pz

Yeah, they've bamboozled a lot of people. The idea that someone can dissect the genetic basis of behavior in people is a compelling one. Unfortunately, the methodology is not. Twin studies thrive not because the research is any good, but because people want to hear the answers.

I've just begun a study of my own, looking at patterns of behavior in different genetic lines of fish. These are very difficult experiments. We're going to spend quite a bit of time developing techniques to quantify behavior. We're already seeing that the range of behavior, even in these highly inbred, nearly isogenetic lines, is immense, so picking out signal from noise is going to be difficult. We're going to have to do hundreds, and eventually maybe thousands, of controlled crosses -- I'm going to have to expand my colony size significantly.

I've been looking at similar animal studies a lot, lately. The comparison with the twin studies in humans is striking.

Animal studies spend a lot of time struggling with issues of control. Subtle environmental differences can rapidly swamp out the effects you are trying to measure -- I've been looking at feeding behavior, for instance, and have been finding that our larval feeding protocols can strongly color the adult response. It's a major pain to set up consistent rearing procedures that do not bias your results.

The human twin studies, of course, can't control anything. Instead, they try to use lots of statistics to argue away the existence of environmental bias. We know strong environmental biases are present, but somehow, these authors always end up arguing that they don't matter.

I mentioned the huge range of variation we see in our animals. This is another complication, and the only way around it is to measure the variation, and to consider it a legitimate part of the phenomenon you are studying. That takes numbers. Preferably big numbers. Personally, I only start to get comfortable with an observation when I've got about a hundred individuals that support it. And no, that doesn't mean I've got 99 animals in group A that act just like all 100 control animals in group B, but that one of the As showed something different so strongly that it skewed the average.

Human twin studies are different. They are all small in number, and because there are no controls, every twin is an independent experiment. Anecdote is big business in this field. Lykken, the guy cited above, dreams of coming up with statistical methods to make even a single observation a statistically significant event...which makes me wonder if he even understands the point of statistics.

The killer for me, though, is the interpretations researchers make. In animal studies, caution is the rule (with some exceptions, of course). In the twin studies...whoa, look out. Anything goes. Look at the subject line here: your happiness is genetically influenced! Now think about the numbers of twins involved, and how each one is an uncontrolled experiment -- this is a ridiculous conclusion. They don't have the data to support it.

There is simply an amazing inverse correlation between the rigor of the science being done, and the magnitude of the claims for a genetic basis for behavior being made. I can't fault the twins researchers for the quality of the underlying science -- it's an unfortunate consequence of trying to study anything in people, where you have so little control over much of anything -- but these interpretations they make...! It's like watching Coyote run off the edge of a cliff. There's nothing to support him, but there he is, and what's worse, people are still believing in him.

ps418

It is amazing. In fact, twin researchers have managed to 'bamboozle' the vast majority of psychologists and geneticists, including leading members of prestigious orginizations like the American Psychological Association and the American Society of Human Genetics, that there is a significant genetic component to many individual differences. So, I suppose that most geneticists and psychologists are, like myself, "extremely credulous." But I guess that twin studies can't take all of the credit, since studies of unrelated twins reared together (URT) have played a major role in shaping the current concensus as well.

It is indeed amazing how when it comes to purely environmental explanations of human behavioral differences, some people will look at the facts with a squinted eye through the wrong end of a telescope, and completely neglect to control for genetic similarity, yet when it comes to genetic and environmental explanations of human behavioral differences, the facts are viewed through an electron microscope. Of course, the notion that, for instance, cognitive abilities and personality traits are thought to have substantial heritability simply because that's the answer that people want to hear, rather than the on the basis of evidence accumulated from twin, sibling, and adoption studies, is laughable.

Interestingly, Herman Muller himself waxed enthusiastically about reared-apart twins and their ability to demonstrate genetic influences on human behavior. He even published a study of one pair of such twins.

1925. Qtd. in Bouchard, TJ., 1997. IQ similarity in twins reared apart: Findings and responses to critics. In RJ Sternberg, E Grigorenko (Eds.) Intelligence, Heredity, and Environment, p. 132.


That's true in a sense. They can't literally control the environment the way you can control the environment in strain and selection studies. This is not unique to twin studies of behavior, or behavior genetics, but applies to virtually every field which studies human diferences. What can be done is to look for relationships between environmental variables and trait variables (for instance, a relationship between income and WB, or parental SES and IQ). In many cases, including the one described in the OP, the environment is found to have a significant effect on individual differences.

