The GWAS hoax....or was it a hoax? Is it a hoax?

A long time ago, in 2000, in Nature Genetics, Joe Terwilliger and I critiqued the idea then being pushed by the powers-that-be, that the genomewide mapping of complex diseases was going to be straightforward, because of the 'theory' (that is, rationale) then being proposed that common variants caused common disease.  At one point, the idea was that only about 50,000 markers would be needed to map any such trait in any global populations.  I and collaborators can claim that in several papers in prominent journals, in a 1992 Cambridge Press book, Genetic Variation and Human Disease, and many times on this blog we have pointed out numerous reasons, based on what we know about evolution, why this was going to be a largely empty promise.  It has been inconvenient for this message to be heard, much less heeded, for reasons we've also discussed in many blog posts.

Before we get into that, it's important to note that unlike me, Joe has moved on to other things, like helping Dennis Rodman's diplomatic efforts in North Korea (here, Joe's shaking hands as he arrives in his most recent trip).  Well, I'm more boring by far, so I guess I'll carry on with my message for today.....




There's now a new paper, coining a new catch-word (omnigenic), to proclaim the major finding that complex traits are genetically complex.  The paper seems solid and clearly worthy of note.  The authors examine the chromosomal distribution of sites that seem to affect a trait, in various ways including chromosomal conformation.  They argue, convincingly, that mapping shows that complex traits are affected by sites strewn across the genome, and they provide a discussion of the pattern and findings.

The authors claim an 'expanded' view of complex traits, and as far as that goes it is justified in detail. What they are adding to the current picture is the idea that mapped traits are affected by 'core' genes but that other regions spread across the genome also contribute. In my view the idea of core genes is largely either obvious (as a toy example, the levels of insulin will relate to the insulin gene) or the concept will be shown to be unclear.  I say this because one can probably always retroactively identify mapped locations and proclaim 'core' elements, but why should any genome region that affects a trait be considered 'non-core'?

In any case, that would be just a semantic point if it were not predictably the phrase that launched a thousand grant applications.  I think neither the basic claim of conceptual novelty, nor the breathless exploitive treatment of it by the news media, are warranted: we've known these basic facts about genomic complexity for a long time, even if the new analysis provides other ways to find or characterize the multiplicity of contributing genome regions.  This assumes that mapping markers are close enough to functionally relevant sites that the latter can be found, and that the unmappable fraction of the heritability isn't leading to over-interpretation of what is 'mapped' (reached significance) or that what isn't won't change the picture.

However, I think the first thing we really need to do is understand the futility of thinking of complex traits as genetic in the 'precision genomic medicine' sense, and the last thing we need is yet another slogan by which hands can remain clasped around billions of dollars for Big Data resting on false promises.  Yet even the new paper itself ends with the ritual ploy, the assertion of the essential need for more information--this time, on gene regulatory networks.  I think it's already safe to assure any reader that these, too, will prove to be as obvious and as elusively ephemeral as genome wide association studies (GWAS) have been.

So was GWAS a hoax on the public?
No!  We've had a theory of complex (quantitative) traits since the early 1900s.  Other authors argued similarly, but RA Fisher's famous 1918 paper is the typical landmark paper.  His theory was, simply put, that infinitely many genome sites contribute to quantitative (what we now call polygenic) traits.  The general model has jibed with the age-old experience of breeders who have used empirical strategies to improve crop, or pets species.  Since association mapping (GWAS) became practicable, they have used mapping-related genotypes to help select animals for breeding; but genomic causation is so complex and changeable that they've recognized even this will have to be regularly updated.

But when genomewide mapping of complex traits was first really done (a prime example being BRCA genes and breast cancer) it seemed that apparently complex traits might, after all, have mappable genetic causes. BRCA1 was found by linkage mapping in multiply affected families (an important point!), in which a strong-effect allele was segregating.  The use of association mapping  was a tool of convenience: it used random samples (like cases vs controls) because one could hardly get sufficient multiply affected families for every trait one wanted to study.  GWAS rested on the assumption that genetic variants were identical by descent from common ancestral mutations, so that a current-day sample captured the latest descendants of an implied deep family: quite a conceptual coup based on the ability to identify association marker alleles across the genome identical by descent from the un-studied shared remote ancestors.

