Modgil & C. Modgil (eds.). (1984). Arthur Jensen: consensus and controversy. Lewes, Sussex, Falmer Press

In a book that's not widely-read but should be, Thomas Bouchard notes in his chapter (The Hereditarian Research Program: Triumphs and Tribulations):

A principal feature of the many critiques of hereditarian research is an excessive concern for purity, both in terms of meeting every last assumption of the models being tested and in terms of eliminating all possible errors. The various assumptions and potential errors that may, or may not, be of concern are enumerated and discussed at great length. The longer the discussion of potential biasing factors, the more likely the critic is to conclude that they are actual sources of bias. By the time a chapter summary or conclusion section is reached, the critic asserts that it is impossible to learn anything using the design under discussion. There is often, however, a considerable amount known about the possible effect of the violation of assumptions. As my colleague Paul Meehl has observed, ‘Why these constraints are regularly treated as “assumptions” instead of refutable conjectures is itself a deep and fascinating question…’ (Meehl, 1978, p. 810). In addition, potential systematic errors sometimes have testable consequences that can be estimated. They are, unfortunately, seldom evaluated. In other instances the data themselves are simply abused. As I have pointed out elsewhere:
The data are subgrouped using a variety of criteria that, although plausible on their face, yield the smallest genetic estimates that can be squeezed out. Statistical significance tests are liberally applied and those favorable to the investigator’s prior position are emphasized. Lack of statistical significance is overlooked when it is convenient to do so, and multiple measurements of the same construct (constructive replication within a study) are ignored. There is repeated use of significance tests on data chosen post hoc. The sample sizes are often very small, and the problem of sampling error is entirely ignored. (Bouchard, 1982a, p. 190)
This fallacious line of reasoning is so endemic that I have given it a name, ‘pseudo-analysis’ (Bouchard, 1982a, 1982b). Pseudo-analysis has been very widely utilized in the critiques and reanalyses of data gathered on monozygotic twins reared apart (cf. Heath, 1982; Fulker, 1975). I will look closely at this particular kinship, but warn the reader that the general conclusion applies equally to most other kinships. Perhaps the most disagreeable criticism of all is the consistent claim that IQ tests are systematically flawed (each test in a different way) and, consequently, are poor measures of anything. These claims are seldom supported by reasonable evidence. If this class of argument were true, one certainly would not expect the various types of IQ tests (some remarkably different in content) to correlate as highly with each other as they do, nor, given the small samples used, would we expect them to produce such consistent results from study to study. Different critics launch this argument to different degrees, but they are of a common class. [Continued in the piece]

In modern language, we might say that critics engage in motivated p-fishing in the data (goal: minimize genetic effects), and then engage in selective reporting and interpretation of the results (report comparisons and their p values when they favor the goal, otherwise leave out). The two original writings from Bouchard are:

Bouchard, T.J., Jr (1982a) [Review of The Intelligence Controversy], American Journal of Psychology, 95, pp. 346–9. PDF
Bouchard, T.J., Jr (1982b) ‘Identical twins reared apart: Reanalysis or Pseudo-analysis’,[Review of Identical Twins Reared Apart: A Reanalysis], Contemporary Psychology, 27, pp. 190–1.

The second paper is tough to get. Here's the fulltext:

Identical Twins Reared Apart: Reanalysis or Pseudo-analysis?

Thomas J. Bouchard Jr.

Susan L. Farber is assistant professor in the Department of Clinical Psychology at New York University.

Thomas J. Bouchard, Jr., is professor of psychology at the University of Minnesota (Minneapolis). His research interests are in the areas of differential psychology, behavior genetics, and industrial organizational psychology.

Product: Identical Twins Reared Apart: A Reanalysis Susan L. Farber New York: Basic Books, 1981. 399 pp. $26.50

History: PsycINFO ReleaseDate: 20-11-2006; PsycCRITIQUES ReleaseDate: 20-11-2006

Abstract

Reviews the book, Identical Twins Reared Apart: A Reanalysis by Susan L. Farber (1981). This book attempts to pull together in a single place all of the data available on identical twins separated early in life and reared apart (MZA twins). It is a Herculean effort that few would have the courage to attempt. Twenty-five percent of the book deals with IQ. This is the most controversial topic covered and the one least satisfactorily dealt with. My general impression is that the compilations are dependable and a good starting place for someone working in a specialized area. Most of the conclusions are consistent with my understanding of the areas (an understanding that is sometimes limited, eg., in the areas cancer, circulatory system disorders, etc.). (PsycINFO Database Record (c) 2017 APA, all rights reserved)

