Thursday, May 28, 2015

The Heritability of Everything

I am getting asked what I think of the recent paper by Polderman et al in Nature Genetics, linked here (firewall).  The answer is that I am ambivalent about it, and rather than try to squeeze my thoughts into a Facebook post, I thought I might expand a little here.

First, the upside.  I would not have believed it was possible to conduct this meta-analysis.  In fact I literally did not believe it when I read the abstract.  The authors of this paper conducted a meta-analysis of every twin study that has been conducted over the last fifty years, including almost 18,000 traits from 2,700 studies.  Not twin studies of ability, or personality, or behavior, but twin studies of everything.  It represents an inconceivable amount of work.  And the meta-analysis itself is beautifully executed.  The graphs are striking, the numerical analysis is sophisticated.  And to top it all off, the data are available in the form of web-based analysis tool. (Question-- is there a library of pdf's to go with the analysis tool?  It will be much more useful to future investigators if it is possible to scan the original reports for additional data that were not included in the main analysis.  I imagine there would be copyright problems.)

Nevertheless, the question has to be asked-- was it worth the effort?  Twenty-five years ago, I named the proposition that everything is heritable the "First Law of Behavior Genetics."  When I said that I didn't feel as though my conclusion was awaiting affirmation via meta-analysis, because it was obvious.  No serious person, then or now, questions whether in general rMZ > rDZ, not even the critics.  (I'll get to what they do question in a second.)  So the rock bottom finding of the meta-analysis, that on average 49% (The data did the authors a favor by not coming out to exactly 50%) of the variability in the traits is attributable to A, just isn't news.  It is a massive, overwhelming confirmation of what we already knew.  (For the record, the other two laws of behavior genetics were confirmed as well.)

Moreover, taken as a number, a unit of analysis, heritability coefficients are funny things to aggregate on such a massive level.  What exactly are we supposed to make of the fact that twins studies in the ophthalmology domain produced the highest heritabilities?  Should eye doctors, as opposed to say dermatologists, be rushing to the genetics lab because their trait turns out to be more heritable?  No.  Whatever else a heritability may be, it is not an index of how "genetic" something is.  It is not, for example, a useful indicator of how successful gene-finding efforts are likely to be.  If nothing else, differences in reliability of measurement are confounded every heritability tallied here.  My point is this-- although it's nice to know that on average everything is 50% heritable, it's hard to attach much meaning to the number itself, or especially to deviations from that number, to the fact that eye conditions have heritabilities around .7 and attitudes around .3.  Having two arms has a heritability of 0.

And as I say, no one really disputes the fact that everything is heritable.  Critics of BG don't say, "It seems to me that if someone tallied the data carefully it would turn out the fraternal twins are just as similar as identical twins."  They say, for example, that the increased similarity of MZs is in fact environmental, the result of violations of the EEA.  Or they say that genetic and environmental contributions to differences can only be separated statistically, not biologically.  Or they say a million other things, none of which I necessarily endorse, but none of which are really refuted by this analysis.  

The hard question about twin studies is why MZ twins are more similar than DZ twins.  I take the softest view possible:  that in a very general way genetic similarity is associated with phenotypic similarity, for everything, and that this can occur without there being specific genes that are linked in specific ways to specific outcomes.  Whatever the unimaginably complex pathways there may be to becoming a fan of beach volleyball, more genetically similar people are going to be more similar in their fandom.  This is true both across established levels of genetic relatedness (twin and family studies) and in the low-level relatedness among everyone else (GCTA).  It says nothing about the reality of volleyball-fandom as a phenotype, nothing about the likelihood of finding volleyball genes.  It is the general causal background noise of genetic influence.  I have always said that the three laws aren't really laws, they are null hypotheses.  One way to characterize this study is that it is a massive confirmation that the null hypothesis is true.

The bulk of the analyses in the paper is concerned with an issue related to this argument, the fit of the additive model.  This is too complicated a question to get into very deeply here.  To me, for anything meriting the word "complex", on a biological level the additive model is obviously wrong.  Does anyone really think that when the day comes when we understand why some people are more extroverted than others the explanation is going to be that there are thousands of individual genes with biologically specifiable independent additive effects?  But anyway, the authors argue that most twin studies are not inconsistent with the hypothesis of additivity, in the quantitative genetic sense, basically that rMZ = 2rDZ.  But as the authors explain, the classical twin model actually has very little to say about additivity.  Basically, you can always draw a straight line through two data points.  