Until it was tried, we really didn't know how tractable such mapping of complex traits might be. Perhaps heritability estimates based on quantitative statistical models was hiding what really could be enumerable, replicable causes, in which case mapping could lead us to functionally relevant genes. It was certainly worth a try!

But it was quickly clear that this was in important ways a fool's errand.  Yes, some good things were to be found here and there, but the hoped-for miracle findings generally weren't there to be found. This, however, was a success not a failure!  It showed us what the genomic causal landscape looked like, in real data rather than just Fisher's theoretical imagination.  It was real science.  It was in the public interest.

But that was then.  It taught us its lessons, in clear terms (of which the new paper provides some detailed aspects).  But it long ago reached the point of diminishing returns.  In that sense, it's time to move on.

So, then, is GWAS a hoax?
Here, the answer must now be 'yes'!  Once the lesson is learned, bluntly speaking, continuing on is more a matter of keeping the funds flowing than profound new insights.  Anyone paying attention should by now know very well what the GWAS etc. lessons have been: complex traits are not genetic in the usual sense of being due to tractable, replicable genetic causation.  Omnigenic traits, the new catchword, will prove the same.

There may not literally be infinitely many contributing sites as in the original statistical models, be they core or peripheral, but infinitely many isn't so far off.  Hundreds or thousands of sites, and accounting for only a fraction of the heritability means essentially infinitely many contributors, for any practical purposes.  This is particularly so since the set is not a closed one:  new mutations are always arising and current variants dying away, and along with somatic mutation, the number of contributing sites is open ended, and not enumerable within or among samples.

The problem is actually worse.  All these data are retrospective statistical fits to samples of past outcomes (e.g., sampled individuals' blood pressures, or cases' vs controls' genotypes).  Past experience is not an automatic prediction of future risk.  Future mutations are not predicable, not even in principle.  Future environments and lifestyles, including major climatic dislocations, wars, epidemics and the like are not predictable, not even in principle.  Future somatic mutations are not predictable, not even in principle.

GWAS almost uniformly have found (1) different mapping results in different samples or populations, (2) only a fraction of heritability is accounted for by tens, hundreds, or even thousands of genome locations and (3) even relatively replicable 'major' contributors, themselves usually (though not always) small in their absolute effect, have widely varying risk effects among samples.

These facts are all entirely expectable based on evolutionary considerations, and they have long been known, both in principle, indirectly, and from detailed mapping of complex traits.  There are other well-known reasons why, based on evolutionary considerations, among other things, this kind of picture should be expected.  They involve the blatantly obvious redundancy in genetic causation, which is the result of the origin of genes by duplication and the highly complex pathways to our traits, among other things.  We've written about them here in the past.  So, given what we now know, more of this kind of Big Data is a hoax, and as such, a drain on public resources and, perhaps worse, on the public trust in science.

What 'omnigenic' might really mean is interesting.  It could mean that we're pressing up ever more intensely against the log-jam of understanding based on an enumerative gestalt about genetics.  Ever more detail, always promising that if we just enumerate and catalog just a bit (in this case, the authors say we need to study gene regulatory networks) more we'll understand.  But that is a failure to ask the right question: why and how could every trait be affected by every part of the genome?  Until someone starts looking at the deeper mysteries we've been identifying, we won't have the transormative insight that seems to be called for, in my view.

To use Kuhn's term, this really is normal science pressing up against a conceptual barrier, in my view. The authors work the details, but there's scant hint they recognize we need something more than more of the same.  What is called for, I think is young people who haven't already been propagandized about the current way of thinking, the current grantsmanship path to careers.

Perhaps more importantly, I think the situation is at present an especially cruel hoax, because there are real health problems, and real, tragic, truly genetic diseases that a major shift in public funding could enable real science to address.