Wednesday, December 23, 2015

The Tucker-Drob Bates Meta-analysis

Elliot Tucker-Drob and Tim Bates have published a meta-analysis [fire-walled] of the Scarr-Rowe effect, the observation that the heritability of intelligence is lower in impoverished families.

The reaction to the analysis has been a little strange.  I read the meta-analysis as broadly supportive of the existence of the effect, more details on that below. To the extent I have some personal attachment to the finding, which I admit, I felt good about it.

But to my surprise, the reaction on Twitter sounded as though they had disconfirmed the finding.  I think the first tweet I saw was this one....

Boy did he get it wrong, I thought, and (as I end up regretting every time) shot off a reply:

To my surprise, Tim Bates said in fact, they were right....

What was going on?  Had I completely misread the paper?

It turns out that of this had started up in response to a more general blog post by Stuart Ritchie (I hope to find the time to comment on that whole argument), in which he described the effect size as an "outlier".

Upon further twittering, Stuart agreed that "extreme outlier" (by the other poster) was an overstatement, but still... what exactly did Tucker-Drob and Bates show?  The effect size we reported in 2003 was indeed the largest in the meta-analysis, however:

1) It certainly wasn't an "extreme outlier" and other than being the largest wasn't an outlier at all.  It was reasonably close to the high-side of the other estimates.  Plus, TD&B performed a quantitative test of the null hypothesis that all US effect sizes were drawn from the same population, and failed to reject it.

2) Not only was the average effect size non-zero in the US, it remained non-zero if Turkheimer (2003), or even every study I have had anything to do with, was removed from the analysis.

3)  Although the mean effect size was smaller than what we reported, but it was by no means trivial, in a p<.05 even though it's ridiculously tiny kind of way.  The TD&B graph of the effect looks almost identical to what we reported, with a somewhat less dramatic y-axis.  Still lots of variation in heritability across SES.

4) The whole process here, in which (quasi-, we weren't the first) discovery samples turn out to have unrealistically large sample sizes, is a perfectly normal part of science.  One discovers things because they are big; after that, when everyone is looking for the effect, big or small, they shrink.  The winner's curse.  All one can hope as an early adopter of a finding is that it remains (a) significantly non-zero, and (b) substantively non-trivial, and the Scarr-Rowe interaction accomplished this, at least in the US.

5)  The US vs. Europe part is interesting, but there is a perfectly reasonable environmental basis for speculation about why it would happen, which is that there is greater socioeconomic inequality in the US.  Speculation, yes, but perfectly good fodder for future studies.  The conclusion that it doesn't happen in Europe, by the way, is exactly what I have concluded in writing at least three times.

It doesn't seem to me that TD&B leaves much for everyone to be arguing about.  The interaction happens, with moderate ES, in the US but not Europe. Period.  Why exactly it happens is unknown.  I have already confessed to the somewhat unscientific feeling of commitment I have to the effect.  I think those on the other side, with more of a hereditarian bent than me, should be big enough to admit that they are actively rooting against it, because it threatens their global assumption that genes always predominate.  In fact I think the best thing about the TD & B paper is how even-handed it is.

Friday, June 5, 2015

B-B-B-Behavior Genetics and Criminology

So referring again to Callie Burt's post, here, while failing to adhere to my own strictures about being brief.  I see two major issues.

First, whether the BG side of the debate is being defensive in taking issue with bringing an end to "heritability studies," or by characterizing the Burt et al stance as "anti-BG".  Burt insists that she is not anti-BG, but aside from the one strictly theoretical quote I mentioned in the last post, as far as I know there is no evidence of that in any of these articles.  She says it wasn't the point of the articles to get into the positive contributions a genetically informed point of view might make, and OK, but then it isn't such a surprise that people take the articles the wrong way.  Really, the same can be said for the BG side.  Mightn't it be a good idea to pay a little closer attention to the EEA and its consequences, not to mention a million other assumptions that twin studies make?  rGE, random mating, the list goes on and on.  I think if you go back to classic papers in the seventies and eighties by people like Eaves, Martin, Heath, Loehlin, etc, they worried about these things a lot, all the time.  It's just good modeling practice, really.

Both sides of the debate are accusing the other of a scorched earth strategy, and I hope it doesn't make me sound too kum-bye-a to say that finding a way to concede that your opponent might have a point about something is a pretty good way to move forward.  Criminology has ignored the possibility of genetic pathways for years; BG sometimes conducts twin studies without putting a hell of a lot of thought into exactly why we are doing it, what the assumptions are, or what the results mean.

