The word jaundiced is not one that I ever imagined encountering in peer review, at least after completing my internship in internal medicine. But several years ago, there it appeared, offered by a referee who admitted reading our manuscript on working-memory impairment in schizophrenia with a “jaundiced eye.” Of course, the reviewer was not referring to a bilirubin-induced yellow haze but rather to a sense of malaise, and perhaps indifference, around yet another attempt to disentangle the biology underlying this common and debilitating aspect of schizophrenia. Indeed, as of the moment I write this essay, a PubMed search using the terms “working memory” and “schizophrenia” yields >3500 articles. Notably, this number drops to zero when one adds “cure” as an additional search term.
If one takes a broader view of psychiatry research over the last several decades, especially from the standpoint of clinician investigators, a justifiable melancholy seems to have set in around the relative lack of progress in treatment and prevention. Hype-generating discoveries that seemed like breakthrough moments have fizzled, due to lack of replication (e.g., Border et al. )1 and failures of late-stage clinical trials.2 Pendulums swung by polarized elements (e.g., impact of rare genetic variants vs. common genetic variants, DSM-5 vs. RDoC) echo decades of division, whiplash, and fatigue in psychiatry.3 Some of the most pressing needs of our most seriously ill patients remain unmet while we look with envy to fields like oncology, where, for example, recent immunotherapies have revolutionized treatment of even widely metastatic cancers.
And yet from another standpoint, opportunities for meaningful translational research in psychiatry have never been stronger. “Big data” approaches now enable unprecedented, high-resolution views of pathophysiology on both micro- and macroscopic levels. New single-cell RNA-sequencing methods canvass cell type–specific gene expression patterns in animal models and postmortem human brain tissue in exquisite detail. The National Institutes of Health–funded Adolescent Brain Cognitive Development Study is prospectively following >11,800 children in the United States through late adolescence with clinical and cognitive testing, brain imaging, and genetics. Meanwhile, the NIH BRAIN Initiative promises transformative new approaches to studying the living brain. With a historic influx of medical students into the field—including a 71% increase in U.S. senior medical students matching into psychiatry from 2012 to 20194—we will have an eager work force to translate these advances into improved clinical care. In short, something about this period feels different, as though we are on the verge of generational change in the practice of psychiatry that echoes the psychopharmacology revolution of decades ago.
At the Harvard Review of Psychiatry, we are fortunate to have a bird’s-eye view of this evolving narrative. Our mission has always been to transmit cutting-edge science and expert perspectives from across the full spectrum of psychiatry to our readers. With a new format, Disruptive Innovation, making its debut in these pages, we now hope to take a more active role in catalyzing translation of these advances into improved outcomes for our patients. We envision Disruptive Innovation as a forum for forward-thinking clinicians, investigators, policy makers, and thought leaders to challenge orthodoxy in thoughtful and well-reasoned ways, and propose new ideas, approaches, and methods to tackle intractable problems in psychiatry. This first entry, while atypical for the series in its self-awareness, is also meant to model our new format. (We encourage prospective authors to refer to our updated Instructions for Authors page for additional guidance.)
The specific innovation proposed herein is not an assay, therapeutic area, or policy, but rather an ethos. And, in fairness, it is not terribly innovative, as it recalls the thinking and practice of a different era—one when there was a palpable sense of excitement about the future of psychiatry, less hindered by the weight of stagnation that we have faced in recent years. In a tribute to his mentor Julius Axelrod, Sol Snyder describes
an infectious exhilaration in the discovery process . . . When a critical experiment was completed, he was often so excited that, standing in front of the liquid scintillation counter, which records radioactivity levels, he almost jumped up and down using body English to accelerate or decelerate the accumulation of radioactive counts, depending on what result he was seeking.5
But enthusiasm alone did not enable this period of discovery. Ross Baldessarini6 has emphasized the role of serendipity—that is, “\chance observations with immediate clinical implications”—in the discovery of lithium, tricyclic antidepressants, clozapine, and other agents that continue to serve as the scaffold of psychopharmacology; he also notes that “serendipity has not yet been replaced by modern neurobiology or advances in industrial or academic chemistry and neuropharmacology.” Rather, Baldessarini argues that contemporary psychopharmacology research has a penchant “to redouble efforts to make the best use of what we have while hoping for the next therapeutic breakthrough.”
There are several threads, both explicit and implicit, in this assessment that seem important to prospects for innovation not just in psychopharmacology but in psychiatry at large. The usefulness of serendipity does not simply rest on the importance of chance observations; it also requires an openness to recognize and follow up on these new leads. In turn, for such exploratory work to run its course, those who evaluate its merit in peer review must be open to new avenues, including those that are orthogonal (or even opposed) to canonical thinking, as long as they are pursued with scientific rigor. By contrast, the prevailing model in pharma—where iterative tweaks to existing compounds are valued over risker and unconventional work—may keep the coffers open but yield asymptotic benefits. The same critique has frequently been applied to grant reviews at NIH, which tend to favor more comfortable ideas through groupthink,7 and to disproportionately reward senior scientists.8 Finally, it is worth recalling that many of the early pioneers of psychopharmacology (e.g., Lehmann, Schou, Snyder) were psychiatrists, and as such were intensely familiar with areas of unmet clinical need.