That's plainly not true. The environment does 'matter' in most cases, and the researchers themselves are usually careful to point this out. Furthermore, bias can be checked for statistically in most cases. For example, with regards to the MISTRA findings on the heritability of IQ, there was an argument about whether there was a significant ascertainment bias in the Minnesota twin study. This argument was largely settled when it was shown that the results of MISTRA replicated across 5 studies of MZAs, including those who were found using national birth registers and which are therefore not nearly as susceptible to ascertainment bias, as well as through the use of a completely different experimental design, such as adoption studies of unrelated children raised together.

Best of luck with your study. No one, least of all me, is going to question that behavior is variable between genetically identical animals. As I've said repeatedly, environment is important in producing individual differences in behavior. Nevertheless, the influence of genes on animal behavior was established long ago, such that Darwin took it for granted in his iThe Descent of Man and Selection in Relation to Sex. If genes do not play a substantial role in influencing human behavioral variation, then humans would be a highly anomolous species indeed.



That depends on what you consider small, and which particular traits we are considering. Some traits have been studied using very large samples of reared-together twins. In the twin studies of WB which I mentioned in the original post, there were large numbers of twins: 647 MZT pairs, 733 DZT pairs, 75 MZA pairs, and 36DZA pairs. The retest sample was smaller, though. That's well over 2000 individuals. The results for reared-apart and rearer-together were identical, within error.

As another example, Bouchard and McGue (2003) list 4 recent, large-sample reared-together twin studies, using both MZs and DZs, of the "Big Five" personality dimensions, with between 250 and ~1000 twin pairs each, spanning 3 countries, all of which produced consistent results, and results consistent with earlier studies on the same traits, and results consistent with reared-apart twin studies, and studies of unrelated siblings reared together. The same can be said for cognitive abilities. Plomin and Spinath (2002) note that the case for a substantial genetic influence on cognitve ability, far from resting upon the MZA studies with limited numbers, is supported by "dozens of studies including more than 8,000 parent-offspring pairs, 25,000 pairs of siblings, 10,000 twin pairs, and hundreds of adoptive families" (Genetics and general cognitive ability (g), Trends in Cognitive Science 6(4), p. 169).

The number of reared apart-twin studies is indeed small (~5), but because of the statistical power of the experimental design, small samples can produce statistically highly significant results. According to Bouchard, "the statistical power of this design is remarkable. For a trait with a heritability of about 0.50. . . 50 pairs of MZA twins have roughly the same statistical power as 1,000 pairs (500 MZ and 500 DZ) of twins reared together - the heritability estimates have the same 95% confidence interval" (Bouchard, 1997, p. 136).

Further, as I have already said, the consistency of heritability estimates across studies, and across experimental designs, makes the case for genetic influence much stronger than it would be for one study or one experimental design by itself. Regarding IQ heritability deduced from MZA studies, Bouchard notes that "one of the striking findings from the IQ data in the MZA studies is the replicability of findings across studies, measures, countries, and cohorts. The studies span over 50 years, involve many different measures of IQ, took place in five different countries, and were conducted in three languages" (1997, p. 146).


I may be misunderstanding you here. The control for each twin is the co-twin. In studies of reared-together unrelated children, the other children are the controls.

Patrick

pz

By golly, you're right.

Lombroso measured the skulls of tens of thousands of criminals and non-criminals, and came to the conclusion that he could tell who was a bad guy from just simple physiognomy. Heck, he could identify prostitutes just by looking at their big toe! This was accepted by the majority of scientists in his day, so he must have been right.

And Yerkes put the statistics of your favorite psychologists to shame: he measured the IQs of 1.75 million servicemen, and determined that black people were roughly half as smart as white people. This, too, had the consensus of a majority, so who am I to question it?

Oh, and Cyril Burt...knighted, no less, and appointed to the highest academic position in his field in England by the accolades of his peers. We should overlook the minor matter of a little fraud, and consider only the weight of authority behind his ideas.

I am well aware of the numbers and statistics behind the twin studies. I guess I should just go along with them. After all, if their p values are less than 0.05 in their measurements of correlation, their inferences about cause must be equally significant. Correlation and cause are the same thing, aren't they?

I'm also really interested in your comment that "the influence of genes on animal behavior was established long ago, such that Darwin took it for granted in his The Descent of Man and Selection in Relation to Sex". I looked through my copy, and I can't seem to find any place where he mentions genes. Where is it?

I did notice several places where he takes it for granted that exercise of a behavior over the course of several generations will lead to the behavior becoming fixed. Since this was long ago, and was accepted by an authority of the magnitude of Charles Darwin, it must be true. It looks like I'm going to have to substantially revise the syllabus for my genetics class.

