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.