Towards a Genomic Psychiatry: Recommendations of the Genomics Workgroup of the NAMHC
In the early 1990s, I was a graduate student and the genetics revolution was moving at full speed. The gene for Huntington’s disease had just been cloned; creating and studying genetic mutations in mice was becoming commonplace; and, the Human Genome Project was ramping up. Gene discovery for mental disorders in this era was in its infancy and many, if not all, of the early findings could not be replicated. Nonetheless, preparing for the day when genes for all the various psychiatric disorders would be cloned and mice carrying these genes would be widely available, I became a mouse neuroscientist, fully expecting my path to become even clearer over time.
While I have achieved a modicum of success on this path, the way forward has not clarified; instead, it has become murkier. It turns out the genetic landscape of psychiatric disorders is incredibly complex. Instead of specific genes for each of the various psychiatric conditions (a “bipolar gene,” for example), we have strong statistical signals for hundreds of loci (locations) in specific regions of the genome that are associated with the risk of developing bipolar disorder, schizophrenia, autism, depression, ADHD, or other disorders. While a few of these loci are powerful risk factors, most contribute only a tiny bit of risk; the as-yet unidentified gene variants embedded in these loci must therefore operate collectively together with environmental and developmental factors to cause disease.
The complexity of the genetic landscape contributes to a conundrum for those of us who wish to understand the neurobiology of these genetic factors—simply making a mouse with the gene variant won’t really help us understand schizophrenia, because schizophrenia results from a combination of multiple genetic and non-genetic risk factors. We don’t even know how to figure out which factors in what combination, much less study that combination in a mouse.
How then do we make progress given the complexity of the genetic landscape underlying psychiatric disorders? To address this question and provide guidance for priority setting in genomics research, NIMH convened a Genomics Workgroup of the National Advisory Mental Health Council. The workgroup was chaired by Dr. Steve Hyman, director of the Stanley Center for Psychiatric Research at the Broad Institute, and Dr. John Krystal, chair of the Department of Psychiatry at Yale University, and comprised experts in genetics and psychiatry from across the country. They submitted their report to me and the Council on January 25th and, after a spirited discussion, the Council approved the report and its principal recommendations.
In considering the complexity of the genetic landscape, the Genomics Workgroup highlighted three main themes. First, the future of gene discovery lies in unbiased, well-powered studies. Second, translating genetic variants into neurobiological understanding and new treatments will require thoughtful, rigorous, and importantly, novel approaches. And third, common resources based on universal data sharing will help speed the way. Here I will highlight these themes, but I urge those in the field to read the full report and consult the synopsis of recommendations regularly. Applications adhering to these recommendations will be prioritized for funding consideration.
The future of gene discovery
For many years, psychiatric genetics was a morass of unreliable findings. Many argued that NIMH should pull back from funding gene discovery, as study after study failed to replicate. The move to genome-wide association studies (GWAS), which required global-scale collaborations to assemble immense sample sizes (requiring the participation of tens of thousands of willing volunteers), has rewritten this story. We now have many examples of statistically rigorous and fully-replicated genetic links to schizophrenia, autism, depression, and other psychiatric disorders.
GWAS and similar large-scale gene discovery strategies work because of their unbiased approach. Previous attempts to map genes to disorders often used a “candidate gene” approach, in which investigators tested the association of specific genes chosen for their putative biological plausibility with specific disorders, one or a handful of genes at a time, in a relatively small sample of affected subjects and healthy controls. Such studies overestimated the statistical rigor of associations; other investigators would then test these associations in different samples and fail to replicate the findings. GWAS tests the association between a disease and a large number of genetic variants across the entire genome. Because there are many places in the genome to test with GWAS, you need many, many subjects to test them all at once. The only way to find a large enough sample was for investigators to work together. So, with NIMH’s help, that is what psychiatric geneticists began to do, working together in collaborations that are still active today.
Genome-scale gene discovery became the new paradigm in psychiatric genetics. Working together, testing genetic associations in an unbiased manner on large samples has been incredibly successful. The Genomics Workgroup report recognizes the power of this approach and argues convincingly it should inform all future genomics studies. In particular, candidate gene approaches based on biological hypotheses should be a thing of the past. Moreover, existing collaborations need to expand their reach, in particular to include a more diverse set of subjects—most genetic samples currently available primarly comprise individuals of European descent. This need for diversity drives the participation of NIMH in projects like H3-Africa, which seeks to foster genomic and epidemiological research in African scientific institutions. NIMH is supporting, for example, an H3-Africa project to map genes for psychiatric disorders in thousands of people from sub-Saharan Africa.
