BrainGate neuromotor prostheses implanted in a human, in motor cortex. A patient controlled the position of a cursor on a computer screen using only their mind. Before it was used in humans, researchers developed and tested the technology in animal models, including nonhuman primates. Since that time, one paralyzed patient used BrainGate to control a robotic arm with a level of precision that allowed him to drink coffee (2012), and another patient moved his own arms and hands following imagined arm movements (2017).

Like suvorexant, the BrainGate brain-computer interface builds on scientific discoveries about the brain that unfolded across decades; both are epic tales of how bench to bedside research unfolds.

Most brain drugs were created via workarounds and refinement

It’s easy to look at the discovery narratives behind suvorexant and BrainGate and assume that most new therapies have a similar epic discovery story behind them—one in which a decades-long understanding of brain function led to a novel treatment. But what happens if we flip the script and ask about how specific drugs were developed? Let’s test the idea for some of the most widely used brain drugs. How about methylphenidate (Ritalin), which is used to treat attention deficit hyperactivity disorder (ADHD)—does that have a bench to bedside discovery story behind it? Well, it turns out, no; methylphenidate was created in the 1940s, before we knew much about the brain. At that time we were not even certain about how neurons in the brain communicate with one another, and whether this happens via chemical transmission. What about oxycodone (OxyContin), the highly effective (but also addictive) pain drug? No, not that one either; oxycodone is a derivative of the ancient remedy opium, and it was first synthesized in 1917, again before we understood much about how the brain works. Maybe one of the modern antidepressants: paroxetine (Paxil), sertraline (Zoloft), or escitalopram (Lexapro)? Not exactly—these are all refinements of another drug. And while these refinements relied on understanding how the brain functions, they are not novel drugs that work in a new way. It turns out that despite the pervasiveness of the bench to bedside narrative in brain research, the idea that a new discovery about the brain leads to a new treatment accounts for only a small fraction of the treatments that exist for brain disorders. Moreover, it continues to be the exception rather than the rule, even in modern drug development.

I’ve mentioned refinements several times now. The idea is fairly intuitive, but what exactly is a refinement in the context of a brain drug? Brain drug refinement is a particularly thorny issue—it involves creating a brain drug that is chemically distinct but operates via the same mechanism as one that already exists. In some cases, this happens with a noble goal: to increase the drug’s efficacy, reduce its side effects, or make it more clinically accessible—for example, so that it can be taken orally instead of intravenously. However, it can also happen for more sinister purposes: to capitalize on another company’s research and development by creating a chemically distinct competitor drug that works in the same way. The legal precedent that allows this to happen dates back to a decision in the 1940s by the US Patent Office. The drug under dispute was the antibiotic compound sulfapyridine, and the Patent Office ruled that adding a nitrogen molecule was sufficient to warrant its own patent. Today, drugs that use a new mechanism of action to treat a disorder are regarded as first-in-class. In contrast, drugs that are chemically distinct but act via the same mechanism are regarded as follow-ons or second-entrants (or third-entrants or fourth …). Here, I refer to all follow-ons as refinements.

To understand how brain drugs can be created in ways not accounted for by a bench to bedside narrative, let’s take a look at the class of drugs known as antipsychotics. Not a single one of twenty-five in this class currently in use has a bench to bedside development story. How, then, were they created?

Not a single bench to bedside story behind 25 antipsychotic drugs

We often associate psychotic episodes with schizophrenia, but they can also follow from other disorders such as bipolar disorder, severe depression, and stroke, and neurodegenerative disorders such as Lewy body dementia. Psychotic episodes can involve hallucinations, like hearing voices. They can also involve delusions, like believing that someone is listening to your thoughts. A class of drugs known as antipsychotics are effective in treating psychotic episodes in some patients.

The first antipsychotic, chlorpromazine (Thorazine), was, like Ritalin, discovered in the 1950s before we knew much about the brain at all. Remember that during this era of drug development, researchers had yet to reach consensus around how neurons in the brain communicate with one another. Before and during this decade, researchers created drugs based not on understanding the brain but on observing how different chemical compounds affect human disease symptoms and animal behavior. In other words, “try it and see what happens.” Often these observations were serendipitous—meaning that researchers found one thing when looking for another.a

Chlorpromazine was developed by a French pharmaceutical company focused on creating antihistamines to treat allergies. In that effort, researchers noticed that many of the antihistamines had sedative side effects, and this inspired them to investigate whether they might have a psychiatric application. In 1952 chlorpromazine was administered as part of a drug cocktail to one uncontrollable manic patient. The effect was immediate and calming—so much so that the patient was eventually discharged. Its use was soon extended around the world to other patients with similar symptoms.

While powerful, chlorpromazine and similar drugs classified as typical antipsychotics also have an unfortunate side effect: they lead some patients to develop disfiguring involuntary movements known as tardive dyskinesia, which sometimes never go away (even if the drug is discontinued). While the mechanism of action of chlorpromazine is not entirely clear, it is known to act as a dopamine receptor blocker, which explains why it can lead to symptoms similar to Parkinson’s disease (a disorder that follows from depletion of dopamine in the basal ganglia). Those side effects are less likely in a newer generation of antipsychotics (sometimes called atypical or second generation) that are more often prescribed today, including clozapine (Clozaril). A Swiss pharmaceutical company created clozapine in 1959 as a refinement of the tricyclic antidepressant imipramine (Presamine). While everyone suspected from its chemical structure that it would have antidepressant effects, it turned out not to—instead, early tests in animal models suggested that its effects were more like the antipsychotic chlorpromazine than they were like imipramine.

While the psychiatric effects of clozapine were immediately recognized, it took several decades to win FDA approval and to reach the US market, as a consequence of two factors. First, many researchers doubted its efficacy because they believed that tardive dyskinesia could not be disassociated from the drug’s psychiatric effects. In other words, they spuriously misinterpreted the absence of involuntary movements as evidence that it would not work as an antipsychotic. Second, in rare cases, clozapine can lead to dangerously low levels of white blood cells, making individuals susceptible to infection. Ultimately, physicians addressed this problem by monitoring levels of white blood cells in the patients that receive it. These issues delayed the approval of clozapine in the United States until 1989, 30 years after it was created. While clozapine remains the most effective treatment for schizophrenia we have today, doctors do not recommend it as a first-line treatment due to side effects and the requirement for regular blood work.

In addition to problems with susceptibility to infection, clozapine also has the side effect of weight gain, leading pharmaceutical companies to create refinements that do not. Drug refinement led to the approval of lumateperone (Caplyta) in 2019 via a process that, unlike its predecessor, relied on an extensive understanding of how neurotransmitters and their receptors work. In search of an alternative for clozapine that does not induce weight gain, researchers began with knowledge built from brain research that the effectiveness of atypical antipsychotics like clozapine relies on their ability to block certain types of serotonin and dopamine receptors, and that side effects like weight gain happen because the drug also binds to other types of serotonin and histamine receptors. They thus attempted to find a drug that would more selectively block the right receptors but not the wrong ones.

That drug was lumateperone.b To develop it, researchers modified a chemical compound with antidepressant activity to create a large number of drug candidates. They then screened these drugs by testing their binding affinities for different receptors. They tested a handful of promising candidates in rats to determine their effectiveness and from them selected one compound. Following clinical trials, lumateperone was approved to treat schizophrenia in 2019, and 2 years later it was approved to treat bipolar disorder. As we can see, refinement can rely extensively on basic research. At the same time, its development is not well described by a bench to bedside account; lumateperone did not follow from a major, novel discovery about brain function, but rather from research into how an existing class of drugs operates, coupled with targeted improvements.

At the time of this writing, there are twenty-five different antipsychotic drugs in use. How many of those operate by a novel mechanism? Only the first: chlorpromazine. The antipsychotic effects of all twenty-four other drugs, including clozapine, happen by binding to the same types of receptors. Instead, what differs between them is how effectively they work and their side-effect profiles; these differences are thought to follow from the strengths with which they bind to those receptors. Remember that chlorpromazine was first developed in the 1950s, based on behavioral observations alone. What this means is that the arc of bench to bedside discovery as we typically understand it has never contributed to an antipsychotic that works in a new way.

Zooming out to brain drugs more broadly, it’s surprising to realize how pervasive refinement is, and consequently how few truly novel brain drugs are created. The frequency of drug refinement is easiest (and arguably most interesting) to quantify for the past few decades where the first-in-class versus follow-on designation has been systematically applied. For new drugs approved by the FDA since 1999, refinement accounts for the overwhelming majority of all new brain drugs: 70%.c In other words, since 1999 only 30% of brain drugs have received a first-in-class designation. In total, in the years 1999–2023 the FDA approved 116 drugs to treat brain disorders, an average of 4.6 new brain drugs per year. Of those, only 35 are first-in-class drugs; the vast majority are follow-ons. This translates to an average of 1 novel brain drug per year (along with 3.6 refinements). As you can see, refinement is much more pervasive than producing truly novel drugs.

One might wonder: If the majority of new brain drugs are refinements of existing drugs, how were the original drugs that are now being refined created? Some are in fact bench to bedside drugs, like the drug levodopa, used to treat Parkinson’s disease. Many others, however, are analogous to the early antipsychotics in that they were created before the mid-1950s. Our most powerful pain drugs—morphine, oxycodone, and codeine—were all derived from the ancient remedy opium and created before 1920. The first antidepressant, iproniazid (Marsilid), was stumbled on in 1952 during clinical trials for the lung-infecting bacteria tuberculosis by observing that patients who received the drug were “joyous.” In 1945 two Danish scientists created disulfiram (Antabuse, approved in 1951) to treat alcohol-use disorder while trying to develop a treatment for intestinal worms. In the process, they tested the drug on themselves and discovered that when they drank alcohol, it made them feel sick. While looking for an antibiotic to treat bacteria resistant to penicillin, researchers stumbled on a substance that inspired the first anti-anxiety drug meprobamate (Miltown, approved in 1955). They observed that one of the compounds had a calming effect on mice, and they refined it into a drug with longer-acting effects.

Treating depression with electricity and magnets

In treating brain disorders, we employ drugs more frequently than we do neuroelectronic therapies. But neuroelectronic therapies are important, particularly for individuals who do not respond to drugs. Like drugs, a bench to bedside description sometimes accounts for the discovery stories behind neuroelectronic therapies—such as BrainGate for extreme paralysis—but it is not the way it always happens. Also like drugs, we often understand that they work but not how, despite considerable efforts to figure them out. Let’s take a closer look at two therapies for depression: electroconvulsive therapy and rTMS.

Electroconvulsive therapy has a long and complex history that predates the earliest antipsychotics and antidepressants. Today, it is an option for individuals after antidepressant drugs have failed; in more than 50% of these cases, it is effective. The treatment involves inducing a brain seizure with electrical current while a patient is under anesthetic and a muscle relaxant. It is typically given two or three times a week over the course of 2 to 4 weeks.

The development of electroconvulsive therapy dates back to the 1930s, when the Hungarian psychiatrist Ladislas Meduna learned that a type of cell in the brain that exists to support neurons, called glia cells, differed in their numbers in different types of brain disorders. In the brains of individuals with epilepsy, there were more glia cells than normal, and in patients with schizophrenia, there were fewer. Meduna (erroneously) hypothesized that schizophrenia and epilepsy might operate in opposite ways. With that rationale in mind, in 1934 he tried using a drug to induce a seizure in a patient with catatonic stupor, a symptom of schizophrenia. As he describes it,

This patient had suffered from catatonic stupor for about four years. He never moved, never ate, never took care of his bodily needs and had to be tube-fed.… two days after the fifth [treatment], on the morning of February 10 [1934], for the first time in four years, he got out of bed, began to talk, requested breakfast, dressed himself without any help, was interested in everything around him, and asked how long he had been in the hospital. When we told him that he had spent four years, he did not believe it.

Inspired by this tremendous success, Meduna proceeded to administer the therapy to twenty-five other patients with psychosis, and in nine instances it was successful. Naturally, other physicians adopted it as well. Later the procedure was modified to induce seizures with electrical current instead of drugs.

Electroconvulsive therapy became a popular treatment for psychiatric disorders in the 1940s. It was an alternative to other procedures like lobotomies in a time before drug treatments (like antipsychotics) existed. Because the seizures could lead to bone fractures, anesthetics and muscle relaxants were introduced. Sadly, during this early period, electroconvulsive therapy was sometimes misused in tragic ways, often without patient consent. The popular novel One Flew Over the Cuckoo’s Nest, published in 1962, depicted the horrors of using electroconvulsive therapy as a punishment for psychiatric patients that were institutionalized. In the 1960s and 1970s, following the introduction of drug treatments, the use of electroconvulsive therapy declined, but it revived again in the 1980s as a treatment for drug-resistant depression (subject to stricter ethical guidelines). Today, doctors weigh its potential for side effects like memory loss and heart problems against the urgency for treatment.

Repetitive transcranial magnetic stimulation (rTMS) is similar in concept to electroconvulsive therapy, but it is less invasive insofar as it does not trigger a seizure. Instead, rTMS induces a less intense series of magnetic pulses that are delivered to stimulate brain activity in a localized region on the surface of the brain, just beneath the skull. When used to treat depression, it is most often targeted at prefrontal cortex and delivered five times per week for 4 to 6 weeks.

The development of rTMS as a technology for brain stimulation dates back to the mid-1980s. While tremendous excitement around fluoxetine (Prozac; approved in 1987) and other selective serotonin reuptake inhibitor (SSRI) antidepressants challenged exploration of rTMS, a small group of brain researchers pushed it forward to success. The application to prefrontal cortex followed functional imaging studies suggesting that activity in that part of the brain was reduced in individuals with depression. The first pilot study using rTMS to treat depression was published in 1995, followed by an industry-sponsored clinical trial in 2007 that led to FDA approval in 2008. The National Institutes of Health (NIH) sponsored a second clinical trial, which successfully reproduced the results of the industry-sponsored study.

As we can see, while findings about the brain inspired the development of both of these therapies, we still don’t really understand how either of them works. Some theories predict that the seizures triggered in electroconvulsive therapy alter levels of serotonin, dopamine, and excitatory neurotransmitters, such as glutamate. Other theories predict that electroconvulsive therapy leads to a reduction in brain inflammation and/or an increase in the release of certain hormones. Yet other theories propose that the effects of electroconvulsive therapy happen via enhanced brain plasticity and the creation of new neurons, neurogenesis. A major challenge in pinpointing its mechanism of action is that many of these things occur following a seizure, and it’s extremely difficult to determine which one of them causes the relief from depression and mania. Similar hypotheses exist about how rTMS works, but its mechanism is also unclear, and it’s unclear whether electroconvulsive therapy and rTMS work via the same or different mechanisms. Like many brain drugs, we know that they work but not how. The most obvious route toward understanding them better begins with understanding how the disorders that these therapies are used to treat—depression and psychosis—manifest in the brain.

The bottleneck to treatments

We have seen that the development of new treatments for brain dysfunction has not typically progressed in an orderly way, from new discoveries about the brain to treating its dysfunction; the process is much more chaotic. That’s not a problem, in principle. But as we think about what’s been holding back the creation of new therapies, we need a realistic narrative about how brain research has worked in the past.

When brain researchers know what causes a brain disorder, they often successfully develop a way to treat it. As of 1995, the blood clots that cause stroke and lead to brain damage can be treated with drugs to dissolve clots if administered within a few hours of the onset of symptoms. As of 2017, the missing enzyme that leads to a language delay and seizures in children with Batten disease can be replaced via infusion. As of 2019, the mutated protein required for muscle movement in spinal motor atrophy can be replaced with a one-time gene therapy to restore the healthy version of it.

There are only a few cases of disorders for which we clearly understand a cause and have not yet been able to develop a treatment. Examples include Huntington’s disease and Fragile X syndrome, both caused by a single gene mutation identified decades ago. Those cases are tricky: the mutation that leads to Huntington’s disease causes the accumulation of a toxic protein that triggers neurodegeneration, and we haven’t yet figured out how to clear (and replace) it. The mutated protein that leads to Fragile X syndrome is thought to have a plethora of functions including regulating the expression of other genes in complex ways, and we haven’t figured out how to restore it.

While those cases do exist, by far the biggest factor holding back the development of new treatments is simple: we do not know enough about the causes of brain dysfunction. In the case of many neurodegenerative disorders, we have a good sense of what degenerates but not what causes the degeneration (or how to prevent and stop it)—Alzheimer’s, Parkinson’s, and multiple sclerosis are all examples. In the case of most neuropsychiatric disorders, we have even less of an idea of their causes and no biological tests for them, including depression, anxiety, obsessive-compulsive disorder, schizophrenia, bipolar disorder, and anorexia. In some of these cases there are treatments, but not ones that followed an understanding of biological causes. Psychiatric disorders are among the most complex and mysterious disorders in all of medicine.

Much of brain research can be thought of as building the knowledge required to identify those causes—the type of understanding of the brain ultimately needed to fix it when it breaks. Sadly, the low-hanging fruit has already been picked; we’ve already accomplished the easiest bits. So now it’s time to buckle down and do all the hard work to figure out how to understand the brain and the causes of brain dysfunction. Given that the human brain is the most complex known object in the universe, it probably won’t be easy. Or will it?

Artificial intelligence—a new path forward?

Our tour through the discovery stories behind treatments for brain dysfunction has shown us that some paths to brain-based treatments circumvent a deep understanding of what causes dysfunction to produce some incredible outcomes. Though that well seems to have run dry, powerful new artificial intelligence tools might provide us with a new way to refill it.

Taking a step back to put these tools into perspective, let’s first reflect on the more traditional approach to developing treatments. Scientists painstakingly try to figure out something (say, how depression works) by creating hypotheses and testing them with experiments, ultimately leading to models that can account for a wide variety of data. Richard Feynman, the revered theoretical physicist and Nobel Prize winner, famously said, “What I cannot create, I do not understand.” That phrase captures the idea that building something like a model (or, in Feynman’s case, deriving something mathematically) is the ultimate test of understanding.

In the past few decades, the relationship between understanding and building models has changed in a fundamental way with the introduction of increasingly effective artificial intelligence and, specifically, machine learning. In contrast to classic approaches to model building, machine-learning models figuratively wire themselves up to do whatever needs to be done. Training these models amounts to adjusting millions-to-trillions of model parameters, often by comparing a model’s best guesses with corrective feedback from a tutor. The magic happens when these massive models are set off to figure out how to solve problems via trial and error and they succeed at finding a solution. The power of this type of approach is that it can create models that aren’t just limited to particular scenarios but can, instead, robustly generalize across many. The drawback of machine learning is that because these models are so complex, we often do not understand how they come up with the solutions they find. This means that the creation of models can no longer be held up as an illustration of understanding; for the first time in history, we can build models by gathering massive amounts of data but otherwise not understand much of anything. Yet we are using these models to help us find treatments for brain dysfunction. The program AlphaFold is one great example.

Solving protein folding without understanding it

A lot of drug development is focused on understanding how molecules interact with one another—for instance, to block a particular type of ion channel activated by a particular neurotransmitter. AlphaFold taps into an enterprise central to this goal: knowing the 3D structure of proteins like ion channels and how they emerge from the amino acid sequences that make them up. You might remember that DNA is transcribed as RNA, which is translated into the amino acid sequences strung together to create proteins. The 3D structure of a protein contributes to determining its function, including the molecules that bind to it (such as a drug). Knowing the 3D structure of a protein is exceedingly helpful in determining its function as well as designing a drug that binds to it.

The older approach for determining 3D protein structures involves crystallizing the protein and then probing it with X-rays to create an electron density map that allows us to infer its structure. Completing this process for a single protein can take years, and to date it has been determined for only a subset of around 10% (~100,000 of ~1,000,000) of existing proteins. Filling this gap, and quickly, has inspired efforts to create models that can successfully predict the 3D structures of proteins based on their amino acid sequences alone, a challenge called the protein folding problem. In the classic approach to model building, researchers predict 3D protein structures based on the principles by which the molecules that make up amino acids interact—for instance, by knowing that an ionic bond can form between the negative charge of aspartate and the positive charge of arginine, maintaining their proximity in 3D. In the machine-learning approach, researchers train models based on the protein structures that have already been determined and then ask the model to predict the as yet unknown structure of other proteins without explicitly building principles into the model; instead, the model implicitly learns what it needs to know. With either approach, a successful model would be able to accurately predict 3D structures of proteins whose structures are unknown.

In 1994 academic researchers interested in this issue organized a biannual competition, the Critical Assessment of Protein Structure Prediction (CASP). Every 2 years the organization released a set of (newly determined and secret) amino acid protein sequences, and competitors submitted their 3D model predictions for those protein structures. Winners in various categories then gave presentations at the meeting, describing what aspects of their approaches led to success. Competitions like this are quite common in computer science. The broader idea is that the process of systematically comparing different models across a set of benchmarks would facilitate the growth of the entire field.

Competitors were submitting machine-learning-based entries to CASP before 2018. But that year, the company DeepMind entered the competition, submitting a deep-learning model called AlphaFold, which outperformed all other models by a comfortable distance in all but one category. Based on the previous rate of acceleration across these biannual meetings, their model was estimated to have increased growth twofold (as if one meeting, or two years, had been skipped). In 2020 the same team delivered a new model that blew the competition away, leading the meeting organizers to declare that the protein-folding problem had been solved. In 2 years AlphaFold achieved growth projected to take 8 to 10 years. No other model entered into the competition came close. It was a breakthrough!d For it, two of AlphaFold’s creators (Demis Hassabis and John Jumper) were awarded the Nobel Prize in Chemistry in 2024.

Like other machine-learning models, AlphaFold works without us understanding how; even though we’ve solved it, we still do not understand the principles of protein folding. Insofar as what we need to know to design drugs is limited to protein structures, we really don’t need to understand those principles. It’s a new type of shortcut to circumvent understanding, and brain researchers are embracing it in all sorts of ways.

AlphaFold is a machine-learning model that makes predictions. Another class of machine-learning model builds on predictive models to generate things like pictures, text, sounds, or even chemical structures. This is how large language models like GPT work—they receive text prompts as input and generate new text as output responses. These models are trained on vast amounts of language data, and what emerges from them is not just the end of a phrase but rather a potent (albeit imperfect) tool for synthesizing and generating knowledge. In other words, they don’t just complete sentences; they synthesize facts and produce stories. Brain researchers (and all humanity) are still trying to wrap our heads around how to leverage these tools to move the field forward.

How might such a tool help us to create new treatments—say, for depression? Conceptually, that would require collecting vast amounts of data to train these models, and if something about the brain is the treatment target, brain data needs to be included. At a more basic level, a researcher could prompt a generative model to design a new chemical compound for a particular target, like an ion channel. At a more advanced level, these models would be trained on many different types of data and would suggest a good target treatment for depression—evaluating drugs and neuroelectronic and behavioral therapies as candidates—and, once determined, design a treatment. In the hypothetical extreme, we might tell AI to cure depression and leave it to the program as we head to the beach.

How likely are each of these scenarios? There’s no question in my mind that machine learning and these very powerful models will play a crucial role in assisting brain researchers in the future. At the same time, I’m skeptical that we’ll get better at treating depression while all the brain researchers are on the beach. These models are smart in some ways and exceedingly stupid in others—they are particularly bad at generalizing knowledge to new scenarios. For instance, tell one to generate a picture of a salmon in a river, and it may hand back a salmon steak floating in a river instead of an intact fish. Intense efforts are underway to improve them, and the experts debate whether that will take one year or one hundred years; no one knows for sure. Until we’ve created AI programs to replace scientists, we should proceed with the assumption that we’ll need scientists to take the lead for the foreseeable future.

Moreover, the significant challenges involved in understanding the brain and treating brain dysfunction—challenges like pinpointing causes—will remain the same whether we involve AI in the solutions or not. In my mind, the most clear-headed way to think about all this is by understanding the challenges we face and considering how AI can be part of the solution rather than the solution itself.

The bench and the bedside work reciprocally

Here, then, is an answer to the question of how brain research works that is quite distinct from the bench to bedside narrative we started with. To date, the creation of new therapies has involved all manner of serendipity and shortcuts that circumvented understanding. It’s not that big breakthroughs in understanding haven’t contributed to new treatments in any way; it’s just that this prototypical description turns out to be not much of a prototype at all—it’s been much more of an aspiration than a realization.

The unidirectional bench to bedside narrative strongly parallels the molecular neuroscience framework with its emphasis on domino chains. Domino-chain causality is such a tempting way to make sense of befuddling complexity. The bench to bedside narrative captures the very satisfying idea that we should begin by figuring out how the brain works, and from there, new treatments will follow. But as I’ve described, many of our existing treatments didn’t take that path, including the first medications for depression, anxiety, and ADHD. Thus we might ask ourselves: Is this unidirectional bench to bedside narrative really the best way to think about how brain research works?

The reality of brain research is much better described as the bench and bedside acting reciprocally, learning and evolving together. This is a more nuanced and complex way of thinking about the process, but one that we need. For instance, to make brain research more impactful, we might consider: If the bench and bedside interact reciprocally, under what conditions do they both thrive? Presumably, when interactions between them are nurtured and facilitated in both directions.

Stepping back, these questions of how brain research has been working begin with the assumption that it is, in fact, working. It’s tempting to point to the treatments that we do have and assume that they came from new discoveries about the brain. For me, insight into the surprising history behind our existing therapies (and the realization of how few of our treatments have followed from understanding) is alarming. It has led me to question the degree to which brain research has been moving forward effectively. There are exceptions—very important ones. But on the whole, it makes it harder to make a strong case that all is good. Minimally, this history reinforces the notion that it’s worth considering whether something might be amiss in the field.

a This is no longer allowed in humans, because the effects can be dangerous. Instead, drugs must undergo extensive safety testing before they are administered to patients.

b During its clinical trials, the company that developed lumateperone asserted that it was first-in-class based on its receptor binding profile. However, the FDA review of the drug declined to acknowledge its first-in-class status (Center for Drug Evaluation and Research, New Drug Therapy Approvals 2019 [2020], https://www.fda.gov/drugs/novel-drug-approvals-fda/new-drug-therapy-approvals-2019), citing the absence of substantial evidence that it operates in a different manner than existing antipsychotics (Center for Drug Evaluation and Research, Multi-Discipline Review, Application Number 209500Orig1s000 [2019]).

c How did I come up with these numbers? I sifted through FDA-approved drugs to identify the subset that are used to treat brain dysfunction. I considered a drug to be a brain drug if it met two criteria: 1) It was used to prevent or treat a brain disorder, and 2) its mechanism of action was thought to occur, at least in part, in the brain. I adopted an inclusive definition of a drug as first-in-class if it was designated as such by the FDA, ChEMBL, or Eder et al. (2014) (Eder, J., Sedrani, R., & Wiesmann, C. The discovery of first-in-class drugs: Origins and evolution. Nat. Rev. Drug Discov. 13, 577–587 [2014]).

d Of note is that while the problem specified by the competition was solved with over 90% accuracy, many challenging problems required for drug development remain, including predicting the structures of proteins when they are bound to others, and predicting protein structures at high spatial resolution.

CHAPTER 3 The most complex thing humankind has encountered

In science, we typically hold up models as the products of understanding. After all, if we truly understand something, we should be able to create a model of it. A model of the eye should describe how the eye encodes and transmits different kinds of information about the world to the brain to enable us to see. But by design, models are slices of reality, not the entirety of it. This is the point that Arturo Rosenblueth and Norbert Wiener satirically highlighted when they wrote, “The best material model of a cat is another cat; preferably the same cat.” This notion of a model is not what we are generally looking for in brain research. Sleep scientists don’t create a model of sleep by pointing to a cat, noting that it robustly recapitulates the phenomenon of interest, and declare that their job is done. Replacing one complicated thing we don’t understand with another complicated thing we don’t understand is generally not what we’re after when we say we want to model something.

Instead, what we more often want is to illuminate how something works, and this requires some degree of abstraction to highlight how causes lead to effects. But that abstraction inevitably comes with a cost. In the famous phrase, “All models are wrong but some are useful,” George Box emphasized that all models, by design, are approximations of reality but not the entirety of it. We don’t seek to model, say, every molecule or even every neuron. Consequently, any model is ultimately doomed to imperfection insofar as it can capture some aspects of a phenomenon but not others. In Box’s own words: “There is no need to ask the question ‘Is the model true?’ If ‘truth’ is to be the ‘whole truth’ the answer must be ‘No.’ The only question of interest is ‘Is the model illuminating and useful?’ ”

If a model cannot include everything, this naturally leads to the question: How do researchers decide what to focus on when they are creating one? This is an important question: to solve specific problems, we need to focus on the right things. We probably won’t arrive at new treatments for depression by creating models of it focused on subatomic particles, like quarks. Likewise, we probably won’t figure out ways to cure Alzheimer’s disease by building models of behavior alone. But how, then, do we decide what we should focus on? Complicating things even more, it turns out that the things thought to matter most about the brain are continuously changing: from molecules to genes to brain activity and on (and on).

Behind the scenes, these different points of emphasis are driven by overarching concepts (often implicit) about what type of thing the brain is. The brain works via hydraulics; the brain is a computer—those best guesses (often metaphors) change with time and inform the questions that brain researchers ask and answer. If the brain is a computer, how does it compute what to do next? Those answers will most likely be reflected in brain activity. If the brain is created via a genetic blueprint, what genetic instructions assemble an eye? Those answers will most likely be reflected in genetic sequences and the proteins that follow from them.

By extension, when brain researchers adopt a new perspective about the brain, they think up different experiments and interpret their data in a new way. Researchers don’t think to ask about how the brain computes until they envision it as a computer; researchers don’t think to ask about how trauma affects development until they envision experience having a developmental influence. Researchers need to explore different types of ideas to determine the ones that stick, and some of those explorations will lead to dead ends—that’s a natural part of the process that we need to embrace.

In the previous chapter, we developed a good sense of how treatments for brain dysfunction have been created across the last century. In this chapter, we’ll look at the ideas about the brain that existed behind those treatments. We’ll appreciate the remarkable number and diversity of ideas—some quite outlandish—that researchers proposed to explain the brain and brain dysfunction. The history is humbling, and it helps us recognize that our contemporary understanding of the brain is but a snapshot of continued evolution and progress. For instance, some might look at the molecular neuroscience framework and its 1990s reductionist ethos and scoff. But those same individuals might reconsider once they learn about the ethos that the field was shifting away from, including the notion that mothers who were inadvertently just a bit too domineering were the cause of their child’s mental illness.

If we keep in mind that perspectives about the brain are constantly in flux, it becomes easier for us to ask and answer the question: From where we are now, how might things need to change going forward? Neuroscience has led to some incredible breakthroughs, but we still do not understand what causes most types of brain dysfunction. It may be time for a change in perspective.

A complete history of brain research would require many books. But to get a good sense of how researchers have thought about the brain over time, we can zero in on one disorder: schizophrenia.

A history of changing perspectives about schizophrenia

Schizophrenia is among the most elusive of psychiatric illnesses. Individuals with the disorder can have bouts of psychosis, including hallucinations (like hearing voices) as well as delusions (of persecution or grandeur). They can have trouble thinking and disorganized speech; they may also withdraw socially and become incapable of enjoyment (anhedonia). The history of changing definitions of schizophrenia is complex and reflects the changing ideas of researchers and society more than changes in those afflicted. A historical perspective of schizophrenia offers us a humbling view of where we are in understanding not only this disorder but also the brain and mental illness more generally.

In an early era, some cultures tragically linked psychosis to demonic possession or curse. But other cultures associated it with healing gifts. Anthropologists have noted parallels between shamans and schizophrenia symptoms, such as introvertedness, interactions with spirits, and periods of madness followed by resolution. Some evolutionary biologists have even interpreted the disorder’s predominance (1% of adults), persistence, and global uniformity as evidence that it was somehow selected for during evolution. Among the hypotheses of what evolutionary advantage it might have instilled is the proposal that shamans played a vital role in the success of early human cultures. Others argue that schizophrenia was not selected for directly but was inexorably linked to functions that were, such as language or social cognition. Still others suggest that it wasn’t selected for at all but instead was selected against and continuously renewed via mutations that happen at a steady rate.

The term schizophrenia was coined by the Swiss psychiatrist Eugen Bleuler in 1911, during an early era in which the idea that many types of brain and mental dysfunction might have anatomical causes, such as brain lesions, was gaining traction. Bleuler used the term to describe the splitting of the mind into different functions that each dominate an individual’s personality for some time. A few decades prior, a similar disorder had been labeled dementia praecox, but it was characterized as a disorder with progressive deterioration, and Bleuler did not believe that schizophrenia was always progressive. In his book describing the disorder, Bleuler pointed to evidence that it was hereditary, although he also admitted that some type of infectious cause could not be ruled out.

Bleuler’s concept of hereditary causes clashed with that of his contemporary Sigmund Freud, who proposed that psychosis follows from repressed memories of traumatic events that emerge in a manner that creates a loss of touch with reality. In clear opposition, Bleuler speculated that it was improbable that the disorder had psychic causes. He acknowledged, however, that psychic events could influence the symptoms, such as the specific delusions that an individual manifests.

Bleuler was refreshingly progressive for his time. To protect patients and their families from exploitation, he was emphatic that there was no known treatment: “Let us openly say to ourselves and to others that, at present, we know of no measures which will cure the disease, as such, or even bring it to a halt.” Bleuler also cautioned that individuals with schizophrenia should be hospitalized only when necessary (when the individual is dangerous or can no longer be influenced) and only temporarily whenever possible. Sadly, many did not adopt Bleuler’s advice.

In the absence of effective treatments for schizophrenia before the 1950s, individuals diagnosed with the disorder were treated in asylums in the United States, and sometimes that treatment was horrific. In addition to prolonged restraint, therapies included sedating drugs, insulin coma, and nonconsensual electroshock therapy. They also included the lobotomy, the severing of connections between prefrontal cortex and the rest of the brain to pacify a patient, at the risk of severe side effects like apathy, lack of initiative, and paralysis.

During this era, society was desperate to find better ways to treat patients with mental illness, leading researchers to focus on the causes of mental disorders at large, and schizophrenia in particular. This led to renewed vigor in the debate that Bleuler and Freud had started around whether the causes of schizophrenia are biological (organic) or mental (functional)—a debate around mental illness at large that continues today. In 1914 the psychiatrist E. E. Southard described the tension around this debate in a memorable way as the difference between brain spots and mind twists. The organic argument focused on whether anatomical differences, or “brain spots,” could be identified in the brains of individuals with mental disorders postmortem. The functional argument focused on whether the causes of mental illness could be traced to traumatic life experiences, or “mind twists.” While Southard argued that brain spots and mind twists were not incompatible in principle, he emphasized that the debate was polarizing in practice.

Proponents of the organic causes of schizophrenia drew inspiration from the serendipitous discovery of the first antipsychotic, which revolutionized psychosis treatment. As discussed in chapter 2, chlorpromazine was originally developed as an antihistamine to treat allergies. Researchers knew that it and chemically similar drugs made patients calm, leading them to wonder if chlorpromazine might have a psychiatric application. Following its initial success with one uncontrollable manic patient in 1952, its use was soon extended to patients with similar symptoms in Europe, Canada, and the United States. The impact of chlorpromazine in psychiatric wards during the 1950s was transformative, nearly eliminating the need for patient restraint. While that particular drug can lead to disfiguring involuntary movements known as tardive dyskinesia, other medications with fewer side effects followed later.

On the other side, proponents of the idea that the causes of schizophrenia were functional (or mental) were invigorated by the ideas that Freud had proposed in the late 1800s. In Freud’s framework, mental disorders were manifestations of repressed memories—most often of traumatic early life experiences (such as childhood sexual abuse). Treatment thus amounted to working with a psychoanalyst to bring the unconscious memories to consciousness for reconciliation, called psychodynamic therapy. Later variants of these theories among the neo-Freudians (in the 1940s) focused on traumas that followed from failed relationships with family members, including mothers.

One influential proposal that emerged in the 1950s–1960s was the idea of the schizophrenogenic mother. This was the notion that schizophrenia was caused by mothers who appeared to be loving but were actually tyrannical and bullying, often despite their generally good intentions. The gist was that mothers “gave birth to healthy children and then literally drove them mad” by creating a toxic home environment. The studies that supported this theory were later analyzed and deemed flawed, and in the 1970s and 1980s the idea of the schizophrenogenic mother was debunked entirely. But in the interim, the idea was put into clinical practice, shaming and blaming mothers for disorders they did not cause and subjecting both them and their children to therapies that, on the whole, did not help. Reasonably, tremendous resentment followed from this period, and “today, memories of that whole era make many people wince.… The psychiatric profession is appalled by the burden and pain that was once inflicted by telling families, and especially mothers, that they had literally driven their children crazy.”

The treatment for many individuals diagnosed with schizophrenia in the 1960s and 1970s combined medication and psychodynamic therapy. Strong advocates of functional causes argued, however, that the effects of antipsychotic drugs were merely sedative-like and not curative. In contrast, they proposed that psychodynamic therapy was a cure. As such, some facilities specialized in medication-free treatment exclusively through psychodynamic therapy alone. One example was Chestnut Lodge, a facility in Maryland. It boasted a high patient-to-staff ratio of around twenty therapists for a hundred patients, facilitating prolonged and intense therapeutic sessions four to five times per week. Because the working premise was that schizophrenia followed from childhood trauma, early phases of the therapy focused on restoring trust with a therapist. Later, the focus shifted to intensive psychotherapeutic work to rebuild a stable ego.

One of Chestnut Lodge’s most famous patients, Joanne Greenberg, wrote a popular semiautobiographical novel about her treatment at the facility following a schizophrenia diagnosis and recovery. In her words, “My story is far from unique. More than one-third of us recover fully with no special treatment whatever, and many others with a variety of treatments and approaches.… We do know that knowledge paired with compassion and the building of trust results in many successes.” Most other patients at Chestnut Lodge with the same diagnosis did not fare as well. An analysis of outcomes from the facility published in 1984 by one of its psychiatrists concluded, “The results are clear; by and large, the treatment as it was constituted failed to alter the momentum of this disease toward lifelong disability.” Of 163 patients with schizophrenia treated at Chestnut Lodge, two-thirds remained chronically ill or marginally functional. The one-third who recovered matched the numbers expected in any treatment setting.

That report dovetailed with an influential lawsuit against the facility in the early 1980s, Osheroff v. Chestnut Lodge, in which a patient diagnosed with depression and denied antidepressant medication sued the facility for negligence and malpractice following his swift recovery on medication at another facility. Even though the case never reached final adjudication, a new precedent had been set: psychotherapy alone would no longer be sufficient as a blanket treatment for all patients. Thereafter, Chestnut Lodge began prescribing medication for schizophrenia as well as other disorders.

Today, schizophrenia is primarily regarded as a brain disorder, but the definition of what that means has changed. Throughout the 1960s a popular view was that a mental disorder was only a brain disorder if 1) a biological cause could be pinpointed for it, and 2) it was responsive to brain-based treatment (through medication or surgery). In the 1980s the view began to shift toward a perspective that presumed that all mental disorders are brain disorders, even if their causes have not (yet) been pinpointed, and even if behavioral therapies were effective interventions. The implicit rationale is that in a feedforward pathway (brain to behavior), interventions at any point along it (including behavior) can be effective, at least in principle, even if the causes of dysfunction lie upstream (in the brain). This was the ethos that led to the molecular neuroscience framework. Four interwoven factors were responsible for this shift.

The first was the fall of psychodynamic approaches. Not only did they not consistently work for schizophrenia, but families (especially mothers) resented the accusation that the cause of their children’s illness was their own toxicity. In the late 1970s families organized into a powerful advocacy group known as the National Alliance on Mental Illness (NAMI) to demand more accountability in psychiatry. Through public service announcements and other forms of media, they sought to destigmatize mental illness. They also lobbied for reform and sat on the National Advisory Mental Health Council (which advises NIMH).

The second factor was that chlorpromazine and other antipsychotic drugs were clearly effective at treating psychotic episodes in many patients. Because these interventions targeted the brain directly, they were interpreted as evidence (although not irrefutable) that the causes of schizophrenia were, in fact, brain-based. A related third factor followed from enthusiasm around enormous breakthroughs in genetics, molecular biology, and noninvasive measures of brain activity such as fMRI. It’s hard to overstate the impact that the discovery of the genetic code (DNA is transcribed to mRNA is translated to protein) in the 1950s and 1960s had on the imagination of researchers. If the code for all life was universal, perhaps even the most mysterious brain functions and dysfunctions—like schizophrenia—could be explained with simple biological mechanisms. As described by one NIMH director: “During the early years of the 1980s, the possibilities of brain research and its impact on the psychiatric field seemed to mount continually. The plasticity of the brain, the effects of environmental forces on brain function, the ability to visualize receptors, and other advances all encouraged optimism.”

The fourth and final factor was more political, reinforcing a shift in government research funding from social interventions toward more classically defined biomedical research. The emphasis on social interventions for mental health dates back to the 1940s, when veterans were returning from World War II with a new type of posttraumatic stress disorder they called shell shock, inspiring government-sponsored mental health research, treatment, and social support. As part of that effort, NIMH was formed to help train mental health professionals and organize mental health care. In the 1960s President John F. Kennedy further expanded government support for mental illness by supporting the targeted replacement of psychiatric institutions with community mental health centers. There, individuals could receive support (including both medications and psychotherapy) while remaining members of their community. Kennedy was inspired, in part, to focus on mental health following a disastrous lobotomy that crippled his sister Rosemary in 1941. In the late 1970s over half of the NIMH budget was directed at supporting these community mental health centers.

In the 1980s the Reagan administration focused on cutting spending, and social support of all types was among the first to go. The new attitude was that “the federal government had no role in mental health services” and that “the Administration was not supportive of research of a broad social nature.” NIMH was thus directed to shift its focus away from mental health services and more squarely toward biomedical research, reorienting research in mental health to focus more directly on the brain.

Together, these forces created a focus on looking inside the brain for the causes of schizophrenia (and other mental disorders). The official NIMH plan for schizophrenia research in 1987 focused squarely on the molecular neuroscience framework account of the brain as I described it earlier, where genes code for molecules that combine to form neurons; neurons combine into neural circuits; and the activity of neural circuits leads to all mental function and behavior (fig. 2). The plan called on genetics, neurochemistry, brain-imaging, clinical phenomenology, and basic behavioral science to solve the riddle of what caused the disorder. The slice of the plan focused on psychosocial treatments emphasized employing the rigorous methodology of clinical trials to identify ways to help individuals with schizophrenia navigate daily life, such as improved social skills and the motivation required to engage in treatment (like medication). Shadows of psychodynamic therapy and repressed childhood trauma were nowhere to be found in the new agenda.

While these converging influences account for why researchers began to focus so intensely on the brain to determine the causes of schizophrenia and how to treat it, they do not explain why they converged on the domino-chain approach to thinking about the brain, not only for schizophrenia but for all brain research. This approach is but one of an infinite number of hypothetical ways researchers might envision what type of thing the brain is. We can thus ask: Where did this particular framework for thinking about the brain come from? And in thinking about the brain in this way, what have we learned about schizophrenia and other brain disorders?

The history behind the domino-chain account of the brain

The early history of brain research is peppered with some outlandish ideas about what type of thing the brain might be. For many ancient Egyptian and Greek scholars, the brain was not so interesting or relevant. Ancient Egyptians (3000 BCE) knew that brain damage had dire consequences, but they focused on the heart as the organ most responsible for determining our individuality. Aristotle (350 BCE) sided with the Egyptians and proposed that the brain exists to cool the blood, something like a car radiator. Aristotle did so in opposition to his teacher, Hippocrates, who argued that the brain (rather than the heart) is the organ responsible for perception, thought, and intelligence. It was not until the mid-1600s that researchers generally agreed that the brain is the center of nervous system function.

One big early question about the brain was how it communicates with itself and the body to move. Elaborating long-held ideas that the brain controls the body via fluids, René Descartes (mid-1600s) proposed that the nervous system consists of fluid-filled tubes that operate via mechanical, fluid-based forces. He likened it to the “grottoes and fountains in the gardens of our kings [where] the force that makes water leap from its source is able of itself to move diverse machines.” In Descartes’s proposal, this hydraulic system interacts with the mind (a spiritual entity) via the pineal gland.

In the mid-1700s the discovery of electricity inspired Luigi Galvani to propose another idea: that nerves operate via electrical signals. In one persuasive and influential demonstration, Galvani showed how the muscles of a dead frog’s leg could be contracted with an electrical pulse.

Following Galvani, the role of electricity was clear, but still in question was whether the nervous system was one continuous reticulum (like the circulatory system) or was parsed into individual cells with gaps between them. In the late 1800s Camillo Golgi and Santiago Ramón y Cajal adopted fervent and opposing views on this topic, with Golgi advocating for a continuous reticulum. Ironically, Golgi developed one of the first stains that enabled the visualization of long axons and dendrites of nerve cells, and Ramón y Cajal used it to support his inferences that individual nerve cells exist. Scientists more broadly adopted the idea of the nerve cell in the early 1900s, although not universally until a bit later (Golgi himself was never convinced).

Molecules matter

Once researchers knew about nerve cells, the next question became: How do they communicate with one another? Galvani clearly illustrated that the propagation of signals along nerve cells was electric, but a gap existed between cells, and so the question thus became: How is that gap crossed? Does it also happen by electrical activity (sparks)? Or might it happen via a chemical process (soups)? The debate became known as “The War of the Soups and the Sparks.”

The Nobel laureate Henry Dale was a prominent figure on the soups side of the debate. In 1936 Dale was awarded a Nobel Prize for discovering chemical transmission at the junctions between nerves and muscles. In his Nobel lecture, he speculated that chemical transmission also happened in the central nervous system. However, the Australian neuroscientist John Eccles was unconvinced by Dale’s experiments, arguing that chemical transmission would be too slow and must happen via sparks instead. How could they resolve this debate? Eccles was inspired by his interactions with the philosopher Karl Popper and Popper’s emphasis not just on experiments that are designed to support a favorite hypothesis, but on ones that can rule some options out. To his enormous credit, Eccles and two of his colleagues performed this type of experiment in 1951, and it demonstrated that Dale was correct and they were wrong. The experiment focused on motor neurons in the spinal cord of an anesthetized cat that controlled the bicep muscle. They knew that these neurons were inhibited by nerves that sensed contraction of another muscle, the quadricep. The question was: Is that inhibitory connection electrical or chemical?

In 1947 Eccles and a colleague had proposed a theory for how electrical connections could be inhibitory. The theory focused on a small “interneuron” between the quadricep sensory input neuron and motor output neuron. While a bit complicated (and ultimately wrong), Eccles’s proposal was that when the interneuron was excited by the sensory neuron, the interneuron generated an electromagnetic field that temporarily disrupted the ability of the motor neuron to fire without increasing the total negative electrical charge within it. However, if exciting the sensory neuron inhibited the motor neuron by increasing its negative charge, this could be explained only by chemical signaling. They performed the experiment in over sixty different neurons and observed inhibition every time. Everyone finally agreed—neurotransmission within the spinal cord was about soups, not sparks.

Because the work of Dale and Eccles had established a role only for chemical neurotransmission in the spinal cord, debates about how neurons in the brain communicated continued for some time. These debates were settled in the 1960s with the emergence of new technology, including histochemical approaches that allowed researchers to localize neurotransmitters to different regions in the brain, and electron microscope images that allowed researchers to visualize those neurotransmitters at individual synapses.

These 1950s discoveries about the soup of the brain set the stage for an even more intense focus on brain molecules in the latter half of the twentieth century. In other words, thinking about the brain as something in which molecules matter triggered an intense focus on molecules. In the period 1990–2023, nearly all the Nobel Prizes awarded for brain research focused on molecules, including discoveries in temperature, touch, olfaction, and day/night rhythms; the molecular cascades within neurons involving proteins such as ion channels and G-proteins; and the molecules involved in the release of neurotransmitters into the synapse. In comparison, a single Nobel Prize was awarded during those three decades related to brain activity and brain function (for insights into spatial navigation).