Jesse

Isn't the methodology of twin studies essentially the same as double-blind tests for medicine? If you want to establish that a drug has some significant effects, you just need to get a large group of people and then randomly select half that group to recieve the drug and half to recieve a placebo...it doesn't really matter if your original group was a representative sample of the population as a whole, they could all be albinos or something, all that really matters is that the choice of who would recieve the placebo was made randomly, so any statistically meaningful difference in between the two groups must be attributed to the drug. If the effect is, say, "reduced flu rates" then this shows that the drug has a meaningful effect on likelihood of getting the flu in at least some proportion of the population, even if you can't always generalize that to the population as a whole. This is still a nontrivial result, since I'm pretty sure there would be no subset of the population that would show any difference between taking a placebo and something totally ineffective, like one of those super-diluted homeopathic cures (and I suspect that in real double-blind tests they do try to get a representative slice of the population as a whole, but my point is that you can get a significant result even if you don't bother).

In the same way, as long as you assume adoption agencies don't use different criteria when looking for homes for separated identical twins vs. separated fraternal twins, and as long as you assume the families themselves have no knowledge of whether their adopted child has an identical or a fraternal twin, then this should be exactly analogous to a double-blind test. If you find a statistically significant difference in correlations with the unseen twin in the two groups, then that demonstrates a genetic effect in at least some subset of the population. You can't necessarily generalize this to the population as a whole--it's possible that something about the types of homes that are more likely to have adopted children is also exacerbating the effects of genes on personality or intelligence or whatever--but it is still a nontrivial result, just like in the double-blind test for a medicine.

ps418

By golly, I can't find much of anything in your latest diatribe that resembles a response to anything that I've written.

<scratches head> Gosh, that Lombroso fellow sounds like quite an idiot. I wonder how he found his way into this thread?

But since you brought it up, I really do find it hard to believe that a majority of scientists --even that long ago-- were credulous enough to belive that prostitutes could be identified by their big toe. But to prove to you my willingness to change my views based on evidence, I invite you to offer the evidence supporting your assertion that Lombroso's ideas were "accepted by the majority of scientists in his day," rather than by a minority of scientists, or just a handful of cranks?

<scratches head again> This is all very interesting, but how is this silly parade of fossilized straw men relevant? After all, I never stated or implied that any proposition should be accepted simply on the weight of 'authority.' What I did point out is the simple fact that your views on twin studies and genetic influences on human behavior are not shared by most geneticists or psychologists.

You must have been Duane Gish's favorite student in logic class! Thanks for that delicious red herring. I love red herrings, especially when spiced up with a liberal dose of derisive sarcasm and served in the finest style of strawman argumentation. Of course, I never once referred to Burt or his twins, nor are any of my assertions dependent on Burt, nor did I suggest that anything should be accepted on the weight of authority alone. But let's not let the content of the thread get in the way. There are 5 seperate reared-apart twin-studies, excluding Burt's, all of which have yielded consistent results. Those studies, in addition to the related research using completely different experimental designs, such as reared-together twins and same-age adoptive siblings reared together, are what I referred to.

I would draw a historical parallel with Haeckel's embryo drawings (or Piltdown man, etc.). Although they were fraudulent in detail, and persisted for a long time, the evidence from developmental biology nevertheless still supports an evolutionary explanation of similarities and differences in animal development. Likewise with Burt and MZA studies of genetic influences on human behavior. The case for genetic influences on cognitive ability is no more dependent upon Burt than the case for evolution is dependent upon Haeckel.

I suspect there may be little value to me or anyone else in responding to such sarcastic rhetoric. But I will respond anyway. Correlation is of course not necessarily evidence of causation. And of course, no one has suggested otherwise. But the right set of correlations, combined with background kowledge, can be causally persuasive, for instance in epidemiology. Just a second's thought will bring to mind numerous contexts in which correlations can be used to make strong causal inferences, sans direct experimental manipulation of the independent variable. For instance, no one has ever taken a sample of pregnant women and experimentally injected them with alcohol to determine the effects of fetal alcohol on childhood cognitive development. But the correlational data is causally persuasive.

I'm glad you found something in my post interesting. I happily concede this point. Darwin did not actually use the word 'gene,' and further, no one in Darwin's era knew that 'genes' per se influenced behavior.

My claim was merely that a genetic influence on animal behavior was well accepted even in the 19th century. But dont let that fact get in the way of your childish diatribe. If you wish to revise your syllabus so as to teach your students that Darwin had some erroneous ideas about the mechanisms of inheritance, you have my encouragement. But that will not change the fact that Darwin was largely correct about the influence of heredity on behavior, both in humans and in other animals.