In this light, it follows that transformative progress in care of our patients will rely not only on technical breakthroughs but also on reinstating a scientific culture that values novelty, creativity, and active mindfulness of our patients. Text Box 1, which reflects varied input from essays, journal clubs, career development sessions, peer review experiences, and healthy debates that colleagues and I have shared over the years, offers one accounting of core scientific values that may promote innovation in psychiatry if implemented as part of good research practice.
Importantly, there is room for dialectics within these principles. One can be both optimistic and critical toward new ideas, without falling into skepticism. Indeed, unless promising new ideas are given some room to grow, it is often impossible to differentiate them from those headed down blind alleys. Agnostic and hypothesis-driven science can coexist; a favorite example is how initial genome-wide association study results in schizophrenia were thought to doom the dopamine hypothesis, until a DRD2 hit emerged after the sample size became sufficient.9 Basic neuroscience is essential, but so is relevance to clinical outcomes. Central to each of these ideals, though, is the importance of collaboration, and the recognition that no single investigator, method, or school of thought is sufficient to achieve measurable gains for our patients.
While certain of these qualities may seem familiar if not intuitive, others run counter to well-entrenched patterns. Ours is a profession where seniority is built over the course of decades; an often-mentioned statistic is that the median age of investigators attaining their first independent R01 grant is now approaching 45,8 and even so, scientists holding their first R01 are still considered “Early Experienced Investigators” by NIH. The reasons for this pattern are complex, and while a comprehensive discussion lies beyond the scope of this article, two opposing factors deserve mention. On one hand, developing the complex skills set necessary for biomedical research indisputably takes time and experience, and the stakes are especially high for clinical studies that entail risk. On the other, there is clear evidence of bias against younger investigators in NIH study sections: during the 10-year period ending in 2014, NIH funding for grantees over 55 increased by seven-fold compared to younger investigators. Looking back over the last 20 years, a net $3 billion in R01 grants has changed hands from investigators younger than 56 to older grantees.8
Consider, though, that Barack Obama went from being an attorney and community organizer to president of the United States in twelve years, and that Mark Zuckerberg rose from college student to billionaire entrepreneur in four. While their rapid ascents are, of course, exceptional, there are many familiar models outside of medicine where success in complex and high-stakes environments can be achieved in relative youth; one suspects that these individuals’ plans would be labeled “too ambitious” in NIH study sections. Some of the best new ideas may come from junior and mid-career investigators, but their impact can be suppressed by the formulaic and deliberate ladder of career progression in our field.
A related obstacle surfaces in how novel ideas are evaluated in peer review. The merits and pitfalls of our peer review system have been the subject of considerable debate. However, one frequently used design, single-blind review, can pose obstacles to innovation in the setting of an entrenched status quo. Many journals—including this one—use a peer review system that is either double-blind or, increasingly, open. This method can protect both reviewers and authors by introducing a level power dynamic and, in the case of double-blind review, minimizing bias. Most journals, though, and most mainstream grant competitions (e.g., NIH, Brain and Behavior Research Foundation) deploy a single-blind process, which introduces an asymmetric power structure that preferentially protects reviewers. This system can amplify ingroup-outgroup effects, which by definition work against novelty. A recent review of >21,000 articles published in the computer science field demonstrated clearly reduced representation of articles written by relatively new, but still experienced, authors within the context of single-blind versus double-blind review.10 Alternatively, a totally open and transparent peer review process, while potentially uncomfortable for reviewers (especially junior ones), also holds them to a higher standard of accountability. My own experience, both as an author and as a referee in open peer review settings, has been one of productive dialogue and relationship building, and has helped me to mature as both a scientist and reviewer.
In peer review, as in all aspects of our work as scientists, there will always be well-intentioned disagreement about best practices and methods. The principles described here are not meant to steer these debates in any one direction but rather to help them become healthier and more constructive, especially in regard to the window of opportunity that is rapidly opening for our field. At the Harvard Review of Psychiatry, we will do our part to cultivate innovation by staying true to these ideals. In particular, we hope that our new Disruptive Innovation series can serve as a platform for moving the conversation forward in ways that generate both momentum for our field and renewed hope for our patients.
Declaration of interest
The author reports no conflicts of interest. The author alone is responsible for the content and writing of the article.
The author thanks Dr. Dost Öngür for his feedback on the manuscript.
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