This intense focus on molecules in the latter half of the twentieth century led to some important new brain drugs. For instance, researchers discovered that neurotransmitters are released at a synapse and then undergo a process of reuptake that returns them to their original location. This discovery led to antidepressants that work by inhibiting neurotransmitter reuptake, including fluoxetine (Prozac, approved in 1987), which inhibits the reuptake of serotonin. Another major discovery was that dopamine is present at high levels in a brain region important for voluntary movement, the basal ganglia, and that dopamine is depleted in the brains of individuals with Parkinson’s disease. These findings led to a new treatment for Parkinson’s patients (Levodopa) in 1970.

With this emphasis on molecules, what have we learned about schizophrenia? Following the discovery that antipsychotics work by blocking dopamine receptors, schizophrenia was hypothesized in the 1960s to follow from hyperactive dopamine transmission. Research since then, however, has associated the negative symptoms of schizophrenia (such as lack of motivation and inability to feel pleasure) with reductions in dopamine receptor activation, suggesting that the disorder is much more complex. A later generation of biochemical theories focused on glutamate, following the discovery that when healthy individuals are given low doses of glutamate (NMDA) receptor blockers, they exhibit some aspects of schizophrenia (such as attention and memory problems). The symptoms of schizophrenia, however, cannot be tied to deficits in a single neurotransmitter pathway; it’s clearly more complex.

Genes matter

Much of the focus on the molecules of the brain (like proteins) could not have happened without genetics. In addition to facilitating that molecular work, genetics has provided added insight into how some types of brain dysfunction follow from genetic inheritance. Both were enabled by the discovery of the universal genetic code for all life, arguably one of humankind’s most significant breakthroughs. In broad strokes, genetic inheritance happens via genes in our DNA that are first transcribed into RNA and then translated to proteins, and the specific code (e.g., GAC is translated to the amino acid aspartate) is the same for all living things. The reality is a bit more complex; for instance, the same gene can encode multiple proteins via modifications at the mRNA stage.

Before 1950, researchers understood that genetic information in humans is organized along pairs of chromosomes and that we inherit one of each pair from our parents. They also had developed the concept of a gene as the smallest unit of genetic information, but the biological and chemical structure of a gene was still a mystery. Work on bacteria in the 1940s pointed to DNA, but exactly how this molecule reflected the genetic program was unclear. The breakthrough happened in 1953 when Francis Crick and James Watson used high-resolution X-ray images of DNA (taken by Rosalind Franklin) to conclude that DNA is configured into a three-dimensional helix, with the base A always paired with T, and C always paired with G.

A few years later, Crick elaborated this concept to propose the Central Dogma, whereby proteins are constructed from amino acid building blocks according to the instructions laid out by DNA, and the conversion from DNA to protein involves the intermediary RNA. In 1961 Crick and Sydney Brenner determined that the sequence of three DNA bases (a codon) encoded each amino acid, and by 1966 all the codons had been decrypted. At odds with proposals that the genetic code is different for higher organisms like humans, researchers determined that the codon sequences, and consequently the genetic code, are nearly universal.

During the 1970s and 1980s researchers sequenced genes of interest, but it was a tedious process. The Human Genome Project was launched in 1990 to sequence the entire human genome at the cost of around US$3 billion. By 2003 it was 90% complete. The effort determined the DNA base pair sequence of a representative human (where the representative was a composite of several humans, to maintain their privacy), where each gene starts and stops, and the DNA sequence for the noncoding regions that account for 99% of our genome.

One question of great interest was: How many genes do we have? Researchers knew that a worm (with 302 neurons) had ~20K genes. The presumption was that we, with our billions of neurons (and other complexities), would have a lot more. Researchers attending a meeting at Cold Spring Harbor Laboratory organized a fun betting pool called GeneSweep to collect the guesses. Of the 460 (presumably well-informed scientists) who entered the competition, the winner was the entrant who made the smallest guess: the project counted around 25,000 genes, and she guessed 25,947. The mean guess was 62,000, and someone guessed as high as 200,000. The small number of human genes surprised nearly everyone. Today, the number of genes continues to be debated. For instance, we now know that those 20,000 or so genes can give rise to 80,000–400,000 different proteins due to posttranscriptional modification.

Alone, the human DNA sequence is a very long and boring list of facts:

.… gene start-GAAGCGTGGTCA … -gene stop …

But having this information allowed researchers to do new things, such as compare human genes with the genes of other species. This is important because it’s easier to figure out what genes are doing in creatures like worms and flies (when analogous genes exist), and thus leveraging cross-species “homologies” can help researchers understand human gene function.

In addition, the Human Genome Project enabled researchers to pursue the genetic causes of diseases in a new way. The old method, positional cloning, allowed researchers to pinpoint the genetic mutation responsible for a disorder by tracing genetic markers through families (where some members have the disorder and others do not). This was the method used to localize the mutation for Alzheimer’s disease (chapter 1), and it was tedious. The technology developed by the Human Genome Project vastly sped up sequencing, and today researchers can sequence an individual’s entire genome in hours at the cost of a few hundred dollars. This process has enabled genome-wide association studies, which compare genetic variation across tens of thousands of individuals to identify the genes associated with a particular disease or trait, such as schizophrenia, autism, or depression.

Insights from nonbrain variants of cancer supported the idea that genes matter for dysfunction, where harmful variants of the genes BRCA1 and BRCA2 lead to breast cancer in over 50% of the women who inherit them. Consequently, individuals who carry these variants are encouraged to undergo increased cancer screening and consider prophylactic removal of their breasts to reduce risk. The perspective that genes matter not just for cancer but also for brain dysfunction led to investigations of how genetic variation is tied to nearly every type of brain dysfunction imaginable—but, alas, only a handful of nervous system disorders have been linked to a single or a small number of gene mutations (like the variant of Alzheimer’s that Carol Jennings’s family carries). More often than not, the genetic variation that leads to brain disorders is highly complex, tied to variation in hundreds of genes. Today, proponents of the perspective that genes matter generally do not focus on individual genes. Instead, they advocate for developing ways to compute total genetic risk based on large and complex genetic combinations (while also advising that the results need to be interpreted cautiously).

Missing from the core notion that genes matter is the role of the environment, which has long been appreciated. We’ve known about the disorder phenylketonuria since the 1930s—it’s caused by a mutation in both genetic copies of an enzyme that breaks down the amino acid phenylalanine. When children with the disorder consume protein, this amino acid builds up in their blood and leads to cognitive impairment. Knowing its cause, doctors treat the disorder with a low-protein diet. A more complex illustration is bipolar disorder, where we know that if one genetically identical twin has it, the likelihood that the other will is not absolute but ~70%, demonstrating that there are factors beyond genes at play.

As a shift away from the metaphor of genes as a blueprint, some researchers have suggested that genes are more like piano keys, and the pianist is the environment. The way this happens is through the regulation of gene expression, epigenetics. For instance, in the 1980s researchers discovered genetic imprinting: that an entire copy of a gene (inherited from either the mother or the father) can be silenced in an offspring, meaning there’s more going on than genetic inheritance. One way this happens is through DNA methylation: adding (or removing) a methyl chemical group to DNA to control its expression. Epigenetic regulation can also happen by changing how tightly DNA wraps around structural chromosome support proteins called histones. It can also occur via the regulation of noncoding DNA that is never translated into proteins but seems to be transcribed to RNA exclusively to regulate genes.

In the era of genetics, with its emphasis on the phrase genes matter, researchers set out to determine more definitively the degree to which schizophrenia was hereditary. While Bleuler and many others noted that it ran in families, there were lingering concerns that it could be infectious—especially following the 1950s discovery of the neurodegenerative prion disease Kuru, which was also transmitted through families but not genetically. Instead, transmission happened in the Fore people of Papua New Guinea via the ritualistic consumption of relatives after they died. There were also those ideas that schizophrenia was triggered by toxic interpersonal family relationships (the schizophrenogenic mother). To answer the question of heritability, researchers in the mid-1970s sought the records of adopted children born to mothers with schizophrenia but raised by families without it. They found incontrovertible evidence supporting a genetic link, including that those children developed the disorder at the same rate as children raised by a mother with schizophrenia (implying that the disorder was tied to the genes, not the mother who raised them). Work done since the 1970s, however, also clearly demonstrates that it’s not linked to just a single gene—rather, using GWAS, it’s been linked to genetic variation in more than two hundred genes.

Researchers also have determined that schizophrenia is not purely genetic—if one identical twin has it, the likelihood that the other will is only 50%. Following on the phrase epigenetics matter, work in the 1990s suggested the biology behind this epigenetic influence: individuals whose mothers were pregnant with them during the Dutch hunger winter famine of 1944–45 were more likely to develop certain diseases, including schizophrenia, and those individuals had different DNA methylation patterns than their siblings. Other factors associated with increased risk for schizophrenia include infections and injury in utero. Today, schizophrenia is suspected to be a neurodevelopmental disorder that follows from some type of disruption during fetal development, as a combination of genetic and environmental factors. However, what those genetic and environmental influences are is not well understood—we still do not have a test that can accurately diagnose the disorder based on genetics, DNA methylation patterns, and/or what happened in utero.

Brain activity (and brain areas) matter

As we move within the molecular neuroscience framework beyond genes and molecules, we arrive next at neurons, neural circuits, and brain activity. The notion that the brain is the type of thing in which functions (like sensation, language, and movement) are located in different parts of it (as opposed to intermingled together) is a very old one. In the early 1800s Franz Gall infamously argued for phrenology: the idea that human personality types could be inferred from the sizes of skull bumps, which reflect brain differences. Other researchers of the period argued that function must be distributed across the brain instead.

Aware of these debates, the surgeon Paul Broca studied patients with a particular deficit: they could not speak but were otherwise intelligent and could understand what was said to them. After looking at the brain of one patient following his death (from other causes), Broca noted a lesion in the frontal cortex, just behind the left eye. Over the next few years, he examined the brains of other patients with the same disorder following their deaths and found lesions in the same location. The region became known as Broca’s area (1861). The neurologist Carl Wernicke (1874) reported on a brain region in which lesions produced a different type of language deficit. Wernicke’s patients maintained the ability to speak, but their understanding of language was impaired. Together, Broca’s and Wernicke’s areas demonstrated that variations of one brain function (language) were localized in the brain.

In the same era, Phineas Gage was working as a foreman for a railroad company when, in 1848, a 3-cm-thick iron rod passed through his eye into his prefrontal cortex. Remarkably, he survived the accident, but his personality changed. He transformed from being friendly and reliable to someone who became (according to his physician) “fitful, irreverent, indulging at times in the grossest profanity, which was not previously his custom.” Modern neuroscience textbooks continue to tell his story—the notion that personality is localized in the brain (insofar as lesions to specific parts of the brain produce specific types of changes) is nearly as profound today as it was more than 175 years ago.

A century later, in the 1950s, the neurosurgeon Wilder Penfield sought to identify the regions of the brain that produce seizures in epileptic patients, and his work carried the side benefit of mapping human brain function. During his procedures, Penfield gave patients a local anesthetic, but they remained awake so they could report their experiences following electrical stimulation to different brain regions. Using this technique, he mapped the somatosensory and motor cortices and discovered that more cortex is devoted to more sensitive body regions (such as the fingers and lips). Penfield also discovered that stimulation of temporal lobe regions can evoke the recollection of memories and the experience of déjà vu. Penfield’s work demonstrated that a diversity of brain functions are localized (at least to the degree that stimulation to particular brain regions could evoke predictable effects). This type of parcellation was later supported by studying the effects of brain damage (like stroke) as well as studies with noninvasive measures of brain activity such as fMRI.

Today, the debate about the localization of function in the brain rages on, with some researchers arguing that the brain is not as localized as many have thought. Instead, these researchers argue that functions are supported by interconnected networks distributed across the brain. A newer generation of analyses seeks to pinpoint those large-scale brain circuits using network-based analyses to identify the networks that work together under different circumstances. These approaches have identified several large-scale brain networks, including the default mode network, which is most activated when subjects focus internally (like when daydreaming). Other examples of brain networks are ones implicated in the deployment of attention, goal-directed behavior, and planning.

What have anatomy and brain activity measures taught us about schizophrenia? One of the most replicable findings in individuals diagnosed with the disorder is a thinning of cortex across many different brain regions (including prefrontal cortex) often accompanied by increased ventricle size. fMRI brain activity measures suggest reductions in activity in some of these same regions, including brain regions associated with working memory function, such as prefrontal cortex. Likewise, estimates of anatomical and functional connectivity between brain regions suggest reductions in connectivity relative to healthy people. Postmortem, the brains of individuals with schizophrenia have ~20% fewer dendritic spines. These measures are not found in all patients; they are trends. They are consistent with the idea that schizophrenia is a disorder that affects brain development. These findings, however, do not shed deeper insights into exactly what causes the disorder or how to treat it.

If schizophrenia follows from environmental and genetic influences in the womb, it’s mysterious why the onset of symptoms does not happen until late adolescence or early adulthood. Presumably, events during fetal development set up a trajectory along a particular developmental path, but no developmental event has clearly been tied to the late onset of symptoms. One hypothesis is that schizophrenia follows when the normal, decades-long developmental process of eliminating extra synaptic connections between neurons happens, but in too much abundance. However, synaptic pruning peaks during childhood, and this hypothesis alone cannot account for the onset of schizophrenia symptoms. Researchers continue to investigate this mystery.

A notable wrinkle: precision medicine

Enthusiasm for the molecular neuroscience framework was reinforced by discoveries of disorders that could be traced back to single-gene mutations, including rare variants of Alzheimer’s (as we saw in chapter 1), Huntington’s disease, and cystic fibrosis. Though not a brain disorder, cystic fibrosis has had a big impact on brain research. The lungs of patients with cystic fibrosis fill with thick fluid, making breathing difficult. In 1989 the cause of the disorder was determined to be mutations in a single gene, CFTR, that creates a protein involved in maintaining the balance of salt and water on body surfaces. Soon after this discovery, researchers developed drugs to enhance the protein’s effectiveness, but initially those drugs were not thought to work. Later, researchers began to design drugs to target specific CFTR genetic mutations. In 2012 the first, ivacaftor, was approved for the 4–5% of patients with one particular mutation. Other drugs for other mutations soon followed. Today, drugs can treat more than 90% of patients with cystic fibrosis. Cystic fibrosis taught us that what appears to be a single disorder can have many underlying causes or subtypes. Designing a patient’s treatment based on their subtype is known as precision medicine.

Disease subtypes do not change the primary goal of brain research, which is still to understand and treat the disordered brain. And yet the existence of subtypes introduces a circular problem that changes everything. To determine the causes of a disorder, researchers typically gather a group of individuals who have the disorder and compare them with those who do not. The goal is to determine a biological marker, or candidate cause, that differentiates the two groups. But before you have a marker, the only way to gather the groups is by their symptoms. And herein lies the problem: precision medicine is built around the idea that the same symptoms arise from many underlying causes. That leads to a chicken-and-egg problem: How can you determine the cause of a disease (chicken) if you cannot even group together (egg) the individuals whose disorder arises from the same cause so you can compare them and discover the cause? It’s circular.

FIGURE 4. The plan for precision medicine. Researchers suspect that patients with similar symptoms have a multitude of underlying causes, and each cause will require a different treatment. The challenge is to identify what those causes are so we can develop treatments for them. The plan for precision medicine begins by measuring biological information (like genetic variation and brain activity) and using that to group individuals into clusters based on these biomarkers—for instance, by noticing that a subset of all individuals have the same genetic mutation. From there, a treatment can be created. Adapted from Insel, T. R., & Cuthbert, B. N. Brain disorders? Precisely. Science 348, 499–500 (2015), with permission from AAAS.

The chicken-and-egg problem applies to many different types of brain disorders, including psychiatric disorders, such as depression, anxiety, schizophrenia, anorexia, and addiction, as well as neurological disorders, such as multiple sclerosis, Parkinson’s, and Alzheimer’s. In all those examples and many others, disease subtypes are suspected. What is the solution? For a long while, the suspected answer was molecular medicine. In broad strokes, the general idea was to gather together patients who have seemingly the same or similar disorders based on their symptoms (like dementia or depression) and find a biomarker, like a genetic mutation, that clustered patients into subgroups within that population (fig. 4). From there, treatments could be created to treat the different causes in each subgroup. This was precisely the agenda that led to tremendous breakthroughs in our ability to treat cystic fibrosis subtypes, as well as multiple types of cancer. This led to tremendous optimism around the idea that precision medicine might extend to all kinds of disorders, including brain disorders. So why hasn’t it worked?

What went wrong with molecular medicine?

The problem is that most brain disorders are vastly more complex than the examples I’ve described. Unlike cystic fibrosis or Huntington’s, which are strongly linked to variation in a single gene, most brain disorders are weakly linked to variation in many genes. The same is true for many types of cancers, including ovarian cancer, which is associated with variation in at least sixteen genes. Still, as long as the number of genes involved remains small, there is some hope that genetic combinations can inform treatments. Brain disorders like schizophrenia and autism, however, are linked not just to tens of genes but to hundreds. Researchers have not yet figured out good ways to interpret or deal with that degree of combinatorial complexity. In addition, understanding how genetic variation leads to brain dysfunction is most straightforward when the genetic variant leads to a mutant protein, but that happens only around 10% of the time. Instead, 90% of genetic variants implicated in these brain disorders occur in regions of the genome that do not code for proteins but instead regulate how other genes are expressed. Understanding how these variants lead to brain dysfunction is considerably more complex.

Another complication is that even when we account for all genetic mutations, we often still cannot accurately predict who will develop a brain disorder versus who will not. Ovarian cancer shares this trait: ~20% of ovarian cancers are linked to genetic variation. As already mentioned, this is also true for schizophrenia, where if one identical twin has it, the chance of the other twin also having it is only 50%. This is because these disorders do not only follow from our genes but from complex interactions between genes and our environment, and we often do not know what those environmental influences are. When a genetic mutation increases the probability that someone will develop a disorder but does not ensure it, this complicates the plan of using that genetic information to develop a treatment. Progress is no longer as straightforward as, say, engineering a mouse with the same mutation to study it.

Taken together, these complications suggest that treating brain disorders will be much more difficult than treating cystic fibrosis. Simply put, brain disorders involve hundreds of genes, and their causes aren’t exclusively genetic. Acknowledging this, the molecular medicine proposal will not be effective for treating most brain disorders. Once regarded as a promising plan, this simple concept of molecular medicine will likely be relevant to only a few disorders with clear genetic links, like Huntington’s. And even in that case, we should not presume that genes operate in simple ways in terms of their interactions with other genes. We no longer have a clear path leading us from genetic variation to new treatments for brain dysfunction.

Where does this leave us? Researchers now better appreciate the enormous gap between genes and brain dysfunction, even when genes are implicated. As captured by the molecular neuroscience framework, genes code for mRNA, which codes for proteins, which create neurons; neurons combine into neural circuits, and activation of the brain’s neural circuits leads to behavioral function and dysfunction. Complexity can enter at each stage. Why would anyone assume that the chasm between genes and dysfunction could easily be crossed in an organ as complex as the brain? As the neurogeneticist Kevin Mitchell observes:

We can’t explain hallucinations or delusions in terms of patterns of gene expression. We can’t even explain the neural pathophysiological states underlying such symptoms in terms of patterns of gene expression. It’s just the wrong level. These states emerge from the trajectories and dynamics of the neural system, over decades of development and experience. Genetic insults at the start may increase the probability of one trajectory or another but they do not underlie or explain the emergent states in any kind of direct or informative way.

So, how to proceed? If genes are too far from brain dysfunction to make any sense of their relation, it’s natural to presume that the problem might be simplified by studying something closer, like brain activity. In parallel to molecules, the idea that signatures of brain activity could be used as biomarkers for brain dysfunction has also elicited tremendous optimism these last few decades. But that hasn’t panned out either.

What went wrong with measures of brain activity?

In the 1980s the optimism around using noninvasive measures of brain activity such as fMRI as biomarkers for disease was tremendous. As expressed by one of the pioneers of that era in 1984, “as they improve and become more accurate, these imaging techniques and other laboratory tests for mental illness will become part of standard medical practice during the coming years, thereby improving the precision of diagnosis and assisting in the search for causes.” The plan was straightforward. First, pinpoint the brain activity patterns that differentiate normal brain function from dysfunction. Next, use that information to develop treatments and cures. The best possible outcome might be a version of precision medicine in which brain scans are used to diagnose and treat individual patients. It seems like a sensible plan. In fact, this plan has to work under the reasonable assumption that all our functions (and dysfunctions) are reflected in brain activity. But that path has also encountered unanticipated roadblocks.

Brain researchers have used fMRI in a number of different ways, and some have been enormously successful. One type focuses on understanding how the average healthy brain is organized. What parts of the brain activate when people remember something? Or plan to speak? To investigate, a typical fMRI experiment compares fMRI activation across two different conditions—for example, to study vision, while looking at a picture versus a blank screen. The researcher then averages these differences in activation across many individuals. This approach is effective for understanding how the human brain is organized. However, it is relevant to inform the causes of brain dysfunction only insofar as it gives researchers a hint about where in the brain they might look.

The second way researchers have used fMRI is more relevant for understanding brain dysfunction. Here, they compare the patterns of brain activation across groups—perhaps a group of patients with the same symptoms versus a group of healthy controls. Using this type of approach, researchers discovered that patients with depression, on average, have lower activation in a region of prefrontal cortex. As described earlier, this approach inspired a groundbreaking new therapy: repetitive transcranial magnetic stimulation (rTMS) targeted to prefrontal cortex as a treatment for depression.

To use fMRI for precision medicine, however, we need to use it in a third way that allows us to make sense of it for individuals, and this is where fMRI has hit a roadblock. Finding that fMRI activation in prefrontal cortex is lower on average when patients are depressed does not necessarily mean you can infer whether an individual patient is depressed based on an fMRI measure of prefrontal activation. The ability to do so depends on the amount of overlap in the depressed and nondepressed groups, and, as it turns out, there’s a lot of overlap. Consequently, you can’t use fMRI brain activation to cleanly diagnose whether an individual is depressed. This is not true just for depression and prefrontal cortex—it’s true for all mental disorders and all brain areas.

Why isn’t fMRI doing a better job of diagnosing individuals? That question has received a lot of attention, and it’s still unclear. It might be a problem of resolution. fMRI measures blood flow as a proxy for neural activity, and it effectively smears together the responses of around a million neurons and brain activity across a few seconds. While researchers continue to push forward on higher resolution and cleverer ways to analyze the data, it’s unclear how far it can be pushed. Another possible complication with fMRI and other measures of brain activity is that the same type of brain dysfunction (like depression) may follow from different types of brain activation in different patients. This could happen if brain functions (like mood) are supported by circuits with many nodes (as opposed to specific brain areas). In this scenario, problems at any node could lead to similar types of dysfunction, and different nodes would be abnormally activated in different individuals with depression. This brings us back to the problem of precision medicine once again. It’s not necessarily a complete road block in principle, but it might be contributing in practice.

To recap, on the whole, neither genetic variation nor brain scans have led us to the causes of brain dysfunction, biological tests to diagnose brain disorders, or insights into treatments. Many researchers question whether these particular measures will be the key to success or whether we need new measures entirely. What is clear is that the naive form of molecular medicine, as it is presented in textbooks, is not the path forward for brain research. The challenge now is figuring out what to replace it with.

Reflecting on history

Taking a step back to mull this history over, we’ve clearly come a long way from the early eras of brain research and their outlandish ideas about what type of thing the brain is, including that it acts as a radiator (to cool the blood) and that it operates via hydraulics. The more contemporary account of the brain as we think of it today can be traced back to a suite of transformational discoveries, most of which happened in the last century. Different eras of that period focused on different parts of the chain, emphasizing the bits they felt “mattered” most to understand brain dysfunction. In that pursuit, most emphasis has been on genes, molecules, and human brain activity (measured with noninvasive techniques like fMRI and EEG).

Looking once more at schizophrenia, as we’ve discussed, today it is suspected to be a neurodevelopmental disorder that follows from some type of disruption during fetal development as a consequence of combined genetic and environmental factors. The gist is broadly consistent with the molecular neuroscience framework, where the environment determines the genes that are expressed as proteins during development, which combine to create neurons and shape neural circuits; in adulthood, the activation of neural circuits leads to schizophrenic symptoms. Beyond these somewhat hand-wavy statements about possibilities, we do not know much about the specifics—we cannot perform a genetic test or use a brain scan to diagnose the disorder.

As described, the bulk of the science feeding into the molecular neuroscience framework was produced by the brain research community across a period of around 50 years. It was a shift away from the idea that most disorders affecting the brain had largely functional (mental) causes. In contrast, in this new framework, all mental disorders are organic brain disorders because all mental processes are biological. In the pursuit of understanding the brain, this era wholeheartedly embraced reductionism. While reductionism need not necessarily lead to oversimplification, a lot of this era of brain research did just that, as exemplified by the idea that a complex phenomenon like depression or psychosis can be entirely chalked up to the amount of certain brain chemicals, produced by the proteins expressed by genes.

How might we think about the role of the molecular neuroscience framework in history? In the mid-1970s the influential philosopher Imre Lakatos described scientific progress as happening through communities that work on research programs that share common principles (a hard core) while working through auxiliary hypotheses. When those core principles shift, the research program shifts as well. Across the twentieth century, psychiatry experienced a shift from a dualistic framework, in which dysfunction could have organic or mental causes, to the molecular neuroscience framework, in which all cases of dysfunction could be traced back to the brain and (in Kandel’s proposal) to genetic expression. While not everyone was on board with this shift, it became the new dominant paradigm in brain research, including research on mental illness, in the 1990s.

Thus far the emphasis on molecules and brain activity has led to an exploding number of new facts about the brain. But we still do not understand the causes of many types of brain dysfunction, and treatments have been sporadic.

While this might all sound a bit bleak, a brighter take is that we are progressing, but things are more difficult than we anticipated. After all, we are wrestling with what some regard as the most complex thing humankind has ever encountered in the universe. Getting it wrong before we get it right is likely a necessary step. But where does that leave us now? If the draft of the Grand Plan, as I’ve described it, does not seem to be working out so well, how should we proceed? In broad strokes, I see two answers to that question.

First, by Kandel’s own admission, the molecular neuroscience framework leaves an enormous gap in explaining how the brain gives rise to mental function. He intentionally left these details unspecified, explaining that filling this gap is “the great challenge.” Indeed, it is imperative that we fill it! How can we begin to explore the potential of brain-based treatments for “depressed mood,” for instance, in the absence of concrete ideas about how the brain gives rise to this mental state? Mainstream depression research has offered some concrete ideas, but they are often pretty crude, such as “depressed mood is caused by less vigorous activity in prefrontal cortex.” More likely, when we experience mood, we are tapping into brain activity distributed across many brain areas—but which ones and how does it work? We still lack good concepts for thinking about this problem.

Second, at all levels, we’ve been oversimplifying ideas about how the brain works, mainly as domino chains. The amyloid hypothesis of Alzheimer’s (presented earlier) is but one example. Thinking about the brain in this way is very intuitive—as humans, we are adept at thinking about things happening in sequence. When systems become more dynamic or multiple things happen in parallel, we tend to struggle a lot more. But we’ve known all along that the brain is chock full of feedforward and feedback loops at all levels and that domino chains are just a simplification. We also know that when a system has both feedforward and feedback interactions, it can behave in surprising, “emergent” ways. As George Box reminds us: “All models are wrong, but some are useful.” We need to ask ourselves: How useful are descriptions of the brain as a domino chain? The facts we have been accumulating may not be the right facts we need to treat brain dysfunction, or at least are an incomplete set. By extension, perhaps it’s time to pause for a moment in the intense effort to pile up bricks in the brickyard (as with the accumulation of more facts about, say, molecules and brain activity) and think a bit more about the edifices we are trying to build. In part 2 I describe how brain researchers might do just that.

PART II What type of thing is the brain?

In discussions of science and how it works, we pay a lot of attention to the role of models and theories and what makes for a good (versus a bad) one. Complementary to that important but well-trodden discussion is a topic that I regard as equally vital but discussed less: How do researchers go about creating a brand new model or theory—one that captures a new way of thinking of what the thing of interest might be like? For this, researchers tap all means of imagination, creativity, and inspiration—wherever they can find it. In the best cases, it leads them to an “aha!” moment of insight. Shifting to thinking in a new way can be the key to unlocking progress.

In the mid-1800s the German chemist August Kekulé was working to understand molecules in terms of the three-dimensional structure of their atoms. One molecule Kekulé was working on was benzene, which we now know is a loop of six carbon atoms; most organic compounds have a benzene ring. But at Kekulé’s time, this was still a mystery. As he worked to figure it out, he liked to take breaks where he would sink into a half-sleep and sometimes visualize atoms fluttering around. In one of these daydreams, “Long lines often fitted together more densely; everything in motion, twisting and turning like snakes. But look, what was that? One of the snakes had seized its own tail, and the figure whirled mockingly before my eyes. I awoke as by a stroke of lightning, and this time, too, I spent the rest of the night working out the consequences of the hypothesis.” That aha! moment sparked Kekulé’s theory that benzene is a chain of carbon atoms configured into a ring. That theory, in turn, led to the synthesis of many benzene derivative compounds, ultimately leading to the ones we use today in medicines such as antihistamines, antipsychotics, and antibiotics.

Like Kekulé, scientists draw their inspiration for what a thing might be like from some other thing. This can include metaphor, where an idea is applied to something that is not directly applicable, such as “thoughts stream.” It can also be an analogy that compares two things: “Like a snake biting its tail, benzene is a ring.” As described by the physicist Robert Oppenheimer, “Analogy is inevitable in human thought because we come to new things in science with what equipment we have, which is how we have learned to think, and above all how we have learned to think about the relatedness of things. We cannot, coming into something new, deal with it except on the basis of the familiar and old-fashioned.” In other words, science is performed by scientists who (like other humans) think and act in particular ways.

In their influential book Metaphors We Live By, George Lakoff and Mark Johnson illustrate how pervasive metaphors are in our everyday lives, especially when discussing abstract things. In those cases, we often rely on metaphors to transform abstraction into something concrete. Consider the abstract concept of an idea and how we talk about it using metaphors of people that we give birth to, father, and spawn; ideas can also be in their infancy and die off. Similarly, when we talk about emotions, we often give them physical orientation: we feel up; our spirits rise; we feel down; we feel low; we even go as far as to call those lows depression. Lakoff and Johnson offer hundreds of examples like these.

They also point out that objectively minded individuals, including scientists, tend to shun metaphors, and this is a mistake. Because our minds naturally tend to think via metaphor, we should embrace this imaginative thinking—what they call imaginative rationality—instead of fear it. Imaginative rationality can be an effective way to approach the first (often undiscussed) step of developing novel and creative scientific ideas—it’s what Kekulé was doing when he spent his time daydreaming. And we can rest assured that once those creative ideas are formulated, the more formal scientific process of testing can kick in, ensuring rigorous science.

In good company with Lakoff and Johnson, the philosopher Mary Hesse has emphasized how pervasive analogy is in scientific thought. “The history of science, in addition to being a progressive discovery of facts, is a history of the various analogies which were believed to be appropriate descriptions of nature in various periods.” In chapter 3 we viewed the history of brain research through this lens, focusing on evolving concepts of the type of thing the brain is. In part 2 we will use the same lens to focus on the present and future, exploring the different and better ways we might think about what the brain might be like to make impactful progress. But before we do that, it’s crucial to remain mindful that while metaphors are an essential first step, they are not the end goal of science. Stopping there can lead science astray.

How metaphors can go awry

While metaphors can be powerful sources of inspiration, they can also veer science off course. One famous illustration was a satirical article published in 1996 by the physicist Alan Sokal, designed to illustrate the flaws of relying on metaphorical arguments alone. In it, he described the cultural and political implications of new work in quantum gravity where “the space-time manifold ceases to exist as an objective physical reality”; consequently, he argued, we can conclude that quantum gravity is a social construct. What?! Sokal intentionally wrote the article to make no sense but to mimic a particular metaphorical style reflected in other publications. Once the paper was accepted to a journal (in cultural studies), he revealed the hoax. Nonsensical comparisons between things and other things are not the path forward for any field, including brain research.

More subtly, metaphors became problematic in a slice of computer science focused on creating better ways to optimize and learn from data, optimization metaheuristics. Around 2000 the subfield began to draw inspiration for new algorithms using metaphors from nature. One of the first papers focused on how antibodies work, the clonal selection algorithm. Soon after, a new evolutionary algorithm based on sheep flocks followed. And then the field exploded with metaphors: bachelors, bacteria, barnacles, bats, bees, beetles, the big bang, birds, bison, black widow spiders, blind naked mole rats, bonobos, butterflies, and buzzards were all thrown into the mix (and those are just the B’s!). As of 2021 a website focused on collecting instances like these, titled the Evolutionary Computation Bestiary, listed a remarkable 260 unique examples of peer-reviewed, published papers in this field.

New ideas are good, right? So why was this metaphorical explosion a problem? In this case, the problem was that it quickly became unclear whether and how all these algorithms fit together. While each paper claimed to present a unique approach, metaphor-heavy language presented an obstacle to discerning whether two published algorithms were the same or different. When held up to closer scrutiny, it turned out that many of the algorithms were novel only with regard to the metaphor that they were attached to; the algorithms themselves were the same as (or a special case of) already published ones: the black hole algorithm turned out to be a simplified version of particle swarm optimization; the grey wolf, firefly, and bat algorithms did as well.

One lesson we can apply to brain research is that metaphors are not the goal of research; the goal is models (the analogs of the algorithms in this computer science subfield). This lesson has two important consequences. First, metaphors, “word models,” and ways of thinking about things in broad strokes must be explicitly formulated as falsifiable models (and, in turn, hypotheses) so that researchers can test their validity. In the words of Wolfgang Pauli, a model or theory that cannot be assessed is “not even wrong.” A metaphor of the brain is precisely this. It ultimately needs to be formulated as a model, most often formalized as mathematical equations. If we fail to take this last step, we risk running in circles trying to test the validity of a metaphor that cannot be tested. Second, when researchers formulate a new model, they are beholden to make a good-faith effort to map its equivalencies to existing ones. Suppose one researcher uses the “firefly” metaphor to inspire a model, but it is mathematically equivalent to an already existing model inspired by “bats.” In that case, there’s no net contribution there. And when models are mathematically different, they should make different predictions so researchers can determine which is more correct.

While we need to keep our eye on the prize of models and theories, thinking about what the brain might be like is an essential first step we should not overlook. Shifts in how we think about it—Copernican insights—may be the spark that triggers the impactful progress we so desperately need.

Chasing Copernican insights

In ancient Greece, philosophers contemplating how the planets move through the universe argued about whether the sun revolved around Earth or vice-versa. Aristotle (~350 BCE) championed the notion that Earth is the center of the universe, and that idea would dominate thinking for nearly two thousand years. There was one observation, however, that did not quite fit with Aristotle’s Earth-centered account and needed to be reconciled. From an Earth-centered perspective, planets like Mercury move in one direction across the sky and then reverse course for a short time before they once again move in their original direction. To account for these trajectories, Ptolemy (150 CE) put forward a proposal with numerous hacks, including that each planet traveled around Earth along a large cycle, and that each planet rotates around a smaller epicycle. While a bit wonky, Ptolemy’s model was quite good at predicting the planets’ future positions in Earth’s sky, and it persisted.

In the mid-1500s Nicolaus Copernicus became suspicious of Ptolemy’s account, guided by an intuition that the model wasn’t quite right. He began to consider “whether there could perhaps be found a more reasonable arrangement of circles, from which … everything in itself would move uniformly.” Driven by that intuition, he developed an exceptionally provocative suggestion for his era: that the planets travel in circles, not around Earth but around the sun. In this sun-centered arrangement, the apparent reversal in trajectories across the sky is due to viewing them from Earth (which moves along its own trajectory).

This shift in thinking about what planetary motion might be like turned out to be the key to unlocking progress. Inspired by Copernicus’s proposal, Johannes Kepler used the carefully collected data of his mentor, Tycho Brahe, to work out a sun-centered, mathematical model of the elliptical trajectories of the planets. Kepler demonstrated that there is a precise relationship between how far a planet is from the sun and the amount of time it takes for that planet to revolve around it. That model, in turn, inspired Isaac Newton in the 1600s to question why the planets move in this way, leading him to the suggestion that a physical force called gravity pulls objects proportional to their mass. Newton’s model provided a prediction of where the planets would be at any time and an explanation of why they moved that way. Today, we continue to use Newtonian physics to describe gravity for everyday purposes (as opposed to, say, what will happen near a black hole).

When I consider the state of brain research today, I suspect that some subfields, including anxiety and depression, are waiting for their Copernican moment. As we will discuss, one influential idea about the brain is that it is a type of information-processing machine that computes. The metaphor of the brain as a computer is a crucial step toward understanding how the brain gives rise to the mind and to behavior, and it has been tremendously successful at helping us understand some things about the brain—like how vision and memory work—and helping us to build artificial intelligence. Ultimately, however, the computer metaphor falls short because it’s not a great way to think about what anxiety or depression might be like. When we focus on the computation of something, we presume that computation is a process with an end goal, of moving from one state to another. Analogously, we can presume that the brain “computes anxiousness,” but we are left wondering: To what end? What problem is the brain trying to solve when it performs this computation? Is the “computation” of anxiety really the right way to think about it? It certainly feels more Ptolemaic than Copernican, and I suspect that I’m not the only one left wondering whether there could perhaps be found a more reasonable arrangement.

Put another way, the gap between the brain-as-a-computer metaphor and the lived experience of patients with anxiety and depression is vast and intimidating. I worry that the computer metaphor helps us begin to build the bridge we need, but alone, it cannot completely traverse that gap. This is true not only for anxiety but also for many other functions of the brain and mind that tend to go awry. Thinking about insomnia, epilepsy, anorexia, autism, or schizophrenia as a deficit in “computation” strikes me as the wrong way to think about the problem from the outset.

There probably won’t be a one-size-fits-all way to think about what all the brain’s functions (and dysfunctions) might be like. But what are the alternatives? Let’s begin with the idea of the brain as a computer, to see what it has to offer (and where it falls short).

CHAPTER 4 Is your brain a computer?

The idea of the brain as a computer—an information-processing machine that computes—is a pervasive one. The gist is that the brain receives information via its senses and then performs computations to determine how the body it’s linked to should behave. To achieve this, it relies on flexible processing modules such as perception, memory, attention, language, and decision-making.

The idea of the brain as a computer can help us understand how the brain and mind are related. In this metaphor, the brain is something akin to the hardware, and the mind is produced from the software it runs. All mental function is thus mediated by the brain. That is, some might suspect that mental function emerges from brain function, but changes in the mind cannot happen without physical changes in the brain.

Thinking about the relationship between the brain and the mind is a crucial step toward understanding the causes of many types of dysfunction, including mental disorders. After all, when we say that we want to understand something about the brain or its dysfunction, what is it that we want to know? Consider attention deficit hyperactivity disorder (ADHD), which is defined by difficulty paying attention. To figure out why that happens, we might begin by describing how the brains of individuals diagnosed with ADHD differ from others on a very big scale, such as the network of brain areas involved. But alone, a list of brain areas is pretty unsatisfying. Alternatively, we might focus instead on a very small scale to understand how medications for ADHD (like Ritalin) change neurotransmission in the synapse. But with that description, we are also left wanting: How does changing synaptic transmission change our ability to focus? It’s akin to explaining the wonders of how children rapidly learn language in terms of ion channels. Ion channels might be involved, but how do they contribute to language? In other words, there’s an enormous gap in this explanation, and one that won’t be filled by adding in descriptions of the biology at intermediate scales. For instance, even if we could pinpoint the specific neural circuits and the specific types of neurons involved in attention, we still would not have a satisfactory explanation of how attention works. Mapping the biological phenomenon is not enough. So what then are we looking for when we say we want to understand how the brain produces something like attentional focus (and how focus is disrupted in ADHD)?

In the 1970s researchers were struggling with this type of question, but in the context of vision. In that era researchers had discovered neurons in the visual system that were activated only when a particular body part, such as a face or a hand, was in view. This naturally led to the idea that our perceptual experience of faces, hands, and such happens when these highly selective neurons fire. While this was a remarkable discovery, the computational neuroscientist David Marr was among those struggling with the idea that this was a satisfying account of how we see. Marr explained that while discovering neurons that selectively respond to faces or hands is intriguing, alone it does not provide us with enough understanding to program a computer to build a face or hand detector. It’s a description of what the brain does but not an explanation of how it does it. An explanation of vision would detail how those body part neurons are created as visual input passes through the different brain areas that make up the visual system, starting in the eye. In other words, it would show us how the visual system “computes.”

As Marr worked through these ideas, he converged on the proposal that a complete explanation of anything that the brain does requires descriptions at each of three levels that I will refer to as why, what, and how.a At the top, descriptions of why focus on the thing that needs explaining, including the problem that an individual is trying to solve (such as seeing and identifying a face) and good ways to go about it. Descriptions of behavior fall at this level. One level down, descriptions of what typically focus on what the brain is doing—what each part is computing. In the case of vision, a what-level description would capture the computations performed by each part of the visual system to construct a neuron that responds selectively to a face. Finally, descriptions of how focus on the way in which those computations are implemented in the biological machinery of the brain, including the neural circuits, individual neurons, and molecular cascades involved.

These ideas are part of larger, clear-headed ways to think about what researchers call levels and mechanisms. The gist is that different types of explanations—such as what is happening with chemicals in the brain versus mental states—exist at different levels of explanation that are not just levels of scale but rather explanations of different types. The overarching goal, broadly construed, is to explain what is happening at each level and how they all connect. And that’s where the notion of the brain as a computer comes in—it’s the “what-level” bridge between how phenomena manifest in the brain and why those phenomena lead to the mind and behavior. In this chapter we’ll begin by focusing on what the notion of the brain as a computer entails, and then we’ll explore its potential for helping us understand brain dysfunction, including ADHD and psychotic delusions.

Is the idea of the brain as a computer a metaphor, a model, or reality?

Keeping our eye on the prize, let’s remember that what brain research is ultimately after are falsifiable models that capture what happens and theories that explain why. Is that what the idea of the brain as a computer is? It sometimes seems like the notion is not quite a model but rather a metaphor for the type of thing the brain is a bit like. At the other extreme, it might be a truism or, equivalently, a description of what the brain must be. In brain research, the notion of the brain as a computer has served (and continues to serve) as all three of these things in different scenarios, depending on the details of how researchers define it.

The metaphor of the brain as a computer has been applied most extensively in the sequential computer sense. Here, the idea is that the brain is a type of thing that accepts input (via the senses) and produces output (behavior), and the transformations between them happen via a step-by-step process. But along the way, all sorts of interesting and flexible, mind-like computations can occur via the operations of cognitive modules (including vision, audition, attention, memory, and decision-making). The operations of these modules are often thought of as sequential and, for the most part, independent, meaning that one completes its job and hands the answer to another module to perform its operations.

Thinking about the brain this way is very intuitive. Consequently, in the absence of obvious reasons as to why they should do otherwise, brain researchers have naturally adopted this thinking to guide their research. Here, when accounting for any brain function (like seeing or hearing), it’s not sufficient to pinpoint what brain areas (visual or auditory) information passes through; one also needs to know what those brain areas are computing and how they are computing it. Brain researchers who think this way acknowledge that it’s a simplification: they know that the brain doesn’t simply process sensory input to determine output; instead, it controls a body that dynamically interacts with the world to achieve specific goals (like catching a ball). It’s a simplification that emphasizes some aspects of reality while ignoring others.

When the idea that the brain is a computer is adopted in a way that is not formalized into a mathematical model, researchers are using it as a metaphor. Thinking about the brain this way has been tremendously impactful insofar as it has led to models of how the brain works. The year 1943 marked a turning point in thinking about one particularly pervasive model, artificial neural networks. Before then, computing (such as adding numbers) was considered one activity among many others that humans performed, such as cooking, walking, or talking. After 1943 computing shifted to the thing that the brain does to support all its functions. This transformation was the result of highly influential work by two neuroscientists, Warren McCulloch and Walter Pitts.

According to McCulloch and Pitts, networks of model neurons are capable of operations that flip between two states, active and silent, a property called all or none firing. These flips reflect the binary outcomes—true (active) versus false (silent)—of logical operations such as AND and OR (fig. 5a). McCulloch and Pitts demonstrated how simple model neural circuits can compute these logical operations, and simple operations can combine to perform more complex computations. In reality, neurons in the brain are extremely complex. The elegance of McCulloch and Pitts’s work is the illustration of how vastly simplified versions of these complex entities networked together can be powerful.

The “deep” artificial neural networks that serve as models of the brain today include many layers of neurons inspired by McCulloch and Pitts (fig. 5b). They also include one additional core element: they learn to do whatever needs to be done. The model neurons begin randomly connected, and they then learn to perform specific tasks through an iterative procedure that adjusts those connections (often based on feedback from a tutor). Obviously, real brains learn too. But in a brain, it happens a bit differently: connections between neurons are adjusted via combinations of hard-wired genetic information, our experience during development, and learning in adulthood (both via explicit feedback from tutors and in other ways). But ultimately, the end-goal is the same: a real or artificial neural network that can “compute.”

One striking example of the idea of the brain as a computer followed a breakthrough in computer vision circa 2012. There, researchers trained an artificial neural network called AlexNet to report which objects appeared in photographs, and it did so much more successfully than any model that came before it.b In turn, brain researchers noticed that AlexNet and other artificial neural networks like it looked a lot like the organization of the visual system in the human (and monkey) brain. While the models continue to be refined, this class of models remains state-of-the-art because they often predict human brain activity better than any other model. Since their discovery, similar approaches have been used to model how the brain does other things, like hear and remember. These neural networks are thus mathematical formulations of the notion that the brain operates as a computer, and they serve as models of the brain whose validity can be tested (and refined).

FIGURE 5. Artificial neural networks. a) The two types of neurons introduced by McCulloch and Pitts. Here, a check reflects a model neuron that is “active” and an x reflects a model neuron that is “inactive.” The first type is activated only when both its inputs are (when 1 AND 2 are active). The second type is activated when either of its inputs is (when 1 OR 2 is active). b) Modern “deep” neural networks consist of many layers of artificial neurons of the types inspired by McCulloch and Pitts. As depicted here, many of these models of the brain are purely feed forward and operate via domino chains.

Finally, the reality of the brain as a computer follows the definition of computer not as I’ve described it thus far, but instead as adopted by computer scientists. Here, a computer is defined as a physical machine that can, in theory, compute any computable function. The idea originated with the mathematicians Alonzo Church and Alan Turing and the notion that an algorithm is a problem that can be solved by an abstract computational device that manipulates symbols according to a set of rules, a Turing machine. According to this definition, some argue that the brain is literally a computer; this is not a metaphor but an inevitable reality. Others counter that because real-world problems like “thrive in your current situation” cannot be broken down into computable functions and yet the brain still figures out how to solve them, it is not a computer. This debate remains unresolved.

One important thing to note is that even if we were to adopt the notion that the brain is the type of thing that can in principle compute anything, this idea is so broad that it’s not very helpful for moving brain research forward. Minimally, we need to ask and answer: What type of computer is the brain? In other words, even if true, the reality of the brain as a computer is so broad that we need to narrow it to make it a testable, tractable model. At the other extreme, the metaphor of the brain as a computer must be formalized into a falsifiable prediction to be tested. In between those extremes, the notion of the brain as a sequential computer has inspired mathematical models of the brain through interactions between brain research and computer science.