Patrick

Jesse

Another way of stating the argument in my last post is that although it is true that we cannot infer causation from correlation in general, the setup of double-blind experiments (in which subjects are randomly assigned to the control group or the test group) virtually guarantees that any statistically significant differences between the two groups must be caused by the factor that we chose to vary (whether this was drug vs. placebo or fraternal twin vs. identical twin). Of course, it is possible that the family a separated twin ends up with is not truly random with respect to the type of twin it has (fraternal or identical)--for example, the ratio of fraternal:identical twins might not be the same in all ethnic groups, and babies of a particular ethnic group are probably somewhat more likely to end up with parents of the same ethnic group. Still, I'd be interested to know which part of my argument pz would disagree with--would he disagree that we can be close to 100% certain that correlation implies causation in a double-blind experiment, or would he disagree that adoption faithfully replicates the conditions of a double-blind experiment?

echidna

pz, like it or not (& I don't particularly), in the field of human psychology, behaviouralists have given a lot of ground to geneticists over recent decades. Of course that's not to say that environment has no part to play in the nature / nurture debate, only that last time I checked, many if not most psychological bodies seemed to acknowledge that genetic factors influence some facets of human behaviour, intelligence being the one I am most familiar with .

ps418

After reading a bit more about genetic and environmental influences on personality, there are a few more points I want to make. First, there are several relevant recent studies, with a combined sample size of ~50,000 individuals, from three continents and using a variety of different kinships, that provide further support for a significant genetic influence on personality, including personality factors relevant to subjective well-being. Second, I want to discuss the data from adoption studies, which support the results of reared-apart twin studies but are far less widely known. And third, l want to look at some of the potential problems and confounds with behavior genetics research, and how they have been, and continue to be, addressed.

Several recent twin studies investigated environmental and genetic influences for each of the Big Five personality factors. For each study, all five factors showed signficant heritability, even greater unique environmental influences, but insignficant shared environment influences. The "Negative Emotionality" factor (roughly, the tendency to experience negative emotions), also referred to as the Neuroticism factor, has a broad heritability of ~0.4-0.6, essentially identical to the broad heritability of the MPQ well-being scale. Jang et al. (1996) calculated a broad heritability of 0.41 for a Canadian twin sample (MZ=123 pairs, DZ=127 pairs); Riemann et al. (1997) calculated a broad heritability of 0.53 for a German twin sample (MZ=660 pairs, DZ=304 pairs); Loehlin et al. (1998) calculated a broad heritability of 0.56 for an American twin sample (MZ=490 pairs, DZ=317 pairs), which is very close to an estimate of 0.58 calculated by Waller et al. (1999) for a smaller American sample (MZ=313 pairs, DZs=91 pairs). Lake et al. (2000) report a sex-difference in the heritability of Neuroticism (M=0.423, F=0.504), based on a combined sample of 45,850 members of extended twin kinships from Australia and the United States. For the personality factor "Extraversion" (more appropriately called "Positive Emotionality") the results were essentially the same. Broad heritability ranges from 0.49 to 0.57, with a mean of 0.54.

These results are strongly supported by adoption studies of personality as well, which I discuss below. And though rats and rhesus monkies can't fill out questionaires, variation in the behavioral and neurochemical phenotypes in these animals that serve as crude mammal models for human personality are clearly genetically influenced (e.g. Champoux et al., 1999, 2002; Fernández-Teruel, 2002; Flint, 2002). It is also significant that the greater behavioral similarity of MZs compared to DZs is evident even in infancy (Freedman and Keller, 1964).

A Caveat About Range-Restriction

An important caveat here is that virtually all of the members of all of these samples grew up and live in US and other relatively wealthy countries (US, Australia, Germany, Canada). This range-restriction is important to keep in mind, because variation in well-being-relevant environmental influences may be limited in the US compared to the rest of the world. Indeed, most of the poor in the US are quite well-off by the standards of most countries, in terms of income, access to health-care, and educational oppurtunities. Thus, factors such as income may account for very little (<4%) of the variance in the Well-Being in a US sample, but account for more variance in a sample including many other countries, including those with more adverse or impoverished environments.

Cross-cultural comparisons of average well-being by Inglehart and Klingemann (2000) suggest that this may be the case. They compare average levels of 'life satisfaction' for the populations of 65 countries. There is substantial variation in the percentages of people who self-describe as "Happy overall," or "Satisfied with life overall." These measures in turn correlate strongly (r=0.7) with the country's economic development (GNP/capita). As might be expected based upon the American data, however, the "correlation weakens as one moves up the economic scale," such that "above $13,000 in 1995 purchasing power parity, there is no significant linkage between wealth and subjective well-being" (p. 171). None of this is to deny the influence of genetic factors on individual differences in subjective well-being -- the authors state: "we find that evidence compelling" (p. 182) -- but that environmental influences are an even larger source of variation. Even in the US samples, the broad heritability is about ~0.4, which means that most of the variance in well-being is the result of environmental differences.