Second is the "heritability studies" question.  Burt claims that the studies she was criticizing were strictly h2-equals studies.  So I read all the studies in the Table.  (By the way, what is it with people whose names begin with B in the BG of criminality?  Barnes, Beaver, Boutwell, Boisvert.  And now Burt! Attn Tim Bates, Tom Bouchard, and Chris Beam).  And, drum roll.... the studies in question are not strictly heritability studies, in fact none of them are, although a couple come close.  They are bivariate twin studies, so let me say a few words about that.

Let's say a sociologist observes that children who are held back a grade in elementary school are more likely to get arrested in high school.  Now of course that is just a correlation, it doesn't mean that getting held back causes delinquency.  Randomly assigning kids to getting held back is out of the question.  What can be done?  So it occurs to the sociologist to find sibling pairs who are discordant for getting held back.  Within pairs, it turns out that the one who was held back is no more likely to get arrested than his sibling who was not held back.

What do we conclude from this?  Presumably it would decrease our impression that holding-back causes arrest, because if that were true why wouldn't it happen within pairs as well as between them?  We might further conclude that the original observed correlation must have been the result of something else that sibling pairs share, eg families and everything that goes along with them.  On the other hand, it might turn out that the held-back sibling is more likely to get arrested than the co-sib.  Does this prove causation?  No, but it strengthens our confidence in a causal hypothesis, as it survived a fairly rigorous test.  In the absence of randomization, this may be the best we can do.

My main point is that this sociologist is doing "behavior genetics."  Among the familial things that siblings share, of course is half their genes.  The other is their family environment.  OK, you say, but it isn't a "heritability study".  But it is.  If you drew sibling pairs at random from the population rather than selecting them for being discordant for held-back, you could partition the held-back variance into a Between and a Within pair component, and B/(B+W) would be the intraclass correlation for sibling pair.  The design is not yet genetically informative, so the correlation would be the "familiality" of being held back.  If you wanted, you could report this quantity, and include a latent variable for it (like an ACE latent variable) when you analyzed the data.

The key to doing a bivariate twin study clearly, in my view, is recognizing that (a) The variance components (the h2-equal part) are not the main point, (b) The within-pair effects (the genetically informed quasi-experimental regression part) are the main point, and (c) The correct way to analyze the within pair effects is to ensure that they are invariant against changes in the variance components, that is ensuring that (a) doesn't interfere with (b).  This is what the Turkheimer and Harden chapter is about.

DZ twins are just siblings, of course, and if you throw in MZ twins and all the assumptions that Burt et al don't like it turns into a bivariate twin study, but the basic logic doesn't change.  Held-back and arrest are related between and within pairs, now in MZ and DZ twins.  Zygosity and the twin assumptions, if you are so inclined, allow you to divide the "familiality" thing from the sibling study into A and C, and I think it is often interesting to think about whether the confounds of the purported causal effect appear to be genetic or family environmental.  However, it remains absolutely true that the magnitude of these components is not the main point-- the within pair relationship between held-back and arrest is the main point, and the data should ideally be analyzed in a way that keeps this relationship invariant to changes in the decomposition of the predictor.

The bivariate criminology twin studies that I read, in my opinion, don't do a great job of keeping the "heritability" issues separate from the within pair regression issues.  I would analyze and report the results differently.  Burt et al, in the same way, see the MZ and DZ twins and the reported heritabilities, and conclude that they must be "heritability studies" even though they are, at least potentially, more than that.  And the great irony is that in most of them, the within pair relationships between X and Y survive the test of having their common genetic background controlled.  So in Boutwell et al, for example, there is a significant within-pair relationship between low self-control and victimization.  This means that in pairs of identical twins, the twin with lower self-control is more likely than the co-twin to be a victim, controlling for whatever genes and family background identical twins have in common.  This is a victory for environmental-- better to say phenotypic-- causation, but it gets lost in both the original report and the objections, because everyone is hung up on worrying about what might have turned out to be heritable.

Well as usual this has turned into more tooting my own horn than resolving this particular debate.  My conclusion is that behavior genetics has an important role to play in criminology, not because criminal behavior has in any important sense turned out to be "genetic" or "biological," but instead because criminology is almost always stuck with inferring causal processes from correlational data, and careful use of twins can help rule out important classes of confounds of those causal hypotheses.  This is less attention grabbing than concluding that "criminality lurks in the genes" like they said in that infidelity study, but ultimately much more useful scientifically

Thursday, June 4, 2015

Callie Burt Replies

Here.  I have a talk to get ready for and I won't be able to think much about this before tonight.  It isn't clear to me, in general, how much arguing I want to do here.  In some ways that's the point, but it gets old and/or nasty quickly.