I'm not perfectly clear about what they do here.  I think that for each comparison they report, they test the null hypothesis that rMZ = 2rDZ.  For 69% of the effects the null hypothesis cannot be rejected.  All this means is that in general the second law of BG holds up (C=0), and that the additive twin model is not violated because rMZ > 2rDZ.  All problems with statistical power (which matters on the level of the individual comparison) are counting in their favor.  So a study with 20 twin pairs in which rMZ = .7 and rDZ = .2 would count as "consistent" with additivity, because the null hypothesis would not be rejected.  But it seems to me it is a big inference to reach any conclusions about the additivity of developmental biology on this basis.  Just by the way, authors, I would be interested to know the percentage of comparisons for which rMZ > 2rDZ, broken down by domain.  If that is in there somewhere I missed it.

So that is what I think.  The study represents an impressive, massive effort; I don't know that it produced anything we didn't know before.  It represents a new style of behavior genetics that I have come to think of as "maximilist".  The authors of this study are not hereditarian, in fact the article hardly takes a theoretical position at all on basic nature-nurture issues.  Instead they amass enormous amounts of evidence in support of a hypothesis that isn't in itself very surprising.  Everything is heritable.  GCTA showing that intelligence is heritable and polygenic is maximilist.  GCTA is a formidable effort in quantitative genetics, but we already knew that intelligence was heritable and polygenic.  The GWAS of educational attainment showing that with half a million people you can find a SNP significant at 10-8 that accounts for a quarter of a percent of the variance is maximilist.  The PGC is maximilist.  Maximilist BG takes the hard issues in BG-- that everything is heritable, but it is hard to get from heritability to meaningful understanding of process, that there doesn't seem to be genes of substantial effect for anything behavioral-- and instead of grappling with them, tries to bury them in an avalanche of data.  

Many of my colleagues, I'm sure, do not agree with what I have written here.  Good.  One of my goals for the next few years is to try to get the field talking about the important questions we face at the interface of data collection and theory.  Unfortunately, that involves disagreeing in public, although I hope we can do so collegially.  So I challenge those of you who disagree-- say so in a comment here, or on the BGAnet Facebook page, or better yet start a blog.  Too many theoretical discussions of BG are old arguments between us and our old opponents-- the EEA people-- and those arguments are in my opinion mostly played out.  It will be much more interesting for us to talk to each other.


Ulrich Schimmack said...


I am a big fan of open discussion of controversial questions.
So here are some quick responses to your blog.

1. Do the authors also report shared environment effects?

Even if we would agree that h^2 = .49 is boring and a natural law of behavioral genetics, the amount of shared environment effects is much less certain and varies across traits. I typically use smoking as an example of a trait with good evidence of shared environment effects.

2. Of course, simple models are false, but the abstract truth that everything is a gene x enviroment interaction is as empty as saying behavior is a function of personality and situation. True, but no prediction of behavior. I think it makes more sense to look first for main effects of single genetic markers before we look for more complex gene x enviroment interactions. Caspi made a splash with the 2003 Science paper, but did it increase our understanding of depression?

3. Height is 90% heritable and the effect can be seen on every playground. Even if gene expression is more complex, the root cause of bell-curved variation in height is probably the "additive" effect of many genes or is there an alternative theory that can explain phenotypic variation in height?

nooffensebut said...

"there doesn't seem to be genes of substantial effect for anything behavioral"

Proponents of this belief, such as yourself, keep talking as if they had won, when, in fact, they have lost. Large meta-analyses have been published for MAOA and aggression.

MAOA, Childhood Maltreatment, and Antisocial Behavior: Meta-analysis of a Gene-Environment Interaction
Candidate Genes for Aggression and Antisocial Behavior: A Meta-analysis of Association Studies of the 5HTTLPR and MAOA-uVNTR

More cases of Brunner syndrome have suddenly presented themselves after a 20-year absence. Research on MAOA and aggression has greatly slowed because, of course, they do not further our understanding. Deniers still talk and write, but that is true for any number of answered questions.

Rosalind Arden said...

Eric, I really agree with you that there is a lot to be discussed in BG. I also agree with you that the Polderman et al article is a blinder - an astonishing, almost marvellous, piece of work. It's like a conductor bringing all the sections together in a tremendous crescendo, before the silence and the deliberation.

You say, in your blog "Does anyone really think that when the day comes when we understand why some people are more extroverted than others the explanation is going to be that there are thousands of individual genes with biologically specifiable independent additive effects? " Don't you think that a decent description of the world around us will need an explanation that delivers exactly the quantity of combinatorial complexity offered by the image you suggest? It seems to me that you have captured it well.

Your point about public discussion is a good one. It is frustrating at scientific meetings when the Big Bears (you know who you are) shift around in their seats looking tense and cross uttering cryptic comments to neighbours, rather than having a fuller discussion, and explaining for the earlier career scholars, what the points of disagreement and contention are. That contributes to the tribalism in science; it's not useful. More open, well-tempered argument please. Glad that your blog promotes that!