Sibley and Ahlquist claimed in 1984 and 1987 to have proved genetically and statistically that humans, chimps, and gorillas, widely regarded as genetically equidistant from one another, were actually not. Rather, they asserted that humans and chimps w ere genetically more similar, and were each others' closest relatives. They were under the same obligations as any scientist: to prove that their conclusions were sustained by their data. In their 1990 paper (J. Mol. Evol., 30:202-236), Sibley et al. acknowledged that the conclusions of their earlier papers had been derived with the use of unreported analytic procedures: had it not been for these data alterations (in their own words) "... it is virtually certain that Sibley and Ahlquist would have concluded that Homo, Pan and Gorilla form a trichotomy" (p. 225).

The alterations were made without consistent objective criteria, as I have exhaustively detailed (Am. J. Phys. Anth., 85:207-219, 1991). The one they used most extensively involved constructing a bivariate plot of their data points, deciding (based on unclear criteria) that 40% of their data constituted aberrant outliers, and (in their words) "moving the aberrant point to the linear regression ... and calculating the new ... value." (1990, p. 232). This is fundamentally illegitimate, especially since they treated their data points as statistically independent in their papers, and neglected to inform readers that they had performed these data transformations. It is difficult to imagine that the papers would have been published had these data analysis procedures been specified.

Roy Britten's circumlocutions do not make the alterations any more legitimate. Indeed, the reason the alterations came to light at all was that Britten, in possession of the only data provided to anyone by Sibley (who had steadfastly refused many requests by many scholars), passed them on without having noticed their problematic nature. The alterations and their illegitimacy, however, were recognized by the fearful post-doc who removed his name from the work (Science, 241:1758, 1988); and by Vincent Sarich, Carl Schmid, and myself (J. Hum. Evol., 17:769, 1988; Cladistics, 5:3, 1989). This leads to the conclusion that the Sibley-Ahlquist data did not actually resolve the trichotomy at all, and were misrepresented as having done so.

Now, was the misrepresentation deliberate? In the best case, the research would be characterized methodological poverty; the omission of the vital information would be coincidental; and the refusal of the authors to allow others to see their data would also be coincidental. In the worst case, they knew exactly what they were doing, the omission was required to conceal the illegitimate analysis; and the sequestering of information was required to conceal the omission of the alteration procedures from the published papers.

The best light in which their work could be cast would be that they "got the right answer", and their conclusions were simply a matter of overzealous prophecy, rather than simple charlatainerie. Even if this were true, it would be irrelevant to evaluating the nature of the data alterations. The larger problem is that this argument places a premium on the conclusion, rather than on the rigor of the data collection and analysis. It reaches its most extreme form in Jeffrey Powell's "replication" of their altered numbers, measuring a non-comparable variable.

One reason to be skeptical of this is Powell's assertion that the "particulars" of the data analysis by Sibley and Ahlquist are of little concern, since they were used in obtaining the correct conclusion. The nature of their data, the methods of analysis, and their subsequent representations in the literature are the central issues; and I am hopeful that few readers will concur that the end ever justifies the means in scientific research. Valid scientific work cannot be conclusion-driven, contrary to Powell's assertion. It carries obvious consequences for the quality of both research and mentorship. It stands to reason that if we need not worry about Sibley's methodology, we need not worry about Powell's methodology either. Unfortunately, some of us do. Quite possibly the decline in popularity of DNA hybridization among mainstream scientists, noted by Kirsch and Krajewski, reflects an appreciation that in this field, "anything goes" methodologically, in generating the "right" answer.

Ultimately the issues center around data falsification, its exposure, and its concealment. Sibley and Ahlquist used covert techniques to alter their data, which they and their supporters can only justify by recourse to the conclusions of other researchers. That is not, and cannot be, a validation of their methodology; it is a non-sequitur.

But is there indeed a genetic concordance favoring human-chimp, as Sibley and Ahlquist concluded, thought their data didn't actually show it? Obviously, if the split among humans, chimps, and gorillas is so close as to be effectively a three-way split, any specific genetic study may randomly appear to link any two of the three genera. There are two classes of data bearing on this problem: (1) those that do not permit any clear bifurcation to be drawn; and (2) those that clearly link two of the three as closest relatives, and contrast with other studies clearly linking a different two of the three. I recently reviewed this literature (Curr. Opin. Genet. Dev., 2:883-889, 1992), and interested readers can find comprehensive references therein. Czelusniak and Goodman cite only their own data and ignore the rest. This is not scholarly, but coming as it does in defense of the work of Sibley and Ahlquist, it sadly does not seem inappropriate.

The scientific issue is that reviewers and readers of Sibley and Ahlquist's papers were misled about the analysis of the data and consequent robustness of the conclusions. That has been public knowledge for several years. The social issues are less clear cut: what to do, who should do it, and to whom it should be done -- which is why I raised it in my review of the books on misconduct. For Sibley's "illegally importing bird parts taken abroad in violation of foreign wildlife laws", I refer readers to the published account (Sports Illustrated, 24 June 1974), which appears to have been of greater concern to falconers than to molecular evolutionists. If I overreached, I extend my apologies to the American Scientist and stand duly chastised.

As for motives and self-interests, I choose not to speculate on those of the correspondents, and I hope that unless The Amazing Kreskin writes in, no one will be distracted by their speculations about mine.

Jonathan Marks
Department of Anthropology
Yale University