Another block in the IQ-hereditarian Jenga tower are the studies of adoptees and their IQs. Given that behavioral geneticists occasionally admit that familial studies can be theoretically confounded by environmental similarity, they typically point to adoption studies as confirmation of their estimates, as they seemingly suffer fewer biases (Joseph 2013). However, there are a number of issues with adoption studies that limit their ability to adjudicate heritability estimation debates.
Before we get into the issues, we should mention the way an adoption study works. There are actually a few different methods that behavioral geneticists can employ to estimate the heritability and environmentality of traits. The first is by comparing the correlation of the adopted children to their biological parents and their adoptive parents. Call these correlations and , respectively. Twice the biological parent correlation yields the heritability, while the adoptive parent correlation is presumably the environmentality, and any excess variance is due to unshared environment. The second is comparing the correlation of a biological sibling reared apart and the adoptee (call this ), twice which yields , and the correlation of the unrelated sibling reared together and the adoptee (call this ), which yields .
Adoption studies of the first form suffer from several issues, most thoroughly reviewed in Richardson & Norgate (2006). They note that the first form can suffer from severe range restriction issues, issues with selective placement (which can inflate both adoptive and biological parent correlations) and family unit effects. Moreover, both forms of adoptee studies suffer from the issue of confounds from epigenetic inheritance, effects from the prenatal and pre-adoptive environment.
In the face of the growing evidence that family study assumptions are violated: inflating and deflating , some behavioral geneticists have attempted to rebut the criticisms of their studies. Following Mike Stoolmiller’s (1998; 1999) founding reanalysis of adoption data using restriction of range models, behavioral geneticists have lashed back with explanations of why they may not be representative of the fact of the matter (Loehlin & Horn 2000). A study commonly cited to this effect is McGue et. al (2007), which purportedly demonstrates that not only does restriction of range not have a significant impact on the shared environmentality components estimated , but that socioeconomic status itself does not impact IQ. There are several issues here: the first is that McGue’s measures are not good estimates of socioeconomic status (SES) (Lerner 2014) that critics are looking for – the measures were only parental education and occupational status, both of which are known to be imperfect representations of socioeconomic status (American Psychological Association 2006; Lott 2012; Kraus & Tan 2015). Moreover, there are numerous other variables that adopted families could be restricted on, and the issues mentioned above with adoption studies could prevent easy detection of the restriction of range. The second issue here is that their method of testing for variance reduction was to compare to the group of adoptive families in their sample to the group of ‘biological families’ in their sample. That adoptive families are selected is well-known: the impact of this selection on correlations is the issue under contention. However, what they neglected to mention was the fact that their biological sample was also restricted in range: the sample of ‘biological families’ has a much smaller range of environments than that of the general population (Nisbett et. al 2012) . And again, their claim that the lack of correlation between socioeconomic status and IQ in adoptive homes is tenuous for a number of reasons. The first is of course the restriction of range, so to attempt to correlate the restricted range of socioeconomic status on IQ to show that there is no effect of restricted range is quite circular. The second is that the power to detect a correlation is not very high: one can visibly detect that the lowest subgroup that ‘bucks’ the trend of increasing IQ by socioeconomic strata has a large confidence interval . The small sample sizes by socioeconomic strata, along with measurement error in both IQ and socioeconomic status prevent us from concluding anything about the effect of socioeconomic status on IQ. One can notice that the regression coefficient of socioeconomic status on IQ in adoptive families is positive (page 458, Table 4) , but the 95% confidence interval includes zero (likely due to the low power in the study & issues with indices). Overall, their result was not surprising given the small SES-IQ correlations in general, the measurement error of both SES and IQ , poor indexing of socioeconomic status (both in terms of the metrics they used , and in terms of the fact that social class is difficult to reducible to a single number – see above) and other statistical issues and confounds involved  .
Moreover, there is powerful evidence that this restriction of range has an influence on familial correlations (Kaplan 2012). Despite claims otherwise, there is very good reason to believe extended familial studies have greater power to distinguish between confounded variance components (Rao et. al 1976), which universally show smaller estimates (Marcus & Feldman 2018).
A review of the older adoption evidence provides significant support for the idea that environments have profound influences on the mean levels of IQ scores that individuals attain. Responding to a critical review of the literature by Musinger (1975), Kamin (1978) gives a good summary of the magnitude of the effects and the relative contribution of genes and environments they estimate . This older literature was later superseded by the data from the Colorado Adoption Project and the Texas Adoption Project examined in Richardson & Norgate (2006), as above.