How can those types of models help us understand brain dysfunction like ADHD?

Filling in the gap between the brain and mind for attention

To illustrate how the general notion of the brain as a computer can be helpful, let’s return to what we know about how pharmaceutical drugs work. We often know something about their effects at the molecular level, but we need to understand how those effects lead to changes in brain function and behavior. For instance, many antidepressants elevate levels of neurotransmitters like serotonin and norepinephrine in the synapse, which presumably affects brain activity in some way, but how exactly, and how does that change mood? Antipsychotic drugs block dopamine receptors, but how does that shift an individual from psychosis to sanity? Some drugs for insomnia bind to receptors involved in making us feel sleepy, whereas others block the receptors involved in keeping us awake—but how does that lead to sleep? Building on a rich and elaborate history, brain drug development has almost exclusively focused on targeting what is happening at the molecular level to change what’s happening at the level of symptoms and behavior. Molecules are the targets of drugs, so understanding the brain at the level of molecules makes sense. But we don’t understand how many of the drugs that we have operate at the what-level—how targeting molecules leads to changes in symptoms. Could filling that knowledge gap lead to new insights that might reinvigorate brain drug development? That seems plausible. But how do we go about making those links? For insight, let’s look at one recent success story: attention and the drug methylphenidate (Ritalin).

Attention deficit hyperactivity disorder affects around 8% of all children and 3% of adults. While impulsivity and difficulties paying attention are a normal part of being a child, individuals with ADHD struggle with these much more than others at the same developmental level. It can interfere with their ability to learn at school and their relationships with family and friends. Some regard ADHD as a type of neurodiversity in which the attentional struggles accompany other benefits, including high levels of passion, drive, and creative thinking. However, it can also lead to problems, such as severe insomnia and an inability to interact with others. For individuals who opt for treatment, one option is behavioral therapy to help with focus. Another is psychostimulant drugs, including Ritalin and amphetamine (Adderall).

Like many of the drugs we’ve discussed so far, Ritalin is an old drug, synthesized in 1944 by a chemist at the Swiss pharmaceutical company CIBA (now Novartis). To test the drug’s effectiveness, the chemist tried it on himself and his wife Rita, who liked it because the ability to focus intensely made her a better tennis player. In honor of his wife, he named it “Rita’lin.” Today, more than 2 million people in the United States use Ritalin annually—many to treat ADHD, but others without a diagnosis (most often college students, for studying). In the early 1970s researchers determined that it operates by blocking the reuptake of norepinephrine and dopamine, leading to higher levels of these neurotransmitters in the synapse. But how does that help an individual pay attention? There’s a big what-level gap in explanation there. How do we fill it?

Understanding how Ritalin works begins by understanding what happens in the brain when you deploy your attentional focus. To get a sense of what that means, take a moment to deploy your own, shifting your attention to different locations without moving your eyes. Begin by looking straight ahead and fixate on something. While maintaining fixation, shift your attention to the right side of your gaze and then to the left. As your attention shifts, you will become more aware of the things on the attended side and less aware of the things on the opposite side. This type of attention is called covert because you can secretly move it around without anyone knowing you’re doing so. It’s important for species where eye contact is a form of aggression (like macaque monkeys). It allows them to home in on what’s happening without shifting their gaze.

A popular way to study covert attention is via a task in which an individual fixates, and two streams of flashing bars appear, one on each side of the person’s gaze (fig. 6a). The participant’s task is to report when the orientation of the bar changes. The difficulty of the task can be titrated from hard to easy by adjusting the magnitude of the change from subtle (90 versus 80 degrees) to obvious (90 versus 60 degrees). Attention comes into the mix with a cue that indicates the side where the change is most likely to appear (on 80% of trials; fig. 6b, top). While participants continue to look straight ahead, they deploy their covert attention to the cued location. As you would expect, participants are more sensitive to detecting a change on the side they are attending to versus on the side they are not. Ritalin boosts attention, enhancing performance even further on the attended side. What is happening in the brain when a participant deploys their attention? And how does Ritalin enhance an individual’s ability to do that?

Behavior in this covert-attention task occupies Marr’s why level. It is the thing that lower levels need to explain. In this case, it’s described as better performance for detecting a change on the side where attention is deployed. At the what level, the goal is an algorithm that links covert attention behavior with what is happening in the brain; it’s a description of what the brain is computing and how it’s computing it. In this task, detecting when a change happens requires comparing the stimulus currently in view with a memory of the one that came before it to determine if it changed.

Researchers think about filling the gap between the brain and behavior in an abstract but ultimately helpful way. The gist is that both the stimulus in view and memory of the last stimulus are reflected in the brain in a “noisy” way, and attention reduces that noise; Ritalin works to enhance that noise reduction even more.

FIGURE 6. Attention at Marr’s why and what levels. a) In this change-detection task, the participant looks straight ahead while trying to detect when one of two flashing bars changes orientation. The task can be titrated from difficult to easy by changing the magnitude of the orientation change. b) Top: Before the trial begins, the participant gets a cue about the side that the change will most likely appear on so they can shift their attention to it (dashed circle). Participants are better at detecting changes on the attended side. Bottom: A what-level, algorithmic model for this task proposes that an individual taps into a noisy internal signal to determine whether a change happened based on the strength of the signal relative to a threshold. In the unattended condition, the internal signal is noisier, and when a change happens (“yes”), more of the internal signal will spill over to the wrong side of the threshold; on those trials, participants will not detect the change. In the attended condition, the internal signal is less noisy, and participants will detect the change more often.

To unpack that a bit more, researchers call the noisy reflection of a stimulus in our minds an internal signal. Because these reflections are noisy, they amount to Gaussianc distributions where more noise translates to fatter Gaussians. The idea is that because this task involves comparing the stimulus in view with your memory of the last stimulus, you can think about this task as answering the question (with each flash), “Did the stimulus change?” where one Gaussian reflects the answer “yes” and the other “no” (fig. 6b, bottom). To decide, you take a random draw from one of those Gaussians—if it did not change, the “no” one; if it did change, the “yes” one. Finally, you see where that draw falls relative to a threshold that separates them. What this means is that when there is more noise (like in the unattended condition), more of the Gaussians will spill over to the wrong side of the threshold, and you’ll be more likely to get the answer wrong. Conversely, when there is less noise (like in the attended condition), you’ll perform the task better.

In this framework, attention operates in a pretty straightforward way—by making the brain’s noisy responses to different images less overlapping (thereby increasing performance). This abstract framework is helpful because it can be linked to what is happening in the brain. But those links don’t jump all the way to norepinephrine in the synapse but rather focus on brain activity to pinpoint where this abstract signal resides. One of the most exciting developments in brain research across the past few decades has been creating new ways to think about what that abstract signal might be. New technologies, which emerged in the early 2000s, allowed researchers to record from large numbers of individual neurons simultaneously. In many cases, including attention, you can think of this technology as linking the brain (Marr’s how) with the algorithm (Marr’s what, which is linked to Marr’s why). They provide us with the link we are most hungry for—a description of how what’s happening in the brain leads to the mind and behavior.

The answer to the question, “How does the brain pay attention?” involves a type of brain noise shared between different neurons. This noise can be observed by repeating the same stimulus again and again. Across repeated trials, individual neurons are not activated in the same way, but their activity is noisy insofar as it varies a little across trials. On some trials, a neuron will be activated a little more than its average, and on others, it will be activated a little less. Shared noise happens when the activity fluctuations in different neurons go up and down together (if one neuron is activated a little more than average on one trial, another neuron will be, too). Uncorrelated noise happens when the activity fluctuations in different neurons all occur independently.

Uncorrelated noise is the best type because when it happens, the brain can get rid of it by averaging the activations of all the neurons together. If the noise is correlated, however, the brain cannot eliminate it by averaging. Understanding this was the critical insight for determining how attention works: attention decorrelates noise at the location where it is deployed, allowing the noise to be averaged out, thereby eliminating it. This, in turn, enhances the distinctiveness of a stimulus when it changes. In sum, attention works at Marr’s what level by increasing distinctiveness, and this happens at Marr’s how level by the brain’s decorrelation of noisy responses.

What causes noise decorrelation in the visual system? It’s most likely controlled by prefrontal cortex, which resides at a higher level of processing than the visual system and reaches back to perturb how it operates. And it is in prefrontal cortex where Ritalin is thought to act—by enhancing its feedback to the visual system, possibly by increasing the levels of norepinephrine in prefrontal synapses. When Ritalin is administered to monkeys, like humans, they perform better on the covert visual attention task. Moreover, day by day, the degree of their improvement is predictable by the degree of decorrelation measured in the visual system, demonstrating the link between them. In sum, building on a nuts-and-bolts understanding of how attention works, we also understand the way that Ritalin works in terms of why (to increase the effects of attention), what (by enhancing distinctiveness of stimuli at the attended location), and how (by reducing correlated brain noise in the visual system, which most likely happens by enhancing feedback from prefrontal cortex through a process that increases norepinephrine).

Filling in the what-level knowledge gap for Ritalin between the molecular and behavioral levels provides an important proof of concept that the algorithm by which brain drugs act can be described in a meaningful way. Descriptions of what is happening in the brain in terms of its activity can be linked to behavior and dysfunction, and they are a more natural place to begin thinking about the most mysterious neuropsychiatric disorders, such as depression and schizophrenia. We know of many brain drugs that work, but we need to understand how they affect what populations of neurons reflect and compute. The insights also lead to the tantalizing idea that future drug discovery might focus not just on the molecular level but also on how drugs affect brain activity viewed through an information processing lens. Given that so many drug companies collectively abandoned the brain-drug-discovery effort around 2011, one can only wonder: Is an integrated, multilevel understanding what is needed to reinvigorate drug development?

Can the idea of the brain as a computer help us understand psychosis?

How do we even begin to think about psychotic delusions? In her book The Collected Schizophrenias, Esmé Weijun Wang describes monthslong bouts of psychosis where she “feels like breaking through a thin barrier to another world that sways and bucks and won’t throw me back through again, no matter how many pills I swallow or how much I struggle to return.” During those periods she has experienced incredibly specific delusions like the realization that her coworkers had been replaced by robots. For a period she also believed that she was dead. Wang’s experience is both heartbreaking and terrifying. We must find ways to help her and other individuals like her. And yet the chasm between what we understand now and a true understanding of what causes these delusions seems so vast. To cross it, we will need clear-headed ideas about what we are looking for and how to proceed. Can the notion of the brain as an information-processing machine that computes help?

Psychotic episodes can involve hallucinations, like hearing voices. They can also include delusions like the ones Wang experienced. As described earlier, antipsychotic drugs block dopamine receptors. While all existing antipsychotics block a specific type of dopamine receptor (D2), it’s unclear how that alleviates psychotic episodes; there’s a big gap in explanation there. And that gap lies right at the heart of the big mysteries about the brain that we are eager to understand: the precipice between sanity and psychosis.

The different types of psychotic delusions probably involve different systems in the brain that are only partially overlapping. A collection of delusions known as misidentification syndromes are among the most baffling in all of brain research. In Capgras syndrome, a patient believes that an imposter has replaced one or more individuals around them. In Fregoli syndrome, a stranger is believed to be a familiar person disguised. These delusions are not limited to people but can involve imposter pets and imposter homes. As Esmé Wang explains, during her episode of Capgras, she unflinchingly believed that robots had replaced her coworkers but also understood that her beliefs were supposed to be a consequence of psychosis. What was happening in her brain at that time?

In 1923, along with his assistant J. Reboul-Lachaux, the French physician Joseph Capgras first described the syndrome that later bore his name. Following the death of her twin sons in 1906, a woman claimed that her husband had been murdered and replaced by one among a rotating set of eighty imposters. She wanted to divorce the double(s) and requested a separation from the courts. She also claimed that many others around Paris were doubles as well. Those imposter delusions were accompanied by delusions of grandeur in which she believed herself immensely rich and from an influential family. She also suffered from delusions of persecution in which she thought someone wanted to poison her and was trying to abduct her for her wealth.

Capgras speculated that his patient had a disturbance in her ability to recognize familiar people. He noted that when you encounter someone you haven’t seen in a while, it is sometimes a struggle to identify them, and he reasoned that a deficit in the recognition system was at fault in this case. He noted that his patient did not have a distortion in her ability to see or remember who was familiar to her, but strangeness accompanied that ordinary sense of familiarity. Those ideas were an insightful start, consistent with how we think about Capgras today.

Across the next century, several theories about the Capgras delusion followed—many of which were less helpful than Capgras’s initial observations. As recently as 1983, one researcher argued against the idea of a biological cause for Capgras with the rationale that no brain lesion could lead to such a specific effect as believing that only specific people are imposters. Instead, he proposed that Capgras syndrome reflects previously repressed feelings that are internalized unconsciously; when those feelings are triggered, they surface into awareness as the belief that their significant other is a double. He suggested that those who treat individuals with Capgras “seek data about early mother-child interactions.” Unsurprisingly, other researchers expressed strong disagreement with the notion that Capgras did not have a biological cause. But what might that cause be?

When viewed through the lens of Marr’s levels, the delusion exists at the level of why—it’s the mental state to explain. One level down, what type of algorithm or computation might be involved? In the case of Capgras, the imposters are people or things familiar to someone, which naturally leads to the idea that Capgras himself first proposed: that it has something to do with personal familiarity. Capgras symptoms also connect with the belief of an imposter that persists despite contradictory evidence, suggesting that it involves some type of belief system. In a wave of debated proposals, researchers discussed whether personal familiarity and familiarity belief were two different computations in different parts of the brain that could each go awry independently (called “factors” by these and other researchers) or a single computation in which familiarity and belief are intertwined in the same part of the brain. In other words, is personal familiarity computed by the brain independently of, and presumably before, familiarity belief in a different location?

The idea is that if familiarity belief is the outcome of two sequential computations in different regions (personal familiarity and then belief), patients with deficits in just the first computation (familiarity) as well as those with deficits in just the second (familiarity belief) should both exist. The debates came down to four patients with deficits in detecting familiar faces but not Capgras delusions, and discussions about whether the deficits in those patients were limited to personal familiarity or more extensively reflected perceptual deficits. The gist of the debate was that those patients could be more trivially explained as having deficits not just in detecting familiar faces but in responding to visual input more broadly—analogous to the idea that without eyes, you also can’t detect visual familiarity, but that does not mean that the eye computes familiarity (rather, it’s a bottleneck that visual information must pass through). With the data from these four patients alone, it was unclear.

In 2017 one group of researchers focused on the how level to determine the brain regions that might be responsible for Capgras. They found several cases of patients with Capgras in the literature, along with the locations of their brain lesions (identified using anatomical MRI). But the lesion locations appeared to happen with little rhyme or reason. To investigate, they used a clever paradigm they had developed called lesion-network mapping. This technique enables researchers to test the hypothesis that symptoms emerge from sites functionally connected to a lesion location, not just the lesion location itself. The broader idea is that functions are supported not by individual brain areas but by networks, and disruptions at different network nodes can lead to functional deficits.

To pinpoint the brain areas that might be affected consistently across all patients, the researchers found seventeen cases (fifteen in the published literature and two from their own clinic), which led them to seventeen brain lesions. Next, in healthy controls, they determined the parts of the brain most strongly functionally connected to those lesioned areas, and they identified the brain regions connected with the greatest number of lesion locations. Through this procedure, they found that one brain area implicated in personal memory and familiarity—left retrosplenial cortex—was functionally connected with all seventeen lesion locations. Another brain area implicated in belief and detecting violations of expectation—right ventral frontal cortex/anterior insular cortex—was functionally connected with sixteen of seventeen lesion sites. Other types of (persecution) delusions were also functionally connected to the brain area involved in belief but not to the area involved in familiarity. Together, these results lead to the conclusion that two factors are implicated in Capgras, not just one.

To summarize what we’ve discussed thus far about Capgras in terms of levels, at the top why level are descriptions of normal behavior: I remember my loved ones, and they are themselves; and the Capgras delusion: imposters have replaced my loved ones. At the what level, two computations are implicated: one for familiarity and another for belief, including detecting violations of expectations. These two computations are linked to two distinct brain regions at the lower how level. One region is connected to familiarity because it has stronger fMRI activation when viewing personally familiar things. The other is linked to violations of expectation because it has stronger fMRI activation when they happen versus when they do not. At an even lower how level, we also know that antipsychotics can alleviate the delusion in some cases, and that these drugs block the dopamine D2 receptor. The field has made nontrivial progress in understanding the imposter delusion since Joseph Capgras first described it in 1923.

That said, these ideas about Capgras may need refinement. Some researchers who study the delusion, including Phil Corlett, promote theories in which delusions follow from computations that are anatomically intertwined because they are shaped by reciprocal feedforward and feedback connections in the brain. “If we allow for feedforward computations about familiarity and surprises related to it (such as ‘That’s not my wife!’) which reach up to affect belief, as well as feed back down from belief to familiarity, then delusions may follow from deficits anywhere in the hierarchy—there is no need to imagine separate familiarity and belief gadgets that are broken independently.” Indeed, the profound implications of thinking not just about feedforward processing but also feedback in the brain is the focus of the next chapter.

Irrespective of whether feedback is involved in shaping the Capgras delusion, a gap remains between dopamine receptors and the brain areas implicated in familiarity and belief. In other words, we still do not yet know: What is happening in those brain areas implicated in the delusion? What types of information do these brain areas receive, and what do they do with it? Are personal familiarity memories stored in retrosplenial cortex, or is that brain area doing something else? Is anterior insular cortex computing violations of expectation by comparing what happens with what is expected? Or is that computed somewhere else, and this region acts like a relay station that all belief information passes through? And how do antipsychotics, by blocking dopamine receptors, influence what these brain areas do?

While these questions are difficult to answer in humans, they are much more tractable in animal models (which is also how we came to understand attention and how Ritalin works). In animal models, researchers can record brain activity at the exquisite spatial and temporal resolution required to understand what is happening in these brain areas and the others connected to them. They can also causally perturb the system to dissociate correlation from causation. We know very little about the functions of the two brain areas implicated in the Capgras delusion (retrosplenial and anterior insular cortex) because very few studies have been performed there. We also need to learn more about the relationship between these brain areas and dopamine. Clear-headed thinking about levels identifies this as a gap we must fill.

When researchers turn to trying to understand those brain areas, how should they go about it? Those brain areas are undoubtedly doing all sorts of things and can be investigated in all sorts of ways. To understand how these brain areas contribute to the Capgras delusion, researchers need to study the subset of computations that best relate to Capgras, including their roles in personal familiarity and belief. The idea might seem obvious (and even essential) that work in humans and animals should co-align and inspire each other to create mappable understanding across different levels of explanation; however, many things stand in the way. So many that a name has been assigned to facilitate the call: interactionist neuroscience. It’s hard to pull off for several reasons—for instance, it’s easier to study mouse-like things in mice, and it does not always immediately make sense to study mouse-like things in humans. However, it’s the most direct route for the integrated, multilevel answers to the big mysteries about the brain that we are most desperate to know. As such, we must ensure that the subset of brain researchers inspired to pursue it can do it. It’s the most viable path forward for understanding how Capgras delusions happen and developing new treatments for individuals like Esmé Wang.

Dispelling confusion about levels and causality

The history of brain research is peppered with confusion about levels and its relationship to “What causes what?” First among such confusion is a big question that we touched on earlier: whether “mental disorders” should be regarded as “brain disorders.” There tends to be a lot of murkiness involved in this question, but it’s a case in which clear-headed thinking about levels can really help pinpoint what the issues are.

The first thing to understand about this debate is that, today, all sides generally agree that the brain mediates mental function. Some might suspect that mental function emerges from brain function (in ways for which the whole cannot be attributed in a simple way to the operation of its parts in isolation), but everyone generally agrees that changes in the mind cannot happen without physical changes in the brain. This is thus not generally a debate about whether a nonmaterial soul contributes to mental function. Rather, the issue comes down to discussing the best level to explain and intervene with dysfunction: Is it the brain, the mind, or some combination of them?

To illustrate what the debate is all about, consider the phrase “insomnia causes fatigue.” We can all agree that the brain mediates this causal chain. Namely, the brain needs sleep to prevent it from entering the brain state that produces the mental state of fatigue. We can also agree that, in this case, thinking about the brain and all its complexity (including its ion channels and neural circuits) isn’t necessary for arriving at the most obvious intervention for fatigue: get some sleep. However, if you are experiencing some type of brain dysfunction that prevents you from sleeping, a doctor’s consideration of what might be happening in your brain might lead to a helpful solution. Consequently, while causality of the mind happens via the brain, whether it’s most helpful to think about it at the level of the mind or brain depends on the situation.

Many of the arguments on the “mental disorders are not brain disorders” side of this debate boil down to an extension of this straightforward idea: once mental variables start interacting in complex ways to “cause” mental disorders, it can be more helpful to think about causal interactions at the mental level (as opposed to the brain level)—like in the insomnia causes fatigue example, where both insomnia and fatigue exist at the mental level. When stated that way, the idea is not so profound. We call the neurodegenerative disorder Huntington’s disease a “brain disorder” as opposed to a “subatomic particle disorder” after all (even though it does ultimately involve a reconfiguration of subatomic particles corresponding to the genetic mutation that causes it).

The commonly held position among researchers is that neither the brain nor the mind will be the singular best way to explain the causes of mental disorders or think about interventions. Neither the term “mental disorder” nor “brain disorder” is thus a great fit to describe these disorders (because these disorders involve not just one but multiple levels). The most critical, nuanced question we need to focus on is where the emphasis should be placed for any specific disorder—or even a specific individual. The answer to that question begins with clear-headed thinking about the problem from the outset, including how it manifests at different levels.

The “what” level as the first elaboration of the molecular neuroscience framework

In brain research, there is a general consensus that it makes sense to think about levels, but there is also a lot of debate about what those levels should be and whether Marr described them in the most helpful way. For example, you might begin by thinking that dopamine operates at the lowest how level. But there are still lower levels of how including the molecular cascades dopamine triggers and their interactions. Moreover, at the how level, you can also ask plenty of why and what questions, such as why dopamine triggers the particular molecular cascade it does as opposed to others. Is it because this particular solution is the most energy-efficient? When Marr originally proposed these ideas, he did so in collaboration with his colleague Tomaso Poggio, and at that time there were four levels (the what level was split into two). Today, Poggio agrees with a singular what level, but he proposes that two additional levels should be added above why (to capture evolutionary forces and learning/development). Many researchers (including myself) who find Marr levels beneficial liken them to conceptual guidelines that are helpful in particular scenarios as opposed to a specific prescription about what all possible explanations should look like.

Philosophers of science advocate for more rigorous ways to think about levels, by considering, for example, a hierarchy where each level serves as a mechanism to the level above. Behavioral descriptions of what an individual does might lie at a higher level, ideas about computation at an intermediate level, and the biology happening within neurons at a lower level still. In this framework, there are no specifications a priori about how many levels there will be or the types of levels a complete explanation will entail. While more rigorous, these types of more generic frameworks often lack the heuristics that people like to rely on to conceptualize what explanations look like for different problems. It’s helpful to consider a problem and think, “We need a Marr what-level description here.”

It’s difficult to understate the impact that the reasonably simple conceptual principle of Marr levels has had on brain researchers. As described by one, in the absence of appreciating levels we’re left with “seemingly unbridgeable chasms between people’s different understandings of what counts as an ‘explanation’ to them.” I remember my own fascination as a PhD student upon realizing that differences in taste about levels were at the heart of fiery debates between two professors in my department—while they were both passionate about understanding the same part of the brain, they differed in what they wanted to know about it. One of them was more interested in computational descriptions of what that brain area was computing, whereas the other was more interested in how that brain area operated by way of different cell types and such. Marr was right in noting that for any question that takes the form of “How does X work?” (where X might be vision or memory or mood or sanity), there will not be a singular level of explanation that captures the answer.

That naturally leads to the question: In the quest to understand and treat brain dysfunction, what do we most want and need to know? For a long while, researchers (including Marr) who have focused on what-level descriptions have drawn inspiration from the ethos of engineers. Simply put, engineers focus on building things, and when that’s the goal, it sets a clear benchmark for success that is difficult to quibble with: the thing you built works or doesn’t. In comparison, what it means to “understand” something is more elusive. This is why some consider building to be the ultimate illustration of understanding (including Richard Feynman when he famously said, “What I cannot create, I do not understand.”). Sometimes you don’t even know what you don’t know until you try to construct something. In addition, the act of having to specify every little bit can reveal that for some of the bits that you thought about, you thought about them wrong.

Consistent with that need, some researchers have pointed out that much too little emphasis has been placed on descriptions of how the brain processes information. In response to explanations that emphasize the brain areas involved in various functions, some have stressed where is not how. Efforts to link neural circuits to behavior (absent an intervening what-level description) have been decried a bridge too far. Likewise, describing that a brain area is involved in a behavior is distinct from understanding how a brain area contributes, and this is true even if the description employs a causal perturbation, like brain stimulation. Similarly, the problem of mapping the brain to the mind has been described as not just about understanding what parts of the brain do different types of things, but understanding what about the brain gives rise to what about behavior. Despite many repetitions of the same chorus across decades, the need to link what’s happening in the brain to the mind and to behavior—Marr’s what level—often has not happened.

This rationale is why descriptions of the brain as a computer have always resonated with me. This way of thinking about the brain emphasizes the what level, and the big gap that exists there. I’ve built my career around that idea, contributing to understanding the what level for vision and memory. All along, the notion that I and many others have held is that if we could understand the brain in a manner that would allow us to build things like it, benefits to society would naturally follow. And that notion has been reinforced—watching the interaction between this arm of brain research and computer science translate into progress in artificial intelligence has been absolutely thrilling.

Among those thrills is the creation of large language models, which have challenged our conceptions of what intelligence is. When one Google researcher asked the large language model LaMDA whether it had a sense of smell and it replied, “My favorite smells are that of a springtime rain shower, as well as the desert after it rains,” many were taken aback. LaMDA has no olfactory input; it can’t smell anything! So how, exactly, did it come up with that response? The dominant idea is that LaMDA is operating as a “stochastic parrot,” “haphazardly stitching together sequences of linguistic forms it has observed in its vast training data, according to probabilistic information about how they combine, but without any reference to meaning.” Before large language models, it wasn’t clear that language could be created “without any reference to meaning.” Rather, many researchers thought that language relied on an innate “grammar template”—a set of rules (possibly genetically encoded) that relied on meaning, on which all language was superimposed. Because these models lack a grammar template but manage to produce language, some researchers no longer think that’s the case. The existence of these models has made researchers rethink language construction entirely; intense efforts are currently underway to leverage the models to better understand how language really works.

The big question is: Given that what-level ideas (and the notion of the brain as a computer) have been so tremendously impactful for AI, why haven’t they also translated into more progress toward treating brain dysfunction? For a long while the answer has been presumed that it’s because we are made of biological stuff (not silicon). To create treatments for dysfunction, it’s that biology that we’ll need to interface with. This implies that we’ll need to understand the function of anything we are interested in at multiple levels—for instance, we will want to focus on understanding not only how Ritalin affects information processing but also how it works at the synapse and how the two are related. Indeed, this must be a part of the story; filling in the gaps to arrive at an integrated, multilevel understanding of any function will be important. Until I sat down to write this book, I also presumed that filling in the what-level gaps between the why and how levels would be sufficient. I no longer think that’s the case.

I suspect that by regarding the brain as a (sequential) computer, we’ve set up the problem in the wrong way insofar as our goal is to understand and treat brain dysfunction. The brain as a computer is an extension of the domino chain, and that’s neither the type of thing that the brain is nor why it breaks. Multilevel understanding is part of the answer but not the entirety of it. The puzzle needs one more piece. In the next chapter, I describe what that piece is.

a Marr called these levels computational theory, representation and algorithm, and hardware implementation. Here I maintain Marr’s definitions but map them onto the terms why, what, and how a bit differently than Marr did.

b For AlexNet and multiple contributions leading up to it, Geoffrey Hinton was awarded the 2024 Nobel Prize in Physics.

c Also called the “normal” distribution, it has the symmetric, hill-like shape shown in figure 6b.

CHAPTER 5 Embracing complexity

To thrive in a world of changing conditions, we must adapt. This is true for basic body functions like temperature, but it also applies to higher-level functions like determining when we should fight, flee, explore, or rest. The gist behind the idea of the brain as an adaptive system is that our health depends on our ability to adapt to change, and that disease can follow when the system is disrupted. This idea has been tremendously influential in medicine, from the regulation of blood pressure to the impact of chronic stress on mental health.

In a book poetically titled “The Wisdom of the Body” (1932), Walter Cannon pondered the remarkable ability our bodies have to maintain stability in the face of change. We are able to adjust not only to external factors like changes in ambient temperature, but also to internal changes, like the enormous amount of heat created when we use our muscles intensely for 20 minutes. Cannon emphasized that the body’s stability does not just happen by chance but instead is something that it constantly works to achieve. He called this process homeostasis.

The notion of homeostasis has been tremendously influential across all arms of biomedical research. At its heart, it is a comparison between where a system is and where it should be, and it involves a mechanism to move the system to the desired state when it falls away from it. Blood pressure is an extensively well-understood example of how this works: pressure receptors in the blood vessels send information to the brain for the comparison between actual and desired pressure, and when pressure is off, the brain triggers changes in heart rate, stroke volume, and the diameter of the arteries to adjust. In this system, maintaining a healthy set point is important to avoid the harmful effects of chronically high blood pressure, such as atherosclerotic plaques. When the system cannot maintain itself, modern medicine has developed ways to restore a healthier fixed point via drugs that do things like reduce heart rate or increase blood vessel diameter.

While a powerful concept, it turns out that homeostasis is not a great description of what the body always needs to do, even in the case of blood pressure. As we shift from lying down to standing up, we rely on anticipatory increases in blood pressure just before we stand to ensure that we do not faint as a consequence of blood rushing away from our heads. The notion of allostasis is an extension of homeostasis intended to capture the fact that for many systems (including blood pressure), the goal is not to maintain perfect stability but to anticipate when changes will happen and meet that demand. More broadly, allostasis is the notion that the brain does not just respond to change but anticipates future needs and proactively adjusts the body to maintain efficiency. Another example of allostasis is the release of insulin triggered in anticipation of eating (by the sight and smell of food and habitual mealtimes), preventing a large rise in glucose when we eat.

Because allostasis is about anticipating future needs, achieving it requires some means to predict what will happen next in our environment. At the appropriate time, the homeostatic set point of a system is then overridden to meet an anticipated need. Another way to think about it is that the system continuously anticipates what it will need and adjusts for it, and homeostasis is the return to a “default” need. Either way you think about it, the end result is a system that can stabilize itself as well as anticipate and react to change.

Homeostasis and allostasis typically require feedback. In the case of temperature regulation, the brain compares what the body temperature is with what it needs to be. If you are too hot, your body will begin to sweat to cool itself; when you reach the right temperature, you will stop sweating. In other words, causes (sweating) lead to effects (body temperature) that are fed back to adaptively influence causes once again. These processes are much more complicated in the brain, and one of the biggest challenges in brain research is clear-headed thinking in the face of circular causal loops. These loops can lead a system to behave in surprising ways because its behavior is determined not just by its parts alone, but by the interactions among those parts. Properties that arise from the interactions among these parts are regarded as “emergent,” and the system is then called “complex.”

A classic example of an emergent property from ecology is the oscillation of a predator/prey interaction such as lynx and rabbits. Lynx eat rabbits; consequently, as the number of rabbits grows, the number of lynx does as well. But the number of rabbits also depends on the number of lynx around to eat them. As lynx deplete their food source, the number of rabbits (and in turn lynx) begins to fall. The consequence of the feedback coupling between predator and prey is an oscillation of both populations that rises and falls periodically (fig. 7); in other words, as lynx and rabbits adapt to changes in one another, something surprising happens. Notably, the causes of this emergent oscillation cannot be understood by studying either predator or prey alone. Nor can it be understood by treating the system as a domino chain. Rather, understanding why the oscillation happens requires appreciating that both feedforward (rabbits to lynx) and feedback (lynx to rabbits) couplings exist.

Here, I refer to any system that both adapts to change and is complex as a complex adaptive system.a This type of system is ubiquitous throughout the brain and can be linked to its dysfunction. In the case of addiction, the brain gives rise to the drug-seeking mind, and once sought, drugs affect the brain’s biology to reinforce drug craving. The emergent property, in this case, is that the brain “gets stuck” in an addictive state. To understand and treat addiction, we have to appreciate that these feedback loops exist and find ways to break them.

FIGURE 7. Simple example of emergence in a complex system. The predator/prey interaction between rabbits and lynx is often modeled with the Lotka-Volterra model, which consists of two interacting (nonlinear differential) equations. In the model, oscillations of population numbers are produced by the interactions between the two species, not from either species alone.

Ideas about the brain as the type of thing that needs to continuously adapt naturally lead us away from thinking about the brain as a feedforward domino chain because a complex adaptive system relies not just on feedforward interactions but also feedback regulation to maintain its balance. These shifts, in turn, naturally lead us to different ways of thinking about how the causes of dysfunction might manifest in the brain. If we approach the problem of dysfunction by thinking about deficits in a domino chain, it leads us to look for the first domino in the chain that caused the disruption so we can repair it. While that may be true of a handful of disorders, that type of approach isn’t working out so well (as we’ve discussed). But if we instead approach the problem of dysfunction by presuming that it’s some type of deficit in a system with adaptive feedback that is trying to regulate itself (perhaps to maintain a set point), it may very well lead us to think about dysfunction in a different and more impactful way.

Let’s first take a closer look at these ideas and then dive into how to apply them to some of the brain’s biggest mysteries: what normal mood fluctuations are for, and what causes depression.

Complex adaptive systems are fragile

We know quite a lot about complex, adaptive systems because the topic is so relevant to engineering. Thermostats maintain a desired temperature in the face of fluctuations. Power systems create or redistribute energy based on changing demands. While the purpose of an adaptive system is to maintain robustness in the face of changing conditions, it turns out that endowing a system with adaptivity makes it fragile to catastrophic failures that are hard to prevent entirely. In April 1986 an accidental power surge ruptured the coolant system that supplied the Chernobyl nuclear reactor, leading to its meltdown, an explosion, and the spread of radioactive contaminants across the Soviet Union and Europe. In August 2003 a single power line in Ohio short-circuited after coming into contact with a tree, triggering a chain reaction that left over 50 million people serviced by the North American power grid (from New York to Ontario) without electricity for several hours to days. These are but a few examples of how fragile complex adaptive systems are and how they can fail (despite best efforts).

Following decades of engineering, we know that adaptivity and fragility go hand-in-hand even in the most clear-cut, engineered cases. Adaptive systems are not infinitely robust but collapse when specific changes happen. As an intuitive example of why, consider a system of three elements set such that they are in equilibrium—it might be an ecosystem with three organisms that live in a web, such as barnacles, mussels, and algae in a tide pool. These organisms not only live in a food web (where both barnacles and mussels eat algae) but also compete for rock real estate in the tide pools such that the expansion of any one species inhibits the expansion of the others. Consequently, in the absence of external changes, all three species will adapt to one another to maintain their numbers at a constant level. A perturbation to this system might be a change in water temperature that one of the organisms (like the mussel) is particularly sensitive to, leading to a rapid decline in its numbers. With a sudden competitive advantage, the barnacles could overwhelm the mussels and eat all the algae, leading to a population collapse. That’s fragility. It happens when a system’s components are recurrently connected such that they depend on one another. While the fragility of an adaptive system can be minimized to some extent, there’s ultimately no way to eliminate it. It is a fact that as systems become more responsive, they also tend to become more fragile. Likewise, as more elements are included in an adaptive system, its fragility tends to increase.

Development is a powerful form of adaptation that allows an organism to optimize for its environment as it grows, but that adaptation also leads to fragility. As an individual matures from the point of fertilization to birth (and beyond), something can lead them to acquire a neurodevelopmental disorder such as autism or schizophrenia. How that happens is a big mystery. How do we explain why a genetically identical twin of an individual with schizophrenia only has a 50% chance of getting it themselves (despite the same genes, the same womb, and the seemingly same developmental environment)? To do so, we need to consider how very small and subtle differences during development might lead to big effects.

One idea that has proven powerful for thinking about how this might work is the notion of a developmental landscape. First proposed by Conrad Waddington in the late 1950s, development is envisioned as a ball that starts at the top (at the point of fertilization) and rolls down a landscape full of hills and valleys to the bottom (reflecting a mature individual; fig. 8a). In this scheme, a developmental disorder—let’s say schizophrenia—is envisioned as happening when the ball ends up in one valley. Not-schizophrenia happens when the ball ends up somewhere else. The landscape is configured such that the valleys are deep at the bottom of the hill, and once the ball ends up in the schizophrenia valley, there’s no way of escaping it. Roll the ball several times, and it will take different trajectories down the landscape and only land in the schizophrenia valley on a subset of times (as a consequence of the initial conditions and tiny bumps along the way that push it in one direction or another). The landscape metaphor provides some intuition for how it is that variation during development that is so small it manifests like chance can lead to big effects (like schizophrenia) in a more mature individual.

FIGURE 8. Attractor landscapes. a) Waddington’s epigenetic landscape (Waddington, C. H. The Strategy of the Genes [Routledge, 1957]). Here, the development of an individual is envisioned as a ball traversing a landscape full of hills and valleys. Whether the individual acquires certain traits, such as schizophrenia, is determined by where the ball ultimately lands. Shown are two runs of the same developmental process with two outcomes, such as might happen for genetically identical twins. Reprinted from Mitchell, K. J. The genetics of brain wiring: From molecule to mind. PLoS Biol. 5, e113 (2007), CC BY 4.0; modified from original by C. H. Waddington. b) Illustration of systems with one and multiple attractor basins.

Today, ideas like Waddington’s landscape are formalized as mathematical models of complex systems. They amount to adding recurrent (feedforward and then feedback) loops into a feedforward network—a pretty simple adjustment in practice, but one with profound consequences for the way the system behaves: those loops can create “attractor basins,” which are activity patterns into which the network is drawn. There are many things that a network might do, but its activity patterns determine what among those things it actually does, and attractor basins draw it into doing a specific thing. The dynamics of these complex systems are most often visualized in the same way: as plots of an energy landscape in which the system’s state (reflected as a ball) always rolls toward lower energies unless perturbed by some outside force. The landscape shape can have valleys (attractors) and hills (repellers), determined by the network configuration. This means that where the network will settle depends on where it starts. A simple network might have a single attractor basin; a more complex network might have many (fig. 8b).

Both developmental and adult plasticity change a network’s parameters and so can change these landscapes. Less developed attractors tend to be shallower, and it’s easier for some change in the network to cause it to jump out of that state—this might reflect what happens early in development or learning when a new state is being acquired. The attractor basin is shallow, and therefore the system might easily avoid settling there. When the attractors become more entrenched, it takes a much larger input or perturbation to move the network to a new state once it’s settled in an attractor basin. This parallels the idea that the brain becomes less able to change across development, which Waddington called canalization. More often than not, development leads the brain to “get stuck” somewhere healthy, but in the case of neurodevelopmental disorders like schizophrenia, the brain gets stuck in a maladaptive state. These ideas do not just apply to neurodevelopmental disorders—in the case of blood pressure, the feedback mechanism that adjusts it creates an attractor such that the system maintains a “fixed set point.”

Some forms of mental illness (like depression and anxiety) are thought to be acquired in a conceptually similar way but during adulthood, through learning. In these “systems” models, some researchers find it helpful to think about recurrent interactions between psychological variables such as stress and different types of emotions. A normal amount of anxiety is thought to be a good, adaptive thing: it motivates us to go to the dentist and to save for retirement. Anxiety can also get trapped, however, in a cycle in which worrying leads to feeling down, which can lead to more worrying, which can lead to less social interaction, which can lead to more feeling down, and so on. This downward spiral can lead us to “get stuck” in a maladaptive attractor state; to get out, we need to break this feedback cycle. In this way, these models can be used both as metaphorical descriptions of how mental disorders happen and explicit descriptions formulated as mathematical models. One advantage of writing down these dynamical systems mathematically is that they can be explored for emergent properties in scenarios that are harder to think through, such as when larger numbers of variables are involved.

Learning is not the only way that we can get stuck. A system can also get pulled into a maladaptive state through overuse. For instance, consider the harmful impact of chronic stress. The fight or flight system exists to help us adapt to stressful situations in the short term, but tapping the system too often can lead to harmful effects such as depression and insomnia. The idea is that our bodies have a system of maintaining a normal stress level, and when we need to increase stress in the short term, our brains do this by releasing stress hormones, including adrenalin and cortisol. If stress hormones are released over a prolonged period, the stress response system becomes overstimulated, leading to chemical imbalances, perturbations in the diurnal rhythm (hence insomnia), and even the atrophy of brain structures (such as the hippocampus). We can think about the fight or flight response as a system that evolved to adapt to short-term stress in a way that made it fragile to stress in the longer term.

As we start to think about the brain this way—as a complex adaptive system—we cannot forget that it’s not sufficient to think about the brain as a control system that regulates temperature, for instance, or that triggers the release of fight or flight chemicals. The brain also has to process sensory input about the world and decide when it’s time to flee and where we should head when we do. In other words, the brain is not just a complex adaptive system; it’s a complex adaptive system that computes. For instance, we can make the important conceptual shift to the notion that stress is adaptive, and too much of it is detrimental, but that leaves the question: How does the brain determine what to be stressed about? Simply pointing to the neural circuits involved in stress (and hormones like cortisol) is not sufficient. Rather, we need to know what those neural circuits are doing to “compute stress.” If, hypothetically, you wanted to construct a machine that works like the brain, that type of description would be required. As we shift from the domino-chain ethos of the molecular neuroscience framework toward systems with feedback, we cannot forget to bring along Marr’s what-level.

When we think about the brain in this new way, the provocative notion that follows is that nearly all types of brain dysfunction are the consequence of the fragility that is inexorably intertwined with the brain configuring itself to adapt to change. No longer are we trying to find that one broken domino in order to fix it. The brain breaks because it is a complex system, and complex systems must be able to adapt to changing conditions—but this adaptability makes them inherently fragile. It’s thus hard to overstate the impact of shifting away from domino chains and toward thinking about the brain as a complex adaptive system; it changes everything. To unpack these ideas a bit more, let’s dive into what they imply for one of the brain’s most mysterious functions—mood—and one of its dysfunctions, depression.

Mood and depression

The purpose of many of the brain’s functions is so clear that we don’t pause to consider why we have them. Perception exists to take in the world. Memory exists so we can store information and access it again later. Language exists so we can transmit information between us. Our motor systems exist so we can act. But what are emotions for? In comparison to these other functions, emotion’s purpose is less clear. You might think that emotions are more of a bug than a feature—a consequence of something going wrong or right in the brain. But it turns out they are not a bug; emotions contribute to our robustness and ability to adapt to change. To unpack why, I need to tell you a bit more about them.

The umbrella term that researchers use for the group of mental functions that includes feeling, emotion, and mood is “affect.” Researchers who study affect discuss the experience of emotions like happiness, sadness, and calmness as “affective states” and the outward expression of those emotions (like smiling or crying) as “affect” itself. Open and contentious questions in this area of research include: What is the purpose of affect? Do other animals experience affective states in the same ways that we do? Did affect evolve to fulfill some function, and if so, what is it?

One influential idea in affect research is the hedonic principle—the notion that affect exists as a gauge that ranges from bad to good, and its purpose is to motivate us to keep the gauge as close to good as possible so we can thrive in life. The idea builds on the notion that the brain operates as an information processor that computes—in this case, the brain computes where things in the world fall along a “good-to-bad for me” scale. The hedonic principle combines the determination of a good-to-bad label with the motivation to approach good things and avoid bad ones. In us, this principle manifests as the powerful feelings we experience, like craving, disgust, joy, and fear, which cause us to approach or avoid something. In other words, “emotions are not just about what is, but also about what matters.” The brain is not just processing information but also trying to anticipate what will be good versus bad, so that it can maximize well-being.

Thinking about affect this way can lead us to rethink how the entire brain works. Typically, researchers who think about the brain as an information-processing machine parcel it up into a set of modules that combine to perform more complex tasks: we pay attention, we make decisions, we see, we hear. However, suppose we instead embrace the idea that the brain’s ultimate goal is to maximize the time an organism spends around beneficial things and minimize the time it spends around harmful ones. How, then, do we think about these modules? As one researcher describes, “You realize that neither the term ‘decision-making’ nor the term ‘attention’ actually corresponds to a thing in the brain.… Instead, there are certain very pragmatic circuits in the brain, and they do certain things like ‘approach’ or ‘avoid.’ … Some of those things are going to look a bit like attention.” The gist here is that when we focus our attention on something, it’s one way to engage with—or approach—it; likewise, pulling our attention away from something or ignoring it is a form of avoidance. To illustrate just how powerful this shift can be, let’s focus on a specific type of emotion and its dysfunction: mood and depression.

In William Styron’s memoir, Darkness Visible: A Memoir of Madness, he powerfully describes his first experience with major depression in his mid-sixties. No obvious event triggered it. As he describes it, his life was quite good—he had a loving wife and a successful writing career; when he was admitted to the hospital for treatment, he had just won a major literary award for his work. Yet somehow an episode of depression kicked in that led him to immense suffering. He describes depression as “so mysteriously painful and elusive in the way it becomes known to the self—to the mediating intellect—as to verge close to being beyond description.”

How do we even begin to understand Styron’s experience with depression and what caused it? As he writes, “the blues”—those minor depressive episodes that we all go through—might give us an inkling of what it feels like, but until you’ve experienced major depression yourself, it’s incomprehensible. But nearly all of us can empathize with Styron’s description because either we are afflicted with depression or we know someone close to us who is. Depression can follow from something palpable—like the death of a loved one or the loss of a job—but its causes can also be more elusive. As Styron powerfully explains, “Most physical distress yields to some analgesia—not so depression. Psychotherapy is of little use to the profoundly depressed, and antidepressants are, to put it generously, unreliable. Even the soothing balm of sleep usually disappears.” Individuals don’t just experience depression; they suffer from it. While we have some ways to help them, those ways aren’t effective for everyone. We must find better ways.

Styron’s experience is horrifying but not unusual: across our lifetimes, around 20% of us will suffer at least one major episode of depression. Of those who do, more than half will experience it again. Compounding the experience of intense suffering is, sometimes, a tragic outcome: depression is the leading cause of suicide. Treatments exist, but they work for only about 60% of those affected. Depression manifests in different forms, such as major depression (all lows), bipolar depression (shifts between highs and lows), and postnatal depression (following pregnancy). Like other psychiatric disorders, biological tests can rule out possible confounding causes (like an underactive thyroid), but there are otherwise no biological tests for it—its diagnosis is based on an individual’s symptoms alone.

Surprisingly, even though we know that antidepressants are capable of modulating mood and alleviating depression (at least in a subset of individuals), we still do not know what in the brain causes mood, and we do not have a great theory of what depression is. The now-defunct theory is squarely in line with domino-chain-like thinking, and it will probably be familiar to you: the hypothesized broken domino was levels of neurotransmitters (like serotonin) that were too low. Antidepressants like the recent generation of SSRIs sought to restore those levels by blocking the reuptake that normally happens after serotonin is released. This idea first emerged in the 1960s but was complicated in the following decades, as technology that could measure levels of serotonin in the synapse became available. Researchers found that SSRIs elevated serotonin very quickly, yet the drug took much longer to actually alleviate symptoms of depression—often several weeks or months. What happens in those extra weeks and months is unclear, but what is clear is that the explanation is not as simple as “SSRIs elevate serotonin, and increased serotonin alleviates depression.” The slow effects of antidepressants suggest that they may be triggering some slower form of plasticity—perhaps one that alters gene expression. Ideas are floating around about what these changes might be. For instance, perhaps, depression is a decrease in strength of connectivity between neurons (and recovery follows a restoration of that connectivity)—but no one really knows.