Adoption Studies Independently Replicate Twin Studies

The large adoption studies that have been carried out over the last couple of decades are just as signficant as the reared-apart twin studies, but are far less widely appreciated. Adoption studies are important because they provide an independent test and replication of the results of twin studies. This shows that the results of twin studies are not due to some peculiar feature of twins, or some peculiar feature of the twin design. For example, if MZAs as a group are no more similar for a phenotype that MZTs, this would suggest that variation in rearing environments play little or no role in producing variance in that trait. The 'shared environmental effect' in reared-apart twin studies is equal to the difference in correlation between MZTs and MZAs, the heritability is equal to the MZA correlation itself, and the non-shared or unique environment effect is 1 minus the variance components for genes and shared environment. For instance, for each of the Big Five personality factors, the mean MZA correlations (0.3-0.6) are not signficantly greater than the MZT correlations, and the DZT correlations are not significantly greater than the DZA correlations. In fact, the difference rarely even attains signficance. For instance, the mean correlation for all 11 Multidimensional Personality Questionnaire scales is 0.5 for MZTs and 0.49 for MZAs (Bouchard et al., 1990; see also Finkel and McGue, 1997). This suggests that sharing a rearing environment, even for an entire childhood, does remarkably little to make people similar with respect to personality.

This can be quantitatively tested with an adoption design. Whereas the shared environment effect is estimated indirectly in twin studies by comparing MZT and MZA correlations, it is directly estimated by the adoption design. If sharing a rearing environment does not make individuals more similar with respect to a trait, then within-pair correlations for genetically unrelated individuals reared together will be insignificant. And this is exactly what has been found in adult adoptees with respect to personality and congnitive ability, for instance in the Texas Adoption Project (Horn et al., 1979; Loehlin et al., 1985, 1997), the Colorado Adoption Project (Alarcon et al., 1998; Plomin et al, 1998; Wadsworth et al., 2001, 2002; Petrill et al., 2003), the Minnesota Adoption Project (Scarr and Weinberg, 1983; Scarr et al., 1993). For instance, the parent-child correlation for Neuroticism in adoptive families is 0.05 (Scarr et al., 1981), and that for Extraversion is (0.04) (Loehlin, 2001), precisely as we would expect based on the twin studies, but flatly contradictory to what we would expect based on any "environment only" theory of personality development. Just as MZ twins are similar whether reared together or apart, unrelated individuals are dissimilar whether reared together or apart.

The adoption design can yield heritability estimates as well, as long as the biological parent(s) are included in the design. If genetic differences are a significant source of variance in personality, then significant correlations between the adoptees and their biological parent(s) should exist even when the adoptees were adopted in infancy and had no contact with their parents. This has been found also. For the Texas Adoption Project, for example, the average adoptive mother--adopted child correlation for all 9 MMPI scales was is 0.00, while the average biological mother--adopted child MMPI correlation was 0.18. By comparison, the MMPI correlation between the adoptive mothers and their biological children was 0.24 (Loehlin et al., 1987). Thus, the parent-child personality resemblance observed in biological families is nearly as great (0.24-0.18=0.06) even when the child has no contact with his/her parents after infancy. And though data is rather limited for biological parents of adopted children, existing data suggest that the parent-child resemblance for both Neuroticism and Extraversion factors is only slightly lower when the child is adopted away in infancy as it is in normal families (Loehlin, 2001). Again, this counter-intuitive result is just what we would expect based on the twin studies.

Adoption studies also replicate twin studies in showing that the relative strengths of genetic and environmental influences change during development, with genetic influences typically becoming stronger with age (McGue et al., 1993). Both cross-sectional and longitudinal adoption studies show that modest but significant correlations between adoptees do exist in early childhood. But in contrast to biological families, these correlations gradually diminish from about 6-18 years, virtually dissappearing by adulthood. During the same time, the adoptee correlations with their biological parents increases. In the Texas Adoption Project sample, for instance, the heritability of IQ increased from 0.38 to 0.78 from middle childhood to adulthood, while the shared environment effect declined from 0.19 to 0.00 (Loehlin et al., 1997). Indeed, one of the tactics used by those who have wished to minimize the influence of heredity on behavior has been to average together data from all age groups (for example, Devlin et al., 1997). Because far more data exist on young children than adults, this averaging will yield relatively lower (but still very significant) heritability estimates and relatively higher shared environment effects, compared to a sample consisting of adults only.