The classic Freeman et. al (1928) and Skodak & Skeels (1945) both provide evidence for environmental contribution, but the more recent French studies have been the object of much more debate (see ). Duyme et. al (1999) reports increases of 7.7 and 19.5 IQ points following adoption, dependent on the socioeconomic status of the adoptive home, while Schiff et. al (1982) reports similar figures. . Similar results have been found in Duyme (1988), Dumaret (1985), Schiff et. al (1978) and Weinberg et. al (1992) (see Table 3), as well as Capron & Duyme (1989) (though see Wahlsten 1993), and for a summary, see Schiff & Lewontin 1986. International adoption studies provide another piece of converging evidence that rearing environment does have long-lasting impacts on cognitive function (van Ijzendoorn et al. 2005).
 One might notice that not a single estimate of heritability appears in their article, perhaps for the obvious reason that once computed, it does not comport with the values estimated in the literature on twins. Consider table 4. The estimator for heritability given correlations of unrelated siblings reared together and related siblings reared together is as follows: , . Subtracting these formulae would yield an estimate of . When this estimator for heritability is used, it implies , which is markedly lower than anything reported for twins. Moreover, one might think the figures for DBI ( for biological families and for adoptive families) may not actually produce a significant heritability figure once estimated with a significance test, though I do not wish to go through the calculations here.
 McGue et. al (2007) provide an explanation for their reduction in variance: “This ascertainment criterion will certainly result in a reduction of IQ variance in both adoptive and non-adoptive families, and indeed the IQ standard deviation we observed in our sample of adopted individuals was less than the normative value of 15. “This reduction in IQ variance has, however, nothing to do with range restriction specific to the adoptive families, as evidence by the comparable level of IQ variance we observed in our similarly ascertained non-adoptive sibling sample.” (p. 459, emphasis added). It is not clear how this is supposed to justify the reduction in variance in the adoptive sample: they simply described their process for restricting the range. Of course the fact that they restricted the range of non-adoptive families could provide a similar reduction in the correlation between siblings, this only ameliorates the concern over the relative comparison between biologically-related siblings reared together’s correlation and biologically-unrelated siblings reared together’s correlation, and not over the actual magnitude of the biologically-unrelated siblings reared together’s correlation. It is also empirically unclear whether the statistical conditions for adjusting for restriction of range are justified for one, both or neither of the cohorts, meaning that there can be no meaningful interpretation of these figures. Even more, as noted later, this explanation cannot suffice for the interpretation of the SES-IQ correlations in adoptive families.
 One could also speculate that there are non-random assignments of adoptees to different SES strata that have systematic effects on the correlations, but these are all completely unknown factors. Given the observed characteristics for socioeconomic status for the adoptive families (see footnote 6), there is surely to be a very small sample size for the lowest socioeconomic strata. The further question of how they decided to construct strata and aggregate data to create the graph is unexamined, and correlations following the removal of certain strata to test for possible aforementioned selection effects do not seem to have been performed or reported.
 They report another correlation in Table 5 (p. 459) following correction for the restriction of range, but it is unclear how they obtain estimates of the correlation between socioeconomic status and IQ that are of the opposite sign of those in Table 4 (p. 458). The sample sizes for the regressions in Table 5 are also not given, and the method for age-sex adjustments requires further inspection given the procedure cited was originally developed for twin data and may be inapplicable to adoptee data where dyad effects differ. They state that “the corrected sibling correlations differ minimally from their uncorrected values given in table 4”, which as we have already and are going to examine in more depth, is an incorrect conclusion based on insufficient data, but is also manifestly contradicted by their own reporting. While it is clear that the coefficients for the correlation between IQ and SES in Table 4 and Table 5 will not differ using a t-test, the fact that the sign of the relationship changed directions is evidence that there is something strange going on here. Note that McGue et. al never actually reported the correlation coefficient for the relationship between their socioeconomic status variable and “I”Q, only the regression coefficient, so the figures are statistically incommensurable. As such, the only appropriate comparison is the sign-test, which indicates there is a disparity, and one that makes no sense in light of the mathematics of selection corrections.