If we don’t know what depression is, how can we treat it? First, we need better ways to think about what it might be like. Thinking about the brain as an adaptive system that seeks to approach good experiences and avoid bad ones puts us on a better track. But this idea speaks only to behavior—why we behave the way we do in a given situation. What is happening in the brain when we approach or avoid? The answer begins with a question: What is mood?

We know mood as an ever-present feeling we continuously experience, characterized by states like happiness, sadness, anxiousness, and calmness. It tends to fluctuate slowly, subject to a multitude of disparate forces that we cannot always pinpoint; some days, we wake up in a better (or worse) mood, and we are not sure why. Mood is not the same as the acute emotions we sometimes feel that are targeted at something. For instance, we are afraid of tigers and disgusted by feces, but this isn’t mood. More often than not, our mood isn’t directed at a specific thing, and it feels more slippery than acute emotion. But mood is very important because it shapes our experience of the world—under periods of good or calm mood, we thrive, whereas periods of low mood (like depression) can incapacitate us. Why does this happen—what is mood for?

To answer that question, researchers need to begin with some idea about what type of thing mood might be. We know that our mood is somehow adaptive insofar as our moods impact our decisions and the outcomes of those decisions determine what we experience; this feeds back to influence our moods. This implies that mood is part of a complex system. Mood certainly feels complex. But from the outset, it’s hard to imagine an equation that captures it as a model, something akin to “mood = a + b.…” What would even go in that equation? What does mood depend on? It’s a bit hard to imagine, though surely mood must involve emotion in some way—so perhaps we should start with emotion.

Today, some researchers propose that we can map many of the emotions we experience on a plane that combines two dimensions (fig. 9). The first emotional dimension traverses from happy to sad and is associated with acquiring rewards. The second emotional dimension traverses from anxious to calm and is associated with avoiding punishments. Neither dimension alone can capture the strong sense we have of emotions. For instance, while we might think of sadness as the opposite of happiness, anxiousness does not fall between them; this implies that it falls along a different dimension. Adding a second dimension creates a plane that can capture all four emotional states I’ve listed and their combinations. For instance, aroused can be thought of as something between happiness and anxiety, and sleepy is its opposite. If we circle back to the idea that emotions exist to motivate us to approach good things and avoid bad ones, these two dimensions correspond to approaching and avoiding, respectively. Researchers are currently trying to pinpoint how these dimensions might map to neural circuits in the brain.

This two-dimensional core affect plane is intended to capture many momentary, acute emotions, but the idea is that it also gives rise to the slower and more mysterious fluctuations we call mood. In some proposals, mood reflects a running average of the acute emotions we experience on this plane. The gist is that if we repeatedly experience rewards or punishments, those emotions spill over (as mood) into how we experience other things. While this seems intuitively like a step in the right direction—if good things have happened to you recently, it puts you in a good mood, whereas if bad things have happened, it sinks you into a low mood—this notion of mood predicts that as we acquire more rewards (and march up the approach axis), we will be increasingly happier, and it turns out it’s not quite right. In the late 1990s researchers demonstrated that happiness is not just about rewards, but also about whether we expect those rewards. Expected rewards make us happy, but surprising rewards make us happier still. Here we are getting closer: mood depends to a certain extent on expectation. Is there a way that we can capture mood in an equation?

FIGURE 9. The two-dimensional core affect plane. The first dimension traverses from happy to sad and is associated with approaching by virtue of rewards. The second dimension traverses from anxious to calm and is associated with avoiding by virtue of punishments. Other emotions, like aroused, are created as combinations of these two dimensions. Adapted from Mendl, M., Burman, O.H.P., & Paul, E. S. An integrative and functional framework for the study of animal emotion and mood. Proc. Biol. Sci. 277, 2895–2904 (2010).

We should anticipate that creating a model of mood will be trickier than it is for other brain functions, like memory. For memory, there is an objective ground truth (something happened or didn’t), and you can create a test to measure how well someone remembers. In comparison, mood is a subjective experience for which there’s no right answer for what your mood should depend on; that makes it more difficult to design a good test. Likewise, we expect that different types of experiences will affect the moods of different people to different degrees; we can’t expect that there will be a fixed equation that will describe how everyone’s moods will fluctuate. This implies that the goal is an equation where mood is allowed to depend on different things (like rewards and punishments), and we allow the degree to which those things matter for mood to be different for different individuals—the mood of some people might be less sensitive to negative experiences (or sensitive for a shorter period). The best we can hope for is to study what an individual’s mood depends on and to see if we can use that model to predict how their moods will fluctuate in the future, given the new things they experience. But having such an equation would be a huge win—among the reasons, quantifying how mood fluctuates and understanding what it depends on is an important step toward understanding how mood is shaped and reflected in the brain.

In 2014 researchers in London set out to determine this type of equation for mood. They simplified the problem by measuring fluctuations in happiness in a context of a gambling task that can be thought of as traversing the “reward acquisition” axis of the core affect plane. Individuals were asked on each trial to choose between certain rewards and gambles—for instance, they could choose a guaranteed reward of £0.1, or they could place a gamble that would amount to either a win of £0.65 or a loss of £0.36 (fig. 10a, top). Every few trials, researchers asked subjects to rate their happiness on a continuous scale from “very unhappy” to “very happy” (fig. 10a, bottom).

In their model of mood, the happiness of an individual could depend on three things.b The first is the amount of reward on trials when an individual selected the certain reward option. The second and third captured what happened on trials when an individual opted to gamble. There, happiness could (in principle) depend on fluctuations between how much money was offered, on average, across the two options (“expected value”). It could also depend on the outcome of the gamble, reflected as the difference between the average and the reward (or loss) the individual received (“reward prediction error”). Because the outcome of these trials is determined by a coin toss when rewards (or losses) happen, it is unexpected. To capture the fact that happiness depends on a running average across events, each of these things was computed as a fading average (where the outcomes of more recent trials had a bigger impact on happiness than ones longer ago).

FIGURE 10. A model to predict happiness fluctuations. a) To induce happiness fluctuations, individuals experienced wins and losses in a gambling task. On each trial, individuals selected between a certain reward and a gamble. Every few trials, subjects were asked to rate their happiness on a sliding scale. b) The data for one individual whose happiness fluctuations (dark solid) were well predicted by a model of happiness fit to their data (gray dashed) but not by the cumulative earnings in the experiment (gray solid). Adapted from Rutledge, R. B., et al. A computational and neural model of momentary subjective well-being. Proc. Natl. Acad. Sci. U.S.A. 111, 12252–12257 (2014), with permission from PNAS.

In the context of this study, what happiness depended on varied from person to person, but once adjusted for each subject, this happiness equation did quite a decent job of tracking the fluctuations of happiness of different individuals across the experiment (fig. 10b, compare the dark and dashed lines). When researchers broke down what happiness depended on (on average, across subjects), they confirmed that it did not just depend on the total amount of reward an individual had accrued (which grew steadily across the experiment, fig. 10b, light gray line). Instead, it fluctuated up and down based on what had happened in the last seven trials or so. In addition, it was more strongly influenced by unexpected wins and losses than by expected ones.

These results, along with others, have profound implications. If we expect things to happen and they do not, reward prediction errors build up. When the things happening are unexpectedly good, we become happy; in contrast, when things are unexpectedly bad, we become sad. And it turns out that this sadness is transformed into the perception that outcomes are worse than they actually are. This makes mood profoundly fragile because it can get stuck in a negative feedback cycle where bad moods lead to the distorted perception of bad outcomes, which in turn leads to worsening mood.

While all this might make mood seem very much like a bug instead of a feature, there’s a different way to look at it that shows us that mood is actually adaptive. We know that reward-based learning exists to help us (and other animals) learn where to find the good stuff. A monkey looking for food will want to learn which trees have the most fruit so it can revisit them later. But it turns out that learning based on rewards alone is an inefficient way to go about things under real-world situations in which overall goodness or badness is changing. For instance, in the spring, when all the trees are starting to bear fruit, learning by visiting each tree individually can be misleading. Rather, a better approach for a monkey in this situation is to realize that conditions are changing and update its expectations about all trees. And this brings us to mood. The fact that mood is driven most strongly by unexpected rewards suggests that it is a signal that can help us learn when things (like our environment) are changing in ways that violate our expectations. The ability to do this is crucial because the world is highly correlated: if rewards (like food) are either bountiful or scarce today, they will probably also be so tomorrow. Likewise, if your bakery sold out of your favorite bread early yesterday and today, it will probably also sell out early tomorrow. What’s exciting is that these aren’t just hand-wavy ideas, they are ideas that have been incorporated into a proper, falsifiable theory.

In this way of thinking about things, mood is a form of adaptability. It reflects the degree to which our environment is changing in ways that impact our well-being, information that is important to help us adapt and learn. Depression is the fragility that comes along with the system: it might happen when too many unexpected changes happen in too short a time, each compounding the percept that things are worse than they actually are.

Formalizing something as mysterious as mood in a way that can be connected to learning and behavior is a thrilling step forward. Equally exciting is the fact that the mood equation points directly to what might be happening in the brain. Rewards and reward prediction errors are tied directly to the brain’s dopamine release. Namely, the brain releases dopamine when rewards (or punishments) are unexpected, and this triggers learning; the gist is that if something is unexpected, that means you don’t know it, so it’s worth learning.

This connection between dopamine and mood gives researchers a solid clue for investigating how depression might manifest in the brain. It suggests that they should focus on the brain areas and circuits implicated in mood and its relationship with learning, including how learning can drive the system into a low-mood state. Researchers have long suspected that brain-based treatments for depression (including antidepressants, transcranial magnetic stimulation, and electroconvulsive therapy) somehow stimulate or reset brain plasticity. This new conceptual framework provides them with new insights into how and why that might work: by allowing a maladapted and entrenched system to relearn itself into a healthier state. In addition, having a new way to think about how low mood and negative outcomes can lead to depression provides researchers with a new way to begin productively stepping toward understanding it.

Likewise, this new framework for thinking about mood sheds insight for where we might look in the brain. As part of the happiness equation study, researchers determined that happiness fluctuations correlated with fMRI activation of anterior insular cortex. This aligns with other work suggesting that this area plays an important role in the conscious experience of feelings. The big question is: What, exactly, is this brain area contributing? Might it integrate across good and bad experiences to compute the running average we experience as mood? That’s a concrete question that can be answered, and formulating questions like this is an important first step. You might also remember that this is the same brain area that was implicated in the belief component of Capgras syndrome in chapter 4. Given that we know so little about anterior insular cortex, it’s essential that we learn more.

These are but the first steps along a long and undoubtedly winding path. Many open questions remain about mood and how it influences our behavior. For instance, inconsistent with the hedonic idea that we work exclusively to maximize good outcomes, we engage in more tedious mood-decreasing behaviors (like housework) when we feel good; this is interpreted as shifting priorities away from short-term outcomes to meet longer-term goals. Researchers have yet to construct models that can predict how mood influences behavior under these real-world conditions in which many different forces and priorities that operate along different timescales compete.

There’s also much work to be done toward understanding how this basic research into normal mood fluctuations connects to mood disorders, including the experience of depression, as William Styron describes it. That said, while affect researchers who take the approach of thinking about mood haven’t yet made it to the end of the path, I suspect they are traveling along the right one. Borrowing from Copernicus, this strikes me as “a more reasonable arrangement” than alternatives (such as the notion of the brain as a sequential computer with a mood module that performs mood computations). Thinking about mood as adaptively shaped by its reciprocal interaction with the percepts of outcomes has long been the basis of therapies like cognitive behavioral therapy (CBT). The recent extension of those ideas into falsifiable theories that mood helps us navigate an ever-changing world may be the key to unlocking progress toward understanding and treating depression. I’m excited because I suspect that this is the type of Copernican insight that we so desperately need.

Stepping back, mood is clearly part of a complex system with many interacting parts that reciprocally feed back on one another—mood affects learning (and thus behavior), which in turn affects mood, and mood can happen along different timescales. Consequently, it isn’t easy to intuit how the system will behave. As I see it, appreciating that mood is part of a complex, adaptive system is the first step, but it does not end there. Formalizing slippery quantities like emotion, mood, and pleasure mathematically allows researchers to nail down ideas and test them. This is the only way we’ll make real, impactful progress toward understanding mood and its dysfunction, including depression.

Thinking about the brain as a complex adaptive system changes everything

When I set out to write this book, I did not know where it would lead. I knew that new treatments for brain dysfunction had not been keeping pace with new discoveries about the brain. I also knew that I could not find a clearly written account of the path forward that I could be optimistic about. The simplified description presented in textbooks (find a mutated gene; create a mouse; create a drug) generally has not panned out. Nor have analogous ideas about brain activity (find a brain area with aberrant activity; target it with brain stimulation), in all but a few cases. More broadly, the molecular neuroscience framework and its domino-chain ethos have not led us to understand the causes of many types of brain dysfunction.

I certainly did not set out to write a book emphasizing our need to appreciate the brain as a complex, adaptive system. In fact, complex adaptive systems did not strike me as an incredibly useful path forward. Early in my career, I did a bit of research in this area, and I left with the impression that this slice of brain research was populated with a lot of physicists focused on special phenomena like oscillations, not because they were particularly useful but because they were mathematically elegant and interesting. Outside of studying things like walking and breathing, I did not see how complex, adaptive systems would get us closer to an impactful understanding of how the brain works.

It was only through the act of sitting down to contemplate the Grand Plan for brain research that I began to comprehend what understanding the brain as a complex adaptive system can do for neuroscience. We’ve seen in this chapter what this way of thinking can do for mood and depression, and odds are that it can be just as useful for thinking about brain dysfunction at large. We know that these types of complex adaptive systems are built to be robust, but endowing them with that robustness makes them fragile in other ways. I am now convinced that this is generally why the brain breaks.

Many types of brain dysfunction probably follow from this fragility, including neuroimmune disorders. Our immune systems are designed to exhibit a powerful form of adaptation in which we build up a response to the pathogens we are exposed to such that when they attack again, we are ready. Without this system, we die (unless extensive measures are taken, like living in a germ-free bubble). The ability to adapt in this way requires an exceedingly complex coordination between our immune systems and the rest of our body to ensure that the immune response does not attack our tissues. It’s such a difficult problem to solve that it’s a wonder that it works more often than it does not. And thus it’s not a complete surprise that sometimes it fails and our bodies fall prey to the attack. Such is the case with neuroimmune disorders like narcolepsy (attack of orexin-producing neurons; chapter 2) and multiple sclerosis (attack of the protective myelin sheath covering our nerve fibers). In the case of neuroimmune disorders, the same factors that lead to the body’s adaptability also lead to its fragility.

Other examples follow from insights based on genetic inheritance. Fragile X syndrome is an inheritable intellectual disability linked to learning. Learning relies on mechanisms that increase the strength of synaptic connectivity between neurons such that when one input neuron fires, it’s more likely that its output neuron will fire as well (long-term potentiation). In addition, learning is modulated by a second, distinct mechanism that weakens synaptic connections (long-term depressionc), and having two mechanisms rather than just one is thought to provide the learning system with more adaptability. However, it also comes at a cost insofar as it makes the brain fragile to a host of new genetic mutations. Fragile X syndrome is caused by the mutation of a single gene, FMR1, involved in the second type of learning.

In sum, thinking about the brain as a complex adaptive system that computes helps us make sense of not only neuropsychiatric disorders like anxiety and depression but also neuroimmune disorders like multiple sclerosis, neurodevelopmental disorders like autism and schizophrenia, and genetically inherited disorders like Fragile X syndrome. Once you begin to think about brain disorders in this way, it becomes difficult to find ones that are an exception to this idea.

We might ask ourselves: Given that the concept is so general, what value does thinking about the brain in this way provide? There are two answers to that question. First, it helps us better understand what we are looking for: when systems have feedback, their dysfunction need not follow from a singular point in the chain—rather, these systems can get fixed at aberrant set points that are determined by the interactions between their parts. Second, it leads us to better appreciate why developing new treatments for dysfunction is such an enormous challenge. Treating brain dysfunction amounts to controlling a complex system, to shift the brain from a less healthy to a more healthy state. As we’ll discuss later, we know from engineering and other systems that this is very difficult. We’ve already started to build some intuition about why. It has to do with the fact that dysfunction is often inexorably tied to systems that are required for robustness—when the immune system mistakenly attacks one of our tissues, the answer is not to turn the entire immune system off (or we’ll die). Another way to say it is that formulating the problem this way helps us realize what we are up against. And it helps us understand why attempts to create new treatments built on the oversimplifications of the brain as a domino chain generally have not been working.

In other words, the shift to thinking about the brain in this way changes everything. But how exactly? What’s the new Grand Plan? What’s the new analog of “find a mutated gene, make a mouse, create a drug”? What’s the new analog of “find a brain area with aberrant activity and stimulate it”? In the next few chapters, my goal is to channel the ethos of this era to describe what that new, emerging Grand Plan is.

a In complexity theory, the term complex adaptive system is sometimes (but not always) used more narrowly to refer to systems that meet a set of specific criteria, such as parts that interact locally with a small number of others to self-organize and systems that learn and evolve. Here, I do not constrain the definition in the same way. While it is clear that brain systems are both complex and designed to adapt to change, they sometimes defy these narrower definitions (for instance, by the parts that interact globally or adaptation that follows from fixed as opposed to evolving mechanisms). Moreover, in many cases, we do not yet know what type of systems these are, yet we still need words to describe them (and good options are limited).

b For readers interested in the equation: happiness(t) =  w 0  +  w 1 ∑ j=1 t γ t−j C R j  +  w 2 ∑ j=1 t γ t−j E V j  +  w 3 ∑ j=1 t γ t−j RP E j where CR refers to certain rewards, EV to expected value, RPE to reward prediction error, and t to trial number; these parameters were all determined by the structure of the gambling experiment. The remaining parameters were fit to the data for each subject, including the weights w₀ through w₃, and γ, a gamma distribution parameter that captures how previous trials were averaged to determine happiness.

c Synaptic weakening, not to be confused with the mental state of depression.

PART III A new era

Let’s presume that thinking about the brain as a complex adaptive system that computes is generally a good idea. What then? Let’s remember that what we are ultimately after is a Grand Plan that we can be optimistic about; we’re looking for a description, in broad strokes, of a promising path forward for brain research that will lead to treatments. We will need to shift away from our current Grand Plan toward something new. But what?

For insight, let’s take a step back and note that the sketch for brain research remains the same—regardless of the type of thing that the brain is, we’re still looking to pinpoint the causes of brain dysfunction and develop treatments. The Grand Plan answers the question: How will we go about it? The details take shape around the presumption of the type of thing that the brain is. When we assumed that the brain was configured as a domino chain, we thought that to treat brain dysfunction, we needed to find and fix broken dominos. This ethos was reflected in approaches such as rational drug design, captured with the phrase “one gene, one drug, one disease.” As we shift to the presumption that the brain is configured into a set of complex systems with feedback, the new Grand Plan becomes something different. Unfortunately, it also becomes less obvious because complex systems don’t fail in ways that are as easy to describe with a pithy phrase. They can fail because of a broken node (like a mutated gene), an aberrant set point (due to the strength of interaction between nodes, like blood pressure), or something else that leads to a shift or collapse. With all this fuzziness, how, then, should we think about the Grand Plan?

One answer involves jumping to the end goal—treatments—to ask ourselves: What will developing them take? Hands down, the most profound and important insight I’ve had while writing this book is that the end goal of treating brain dysfunction amounts to one of the most formidable of all possible challenges: controlling a complex system. Not in the creepy or cartoonish sense of “mind control,” but in the sense that treatments require shifting the brain from an unhealthy to a healthier state. This challenge is so formidable that there are questions about whether it can even be done in principle (much less in practice). The answer depends on exactly what type of complex system we’re dealing with.

To illustrate, let’s look at what happened when we tried to control another complex system: the weather. Today, we don’t try to influence the paths of hurricanes. Why not? It’s not because we haven’t tried. Often forgotten about the history of weather research is that we did try, only to realize that it probably won’t work. Thus, we need to ask ourselves: What makes us think that the brain will be any different? After all, an epileptic seizure or psychosis might be likened to a tornado or a hurricane insofar as it’s a complex system gone awry. Under what conditions can we effectively control a complex system?

Learning from the history of weather research

Breakthroughs in weather research date back to the early 1900s, when researchers began to formulate the types of weather forecasting models that we use today. Those weather models idealize Earth’s atmosphere as a complex system composed of fluid that lies on a rotating sphere, subject to the fundamental laws of thermodynamics and hydrodynamics. At the core of those models is a set of interacting nonlinear differential equations for things like motion, wind direction, and energy. A global weather prediction begins by dividing Earth’s surface into a two-dimensional grid of thousands of squares and the atmosphere into a handful of layers. The equations are used to create a model to predict what will happen at each point in this three-dimensional grid. To generate the prediction for the first time step, a computer seeds each of the seven equations with current weather conditions (temperature, atmospheric pressure, etc.) and computes their solutions. It then uses those solutions to seed the predictions for the next time point, and so on.

The meteorologist Lewis Fry Richardson was among the first to come up with the idea that the weather could be forecast in this way. In 1916 he set out to compute a weather forecast for a region in Europe retroactively (for a day that had already happened). This predated the existence of the computer, and the calculations had to be performed by hand. Richardson began by seeding the equations with the weather measurements taken at 7 a.m. that day, and he worked to iteratively solve the equations to predict the weather six hours later, at 1 p.m. It took him 6 weeks. Ultimately, his calculations weren’t accurate—he predicted outlandish changes in barometric pressure of the type observed only during a hurricane, whereas the weather that day was relatively calm. However, the notion that predictions could be computed in this way planted a seed of imagination in many that this could, in principle, be done. Richardson proposed one creative idea about how to go about it: a human “forecast factory” that would employ 64,000 people to solve the equations to create weather predictions for the globe. While that never happened, the notion of the weather as a complex dynamical system that could be modeled and forecast was impactful, inspiring the creation of the modern computer.

As World War II began to wind down in the mid-1940s, the Princeton mathematician John von Neumann and the industrial researcher Vladimir Zworykin (who helped develop the television) approached government officials in Washington, DC, to request funding to create new computing infrastructure for weather prediction. They proposed a two-step plan: first, predict the weather; second, control it. As described in their proposal, “Only with exact scientific weather knowledge will effective weather control be possible.” US government agencies became quite excited about the idea of weather control and its potential to head off weather disasters and use weather as a weapon in battle. The team thus received funds to pursue the Meteorology Project, supporting the development of computing infrastructure and the refinement of weather models.

Over the next few decades, researchers around the globe set out to figure out how to control the weather. In 1946 researchers at General Electric (GE) successfully created snow over New York by releasing dry ice from a plane into the clouds. A year later, the dangers of messing with the weather were brought to life by Project Cirrus, a US government effort focused on disabling hurricanes. A hurricane was forecast to remain at sea, and researchers thought it would make an excellent test bed for an attempt to dissipate one. To try it, they dropped 80 kg of dry ice from a B-17 bomber with the intent of disrupting the hurricane’s internal structure. But the worst possible thing happened: the hurricane’s trajectory changed 130 degrees, and it landed in Georgia.

Following that incident, hurricane-targeting efforts were put on hold until they were revived again in 1962 with Project Stormfury, which lasted a few decades but failed to achieve any success. Over the years, other countries, including Russia and China, have also tried it, to no avail. In short, 75 years following the onset of the Meteorology Project, we’ve achieved step 1 (forecasting), but step 2 (weather control) hasn’t panned out. So what went wrong? The answer, in large part, is chaos.

Researchers ultimately discovered that weather is subject to “the butterfly effect,” meaning that small perturbations can have big effects that are difficult to predict. The effect was so named by Edward Lorenz after the idea that a butterfly flapping its wings over Brazil can cause a tornado in Texas. The fact that weather forecasts are much more accurate for the next few days than they are for the next few weeks follows from the butterfly effect. We can measure current conditions with only a certain degree of accuracy, and those small errors in our measurements of what’s happening now turn into big errors in our model predictions later. For the same reason, chaotic systems are exceedingly hard to control—it is difficult to predict the longer-term consequences of any given perturbation applied right now.

To build intuitions around how this works, let’s spend a few moments with a simple but powerful equation called the logistic map, popularized by the mathematician and ecologist Robert May in the mid-1970s. This equation illustrates how even a simple system can reflect different types of attractor states, including chaos. This equation is recursive, meaning that it computes the value of x at the next time step, xt₊₁, based on the value of x at the current time step, xt. It includes a single parameter, R:

xt₊₁ = R × xt × (1− xt)

How the behavior of this “system” unfolds in time, including the attractor state that it settles into, is determined by R. When R is less than 1, the system collapses to zero (fig. 11, R = 0.9). When R is between 1 and 2, the system converges to a fixed value and remains there indefinitely—this is called a fixed point attractor (here, the system converges onto the number 0.333; fig. 11, R = 1.5). When R is set to values around 3, the system settles into a periodic oscillation that repeats forever, called a limit cycle attractor (fig. 11, R = 3.2). Finally, when R is set to 4.0, the system’s behavior becomes bizarre: the oscillation becomes aperiodic, and the future trajectory of the system becomes exceedingly sensitive to the initial conditions. If you begin at x₀ = 0.2, you get one particular trajectory (fig. 11, R = 4, dark line). If you begin at a number really close but not exactly the same (like x₀ = 0.2000000001), you get a second trajectory that aligns with the first for a while before it diverges (fig. 11, R = 4.0, light gray line). This is called a strange (or chaotic) attractor. Like the weather, small changes in initial conditions can lead to big effects later. This is also why it’s so difficult to control a chaotic system: if you are just a tiny bit off with a perturbation, that deviation can have unpredictable effects down the line.

Even without following the math, you can appreciate the most important point: the same complex “system” (captured by an equation) can behave differently depending on how its parameters are set. The logistic map has been used to model what happens to populations in ecology whose generations don’t overlap because one is already gone before the other is born (like some fish and insects). In it, R reflects the proportional growth rate of a population: if it’s too small, the population collapses; if it’s just right, the population size settles into a steady state (or oscillates); if it’s too large, chaos ensues.

FIGURE 11. The logistic map. Shown for the same, simple equation for different values of the parameter R (labeled). Changing the value of R results in four types of attractor scenarios: collapse (R = 0.9), fixed point (R = 1.5), oscillation (R = 3.2), strange/chaotic (R = 4.0). Dark lines correspond to the initial condition x₀ = 0.2. Gray line in the bottom panel corresponds to the initial condition x₀ = 0.2000000001.

While intriguing, what does this have to do with the brain? It turns out that some of our best models of the brain operate at the knife edge of chaos. In these “recurrent neural networks,” neurons not only are connected in a feedforward way but are also recurrently coupled to one another via feedback, and the strength of those recurrent interactions between model neurons controls where the network sits. If neurons are too interconnected, a small input will trigger every neuron to fire; if neurons aren’t connected enough, even a giant input will peter out before it makes its way to the network end. If neurons are connected by just the right amount, however, an input can and will be processed in a sensible way by a subset of model neurons. And that “just the right amount” turns out to be the edge of chaos, implying that it could take just a little nudge to send it over the edge and into a chaotic regime.

Simply put, chaotic systems are the worst-case scenario where small changes have big effects that are difficult to predict. If brain dysfunction is anything like a recurrent neural network that has landed in chaos, trying to shift it back to a more stable state might be exceedingly tricky because the effects of perturbations are so unpredictable. It’s the equivalent of trying to perturb the weather to dissipate a hurricane. But even if brain dysfunction maps to a complex system in a nonchaotic regime, we expect that control will still be difficult because perturbations to complex systems generally tend to reverberate in unexpected ways. When those perturbations are therapeutic interventions, those unexpected things can be side effects and/or recalibrations of the system in a way that confers treatment resistance. From this vantage point, we can begin to see the enormity of the problem we’re up against in our efforts to treat brain dysfunction. From here, it’s not so surprising that new treatments have not been more forthcoming (despite all those facts about the brain we’ve been amassing).

While the challenge in developing new treatments is formidable, all hope is not lost. Take seizures, for instance. If a seizure is a sign of the brain entering an aberrant state, the brain appears to also have internal mechanisms for restoring normal function. Under severe conditions, seizures can continue for hours—illustrating that the brain is physically capable of it—but normally, they last only minutes. Likewise, individuals will often enter and then exit depressive and psychotic episodes days or weeks later. More broadly, we know that the brain has self-organizing loops and other mechanisms that keep it functioning. While we currently don’t understand those mechanisms very well, tapping into them could lead us to better treatments and preventions (in the latter case, perhaps akin to the fences used to prop up the snow to prevent avalanches). In fact, this may be a good description of how some current drugs (for epilepsy and psychosis) operate; we don’t yet know, and figuring this out is of the utmost importance.

Stepping back, once we appreciate the magnitude of the challenge we are up against in our quest to create new treatments for brain dysfunction, we begin to realize that as we shift away from thinking about the brain as a domino chain and toward thinking about it as a complex system, we need to rethink the Grand Plan entirely. To achieve the end goal of effective treatments, we’ll need to reconsider each step leading up to it, including how we go about the nuts-and-bolts, foundational research targeted at understanding how the brain works. For instance, if brain dysfunction reflects a complex system gone awry, it helps to have a model that accurately captures the system’s complexity in the exploration of possible treatments. More broadly, in any scientific field, research is often thought of as loosely evolving through stages of description, understanding, predicting, and ultimately control. As we shift to thinking about the brain as a complex system, we’ll need to rethink how we approach each of these in turn. This is what we will do in part 3.

The first challenge, describing (chapter 6), focuses on what a system does via accurate and repeatable measurements of it. How do we go about measuring mysterious brain functions like consciousness or sanity? We have a sense of what these things are (you are conscious; a rock is not), but we don’t have well-agreed-upon definitions for them that we can transform into measurements. Presumably, once we understand these things, we’ll know exactly how to measure them. But before that, we need to start somewhere. So, how do we go about measuring brain functions that we don’t yet understand? As we’ll see, there are special considerations for how we go about this when we expect that these functions are emergent properties of a complex system (where the whole follows not just from the parts but also from their interactions).

The second and third challenges focus on understanding how a system works (and how it breaks) and predicting what will happen next (chapter 7). The two are woven together insofar as both the behavior of a complex system and its causes are often hard to intuit, and both challenges thus must be tackled by building models of how (and why) these systems behave the way they do. It turns out that complex systems have special properties that follow from their feedback loops, where causes lead to effects that are fed back as causes once again; this requires that we rethink even the basic definition of what it means to “cause” something, how causality manifests, and how we’ll go about pinpointing the causes of brain dysfunction. In that pursuit, we can borrow from fields like ecology, where the special properties of complex systems are leveraged—for instance, to forecast when something unexpected like a big change is about to happen (like a seizure or a depressive episode) and to determine when variables are causes versus simply correlations.

The final challenge focuses on controlling (chapter 8) the brain when desired. This is the formidable challenge we must overcome to develop effective treatments that will shift the brain from an unhealthy to a healthy state. As we’ve already discussed, complex systems are exceedingly difficult to control. But this is simply the reality we are up against, and the only way to overcome it is to face it head-on. Engineers who need to control complex systems (like the International Space Station) face this challenge, as do cancer researchers. What can we learn from their successes and failures?

To recap, as we shift away from thinking about the brain as a domino chain and toward thinking about it as a complex system, figuring out the new Grand Plan for brain research will require more than a simple find-and-replace “domino” in the phrase “find the broken domino and fix it” with some other term. Instead, it will require that we circle back to the drawing board and rethink how we approach each of the big challenges of science (description, understanding, prediction, and control). Together, those insights will combine to form the new Grand Plan.

CHAPTER 6 Measuring brain and mental health

To help individuals with brain dysfunction, we need to begin by describing what the healthy brain does and how the dysfunctional brain differs, and capture those differences with some type of measurement. From there, researchers can pursue the causes of those differences and figure out ways to restore the dysfunctional brain to health. But sanity, craving, and consciousness are all very hard to measure. Why? Because measurements rely on definitions, and these things are not well defined. We have a sense of what psychosis is and that it differs from mania, but they also have a lot in common—where is the boundary between them? We are confident that we are conscious and that rocks are not, but how about a spider or a mouse? If we already knew the answers, we could use them to guide us toward definitions and measurements. But in the absence of already knowing, we have a circular problem: we need understanding to create measurements and measurements to create understanding. How do we even begin?

The challenge of figuring out how to define what it is that the brain does is exacerbated by knowing that the brain’s functions are likely to emerge from complex systems where more is not just more; “more is different.” In 1972 the physicist Philip Warren Anderson coined that famous phrase. The context was an article pondering why all science doesn’t just boil down to physics if elementary physical laws govern all happenings in the universe. The answer, Anderson explained, is that new properties emerge from the collective behavior of the parts. Collective behavior cannot be inferred from understanding the parts in isolation, but it’s also not mystical; it is simply a consequence of both the parts and how those parts interact. Physicists often offer as an example the magnetism of iron, which cannot be inferred from iron molecules alone because it requires the alignment of the spins of iron particles. Biologists point to the collective behavior of a bird flock, which moves together through spins and twists while also maintaining the ability of every individual bird to respond to a predator.

The consequence of emergent properties, as Anderson describes, is that “the relationship between the system and its parts is intellectually a one-way street.” The reason we have chemists, biologists, psychologists, and sociologists (not just physicists) is that it’s exceedingly difficult to infer collective behavior from the parts; we cannot infer the properties of life from the rules governing molecules and their interactions.

If the relationship between the brain and its parts is also an intellectual one-way street, we will not figure out what the brain does by exhaustively studying the principles by which its 86 billion neurons interact. It’s not that this type of “bottom-up” agenda hasn’t been suggested—it’s explicitly put forward in the same popular undergraduate textbook that describes the molecular neuroscience framework: “In neuroscience, there is no need to separate mind from brain; once we fully understand the individual and concerted actions of brain cells, we will understand our mental abilities.” The exclusively bottom-up approach implied by this quote is simply not an effective way to measure and understand a complex system in practice. The reason is that the number of possibilities is too massive. Taken to the extreme, this approach amounts to determining every possible activity pattern of those 86 billion neurons; even if we make the simplifying assumption that each neuron can be in one of two states (activated (“on”) or not (“off”)), that amounts to mapping 286 billion possible states. That number is vastly larger than the number of molecules in the universe (2⁸⁰). Clearly this is not the path forward.

So, how do we go about measuring the emergent properties of a complex system in the absence of understanding it? We can glean insights into how to make our way out of this circular conundrum from a surprising place: how scientists figured out how to measure temperature in the seventeenth century. Analogous to the many mysteries about the brain today (like consciousness), what temperature is, and why ice melts and then evaporates as temperature changes, were not understood at the time. Figuring out how temperature works began with nothing more than our own bodily sense of hot and cold (we can feel these things, after all) and observations like “water freezes and boils.” Ultimately, we figured out not only how to measure temperature with the precision of a billionth of a degree of absolute zero, but also how emergent properties like phase transitions, including freezing and boiling, work. In his book Inventing Temperature, the philosopher Hasok Chang insightfully describes the history behind how humanity achieved this remarkable feat. The story offers insights for brain research and gives us reason to be optimistic that we will ultimately understand the brain.

At the heart of the story Chang tells is the process used to measure and understand, which he calls epistemic iteration. Here, epistemic refers to the word philosophers use to talk about what we know, and the phrase simply means iterating what we know. It can be applied to any scenario when we have a sense of what we want to measure but not yet deeper insight into what it is. The first step is to jump in with a best guess about what something is and how to go about measuring it. It’s alright that our guess is not perfect; it’s likely good enough to make an advance. The next step is to refine the definition and measurement to make it more precise and account for more things. This process happens iteratively until a good answer—both a measurement and a theory about it—emerges.

Epistemic iteration is a way out of the many circular problems we face in brain research. Once clearly stated and understood, it might appear trivial insofar as, in many cases, it describes what brain researchers are already doing. So where’s the insight? Conceptual clarity can lead to new perspective and understanding, including insights into the potential pitfalls that can happen along the way.

Learning from the history of temperature (and memory)

It’s both compelling and daunting to think that where we are now in our understanding of things like consciousness and depression is analogous to where scientists were in the early seventeenth century when they set off on the quest to understand temperature. Scientists began their pursuit of temperature with intuition based on their bodily sensations of hot and cold, some observations about the world (including that puddles freeze and evaporate), and some rudimentary devices to measure it. From there, it took about 250 years to create a well-agreed-upon way to measure temperature and a theory about how it works. In the case of the brain’s most mysterious functions, like consciousness, we are in a similar position—we have a sense of what consciousness is based on our own experience, some observations in the world (including that when people are sedated, they are unconscious), and some rudimentary devices to measure it (such as consciousness scales based on how well an individual can follow commands or react to a toe pinch). Researchers traversed the chasm from the early days of temperature all the way to thermodynamics, and insight into how they proceeded can help inform how we should tackle understanding consciousness in modern times.

The first step toward understanding temperature was the creation of a primitive measurement tool: the thermoscope. Philo of Byzantium in 250 BCE created the first known version of the device. But for the next 1,850 years, not much happened; the device reemerged in history when Galileo (re)invented it around 1600. A thermoscope works by immersing the open end of an air-filled glass bulb in water. When the bulb cools, air is compressed and the water rises. Thermoscopes measure temperature changes, but they lack any type of numerical scale and weren’t aligned with one another in any systematic way. Finding that scale took around 150 years.

The hunt for a standardized temperature scale that all thermometers could use began in earnest around 1700. A scale required fixed points that all thermometers could be calibrated to—but what should those fixed points be? Suggestions ranged widely. Edmond Halley (of Halley’s Comet fame) suggested the boiling point of alcohol. Daniel Gabriel Fahrenheit (who invented the temperature scale that bears his name) proposed body temperature. One French scientist suggested the Paris Observatory cellars, which were renowned for their temperature consistency. Another French scientist suggested the melting point of butter. At this moment in the history of temperature, more than any other, I wonder about parallels with brain research today, 300 years later. It’s easy to smirk at the idea that the melting point of butter would be a rigorous reference. But will future scientists in 300 years smirk about how we measure consciousness and depression today? Probably. Thinking about scientific progress through the lens of epistemic iteration encourages a bit of well-reasoned intellectual humility.

Ultimately, the freezing and boiling points of water won out as fixed points that could be used to standardize different thermometers. While those fixed points were agreed on in principle, it was unclear how fixed those points were in practice. Researchers either knew or suspected that water’s freezing and boiling points could depend on all sorts of factors, such as atmospheric pressure and the type of container water was placed in (say, glass versus metal). In 1776 the Royal Society of London created a committee to sort out the details. That committee decided that the field should proceed by standardizing the parameters for calibrating thermometers (including the atmospheric pressure, type of container, and such). While this all might sound like a sensible and even obvious way to proceed when we want to standardize a way to measure something, consider that today there are a remarkable 280 different ways to measure depression; a standardization committee analogous to the 1776 thermometer group did not meet until 2019.

To this point, progress in measuring temperature happened independent of theories about how it worked. That is not to say that theories about temperature did not exist, but rather that they did not contribute in any substantial way to the development of the thermometer. But even so, we did ultimately arrive at those theories. Skimming over many of the details, the first phase involved a debate about whether temperature was governed by the existence of heat matter (called caloric), cold matter (called frigorific radiation), or some combination of both substances. The idea of cold matter was the notion that the temperature of a substance can be lowered by the absorption of cold matter (not just the loss of heat). Caloric theories won out. In the next phase, which happened in the late 1700s, thermometers tested predictions of caloric theories, and those predictions turned out to be at odds with experimental results. This led to the search for new theories and, in the mid-1800s, to notions that we know today as thermodynamics: the idea that temperature is not a separate substance but the kinetic energy of the moving particles that make up a substance, which are constantly in flux.

Once we knew what temperature was, we wanted to understand how different materials transitioned from one state to another, dependent on temperature. In the case of water, an electrostatic force draws the positively charged hydrogen atoms from one H₂O molecule to the negatively charged oxygen atoms of another. In the liquid state, individual water molecules have an intermediate amount of kinetic energy such that those bonds are continuously formed and broken, and the molecules slide past one another. When water freezes, the molecules have slowed enough such that attractions between them configure into a hexagonal pattern; when water boils, the molecules have acquired enough kinetic energy to break the bonds between them completely. Notably, the phases of water are an emergent property of the interactions between molecules. They do not involve changes to the molecules themselves.

In sum, the development of the theories we have today about temperature reflects one path out of the circular conundrum between measurement and understanding. Starting with a sense of what temperature is and a few observations about it, scientists began by creating a device to measure it from the “top”: the thermometer. The first generation of thermometers did not get the measurement quite right, but they were good enough to kick off a process of refinement that happened over around 250 years. Much of the focus during that period was on standardizing different thermometers to make the same measurements. While theories about temperature were created in parallel to measurement devices, they did not play a role in developing the devices per se. Rather, the existence of precise devices enabled scientists to test the predictions of candidate theories about what causes temperature and iterate on those theories until they arrived at good ones. Ultimately, those theories required considering how the properties of the whole (like water) emerged from not just its parts (water molecules) but also their interactions.

Epistemic iteration is a solution to the circular problem we face when we want to measure something that we have a sense of but do not yet understand. We begin by taking our best guess, and we go for it. But we also acknowledge that we are likely to get it wrong before we get it right, and we thus work to refine our guesses. We can point to things that happened during the quest to develop temperature that were beneficial, including an emphasis on standardizing and measuring temperature well before evaluating theories about it. Should the same things be pursued in the same order for all scientific quests? No. Chang emphasizes that through the lens of epistemic iteration, we can look back in history and see how each step toward progress followed from earlier steps, but we cannot deduce how these steps will unfold for all types of problems. In other words, it’s a framework for conceptualizing the problem, not a step-by-step prescription for solving it.

Indeed, if we look at the history of human memory research through the lens of epistemic iteration, we can see that it happened differently. Ideas about memory, as we know them today, can be traced back to the early 1900s with memory researcher Richard Semon’s proposal that excitation in the brain leaves behind an imprint called an engram, and this engram is the physical basis of a memory. A little over a century later, we now know where this happens in the brain (the hippocampus) and how it happens (via the excitation of neurons, triggering a cascade of molecular events), and we have sophisticated theories about how memories are triggered by things that are associated with them (like a photograph). We can even reactivate, erase, and implant memories, at least in mice. How did all this progress transpire?

Unlike measuring temperature (which is everywhere), measuring a memory in the brain required first figuring out where in the brain to look (the hippocampus), a step that took about 50 years. “In search of the engram,” Karl Lashley trained rats to navigate mazes for food and lesioned different parts of the brain to see if those lesions impaired the rats’ ability to form a memory of where the food was located. He found that while the size of these lesions correlated with the rats’ cognitive impairment, the location of the lesions did not. From this, Lashley concluded that memory did not require any particular part of the brain but was instead distributed across large swaths of it—but he missed something important. In the 1950s and 1960s, Brenda Milner revealed through work with human patients that Lashley had overlooked one crucial structure: the hippocampus. Damage to it led to memory impairment in the patients she worked with, including Henry Moliason, known as “H.M.” until his death in 2008. H.M. could tell detailed stories about his childhood experiences but could not store new memories.

Following the suggestion that memories might involve the hippocampus, brain researchers next turned to how memories are stored in the brain. Whereas the researchers studying temperature created a way to measure temperature independent of theories about how temperature worked, memory researchers relied on theories of how memories are stored in the brain before they measured them. One influential proposal from Donald Hebb suggested that memories are stored in assemblies of cells, and that synaptic connections between these cells are strengthened when the activation of one neuron triggers another; the idea is reflected in the famous phrase “neurons that fire together wire together,” today called Hebbian learning. Hebb’s proposal inspired a group of researchers (including Eric Kandel) to measure memories by mapping out the molecular cascades that caused them, first in the sea slug Aplysia and then in mice.

In the early 2000s this work was extended with biotechnological breakthroughs that could manipulate memories. The engram experiments, as they were affectionately called, incorporated new optogenetic tools that allowed researchers to insert light-sensitive molecules into neurons in a mouse by infecting them with genetically engineered viruses, and then to manipulate the neurons’ activity by shining light on them. In these experiments, light-activated molecules are inserted into the subset of hippocampal cells that are activated as a memory is stored, allowing researchers to activate—and manipulate—that specific subset in an experimental setting. The engram experiments confirmed that hippocampal neurons store memories, and by manipulating those neurons, you can change the memory itself.a They were among the biggest (and most exciting) success stories of brain research in the twentieth century.

At the same time, the engram experiments leave an important gap unfilled: How does this description of memory in the brain give rise to the experience of memory in the mind? When I see someone, it often triggers a memory of their name. Conversely, when I hear their name, I often remember what they look like. How does (seeing or hearing) one thing trigger the memory of another? Descriptions at the level of molecules don’t answer that critical question. For that, researchers have turned to a more computational approach that emphasizes how memories emerge from a complex system.

The physicist John Hopfield was among those who decided to work on this problem in the late 1970s. His goal was to build a model of memory. He began with the type of domino-chain, feedforward neural network model that was popular at the time and proceeded to add recurrent connections to it, motivated by the knowledge that memories are bidirectional (insofar as one part of a memory triggers the rest of it). As he proceeded to construct network models for memory, he noticed something that only a physicist would—a link between the reciprocal connections he was using and the mathematics of “spin” used to describe magnetism. That led him to the idea that networks with emergent attractor dynamics would be a good framework for memory. In these networks, when something triggers a memory (like a name), this places the network activity near an attractor state. The network then “falls” into it, thereby evoking the recollection of a memory (the face associated with it). Because these attractor dynamics emerge from network interactions as opposed to individual neurons or synapses, they offer a classic example of how “more is different.” For this work, Hopfield was awarded the 2024 Nobel Prize in Physics. Modern theories of memory work via similar principles, and today memory researchers are working to determine how these two different ways of thinking about memory—at the molecular and network levels—fit together.

So if we look at the histories of temperature and memory side by side, what is different, and what is similar? As we’ve already described, the path of epistemic iteration was different for each: measurements and theories of temperature were developed separately, whereas measurements of memory relied on theories about how memories are stored in the brain. Notably, breakthroughs in both temperature and memory measurement followed from technological developments. Likewise, a complete understanding of the effects of both temperature and memory ultimately required appreciating that they are emergent properties of a complex system.

Despite the different paths that a field might traverse, the conceptual clarity provided by epistemic iteration and how it has unfolded in the past—through the standardization and refinement of measurement, a combination of both bottom-up and top-down approaches, and ultimately an emphasis on complex systems—has the potential to streamline progress. It helps us conceptualize what we are trying to do in brain research and how to proceed. The parallels between brain research today and temperature research in the seventeenth century are intriguing. Like the scientists of that time, we are puzzling over our fixed points as we try to create our devices. But temperature is also just one thing, whereas the brain does many things, and in brain research today, some things (like memory) are more advanced than others (like mood). One advantage we have over seventeenth-century researchers is more conceptual clarity about what we’re up against. Today, it makes sense to leverage that clarity to reassure ourselves that understanding the brain can be done and to leverage epistemic iteration to expedite that understanding.

As we shift away from thinking about the brain exclusively as a domino chain and toward thinking about it as a complex system, how do we need to rethink measuring and describing the brain? Can we expedite understanding by thinking about it this way from the beginning (as opposed to tacking it on at the end)? For answers, let’s have a look at consciousness.