Keywords

identical twins; intelligence quotient; cancer; circulatory system disorders; child rearing

This book attempts to pull together in a single place all of the data available on identical twins separated early in life and reared apart (MZA twins). It is a Herculean effort that few would have the courage to attempt. The author has arranged the data in a logical fashion. There is an introductory chapter that deals with methodological issues (biases, design problems, etc.), a chapter that reviews prior studies, a chapter that describes the entire population of such twins and assigns them case numbers, and chapters on physical traits, physical symptoms and disorders, psychosis, IQ, personality, and a summing up. Twenty-five percent of the book deals with IQ. This is the most controversial topic covered and the one least satisfactorily dealt with. Consequently, I will devote most of the review to it, with the expectation that other reviewers will focus on different topics.

Farber's approach to the analysis of the IQ portion of this data set is akin to the approach of Leon Kamin (1974). The data are subgrouped using a variety of criteria that, although plausible on their face, yield the smallest genetic estimates that can be squeezed out. Statistical significance tests are liberally applied and those favorable to the investigator's prior position are emphasized. Lack of statistical significance is overlooked when it is convenient to do so, and multiple measurements of the same construct (constructive replications within a study) are ignored. There is repeated use of significance tests on data chosen post hoc. The sample sizes are often very small, and the problem of sampling error is entirely ignored. It cannot be argued strongly enough that significance tests simply do not protect against drawing false conclusions when post hoc procedures are used. The results seriously abuse statistical theory and reinforce the widespread belief that scientists can prove (or disprove) anything with statistics. In sum, the treatment of the IQ data is an exercise in obfuscation. Perhaps this new approach needs a name. I suggest the term "pseudo-analysis."

This approach should be contrasted with the rapidly developing methodologies of meta-analysis introduced by Glass and colleagues in educational psychology (1981), and Hunter, Schmidt, and colleagues in industrial/organizational psychology (1981). For years reviewers in both domains bemoaned the inconsistency of findings and postulated innumerable moderator effects. It is now known that the conflicting results are most often artifactual. That is, they depend entirely on such artifacts as sampling error, differing quality of measurement from study to study, differing reliabilities, and so forth. The meta-analyst depends heavily on pooled data and the idea of constructive replication.

The literature on the IQs of monozygotic twins reared apart (MZAs) is unique in that almost all the actual IQs are available (often on more than one test). Farber has prepared a table with MZA twins ordered by degree of separation. Group I is made up of Highly Separated cases (n = 45). Group II is composed of Mixed Separation cases (n = 23). Group III consists of Little Separation cases (n = 27), and Group IV includes twins separated after four years (n = 11). The table lists (when available) sex, handedness, birth weight, birth order, age of separation, knowledge of twinship prior to reunion, age learned of twinship, age met, age seen by investigator, a measure of contact over four developmental periods, years apart and degree of contact, rearing status (parent, relative, other), and reference for case. It is an extremely useful table. Later in the book the same ordering is used to report twin IQs. I was somewhat surprised and distressed to find that the author chose not to include Otis IQs for the Newman, Freeman, and Holzinger sample, nor did she include the Raven raw scores for the Juel-Nielsen sample. The point is not minor. Both Farber and Kamin have criticized the Stanford-Binet used by Newman, Freeman, and Holzinger. The Otis gives almost the same intraclass correlations and means as the Stanford-Binet, however (ri = .74, mean = 97.16, SD = 13.58 for Otis; ri = .68, mean = 95.68, SD = 13 for the Stanford-Binet). Multiple measurement thus reveals that the criticisms of the Stanford-Binet data are simply spurious. The same story applies to the Juel-Nielsen data. Farber cites Kamin regarding problems of standardization of the Wechsler-Bellevue test (W-B) in Denmark. The Raven scores, however, when transformed to IQ equivalents using Raven's percentile table "where the raw score values have been noted with the corresponding probit-values (with regard to age grouping)" yield a twin correlation of .73, the Raven IQ and W-B IQs correlate .82. Again, two different tests, based on different norms, give very similar results. The criticism of the single test is thus shown to be spurious. Farber, like Kamin, makes a variety of criticisms of the Dominoes and Mill-Hill used by Shields. Shields (1978) in his last publication before he died defended himself well against a number of unjustified accusations, and I will not repeat his arguments here. I will show below that Shields's results are so comparable to that of the others that these criticisms must also be considered spurious.