 For one, consider that they used different metrics for IQ for adolescents below and above 16: “Adolescent IQ was assessed using an abbreviated version of either the WISC-R (for adolescents age 15 years and younger) or the WAIS-R (for adolescents age 16 or older)” (p. 454) They report sibling age pair differences as 2.4 years in adoptive families and 2.1 years in non-adoptive families (this is significant by a t-test, however it is unclear if the age-sex corrections they mentioned correct for this disparity which would deflate adoptee correlations and inflate non-adoptive correlations due to age effects), but not whether these differ between adoptive and biological dyads, neither do they mention the particular age composition of adoptive and biological dyads, specifically as to whether there were different proportions of non-matching tests: what percent of adolescents (adoptive, biological and altogether) dyads had one sibling take the WAIS-R and one sibling take the WISC-R? These are unknown questions as to how these instruments operate differentially by age or by various environmental factors which prevent us from making firm conclusions. Moreover, they report that they only administered the “abbreviated form consist[ing] of four subtests, two verbal (Vocabulary and Information) and two performance (Block Design and Picture Arrangement), selected because performance on these subtests correlates 0.90 with overall IQ when all subtests are administered,” (p. 454). Why did they not perform the computations throughout the article for each of the four subtests to see if there is issues regarding aggregation, or if there are any selection effects specific to certain abilities?
 For one, consider that the two metrics that they combined to construct the socioeconomic status variable were parental education (both maternal and paternal) and occupational status (both maternal and paternal). We should first note that an entire 60.7% of adoptive mothers were college graduates, and 66.1% of adoptive fathers, in comparison to respective figures of 44.2% and 44.7% for non-adoptive parents. The rapid increase in college graduation for the American populace makes college education a very poor index of socioeconomic status, especially given the range restriction and noise induced due to sampling. The second index used was the Hollingshead classification scheme, which has long been known by sociologists to provide little information into the dynamics of class structure (Duncan & Magnuson 2001; Haug & Sussman 1971a, 1971b; Mueller & Parcel 1981; Rothstein & Wozny 2011). There was no mention of any indices of neighborhood socioeconomic status, schooling quality, or the various other aspects of social class. Additionally, they reported that “[i]n the 617 assessed families, 613 (99.4%) of the mothers and 551 (89.3%) of the fathers were assessed”, meaning that there was differential survey completion by parental sex, especially problematic given the adoptive-parent effects are known to be more salient with regard to fathers (Richardson & Norgate 2006). Further non-reporting for education and occupation present further issues in interpretation.
 Consider for one that their ascertainment involved only adoptive families that had another biological child; “Eligibility requirements for adoptive families included having: … a second adolescent in the home who was not biologically related to the adopted adolescent”. This would ensure that the contrastive effects mentioned by Richardson & Norgate (2006) would occur, deflating adoptee-adoptive parent correlations. They also mention that the second child that is unrelated into the home could also be adopted, “[t]his second child could have been biologically related to one or both of the parents or, like the first child, adopted and placed prior to age 2 years”. They reported that 285 families of the 409 total adoptive families were composed of two adoptive children, presenting an issue when interpreting their corrections of the adoptee-unrelated child correlation from child IQ-parent SES given that the biologically unrelated child may have (doubly) deflated correlations due to prenatal, epigenetic and other effects.
 Another interesting fact is that one can note both the increased age of adoptive parents relative to non-adoptive parents (p. 455, Table 1), and that the standard deviation is lower in adoptive parents, providing evidence for the age effects mentioned by Richardson & Norgate (2006).
 Kamin notes the large increases of IQ for adoptive children in comparison to their counterfactual sibling IQs. The ‘two-realms’ hypothesis wherein the causes of group differences (adoptive group IQ vs biological group IQ) differ from the causes of individual differences (adoptive parent-adoptee correlation vs biological parent-adoptee correlation) has been criticized by Turkheimer (1991) [also see Turkheimer (1990), Locurto (1990), whose paper will have to be the subject of another critical discussion], who suggests that this model is only possible when environmental variation exists solely between groups and not within groups. Stoolmiller (1998; 1999) concurs, stating that the environmental variation may just be restricted so severely as to create the environmental variation existing predominantly between groups. However, the veracity of these claims regarding the falsity of the two-realms hypothesis is uncertain, as Leve et. al (2014) report significant mean increases in achievement and IQ despite near-null correlations of adoptive parent and adoptees. How this can be explained within a model that unifies mean and variance effects is beyond me, though this is a question for those who think in behavioral geneticists obscurantist terminology. A possible explanation is that there exist environmental influences on IQ that do not covary with parental IQ in a way that is detectable, or at all. Another more parsimonious explanation would be to adopt the view that adoptive parents have unique dyadic relationships with their children that decreases similarity (Richardson & Norgate 2006).