Iterating consciousness

Following a stroke, Richard Marsh experienced the horror of locked-in syndrome: he was awake and aware but completely paralyzed and unable to communicate in any way; he could not even blink his eyes. His doctors thought he was in a coma, and they expected that he would not recover from it. As he looked on helplessly, they suggested to his wife that his life support should be discontinued because, for all intents and purposes, her husband was already dead. As Marsh recalls thinking, “Already dead? What kind of doctor can’t tell a living person from a dead one? What sort of place was this? … How could I be dead if I could hear every word they said? How could I be dead if I could feel my wife’s breath and see the tears in her eyes as she leaned towards me?” Fortunately, his family opted to give it a bit more time, and Marsh regained his ability to blink voluntarily. This allowed him to communicate, starting with one blink for “yes” and two blinks for “no.” He also began to move his eyes, and his physicians posted a board so he could spell out words by shifting his gaze to individual letters. Among his first words were T.H.A.N.K.Y.O.U. Mercifully, Marsh continued to recover and eventually regained almost all his motor function.

Among individuals with locked-in syndrome, Marsh is one of the fortunate who recover. The opposite is true for individuals with amyotrophic lateral sclerosis (ALS, which, you might recall from earlier, is a progressive neurodegenerative disorder that can lead to becoming locked in). For individuals like Marsh, those with ALS, and others with locked-in syndrome, we need to figure out better and different ways to measure consciousness.

There are also other good reasons to measure consciousness, among them that it might allow us to help the tens of thousands of individuals who fall into a coma each year. Disorders of consciousness, including coma, can follow from damage to the brain via either physical forces (like a car crash) or internal damage (like a stroke). In the most severe cases, brain damage leads to a prolonged vegetative state, but it can also lead to less severe states of disorder, in which a patient shows minimal or inconsistent awareness. Finding ways to measure levels of consciousness in patients with brain damage is of the utmost importance.

Clinically, consciousness is typically measured by the Glasgow Coma Scale, introduced in 1974 to make the quantification of consciousness more systematic. Before it, physicians would diagnose patients into categories like “comatose” and “stupor,” but the boundaries between them were ill-defined and inconsistent. These fuzzy categories led to adverse outcomes like misdiagnosis that delayed effective and life-saving treatments (for conditions like bleeding in the brain). The Glasgow Coma Scale quantifies the degree to which an individual’s eyes are open spontaneously (versus to pain or not at all), their verbal response (from normal to confused to none), and their motor response (from obeying commands to abnormal pain response to none). The three measures can be considered individually or combined into a single score, and both approaches are used to guide decisions about treatment and monitor outcomes, especially following a head injury.

While a good step toward measuring consciousness, measures like the Glasgow Coma Scale are not effective when patients are conscious but paralyzed, so they would not help locked-in patients like Marsh. We need better ways to measure consciousness that do not require patients to talk or otherwise respond, so that we can catch these cases. Studies have shown that approximately 15% of coma patients who are unresponsive to spoken commands (and sometimes also painful stimuli) still have brain activity in response to those commands. And an estimated 1% of individuals anesthetized for a surgical procedure experience accidental awareness and remember parts of surgical procedures in which consciousness was not intended. How can we measure consciousness in these cases?

Measures of brain activity (like EEG) could, in principle, be used. When an individual needs to be sedated for a surgical procedure, anesthesiologists typically measure anesthetic depth via things like heart rate, blood pressure, and the concentration of the anesthetic exhaled. They sometimes also add brain activity (measured via EEG) to this list, but the challenge is in figuring out what to do with that data, and, in turn, whether EEG is the correct measurement tool. How do various measures of brain activity correlate to consciousness? Thus far researchers have tried measures of consciousness based on things like how large brainwaves are or how quickly brain activity reflects a sound, but these haven’t been great predictors of anesthetic depth. But perhaps this is exactly the type of situation that epistemic iteration is well-posed to address: if we knew how the brain gives rise to consciousness, we would probably know exactly what to measure. In the absence of a definition of what consciousness is or how it works, how do we begin?

One answer is that we need to jump in with epistemic iteration, take our best guess, and refine from there. But where and how should we jump in? Should we start at the top (as we did with temperature) to get a good measurement of consciousness level, with the idea that the measure (once developed) can be used later to test possible theories about where it comes from? Or should we jump in at the bottom (as we did with memory) to focus on the molecular level and create a theory about where consciousness comes from, anticipating that a more holistic understanding of how consciousness emerges will naturally follow?

Channeling the molecular neuroscience ethos of the 1990s, a subset of brain researchers opted for the latter, focusing on how anesthetics work. While clinicians have used anesthetics since the mid-1800s (and anesthesiologists generally know how to use them effectively), we still do not understand how they modulate consciousness. In pursuit of the answer, researchers focused on how anesthetics affect the brain at the molecular level, such as ion channels. They speculated that once a protein in the brain affected by anesthesia was identified, they could create a mouse model with a mutated version of that protein, to see if the mutation rendered the mouse insensitive to anesthesia. The idea was that if something contributes to the sedative properties of anesthesia, mutating it will interfere with that sedative property. Throughout the 1990s this approach identified a handful of molecular entities affected by anesthesia, including proteins involved in GABA neurotransmission. In turn, this led to an exceedingly detailed understanding of how anesthesia affects those proteins (such as the three-dimensional structure of GABA neurotransmitter receptors). It also led researchers to discover that injections of anesthesia into a specific brain area (a part of the hypothalamus) alone can produce sedation in rats. These results were extended to define a network of brain areas involved in anesthesia, which overlap with the ones known to modulate sleep.

While this bottom-up approach has revealed some facts about how anesthesia operates, there are indications that what has been revealed thus far is but a small slice. For instance, mutating any of these implicated proteins in a mouse (like a GABA receptor) only modestly impacts the effects of anesthesia, suggesting that any of these proteins alone is not necessary to induce an anesthetic state. Researchers have also learned that anesthetics bind to a shocking multitude of protein targets: an estimated 10–15% of detectable proteins (and at least 300 in total) scattered throughout the brain. What subset is responsible for the effects of anesthesia (as opposed to proteins that anesthetics bind to with no functional consequence)? Analogous to the relationship between psychiatric disorders and the hundreds of genetic variants that are associated with them, it’s unlikely that we’ll understand the fuller picture of how anesthesia modulates consciousness by studying these proteins one by one (or in small combinations). It is likely that we will need to take a different approach.

More recently, a suite of complex systems-inspired, top-down approaches have sought ways to quantify consciousness level based on measures of brain activity. These measures focus on quantifying the complexity of brain activity patterns, either as they happen naturally or following some type of stimulation (like a magnetic pulse applied noninvasively to stimulate the brain). All these measures begin with the assumption that consciousness is an emergent property of a complex system in which many neurons and brain areas interact. They all recognize that straightforward measures of brain activity, such as the degree to which it is synchronized or desynchronized across brain areas, aren’t suitable measures of consciousness. For alternatives, they turn to theories about how information processing in the brain works.

As we discussed earlier, some theories about the brain propose that it needs to maintain a delicate balance at the knife edge between order and chaos. It’s a state called “criticality.” The gist builds on the idea that in real brains, connections are reciprocal: if one part of the brain (let’s call that A) connects to another part (let’s call that B), part B also sends connections back to part A. As such, when activity in A is triggered, it reverberates through the network to produce a burst of activity. In a healthy brain, connections are balanced such that its activity patterns will be ones in which short bursts of activity are frequent and large bursts are rarer. In fact, in a brain poised at the knife edge, the frequency of those activity bursts falls off in a predictable way (as a power-law). In comparison, when a brain becomes uncalibrated, longer bursts will happen either too rarely (nudging toward a coma) or too often (nudging toward a seizure). At the knife edge, the brain is optimally positioned to do all the many things it needs to do. The idea follows from studies of criticality in artificial recurrent neural networks, which perform optimally when positioned at the critical boundary. In such networks, neurons need just the right level of connectivity between them for an input to be processed in a sensible way by model neurons.

Following these insights, researchers have figured out how to predict how close a brain is to the critical boundary by measuring brain activity. Their predictions are probably in line with what you might expect. Anesthesia results in brain activity patterns that fall away from the boundary on one side. Seizures result in brain activity patterns that also fall away from the boundary but on the other side. Natural brain activity patterns fall very near the boundary. Surprisingly, the hallucinogen LSD produces brain activity patterns that are closer to the boundary still.b A related approach has focused on quantifying the complexity of the echoes in brain activity that follow a pulse induced noninvasively by transcranial magnetic stimulation. This approach was able not only to distinguish individuals who were awake from those who were under anesthesia (or sleep) but, when applied to patients in a coma, revealed that nine of forty-three patients had brain activity that reflected consciousness, suggesting that they were “locked in.” Likewise, when this measure was applied to individuals in advanced stages of ALS, researchers found brain activity patterns that reflected consciousness but were more variable than healthy controls, suggesting that these patients were alert during some periods but also that their alertness was more unstable and fluctuating.

These approaches are among the first exciting and successful (albeit imperfect) steps toward quantifying consciousness in paralyzed patients. With refinement, they may help us identify the patients that are “locked in,” as well as how effective anesthesia is. Alone, it’s hard to see how the bottom-up approach to understanding consciousness would achieve the same goal. Notably, the top-down pursuit can take on many forms, but it begins with the assumption that a domino chain does not produce consciousness; instead, consciousness is an emergent property of a complex dynamical system with feedback loops.

Consistent with epistemic iteration, the next steps for understanding consciousness require iterating these measures. That will likely involve coming up with theories of how consciousness comes about, and that understanding will hopefully lead us to treatments for disorders of consciousness. These top-down measures will likely meet the bottom-up insights of the 1990s somewhere in the middle, probably at the level of neural circuits and the network of brain areas involved. That is not to suggest that the path forward will be easy—theories about how the brain gives rise to consciousness are among the thorniest and most controversial in brain research. But as far as I know, all contemporary theories of consciousness presume from the outset that consciousness is an emergent property of a complex system; they all agree that it is there that we need to focus.

Standardization, epistemic iteration, and emergence (for depression)

Like temperature, memory, or consciousness, mood and depression are something we have a sense of based on our experience, but not (yet) a good definition that we can use to create a definitive measurement. Once we understand depression and what causes it, understanding how to measure it should be obvious. But because we do not understand depression, we need to start somewhere else. What’s the right way to measure depression in the absence of understanding? In chapter 5 we discussed understanding mood with the implicit assumption that we had a good way to quantify it. In those experiments, subjects were asked to rate their happiness on a continuous scale. Is this the best way to measure mood in all cases? How have researchers approached it?

In the early to mid-1900s, psychoanalytic approaches and unstructured interviews were used to diagnose depression. The problem with these measurements is that the diagnosis varied wildly across practitioners and patients. In the 1960s and 1970s, depression scales increased diagnostic reliability. Among them was the most commonly used scale today, the Hamilton Rating Scale for Depression (HRSD), which asks clinicians to perform a diagnostic interview to rate whether patients have depressed mood, a suicidal tendency, loss of interest in work, and weight loss. In comparison, the Beck Depression Inventory (BDI scale; introduced in 1961 and revised in 1979) asks patients to self-report whether they are feeling discouraged, whether they have been crying, and if they are sad. Altogether, researchers have developed a remarkable number of depression scales—more than 280!—and for a long while, they did not generally agree on which to use when. This led to a few problems.

First, when different scales measure the same thing, they cannot be compared. Trials for pharmacological interventions for depression (like antidepressants) often use observer-rated scales. These scales require a skilled observer to rate depression severity along several dimensions following an interview that asks the patient about their interest in social activities and whether they’ve been sleeping, but without directly asking patients to rate those quantities themselves. For example, Depressed Mood may be judged by the observer to lie on a scale of severity from absent to sometimes to only feeling this state. In comparison, trials for behavioral interventions (like cognitive behavioral therapy) often use self-rated scales in which patients rate the severity of each type of dimension themselves. With different measures, it’s not possible to compare the effectiveness of the two different types of interventions. What we need for depression is the same thing we need for temperature: a well-agreed-on way to measure depression that we arrive at through standardization.

The second problem highlights the issues with adopting measures prematurely. Insofar as the field of depression has a standard, it is the HRSD, developed in the 1960s. The spirit behind preserving an old scale is that the outcomes of studies performed today can be compared with studies from earlier decades. The problem, however, is that the HRSD scale has flaws, such as weighting different symptoms (like depressed mood, guilt, and suicidal ideation) equally with the presumption that they all “matter” for depression to the same degree (as opposed to determining that in a principled way). As described by one group of researchers, “Since the HRSD was published over half a century ago, scientists put a man on the Moon, invented the internet, and created powerful computers small enough to fit in people’s pockets. Yet, the HRSD remains the gold-standard scale for depression, used in over 90% of antidepressant trials.” When measures are standardized and not allowed to evolve, we are obstructing epistemic iteration.

In 2019 a group of public and private funding agencies banded together to create a committee to discuss standardized measures for depression—an analog of the 1776 Royal Society Committee for temperature standardization. In considering different depression scales, they prioritized ones that are freely available, shorter scales that can be administered quickly, and scales that have been proven to measure meaningful quantities for mental health. The group arrived at three scales for depression: two for adults (older than 17) and one for children and adolescents. They also adopted the DMS-5 cross-cutting assessment to measure mental disorders broadly, an assessment of disability, and demographic information about sex at birth and age. Funding agencies in Canada, the United States, Australia, and the UK have agreed to make adopting the measures a condition of funding. Several journals have also agreed to support the effort by strongly encouraging authors to adopt them (or explain why they cannot). It’s a big step forward for the standardization of depression measurement.

Even so, the group emphasized that these measures need to be assessed and allowed to evolve continually, as there are known problems that will need to be solved over time. For instance, some questions depend on culturally relevant contexts, such as poor appetite and overeating. In addition, the validity of the measures has been tested much more extensively in higher-income countries, and their validity in other contexts is not well known. The group wisely acknowledges the need for epistemic iteration: “The first set of common measures were not selected to confer a higher status on individual scales, but rather to ensure that researchers are at least asking some of the same questions.”

The absence of standardized measures for depression has made it difficult to combine data across different studies. The dream for depression research is something analogous to what has happened with protein crystallography: a central database to which all results in the field are uploaded and can be compared because they are based (at least in part) on the same measures. In the era of big data and the power of machine learning, standardization of measurement is an important first step toward developing theories about what depression is.

Part of the rationale behind the standardization of measurements for things like depression is that having a lot of comparable data is useful. Today, the data on depression (and so many other things) is coming in at an unprecedented pace. Along with measures of depression itself, we have measures of its many possible causes: genomics, brain activity data, health status, exercise, diet, socioeconomic status, recent life history, and longer-term life history (to name a few). Circling back to chaos in the brickyard, those bricks (à la data) are piling up quickly! Setting aside for a moment the question about how we plan to turn those bricks into edifices, what considerations should we be mindful of in the measurement effort as we shift away from thinking about the brain as a domino chain and toward thinking about it as a complex system?

First and foremost, it’s important to remember that a complex system’s emergent properties happen via interactions between its parts, and they cannot be predicted from the parts in isolation. On one hand, that is a pretty trivial statistical statement: if X and Y interact nonlinearly, you need to study them simultaneously (not one at a time). Let’s say something happens only when X and Y are both “on”; you won’t figure it out if you first flip X on (and then off) and then flip Y on (and then off). On the other hand, it’s worth emphasizing that in brain research, causes are often measured one at a time rather than simultaneously. For instance, one meta review of depression found a remarkable 93% of studies published between 1980 and 2014 focused on a single causal variable for it (such as insomnia, financial stress, or genes); only 7% studied the interactions between two or more causes.

The take-home message here is that insofar as we are working with complex systems with properties that emerge from interactions between causes, we need to study the causes simultaneously (not one by one) as we pile up those bricks. And that’s largely not what we’ve been doing. In the case of brain activity data, it requires that the neurons and brain areas be recorded simultaneously (not independently). In the case of genetics, the same is true: genetic variants must be measured simultaneously for the same individuals (not independently across individuals). We must shift to making those measures simultaneously to build up effective data sets to analyze later.

The promise and pitfalls of epistemic iteration

Personally, as a brain researcher, learning about the history of temperature and Chang’s description of epistemic iteration has offered me reassurance against a type of existential angst that I didn’t even know I had. Looking back, I can see that I had internalized the assumption that each generation of brain researchers locked down understanding for some subset of things so the next generation could move along to other things; I envisioned that this was how global progress was achieved. But as the years passed, I began to intuit that this was not what was happening. While the accomplishment of facts collected and papers published cannot be disputed, it’s hard to find evidence of understanding and progress. On pessimistic days, one might begin to suspect that what’s happening is, in fact, chaos in the brickyard. We are deconstructing the brain into many piles of bricks, for sure. But to what end? Where are those edifices? What understanding are we really locking down?

Epistemic iteration takes a different perspective, suggesting that progress in brain research happens by making our best guess, trying it out, and refining from there; it is through refinement that the generations build on one another. For me, epistemic iteration softens the blow of realizing that, as brain researchers, we’ve been oversimplifying how we think about the brain. It reassures us that getting things wrong (or at least incomplete) before we get them right is an expected part of the process; the fact that we are not getting things right out of the gate does not imply that those efforts and developments are wasteful (as those amazing engram experiments illustrate!). There are good historical and philosophical reasons to expect that progress will emerge as long as we proceed thoughtfully.

Among those thoughtful next steps is keeping in mind the scenarios in which epistemic iteration might not work. The process rests on the assumption that a good initial guess is good enough to make an advance. But the process might get stuck if this guess is not even in the ballpark. Researchers call it a local minimum, an idea that draws from powerful analogies from mathematical modeling.

Mathematical models have parameters, and the goal of fitting a model is to find the best set. For a given set of parameters, you can compute how poorly a model fits some data, called its error. You might think of the data as some points and the model as a line that attempts to fit through them; the error is a measure of how far the points are from the line. Finding the best parameters for a model involves starting with a guess and then gradually changing parameters to see if a different set has less error. This happens iteratively until no better parameters can be found. This process amounts to traversing down the error surface until you find the bottom. The ideal scenario is one in which the error surface traced out by different parameters is like a bowl with a single lowest point—this is true for simple models. However, the error surface of complex models can be bumpy and full of valleys and peaks (fig. 12). This is where the idea of the local minimum comes in: if you start near one of those valleys and slowly change your parameters, you’ll iterate your way into a local minimum and get stuck there instead of converging on the best solution. In other words, the best set of parameters lies elsewhere entirely. Analogously, if brain researchers start with their best guess about how something works, it might be so far off that they spend all their time refining their way into a local minimum. In this scenario, the real answer lies somewhere they don’t think to look.

FIGURE 12. How to prevent epistemic iteration from getting stuck in a local minimum. Epistemic iteration can fail to converge on the right answer for reasons analogous to the reasons model fitting can get stuck in a local minimum. Model fitting begins with an initial guess of the parameters (analogous to how disorders are characterized in the DSM). Next, the parameters are adjusted to determine the best ones by marching down the error gradient. If the error surface is bumpy, the process can get stuck in a local minimum and fail to converge on the best parameters (analogous to a disorder that is misunderstood). One way to prevent this is to start with multiple guesses and determine which leads to the smallest error (analogous to pluralism). Adapted from Kendler, K. S. Epistemic iteration as a historical model for psychiatric nosology: Promises and limitations. In Philosophical Issues in Psychiatry II: Nosology, ed. K. S. Kendler & J. Parnas, 306 (Oxford University Press, 2012).

The idea of getting stuck in a local minimum comes up in psychiatry. There, researchers are concerned that many of the psychiatric diagnoses described in the DSM “aren’t even in the ballpark” with regard to grouping patients with the same causes. If that’s true, refining them through iteration won’t help. How do we avoid the pitfall of local minima? Circling back to the model-fitting analogy, this problem is avoided by starting with many different initial guesses, or equivalently, from many different positions on the error surface, to see if they all converge on the same solution (and if not, picking the one with the least error). By extension, philosophers like Chang emphasize the importance of pursuing different paths toward understanding the same question, a commitment to pluralism. The gist behind pluralism is not just to pursue one account but to go after as many good accounts as possible.

a The engram experiments were also performed in a nearby brain area, the amygdala, which stores memories about threat-related associations such as when a tone is followed by a light shock.

b The researchers involved in this study caution that precisely where each of these states falls relative to the knife edge may reflect some measurement error. As such, the notion that LSD drives the brain closer to the knife edge needs more consideration and replication.

CHAPTER 7 What causes what?

The second and third main goals of science are intertwined: to understand what causes brain function (and dysfunction) and to predict its future course. So much of understanding and prediction revolves around the question: What causes what? To understand the depression that is afflicting an individual, we want to know what caused it. And likewise, to predict a future depressive episode, we need a model that captures those causal influences. When working with a domino chain, pinpointing causes and creating predictions is pretty straightforward: A leads to B leads to C (and so on), and the goal is to pinpoint A, B, and C. In comparison, as we shift toward thinking about the brain as a complex system full of feedback loops, we’ll have to rethink how to approach causality (and thus understanding and prediction) entirely.

To illustrate the challenges involved in this shift, let’s consider for a moment: What will it take to stop the US opioid epidemic? The rise of illicit opioid use and opioid-related deaths is staggering: in the 20 years from 2001 to 2021, the number of annual opioid-related deaths per year rose 7.5-fold. Presumably, figuring out how to stop the trajectory of this epidemic involves answering the question: What is causing the rise in opioid addiction? If you ask a brain researcher who studies neural circuits, they will tell you that the powerful synthetic opioid drugs available today (like fentanyl) hijack the brain’s system for regulating motivation and action in two ways: by directly binding to mu-opioid receptors (in a brain area called the nucleus accumbens) as well as by triggering the release of dopamine and in turn plasticity that reshapes neural circuits; this leads to intense future drug craving. But if you ask a geneticist, they will tell you that there’s more to it than just that, given that around half of an individual’s vulnerability to addiction is tied to genetic variation. A social worker will chime in that the current US opioid epidemic can’t just be about biology, given its clear association with social isolation, poverty, and trauma. A lawmaker will argue that the opioid epidemic would never have happened if large pharmaceutical companies hadn’t pushed so many drugs in their efforts to chase profits. All these answers are valid; there is no singular thing that “causes” opioid addiction. Moreover, all these causes are important for thinking about ways to prevent and treat addiction; we cannot just focus on, for instance, the opioid receptor and expect to solve the problem. But how do all these different causes fit together? Should we consider them overlapping causes that manifest in different ways (perhaps at different levels)? Or are they distinct causes?

In a complex system, the challenge of clear-headed thinking about causality is exacerbated by circular loops, when causes become effects that circle back as causes. In the case of addiction, the brain gives rise to the drug-seeking mind, and once sought, the drugs affect the brain’s biology to reinforce drug craving. To treat addiction, we have to appreciate that those feedback loops exist, and we have to find ways to break them. But when feedback happens, teasing apart causes and effects can be a challenge. Let’s circle back to our example of the lynx and rabbit ecosystem, where population fluctuations of lynx and rabbits are heavily intertwined. In this ecosystem, the “cause” of the oscillation in the numbers of both species is a bit hard to describe because it’s an emergent property that follows from the interaction between predator and prey. Arguably, the best way to capture causes in this ecosystem is to build a model that simulates it and then do our best to wrap our heads around how that model works.

The challenge of thinking about causality is exacerbated by the fact that many of us (including brain researchers) have unknowingly internalized different meanings of what causality is. Here, I’m not referring to the well-trodden ground of confusing correlation with causation—for instance, while the rooster always crows right before the sun rises, the rooster does not cause the sun to rise. Rather, I’m talking about causality proper: cases in which things (or events) actually do give rise to other things (or events). It turns out that some notions of causality align pretty squarely with domino chains, whereas others better align with ideas about complex systems.

Let’s imagine the following scenario: researchers are interested in understanding what happens in our brains that allows us (or causes us) to read visual text. In their investigations, they find that one of the first brain areas in the visual system, V1, is activated in an fMRI scan when people read. Researchers also find that people can no longer read when this brain area is damaged. Does V1 “cause” reading? Some brain researchers argue, perhaps but not necessarily, because it could be that another brain area is actually responsible for what needs to happen for us to read, and V1 does something simpler (like act as a relay station that reading information passes through). Other brain researchers argue yes, absolutely—anything that can affect an outcome (through perturbation, not just correlation) has a causal influence on it. These groups of researchers are clearly tapping into different ideas about causality. What’s going on here?

The first group of researchers is tapping into a concept called causal production—the idea that what we want to do in brain research is pinpoint the things that generate or bring about other things. In the case of reading, we are interested in brain areas like the human visual word form area, which transforms simple shapes into letters and words, and Broca’s area, which supports language comprehension. In comparison, we aren’t interested in V1 because, while it serves as a bottleneck for visual input in the brain, processing there doesn’t support reading any more than other types of seeing. This distinction is often referred to as the difference between “necessity” (V1) and “causality” (Broca’s area). The distinction is important for understanding why some people without other visual deficits have trouble reading.

To take this example a little further, imagine that in an investigation of the causal influences on reading, someone stops reading because a bee stings them on the elbow—does this imply that the elbow is causally involved in reading? Or even the bee? That seems a bit silly. It would imply that understanding what causes reading involves documenting every possible thing that can distract someone from it—floods, fires, and loud noises would all “cause reading” by this definition. Clearly, an exhaustive account of all possible “causes” under this definition is not what we are trying to accomplish in brain research.

Causal production is the type of causality that many brain researchers have internalized. While the logic might appear to make tremendous sense, other researchers argue that it is important to use a broader definition of causality: anything that has an impact in any way. This is known as causal dependence.a Under this definition, V1 is causally involved in reading because, without it, you can’t read visual text. Distractions like bee stings are also causal for reading. While it may seem a bit far-fetched, this more expansive definition is motivated by the notion that there needs to be some concept of causality that captures all possible things that have an influence—it’s the notion that things are causal or not. Practically, this matters in brain research because it leads to a more complete list of potential targets for therapeutic treatments. Some of those targets will be the ones involved in “production”—dysfunctional circuits that can be modified using, for example, therapeutic brain stimulation. Some effective treatments, however, will not act through production at all—for example, minimizing distractions might be part of an effective treatment for an individual with ADHD.

The notion that one or a few “special causes” “produce” things is not a good account of complex phenomena. There is clearly no singular thing that “produces” addiction. Insofar as addiction emerges from a complex system, it follows from interactions between different causes. As such, when working to develop preventions and treatments, we cannot just focus on any one of its causes in isolation.

In light of these different definitions, how should we best think about causality? Neither definition seems quite right insofar as neither really captures what we want to know. The problem with causal production is that it’s too limited; it leads researchers to oversimplify and implicitly adopt positions like the fallacy of the single cause: the idea that there is one or a few “most important” causes to be extracted; this is not a good account of complex phenomena (like opioid addiction). But the problem with the second definition, causal dependence, is that it’s too broad to be useful—clearly an exhaustive documentation of all possible influences is not what we are after (as the bee sting while reading example illustrates). So what are we after with regard to causality in brain research?

As we work to answer that question, it’s useful to highlight that our first definition, causal production, reflects something close to a domino chain way of thinking about the brain; it presumes that there will be one or more important “dominos” that cause things (like brain function and its dysfunction). As we shift toward appreciating that the brain is not composed of domino chains but rather complex systems, we will need to abandon this type of thinking. But it’s also a mistake to assume that the only alternative is to exhaustively document causal influences. It turns out that asking “if” things are causal is the wrong question. Instead of “if,” what we are really interested in is how causal influences interact.

To get to how, we need to create mechanistic models rather than lengthy yes/no checklists. Some influences might be linked to the same phenomenon, across levels—for example, in Huntington’s disease, a genetic mutation leads to a mutant protein that triggers a type of neurodegeneration and loss of function. Or there might be many different types of causal influences that interact across levels, such as when genetic predisposition and poverty interact to cause addiction. Models can reflect how causes interact quite well, though creating a good model can be difficult. By definition, a model needs to simplify the phenomenon in question—we aren’t interested in capturing everything about reality (like every molecule’s position)—but at the same time, a model needs to be complex enough to capture the causes underlying the phenomenon we are interested in. Getting that balance right is one of the big challenges, but once we have good models, they can help us create new treatments for brain dysfunction.

To illustrate how this might work, let’s focus on a problem we’ve already begun to puzzle through: opioid dependence and addiction.

Finding ways to treat opioid dependence and addiction

In his memoir In Pain, the bioethicist Travis Rieder describes his experience with opioid dependence. Like so many others, his battle began with a painkiller following an accident. Later, his withdrawal experience was terrible. As he describes it, “I came to truly understand something that I had only abstractly known before: I now understood clinical depression, and the way in which each of us, despite our sense of being an ethereal, mental being, is lashed to a physical body that can malfunction. My brain was malfunctioning, and multiple times per day it would send me to the darkest place I’ve ever been.”

Rieder’s experience began with a motorcycle accident and horrible damage to his left foot. Like many others, Rieder felt some pain right away following the accident, but the intense pain was not immediate—that was still to come. In that way, pain is a bit different from other senses, where a “stimulus” leads to a “percept”—given a visual input, you immediately see a picture; given an auditory input, you immediately hear a sound. In contrast, mangle your foot, and some sense of pain will be immediate, but the intense pain will take some time to kick in.

The sensory receptors that trigger the sensation of pain are nociceptors, embedded in the skin and other organs. When activated, they send a signal down their fibers to activate neurons in the spinal cord to send signals to the brain. Different types of nociceptors send signals at different rates: some are fast (immediate pain), and others are a bit slower (throbbing pain). Another cause for the delay is that damaged tissue takes time to swell, and swelling activates more nociceptors. But these factors alone don’t explain why it takes time for the sensation of pain to ramp up, because pain isn’t just about what’s going on with these nociceptors. The experience of pain can lead to an increasing spiral of pain sensation that becomes difficult to control, even with large doses of intense pain medications. Pain specialists understand that this spiraling exists, even though no one understands why. They know that it’s important not to “get behind the pain” and will often use pain drugs (including opioids) to stay ahead of it.

The opioid drugs are by no means new—morphine, oxycodone, and codeine were all originally derived from opium, a drug that has been around for thousands of years. The Sumerians cultivated it in lower Mesopotamia as early as 3400 BCE. Opium is derived from the poppy plant Papaver somniferum, which also produces poppy seeds. It’s created by slitting the poppy’s immature seedpods and drying the emerging viscous white fluid. That type of raw opium was used in medicine throughout the early 1800s. Its effects are attributed to a handful of chemically similar but distinct compounds, including morphine, codeine, and thebaine.

While opium itself was used medically in the early 1800s, the problem with it was that different batches were inconsistent in terms of power. The search for something more reliable led to morphine, first extracted from opium in 1804 and poetically named after Morpheus, the Greek god of dreams. The isolation of codeine from opium followed soon after morphine, in 1832, and oxycodone followed in 1917. In contrast to morphine and codeine, oxycodone was created not simply by isolating a substance already present in opium but by modifying one of those substances, thebaine. The modern drug OxyContin, approved by the FDA in 1995, is simply an extended-release form of oxycodone that allows for dosing every twelve hours as opposed to the more frequent dosages required for earlier formulations.

Opioid drugs act in a few different ways to relieve pain by tapping into the endorphin system, a class of chemicals created in the pituitary gland and hypothalamus. Endorphins are released when you are injured and during extensive exercise—they are the chemicals responsible for the “runner’s high.” Opioid drugs operate by binding to the receptors that exist for the endorphins to work, called opioid receptors. To alleviate pain, they do not reach back to block the activation of the pain receptors (the nociceptors) themselves. Instead, they bind to opioid receptors in the spinal cord, which blocks the transmission of pain signals to the brain as well as within the brain itself. This is why local infusion of morphine into the spinal cord can be an effective pain treatment for some patients.

Opioid drugs are quite effective at alleviating many types of pain. The problem with them is that they also can lead to tolerance, dependence, and addiction. Tolerance happens when the same amount of drug becomes less effective—it’s a bit unclear how this happens, exactly, but it involves some sort of adaptation, where more drug is required to trigger the same effect downstream of where the opioid binds to opioid receptors. When opioid tolerance happens, all sorts of systems readjust themselves, including sleep regulation. Following a reduction or sudden removal of the drug, it takes a while for everything to adjust back. During this time, an individual who is dependent on taking the drug needs to slowly taper the drug down to minimize withdrawal symptoms, which can include dreadful experiences like severe insomnia, vomiting, alternating sweats and chills, and depression—all symptoms that Rieder experienced. This type of tolerance is a good indicator that opioids are not part of a domino chain but rather a complex system that is continuously adapting.

One of the trickiest things about opioid drugs is that they can cause not just dependence, but also pleasure and craving. This happens because these drugs interact not only with the brain’s pain system but also with its midbrain reward system. This reward system is thought to orient us toward things that are good for survival, like food and sex (and exercise), by making them pleasurable. But this system did not evolve in a world where opioids and other drugs were easily accessible, and it wasn’t designed to be robust for the types of massive rewards that happen when you (say) ingest opioid drugs. When drugs bind to mu-opioid receptors in this part of the brain, it triggers the sensation of intense pleasure. It also triggers the release of dopamine and, in turn, plasticity, which is thought to lead to future drug craving. Other drugs, like cocaine and amphetamines, act in a similar way. When those cravings drive an individual to continue to use the drug despite negative consequences, that’s when we declare it an addiction.b

Biological insights into addiction have led to what is known as the “brain disease model of addiction,” which views addiction as a chronic disease akin to diabetes. The gist behind it is that a vulnerable brain gets hijacked by addictive drugs, making drug-related behavior increasingly less voluntary, leading to a loss of free will. When recovery happens, the brain remains sensitized, leading to chronic risk. Proponents of that idea argue that the case for it is pretty straightforward: insofar as our brains produce all our behavior, addictive behavior must also be produced by the brain. Moreover, we understand a lot about the circuits involved, and there’s clear evidence that our genes contribute to genetic risk for addiction. They argue that viewing drug addiction as a disease goes a long way to destigmatizing it—after all, if someone has a disease, it’s typically not their fault.

Others vigorously oppose this idea. Opponents point out that it’s a hypothesis that we have yet to find definitive proof for: we cannot look at the brain of an individual or give any other type of biological test and determine whether that individual is addicted. Moreover, they argue that while the brain disease model of addiction might be destigmatizing, it’s also disabling insofar as it denies the control and agency that individuals have over their addiction, which is central to their recovery. They also argue that the brain disease model of addiction directs research toward investigations of the brain and away from psychosocial factors such as employment status, racial discrimination, neighborhood characteristics, and policing. From 2000 to 2015, “deaths of despair” more than doubled in the United States (but not in Europe, Canada, Australia, or Japan), and the largest contributors to those deaths were suicide and drug poisoning related to drug addiction. The factors leading to this alarming difference between the United States and other countries are thought to be linked to increasing inequities in the United States, particularly in rural communities.

As an alternative to (or an elaboration of) the brain disease model of addiction, a different perspective views addiction through the lens of complex systems as a dynamic interaction of biological, psychological, and environmental factors. One advantage of such a perspective is that it allows for reciprocal interactions between the brain and the environment in a way that can destigmatize (by acknowledging that biological factors like genetics exist) while also allowing for the agency required for recovery. In an exclusively domino-based perspective of addiction, the goal is to break the feedforward chain. In a systems perspective, the mind and the environment can both feed back to affect the brain, and as such, it’s as essential to evaluate environmental influences as targets for intervention.

Dynamical systems accounts of opioid addiction have been used to evaluate the outcomes of possible interventions. Researchers create models that capture how different causal influences on addiction interact within a community (like access to drugs as well as access to addiction therapies) and then use those models to make predictions of what will happen if different interventions are applied.

While prescription opioids account for a small subset of opioid-related deaths (in the United States, 8% in 2021), the bulk of these deaths (and their rise) follow from synthetic and illicit opioids like fentanyl. In 2017 the White House declared that the opioid crisis had become a public health emergency, and Congress allocated funds to find a way to stop it. As part of that effort, the “HEALing communities study” was launched to find ways to reduce opioid-related deaths in local communities by 40% over 3 years. Teams competed for funds by submitting plans about how to accomplish this ambitious goal via combinations of programs and interventions. The funds to execute their plans were awarded to teams in four US states (Kentucky, Massachusetts, New York, and Ohio). While each team had a slightly different plan, they largely converged on overlapping evidence-based approaches, including access to medications used to reduce drug craving (like methadone and buprenorphine) that work by binding to the same opioid receptors that the opioid drugs themselves do; they do so in a way that the effects are weaker and do not lead to euphoria. For drugs like these, however, the success of long-term compliance is mixed—about half of the people who use these medications relapse. Thus, the plans also included increasing access to naltrexone, a drug that can reverse the effects of opioids during an overdose, as well as increased preventative measures such as physician education and prescription drug monitoring.

The teams set out to execute their ambitious plans in 2019. Tragically, these plans were then dramatically disrupted when the COVID-19 pandemic hit in the spring of 2020, leading to increased social isolation, more limited access to treatment, and increased drug use. While the research teams did their best to find solutions (such as pivoting to delivering treatments via telehealth), opioid-related deaths in these communities did not fall but continued to rise, leading researchers to reevaluate how to best proceed.

To figure out the best path forward, researchers went back to the models, now focused on predicting the impact of different interventions in the new reality following the pandemic. Their models did not presume a simple domino chain causal structure (such as treatments lead to recovery lead to reductions in death) and did not focus on a single type of treatment (like medication to prevent craving). Instead, they allowed for complex and dynamic interactions between recovery and relapse in different populations as well as interactions between different types of interventions, which would be difficult to predict without a model. The success of the model was verified, in part, by its ability to predict changes in opioid-related deaths with time.

The model was then used to evaluate future outcomes under different “what would happen if” scenarios. One overarching insight that researchers took away from this effort was that the interventions on the table were expected to have only a modest impact on opioid-related deaths (decreasing them by <20%), and the gains would be lost when the programs were over. To achieve a more ambitious goal of a 40% reduction in deaths, the model predicted that communities would need to extend the program by 1 to 3 years and increase the number of individuals taking medications by fivefold. These are substantial changes to an already ambitious program. As one researcher concluded, “We’re in the middle of a public health emergency. It’s time to act, and the scale of those efforts must be at a much higher level than what we have seen so far.”

The outcome of the HEALing communities initiative is, of course, extremely disappointing. Despite its sizable price tag ($350 million), it failed to meet its ambitious goals—in part due to complications following COVID-19. That said, with the models that emerged from the project, we are now empowered to find better solutions going forward. Notably, those models could not have been created without the project because they rely on the data collected by it (to quantify the impact of different interventions). It’s this iteration between models and data that will help us to find the right interventions—those that actually have a good chance of working. Ultimately, it is likely that complex dynamical systems models will be instrumental in solving the US opioid epidemic.

Leveraging shadows

In the pursuit of understanding and predicting complex systems, the approaches I’ve described so far focus on creating explicit models of phenomena (like opioid-related deaths) based on knowledge about how the variables they depend on (like access to drugs to reduce craving and physician education) interact. However, this is not the only way to go about it. Remarkably, when working with a complex system, one need not necessarily involve a model at all, and both inferences and predictions can still be made (at least in some cases). This fact follows from the seeming magic of a theorem established by the Dutch mathematician Floris Takens in 1981. If we assume that the brain operates as a complex dynamical system where interactions between its variables change as the behavior of the system does, it turns out to have an exceedingly nifty property: information about how one causal variable fluctuates over time contains information about how all the other causal variables fluctuate, reflected as “shadows.” This means that you can reconstruct the entire system just by measuring how a single variable changes over time. This counterintuitive ability has been coined “the flip side of chaos,” and it has all sorts of important implications. Among them, you can make future predictions without building an explicit model of the system and—shockingly—without even pinpointing what all the causes are. While brain researchers have only begun to leverage the power of this theorem, ecologists have been using it for decades.

One example involves predicting the number of sockeye salmon that will return from the ocean to spawn in Canadian rivers. In the 1950s and 1960s, researchers noted that the number of salmon returning to spawn was inversely correlated with Pacific Ocean temperatures in any given year—colder ocean temperatures meant more fish in rivers. It was such a great predictor that they began to use it as a guide to set fishery catch limits ahead of each season. But in the 1970s the correlation between ocean temperature and fish numbers disappeared, as if it were a mirage. Clearly, temperature was not the only variable at play. Researchers attempted to pinpoint the other factors, such as the ocean conditions the juvenile fish returned to before they came back to spawn. However, incorporating those variables into forecasting models did not improve the predictions.

A team of ecologists and mathematicians led by George Sugihara were among the first to determine how to improve fishery forecasts, building on Takens’s theorem.c The team recognized that the number of salmon returning each year might be caused by several things that might interact with one another. Still, all the information about those causes could be captured (in principle) by a measure of how just one of them fluctuates over time. They realized that they could reconstruct the system by focusing on the relationship between time-delayed versions of those measurements; because of the nonlinear interactions between causal influences, when the system lands in the same “state,” it tends to follow the same trajectory. And once that trajectory was mapped out, accurate forecasts could be made. When applied to predicting the numbers of spawning salmon, the approach was far better than existing models.

As described by one fisheries researcher in 2009, this new type of approach was disconcerting to other researchers when first introduced: “In fisheries, the classical approach is to model populations based on first principles. We know how fast [individual fish] are growing, how fast they are reproducing, how old they are when they mature, how many babies they have. George’s approach is an entirely different one. He looks at past behavior to see if he can predict future behavior.” That’s the seeming magic. Sugihara’s approach (called empirical dynamical modeling) has worked for predicting when the red tide will happen off the coast of Southern California, the impact of climate on the transmission of dengue in Puerto Rico, water flow in the Florida everglades to help with restoration efforts, and many other things.

In addition to forecasting where a system will be in the future, Sugihara and his team have used Takens’s theorem to infer whether and when different variables are causally related. For instance, the numbers of both sardines and anchovies vary with time, and one tends to peak while the other is low, leaving researchers to wonder: Do they somehow interact directly with one another, perhaps via some competitive ecosystem relationship? Using conceptually similar approaches to the ones used for forecasting, they could tease apart correlation from causation, and through this they determined that the two populations do not strongly interact. Instead, they both strongly interact with a third variable, sea temperature. The interpretation here is that temperature influences how these fish populations will fluctuate or is a proxy for something that drives population fluctuations.

Brain researchers have taken this approach, called convergent cross-mapping, to help solve a problem associated with brain stimulation therapies. As we’ve discussed, brain stimulation is a causal intervention that works by perturbing brain activity. It often requires placing stimulating electrodes in precisely the right place, but it’s not always clear where that is—the difference between “right” and “wrong” can be less than a millimeter. One way to find the right place is to implant a device with many electrodes and try them out one by one. But that can be problematic for a few reasons—among them, sometimes the effects of stimulation take weeks or months to kick in, and trying them out one by one can take a lot of time. In some cases, stimulating in the wrong place can even be dangerous. Is there a way to do this without stimulating the brain? This question boils down to predicting causality: If I stimulate this electrode, what effect will that perturbation cause?

To predict which brain stimulating electrodes will cause the biggest effects, researchers applied convergent cross-mapping. They implanted a device containing ninety-six electrodes into prefrontal cortex of a monkey, with the goal of predicting what would happen to the monkey’s brain activity if brain stimulation was delivered through different electrodes. Importantly, they wanted to predict these effects before performing any stimulation—simply by observing normal brain activity recorded on the electrodes alone. The nifty trick here is that as long as brain activity on different electrodes is strongly coupled, you can infer which electrodes are aligned with the neurons that have the strongest causal influence on the other neurons. The idea is that those are the neurons you want to stimulate to have the biggest effects. Indeed, this is exactly what they found. These are critical first steps toward applying this approach in humans as they are fitted with deep brain stimulation devices. No doubt, convergent cross-mapping will also be used in many other applications in brain research going forward.

Predicting tipping points

So far, we’ve discussed a few ways to forecast a complex system. One way involves building an explicit model of how it operates; this is how weather forecasting works. Likewise, a model of opioid addiction can be used to forecast the consequences of different types of interventions. In some cases, these model-based approaches can and will work. But will we ever be able to reduce the complexity of the brain down to a smallish number of variables that we can measure in an individual, plug into a model, and use to forecast where their brain will be in 2 days or 2 weeks? That’s unclear.

Other ways of forecasting do not involve a model at all and may ultimately be more useful for understanding the brain. We’ve described how model-free approaches that have been used to understand ecosystems have shown some promise when applied to predicting brain activity using brain stimulation. But the degree to which these methods will be ubiquitously useful in understanding the brain is not yet clear. A complementary, less restrictive approach tries not to predict exactly where a system will end up (like the temperature tomorrow) but instead measures the chance that a big transition is about to happen—like an ecosystem collapse. This same method can be used to predict brain dysfunction—for instance, when a seizure or a depressive episode will happen. It works whenever a complex system shifts suddenly after reaching a “tipping point.” These types of systems exhibit generic signatures when they are about to undergo a sudden change between regimes, regardless of the system’s details, and these signatures are relatively straightforward to measure. For this approach, we can also thank the ecologists.

How does this method work? It builds on the idea of attractor states—energy basins that a system falls into, subject to small perturbations. Recall that we can envision these states as valleys into which a ball can roll and get stuck. When the system is not near a tipping point but is instead resilient and stuck in a deep attractor, the response to perturbations (the ball’s wiggles) will happen fast due to the steep slope, but they also won’t go very far (fig. 13a). In other words, the responses are shorter in duration and have lower variance. But before a big shift, the system exhibits a loss in its resilience, the attractor basins become shallow, and the system becomes more susceptible to being tipped into the new state. In other words, when the system is near a tipping point, the same sized nudge will move the ball more sluggishly, but farther—or equivalently, will produce responses that are longer duration and higher variance (fig. 13b).d The shift from the less sluggish state far from a tipping point toward the more sluggish state close to one is a signature of “critical slowing down.”

In ecology, these ideas have been applied to predict shifts in rangeland, fish, and wildlife, including when locusts will swarm. They’ve also been put to the test in laboratory experiments where researchers can impose causal manipulations on, for instance, colonies of cyanobacteria. These bacteria grow in clusters and at moderate light levels, and the bacteria themselves provide the shade required for their own healthy growth—a colony clustered together can withstand more light than when the bacteria are dispersed. In this system, an attractor is created via a positive feedback loop from bacteria providing their own shade. At some light level intensity, however, this mechanism no longer works, the system reaches its tipping point, and the colony collapses. To see if they could predict when this tipping point was about to happen, researchers induced perturbations by flushing away some of the colony with a solution and measuring how it recovered. Crucially, the tipping point could be predicted by the critical slowing down of the population, measured by the sluggishness with which the density of the cyanobacteria colony recovered from flushing perturbation.

FIGURE 13. Critical slowing down. a) The energy landscape of a high resilience state, far from a tipping point. Here, responses to small perturbations (reflected by the ball’s wiggles) are short duration and low variance. b) The energy landscape of a low resilience state, close to a tipping point. Here, responses to small perturbations are longer in duration and higher variance. Adapted from Scheffer, M., et al. Anticipating critical transitions. Science 338, 344–348 (2012), with permission from AAAS.

In brain research, the same idea has been applied to forecast seizures. While therapies like medication and brain surgery can help individuals reduce the frequency and intensity of their seizures, they sometimes cannot stop them altogether. When severe seizures happen, medications must be administered at or near the time of a seizure to ensure that they don’t lead to brain damage (and possibly death)—but these drugs have sedative properties, so they cannot be taken continuously. Individuals with epilepsy report that the unpredictability of their seizures is one of the most concerning issues they face.