One rule I have sometimes considered is that a reply has to be less than half the length of whatever it is replying to.  Exponential decay being the rapid process that it is, after a few back and forths the disputants can yell,





at each other and that will be the end of it.  I think Callie's post is longer than mine, but I hadn't invented the rule yet.

Monday, June 1, 2015

The Criminology Debate

As most readers will know, there has recently been an extended debate about the value of "heritability studies" in the journal Criminology.  Burt and Simons original paper is here, with a reply from Barnes et al here, a rebuttal from Burt and Simons, here, and a reply here.  I was briefly involved in the editorial process, between the original paper and the reply.  This is a long complicated argument, the authors have done a good job stating their positions, they don't need me to referee it, and I spend far too much time arguing about theory anyway.  So I am not going to work my through all of it point by point.

What I do want to comment on is the use of my name as catch-all reference for the idea that "heritability studies" (see Point 3 below) are flawed.  Burt and Simons cited me this way in the original article, and then in a very strong way in the first sentence of their rebuttal.  Are Burt and Simons really "echoing the calls" of behavioral geneticists in calling for an "end to heritability studies"?  That is what I want to address in this post, although I won't be able to resist some more general comments along the way.

1)  One problem in this whole debate, evident in the sentence quoted above, is the purple language used on both sides, something I can be guilty of myself.  Calling for an end to a certain kind of study sounds a lot like encouraging scientific censorship, which is the way Barnes et al. took it.

2)  If nothing else, the generic citations of Rutter and Turkheimer as a kind of appeal to authority is a lousy way to argue.  What did I say, exactly, and why is what I said relevant to the current argument?  Many people on the BG side of things could care less what Turkheimer says, because they think I am completely wrong.  And if people on the other side of the argument were paying attention, they wouldn't like a lot of what I have had to say either, see below.  Science isn't about authority.

3)  One ongoing problem I have with a lot of recent anti-BG writing is the whole idea of a "heritability study".  Evan Charney is another person who trades in this idea.  A heritability study isn't a thing.  A heritability is a descriptive statistic, an effect size, not a kind of study.  It is kind of like writing a critique of social psychology and railing against "F-ratio studies."

4)  What Burt and Simons think they mean by a "heritability study" is a study that has no point other than estimating the heritability of something.  My friend Ron Yeo used to refer to these as h-squared-equals studies.  On this point they can cite me, and the 2011 paper they cite is a reasonable source.  The heritability of criminality doesn't mean that it has somehow turned out to be "biological" and whether the estimated value in some twin study is .3 or .65 makes very little difference and doesn't tend to replicate anyway.  In fact, the one and only time I have ever written anything about criminal behavior was in my first (1998) paper on this subject, when I got after Sarnoff Mednick for overinterpreting the heritability of criminality. But see next point.

5)  Barnes et al are right: I do twin studies for a living, and it would be mighty hypocritical of me to declare that they are useless in general.  As a BG person who has spent a lot of time criticizing the heritability concept, I have made it a discipline to never suggest that my doubts about numerical heritabilities should lead to a general dismissal of genetic effects on behavior or the behavior genetic enterprise generally.  The one thing that is for sure about the heritability of behavior is that it isn't zero (or one), and while I doubt that this fact has deep implications for how we think about ourselves as human beings (we already knew that we were biological, genetic beings), it has profound implications for how we conduct ourselves as social scientists.  Bottom line, it means that we can never interpret correlations among biologically related people, or within individual people across time, as necessarily environmental in origin.  This fact has nothing to do with numerical heritabilities, the EEA, rDZ=.5, the additivity of genes and environment, or any of the other long-standing bones of contention.  It is true under the loosest possible interpretation of the meaning of quantitative genetics.

