About as bad as behavior genetics reporting gets

A story in the New York Times a couple of days ago, linked here.  The story was prompted by a paper in Evolutiona and Human Behavior by Brendan Zietsch et al, linked here. The title says it all:  "Infidelity Lurks in Your Genes."  I should say at the outset that the article itself is fine.  I'm not sure I buy the argument that the heritabilities they estimate are higher than others in meaningful ways, and there are obvious reasons to be skeptical about the small sample candidtate gene results, but in the paper the authors are perfectly up front and thoughtful about the limitations of their conclusions.
and in fact, the OXTR and sexuality work has most of what you could want out of this kind of study, especially meaningful animal models.  This post is not about the science.

But the Times article gets just about everything wrong.  Of course, there is the ridiculous overstatement of the psychological meaning of heritability.  OK, infidelity is heritable, but so is everything else, so if infidelity lurks in our genes so does everything, which I suppose is true.  What they mean is, likelihood of infidelity not independent of genetic endowment.  The important lesson of complex behavior genetics is about the human condition-- we all create our selves and regulate our behavior in the constant presence of genetic endowment-- and not about anything particular about individual behaviors.  There is no other aspect of sexual behavior to contrast with infidelity that does not lurk in our genes and is therefore under our perfect pscychological control.  The world doesn't work that way.

Then there is the confounding of the twin evidence and the candidate gene work.  See the paragraph that begins "He found that 9.8%..." It starts out talking about candidate genes, and then switches to saying that 40% of the variance can be attributed to genes.  The average NYT reader would have absolutely no idea that it isn't OXTR and vasospressin that acount for 40% (in fact they account for a couple of percent, and that is almost certainly an over-estimate)

Then there is the  evolutionnary  part, which is like a parody..  Men cheat because there is an evolutionary advantage to reproducing with many women.  But women cheat too.  (I like the old jingle:  Hoggamus higgamus, men are polygamous.  Higgamus hoggamus, so are women.)  Why do women cheat?  Well, because they enjoy it!  But don’t worry, that has a biological explanation too, they enjoy it because dopamine.  Once again, I know there are many interesting evolutionary things to say about fidelity and infidelity, and reward systems or whatever.  But it should be a science reporters job not to reduce them to nonsense.  It does the field no good.

The article closes with a story of an acquaintance of the reporter who has cheated on her partner repeatedly and compulsively over the years.  (By the way, this seems like a lot of information to reveal.  A bisexual woman, apparently married to a man, who is an acquaintance of the writer.  The guy is a psychiatrist.  He should be careful.) Recently the relationship has been bad, so the writer can write it off to psychological causes.  But she also cheated early on in the relationship, which the writer takes as evidence that her cheating is “innate”.

People, like I say, are partially self-determining organisms who are born into the world with evolved impulses, some of them universal and some of them differing among individuals.  Managing the relation between the evolved impulses that we share with voles and our complex self-regulating psychology (which also evolved, of course, but only exists in primitive forms in voles) is the essential human activity; understanding it is the ultimate goal of psychology.  Nature didn’t do us the favor of giving us some desires that are innate and others that are strictly psychological, although it is always tempting to think that way because the alternative is so daunting.  From the point of view of humans-as-biological-entities these questions are the basis of evolutionary psychology and behavior genetics; from the subjective point of view of living people they are (forgive me) psychoanalytic.

I have gathered recently that there is a movement in meteorology to change the way weather forecasting is discussed in the popular press.  The excellent Capital Weather Gang in the Washington Post no longer scream headlines like, “Blizzard to Bury DC!”.  Instead they talk in terms of probabilities and confidence intervals, discuss how their forecasts might go wrong, weight the different possible outcomes, consider the limitations of existing weather models.  (Those of you in the mid-Atlantic might also want to check out the WxRisk feed on Facebook.) It’s less than thrilling than Blizzard! But ultimately more interesting, and leaves readers with a sense of what meteorologists actually do.  We need a similar kind of popular press reform in BG.

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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.