Ongoing research on "virtual twins" by Nancy Segal and colleagues illustrates these patterns for cognitive ability (Segal 1997, 2000). Her adoptive sample consists of 90 pairs of reared-together, same-age, unrelated children (dubbed URT-SA's). The children consist either of a biological child and an adoptee, or two adoptees, who are within 9 months of age and have been reared together from infancy (average adoptive age is ~50 days). Mean intraclass IQ correlations for this sample is 0.26, which is significant, and expected because the mean age of the sample is only 9.4 years. For similar-aged MZTs and DZTs, the same r's are 0.86 and 0.6. The IQ subtest profiles (a profile of cognitive weaknesses and strengths) correlate 0.08, compared to 0.45 and 0.24 for MZTs and DZTs, respectively. Average within-pair score differences are 13.26 pts, compared to 17 pts for random individuals, 10 pts for DZTs, and 6 pts for MZTs. Although only 5% of the sample is 20 or older, and most are Segal (2000) reports a trend for increasing pair dissimilarity with age, as expected. In the Texas Adoption Project, the sibling IQ correlation was 0.26 at 10 yrs of age, but declined to 0.02 at 18 yrs of age (Willerman, 1987).

Finally, the caveat stated above should be restated for the adoption data-- the worst home environments in society tend not to be represented in adoptive families, which are mostly middle or upper class. There is every reason to believe that some environments, particularly those at the extremes of neglect and abuse or envionmental deprivation, will have a significant and lasting negative effect on personality and cogntiive development. Nevertheless, these studies do span a wide range of environments, and generalize suprisingly well. Even Eleanor Maccoby, the matriarch of child-development research, admits that, in general "the behavior geneticists have made their case. Children's genetic endowments do clearly affect how individuals develop- in comparison to other children-- to a much greater extent than was thought to be the case during the years of the ascendency of reinforcement learning theories and psychodynamic theories" (2000, p. 11).


The Problem with Socialization Research

This set of findings highlights a critical weakness in socialization research based on correlational studies within 'traditional' biological families. There are countless examples of sociological research looking at correlations between members of biological families, and using these correlations to make causal inferences about socialization. For instance, anxious mothers tend to have anxious children, and this is interpreted to mean that the child's anxiety is caused by internalizing the mother's anxious behavior -- an environmental transmission. The problem with that type of causal inference is that genetic and environmental influences are completely confounded in a 'normal' biological family, because children get both environments and genes from their parents, and the design does not allow one to disentangle the relative effects of each. Even worse, when you do "control" for genetic similarity using an adoption design, or "control" for rearing environment similarity using a reared-apart twin design, it becomes apparent that the shared genes are sufficient to produce many of the familial correlations thought to result from environmental transmission (e.g. Rowe, 1994; Harris, 1995, 1998; Cohen, 1998). Whatever flaws or potential problems there may be with behavior genetics, they are minor compared to the flaws in much traditional social science research based on the family model, which does not even attempt to control for genetic relatedness, and effectively assumes that behavioral differences are always the result of environmental differences, despite overwhelming contrary evidence.

In fact, failure to control for genetic relatedness actually limits the ability to identify relevant environmental influences as well (Pike et al., 1996; Reiss et al., 2000), a point that medical and psychiatric researchers understood long ago and now take for granted. Schizophrenia provides an excellent example of how genetically-informed research can be used to test hypotheses about environmental influences. The reigning theories of schizophrenia until a few decades ago were largely based on bad mothering (schizophrenogenic mothers). Today there are few psychiatrists who would dispute that genetic factors are significant in the etiology of virtually all forms of mental illness and behavioral disorders.

Adoption studies showed that, for the children of schizophrenics, the risk of developing schizophrenia is about the same whether the children are reared by their schizophrenic biological parents or by unaffected adoptive parents. Twin studies showed that MZ twins reared together are about 2-3 times more likely to be concordant for schizophrenia than are DZ twins reared together. Further, twin studies of disconcordant pairs have shown that the children of the unaffected twins are just as likely to develop schizophrenia (17.4%) as are the children of their affected cotwins (16.8%), so parental expression of schizophrenia does little or nothing to increase the genetic risk (Gottesman and Bertelsen, 1989). These facts cast considerable doubt on the purely environmental theories of schizophrenia that prevailed previously, to say the least.

Discordant twins are also valuable for determining which environmental influences are relevant to schizophrenia. For instance, Torrey et al (1994) found that affected twins in discordant pairs experienced more delivery complications and displayed subtle neurological deficits compared to the unaffected cotwins -- environment refers to all nongenetic facotrs, and need not mean "psychosocial."


