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Policy Brief: A $2 Billion Proposal for Research in Neuropsychiatric Disease

29 March 2010. Just as SRF has finished posting our look at the state of schizophrenia genetics (see SRF related news story), eight prominent geneticists and neurobiologists (including three Nobel laureates) have added a timely postscript by laying out their vision of how best to move forward with research in schizophrenia and other neuropsychiatric diseases. Their proposal, set forth in a policy piece in the March 25 issue of Science, calls for a $2 billion international effort over the next 10 years, with half to go to sequencing 100,000 complete personal genomes and half to be used to integrate genomic findings with neurobiology.

No one would argue that a significant influx of research funds earmarked for neuropsychiatric disease is warranted. As lead author Huda Akil, University of Michigan, Ann Arbor, and her colleagues point out, the top three diseases (schizophrenia, depression, and autism) add up to the leading cause of disability in North America and Europe, with the cost in lost earnings estimated at $200 billion per year in the U.S. alone. Yet there have been no major advances in prevention or treatment in 20 years or more.

The lack of results stems partly from the complexity of the problem. Schizophrenia and other neuropsychiatric disorders result from disruption of neural circuits, Akil and colleagues write, but because the development and function of circuits is so complicated, there are likely many routes to disease. That leads Akil and colleagues to call for a turn away from approaches like genomewide association. “Starting from a diagnosis and searching broadly for genetic causes that are commonly shared across all affected individuals is not likely to succeed....” they write. Instead, they espouse an approach of whole-genome sequencing that can detect private mutations and take into account the genetic and neurobiological heterogeneity of these disorders. The National Institutes of Mental Health is already moving in that direction, funding some whole-genome sequencing for psychiatric disorders, but the vision of Akil and coauthors would dramatically escalate current efforts. (For more discussion on the pros and cons of this shift in focus, see SRF Genetic series, Part 4.)

The second billion-dollar project, aimed at the integration of genetics with the latest techniques for studying circuit function in humans and in experimental animal models, seems less clear-cut than the genomic goal. An important component appears to be the production of animal models based on yet-to-be-discovered human genes.

The article gives the views of eight individuals. Now we would like to hear what the rest of you think. What is there to like about this proposal? What possible pitfalls do you as researchers and SRF readers see?—Pat McCaffrey.

Akil H, Brenner S, Kandel E, Kendler KS, King MC, Scolnick E, Watson JD, Zoghbi HY. The future of psychiatric research: genomes and neural circuits. Science. 2010 Mar 26;327(5973):1580-1. Abstract

Comments on News and Primary Papers

Primary Papers: Medicine. The future of psychiatric research: genomes and neural circuits.

Comment by:  David J. Porteous, SRF Advisor
Submitted 29 March 2010
Posted 29 March 2010

This Perspective is important, not least because of the collective scientific authority and policy influence of the coauthors. But it will also be controversial and there will be dissenters who will need winning over or convincing.

When the Human Genome Project was first mooted, there were passionate dissenting voices, arguing against such a costly investment, but in hindsight only the most blinkered would deny the all-pervasive and positive impact on biomedical science. Be in no doubt, however, that we have just reached the end of the beginning in terms of genome capacity and impact. Next-generation sequencing will change everything, again. Already, the power of complete genome sequencing in related members of an affected family has been demonstrated for genetic heterogenous conditions, such as Charcot-Marie-Tooth neuropathy (one proband sequenced completely and affected and unaffected relatives tested for all possible causal variants; see Lupski et al., 2010), and Miller syndrome/primary ciliary dyskinesia (one family of two parents and two affected offspring; see Roach et al., 2010). The stage is set for this to impact major psychiatric conditions, but it would be wise to learn from these early examples and choose carefully the samples that are fed into the machine. Family-based samples must be top of the list, as these will allow the wheat to be sorted from the chaff of genome variation. We know about the chaff of GWAS studies; this is an opportunity to be more incisive and insightful.

Overlooked in the Perspective is that we can not only compare genomes with base pair resolution on a large scale and at low cost, but use the same technology also to generate quantitative transcriptional profiles, including splice variants, by sequencing RNA (as cDNA) from cells (including single cells), tissue (micro-dissected, fresh or postmortem), throughout development and across species. Couple both genomic and transcriptomic outputs to statistical, bioinformatics, and structure/function analyses and we will have a new biology of the brain.

So for me, the argument for major new investment in psychiatric genomics is incontestable. Can the same be said for neural circuitry? Here the gamble and the payback are less certain. Without question, the new imaging and labeling tools are advancing at an impressive pace and merit further investment, but there is no sign yet that they can be democratized in the powerful manner of genomics. Advanced in vivo proteomic techniques (Krüger et al., 2008) and methods for neuronal cell-type-specific translational profiling (Heiman et al., 2008) should not be overlooked, but for me, perhaps the most obvious omission from the mix is the potential of induced pluripotent stem cell technology (Park et al., 2008) to bypass the limited access to patient-specific neuronal cells.