These larger, more diverse collaborative datasets will allow us to achieve a deeper level of genetic understanding. While we do indeed know hundreds of places in the genome where variation affects risk for psychiatric disorders, we don’t yet know which genes are affected and how. We must now proceed to finer mapping of these risk locations, to identify the actual genes that are underlying the genetic risk. But we can’t just pay attention to genes—the regions of the genome that contain the code for proteins—because the regions of our genetic code that lie between genes play important regulatory roles. Finally, we need also to enrich our genetic datasets with better phenotyping, so we can examine the genetics of psychiatrically relevant behaviors beyond DSM diagnoses, focusing on core deficits (such as cognition, emotion regulation, etc.) that might hew more closely to the underlying biology.
From genetics to neurobiology
Understanding how genetic variation increases the risk for disease from a biological perspective is the key to unlocking novel treatments. It is crucial, then, that we use these gene variants as biological clues, to delineate the biology and pathophysiology of psychiatric disorders. But with so many statistically significant variants to study, NIMH cannot afford to expend resources chasing down links with weaker evidence tying them to disease. Going forward, studies aimed at understanding the neurobiology of genetic risk should focus on those variants which achieve genome-level significance.
For some genetic variants, such as single gene mutations, and duplications or deletions of whole chunks of the genome, the effect on risk is large enough that it makes sense to try to study them in cellular and non-human animal experimental systems. Studying the effects of these variants on the cells and circuits of the brain has the potential to reveal important information about the neurobiology underlying the behaviors that are affected in psychiatric disorders.
For most genetic causes of psychiatric illnesses, however, studying single mutations no longer make sense. In these cases, some unknown combination of multiple genetic variants, interacting with environmental causes and developmental events, leads to increased risk. Just as genome-scale GWAS enabled the discovery of these variants, we need a genome-scale neurobiology to understand them. We need novel methods using diverse cellular systems, such as human iPSCs and organoids, that reflect the complexity of the human genetic background. We need a systematic approach to understanding the effects of risk variants on gene regulation and expression across the brain and in a diverse array of cell types. And we need computational modeling and experimental approaches aimed at forming and testing hypotheses about how these variants might interact to affect brain function and increase risk.
To support such efforts, NIMH, on its own and with its NIH partners in the BRAIN Initiative, is committed to developing new technologies and supporting systematic efforts to enable genome-scale neurobiology. To this end, we support PsychENCODE, a collaborative effort to understand how the genome regulates gene expression throughout the brain in healthy people and individuals with mental disorders, as well as the BRAIN Initiative’s Cell Atlas project, which aims to characterize and map all the various cell types of the brain.
We will continue to support the use of appropriate experimental systems, including model animals, for studying disease mechanisms at the molecular, cellular, and systems levels. However, in keeping with the Genomics Workgroup recommendations, and in line with a growing consensus among animal researchers, we must remember that no non-human organism can recapitulate all the requisite features of a human disease, regardless of how accurately it might recapitulate a risk gene for that disease. Therefore, NIMH will continue to prioritize studies that seek to use experimental systems to test specific biological hypotheses over those that seek to establish or validate models that reproduce symptoms or behaviors affected in psychiatric disorders.
A final set of recommendations in the report pertain to the development of shared resources. To carry out gene discovery and to translate genes into neurobiology and treatments is an ambitious effort that will require NIMH to continue our commitment to and support of the kinds of collaboration that enabled the first GWAS studies. Several steps are needed to facilitate this collaboration. Human studies should be designed from the beginning with data sharing in mind; this will require the appropriate consents. Indeed, wherever possible, institutional review boards should be asked to examine consents from completed studies to determine whether they give sufficient justification to permit the data to be shared with approved researchers. Next, NIMH has been increasingly requiring broad data sharing, moving towards a data sharing plan which permits sharing as soon after data acquisition as is feasible, with suitable processes in place to ensure that the scientists collecting the data are appropriately recognized for their contributions. Where practical, these sharing requirements are also applied to studies in experimental systems, to encourage scientists to mine the complex datasets that will be generated by the genome-scale neurobiological experiments of the future.
We believe that the recommendations of the Genomics Working Group are sound and will maximize our ability to continue on the successful path towards gene discovery in neuropsychiatry. These recommendations also lay the groundwork for using these genetic discoveries to uncover the molecular pathophysiology of these disorders, and to facilitate a genuine understanding of the biological underpinnings of psychiatric disease. Thank you to all who participated in the generation of the report, including the workgroup members, and especially Drs. Hyman and Krystal for their leadership.
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