The Prenatal Environment and Other Potential Confounds

By eliminating the shared rearing environment, reared-apart twn designs effectively eliminate most of the methodological criticisms of traditional twin designs. One potential remaining confound is the prenatal environment -- no DZ twins share a chorion, while two-thirds of MZ twins do share the chorion. To the extant that the shared chorion affects trait similarities in MZ twins, this could lead to a mis-calculation of heritability and shared environment effect in twin studies (but not in adoption studies), which assumes that there is no common environmental source of variance for MZAs. This possibility, which has been widely cited as a "major flaw" by some critics of behavior genetics, has been investigated by assessing intrapair correlations of MZ twins seperated by chorionic status. For instance, Jacobs et al. (2001) reported small but significant differences on 2 out of 15 WISC-R subscales (arithmetic and vocabulary) between monochorionic and dichorionic twins, accounting for about 10 and14% of the score variance on those two scales. There was no significant difference between the groups for 'total IQ' or the other 13 scales. Reise (1999) failed to find any differences on measures of child tempermant (irritability, resistance to soothing, activity while awake, activity during sleep, reactivity, and reinforcement value). The East Flanders Prospective Twin Study (EFPTS) in Belgium will allow for further testing of chorion effects on a variety of measures using a large and representative sample of twins. For instance, Wichers et al (2002) recently showed from an analyses of the EFPTS data (n=760 twin pairs) that chorionicity is not a confounding factor with regards to childhood psychiatric symptoms, and both monochorionic and dichorionic twins correlate the same for measures of psychiatric symptomatology (the Child Behavior Checklist, or CBCL).

Some Other Potential Confounds

There is some interesting related research looking at other potential confounds, particularly other violations of the "equal environments assumption" of classical twin studies, where heritability is calculated by comparing MZ and DZ correlations. Any environmental influences that unequally influences one type of twin may bias the results of twin studies. The chorion is one example of a potential violation of this assumption.

Some some critics of behavior genetics have appeared to argue that _any_ systematic differences in any kind of environmental influence between MZs and DZs renders uncertain the evidence for genetic influence on behavior. This is erroneous, as there are at least three different ways to calculate heritability (classic twin studies, reared-apart twin studies, full-adoption design), and only one of these methods makes an "equal environments assumption." And more importantly, it is possible to test for specific violations the equal environment assumption by examining relationships between measures of environmental similarity and with-pair trait differences, and the results of such tests have largely supported the validity of the assumption.

For instance, it could be assumed that MZTs are more similar than DZTs because parents tend to treat MZTs more similarly growing up, emphasizing their sameness and downplaying their differences. This possibility was explored by Loehlin and Nichols (1976), using a very large set of twins (n=850 pairs), and a questionaire designed to assess many different forms of childhood parental treatment. Some parents of course attempted to treat their twins identically and emphasize their similarities (dress them alike, give them the same toys, have them share a bedroom, have them placed in the same classes at school, etc), while other parents did the opposite. No signficant correlations between individual or composite measures of parental treatment and the actual trait similarities were found (see also Morris-Yates et al., 1990; Kendler and Gardner, 1998; Xian et al., 2000; Cronk et al., 2002). Scarr and Carter-Saltzman (1979) tested for the possibility that parental expectations based on zygosity infuenced IQ similarity in twins. This was done using a sample of twins with misdiagnosed zygosity -- DZ twins who were mistakenly thought to be MZ by their parents, and vice versa (a few percent of twins are misdiagnosed). The results of psychological testing showed that similarities reflected the true zygosity, not the parental expectations (see also Kendler et al., 1993).

Another possibility is that genes influence personality and cognitive ability very indirectly, by influencing appearance. For instance, two twins are both tall, dark and handsome due to their shared genes, which (the thinking goes) elicits the same treatment from the people in their environment, which in turn gives them similar personalities and cognitive abilities. It is easy to test this hypothesis (see discussion in Bouchard 1997, pp. 149-153) by looking for relationships between appearance and psychological traits. For instance, you could look at a sample of DZ and MZ twins, and see if those who are more similar in appearance are also more similar on psychological traits. With the exception of a handful of traits, they aren't (Matheny et al., 1976; Plomin et al., 1976; Kendler et al., 1994; Heterma et al., 1995).

This is supported by research relating appearance to various psychological traits in the general population. For instance, attractiveness is correlated 0.04 with IQ (n=3,497), 0.04 with general mental health (n=2,597), 0.09 with social anxiety (n=1,155), and 0.07 with a measure of dominance (n=2,858) (Feingold, 1992). Despite the general lack of association of appearance with objective measures of personality and ability and mental illness, it is true that "attractive people" tend to be rated as more intelligent, more mentally healthy, and so on, by peers. There is at least one variable that objectively significantly correlates with attractiveness -- a measure of 'social skills' (0.23, n=1,050). People may indeed be treated somewhat differently on average based on their appearance, and in this respect MZs are treated more similarly than DZs, but this appears to have little if any influence on most personality or cognitive traits studied by behavior genetics.