Lupski JR, Reid JG, Gonzaga-Jauregui C, Rio Deiros D, Chen DC, Nazareth L, Bainbridge M, Dinh H, Jing C, Wheeler DA, McGuire AL, Zhang F, Stankiewicz P, Halperin JJ, Yang C, Gehman C, Guo D, Irikat RK, Tom W, Fantin NJ, Muzny DM, Gibbs RA. Whole-Genome Sequencing in a Patient with Charcot-Marie-Tooth Neuropathy. N Engl J Med . 2010 Mar 10. Abstract

Roach JC, Glusman G, Smit AF, Huff CD, Hubley R, Shannon PT, Rowen L, Pant KP, Goodman N, Bamshad M, Shendure J, Drmanac R, Jorde LB, Hood L, Galas DJ. Analysis of Genetic Inheritance in a Family Quartet by Whole-Genome Sequencing. Science . 2010 Mar 10. Abstract

Krüger M, Moser M, Ussar S, Thievessen I, Luber CA, Forner F, Schmidt S, Zanivan S, Fässler R, Mann M. SILAC mouse for quantitative proteomics uncovers kindlin-3 as an essential factor for red blood cell function. Cell . 2008 Jul 25 ; 134(2):353-64. Abstract

Heiman M, Schaefer A, Gong S, Peterson JD, Day M, Ramsey KE, Suárez-Farińas M, Schwarz C, Stephan DA, Surmeier DJ, Greengard P, Heintz N. A translational profiling approach for the molecular characterization of CNS cell types. Cell . 2008 Nov 14 ; 135(4):738-48. Abstract

Park IH, Arora N, Huo H, Maherali N, Ahfeldt T, Shimamura A, Lensch MW, Cowan C, Hochedlinger K, Daley GQ. Disease-specific induced pluripotent stem cells. Cell . 2008 Sep 5 ; 134(5):877-86. Abstract

View all comments by David J. PorteousComment by:  Michael Owen, SRF Advisor
Submitted 30 March 2010
Posted 30 March 2010

By and large, I agree that this is how the big picture looks.

Regarding the genetics: I disagree that we now know that “private” mutations are responsible for disease in many cases. This is conjecture, since no pathogenic point mutations have yet been identified. Moreover, a number of the rare pathogenic variants that have been identified to date (CNVs) are not private, and I see no reason to suppose that the situation will be different for point mutations. However, I very much agree that the focus is going to have to be on very large samples to get full traction on the genetics. Some people think that as we move to sequencing over the next few years, the focus should shift away from very large samples to studies of families. However, given the findings from linkage, where single families with cast iron linkages are extremely rare, and the huge statistical challenges to identifying association with individually rare variants, the samples required will be just as large as those that will be required to identify common risk variants by GWAS, i.e., tens of thousands. So the focus now needs to be on amassing the sample base for these large studies. As we wait for the cost of sequencing to come down over the next few years, it will be possible to subject these samples to GWAS with the current SNP chips (the costs of these are falling); this will identify more common risk variants. And also bear in mind that as we get data from the 1000 Genomes Project and other sequencing studies, it will be increasingly possible to impute a greater proportion of the rare variants from the SNP-chip data. This is not to say that studies of smaller, well-characterized samples and families will not be useful; by delivering greater homogeneity (phenotypic and genetic, respectively), they might well be fruitful, but even if robust findings can be obtained in this way, these studies will only reveal a very small proportion of the picture. There will still be a need to test the generality of the findings in larger, more representative cohorts.

I also agree that the role of computational biology is likely to be critical in interpreting genetic findings. This will be required to distinguish true risk mutations from the many others that will be neutral with regard to the phenotype under study, and to interpret the data in individual cases where several rare mutations and many common variants are likely to be playing a role.

Regarding the circuit analysis: There seems to be a bit more hand waving here. However, I do think that we need systematic efforts to define the relationships between brain phenotypes and psychopathology. One point not mentioned in the article is that this will need to be directed against an understanding of psychopathology at the level of symptoms and syndromes and not diagnoses. Most of the studies to date are small scale, and use a variety of different measures, and they tend to focus on brain phenotypes in very simplistic ways. We need to know which of these relate to which aspects of the rich psychopathology seen in patients and which are endpoints in themselves (i.e., they index the same risk factors as the psychiatric phenotypes but do not mediate risk). Defining causal pathways in humans is difficult and requires sophisticated statistical approaches and large samples, but it is possible. However, there will also be a need to complement the human work on neural circuits with studies of experimental animals where mechanistic insights are easier to glean. Here what is needed is work aimed at establishing correspondence across species and being able to move programs of work from animal to humans and vice versa.

Finally, I agree that the integration of genetics with neuroscience is going to be key to understanding psychiatric illness. A genetic risk variant that is robustly associated with a disorder allows studies of neural circuits to be firmly anchored to the etiology of the illness, though I stress again the need to be cautious about inferring that specific brain phenotypes mediate disease risk.

View all comments by Michael Owen