The ability to forecast when a seizure will happen requires that seizures aren’t just triggered spontaneously, but that the brain somehow ramps up to one for hours or minutes before it happens. Plenty of evidence suggests that this is often the case. Some patients can tell when a seizure is a few days away, but generally not when it is minutes away—which is when seizure drugs would need to be administered. The rising phase of a seizure is referred to as its aura, and it can occur hours or days before seizure onset. For a small fraction of patients, like the author Fyodor Dostoevsky, the auras induce “such happiness as is impossible under ordinary conditions, and of which other people can have no notion. I feel complete harmony in myself and in the world and this feeling is so strong and sweet that for several seconds of such bliss one would give 10 years of one’s life, indeed perhaps one’s whole life.” For other individuals, the aura can evoke a sensory sensation like a smell, taste, or color; a memory; or déjà vu. This suggests something is happening in the brain leading up to a seizure. How do we tap into it and transform it into a prediction to alert an individual when a seizure is about to happen?

Broadly, it’s important to appreciate that the goal of seizure forecasting is not to create a single fixed algorithm and apply it to all individuals, like “sum the activity on electrodes 6 and 9 and average it with heart rate.” This is because the most predictive features are different for different people—for some individuals, the time of day will matter, but for others, it will not; for some individuals, all the electrodes will be informative, but for others, they will not. Instead, the goal of seizure forecasting should be thought of as figuring out an algorithm that can be adjusted for each individual. One way to accomplish this is to leverage measures of critical slowing down. Let’s take a closer look at how this works.

A small but important seizure-forecasting clinical trial took place in Australia in 2010. In it, fifteen patients were implanted with intracranial EEG recording devices that would record brain activity continuously and would ideally predict when a patient was about to have a seizure. Data were collected from each of those fifteen patients for 185–767 days, during which over a total of 2,500 seizures happened. Seizure prediction in this trial was not wildly successful, but it gave researchers the extremely valuable data they needed to create new ways to forecast seizures.

In a more recent study, researchers applied the approach of critical slowing down to the very long EEG recordings collected during the Australian clinical trial. They measured critical slowing down as the sluggishness of the naturally induced EEG fluctuations and their variance. In the data, they found evidence for two types of rhythms. First, critical slowing down fluctuated along timescales of minutes and had a daily rhythm. Second, it also fluctuated along longer timescales of days to weeks. The researchers combined the two types of rhythms to determine a seizure prediction algorithm for each patient that classified the degree of seizure risk. Their algorithm did a better job at predicting when seizures would happen than any of the algorithms that came before it, correctly predicting around 80% of seizures that did happen (as high risk) and misclassifying less than 10% of seizures that occurred (as low risk). It’s a big step forward. Conceptually similar approaches have been applied to measures of psychological variables (like emotions) to predict when an individual will enter or exit a depressive episode.

Stepping back, the approaches described here for leveraging shadows and predicting tipping points are different from approaches used to predict the weather. Here, we don’t have an explicit model that is used to make these forecasts. Instead, researchers leverage the signatures of nonlinear dynamical systems and the predictability that follows from the “flip side of chaos.” Likewise, theories (like Takens’s) and tools (like convergent cross-mapping) that allow researchers to infer “what causes what” and tease it apart from correlations in complex dynamical systems are a huge step forward. For both understanding and prediction, throwing out the equations can be a fruitful approach. I expect that these nifty tricks will be widely deployed in brain research as the field shifts more and more toward thinking about the brain as a complex system, and how to treat it when it breaks.

Principles are beneficial; magic bullets are reckless

As I sat down to write this book, it was easy to get caught up in the awe, fascination, and excitement of it all: the idea that insights proven to be effective for understanding salmon runs and how cyanobacteria thrive can help us to also understand opioid addiction and depression. But those periods of excitement about complex systems were interspersed with sobering skepticism, and a voice in my head saying: So what? Ultimately, shifting to thinking about the brain as a complex system clearly matters, but how much does it matter? Will it really open some bottleneck to treatments? After all, researchers long ago appreciated that the weather, ecosystems, and climate are complex systems, and it’s not like we’ve definitively figured those things out.

Channeling that skeptical voice, it is worth appreciating that the shift toward thinking about the brain as a complex dynamical system has strong parallels to shifts that happened in other fields decades ago. In ecology, food chains became food webs, and by the 1970s the emphasis shifted away from specific elements toward the processes that stabilize and destabilize ecosystems. In the 1980s the Santa Fe Institute was founded to focus explicitly on the principles that govern complex systems of all types, from slime molds to human social networks. Circa 2000 a close cousin to brain research, cellular biology, shifted away from understanding genes in isolation to how they interact. In that field, researchers concluded that “The current paradigm in biology—variously described as ‘single gene,’ ‘reductionist,’ or ‘linear’—is not likely to be successful on its own.” Like in brain research today, there was a strong push to understand what was happening in cells as interacting parts configured into systems.

While we need to be careful about overgeneralizing, we also can learn a lot from the wins, frustrations, and conversations around complex systems in other fields across the past decades, starting with the criticisms. Two notable ones are reflected in a Scientific American article in 1995 titled “From Complexity to Perplexity,” which challenged how researchers at the time were going about what we’ve been talking about here: understanding and predicting the behavior of complex systems.

The first criticism focused on the notion that systems of different types (from the economy to ecosystems to immunology) share underlying principles. Taken to the extreme, the speculation is that complex systems will be governed by a shared set of grand unified principles, implying that the goal is to find them. In a less extreme form, it’s the notion that the lessons learned from studying one thing (like the economy) can be usefully applied to inspire progress in another field (like ecology). Much of the conversation around complex systems since 1995 has centered on the question: To what degree can insights into one system help us understand how others work? In broad strokes, the answer has turned out to be mixed (at least so far). There are useful principles that generalize across systems—some of which are highlighted in this chapter. At the same time, each system has also proven to be unique. From this, we might reasonably walk away with the suspicion that this might be true within the brain as well—while some breakthrough in understanding how motor function works might inspire insight about how feelings do, “solving motor function” will not automatically result in “solving mood.”

One good way to think about it might be analogous to how we think about termite mounds, where the shapes of mounds for different species are distinct. You’ve probably seen pictures of the tall mounds from the grasslands of southern Africa (of the genus M. michaelseni) that can grow to over 4 meters. But they aren’t all like that; other species of termites (like the genus C. cumulans) have mounds that are short and fat. The mound shapes of these different species are thought to emerge from a complex system shaped by interactions between the environment (specifically airflow) and the termites’ collective behavior (determined by the diffusion of pheromones throughout the growing mound). In climates with larger temperature differences between night and day (like the grasslands), there is more effective airflow moving the pheromones around, and this drives the termites to build taller mounds. But this interaction alone cannot explain the differences between termite mound shapes; you can’t put one species into the same environment of another species and expect to get the same shape. Instead, each species has evolved differently to conform to its niche. I expect that different brain functions (and their dysfunctions) will be similar insofar as they share some underlying principles but also have differences that mean they are not interchangeable. As such, the types of general approaches to understanding and prediction that we’ve discussed in this chapter will be helpful, but they should not be confused with some magic bullet that will unlock all the mysteries of the brain. We’ll still need to figure out how they work—or not—for each type of brain function and dysfunction, in turn.

The second criticism in the Scientific American piece questioned the act of creating models that can predict what will happen but are not based on explicit understanding of how a system works. Today that can happen in two ways: either by the model-free approaches I’ve described in this chapter or by training models via machine learning (like the models AlphaFold and AlexNet that we’ve already discussed). Either way, the concern is that while these approaches might be useful for prediction, they are not useful for understanding because they take us “from complexity to perplexity” (not insight). Fortunately, researchers working with complex systems today have started to figure out ways to move from perplexity to understanding, thereby shedding light on how the brain works.

To illustrate, let’s focus for a moment on how models of complex systems trained with machine learning have been used to understand the big mystery of how we can flexibly switch between making different types of decisions about the same information. Imagine viewing an old photograph with many people in it, and wanting to first find yourself and then find someone else. How does your brain flip between those two goals? The cartoon answer is that a little person somewhere in your head decides what you’ll look for and pulls a lever to make that happen; it’s what the philosopher Daniel Dennett called the “Cartesian theater.” Obviously, that’s not right. But how does it “really” work? This is actually among the biggest mysteries in all of brain research.

Studies of this question often use simplified visual stimuli with just two properties, like movement and color, which appear in different combinations on different trials. On some trials, individuals will be instructed to report motion (Is it moving right or left?); on other trials, color (Is it red or green?). In one study, researchers focused on brain activity in prefrontal cortex in monkeys who reported their decisions with an eye movement to one of two targets (a rightward eye movement for either rightward motion, on motion trials, or red, on color trials; a leftward eye movement for either leftward motion or green). But typical of the activity in this part of the brain, the activity of individual neurons reflected all sorts of different things in different epochs of the trial: variables like motion, color, the decision, and how far along the monkey was into each trial as well as complex and confusing combinations of these things. Even when considered from the perspective of combining the individual neurons into a population as a whole, it was difficult to figure out what was going on.

For insight, the researchers trained a type of complex systems model called a recurrent neural network to perform the same task. They found that it recapitulated many notable signatures of the data, implying that it was a reasonable model of what was going on in the brain. Crucially, they did not stop there but also made the important additional step of peeking inside the model to see how it worked. They found that despite whether the decision on a trial had to be made based on motion or color, the network solved the task by settling its population activity along an attractor. Recall from figure 11 that attractors can come in many types (including fixed points, oscillations, and chaotic); in this case, the type of attractor involved was one that formed a line; the decision (of which way to move the eyes) was reflected by where the network activity relaxed onto that line.

The next question was: How did the network switch between the motion and color task, akin to the “little person pulling the lever” in the Cartesian theater? Like the monkey, the network received input about what task it should perform on each trial based on a visual cue about whether each trial was a motion or color trial—but how did that input affect the type of decision that the network made? The answer was that this input amounted to a perturbation to the network (what the researchers called a “selection vector”) that determined how the network would settle onto that line attractor. In the case of a motion trial, the perturbation adjusted network activity such that the network settled into a decision based on the motion of the stimulus; in the case of a color trial, the perturbation adjusted the network to settle into a decision based on color.

The results of these experiments are both philosophically profound and demystifying. While an enormous simplification of the decisions that we make every day, they indicate that what we typically think of as a little person inside our heads pulling levers can be captured in the framework of complex dynamical systems. One important take-home message from this study is that it would be impossible to infer what is happening by looking at the responses of individual neurons recorded one at a time. Viewing the brain through the lens of dynamical systems where the interactions between neurons (here covariation in their firing) lead to emergent properties like attractor dynamics was key to these insights. Also crucial were complex dynamical systems models trained by machine learning. But in this case, complexity did not lead to perplexity; complexity led to insight (because the researchers took a peek in the box to determine how those models work). It’s important and exciting! And this is but one example of how recurrent neural networks and a focus on attractor dynamics have led to insights into how different brain functions work, from memory to motor systems.

Circling back to the larger question of whether there is “one principle that rules them all” underlying complex systems, we can ask ourselves a smaller question: Do we think that the Grand Plan for brain research should involve all researchers applying the same suite of tools or principles? Absolutely not! The concerns expressed in the Scientific American piece are on point insofar as there will not be a grand unified theory or another type of magic bullet for understanding different brain systems, because these systems are all, ultimately, unique. As such, we should be wary of fads that focus too much on a particular thing (like a line attractor) or a particular tool (like a recurrent neural network). While new ideas and tools are an important component of progress, we must remain mindful that we do not expect emergent properties to follow from one (or a handful) of things; instead, they will follow from many things and their interactions.

So pinpointing those shared principles and leveraging those shared tools is an important component but not the entirety of the Grand Plan for brain research. But what, then, is the rest? I’ve thought about it a lot, and I believe that, ultimately, there’s no way around it: it will require all the research and hard work that goes into building a model of each and every thing we are interested in. One model for mood. A different model for memory. And yet a different model for motor function. There’s no way around building those models if we ultimately want to treat depression, dementia, and paralysis.

So now let’s fast-forward and assume that we have those models of depression or dementia or paralysis in hand. How can they lead us to treatments?

a This notion is similar to causal inference, or an interventionist account of causality. It is different from correlation insofar as the bar of causality is held to the notion of the counterfactual that if X did not happen, Y would not have happened either. In other words, it depends on the notion of perturbation, not just correlation.

b The DSM classifies substance use disorders along a spectrum from at risk to severe, where meeting six or more of eleven possible criteria indicates a severe opioid use disorder; following on the term used by some clinicians, I refer to this as “addiction.” Five of those criteria relate to negative consequences, like continued use despite adverse effects on physical and mental health. American Psychiatric Association. Diagnostic and Statistical Manual of Mental Disorders, Fifth Edition, Text Revision (DSM-5-TR) (2023).

c The team also included Robert May, who popularized the chaotic logistic map equation depicted in figure 11.

d Here the duration of responses is measured by computing the correlation of the signal with itself across different time shifts, the autocorrelation, where longer duration responses lead to autocorrelations across longer delays.

CHAPTER 8 From understanding to treatments and cures

In many cases, the end goal of science is to control. Treatments for brain dysfunction amount to control in the sense that the goal is to move a system from an unhealthy to a more healthy state. In the case of depression, the goal is to shift low mood out of a depressive episode. For Parkinson’s or Alzheimer’s disease, the goal is to shift cells from degenerating back to healthy functioning.

Early in this book, we discussed how brain researchers and pharmaceutical companies have created treatments for brain dysfunction via strategies that amount to “find the broken domino and fix it.” They have pursued highly selective compounds that seek to repair dysfunctional drug targets, reflected in the phrase “one gene, one target, one disease.” They have also focused on stimulating aberrant brain activity with high specificity and precision. While many researchers today continue to focus on both approaches, neither has been working out so well (for all but a few cases). Now that we understand that the brain is a complex system with emergent properties, we begin to suspect why it might be the wrong approach: brain dysfunction may not manifest as individual, broken dominos, and treatments may not be as simple as perturbing a single aberrant target. Sometimes there’s a question of whether treatments are even possible. Insofar as a complex system sits in a chaotic regime, it is subject to the butterfly effect, where small effects can have big consequences that are hard to predict. As described earlier, the weather is a complex system, and we do not dare to try to influence the paths of hurricanes in part because the system is chaotic. Even when a system is not chaotic, it still can be exceedingly difficult to control, because perturbations reverberate in unexpected ways.

So what, then, should we be doing instead? How do we approach the problem of figuring out how to control a complex system? Notably, we aren’t just interested in “change” but change in a particular way and with minimal side effects (so we need to consider reverberations of any perturbation we perform). Likewise, complex systems are often configured to regulate themselves adaptively, which can lead to treatment tolerance; we need to find ways to prevent it.

One approach to both challenges is conceptually straightforward: create detailed models of the system of interest and use those to guide therapeutic development. In the case of depression, we develop a model of mood; in the case of Parkinson’s, we create a model of the factors that support healthy dopamine neurons. The spirit behind this idea appreciates that causality is difficult to intuit in complex systems, so we’ll need to rely on models to find our way through the morass. With those models in hand (validated with data), we can work to understand ways to shift a system from a less healthy to a more healthy state robustly and with minimal side effects.

One of the biggest challenges we face in this pursuit is the immense complexity of the systems of interest. In a typical genetic network, genes and their proteins are functionally diverse and interact in nonlinear ways—one gene might code for a protein that regulates the expression of another, which feeds back on the first but is also degraded by a third, and so on. Things can become even more complicated when the heterogeneity extends across levels, such as the regulation of the brain’s fight or flight response. In that case, hormones, brain circuits, and organs coordinate through reciprocal interactions to trigger and support all the energy and movement required for us to attack (or flee) and then stop again when it’s over. Understanding how heterogeneous complex systems work is an enormous challenge. It shows up in engineering, where large-scale systems are broken down into subsystems that interact. Let’s take on one example: the International Space Station (ISS).

The ISS orbits around the Earth as a research laboratory, an international collaboration to conduct experiments in biology, physics, meteorology, and other fields. It’s constructed from several pressurized modules. As the ISS moves, the position of each of the modules needs to be sensed and coordinated via thrusters to keep the entire ISS intact. The ISS is a complex dynamical system in which its parts (the modules) interact with one another nonlinearly (via physical forces) to determine its future position. Controlling it is a tremendously complex problem, because approximately a thousand variables describe the structure of each module, and maintaining the stability of the structure amounts to coordinating between all of them. In July 2021 one of the modules unexpectedly began firing its thrusters, sending the controllers of all the other modules scrambling to compensate so the entire space station did not break apart, plunge, or enter into an uncontrollable spin. The only way such rapid, responsive coordination can be achieved is by reducing the immense number of variables that need to be controlled into something simpler; engineers accomplish this through a process known as model reduction.

The goal of model reduction is to create a simplified model of a system that retains the main features of an original, more complex model. In the case of dynamical systems, where future behavior depends on past evolution, the desired features to retain are often accurate predictions of “if such-and-such happens, such-and-such will follow.” Accurate dynamical systems models are required to predict how a system will evolve and determine how to control it to keep it in or move it to a desired state. In the case of the ISS, dynamical systems models of each module are used to determine how to control each thruster in a coordinated way across all the modules to guide its position.

When a complex system comprises heterogeneous parts (as opposed to repeated copies), more often than not, reducing its complexity does not come for free. Some details might not matter for the problem at hand and can be disregarded. Suppose you want to control the position of the ISS. In that case, you need to retain some aspects of its physical structure in your model (like how much the connections between its modules can bend) but not other information (its color is irrelevant). At some point, however, the curse of complexity ultimately sets in where a trade-off needs to be made between throwing out information that is relevant (perhaps in some minimal way) and creating a model that is simple enough to be useful. In the case of the ISS, if the model is too complex, computers may not be able to compute what needs to happen quickly enough to react to a misfiring thruster; if the model is too simple, however, the thrusters will respond in the wrong way—an error in either direction could lead to the destruction of the ISS.

In neuroscience, researchers face an analogous challenge to that faced by ISS engineers: figuring out how to reduce the real-world complexity of dynamical systems to something tractable that can be modeled to predict its future state, infer its fragile points, and predict what treatments might be effective. In cases where the complexity follows from interactions between heterogeneous parts, like genetic networks, the curse of complexity kicks in, and navigating the way through it becomes as much of an art as a science. In neuroscience, researchers are just beginning to find ways through this type of thicket, whereas some other areas of biology, including cellular biology, are a bit more advanced. Let’s begin with insight into how to go about it, drawing some lessons from cancer research.

Learning from cancer

The development of cancer drugs has gone through three big waves. In the first wave, drugs were created to target the process of cell division. While effective at stopping cancer, those drugs were also toxic to healthy cells, leading researchers to pursue drugs that were more specific to cancer cells. In the second wave, researchers searched for genetic variants that were expressed in an individual’s tumor and developed drugs specifically to target them (as part of the dawn of precision medicine). One success story was the development of the drug trastuzumab to treat breast cancer in individuals with tumors that overexpress a gene called HER2, which happens in 20–30% of breast cancers. The drug binds to the protein and inhibits new cells from replicating. Multiple studies since its approval in 1998 have concluded that outcomes are significantly better when it is administered versus other therapies.

While promising, this approach of targeting genetic variants did not work for all types of cancer. In some cases, the drugs weren’t effective in the ways researchers expected them to be based on what they knew about a genetic network, and it was unclear why. In other cases, the drugs worked for a short period but became ineffective later as the cancer became resistant. Because of this, cancer research has now entered a third wave in which researchers better appreciate that these genetic networks are configured as complex systems that must be considered in their entirety to develop successful treatments. Here, we discuss two ways cancer researchers are approaching it: one to identify targets using model reduction (analogous to controlling the ISS), and another to combat drug resistance via control at multiple nodes (also called combination therapy).

The first approach seeks to identify genes that might be good targets by building a detailed model of a genetic network (as a complex system), followed by reducing its complexity to something more tractable (analogous to controlling the space station). The blood cancer T cell large granular lymphocyte leukemia has been modeled this way. This cancer follows from the proliferation of a type of white blood cell that is part of a normal immune system, the cytotoxic T cell. These cells attack foreign cells and cells infected with viruses, and they exist throughout the body. In this form of leukemia, they are overproduced, which can lead to an enlargement of the spleen, fever, weight loss, and fatigue. Available treatments include immunosuppression or chemotherapy (which introduces toxic substances to the body for a short time to kill the cancer but also damages other tissues). Due to their side effects, researchers are working to find more targeted therapies.

Like other cancers, this form of leukemia is thought of as a switch in a cell from a healthy to a cancerous state. In this case, the process of normal cell death (apoptosis) has been turned off, and the ambitious therapeutic goal is to find a way to switch it back on again. If that’s possible, clues to treatment for this type of cancer would lie somewhere in the genetic network that controls the switch. However, that network is exceedingly complex and heterogeneous—it involves at least 60 proteins interacting via 142 connections. If we make the simplifying assumption that each of the proteins is either “on” or “off,” this still amounts to a network that has one quintillion (10¹⁸) possible states! Clearly, the path forward does not involve determining how each of those quintillion states determines whether the cell is in a cancerous state; it’s simply an intractable approach. Instead, researchers began by constructing a complex model of this system, capturing all 60 proteins and their 142 interactions (fig. 14a). To simplify the problem, they made the assumption that each gene was either expressed or not. The spirit behind the approach is to make the problem more tractable, but to do so in a way that can be tested for its ability to recapitulate reality, which is done by comparing the model’s behavior with data from biological experiments. Not only did the model recapitulate known behavior, it also passed the gold standard of any modeling effort: predicting something that was not already known and verifying that it was true. In this case, the model predicted that inhibiting a particular protein would induce cell death in cultured cells with leukemia (but not normal cells), and it did.

FIGURE 14. Genetic network controlling normal cell death and leukemia. a) The full genetic network includes 60 proteins (ovals) that interact via 142 connections (lines) to control whether normal cell death is turned on or, in the case of leukemia, off (indicated by the star). b) A massively simplified version of the network reduced to just 5 proteins designed to capture how normal cell death is controlled. The network includes 3 proteins configured into a domino chain backbone. When the backbone is activated, normal cell death happens; when inactivated, leukemia results. The network also includes 2 controller proteins with reciprocal interactions with the backbone; when too much of either controller protein is produced, the backbone is inhibited and leukemia follows. Adapted from Saadatpour, A., et al. Dynamical and structural analysis of a T cell survival network identifies novel candidate therapeutic targets for large granular lymphocyte leukemia. PLoS Comput. Biol. 7, e1002267 (2011), CC BY 4.0.

From here, the researchers focused on simplifying this still very complex model into something more tractable via model simplification. They removed the things that didn’t matter for the question at hand, leaving a simplified model with just five proteins that recapitulated what they were most interested in: the “healthy” and “cancerous” states of a cell and what triggered a shift between them (fig. 14b). They inferred that the healthy state followed from the activation of three proteins configured into a domino-chain backbone (that triggered normal cell death), and that the cancerous state followed when this domino chain was inactivated (thus turning normal cell death off). Whether normal cell death was activated or not was determined via reciprocal interactions between the backbone and two “controller” proteins that interacted with the backbone via reciprocal inhibition to keep the system in a healthy balance. This provided the researchers with a strong intuition for the types of interventions that might shift the cell from a “cancerous” back to a “healthy” state—for instance, because cancer follows when too much of either controller protein is around, a healthy state could be restored by reducing the amount of a controller protein that is too abundant. Ultimately, the researchers were able to use the model to infer the targets that will (and won’t) be effective for controlling cancer, and those targets are currently being pursued. Remarkable!

In the development of modern cancer drugs, a second type of approach focuses on combating drug resistance. Acquired resistance happens because genes are part of networks configured to regulate themselves via systems with multiple paths and feedback loops. When a cancer drug is administered, it changes the proteins that a cell expresses. That drug becomes less effective when the cancer can find and follow another path to cell proliferation. One way to tackle the challenge of drug resistance is to simultaneously administer both the original drug and one or more that block the other paths to cancer. The drug seribantumab was developed with this notion in mind—the idea behind it is that it blocks changes in a pathway known to confer cancer drug resistance of many different types (including ovarian, breast, and lung cancer). The trajectory from the initial modeling effort to the first clinical trials spanned a decade, ending in 2016. As the authors say, “To our knowledge, this is the first example of a drug designed and clinically tested using the principles of Systems Biology.” Clearly, these approaches are quite new.

After confirming its effectiveness in cell lines, seribantumab began to make its way through clinical trials. In the first wave of trials, the drug was determined to be ineffective. However, a post hoc analysis suggested that it was effective in a subset of patients with particular genetic biomarkers (analogous to cystic fibrosis). A second wave of clinical trials that targeted patients with those biomarkers was initiated but then paused in the spring of 2023 following the hire of a new CEO and a reevaluation of the company’s financial portfolio. Today, the drug’s effectiveness remains to be determined. Clearly, this outcome highlights that while the science behind creating a drug is always a bottleneck to a new therapy, other factors are typically at play (a topic I will circle back to in the next chapter).

In sum, researchers working to develop cancer therapies have started to approach drug development from the perspective of complex adaptive systems. While therapeutic development in brain research is less advanced than cancer, complex systems are just as relevant for the brain. For a look at how this perspective might help, let’s look at Parkinson’s disease.

Parkinson’s disease

Parkinson’s disease begins with subtle symptoms, such as a bit of tremor in the hands, typically around age 60. It is a progressive neurodegenerative disorder that escalates across a period of years to increased difficulty moving, including talking and writing. While complications (like difficulty swallowing) can lead to death, the disease is not typically fatal but causes fatality’s tragic alternative: progressive suffering. In its advanced stages, an individual can be bedridden and require around-the-clock care to complete everyday tasks, like eating. As the saying goes, individuals typically “die with Parkinson’s, not from it.” The disease is by no means new; it is reflected in Indian writings as early as 1000 BCE. It came to bear its name following the descriptions of the English surgeon James Parkinson in 1817. As Parkinson described it, the disorder is characterized by involuntary tremors and difficulty moving while leaving “the senses and intellects being uninjured.” More than 200 years after the publication of Parkinson’s monograph, we still have no way to stop (or even slow) the disease.

Benjamin Stecher was diagnosed with Parkinson’s at the atypical but not unheard of age of 29. While his family has no history of the disease, he carries a mutation in a gene linked to it, GBA1. At the time of his diagnosis, he was working as the managing director of an education company in Shanghai, ramping up his professional career and contemplating plans for his future. His diagnosis changed those plans. For most of the past decade, he has traveled the world, meeting individuals on the bleeding edge of research and asking probing questions, all while writing and advocating to raise awareness about the disease. He regularly lectures at biomedical research centers and has coauthored two books about Parkinson’s with respected neurologists.

Stecher often challenges researchers to justify their approaches in thoughtful, clear ways. Following a talk by the world-renowned researcher Virginia Lee about her hypothesized causes of Parkinson’s, he approached the microphone to ask, “What experiments do we need to run to disprove [it]?” As part of a panel at the National Institutes of Health, he’s challenged researchers about waste and urged them to consider alternatives: “All of our models are just models, some are useful in answering specific questions, but too often we seem to forget that none recapitulate anything that any human really has. I have been to over a hundred labs and clinics all over the world and have never seen a mouse, monkey, or worm with anything that I would call Parkinson’s.” These are but a few examples of how Stecher stimulates important conversations. He has seen how researchers get trapped in a type of inertia that isn’t always beneficial. He urges them to pause and thoughtfully consider whether things are on track. By challenging and inspiring researchers, Stecher and patient advocates like him contribute to the development of treatments and cures in innumerable ways.

Today, Stecher manages his disease with a combination of medication and an adaptive deep brain stimulation device implanted into his subthalamic nucleus. He lives in one of the world’s hubs for biomedical development, Toronto, and has access to many advanced treatment options. For that, he’s exceedingly grateful. However, he is also painfully cognizant of the fact that what he and other patients need most is some way to stop or even slow the progression of the disease (as opposed to just treating its symptoms). We need to find those ways.

The motor symptoms of Parkinson’s happen as a consequence of the death of dopamine-releasing neurons in a part of the brain called the basal ganglia. What triggers those cells to die is unclear. One idea is that the enormous size of these neurons (specifically their enormous axonal arbors with around a million neurotransmitter release sites per neuron) requires a tight energy budget, leaving them especially vulnerable to unknown degenerative triggers. A related idea is that these cells fire in a special, rhythmic way that relies more on calcium than other cells, and calcium interferes with the cell’s energy powerhouse: the mitochondria.

While different, Alzheimer’s and Parkinson’s have a lot in common. Similar to the beta-amyloid clumps associated with Alzheimer’s disease, Parkinson’s is also associated with abnormal protein clumps (but of a different type) called Lewy bodies, composed, in part, of a protein called alpha-synuclein. Fritz Lewy discovered those clumps in 1912 while working in the laboratory of Alois Alzheimer (who had previously described the amyloid plaques associated with the disease that came to bear his name). Like beta-amyloid plaques, Lewy bodies are suspected to be toxic, but we do not know why they form or whether their formation triggers the disease. In Parkinson’s, those clumps are enriched in the regions of the basal ganglia that produce dopamine.

Like Alzheimer’s, we currently do not have a cure for Parkinson’s. Treatments for Parkinson’s, however, are more effective at alleviating the symptoms than they are for Alzheimer’s. The first-line treatment for Parkinson’s, levodopa, dates back to 1970. Its development began in the 1950s with the discovery that dopamine is present in the basal ganglia and that structure is important for movement. This and other discoveries linking Parkinson’s to dopamine depletion convinced two researchers to try administering levodopa to twenty Parkinson’s patients in 1961. The rationale was that while dopamine ingested as a drug cannot cross the blood-brain barrier and enter the brain, its precursor, levodopa, can; once there, the brain would convert levodopa into dopamine. As one of those researchers describes it, the effects were seemingly miraculous, immediately restoring normal motor function in those patients for a few hours:

It was a spectacular moment to see the patients who could not walk, could not get up from bed, could not stand up when seated, start walking. They all performed these activities like normal. Speech became better. The associated movements, the face expressions; they started laughing and then actually crying with joy. These were patients who could not be helped by any doctor. And then levodopa produced the effects. It was really very spectacular.

Following clinical trials, the drug was approved in the United States in 1970.

Clinically, the administration of levodopa to patients is not straightforward. Its effectiveness tends to wane with time: after a period in which the drug is effective, the same amount of the drug becomes effective for a shorter duration. It’s unclear whether this happens due to drug tolerance or as a consequence of neurodegeneration. Unfortunately, as the dosage is increased, it can lead to involuntary movements (dyskinesia) as well as an increased risk of addictive behaviors like gambling. Because enzymes naturally exist in the brain to degrade levodopa, it is often given in conjunction with inhibitors of those enzymes (such as the drug carbidopa). Since levodopa was approved, other drugs that work via other pathways (like istradefylline) can be used in concert, and that is a win. But sadly, none of the drugs discovered thus far slows disease progression.

When medication begins to become less effective or problematic, both surgery and deep brain stimulation (DBS) can sometimes be used to alleviate some of the tremors, rigidity, and slowness of movement associated with Parkinson’s. DBS involves the surgical implantation of electrodes deep into the brain, into specific nuclei of the basal ganglia, and the stimulation of the surrounding brain tissue by an electrical current. The development of DBS hinged on a serendipitous discovery. In the 1980s one approach to Parkinson’s treatment involved surgical removal of part of the thalamus, but the surgical outcomes were variable and could lead to adverse effects that were irreversible. The procedure involved inserting an electrode into the area prior to removing it to determine whether there was an effect on the patient’s symptoms. While performing one of these procedures in 1987, the French neurosurgeon Alim-Louis Benabid explored what happened when the frequency of stimulation was increased to high frequencies (to 100 Hz), and he was surprised to observe that this form of stimulation mimicked the effects of surgical removal. This led him to suggest that stimulating electrodes could be implanted into the brain as an alternative to surgical removal of the brain area, with the advantage that the procedure could be reversible.

Building on decades of research on the neural circuits involved in movement in the basal ganglia, DBS was developed and tested in a nonhuman primate model of Parkinson’s disease and published in 1992. It was then tested in humans and approved by the FDA in 2002 for individuals with Parkinson’s when drugs begin to become less effective. When DBS works, it typically continues to work for several years. However, it does not delay the progression of the disease.

What we ultimately need for Parkinson’s is some way to prevent and stop the neurodegeneration from happening. Several different approaches have been attempted but failed in clinical trials. One approach is strongly analogous to the new Alzheimer’s drugs, but instead of creating antibodies that target beta-amyloid, the antibodies target alpha-synuclein. Thus far, those trials have not alleviated symptoms or slowed disease progression. Like debates around the role of beta-amyloid in Alzheimer’s, researchers discuss whether mutated alpha-synulcein is a toxic trigger or whether it’s the loss of normally functioning protein that’s the problem (or something else altogether).

Also, like Alzheimer’s (and so many other brain disorders), what we call Parkinson’s disease is thought to follow from not just a single cause but many underlying causes. Consequently, cures may not take the form of a singular approach but many different ones that target, for instance, genetic variants (analogous to the targeted cancer treatments we discussed). Around 5% of individuals with Parkinson’s carry mutations in the GBA1 gene (like Stecher). That subset has many symptoms that are clinically indistinguishable from other individuals with Parkinson’s, but in their case, the disease is thought to be linked to that gene specifically; how exactly is unclear. GBA1 codes for an enzyme called GCase that is responsible for converting one lipid molecule (let’s call that lipid A) into another (let’s call that lipid B) in a cellular organelle called a lysosome; lysosomes are responsible for breaking down waste in neurons (including alpha-synuclein). Depending on the genetic variant an individual with a GBA1 mutation carries, their risk for developing Parkinson’s increases two to fivefold relative to others who do not carry the same variant. Not everyone with these variants will develop Parkinson’s, but the disease tends to progress more quickly in those who carry one of these variants and do develop the disease.

How exactly might a mutation in GBA1 lead to Parkinson’s? That’s not completely clear. Early on, researchers were thinking about it in a pretty straightforward way: GCase converts lipid A to lipid B; a second enzyme (let’s call that enzyme 2) does the opposite (fig. 15a). In patients with the GBA1 mutation, GCase is underactive, leading to less lipid B than normal and an accumulation of lipid A; either could be the culprit. Evidence that the latter was the problem comes from Gaucher’s disease, where individuals have mutations in both copies of GBA1, and the accumulation of lipid A is known to be toxic. The pharmaceutical company Sanofi thus set out to create a drug called venglustat to inhibit enzyme 2 with the rationale that it would tackle both problems at once (by leading to more lipid B and less accumulation of lipid A). Sadly, while the drug operated as intended and decreased levels of lipid A, it did not improve symptoms in Parkinson’s patients over 52 weeks of treatment; in fact, it exacerbated them. As the Parkinson’s researcher Peter Lansbury describes, “It’s so much more complicated than this, unfortunately.”

But what to do instead? As venglustat was making its way through clinical trials, Lansbury and his team at BIAL Biotech were working to find a complementary approach. Channeling the ethos of this new era and its focus on complex dynamical systems, Lansbury and colleagues took a step back to consider the entire metabolic pathway that included lipid A and lipid B and realized that the conversion between them was much more complex than two enzymes that shuffled one to the other and back again; the pathway had many more intermediates (and only a subset happened within the lysosomes; fig. 15b). They collaborated with researchers to model the pathway as a complex dynamical system to determine how to restore its function to a normal, healthy state. With those models in hand, they could see why venglustat did not work: inhibiting enzyme 2 would not return lipid B to healthy levels. However, an activator of GCase would accomplish that goal and prevent lipid A accumulation, so they opted for that approach instead. That drug is called BIA-28-6156, and it’s currently making its way through clinical trials. Those trials are estimated to end in 2026, and fingers are crossed for a positive outcome.

FIGURE 15. Genetic network involved in GBA1 mutation-related Parkinson’s. GBA1 mutations result in an enzyme GCase that is underactive (GCase*). a) The rationale behind the development of the drug venglustat, designed to inhibit Enzyme 2 to increase the amount of lipid B and avoid the accumulation of lipid A. This was not effective. b) The rationale behind the development of the drug BIA-28-6156, based on a more complete understanding of the metabolic pathway. The drug is designed to activate GCase*, leading to less lipid A accumulation and more lipid B. Adapted from den Heijer, J. M., et al. A phase 1B trial in GBA1-associated Parkinson’s disease of BIA-28-6156, a glucocerebrosidase activator. Mov. Disord. Off. J. Mov. Disord. Soc. 38, 1197–1208 (2023), CC BY 4.0.

The story of the search for a treatment for GBA1-associated Parkinson’s exemplifies how incredibly challenging it will be to develop treatments for brain dysfunction, even when we can tie a disorder to a single gene, given that what we’re dealing with here is a complex dynamical system. The only way forward is to take on the challenge like Lansbury and his team did: by capturing that complexity with a model and finding some way to shift the system back to a healthy state. Alzheimer’s researchers are beginning to view that disease in a similar way: as a nonlinear and dynamic interaction between parts of cells and organ systems that exists at a “level of complexity [that] confounds intuition.” For cancer, Parkinson’s, and Alzheimer’s, progress has been impeded by oversimplification, and researchers are beginning to realize that the only way forward is to embrace the less intuitive (but also much more accurate) framework of complex adaptive systems.

Tapping the brain’s control systems

In the approach we’ve just discussed, the path to a new treatment begins with a model of a system that contains a lot of detail and complexity; from there, the goal is to simplify the model to infer a treatment. The hope is that we can find ways to restore a system to health by perturbing the expression of a few proteins or activity in a small number of brain regions. While this approach can work in principle, it also requires a tremendous amount of time and effort. In some cases, we may be able to take a good guess at what those control nodes are even before creating complex models (although models can still help us understand how to tap these nodes most effectively). Examples include tapping the systems that the brain uses to control itself, such as the brain’s arousal system, which controls wakefulness via neuromodulators such as norepinephrine. The gist is that the release of norepinephrine works to increase alertness, arousal, and attention and “wake you up” when something interesting or important is happening. Because the arousal system interacts with so many other systems, including the ones that maintain the brain’s balance as well as mood, therapies for disorders such as epilepsy and depression can work by tapping into (and controlling) the arousal system.

Vagus nerve stimulation is an existing therapy that is thought to work this way; it is approved clinically to treat drug-resistant epilepsy and depression. The vagus nerve runs from the body to the brain and can be accessed via the neck. Vagus nerve stimulation typically involves the implantation of a cuff around the vagus nerve and then periodic stimulation of that nerve by a battery pack implanted in the chest. It’s thus invasive but less so than the implantation of electrodes required for deep brain stimulation. It is typically administered periodically (e.g., every 5 minutes for 30 seconds each time over several weeks or months) along with an option for a patient or caregiver to trigger it during the onset of a seizure. Some newer “closed loop” systems monitor heart rate and are triggered by changes in heart rate patterns characteristic of seizure activity.

Remarkably, vagus nerve stimulation as a treatment for epilepsy dates back to the late 1880s. It was first developed by the American neurologist James Corning, who believed, along with others, that epilepsy was caused by excessive cerebral blood flow. He developed a number of instruments to treat epilepsy that acted to compress the carotid artery. In 1884 he extended his “carotid fork” to administer a current to stimulate the vagal nerve fibers and slow heart rate, further reducing blood flow to the brain. Corning’s method was not incredibly effective. Over the next century, vagus nerve stimulation was sporadically investigated as a treatment for epilepsy in animal models to determine the best stimulation parameters. In the 1980s researchers at Wake Forest University extended a cardiac pacemaker to stimulate the vagus nerve and tried it on four patients with epilepsy with promising results. Clinical trials followed, and vagus nerve stimulation was approved for treatment-resistant epilepsy in 1997. The application of vagus nerve stimulation to treat depression followed from the serendipitous observation that it improved mood in epileptic patients. This led to a pilot study with promising results, clinical trials, and the approval of vagus nerve stimulation for drug-resistant depression in 2005.

The mechanism of vagus nerve stimulation is not well understood. It is likely to act at least in part through the neurotransmitter norepinephrine. Norepinephrine is produced by a brain structure called the locus coeruleus that is indirectly innervated by the vagus nerve, and the idea is that this therapy increases the amount of norepinephrine released. In animal models, lesions of the locus coeruleus prevent the protective effects of vagus nerve stimulation. How exactly these increases in norepinephrine might prevent seizures or treat depression remains unknown. However, recall the notion that the brain is optimized to process information by positioning itself at the critical boundary, and seizures result when the brain falls off that knife edge onto one side. In this context, the arousal system is thought to have many of the characteristics required to control the brain by affecting all neurons in the same way through the release of norepinephrine. One idea is that vagus nerve stimulation works by facilitating global rebalance, thus restoring the brain to its knife edge, its healthy state. A better understanding of whether and how this works may be a key to improving vagus nerve stimulation and developing other neuromodulation-based therapies in the future.

Leveraging the brain’s plasticity

When possible, tapping the brain’s “control” systems is a great therapeutic approach—but it will not work in all cases. Nor will reducing exceedingly complex models to a small number of control nodes. In principle, restoring a system to health could require changing the expression of hundreds of proteins or the activity of millions of neurons, each a bit differently—this would be beyond the technology we’ll have to deliver treatments anytime soon. As a consequence of the curse of complexity, control in some systems simply may not be reducible to a small number of elements.

In these cases, what should we focus on instead? Some of our most promising emerging therapeutic interventions tackle this challenge by extending the brain’s own natural plasticity. The general idea is that the brain has become entrenched in an unhealthy place and can be restored to health by extending its own remarkable mechanisms for learning and adjusting to new situations. The challenge is to figure out how to enhance those natural mechanisms when innate plasticity falls short.

Plasticity is essential for recovering from a stroke, which can lead to brain damage due either to a lack of blood flow to regions of the brain (an ischemic stroke) or to bleeding in the brain when a blood vessel bursts (a hemorrhagic stroke). Each year, around 17 million people experience a stroke, and of those, about 80% have impairments of the arms and hands that impede their ability to perform everyday tasks. Most often, strokes happen on only one side of the brain, and limb impairment is thus isolated to one side of the body (the opposite side). For over a century, we’ve known that when a stroke happens, an affected limb is more likely to recover if an individual actively works to relearn how to use it. Today, that often occurs through rehabilitation therapies that constrain the hand and arm movements on the good side (often with a sling or a splint) to encourage movements with a damaged limb. When damage is extensive, however, patients may be unable to recover using this approach.

A newer generation of therapies seeks to help individuals recover from stroke damage by leveraging the power of noninvasive brain-computer interfaces. Traditionally, the motor cortex on one side of the brain is thought to control the opposite side of the body. IpsiHand therapy builds on discoveries suggesting that the information in the brain required for arm and hand movement is also located on the same side of the body, including noninvasive imaging studies in humans (fMRI, PET, and MEG) in the 1990s. IpsiHand works by measuring these “ipsilateral” (same-side) brain signals with an EEG, then uses them to control an exoskeleton device that helps a patient’s hand move. The goal of the device is to provide feedback that will help patients learn how to tap into those ipsilateral signals to control their limbs. One significant advantage is that it’s a type of training that individuals can do at home. That training involves patients doing things like visualizing opening and closing their hand for around an hour a day, 5 days a week, for 12 weeks. It received FDA approval in 2021. While IpsiHand is still new, it has been demonstrated in some patients to be an effective way of improving arm mobility when other methods have failed.

Another class of approaches that seek to tap the brain’s plasticity mechanisms focuses on reopening the type of plasticity that happens during development. Amblyopia is a developmental disorder that follows from an imbalance of the eyes during childhood; it affects around 3% of all children. The imbalance of a stronger versus weaker eye can lead the brain to “shut down” information coming from the weaker eye, resulting in blindness in that eye as well as deficits in types of vision that rely on the brain processing the same information with both eyes, such as depth perception (which is important for activities like driving). It is often treated during childhood by patching the stronger eye to encourage the weaker eye to develop. When treatment is administered to older children or adults, it is often less effective because the brain becomes less plastic with age.

Building on work investigating how this happens, researchers discovered that a protein called Lynx1 ramps up as the developmental plasticity period closes, and that in mice engineered to lack Lynx1, the developmental period does not close. They also discovered that once expressed, Lynx1 suppresses signaling by the neurotransmitter acetylcholine in visual cortex. They thus wondered whether drugs that block the breakdown of acetylcholine might reopen the critical period for adults with amblyopia that was left untreated. Fortunately, one drug of this type, donepezil, is already FDA-approved for a different purpose (to treat the cognitive impairment associated with Alzheimer’s disease). In a small pilot study of individuals with amblyopia, 16 people ages 9–37 received donepezil for 12 weeks, and results suggest that it works, at least to some degree. You’ve probably seen the vision test charts that ask someone to read lines and letters of different sizes where each line indicates what an individual can read relative to “normal” vision (where 20/20 indicates that an individual can read at 20 feet what a “normal” individual also can, whereas 20/40 means an individual can read at 20 feet what a normal individual can read 40 feet away). The average vision for these patients in the amblyopic eye was 20/125 before the treatment and increased to 20/90. While that’s a modest change, and larger, placebo-controlled clinical trials are needed to confirm these results, it may indicate that researchers are on a good path.

Another therapy that is currently being explored by virtue of its hypothesized ability to reopen a developmental period is the psychedelic MDMA (“Ecstasy”). In mice, a type of social learning is developmental: adolescent mice that spend time with other mice in one environment and then alone in another prefer the environment they experienced with the other mice (even when the other mice are no longer around). But this is only true for young mice; adult mice do not learn to associate an environment with the social experience. However, if the adult mice have the experience while on MDMA, they learn the association in the same way the young mice do. This happens with other psychedelics as well, including LSD, ketamine, and psilocybin (from hallucinogenic mushrooms). More than 100 clinical trials are currently underway to use psychedelics to treat a wide variety of disorders, including addiction, posttraumatic stress disorder (PTSD), depression, psychosis, obsessive-compulsive disorder, and chronic pain.

In many of these exploratory therapies, the psychedelic is intended to enhance plasticity, but alone, that is not enough—relearning needs to happen as well, and it must be specific to the problem an individual is experiencing. Psychedelics are thus coupled with therapy with a trained counselor to help ensure that the right type of learning happens. For Sandra, a woman who suffered from PTSD following an abusive marriage, this therapy worked when many others had failed. Before the treatment, she experienced daily flashbacks that would sometimes trigger panic attacks. Traditional therapy wasn’t helping convince her that she was safe. So she arranged for a psilocybin-psychedelic therapy session where a therapist led her through a night in which her ex-husband almost killed her. As she explains it, “I could see his fist just go up, but every time it went down to hit me in my face, it just turned to these beautiful leaves, leaves everywhere.… And I think in my head, it changed that memory for me.”

At the same time that many compelling stories like this exist, the evidence supporting this type of therapy is mixed, and researchers have many concerns. Among them: that psychedelics are simply a powerful placebo that work not because of their direct effects on the brain but because people are so convinced that they are effective. Why is that a problem? Because they are not risk free. For instance, they can trigger psychosis in people with a predisposition for psychotic disorders. It’s also essential to remain mindful that not all learning is beneficial; it also has a dark side. As patients relive those traumatic memories, it can trigger distress that manifests as anxiety, uncontrollable thoughts, and nightmares. Reliving the experience of a traumatic event can reinforce the trauma, and the therapy is not always successful. That is not to suggest that there’s not tremendous optimism around psychedelic-based therapies—there is. To protect and help patients, the field just needs to proceed rigorously and cautiously.

Stepping back, a common thread through all these approaches is the assumption that the brain is entrenched in a maladaptive state and needs a “do-over” to relearn a better one. Of note is that in some cases, the do-over may not involve a brain-based intervention at all but instead may tap into the brain’s remarkable plasticity mechanisms via behavioral interventions alone. In fact, therapies that incorporate some form of behavioral intervention may turn out to be the only approach with the precision required to restore some types of dysfunctional neural circuits to health. As described by Yael Niv, a computational neuroscientist and mental health researcher at Princeton, “Psychotherapy can activate the specific neurons and synapses that need reshaping—and then modify them, whether through behavioral methods as in cognitive behavioral therapy, or through talk therapy. Pharmacological interventions cannot provide the precision required, and it is hard to imagine that future methods will ever be capable of targeting with the same precision that is so readily available behaviorally.”