It will be a few days before I get back to the message board. So, if I take a few dats to respond, please don't think that I'm not ignoring you.

Patrick



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ps418

Rather than start a new thread on this topic, I'm digging up this one instead.

Although twin and adoption studies demonstrate that individual differences in the personality traits anxiety and 'neuroticism' are partly a function of genotype differences, the next step, crucial for understanding the relevant causal processes, will be to identify specific alleles that are associated with variance in these traits. However, because these traits are quantitative and possess a signficant additive genetic component, we should not expect to find one or two genes with very large effects, but numerous genes with small effects, so-called quantitative trait loci, or QTLs. This makes such associations much harder to detect than for genes associated with discontinuous traits (e.g. PKU), because the smaller the effect, the larger sample size needed to detect an association with statistical significance, and the greater the possibility of detecting a spurious association. This explains why progress in identifying QTLs underlying complex quantitative traits has been much slower than for single-gene, single-disorder, discontinuous traits.

Despite these challenges, several recent QTL associations with anxiety/neuroticism have been reported, and now await replication. Fullerton et al. (2003) performed a genome-wide scan for loci associated with variance in the personality factor neuroticism. Signficant associations were reported for regions on 1q, 4q, 7p, 12q, and 13q. One region on 1q is reported to be syntenic (at a homologous locus) with a previously described QTL associated with emotionality in mice.

Sen et al (2003) have reported the first specific gene variant associated with variance in neuroticism. The variant is a G->A SNP resulting in a substitution of methionine for valine in the brain-derived neurotrophic growth factor (BDNF) protein. The sample included 441 subjects (268 female), who were genotyped for the BDNF polymorphism. Personality assessment was based on a 181 item NEO personality inventory. The results indicate a signficant association of the polymorphism with neuroticism. The lowest neuroticism scale scores are associated with met/met homozygotes, while the val/val group scores the highest, and the met/val heterozygote group scores intermediately. Sen et al. estimate (p. 399) that the polymorphism accounts for 4% of the genetic variance in their sample, fairly substantial as far as QTLs go.

Enoch et al (2003) report an association of anxiety in women (measured with harm avoidance scales of the Tridimensional Personality Questionnaire) with a functional polymorphism in the catechol-O-methyltransferase (COMT) gene, which is involved in the metabolism of the catecholamine neurotransmitters dopamine and norepinephrine. The polymorphism is a G->A mutation at codon 158, resulting in a Val ->Met amino acid substitution and a marked reduction in COMT enzyme activity. The sample consisted of 401 individuals, 149 caucasian (92 women) and 252 native americans (149 women). Highest anxiety scores were found for the met/met homozygotes. Also reported was an association between the met/met genotype and low-voltage alpha resting EEG (characterized by weak or no alpha waveform at rest), a phenotype which had previously been associated with anxiety.

Recently this same poymorphism was shown to be associated with individual differences in pain tolerance and mu-opioid response to painful stimuli by Zubieta et al. (2003). In this study, 29 subjects were subjected to a 'pain challenge' involving injections of saline solution into their masseter muscles. Pain was assessed using McGill Pain Quesionnaire, and an affect scale. Also assessed, via PET scan, was the brain's mu-opioid response (mu-opiod receptors are the ones which interact with most opiates, as well as natural endogenous pain-kilers) to the pain challenge. The results indicate that met/met homozygotes showed reduced mu-opiod system activation and greater affective pain ratings, compared to met/val heterozygotes. For val/val homozygotes, the reverse was true -- they showed greatest mu-opiod activation, and lowest affective pain ratings, in response to the pain challenge.


Enoch et al., 2003. Genetic origins of anxiety in women: a role for a functional catechol-O-methyltransferase polymorphism. Psychiatric Genetics 13, pp. 33-41.

Fullerton et al., 2003. Linkage Analysis of Extremely Discordant and Concordant Sibling Pairs Identifies Quantitative-Trait Loci That Influence Variation in the Human Personality Trait Neuroticism. American Journal of Human Genetics 72.

Sen et al., 2003. A BDNF Coding Variant is Associated with the NEO Personality Inventory Domain Neuroticism, a Risk Factor for
Depression. Neuropsychopharmacology 28, pp. 397-401.

Zubieta et al., 2003. COMT val 158 met Genotype Affects Opioid Neurotransmitter Responses to a Pain Stressor. Science 299, pp. 1240 - 1243.

Patrick