The overall analysis of the IQ data yields the following results: ri = .75, mean 96.8, SD = 12.8. This set of data is, however, considered by Farber to be biased in a variety of ways—principally by contamination due to contact. This problem is treated in two ways. The first involves analysis of all of the cases. An analysis of variance (A-Sex; B-Degree of Contact, 9 levels; A X B; C-Pairs; D-Individuals) was conducted on the Verbal, Performance, and Full Scale IQ scores. A second analysis with a second measure of separation was also used. The results of both analyses are shown in a table where intraclass correlations are given with and without "separation" taken into account. This table is a masterful example of the ignoring of significance tests when they are inconveniently insignificant. In 13 out of 18 significance tests, separation has no effect. For the combined sexes separation has no statistically significant effect for Verbal, Performance, or Full Scale IQ. A similar misleading analysis is carried out on a "PURE" sample (one significant effect out of six statistical tests).

By this point I was persuaded that separation probably had little or no effect on similarity between twins. I decided to calculate intraclass r's for the Highly Separated group for whom I had expected to find an analysis but had not. The results were surprising! For the entire group: n = 39, ri = .76, mean = 97.42; SD = 14.28. For the females: n = 26, ri = .76, mean = 97.96, SD = 14.29. For the males: n = 13, ri = .76, mean = 96.35, SD = 14.20. The three arrays show the slight depression in IQ characteristic of most twin samples, a standard deviation comparable to the normative population, identical intraclass r's that are indistinguishable from the full sample where separation is ignored (full sample males, n = 32, ri = .74; females, n = 50, ri = .76; combined sex, n = 82, ri = .75). If we drop the Shields data over which the author frets so much, the results are the following: n = 28, ri = .78, mean = 99.36, SD = 14.94. Notice that the correlation goes up, not down. The Highly Separated group mimics the full sample perfectly. The inclusion or exclusion of the Shields data makes no difference whatsoever.

Farber, in her introductory chapter, quotes Fuller and Thompson regarding the limited contributions of statistical methodology to our understanding of the genetics of behavioral traits. She then concludes, "My own evaluation, particularly of the allegedly scientific analyses made of the IQ data, is more caustic. Suffice it to say that it seems that there has been a great deal of action with numbers but not much progress—or sometimes not even much common sense."

Unfortunately analyses of the IQ scores in this book consist of the following: a great deal of action with numbers (there are 70 tables, graphs, and figures dealing with IQ); retrogression as opposed to advance in our understanding; inferences either flatly wrong or nonsensical; conclusions widely at variance with what we know about intelligence and IQ tests, irrespective of the MZA data.

The IQ correlation between MZA twins is between .75 and .80 and is probably not influenced by most of the so-called artifacts bandied about by critics of this literature. McNemar (1938) predicted precisely these values in his review of the very first MZA study when he corrected the Newman, Freeman, and Holzinger data for age and range—Binet .767, Otis .796.

I have passed a harsh but, I believe, a fair judgment on the IQ analysis. What about the remaining topics? My general impression is that the compilations are dependable and a good starting place for someone working in a specialized area. Most of the conclusions are consistent with my understanding of the areas (an understanding that is sometimes limited, e.g., in the areas cancer, circulatory system disorders, etc.). In the personality area Farber suspects that "twins who had the least opportunity to influence each other were the most similar." Although reported elsewhere by others, this is a daring conclusion, and there is a suggestion in our own data that this may be confirmed.

The case index, subject index, and name index are excellent. The bibliography is good, but not excellent. The best single reference on primary bias in twin studies (Price, 1950) is not cited.

This is not the definitive work on identical twins reared apart, and because of the flaws outlined above I cannot recommend it as an introduction to the topic area. It will, however, serve as a useful resource for specialists in the area of twin studies.

References

G. V. Glass, B. McGaw, & M. L. Smith Meta-analysis in social research. Beverly Hills: Sage, 1981.
J. E. Hunter, F. L. Schmidt, & G. B. Jackson Integrating research findings across studies. In conference paper. Methodological innovations in studying organizations. Greensboro, North Carolina: Center for Creative Leadership, March 1981.
L. Kamin The science and politics of IQ. New York: Erlbaum, 1974.
B. Price Primary bias in twin studies: A review of prenatal and natal difference producing factors in monozygotic pairs. American Journal of Human Genetics. 1950, 2, 293–352.
J. Shields. MZA twins: Their use and abuse. In W. Nance (Ed.), Twin research psychology and methodology. New York: Liss, 1978.

Missing in original but:

McNemar, Q. (1938). Special review: Newman, Freeman, and Holzinger's Twins: a study of heredity and environment. Psychological Bulletin, 35(4), 237–249. https://doi.org/10.1037/h0055700

Just Emil Kirkegaard Things

Thomas Bouchard on pseudoanalysis