Don’t speculate. Just show.

With the end-goal of “control,” so much of the discussion about treatment development has parallels in engineering. It reminds me of a formative experience I had during a summer course focused on brain-inspired robotics and the types of circuits that drive computers and other devices. I was there to give a lecture, and among the many I’ve given since, it remains one of my most memorable. Following my talk, a student raised his hand to express frustration about how it had unfolded. And then, to my surprise, the other students began clapping in agreement. I was left standing there, speechless.

Why were the students so frustrated? The course participants were graduate students in engineering from around the world. They spent a few hours each day listening to lectures. The rest of the time, they created new robots and circuits. I was part of a group of scientists brought in to describe new discoveries in brain research with the idea that these insights might inspire some novel and creative engineering. My lecture focused on how we identify objects as we look at them, a problem that robots must also solve.

Throughout my talk, another brain researcher stopped me several times to point out his disagreements with my approach and my interpretation of the data. This type of debate is not unusual in brain research, especially in the leisurely context of a summer course, and it didn’t strike me as odd or inappropriate as it was happening. Brain researchers do experiments, collect data, and make inferences from those results. Consequently, we spend time discussing not just what we know and how we know it but also the legitimacy of our knowing. In the eyes of the engineering students, however, that discussion was wasteful. The disappointed student explained that this interaction had taken up an unfortunate amount of time and prevented me from telling them more about what they were hungry to learn: how object identification works in the brain—hence his (reasonable) frustration.

In that same course, the lectures delivered by engineers were organized a bit differently from my own. They were typically set up as a buildup for the main event at the end—a demonstration of a robot or a circuit in action. In one case, the demo involved a robot navigating around obstacles. In another, the demo was a circuit that detected movement. The engineers didn’t spend time discussing the legitimacy of their approaches or inferences. I gathered that this was because their design would work or not, and we would all see that for ourselves in the demo. Don’t speculate. Don’t discuss. Just show.

Simply put, when the goal is building, it simplifies things insofar as it sets a clear benchmark for success that is difficult to quibble with. By analogy, the ability to “fix” something sets a similar bar. If you want to claim that you understand something, show us that you can fix it when it breaks. Don’t speculate. Don’t discuss. Just show.

In this new era of AI and machine learning, building doesn’t necessarily mean that we understand something in the classical sense because we can train models (and, in turn, robots) that figuratively wire themselves up to do whatever needs to be done. In chapter 2 we learned that fixing is similar insofar as many of our existing therapies for brain dysfunction were not developed based on understanding. However, we can say that, like building, the inability to fix something is probably indicative of the absence of understanding. And if you don’t try to fix it, how do you even know?

E. J. Chichilnisky is a researcher at Stanford who has worked to understand the retina with the broader goal of developing technology for treating incurable blindness. Throughout his career, he has characterized the many different cell types that exist in the retina and the different types of information about the visual world that they convey to the brain. Today, Chichilnisky oversees the Stanford Artificial Retina project, which aims to develop an electronic implant to restore vision to people blinded by retinal degeneration. What differentiates their approach from others is that they aim to reproduce the retinal neural code based on tailored knowledge about the cell types they are stimulating. In the current stages of this work, they are trying to figure out exactly how to reproduce this neural code and build the hardware that can do it.

Their research involves recording how patches of the retina respond to visual inputs such as images. Then, they determine how to re-create those same responses with electrical stimulation. They soon aim to test experimentally whether this recapitulation of retinal signals can mediate useful vision. As a metaphor, you can study to learn another language, but you’ll know how well you can speak it only if you get out there and talk to someone else. That’s what Chichilnisky and his team are trying to do: test whether they understand the language of the eye by “talking” to the brain and seeing if it can be understood. One thing that I find both fascinating and admirable about Chichilnisky’s research is the multifaceted motivation behind his work. First and foremost, he’s driven to help people with blindness. At the same time, it’s not only about that: “I spent a large part of my career characterizing the details of the retina, and I’m left wondering: what details do versus do not matter for seeing? We can answer that question by determining the cell types and the activation patterns that are or are not needed to recapitulate vision with electrical stimulation—it’s the ultimate causal test of function. Moreover, the engineering goal focuses our basic research on figuring out the relevant things we need to know.”

Chichilnisky’s right. I’ve experienced the same in my own recent work: reframing the problem of understanding some brain function in terms of your ability to “fix” it refocuses the research on different things. And this is all mixed up with an era in which researchers have access to a whole host of new ways to “just show” via new tools to causally perturb the brain, like optogenetics. Some of these ways have a clearer throughline to treatments for brain dysfunction than others, and from my viewpoint, it only makes sense to prioritize those throughlines as a win-win.

Many brain researchers, including Chichilnisky and myself, were motivated to pursue a career in neuroscience in part because we were curious to understand more about the brain, the mind, and how we work. As it happened for both of us (and also for other researchers I know), it’s natural to transition from curiosity about the brain, through a career of figuring out some slice of the puzzle, to wondering how much of what you’ve figured out really “matters.” I don’t regret a moment of my career to date; I’ve had a rich and wonderful experience, and it’s been thrilling. But I can also now see how considering how the brain breaks triggers a host of new considerations about “what matters” most about it.

Stepping back from my personal experience, to create new treatments for brain dysfunction, we need two things to happen in brain research. The first is what I’ve been talking about throughout the book: we need to shift away from thinking about the brain as a domino chain toward thinking about the brain as a complex adaptive system. The second is that we need to keep many eyes focused on treating brain dysfunction—in the form of the formidable challenge of controlling complex systems to shift the brain from disease to health—as the end goal, even from the earliest (basic research) stages.

CHAPTER 9 A new era in brain research

Over 30 years ago, Carol Jennings helped researchers pinpoint the gene in her family that leads to Alzheimer’s disease; tragically, we still cannot offer her family a cure (or even a highly effective treatment). Benjamin Stecher has spent the past decade advocating for individuals with Parkinson’s, and we cannot do anything to stop the progression of his disease. Nor can we stop the progression of ALS or Huntington’s. Likewise, many individuals cannot escape opioid dependence in the same way that Travis Rieder did; a death from an opioid-related overdose happens in the United States every 8 minutes. Similarly, many individuals do not recover from severe bouts of depression in the same way that William Styron did; a death from intentional suicide happens in the United States every 10 minutes. Individuals afflicted with these and other types of brain dysfunction need better solutions than the ones we can offer today.

For decades, many tens of thousands of brain researchers have been working to help find those solutions. The discovery of the genetic code in the 1960s, coupled with rapid developments in biotechnology, computational power, and noninvasive imaging, ushered in an era of tremendous enthusiasm that we would arrive at solutions quickly. Unfortunately, those solutions have not been as forthcoming as many hoped. It’s not that nothing has been happening; it has! Novel treatments for pain, insomnia, postpartum depression, paralysis, spinal motor atrophy, and other disorders have emerged over the past few decades, built from insights into how the brain works. But clinical trials of Alzheimer’s, Huntington’s, Parkinson’s, depression, psychosis, and other disorders have failed for reasons that we don’t understand. That, coupled with the absence of leads to chase, led many major pharmaceutical companies to abandon the brain drug development effort in 2011, and not much has changed since. Researchers themselves are growing concerned. We need a new “Grand Plan.”

What I affectionately refer to as the Grand Plan for brain research is a description, in broad strokes, of how we’ll go about finding the causes of brain dysfunction and develop treatments. My own journey with this book began with the realization that I could not write down a Grand Plan for brain research that I was optimistic about—one that could describe how we plan to go from where we are now to new therapies. I knew the sketch: figure out the causes of brain dysfunction and create treatments. But what is the plan to accomplish that? What I knew was that the way the plan was formulated in the 1990s and depicted in popular textbooks (like find a gene, make a mouse, create a drug) wasn’t going to work. It took me the better part of 2 years to sift through the history, philosophy, and science required to see the emerging alternative, and at times it was overwhelming. But the act of writing it down helped me understand what the new and promising Grand Plan for brain research is. Now that I can see it, I’m optimistic and grateful to know it. I’m also ready to dive in and contribute.

The seemingly straightforward fact that the Grand Plan so squarely follows from assumptions about “the type of thing that the brain is” has been vastly underappreciated. While not often explicitly stated, inferring those assumptions is pretty straightforward. Since the 1990s the assumption has been that the brain can be approximated largely as a linear domino chain (fig. 2). The molecular neuroscience framework focuses on the chain of events from genes to proteins to neurons to neural circuits to function. Likewise, the notion of the brain as a sequential computer is that it receives sensory input and passes it along to a series of modules to arrive at a behavioral response. Similarly, many hypotheses about dysfunction are triggering causes that lead to effects, including the hypothesis that toxic protein clumps initiate both Alzheimer’s and Parkinson’s, and depression follows from less vigorous activity in prefrontal cortex. The domino-chain approach implies that brain dysfunction follows from an aberrant domino; it can be captured with the phrase “find the broken domino and fix it.” It’s instantiated in brain research by the notion that we can “find a mutated gene, create a mouse, develop a drug.” Or “find a brain area with aberrant brain activity and stimulate it.”

What the domino-chain presumption misses is that the brain must continuously adapt to changing conditions, and how it accomplishes this typically involves feedback. In this type of system, causes lead to effects that feed back again on causes. Their behavior can no longer be captured by domino chains, and their dysfunction typically cannot be described as “broken dominos.” This is because they tend to exhibit emergent properties that cannot be inferred by studying their parts in isolation. Consequently, dysfunction can amount to things like a system set at the wrong point, where the set point is determined not by nodes but by the strength of their interactions.

We also need to remember that while the entire purpose of feedback is adaptation such that a system is robust to some types of changes in the world, endowing them with that robustness makes them fragile in other ways. Many types of brain dysfunction probably follow from this fragility. The fact that neurodevelopmental disorders like autism and schizophrenia are not entirely genetically inherited but also often have no clear-cut environmental causes is thought to follow from powerful adaptations during development where small perturbations lead to big effects. Our immune systems also exhibit a powerful form of adaptation that seeks to identify and destroy minute quantities of invading pathogens. When it becomes imbalanced, neuroimmune disorders like multiple sclerosis can follow. Depression is thought to happen when the mood system, which is thought to exist to help inform us about global changes so we can adapt to them, gets stuck in a negative feedback cycle in which bad moods lead to the distorted percept of bad outcomes, which in turn leads to worsening mood. Likewise, the brain’s fight-or-flight response exists to help us adapt and respond to threats, but its overuse can be harmful. Conceptually, adaptability is the brain’s superpower, but its unavoidable by-product is fragility; this fragility is why the brain breaks.

While notions of adaptivity, feedback, and fragility are not new (for instance, homeostasis dates back to the 1930s), thus far, they’ve often been missing the same notions that the brain-as-a-computer sought to fill. Namely, a catalog of the brain’s (recurrent) circuits, their activity patterns, and how they map onto the brain’s functions does not provide enough information to build something like the brain. For instance, we can suppose that feelings motivate us to approach good things and avoid bad ones, but how exactly does the brain figure out what those things are? Presumably, it happens via learning, based on experience. But how exactly does the brain transform sensory input into a determination of whether something out in the world is good or bad? Answering that question is a crucial component of understanding how the brain works.

As I see it, breakthroughs in the future of brain research will extend the 1990s molecular neuroscience ethos to capture how the brain processes information and adapts to its changing needs. We will increasingly begin to think about the brain as a complex dynamical system that adapts to regulate itself and continuously interacts with an environment that it learns from. We will increasingly realize that the brain’s dysfunction follows from its fragility and that treatments amount to controlling a complex system—something we know is exceedingly hard to do. The brain will turn out to be more like the weather than a domino chain. But unlike the weather, there is more hope that we will indeed be able to influence it, to shift it from unhealthy to healthy states, because the brain has so many mechanisms to control and keep itself in balance.

Where did we go wrong?

Given that thinking about the brain as an adaptive system makes so much sense (dating back to the 1930s), what led us to believe otherwise? What led us to oversimplify the brain as a domino chain (fig. 2), ignoring all the feedback loops between the elements at each level as well as between the levels (fig. 16)? The answer begins by appreciating that in science, what it means to “understand” something (instantiated as a model of it) is not as straightforward as you might think. Namely, models do not just make predictions that can be falsified; they also capture the phenomenon of interest while illuminating how it works. Illuminating how something works requires some degree of abstraction to highlight how causes lead to effects. Consequently, any model is ultimately doomed to imperfection because it will capture some aspects of reality but not others. In the words of George Box: “There is no need to ask the question ‘Is the model true?’ If ‘truth’ is to be the ‘whole truth’ the answer must be ‘No.’ The only question of interest is, ‘Is the model illuminating and useful?’ ”

Given that you cannot include all reality in a model, any researcher’s challenge is deciding what to include versus what not to. Any system with feedback can be simplified by just including its domino-chain backbone (where, here, the feedback is ignored as part of the simplification). While some properties will be captured, others will not. For instance, if you measure the fluctuations of rabbits and lynx, you’ll be able to describe why the lynx populations are oscillating in a model of the system as a domino chain (lynx eat rabbits)—it’s because their food source is. What you’ll fail to be able to describe is why the rabbits are oscillating in the first place; simply treating that phenomenon as the “input” of your domino chain (and chalking it up to a problem to be figured out later) is a mistake. This is the type of mistake we’ve been making in brain research.

Another way to say it: the emergent properties of systems with feedback are both a benefit and a curse. Even the simplest systems with feedback (like the logistic map described earlier) can behave in surprising ways, depending on how their parameters are set. As long as we set the goal for researchers to “create models that account for things,” there are much easier paths to traverse than ones that attempt to take on emergent complexity. To move forward in a manner that is impactful for understanding brain dysfunction, we will need to shift toward appreciating that the “things” to be explained need to be defined in ways that require feedback. If we perseverate on problems that are too static and too simple, Occam’s razor will continually draw us back to domino chains. Understandably, we spent a few decades applying that approach to focus on tractable problems and solutions. Moving forward, if we want brain research to be impactful, we must move beyond those easier problems and tackle harder ones. We have to commit to understanding the dynamics of these systems—equivalent to focusing on why lynx and rabbits both oscillate, as opposed to focusing on the simpler question of why it is that when there are more rabbits around, lynx proliferate. To unpack how that might apply to brain research, let’s discuss the distinction between processes and things.

FIGURE 16. A framework for thinking about the brain as a complex adaptive system. While the same stages of the molecular neuroscience framework (depicted in fig. 2) remain, in this new framework, the stages connect via more extensive feedback, and each stage is modified to include reciprocal connections between its elements. Because of these combined feedforward and feedback interactions, dysfunction can happen not only following a broken element at any one stage, but also due to the strengths of interactions between the elements or the stages.

Processes, not things

A shift to thinking about the brain as a complex dynamical system instead of a domino chain naturally traverses an ancient philosophical debate about what the universe is made of: processes versus things. In the things way of thinking, the world is made up of just that—things (dogs, cats, me, you, this book, that pencil). Likewise, the brain is something akin to a computer made up of modules that perform functions like seeing, hearing, and remembering. In contrast, the process way of thinking shifts the emphasis from thinking about things in a static way to acknowledge that everything is constantly changing. It’s the famous idea proposed by Heraclitus that you can’t step into the same river twice because the river you would step into a second time is a changed river and not the same as the one you stepped into before. From a process perspective, the idea of a thing called “a dog,” “a river,” or “you” is an abstraction that captures some aspects of reality (the ones that are constant for some time) but fails to capture some others (that nothing lasts forever). The river is an illustrative but silly example (after all, that is the “same river,” as we all know). The real question is: Are there cases in which we misunderstand the brain and mind by artificially regarding the brain and its functions as things? I believe the answer is yes.

While things are natural to think about, processes are less so; in fact, we often don’t have good words with which to talk about them. Imagine talking about a cat, not as a thing but as an impermanent process (it’s mortal, after all): analogous to raining, we might refer to it as “catting.” This doesn’t resonate well, because we think about cats as things, and focusing on their impermanent nature doesn’t make sense. But now consider the more powerful example of a shift toward process-based thinking focusing on notions of personhood during pregnancy. The question is: When someone is pregnant, how many individuals exist in their body? Society debates a lot about when the number shifts from one to two, and this distinction is made from a categorical “things” perspective. As long as the number is one, the fetus is a part of the singular whole, analogous to other parts of the pregnant body (like a kidney). The somewhat dubious idea is that at some point, the number categorically shifts from one to two based on an event (that might reflect the ability of the fetus to live outside the womb or some measure of sentience).

A different, process-based account of pregnancy is one in which a pregnant individual is neither one individual nor two but something in between. The gist is that a pregnant individual is in the process of bifurcating, and bifurcating is not an instantaneous event; it’s a process. This way of thinking follows the notion that organisms (including ourselves) are better understood as evolving processes rather than things. In this way of thinking, the bifurcation could be considered complete at the moment of birth.

Analogously, researchers who think about the brain as a computer often think about it as a conglomeration of neural networks that exists in two regimes. In the second regime, the brain’s modules have learned what they need to do—whether it’s determining the objects in pictures (seeing), the content of sounds (hearing), or remembering that person’s name (memory)—and they do it. This is a very “things” way of thinking about the brain. In contrast, the first regime is more process-like; it’s the phase in which the brain’s modules are incapable of doing much at all and are learning what needs to be done. In this phase, the network is continuously changing, and it’s unable to perform its job well. Once it learns how to do it, learning stops. The implication here is that “things” are the desirable state and “processes” are the messy, underdeveloped (child-like) bits.

The problem with thinking about the brain this way is that our brains and minds continuously learn, adapt, and change. Thinking about the brain from a things perspective is part of why brain functions like emotion, problem-solving, and sanity remain so mysterious. Earlier, we learned that theories about mood suggest it’s part of a system designed to learn and adapt to change—an integration of how surprising recent events are, which influences how we will feel about the things that happen next. Turn off the learning, and mood makes no sense. In this case, learning is not the means to an end because there is no end; learning will forever be continuous. By extension, the brain is not merely an information-processing machine. Instead, the act of processing information changes the brain (and, in turn, the mind). Appreciating this more dynamic, process-based account where the brain continuously learns and adapts will be crucial for understanding the most mysterious brain functions, including mood.

Over the course of writing this book, I’ve come to realize that the human brain’s biggest and most wondrous mysteries do not just include what is typically held up as intelligence. They also include the wonders of how the brain so powerfully drives the mind’s desire and motivation through emotions that are a feature (not a bug), as well as how the brain maintains its stability, including its sanity, by reconciling ever-changing outward and inward worlds.

The new Grand Plan

Simply put, if we want brain research to be impactful for treating brain dysfunction, it’s time to turn our backs on those devilishly tempting domino-chain accounts and embrace the complexity that comes along with thinking about the brain as an adaptive system chock full of feedback loops. It’s a shift away from thinking about brain dysfunction as broken dominos and toward it as a system in which robustness to change comes at the price of fragility. It’s a shift away from thinking about the brain as a sequential information processing machine and toward thinking about it as a system that adaptively seeks good things (and avoids bad ones). It’s a shift away from thinking about treatments as fixing broken dominos and toward treatments as controlling a complex system (where perturbations reverberate in unexpected ways). It’s all the shifts in perspective that follow when we begin to think differently about the type of thing that the brain is. The fragility of an ecosystem or a power grid cannot be captured by a domino chain; the fragility of the brain cannot either.

With these shifts, we’ll have to circle back to the drawing board to rethink everything, starting with what the word “cause” means. We need to broaden our view of causality beyond the notion that there are simple and singular causes that produce brain functions (like reading). Still, at the same time, we aren’t looking for exhaustive yes/no checklists of all possible causal influences (like all the things that disrupt reading, including bee stings). Instead, what we want are models that describe how causal influences interact. And those models begin with the assumption that the brain is not a linear chain but a dynamical system.

Working backward, the presumption that we are working with complex systems helps us begin to appreciate the enormity of what we are up against in the quest to treat brain dysfunction. Treatments amount to controlling a complex system in the sense that they are intended to shift the brain and mind from a less healthy to a more healthy state. It’s a highly nontrivial problem. The weather is a complex system, and we cannot control it in anything but the most trivial ways. In the case of the weather, it’s mainly because it’s the type of (chaotic) system where the impact of even small perturbations is exceedingly difficult to predict. More generally, the challenge is that perturbations in complex systems reverberate because the parts are so reciprocally connected. When our immune system falls out of whack and begins to attack our bodies, we can’t just shut it off (because we will die). But it’s exceedingly difficult to influence in the way we need to, for instance, when an individual’s immune system begins to attack the myelin sheath that insulates neurons (as in the case of multiple sclerosis).

OK, that’s great, but what’s the new analog of “find the broken domino and fix it”? What’s the new version of “find a mutated gene, make a mouse, create a drug”? Or “find a brain area with aberrant activity and stimulate it”? The challenge is that complex systems resist pithy phrases because they don’t fail in ways that are as easy to describe. The cause could be a broken node, an aberrant set point (due to the strength of interaction between nodes), or something else that leads an emergent property to change. The new Grand Plan can’t be captured more succinctly than “create and test models of the brain as a complex adaptive system to infer fragility and determine control.” The phrase launches from the presumption that we have a way to characterize dysfunction via some type of measurement. It emphasizes that the goal is to create a complex dynamical systems model to figure out the causes of the disease (fragility) and how to restore health (control). It’s a less pithy phrase than the one about dominos, for sure. But that’s the reality we’re up against. If we want brain research to be impactful, we must stop dreaming of magic bullets and embrace complexity.

The Grand Plan is shaped around working assumptions about the type of thing the brain is, and even if we presume that it’s a complex adaptive system, that’s still an enormous class of possible things. I’ve thought a lot about whether I can spell out a new grand plan in any more detail, and I’ve concluded that I can’t—the field is currently going through a period of transition, and it’s unclear which ideas about complex systems will have the biggest uptake. What metaphor for the brain will replace the computer? That’s still unclear. Insofar as I’m trying to channel the ethos of this era, it would be dishonest for me to suggest that we’ve converged on some set of well-agreed-on ideas. At the same time, I acknowledge that’s a bit unsatisfying. So let me switch hats from Nicole, the curator, to Nicole, the brain researcher with strong personal opinions. Here, I’ll share the emerging ideas that I’m most excited about, with a note that these ideas are a bit speculative and controversial.

The powerful metaphor I keep circling back to envisions the brain as a coin with two sides. The first side focuses on what the brain does—its functions (including adaptive functions) like seeing, remembering, feeling, and deciding. The second side focuses on keeping the brain in balance. Let’s start with the first side. We know that when brains “compute” to perform their functions, they do so via a system of loops, where one part of the brain connects to another, and that part connects back again; consequently, the brain’s functions are typically “emergent properties” of a network that is highly interconnected. We discussed an example of this earlier, where a recurrent neural network was used to model switches between different types of decisions in prefrontal cortex (thus replacing the obviously wrong idea that this happens by a little person in our heads pulling a lever).

For this type of network to operate effectively, neurons must connect via excitation and inhibition with exquisite balance. If excitation dominates, even a small sensory input (like a quiet sound) will trigger an amplifying loop of runaway brain activity, leading to a seizure. If inhibition dominates, even a giant sensory input (like a loud sound) will fail to stimulate brain activity, leading to a coma. If the balance is right, however, the brain can operate as it should. That balanced point positions the brain at the knife edge of order and disorder, called “criticality.”

This brings us to the other side of the coin, which describes how the brain maintains health by keeping itself balanced right at this knife edge. This side of the coin involves a type of homeostasis. Extending Walter Cannon’s “Wisdom of the Body,” we might consider it the “Wisdom of the Brain.” Across decades of work, researchers have determined that there isn’t a single way that the brain continually balances itself; there are many. Some mechanisms work to stabilize the excitatory connections between neurons; others work to stabilize the inhibitory ones. Yet others work to adjust how excitable the individual neurons themselves are. It’s complicated. Moreover, this rebalancing act has to happen continuously as the brain continuously learns and adapts.

The two sides of this coin, positioned at the knife edge of disorder, suggest a powerful way to think about how the brain functions and what leads to its dysfunction. One side focuses on how the brain’s functions emerge from connectivity and dynamic patterns of activity; the other focuses on how the brain keeps itself balanced to function as intended. Notice that both rely on the presumption that the brain is not a domino chain but has both feedforward and feedback connections.

Researchers have worked to transform these metaphorical ideas into a set of well-formulated mathematical theories, complete with falsifiable predictions. Among those predictions is that when networks of neurons are poised at criticality, they are best able to process information. The prediction is difficult to test in real networks because it’s difficult to systematically manipulate an actual brain in the ways that are required (for instance, to shift the balance between its excitation and inhibition). However, it’s trivial to test in the artificial neural networks often used to model the brain. There, researchers continue to quibble about whether information is maximized right at the knife edge or merely very close to it. Some also argue that maintaining a real brain right at the knife edge is dangerous (because small changes could trigger a seizure), and they suggest that the brain probably keeps a buffer zone away from the edge for safety. Still, they generally agree that the gist of thinking about the brain somewhere near the knife edge must be correct.

What I find most exciting about this proposal is all the ideas—the Copernican insights—that are being triggered by a shift to thinking about the brain in this new way. We’ve discussed how these ideas have already been central to creating new ways to measure one of the brain’s most mysterious functions—consciousness—including consciousness in patients that may be “locked in.” These ideas have also led to new insights into an equally provocative mystery: why we need to sleep. Launching from the notion that sleep might have something to do with restoring brains to the knife edge, researchers have measured where rats’ brains fell relative to the knife edge around the clock as rats engaged in everyday laboratory behavior (such as playing and interacting with other rats) and sleeping.

To measure whether the rats’ brain activity patterns fell at the knife edge, the team drew from earlier work linking the knife edge to cascades of brain activity, called avalanches. You might remember the idea from when we discussed it for consciousness. The gist builds on the idea that in real brains, connections are reciprocal, and consequently, the activation of a brain area reverberates to produce a burst of activity. When the connections in the brain are balanced such that the brain is positioned in its healthy “just-right” regime, short bursts of activity are frequent, and large bursts are rarer. In fact, right at the knife edge, the frequency of activity bursts falls off as a power-law. This benchmark provides researchers with something to compare an actual brain to and determine whether it’s poised right at the edge. In comparison, when a brain becomes uncalibrated, longer bursts will happen either too rarely (nudging toward a coma) or too often (nudging toward a seizure), and researchers can determine that as well.

The researchers found that during the day, the rats’ brains naturally deviated from the knife edge. However, sleep restored their brains closer to it. To be sure that the differences were caused by wakefulness and sleep (as opposed to some other factor, like the times imposed by a day/night rhythm), the researchers mimicked modest sleep deprivation by keeping the rats up for an additional 90 minutes beyond their typical sleep time. With this modest sleep deprivation, deviations from the knife edge increased significantly. However, a bout of sleep restored their brains to healthy levels. These results support the idea that brains gradually become uncalibrated during normal wakefulness, and one function of sleep is to recalibrate and bring them back to the knife edge again.

Other researchers are connecting these ideas about sleep to notions of how brain dysfunction might follow from sleep disruption—either because sleep is not happening enough or because something prevents it from happening effectively. One example is the (still speculative) proposal that the progression of Alzheimer’s disease follows from a brain that becomes incapable of fully restoring itself during sleep, leading to its progressive decline. Until now, it’s been difficult to determine the consequences of ineffective sleep because we haven’t had good ways to measure how sleep-restored a brain is. Following ideas about the relationship between sleep and the knife edge, we may be one step closer to measuring a brain’s sleep restoration, enabling us to test ideas about the relationship between quality of sleep and Alzheimer’s.

Ideas about the brain operating at the knife edge are also leading researchers to new insights into some of the brain’s most mysterious disorders. Phelan-McDermid syndrome is a form of autism spectrum disorder that leads to developmental delay and intellectual disability. This disorder’s cause is clear: it follows from mutations in a single gene (SHANK3). While we’ve known about this mutation for decades, we don’t understand how the complex symptoms of the disorder (like intellectual disability) follow from mutations in this gene. In experiments that involve recapitulating this mutation in mice, researchers have shown that the mutation leads to an impairment in one of the homeostatic mechanisms that the brain uses to maintain balance. While this result still needs to be replicated in humans, it suggests that the mutation responsible for Phelan-McDermid syndrome may lead to an inability of the human brain to maintain itself at the knife edge. One of the things I find most compelling about this particular way of thinking about the brain is the natural throughline across molecular, algorithmic, and functional (Marr’s how, what, and why) levels, because connecting these levels can expedite the development of new treatments.

In the long run, will the idea of the brain as a two-sided coin poised at the knife edge of disorder become the new way of thinking? And will the new Grand Plan come to be shaped around that idea? Only time will tell. But as I write this, I’m seeing evidence accumulating in support of the idea, and I’m optimistic. The idea is inspiring ways to measure things we’ve never been able to measure before, like sleep restoration and consciousness. It’s providing new leads for understanding exceedingly complex things, like the symptoms associated with some types of autism spectrum disorder. While none of us can tell the future, I can say it’s certainly one promising idea that researchers (including myself) will pursue. It builds out the idea of the brain as a complex adaptive system, not a domino chain.

Reconsidering the edifices

In this book, I’ve sought to elevate the conversation around the bottlenecks to new treatments for brain dysfunction. I commend others who have stuck their neck out to offer different views of those bottlenecks that we can debate and discuss; among them is the former NIMH director Steve Hyman.

As Hyman sees it, the thing most holding back treatments for brain dysfunction (and particularly mental dysfunction) is individual variability and the chicken-and-egg problem it creates. We have plenty of evidence that many neurological and psychiatric disorders (like depression) follow not from a single cause but from a multitude of them (such as variation in different genes or aberrant activity in different nodes of a network). It implies that what we think of today as “disorders” may not have singular treatments but require precision medicine-based approaches that pinpoint the disorder subtype that an individual carries, like cystic fibrosis and many cancers. The challenge researchers face is thus: How do you identify causes if you can’t cluster individuals with shared causes (fig. 4)? That’s the chicken-and-egg problem of precision medicine, a genuine, hard problem that must be solved. It’s also a problem that’s been discussed extensively and one for which entire programs at the National Institutes of Health (such as the RDoC program at NIMH) have been shaped (thanks, in part, to Hyman).

Hyman is among those who enthusiastically point to new technologies like large-scale genetic screens, proclaiming “Progress at Last.” He argues that research into mental disorders has reached an inflection point due to the existence of large-scale genetic screens that (if appropriately interpreted) can provide researchers with “finding tools” to identify the causes of mental disorders. Acknowledging that individual genes contribute in only small ways, Hyman highlights the neurobiological insights that can be gained from rare variants that are strongly associated with them and the role that combining across genes to compute risk can play in diagnosis.

While I agree with Hyman’s suggestions that these are reasonable and promising paths to pursue, I believe that progress will require one more fundamental piece. Hyman’s account emphasizes technological developments as the bottleneck with the presumption that edifices haven’t been going up because we’ve been brick-limited. Here, I’m sticking my own neck out to claim that the only way we’ll solve the chicken-and-egg problem of individual variability is to also change the blueprints to reflect a shift toward thinking about the brain as a complex adaptive system. In other words, “Progress at Last” will require both collecting the right bricks as well as getting the blueprints right. Ultimately, Hyman agrees, “We are brick-limited, but having the bricks alone does not spit out an easy answer to the question of ‘What is the mechanism causing mental illness?’ in a person. The answers will require interdisciplinary approaches that respect complexity.”

What does the path forward look like? A fruitful route to the end goal of controlling a complex system begins by understanding it (ideally with great detail). Like the color of the International Space Station, some of those details ultimately won’t matter in the end for control. However, we can’t be sure what will versus won’t matter from the outset. As Hyman highlights, the -omics revolution is now providing us with massive amounts of data. It includes genomics (to map genes and genetic networks), epigenomics (to map genetic modifications), proteomics (to map proteins and protein networks), connectomics (to map how neurons connect together in cellular and brain-wide circuits), and organomics (to map how organs influence one another). Likewise, revolutions in new ways to record brain activity are providing us with massive amounts of data recorded with multichannel electrodes, optical imaging, and noninvasive measures like fMRI and EEG. We also have a multitude of behavioral measures that are increasingly being standardized, as we’ve discussed for depression. It’s chaos in the brickyard of brain research, and the question is: What should we do with the bricks that are piling up so quickly? The answer is not to configure them into a domino chain but to consider them components of a complex dynamical system.

I am optimistic that the time is ripe for breakthroughs in brain and mind research, for three reasons. The first relates to the fact that the emergent properties of complex systems follow from interactions between their parts. This implies that we need to measure their parts simultaneously (not one at a time) to study them. Following on breakthroughs in biotechnology and computation, we are able to collect and process this type of data at all levels (including genetic, brain activity, and lived experience) for the first time. The second follows from breakthroughs in AI that enable us to train neural networks with feedback to solve nontrivial tasks, allowing us to consider these as models of the brain rather than massively simplified toy models of what the brain might be a bit like. The final reason follows from insights into how these models work, which are providing us with novel ideas about how the brain and mind operate. Ultimately, figuring out ways to control these systems, in the form of treatments, will require these models and insights.

All the other things that need to happen

By focusing on the need to shift to thinking about the brain as a complex system, I do not mean to imply that all will be solved once we do. I recognize that in developing new treatments, there are many practical and technical challenges that I have not addressed in this book.

One example is Huntington’s disease. It is a neurodegenerative disorder that typically begins with minor twitching that evolves into more pronounced, involuntary jerky movements called chorea. It is caused by the mutation of a single gene, HTT, that codes for the protein huntingtin. In most of us, huntingtin transports nourishing substances down the axons of neurons, helping them thrive. In individuals with the HTT mutation, the protein is toxic and triggers premature cell death. Healthy versions of the HTT gene include a stretch of 10–36 repeats of the genetic sequence CAG, the codon for the amino acid glutamine. During DNA replication, DNA polymerase can perseverate on these tandem repetitions, creating a loop that produces extra copies of the already repeated codon. When the number of CAG repeats exceeds around 36, the mutant protein tends to get cleaved into small fragments that aggregate within neurons and become toxic. The severity of the disorder and its age of onset are linked to the number of CAG repetitions an individual carries. In those who are afflicted, the number of repeats can proliferate across generations.

The problem is that we’ve known all this for more than 30 years, and we still don’t have a treatment or a cure for Huntington’s. It’s a case in which it’s unclear how shifting toward thinking about the brain as a complex dynamical system will be the key to unlocking progress. Rather, the most likely solution for Huntington’s will be to eliminate the mutation, probably via gene editing techniques like CRISPR. While gene editing therapy has been approved for sickle cell disease, it involves genetically modifying blood stem cells outside the body and then replacing them. Unlike blood cells (that turn over across our lifespan), we are born with most of the neurons in our brain; thus they cannot be edited outside the body and then replaced in the same way. Gene therapy for Huntington’s will therefore require a different approach, but one that (ultimately) seems feasible. Other disorders linked to single gene mutations, including the rare variant of Alzheimer’s disease that Carol Jennings’s family carries (described in the opening of the book), may ultimately benefit from similar gene editing strategies. But it’s unclear how gene editing could help with disorders that are more weakly linked to many different genetic variants (like depression and most cases of Alzheimer’s disease).

There are also many other impediments to new therapies. Among them are the enormous risk and cost of clinical trials, the lack of financial incentives to develop treatments for rare disorders and brain stimulation devices, and the complexities of working with the FDA to define endpoints for clinical trials. Likewise, the phases of brain research that precede clinical trials are fraught with many unsolved problems, including issues with replicability, increasingly perverse incentive structures for researchers to publish quantity over quality, and a grant system that rewards researchers for “staying in their lane” as opposed to integrative, collaborative efforts. We also need to find more and better ways to conceptualize and integrate brain-based versus psychological and social interventions. All those are genuine problems that we need to address (and each could be the topic of its own book).

By focusing on the need to shift to thinking about the brain as a complex system, I intend to amplify what I see as one of the biggest and most underappreciated bottlenecks in brain research as a whole. It affects the entirety of it, given that how we think about “the type of thing that the brain is” informs research at every stage, from the nuts-and-bolts understanding of how the healthy brain works to understanding its dysfunction and how to treat it.

The special considerations of minds

I do not know how far we are away from curing (or even effectively treating) Alzheimer’s. But it doesn’t strike me that it’s out of the realm of possibility that the answer is “not far.” I don’t want to trivialize what needs to be done; it’s anything but trivial. But we have a good concept of what needs to happen. In that way, it’s like cancer, where the problem is clear: something stops normal cell death, and the goal is to kill the cancer cells or return cells to their healthy state. Likewise, the neurodegeneration associated with Alzheimer’s, Parkinson’s, and multiple sclerosis is triggered by something, and the goal is to figure out how to stop it and return cells to their healthy state. Incredible strides have been made in cancer research over the past decade. It wouldn’t be a huge surprise if that started to happen for Alzheimer’s and other neurodegenerative diseases as well (and I hope it does!).

In comparison, the gulf between where we are now and curing or effectively treating many psychiatric conditions seems more vast. This is because we often can’t even say what the goal is beyond jumping from the word “cause” to a description of disorder symptoms, like “treat the causes of psychosis” or “treat the causes of depression.” These are clearly disorders that follow from interactions between brains, minds, and events in the environment, and we haven’t yet found good ways to think about them. What, then, does the path forward look like?

By analogy with understanding temperature, we’ve figured out some ways to measure the mind (at least symptomatically), but we’re a bit lost in terms of theories about the forces that give rise to it. Let’s compare temperature with depression. At one point in history, temperature researchers had figured out ways to measure temperature via thermometers; today, depression is diagnosed based on symptoms. Temperature researchers had ruled out “caloric” theory (which proposed that heat was a physical substance); for depression, we’ve ruled out simple theories like it’s caused by reduced levels of neurotransmitters in the synapse. The next step for temperature was the development of a theory about it—thermodynamics—and the idea that temperature is about kinetic energy. What is the next step for depression? My guess is that we’re not just looking for some type of biomarker. Like temperature, I bet that the next big step will be a theory that suggests what we should measure in the brain or behavior—perhaps of the type I introduced earlier. There, I described how researchers are beginning to write down equations about what mood depends on, and the terms in those equations (like surprise, also called reward prediction error) can be linked to things in the brain (like dopamine release). Similarly, we now have a remarkable class of AI models (like large language models) that are helping us link algorithms to intelligence. I suspect we are on the cusp of some incredibly exciting science that will help us bridge the brain and the mind.

In the quest to understand minds by studying brains, it’s also helpful to differentiate research focused on understanding versus research focused on creating treatments. The two differ insofar as the end goal of brain research is not necessarily brain-based interventions for mental disorders. As described by the psychiatrist Kenneth Kendler, brain research can help us understand the mind and psychiatric illness by “expanding the domain of the understandable.” The gist behind this idea is that understanding how the brain works can inspire new ideas about the mind and its dysfunction that are then incorporated into behavioral theories (and, in turn, developed into behavior-based treatments, like talk therapy).

There exists a continuum of positions on how research on mental disorders should proceed. At one extreme, some believe that the regular ups and downs of living have been overmedicalized. They point to the financial interests of pharmaceutical companies as the driving force. We are medicating our most energetic children to make them complacent to sit unnaturally for hours and learn. We are creating societies that make people miserable and then providing happiness pills to the most sensitive among us to take the misery away. Advocates of this position argue that we need to focus our research efforts on psychological and social interventions to alleviate the misery, not brain-based ones.

At the other extreme is the position that all mental disorders should be thought of as brain disorders. The motivation behind it circles back to the notion that no force in the universe gives rise to the mind other than the brain, and so all mental illness must ultimately be reflected in the brain. Advocates of this position argue that the goal is not to medicate away misery but rather to treat mental illness in the same way that we treat other medical disorders, like diabetes. Of course, environmental factors play a role—clean air, healthy food, exercise, and freedom from both trauma and extreme stress are important, but the same is true for individuals with diabetes as well; in this view, diabetes is conceptually no different than depression. Advocates of this position acknowledge that, yes, of course, we should research the psychological and social factors that exacerbate these conditions (as we do for diabetes research). However, the bulk of our research efforts and dollars should focus on the biological phenomenon that is the bottleneck for disease (in the case of diabetes, the pancreas and insulin; in the case of mental disorders, the brain).

As a brain researcher and professor embedded in a psychology department (with a clinical psychology program), I know researchers who hold positions at many points along this continuum. However, I do not know anyone who adopts the position of either extreme. Some of my colleagues are vocal opponents of the overmedicalization of mental illness, and they argue that we should be investing more extensively in psychological and social prevention and treatments. Most also acknowledge, however, that brain-based interventions are required and effective for at least some individuals, and that brain research to treat mental disorders is worth investing in going forward. Conversely, I don’t know of any brain researchers who think brain-based interventions like antidepressants should be the only (or even the first) treatment for depression or anxiety, or that brain-based interventions will ever be the singular approach. Disputes within the community amount to questions over how to direct resources (in terms of effort and research dollars) for brain/mind research: Should it be 10/90? 50/50? 90/10? And to what degree can and should we remove financial interests (for instance, of pharmaceutical companies) from the equation?

My own take lies squarely in the middle of these two extremes. I am concerned and alarmed by the rise of misery, and I do not think we should try to medicate our way out of it; we need to do more to alleviate it through social restructuring. I am also extremely alarmed by the degree to which medication is prematurely and needlessly pushed on us by our doctors without first trying other options, like behavioral therapies. But it is clear to me (and probably everyone else) that psychological and social interventions will not be the route to good treatments for neurological disorders like Alzheimer’s and Huntington’s disease. My take is that they also won’t be the exclusive path to treating psychiatric disorders, in part because some of those interventions will target the brain. Even for ones that do not, my strong intuition is that an impactful understanding of the mind will require understanding the brain, as Kendler says, “to expand the domain of the understandable.” Consequently, I believe we need a distributed portfolio for mental health research that focuses on both brain and mind research.

I’m also moved by the notion that there are two different and complementary ways to “know” minds. The idea was popularized by the psychiatrist Karl Jaspers in a psychopathology textbook first published in 1913. The first way of knowing minds resides in the natural sciences and focuses on objectively understanding them, with questions like: How do minds work? Under what conditions do minds thrive? What causes mind dysfunction? The other way we understand minds is through the empathetic ways we come to know an individual’s mind. What is their story? When they are depressed or anxious, what caused it? With a focus on storytelling, the latter better captures the beauty, tragedy, and complexity of the human condition, and it overlaps with the domain of the humanities. Certainly, something profound can get lost when we focus exclusively on minds objectively. Psychiatrists have to navigate both ways of knowing when treating their patients.

In comparison, researchers focused on understanding how minds work must be objective. Finding ways to incorporate the diversity of causes for mental disorders is part of that agenda. But with so much at stake in brain and mind research, they must focus on developing rigorous, verifiable knowledge that will ultimately lead to good options that psychiatrists can use to treat their patients. The quest of a brain and mind researcher might be intensely motivated by empathy for individuals with dysfunction; for many, that is what gets them out of bed in the morning and into the lab. But once there, the first way of knowing needs to kick in for them to contribute rigorously to science.

Perspective Neuroscience

This book began as a personal quest to understand the Grand Plan for brain research. In the pursuit of understanding what was happening in brain research globally (and why), I found myself mulling over some fundamental questions, like: How is brain research supposed to work? What is the collective Grand Plan toward progress? I was surprised by how much I struggled to find answers clearly written down; I just assumed that these things were documented somewhere. It turns out that if you look, they are pretty hard to find.

As I finally sat down to puzzle through what the field was up to, it wasn’t just illuminating; it was transformative. I began to see that much of what I had presumed to be true was not (or at least not entirely). For instance, I assumed that the new drugs introduced each year were more novel than they are. Likewise, I assumed that new drugs followed from novel discoveries about the brain more than they do. I also presumed that thinking about the brain largely as a domino chain was “close enough” to accomplish what “we” want to do. Moreover, while I noticed that some researchers thought in other ways (like thinking that oscillations were worth studying, or that evolutionary perspectives were useful, or that “process-based” accounts of the brain and mind were important), I could not see the logic behind them, and it was hard to find their justification explicitly written down.

The type of discussion I’m referring to here doesn’t have a name but needs one; I call it Perspective Neuroscience. That title follows from what this type of discussion is often called when it appears in a scientific journal: a perspective piece. Walking away from this exercise, I’m leaving with the impression that we should be doing much, much more of it. Perspective Neuroscience draws on insights from several existing fields, but it’s not squarely in any one of them. It overlaps with the history of science and what philosophers call methodology, which aims to describe the methods scientists should and do use to go about their work. However, only a subset of what philosophers discuss is of practical interest to inform how the brain works. Perspective Neuroscience incorporates practical discussions that go beyond the traditional philosophical boundaries. Its goal is not to arrive at a narrow prescription of how ideas about the brain and brain research should proceed (which may be misguided), but rather to establish a set of overarching ideas and encourage thoughtful discussion around them. The principled need to pursue multiple paths to answer any big question is known as pluralism, as I described earlier (which I advocate for).

There are a few arguments against investing time and effort in Perspective Neuroscience. First among them is that it’s somehow not “real” science and thus a waste of time. I can appreciate the sentiment that scientific progress depends on scientists seeing through the nitty gritty and hard work that traverses from questions to answers. We can’t all sit around and just think (and write books!). But I caution that answering questions that aren’t worth answering is just as much of a waste. How many quarks are in a neuron? Let me count.… But wait—who cares? Why is that worth knowing? Brain research breaks when the number of “papers published” or “facts collected” becomes the goal. Perspective Neuroscience helps us thoughtfully consider what ideas we should invest in and how to go about it. It requires researchers to think explicitly about the Grand Plan instead of getting wrapped up in the inertia of continuing along the path that has seemingly worked before.

A stronger argument against spending too much time engaging with Perspective Neuroscience is one expressed by the philosopher Michael Strevens: “Although scientists know very well how to implement their methods, they don’t know what it is about those methods that really matters, and why … you’ll find no more agreement among the [historians, sociologists, and philosophers] than you do among working scientists.” In other words, no one really knows how science works. Likewise, science typically plows ahead quite successfully in the absence of explicit Grand Plans of how to proceed, and efforts to formalize Grand Plans tend to be contentious. Consequently, if you suspect something might be a bit off, it isn’t easy to diagnose what that might be (and one wonders if it’s worth trying). As a wise group of researchers once wrote, “Predicting the future of brain research is a fool’s errand.”

On the other hand, if we don’t lay out some notion of the path forward, we will likely wander around in the woods and get lost. We need to mark some paths and create some maps, minimally, because we need something to debate and discuss. While there is some truth to what Strevens is pointing to, the simple fact is that insofar as we are interested in understanding how the brain works, we internalize ideas about what the answers look like (and how more answers should be chased). It only makes sense to make those implicit ideas and the Grand Plan explicit so we can discuss them with one another (as well as ourselves).

The beginning of a new era

No one doubts that the brain incorporates feedback. We all know that the brain is not actually a domino chain. But for a long time, the big question has been: Does it matter? What’s a few loops, after all? Do they do anything? I didn’t see why those loops mattered until I connected the dots between where we are now and where we want to be.

The shift to thinking about the brain as an adaptive system is an enormous shift that will have profound implications for my work going forward. Before this book, I focused squarely on sifting through an immense amount of complexity about whatever system I was working with to arrive at elegant, intuitive descriptions of how it works. I still am very much committed to that. I now realize, however, that this can most easily be done in systems that can be approximated as domino chains, and thinking about the brain this way will fall short of what we need to know to understand the brain’s dysfunction. In my future work, I am committed to investigating the brain in ways that better capture the complexity and fragility and marvels of the human brain. I envision that this will involve focusing squarely on its adaptability. It is a new era for the field, including me.