6)  I suspect that Burt and Simons think they have this point covered.  Early in their first paper, they have a very nice paragraph (bottom of 225) about how they have no intention of dismissing the importance of genes for criminal behavior, or of endorsing radical environmentalism or social determinism.  That's a nice sentiment, but I don't think they live up to it.  Where in the remainder of their articles is a concession that genetic pathways rule out certain interpretations of the data, an acknowledgement that criminology has to take genetics into account when it is interpreting its findings?  Like every anti-BG paper I have ever read, they spend the rest of their paper finding something to attack in every single genetically oriented paper they can find.  Twin study?  EEA.  Adoption study?  Prenatal effects.  If all of non-experimental social science were held to this standard it would just go away.  The fuzziness of the "heritability study" concept allows them to fade from doubts about heritability coefficients, with reasonable citations to me, to dismissal of behavior genetics or even quantitative genetics in general, which is wishful thinking and for which I offer no support.

7)  Basically, I think post-heritability twin studies are useful as quasi-experimental tools to investigate causal hypotheses about observed associations when random assignment is impossible.  The best citation to my ideas about how twins can be used to do useful social science is Turkheimer and Harden (2014), in Reis and Judd, Handbook of Research Methods in Social and Personality Psychology.  It's a commercial book and I won't post the link here, but if buying it presents a financial hardship let me know.

8) Now the question is whether the studies that Burt and Simons list are h2-equals-studies or more interesting genetically informed social science.  I'm not going to take the time to go through them one at a time, but the several I looked at were bivariate "quasi-causal" (as we call them in our lab) studies.  Ironically, the ones I looked at were actually quite consistent with phenotypically causal interpretation, ie the effects don't go away when you control for genetics.  This is something that genetic researchers often miss:  they think they are supposed to be interested in genetic pathways, A effects, but in fact the interesting hypotheses are usually about E effects, associations within identical twin pairs that remain with genetic differences controlled.  See Turkheimer and Harden.

9)  Moffitt and Beckley wrote a nice reply about epigenetics and I won't go into depth about it.  I think that people who think that epigenetic explanations of behavioral differences are important should go ahead and do the research and show it.  I doubt very much that a demonstration of meaningful epigenetic effects would meet with any opposition in the behavior genetic community.  Epigenetics of behavior is behavior genetics.  Epigenetics and classical genetics aren't at odds on a biological level, and there is no reason they should be at odds in social science.

10)  Like a lot of recent anti-BG theorists, Burt and Simon are just wrong about GCTA.  I have my doubts about some aspects of GCTA, discussed here.  But Burt and Simons cherry pick the few studies that have produced zero GCTA-heritabilities, and ignore the many others that look almost exactly like twin studies with somewhat smaller effects.  And it makes perfect sense inside the paradigm that the effects would be smaller.  Differences between twin heritabilities and GCTA heritabilities are interesting, varied in magnitude, and as far as I know still awaiting thorough theoretical explanation.  But the idea that GCTA has shown that twin studies were wrong all along isn't even close. In fact, the conclusion of my GCTA paper captures my overall thoughts on heritability in both directions, as follows, noting especially the first sentence:

The Visscher et al. (2010) program should drive a stake through the heart of a classical line of argument against classical behavioral genetics and its attendant statistical assumptions. Nevertheless, it is difficult to see how their will make much of an impact on the more contemporary problem, which is that quantitative genetics, despite demonstrating the universality of heritability, has failed to offer much in the way of etiological insight into complex behaviors, and moreover that the very ubiquity of heritability has made it problematic to differentiate between heritable phenotypes that have genetic mechanisms and those that do not.

So in conclusion:  if you want to cite me as a critic of some general version of BG, the citation should be limited to the idea that numerical heritabilities aren't very important per se, and that studies that do nothing other than estimate them are no longer very important.  The next sentence should be something about how I do maintain that nonzero heritability is important methodologically, and that there are many scientifically useful things to do with twins other than just estimating heritabilities.  Better yet, be very specific about what it is I am supposed to have said when you cite me.

One more self-quote and I'll shut up.  At the end of my 1998 paper (Almost 20 years ago!  Yikes.) I said,

I will close with two recommendations, one very practical and the other theoretical, for future discussions of nature-nurture.  The practical suggestion is that all sides of the issue should stipulate the first law of behavioral genetics and refrain from further discussion of whether or not the heritability of anything is equal to zero.  As a reader of behavioral genetics, keep a pencil by your side and lightly excise everything either asserts nonzero heritability or attempts to explain it away:  Much space could be saved in our journals (even those containing sophisticated multivariate genetics or well-informed opposition) if this recommendation were put into effect.

Friday, May 29, 2015

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.


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.

Tuesday, February 19, 2013

Development and Psychopathology

Chris Beam and I have a new paper out at Development and Psychopathology.  Link here.