Stepping back to reflect, every scientific career has phases coupled with the broader goings-on in a field. My own can be summarized by my relationship with the largest annual meeting in all brain research, the Society for Neuroscience Meeting. The first time I attended it was in Washington, DC. The meeting is enormous. Attended by around 30,000 brain researchers each year, it can be accommodated by only a few venues in the United States. Across its five days, scientists exhibit their new work in about 14,000 presentations as talks and posters. The first time I attended, I was an undergraduate, there to deliver a poster on a small project I was involved in. While my presentation went just fine, I overloaded myself trying to wrap my head around the rest and fled to the Smithsonian Museum, just around the corner.

In later years as a trainee, first as a PhD student and then as a postdoc, for me that meeting morphed from overwhelming to thrilling. I no longer tried to take in the entire meeting but focused on what was happening in the subfield I worked in at the time (vision). The most exciting discoveries were delivered as short talks organized into sessions. We packed in wall-to-wall to hear them, and they left us buzzing and discussing for weeks. With a new set of things to buzz about each year, I always left the meeting with the sense that important things were happening. It was exhilarating to be part of it.

As a professor, my experience of the meeting morphed again, this time from exhilaration to disenchantment. I attempted to glean the significant developments across the entire field and began to wonder: Globally, are we making real progress? Or are we collecting crumbs of facts along a path with an uncertain destination? For answers, I turned to the largest talks delivered by individuals who had made the biggest discoveries. On a few occasions, I got really excited by those talks, and in those moments, I felt the same thrill as in my earlier days—I was part of an enterprise that was big and important and progressing! But more often, I was left underwhelmed, scratching my head. Facts, absolutely. Nobel Prizes, awarded—but by what rationale? Will these insights better enable us to fix brains? Does this work inform a big idea? I wasn’t always so sure.

At some point, I began avoiding the biggest meeting in brain research. I didn’t explicitly understand why I stopped going; I just stopped. In retrospect, the enormity of the meeting forced me to confront a type of existential dread about the field at large, and that led me to question the value of my contributions to it. A lot of what was happening struck me as a bit wasteful. With tens of thousands of individuals working on these problems, we should see more impactful progress toward understanding and treating brain dysfunction. I wondered: Is my work somehow an exception? My own grants have always included phrases like, “These results could inform new treatments for deficits in memory such as age-related dementia.” Insofar as that was the goal, I wondered: What makes me think that my contributions aren’t wasteful, too?

Now that I’ve had the opportunity to spend a few years thinking and writing this book, I’m ready to return to the annual meeting. In part because my perspective on how science works has changed, I now better appreciate that, in science, we won’t get things right immediately out of the gate; that’s just not how science works. Instead, we begin by taking our best guess, and we iterate our way to good solutions. Each generation need not definitively “lock down” certain answers for the next generation to build on their work. Even more than that, I can see that I was picking up on something fundamental: the Grand Plan of “find the broken domino and fix it” wasn’t panning out, and I was intuiting it (albeit not in a way that I could explain at the time). Now that we’ve spent a few decades working out those domino-chain backbones, and now that we realize how important the feedback loops are, we’re ready to incorporate them.

The real reason I’m ready to return to the annual meeting is that I can see that the field is shifting toward a new Grand Plan: “create and test models of the brain as a complex adaptive system to infer fragility and determine control.” It’s one that I’m optimistic about because I believe it will lead us to new treatments for brain dysfunction. Success requires us to rethink how we approach everything, from what causality means to how we conceptualize the types of treatments that are likely to be successful. It also requires us to revise the textbooks. But I believe we’re ready to embrace it. I, for one, am excited to dive in and help make it happen, and I know that many others feel that way too. This shift, and all the excitement around it, is the new ethos of brain research. It marks the beginning of a new era—not just for “fixing” the brain when that needs to happen, but for understanding ourselves and the stuff we’re made of, too.

ACKNOWLEDGMENTS

Writing this book was a transformative journey, and I am grateful to everyone who helped make it happen. First and foremost, to my editor, Hallie Stebbins, who helped me transform an unruly, unanswered question into a book. I liken the process to earning a second PhD, where Hallie served as my wise and patient PhD mentor, and I operated as a graduate student with some creative but ill-formed ideas about how to proceed. Along the way, Hallie contributed in innumerable ways, including pulling the project out of the weeds on at least two occasions. I am tremendously grateful to Hallie for all that she invested in this project, and to Princeton University Press for empowering her to make it happen. I benefited from a model designed to transform big questions into answers, and I am thankful that Princeton University Press exists. I appreciate its support at all levels, including its sponsorship of a writing course with Helen Sword.

I also appreciate the individuals who shared their experience with brain and mental dysfunction and gave their blessings for me to share their stories with you, including Stuart and John Jennings (husband and son of Carol Jennings), Travis Rieder, Benjamin Stecher, and Esmé Weijun Wang. While I did not have the privilege of interacting with William Styron or Richard Marsh, I learned from them through their writing. When this project became overwhelming, the moving firsthand accounts of all these individuals motivated me to plow forward.

Special thanks go to Daphna Shohamy for her generous and multifaceted support as a “book doula.” Also to Joseph Meyer for providing extensive and well-informed feedback on drafts from the perspective of a family touched by these issues. And to Jason Karlawish and David Sussillo for nudging me to see through the “ask” to a more coherent and fleshed out “answer.”

This book covered expansive territory, and I reached out with many inquiries and requests for help. I am grateful to the long list of individuals who responded, including Awais Aftab, Bruno Averbeck, David Barack, Dani Bassett, Michele Basso, Hanah Bayer, John Beggs, Rebecca Berman, Bill Bialek, Simon Bohn, Jagpreet Chhatwal, E. J. Chichilnisky, Paul Cisek, Marlene Cohen, Phil Corlett, Mark Desposito, Theresa Desrochers, Jim DiCarlo, Eran Eldar, Martha Farah, Paul Glimcher, Josh Gold, Dan Goodman, Catrina Hacker, John Hardy, Cate Hartley, David Heeger, Keith Hengen, Mark Humphries, Steve Hyman, Thomas Insel, Barnes Jannuzi, Yohan John, Joe Kable, Roozbeh Kiani, librarian Sam Kirk, Brian Knutson, Peter Lansbury, Joe LeDoux, Carol Mason, Luca Mazzucato, Barb Mellers, Earl Miller, Kevin Mitchell, Chris Moore, Tony Movshon, Brigitte Nerlich, Bill Newsome, Yael Niv, Desmond Oathes, Bijan Pesaran, Luiz Pessoa, Steve Piantadosi, Viola Priesemann, Lauren Ross, Ayelet Ruscio, Robb Rutledge, Andrew Scull, Robert Seyfarth, Shan Siddiqi, Eero Simoncelli, Tania Simoncelli, Sergey Stavisky, Peter Sterling, Andra Stratton, Veit Stuphorn, George Sugihara, Gina Turrigiano, and Jonathan Victor, as well as those whom I have (undoubtedly and regretfully) forgotten to acknowledge.

I also thank the Simons Foundation’s Collaboration on the Global Brain and everyone involved in making it happen, including Jim and Marilyn Simons and David Tank. It was through my participation in that program’s annual meetings and workshops that I first began to appreciate how dynamical systems are transforming our understanding of the brain and mind.

My efforts to channel the ethos of our era also benefited from innumerable interactions on social media. I appreciate the many researchers who shared their perspectives, as well as the individuals with brain and mental disorders who opened up to help me (and others) understand.

Finally, much gratitude and love to my partner Alan Stocker for his patience and tolerance of a project that occupied so much of my headspace for so long—as well as for providing me a host of wonderful reasons to maintain my own balance to ensure that this massive project did not take over my everything.

NOTES

Chapter 1: The Grand Plan

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Part I. How did we get here?

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Chapter 2: From bench to bedside

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Chapter 3: The most complex thing humankind has encountered

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Part III: A new era

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Chapter 7: What causes what?

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Sugihara’s approach. McGowan, J. A., et al. Predicting coastal algal blooms in southern California. Ecology 98, 1419–1433 (2017); Nova, N., et al. Susceptible host availability modulates climate effects on dengue dynamics. Ecol. Lett. 24, 415–425 (2021); Saberski, E., Park, J., Hill, T., Stabenau, E., & Sugihara, G. Improved prediction of managed water flow into Everglades National Park using empirical dynamic modeling. J. Water Resour. Plan. Manag. 148, 05022009 (2022); Sugihara et al. Detecting causality in complex ecosystems.

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Chapter 8: From understanding to treatments and cures

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The pharmaceutical company. Giladi, N., et al. Safety and efficacy of venglustat in GBA1-associated Parkinson’s disease: An international, multicentre, double-blind, randomised, placebo-controlled, phase 2 trial. Lancet Neurol. 22, 661–671 (2023).

As the Parkinson’s researcher. 2022 Neurodegenerative Disease Workshop: Peter Lansbury, Bial Biotech/Harvard Medical School (2022).

Channeling the ethos. den Heijer, J. M., et al. A phase 1B trial in GBA1-associated Parkinson’s disease of BIA-28-6156, a glucocerebrosidase activator. Mov. Disord. Off. J. Mov. Disord. Soc. 38, 1197–1208 (2023).

    Alzheimer’s researchers are. Rollo, Crawford, & Hardy. A dynamical systems approach.

Examples include tapping. Shine, J. M. Neuromodulatory control of complex adaptive dynamics in the brain. Interface Focus 13, 20220079 (2023).

It was first. Lanska, D. J. J. L. Corning and vagal nerve stimulation for seizures in the 1880s. Neurology 58, 452–459 (2002).

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This led to. George, M. S., et al. A one-year comparison of vagus nerve stimulation with treatment as usual for treatment-resistant depression. Biol. Psychiatry 58, 364–373 (2005).

One idea is that. Shine. Neuromodulatory control of complex adaptive dynamics.

Each year, around. Feigin, V. L., et al. Global and regional burden of stroke during 1990–2010: Findings from the Global Burden of Disease Study 2010. Lancet Lond. Engl. 383, 245–254 (2014).

about 80% have. Langhorne, P., Coupar, F., & Pollock, A. Motor recovery after stroke: A systematic review. Lancet Neurol. 8, 741–754 (2009).

For over a century. Oden, R. Systematic therapeutic exercises in the management of the paralyses in hemiplegia. JAMA 70, 828–833 (1918).

Today, that often. Kwakkel, G., Veerbeek, J. M., van Wegen, E.E.H., & Wolf, S. L. Constraint-induced movement therapy after stroke. Lancet Neurol. 14, 224–234 (2015).

IpsiHand therapy builds. Chollet, F., et al. The functional anatomy of motor recovery after stroke in humans: A study with positron emission tomography. Ann. Neurol. 29, 63–71 (1991).

IpsiHand works by. Holmes, C. D., et al. IPSIHAND BRAVO: An improved EEG-based brain-computer interface for hand motor control rehabilitation. In 2012 Annual International Conference of the IEEE Engineering in Medicine and Biology Society, 1749–1752 (2012).

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When treatment is. Holmes, J. M., & Levi, D. M. Treatment of amblyopia as a function of age. Vis. Neurosci. 35, E015 (2018).

Building on work. Morishita, H., Miwa, J. M., Heintz, N., & Hensch, T. K. Lynx1, a cholinergic brake, limits plasticity in adult visual cortex. Science 330, 1238–1240 (2010).

In a small pilot. Wu, C., et al. Durable recovery from amblyopia with donepezil. Sci. Rep. 13, 10161 (2023).

Another therapy that. Nardou, R., et al. Oxytocin-dependent reopening of a social reward learning critical period with MDMA. Nature 569, 116–120 (2019).

This happens with. Nardou, R., et al. Psychedelics reopen the social reward learning critical period. Nature 618, 790–798 (2023).

More than 100. Kurtz, J. S., et al. The use of psychedelics in the treatment of medical conditions: An analysis of currently registered psychedelics studies in the American drug trial registry. Cureus 14, e29167.

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As described by. Niv, Y. Personal communication.

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Chapter 9: A new era in brain research

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The discovery of. Pardes. NIMH during the tenure of Director Herbert Pardes.

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That balanced point. Beggs. The Cortex and the Critical Point.

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INDEX

A page number in italics refers to a figure.

adaptation, 224–25; learning and, 229; and shift in thinking about the brain, 246–47. See also complex adaptive systems

Adderall, 98

addiction: brain disease model of, 180; causality and, 173, 175, 176; complex dynamical systems and, 180–81, 182, 183; DSM categories and, 179; feedback loops and, 116–17; to opioids, 179–83; psychosocial factors in, 180

aducanumab, 3

affect, 123–24

affective states, 123

AlexNet, 95–96, 95n

allostasis, 115–16

AlphaFold, 48–51

alpha-synuclein, 207, 209–10

Alzheimer, Alois, 2, 3, 207

Alzheimer’s disease, 1–5; alternative causes of, 4; effective treatment seeming close, 240; lacking highly effective treatments, 4, 7; localizing the mutation for, 69; memory impairment in, 1, 6; molecular neuroscience framework and, 14, 19; new thinking about the brain and, 18–19; nonlinear and dynamic interactions in, 211; rare mutations for, 2–3, 4–5, 239; similarity to Parkinson’s disease, 207, 209; sleep quality and, 235; unknown cause of, 47

Ambien (zolpidem), 31

amblyopia, 215–16

amphetamines, 179; Adderall, 98

amygdala, 157n

amyloid-beta, 3, 14, 19, 207

amyloid-clearing drugs, 3–4

amyloid hypothesis, 3–4, 14, 18–19

amyotrophic lateral sclerosis (ALS), 35, 159, 164, 222

analogy, 86, 87

Anderson, Philip Warren, 149–50

anesthesia, 160–62, 163–64

animal models, 12

Antabuse (disulfiram), 43

anterior insular cortex: in Capgras syndrome, 106, 107–8; happiness fluctuations and, 133

antidepressant drugs: antipsychotic as refinement of, 40; created in tuberculosis research, 8, 43; denied at Chestnut Lodge, 60; effective in some individuals, 125–26; electroconvulsive therapy if failure of, 43–45; neurotransmitter reuptake and, 66; neurotransmitters and, 97; as refinements of other drugs, 38; slow effects of, 126

antipsychotic drugs: atypical or second generation, 40–41; blocking dopamine D2 receptors, 66, 97, 103, 107; in Capgras syndrome, 107; effective in many patients, 61; not from typical bench to bedside, 39–42; typical, 40

anxiety, 5, 9, 121

Aplysia, 156

apoptosis, in T cell leukemia, 201–4, 202–3

APP gene mutation, 3, 4–5, 14

Aristotle, 63, 89

arousal system, 212, 213–14

artificial intelligence (AI), 10, 20, 47–51; breakthroughs in, 238; computer metaphor of the brain and, 89, 112–13; helping to bridge brain and mind, 241; understanding and, 219. See also large language models (LLMs); machine learning

artificial neural networks, 94–96, 96; attractor dynamics of memory in, 157–58; breakthroughs in AI and, 238; deep, 95, 96; knife edge of criticality and, 233; recurrent, 163

attention, 98–102; at Marr’s what and how levels, 102; at Marr’s why and what levels, 99, 100; maximizing benefit and, 124; noise reduction and, 100–102

attention deficit hyperactivity disorder (ADHD): gap in explanation of, 91–92, 98; minimizing distractions and, 175; overview of, 98; Ritalin for, 9, 37–38, 92, 98, 99, 100

attractor basins, 119–21, 120; tipping points and, 187–88, 188

attractor dynamics of memory, 157–58

attractor landscapes, 119–21, 120

attractors: as line in recurrent neural network, 194–95; types of, 143, 144

autism: brain as complex adaptive system and, 136; as neurodevelopmental disorder, 119

autism spectrum disorders, 235–36

basal ganglia: deep brain stimulation of, 206, 208–9; dopamine-releasing neurons in, 66, 206–7

Batten disease, 46

Beck Depression Inventory, 165

bedside, 31

behavioral interventions, 10, 217–18, 241. See also cognitive behavioral therapy (CBT)

Belsomra (suvorexant), 31–34, 33

Benabid, Alim-Louis, 208–9

bench, 30

bench to bedside narrative: brain drugs created via, 42–43; brain drugs not created via, 37–43; brexanolone as one success in, 7–8; frustrating in brain research, 6–11; in insomnia treatment, 31–34, 33; interventions lagging discoveries in, 10; in neuroelectronic therapy, 35–37; not leading to new treatments, 29–30; not the history of current treatments, 20, 30; sometimes happening, 30–37; working reciprocally, 52–53; world’s influence on brain and, 10

benzene, 85–86

bipolar depression, 125

bipolar disorder, lumateperone for, 41

Bleuler, Eugen, 57–58, 70

blood pressure, 15–16; allostasis and, 115; fixed point of, 115, 121; homeostasis and, 114–15

bottom-up approach, 24–25, 150; to anesthetics, 161–62; in epistemic iteration, 158

Box, George, 54–55, 226

Brahe, Tycho, 89

brain: as coin with two sides, 232–36; different concepts of, 55; early ideas about, 63–64; mechanisms to keep it functioning, 145; modeling at the edge of chaos, 144; somehow giving rise to mental function, 82; steps leading to control of, 146–47; treating the mind or brain, 25–26; type of thing it is, 223–25, 230, 240. See also brain as a computer; brain as complex adaptive system

brain activity: anesthetic depth and, 160–61; in animal models, 107–8; avalanches of, 234; cascades of, 234; in coma patients, 160; consciousness and, 160–61, 162–64; critical boundary and, 163, 234; problem with measures of, 78–80; regions in the brain and, 71–73; technology for recording of, 36, 72–73, 237

brain areas, 71–73; distinct from understanding, 112; large-scale networks of, 73; technology for mapping of, 36, 72–73

brain as a computer, 20, 55; artificial neural networks and, 94–96, 96; as extension of domino chain, 113, 223; learning and, 229; mathematical models and, 97; meaning three different things, 93–94; as a metaphor, 89, 90, 94, 97; with mind produced from software, 91; as a model, 93–94; reality and, 94, 96–97; “things” thinking and, 229; as what level of explanation, 93, 112–13

brain as complex adaptive system, 20, 134–37, 139, 190–91, 227, 231, 236, 237; causality and, 172–73; different brain functions and, 192–93; unsuccessful treatments and, 197–98

brain-computer interfaces, 35–37; aiding stroke recovery, 215

brain disorders or dysfunction: bottleneck to treatments of, 46–47; causes not exclusively genetic, 77; chaos and, 144–45; complex combinations of genes in, 69, 76; costs of, 5; feedforward and feedback interactions in, 117, 227; fragility and, 135, 224–25, 230; hundreds of genes in, 76, 77; impediments to new therapies for, 238–40; individual variability and, 236–37; lacking knowledge of causes, 46–47, 51; questioning whether mental disorders are, 108–10; shifting to more healthy state, 197–98; sleep disruptions and, 234–35; social, economic, and environmental factors in, 10, 13; subtypes of, 74–76; trying to control a complex system and, 145. See also mental disorders

brain drugs: first-in-class vs. follow-ons, 42, 42n; gene expression and, 14; mostly workarounds and refinements, 9, 37–43; new drugs introduced per year, 7, 8, 42; now requiring safety testing, 39n; pharmaceutical companies ending development of, 6–7, 16, 30, 103, 223; some coming from bench to bedside, 42–43

BrainGate, 36–37

BRAIN Initiative, 10

brain networks, large-scale, 73

brain research: curiosity-driven or “basic,” 18; global resources devoted to, 10; going through period of transition, 231–32; needed to create new treatments, 221; new ethos of, 249; new paradigm in 1990s, 81; not effectively moving forward, 52–53; optimism about breakthroughs in, 238; papers published per year, 7, 8, 245; parallels with temperature research, 158; piling up data, 17–18; revolutionary technologies in, 10; stages of, 146–47; successful treatments based on, 222–23; two ways to move forward, 82–83. See also bench to bedside narrative; Grand Plan for brain research; molecular neuroscience framework

brain stimulation therapies, and convergent cross-mapping, 185–86

breast cancer: harmful gene variants in, 69, 200; trastuzumab in HER2 overexpression, 200

Brenner, Sydney, 68

brexanolone, 7–8

brickyard, chaos in, 17–18, 83, 167–68, 237

Broca, Paul, 71–72

Broca’s area, 72, 174

building things: as benchmark for success, 219; understanding and, 111–12, 219

buprenorphine, 181

butterfly effect, 142, 197

canalization, 121

cancer drugs: combating drug resistance, 16–17, 204–5; targeting cell division, 200; targeting genetic variants, 200–201; using model reduction, 201–4, 202–3

Cannon, Walter, 114, 232

Capgras, Joseph, 104, 107

Capgras syndrome, 104–8; how level of brain regions in, 106–7; personal familiarity and familiarity belief in, 105–6, 107, 108; summarized in terms of levels, 106–7

carbidopa, 208

Cartesian theater, 193, 194

causal dependence, 175–76, 175n

causality: brain as complex adaptive system and, 172–73; complex systems and, 146, 183; different meanings of, 173–75; feedback and, 146, 224; modeling interactions in, 230; prediction and, 172; understanding and, 172

causal loops, circular, 116–17, 173

causal production, 174–76

causal variables, and Takens’s theorem, 183–86

causation versus correlation, 146, 173–74, 175n, 185, 190

causes of disorders: levels of explanation and, 108–10; missing knowledge of, 46–47, 51; often measured one at a time, 168

cell death (apoptosis), in T cell leukemia, 201–4, 202–3

Central Dogma, 67

Chang, Hasok, 151, 155, 168, 171

chaos in the brickyard, 17–18, 83, 167–68, 237

chaotic attractor, 143, 144

chaotic systems, 142–45, 144

Chestnut Lodge, 60–61

Chichilnisky, E. J., 219–21

chlorpromazine (Thorazine), 39–40, 41–42, 58–59, 61

chronic pain, 5, 29, 217

Church, Alonzo, 96

clinical trials, 10, 12, 31; failed for many disorders, 223; risk and cost of, 239; selecting a compound for, 34

clozapine (Clozaril), 40–41, 42

cocaine, 179

codeine, 43, 178

cognitive behavioral therapy (CBT), 26–27; for insomnia, 31; mood and, 134

collective behavior, 150

coma, 159–60; knife edge of chaos and, 163, 232

community mental health centers, 62

complex adaptive systems: with adaptation leading to tolerance, 198; computations of, 122–23; definitions of, 116, 116n; difficult to control, 136–37; fragility of, 118–19, 122, 123, 135, 230; mood as part of, 134; as only way to progress, 211–12. See also brain as complex adaptive system; complex systems

complex systems: addiction and, 180–81; causality and, 146; criticisms of studies of, 191–94; interactions among parts of, 116, 150, 231; mathematical models of, 119–20, 122; measuring emergent properties of, 151; Parkinson’s disease and, 210–12, 211; predicting sudden changes in, 187–90, 188; weather forecasting and, 140–42. See also complex adaptive systems; controlling complex systems; emergent properties

computations: by cognitive modules, 94; of complex adaptive systems, 122–23; at what level of description, 93

connectomics, 10, 237

consciousness: coma and, 159–60; measurement of, 160–64, 233

controlling complex systems, 197–98; curse of complexity and, 214; difficulty of, 136–37, 140, 145, 147; even if not chaotic, 198; shifting brain from disease to health, 221, 230–31; stages of research and, 146

convergent cross-mapping, 185–86, 190

Copernican insights, 133–34, 233

Copernicus, Nicolaus, 89, 90

core affect plane, two-dimensional, 127–28, 128

Corlett, Phil, 107

Corning, James, 213

covert attention, 99, 100

COVID-19 pandemic, and opioid addiction, 182–83

Crick, Francis, 67–68

CRISPR, 10, 239

criticality, 162–64, 232–33. See also knife edge of chaos

critical slowing down, 187–88, 187n, 188; seizure forecasting and, 189–90

curse of complexity, 200, 214

cyanobacteria, predicting colony collapse, 187–88

cystic fibrosis, 74, 76, 77

Dale, Henry, 65

decisions, neural network study of, 193–95, 232

deep brain stimulation (DBS), 206, 208–9

default mode network, 73

dementia. See Alzheimer’s disease

dementia praecox, 57

Dennett, Daniel, 193

depressed mood, 82

depression: artificial intelligence and, 51; compared to understanding of temperature, 241; different forms of, 125; drug-resistant, 212–14; electroconvulsive therapy for, 43–45; fMRI in, 79; lacking good theory of, 126; lifetime incidence of major episodes, 125; major depression, 125; measurements of, 153, 164–68; mood and, 126, 127, 132–34, 224; not curable, 5; predicting episodes of, 190; rTMS for, 45–46; stress and, 122; stuck in attractor state, 121; Styron’s experience of, 124–25; treatments stimulating brain plasticity, 132; unexpected changes and, 132; vagus nerve stimulation for, 212–14. See also antidepressant drugs

Descartes, René, 64

description: vs. explanation, 92; measurement and, 146; three levels of, 92–93, 93n

development, 119–21; leading brain to get stuck, 121; mental disorders and, 13; therapies to reopen, 215–16. See also neurodevelopmental disorders

developmental landscape, 119–21, 120

“disorder,” ix

disulfiram (Antabuse), 43

DNA: noncoding, 70; protein synthesis and, 48–49, 67–68. See also genome

DNA methylation, 70, 71

domino chains, 13–15, 14; causality and, 174, 176; computer model of brain and, 113; in defunct theory of depression, 126; evolving beyond ethos of, 18–19, 20; in genetic network controlling cell death, 202–3, 203–4; Grand Plan for brain research and, 223–24; problems of, 15–17, 82–83; tractable problems and, 226–27. See also molecular neuroscience framework

domino chains, historical background, 63–74, 80; brain activity and areas in, 71–74; early beliefs about the brain, 63–64; genes in, 67–71; molecules in, 64–67

donepezil, 216

dopamine: depleted in Parkinson’s disease, 29, 40, 66, 206–7; opioid addiction and, 172–73, 179; reward prediction and, 132

dopamine receptor blockers, 40, 41

Dostoevsky, Fyodor, 189

drug resistance, 16–17

drugs. See brain drugs

DSM: psychiatric diagnoses in, 170–71; substance use disorders in, 179n

“dysfunction,” ix

Eccles, John, 65–66

“Ecstasy” (MDMA), 216

EEG: brain-computer interface using, 215; measuring brain activity, 160–61; seizure forecasting and, 189–90

electroconvulsive therapy, 43–46; nonconsensual, 44, 58

emergence: in addictive state, 116–17; compared to reductionism, 24; with feedforward and feedback loops, 83; of mental function from brain, 109; in predator/prey interaction, 116, 117

emergent properties: attractor dynamics as, 195; brain’s functions as, 232, 233; causal loops and, 116; of complex systems, 150–51, 158, 162, 164, 167–68, 195; consciousness as, 162, 164; defined, 116; interactions between parts and, 167–68, 224, 238; mathematical models and, 122; phases of water as, 154, 155; of systems with feedback, 226; temperature and memory as, 158

emotions: adaptation to change and, 123, 229–30; as affective states, 123–24; on core affect plane, 127–28, 128

empirical dynamical modeling, 185

endorphins, 178

engram, 155–56

engram experiments, 156–57, 157n, 169

environmental factors, 10, 13–14, 14; in addiction, 180, 181; genes influenced by, 69–70, 77; in neurodevelopmental disorders, 71

epigenetic landscape, 120

epigenetics, 70, 71

epigenomics, 237

epilepsy: incurable, 5; mapping brain regions and, 36, 72; vagus nerve stimulation for, 212–14. See also seizures

epistemic iteration, 151; for measures of depression, 167; for measuring consciousness, 161–64; memory research and, 155–58; overview of, 151; pluralism in, 170, 171; promise and pitfalls of, 168–71; stuck in a local minimum, 169–71, 170; temperature and, 151, 152–55, 158; the way science works, 248

escitalopram (Lexapro), 38

explanations. See levels of explanation; Marr levels

Fahrenheit, Daniel Gabriel, 153

feedback: adaptation to change and, 224–25; brain as complex system with, 20, 136, 139, 227; causality and, 146, 173; cognitive behavioral therapy and, 26; in homeostasis and allostasis, 115–16

feedforward and feedback interactions, 82–83; balancing brain at criticality, 233; brain disorders and, 117, 227; in Capgras syndrome, 107; in predator/prey oscillations, 116

fentanyl, 172, 181

Feynman, Richard, 48, 111

fight or flight response, 122, 198, 224–25

first-in-class drugs, 38, 41n, 42

fishery forecasts, 183–85

fixed point attractor, 143, 144

fluoxetine (Prozac), 45, 66

fMRI of brain activity, 36; in Capgras syndrome, 107; in happiness fluctuations, 133; localization by, 73; problems with, 78–80; in schizophrenia, 61, 73

follow-on drugs, 38, 42

fragile X syndrome, 46, 135–36

fragility: brain dysfunction and, 135, 224–25; of complex adaptive systems, 118–19, 122, 123, 135

Franklin, Rosalind, 67

Fregoli syndrome, 104

Freud, Sigmund, 57, 58, 59

GABA inhibitory neurotransmitter, 31

GABA neurotransmitter receptors, 161–62

Gage, Phineas, 72

Galileo, 152

Gall, Franz, 71

Galvani, Luigi, 64

Gaucher’s disease, 210

gene editing, 239

gene expression: environmental influences on, 13, 14; psychotherapy and, 13–14; regulation of, 70

gene mutations: believed to cause disorders, 12; in subtypes of disorders, 74–76, 75

genes: cross-species homologies of, 69; total number of, 68

genetic code, 12, 61–62, 67–68

genetic imprinting, 70

genome: Human Genome Project, 68, 69; noncoding regions of, 68, 76. See also DNA

genome sequencing, 68, 69

genome-wide association studies (GWAS), 10, 69; of schizophrenia, 71

genomics, 237

Glasgow Coma Scale, 160

glia cells, 44

Goate, Alison, 3

Golgi, Camillo, 64

Gordon, Joshua, 7

Grand Plan for brain research, 11–15, 17; assuming the type of thing the brain is, 223–25, 231–32; broken domino plan not panning out, 248; different tools and principles in, 195; new, 223, 230–36, 248–49; not working out well, 82; rethinking of, 137, 139–40, 145, 147; succinct statement of new plan, 231, 248–49; thinking explicitly about, 245–46

Greenberg, Joanne, 60

Halley, Edmond, 152–53

Hamilton Rating Scale for Depression (HRSD), 165, 166

happiness, 123, 126; on core affect plane, 127–28, 128, 129; equation for, 129–31, 129n, 133; model to predict fluctuations in, 129–31, 130

Hardy, John, 2–5, 18–19

Hassabis, Demis, 50

Hawking, Stephen, 35

Hebb, Donald, 156

Hebbian learning, 156

hedonic principle, 124, 133

Heraclitus, 228

Hesse, Mary, 87

high-throughput screening, 33–34

hippocampus: atrophy under stress, 122; memory and, 155–57; optogenetic manipulation of, 156–57

Hippocrates, 63–64

homeostasis, 114–16, 225, 232

Hopfield, John, 157–58

how level: descriptions of, 93; interacting causes and, 176; technology linking Marr’s what with, 101

Human Genome Project, 68, 69

Huntington’s disease: incurable, 5; known cause of, 46, 77, 238–39; lacking highly effective treatments, 7, 222, 239; level of explanation of, 109, 176

Hyman, Steve, 236–37

hypothalamus: anesthesia and, 162; endorphins created in, 178

identical twin: of individual with bipolar disorder, 70; of individual with schizophrenia, 77, 119, 120

imaginative rationality, 86

imipramine (Presamine), 40

information processing: changing the brain, 229; emotions and, 124; by neurons poised at criticality, 233; what level and, 112

information-processing machine, 91

Insel, Thomas, 9, 13

insomnia, 31–34, 33; drugs binding to receptors and, 97; levels of explanation of, 109; stress and, 122

insulin release, in allostasis, 115

interactionist neuroscience, 108

internal signal, 100, 100–101

International Space Station (ISS), 198–200

iproniazid (Marsilid), 8, 43

IpsiHand, 215

istradefylline, 208

ivacaftor, 74

Jaspers, Karl, 243

Jennings, Carol, 1–3, 4–5, 14, 69, 222, 239

Johnson, Mark, 86

Jumper, John, 50

Kandel, Eric, 12–13, 17, 81, 82, 156

Kekulé, August, 85–86

Kendler, Kenneth, 241, 243

Kennedy, John F., 62

Kepler, Johannes, 89

ketamine, 216

knife edge of chaos, 144–45, 162–64, 163n; balance point of brain at, 232–33, 235; coma and, 163, 232; seizures and, 163, 213, 232; sleep and, 234–35; vagus nerve stimulation and, 214

Kuru, 70

Lakatos, Imre, 81

Lakoff, George, 86

LaMDA large language model, 112–13

Lansbury, Peter, 210–11

large language models (LLMs), 50–51; helping to bridge brain and mind, 241; making language rethought entirely, 112–13. See also artificial intelligence (AI)

large-scale brain networks, 73

large-scale genetic screens, 236–37

large-scale neural recording, 10

Lashley, Karl, 155–56

learning: brain as a computer and, 229; in brain’s figuring things out, 225; connections between neurons and, 95; by deep artificial neural networks, 95; fragile X syndrome and, 135–36; gene expression and, 13–14; Hebbian, 156; mood and, 132, 229; plasticity of the brain and, 214–15; psychedelic therapy and, 217; reductionist approach to, 24; reward-based, 131–32; stuck in attractor state, 121–22

lecanemab, 3–4

Lee, Virginia, 206

lemborexant (Dayvigo), 34

lesion network mapping, 106

leukemia, T cell large granular lymphocyte, 201–4, 202–3

levels of explanation, 92–93, 93n; causes of disorders and, 108–10. See also Marr levels

levodopa, 42–43, 66, 207–8

Lewy, Fritz, 207

Lewy bodies, 207

Lexapro (escitalopram), 38

lobotomy, 58, 62

locked-in syndrome, 35, 159, 160, 163–64, 233

logistic map, 142–43, 144, 226

Lorenz, Edward, 142

Lou Gehrig’s disease, 35

LSD, 163, 163n, 216

Luhrmann, Tanya, 25

lumateperone (Caplyta), 41, 41n

machine learning, 10, 48; BrainGate use of, 37; generative models with, 50–51; overview of, 48; protein structures and, 49–51; understanding decisions and, 193–95; understanding therapies and, 219; without understanding, 50. See also artificial intelligence (AI)

major depression, 125

Marr, David, 92

Marr levels, 92–93, 93n, 110–12; attention at why and what levels, 99, 100; brain researchers’ heuristic use of, 111; expediting new treatments and, 235; limitations of explanation by, 110; philosophers’ more rigorous versions of, 110–11; technology linking of, 101; understanding and, 112. See also how level; levels of explanation; what level; why level

Marsh, Richard, 159, 160

Marsilid (iproniazid), 8, 43

mathematical models, 19, 88; fitting with parameters, 169–71, 170

May, Robert, 143, 184n

McCulloch, Warren, 95, 96

MDMA (“Ecstasy”), 216

measurement: of brain functions, 146; of depression, 153, 164–68; of dysfunctional versus healthy brain, 149; epistemic iteration and, 151; new Grand Plan and, 231; standardization of, 153, 154, 158, 166; of temperature, 151, 152–53, 154, 155

Meduna, Ladislas, 44

melatonin, 33

memory: epistemic iteration and, 155–58; investigation of, 6

mental disorders: affecting 970 million people worldwide, 5; debating whether organic or functional, 13, 58–59, 60, 81; drugs not based on understanding, 8–9; drugs working for only some individuals, 7, 8; interventions targeting the mind, 26–27; lacking an understanding of the mind, 17; often resistant to treatments, 5; overmedicalized, 242; path forward for, 240–44; questioning whether they are brain disorders, 108–10; refinements of old drugs, 9; social interventions for, 62; stuck in maladaptive attractor, 121; treating the brain or the mind, 25–27; unknown causes of, 47. See also behavioral interventions; brain disorders or dysfunction; mind; specific disorders

meprobamate (Miltown), 9, 43

metaphors, 86–87; going awry, 87–89

Meteorology Project, 142

methadone, 181

methylphenidate (Ritalin), 9, 37–38, 92, 98, 99, 100, 102

migraine: new generation of drugs for, 10; treatment decisions for, 26

Milner, Brenda, 156

Miltown (meprobamate), 9, 43

mind: brain as computer and, 91; gap between brain and, 17, 20, 82; shifting to healthy state, 231; treating the brain or mind, 25–26; two different ways to know about, 243–44. See also mental disorders

misidentification syndromes, 104

Mitchell, Kevin, 77–78

model reduction, 199–200; cell death in leukemia and, 201–4, 202; of International Space Station, 198–200; in neuroscience, 200

models: of a brain function or disorder, 23–25; different for each thing, 195–96, 198; with domino-chain backbone, 226; falsifiable, 88, 93; to guide therapeutic development, 198; of interacting causes, 176; machine learning and, 48–51; in new Grand Plan, 231; as simplification, 11, 54–55; understanding and, 48, 50, 54; useful, 54–55, 226. See also mathematical models

molecular medicine, 12–13, 75–76; problems with, 76–78, 80

molecular neuroscience framework, 13–17, 14; bottom-up approach in, 150; compared to complex adaptive system, 227; complexity at each stage of, 77–78; elaborations of, 20; evolving beyond, 18–19; factors leading to shift toward, 61–63; field shifting away from, 56; historical role of, 81–82; principles of, 13–14; reductionism at heart of, 24; schizophrenia and, 81; shift from functional (mental) causes, 81; shift toward systems with feedback, 122–23; three problems with, 15–17. See also domino chains

Moliason, Henry (“H.M.”), 156

mood: adaptability and, 131–32, 133–34; as affect, 123; basic features of, 126–27; core affect plane and, 127–28; depression and, 126, 127, 132–34; emotion and, 127; formalizing mathematically, 134, 241; fragile in negative feedback cycle, 131; learning and, 132, 229; not understood, 126; open questions about, 133–34

morphine, 43, 178

motor cortex, BrainGate implantation in, 37

mouse brain, 12

multiple sclerosis, 5, 47, 135, 224, 231

mu-opioid receptors, 172, 179

naltrexone, 181

narcolepsy, 32, 33, 34, 135

National Advisory Mental Health Council, 61

National Alliance on Mental Illness (NAMI), 61

National Institute of Mental Health (NIMH), 7, 9, 13, 61–62, 236

neo-Freudians, 59

nerve cells. See neurons

networks, landscape models of, 119–21

neural networks: BrainGate use of, 37; recurrent, 144–45, 163, 194–95, 232. See also artificial neural networks

neurodevelopmental disorders: adaptations during development and, 224; attractor basins and, 121; autism as, 119; brain as complex adaptive system and, 136; schizophrenia as, 71, 73–74, 80–81, 119, 121

neuroelectronic therapies, 35–37, 43–46

neuroimmune disorders, 135, 136, 224, 231

neurons: crossed by soups or sparks, 64–66; early ideas about, 64; excitation and inhibition by, 232–33; at how level of explanation, 93; learning and, 95; modeled by recurrent networks, 144–45; in molecular neuroscience framework, 63, 77; recording from large numbers of, 101

neuropeptides, 31–32

neurotransmitters, 31–32, 65–66; reuptake at synapses, 66; schizophrenia and, 66–67

Newton, Isaac, 89–90

Niv, Yael, 218

nociceptors, 177, 178

nonlinear dynamical systems, 19

norepinephrine: in arousal system, 212; vagus nerve stimulation and, 213

Occam’s razor, 226–27

-omics revolution, 237

opioid dependence and addiction, 176–83; deaths from overdose in, 180, 182, 222; models to evaluate outcomes, 181, 182, 183. See also addiction

opioid epidemic, 172–73; COVID-19 pandemic and, 182–83; HEALing communities study in, 181–83

opioid receptors, 172–73, 178–79, 181

opioids: adverse effects of, 5; for chronic pain, 5; mechanism of action, 178; reward system and, 179; tolerance to, 178–79

opioid withdrawal, 177, 179

opium, 38, 43, 178

Oppenheimer, Robert, 86

optimization metaheuristics, 87–88

optogenetic tools, 10, 220; in memory experiments, 156–57

orexin, 31–34, 33, 135

organomics, 237

oscillation, 143, 144, 173, 226–27

ovarian cancer, 76–77

oxycodone, 38, 43

OxyContin, 38, 178

pain: chronic, 5, 29, 217; sensation of, 177

pain drugs: derived from opium, 5, 38, 43; to stay ahead of pain, 177. See also opioids

Parkinson, James, 205

Parkinson’s disease, 205–12; activator of GCase for, 211, 211; deep brain stimulation for, 206, 208–9; dopamine depletion in, 29, 40, 66, 206–7; GBA1 mutations and, 205, 209–12, 211; levodopa for, 42–43, 66, 207–8; modeling complexity of, 210–12, 211; progression not slowed by treatments, 5, 208, 209; similarity to Alzheimer’s disease, 207, 209; symptoms of, 205; unknown cause of, 47

paroxetine (Paxil), 38

Pauli, Wolfgang, 88

Paxil (paroxetine), 38

Penfield, Wilder, 36, 72

Perspective Neuroscience, 244–46

pharmaceutical companies: cancer drug paused by, 204–5; ending brain drug development, 6–7, 16, 30, 103, 223; financial interests in treating mental problems, 243; multilevel understanding needed by, 103; opioid epidemic and, 173; overmedicalizing problems in living, 242

Phelan-McDermid syndrome, 235

phenylketonuria, 70

Philo of Byzantium, 152

phrenology, 71

Pitts, Walter, 95, 96

plasticity of the brain: attractor landscapes and, 121; opioid addiction and, 172–73, 179; therapies based on, 214–18

pluralism, 170, 171, 245

Poggio, Tomaso, 110

Popper, Karl, 65

positional cloning, 69

postpartum depression, 125; new drug for, 7–8

posttraumatic stress disorder (PTSD): psychedelics for, 217; in shellshocked veterans, 62

precision medicine, 74–76, 75, 78, 79–80; genetic variants in cancer and, 200; mental dysfunction and, 236

predator/prey interaction, 116, 117, 173, 226–27

prediction: causality and, 172; complex systems and, 146; model-based approaches to, 186; Takens’s theorem and, 183–86; of tipping points, 186–90, 188

prefrontal cortex: attention and, 102; in depression, 79; lobotomy and, 58; rTMS targeted at, 45; in schizophrenia, 73; switching between tasks and, 193–94, 232

pregnancy, as a process, 228–29

premotor cortex, BrainGate activated in, 36, 37

Presamine (imipramine), 40

prion disease Kuru, 70

process-based thinking, 227–30

protein folding problem, 49–51

protein structures, and drug development, 50n

proteomics, 237

Prozac (fluoxetine), 45, 66

psilocybin, 216–17

psychedelics, 216–17

psychiatric disorders. See mental disorders

psychiatry: problems with DSM and, 170–71; shift from dualistic framework, 81

psychodynamic therapy, 13, 59; fall of, 61, 63; for schizophrenia, 60–61

psychosis, 5. See also schizophrenia

psychotherapy: gene expression and, 13–14; precision of, 218

psychotic episodes, 39, 61, 103

Ptolemy, 89, 90

Ramón y Cajal, Santiago, 64

rational drug design, 16, 139

Reagan administration, 62

recurrent loops: in mental disorders, 121–22. See also feedforward and feedback interactions

recurrent neural networks, 144–45, 163, 194–95, 232

reductionism, 24–25, 81, 191

repetitive transcranial magnetic stimulation (rTMS), 45–46, 79

retina, understanding to re-create, 220

retrosplenial cortex, in Capgras syndrome, 106, 107–8

Richardson, Lewis Fry, 141

Rieder, Travis, 177, 179, 222

Ritalin (methylphenidate), 9, 37–38, 92, 98, 99, 100, 102

RNA: noncoding DNA and, 70; in protein synthesis, 67–68, 77

Rosenblueth, Arturo, 54

sadness, 123, 126

Santa Fe Institute, 191

schizophrenia: brain as complex adaptive system and, 136; brain regions implicated in, 73; changing perspectives about, 56–63; clozapine for, 40–41; developmental landscape and, 119, 120; evolution and, 57; global uniformity of, 57; horrific treatments for, 58; incurable, 5; late onset of symptoms in, 73–74; linked to hundreds of genes, 70–71; lumateperone for, 41; as neurodevelopmental disorder, 71, 73–74, 80–81, 119, 121; neurotransmitter pathways and, 66–67; not only linked to genes, 77; prevalence of, 57; psychosocial treatment for, 63

schizophrenogenic mother, 59, 70

second-entrant drugs, 38

seizures: auras of, 189; knife edge of chaos and, 163, 213, 232, 233; prediction of, 188–90. See also epilepsy

selective serotonin reuptake inhibitors (SSRIs), 45, 66, 126

Semon, Richard, 155

seribantumab, 204–5

serotonin, and depression, 126

serotonin receptor blockers, 41, 126

sertraline (Zoloft), 38

sleep: need for, 233–35; opioid tolerance and, 179

social support, 10

Society for Neuroscience Meeting, 247–48

Sokal, Alan, 87

Southard, E. E., 58

spinal motor atrophy, 46

Stecher, Benjamin, 205–6, 209, 222

strange attractor, 143, 144

stress, short-term or chronic, 122

Strevens, Michael, 246

stroke: drug treatment for, 46; locked-in syndrome following, 159; recovery from, 214–15

Styron, William, 124–25, 133, 222

Sugihara, George, 184–85

suicide: caused by depression, 125; drug addiction and, 180; in US every 10 minutes, 222

sulfapyridine, 38

suvorexant (Belsomra), 31–34, 33

Takens, Floris, 183

Takens’s theorem, 183–86, 190

tardive dyskinesia, 40, 59

tau protein, 4

temperature: brain’s regulation of, 115; compared to understanding depression, 241; development of theories of, 153–55; history of measurement and, 151, 152–53, 154, 155, 168

termite mounds, 192

thebaine, 178

theories, 93

thermoscope, 152

“things” way of thinking, 230–31

Thorazine (chlorpromazine), 39–40, 41–42, 58–59, 61

tipping points: prediction of, 188

tipping points, prediction of, 186–90

tolerance: to opioids, 178–79; to treatment in complex systems, 198

top-down approach, 24–25; to consciousness, 162–64; in epistemic iteration, 158, 161

transcranial magnetic stimulation: consciousness and, 163–64; repetitive (rTMS), 45–46, 79

trastuzumab, 200

trauma: brain disorders and, 10; development and, 55

traumatic life experiences, 57, 58, 59; psychodynamic therapy and, 60, 63

Turing, Alan, 96

twins. See identical twin

understanding: building models and, 146; by building things, 111–12, 219; causality and, 172; measurement and, 149, 151, 154; multilevel, 113

vagus nerve stimulation, 212–14

venglustat, 210–11, 211

visual system: amblyopia and, 215–16; artificial neural networks and, 95–96; artificial retina project, 220–21; causality and, 174; levels of explanation of, 92–93; noise decorrelation in, 102; Ritalin and, 102

von Neumann, John, 141

Waddington, Conrad, 119–20, 120, 121

Wang, Esmé Weijun, 103–4

Watson, James, 67

weather control, 141–42

weather forecasting, 140–42

Wernicke, Carl, 72

Wernicke’s area, 72

what level: in complex adaptive systems, 123; descriptions of, 93; drug development and, 98; as insufficient for understanding, 113; too little emphasis on, 112

why level: attention at, 99, 100; Capgras delusion at, 105; descriptions of, 93

Wiener, Norbert, 54

Zoloft (sertraline), 38

zolpidem (Ambien), 31

Zworykin, Vladimir, 141