The article by Serge Lang (1993) in this journal on the Baltimore case is, I believe. a major contribution to the understanding of that extremely complex and important case. Lang's views on matters of ethics and scientific responsibility are generally in close accord with mine. On one point. relating to myself, I will offer a correction of a perfectly natural. and indeed flattering. inference that he has drawn concerning my conduct. Like him, I now strongly support the validity of Margot O'Toole's challenge that called for a published correction to the disputed paper in Cell (Weaver et al., 1986) and thereby initiated the controversy that remains officially unresolved.
In early April 1988, Representative John Dingell invited me to testify at the April 12th hearings of the House Subcommittee on Oversight and Investigations, of which he was and is chairman. I agreed to testify. The transcript of these hearings was later published under the title Fraud in NIH Grant Programs (U.S. Congress, 1988). (I comment later on this title.) I had had experience in these matters. Part of my testimony concerned several cases of fraud that I had encountered when I was editor-in-chief of the Journal of Biological Chemistry; (1958-1967). I also discussed the great risks to which responsible whistleblowers expose themselves when they challenge higher authority to protect the public interest (U.S. Congress. 1988. pp. 145-151. 163-170). I had become well aware of these problems when I served as a member. and for 2 years as chairman. of the Committee on Scientific Freedom and Responsibility of the American Association for the Advancement of Science (1976-82). Help and support for whistleblowers who appeared on investigation to have acted responsibly in the public interest was one of the major concerns of that commitee.
In his discussion of the Baltimore case, Lang (1993, p. 43) quoted a passage from my testimony at the hearings, which reads as follows:
If a young scientist believes that he or she has witnessed a case of fraud. and comes to ask me about reporting it to the authorities, I would have to warn him or her emphatically about the dangers of doing so. If the potential whistlebiower decided nevertheless to proceed, I would admire and greatly respect the person and the decision, but I would have serious anxiety about the future of that individual. as the system operates today. (U.S. Congress. 1988. p. 149)Lang (1993. p. 43) quite naturally infers from this passage that I spoke with Margot O'Toole in mind, and that therefore I "was one of the earliest scientists to speak out" on her behalf. Lang is generous to me in drawing this inference. but he bestows on me an honor that I do not deserve. It is quite likely that the thought of Dr. O'Toole's predicament passed through my mind as I spoke. but in fact my failure to mention her name in my testimony was due to a clear and conscious decision. From the beginning I had become convinced that she was a very honest person, but from the virtual unanimity of the senior people at Tufts and the Massachusetts Institute of Technology (MIT). who told her she was wrong or that her concerns were trivial, I was, at that time, led to wonder if she had somehow failed to comprehend the scientific issues involved. I was still troubled and uncertain about the situation, and chose to say nothing about her when I spoke, although I was well aware of the case.
Lang's perfectly natural misunderstanding of my attitude at that time led me to reexamine the transcript of those hearings, to reread copies of some letters I wrote after the hearings, and to recall an important telephone call from David Baltimore. All this reinforced my present support of Dr. O'Toole, but it has also revived some serious concerns of mine concerning the conduct of the 1988 Dingell hearings. I indicated some of these concerns briefly in an earlier article (Edsall, 1991), (See also Greenberg (1991). These two articles were sharply attacked in a letter in the November 1991 issue of the Journal of NIH Research (vol. 3), from J. Press and D. Parker, p. 12, with rebuttals from M. O'Toole, D. S. Greenberg, and J. T. Edsall, pp. 13-14) but they call for a fuller explanation here.
By 1988 I had been in close touch with Ned Feder and Walter Stewart for some years during their controversial activities at the National Institutes of Health [NIH], concerning scientific misconduct. I supported them vigorously in their long fight to publish a paper on the sloppy deviations from sound scientific practices by various listed coauthors of papers by the fraudulent John Darsee, and on the associated deficiencies of some of the reviewers of these papers. Threats of lawsuits against both authors and publishers blocked acceptance of the manuscript for a few years. The disputed paper was finally published (Stewart & Feder, 1987) after the authors agreed to some deletions. I consider it an important contribution to the promotion of honesty in doing and reporting scientific work.
Feder and Stewart then clashed with David Baltimore in a dispute over the validity of the controversial data in the Cell paper. I followed the controversy with concern and for some time found it difficult to judge who was right. I read the disputed paper; dealing as it did with the idiotypes of antibodies induced by the injection of a transgene into developing mice, it was well outside my area of real competence in science.
I had been involved in controversies before, and had relished the involvement; I clearly understood the issues involved and knew unequivocally which side I was on. In this case I hesitated to conclude whether David Baltimore was right or wrong in refusing to turn over the relevant laboratory records for Feder and Stewart to examine in connection with their inquiry. He refused, on the grounds that they were incompetent, being nonexperts in immunology, to judge the disputed evidence and therefore did not deserve access to his records, with all the trouble and loss of time that providing such access would cause him and others in his laboratory. Thinking what I would do under similar circumstances, I remained undecided. This, I think, is a fairly accurate description of my attitude at the time. Even now I consider that there are ambiguities in such situations and that no simple rule will decide the answer.
However, Feder and Stewart refused to be intimidated. They put themselves through a sort of "crash course" in the relevant areas of immunology and studied the aspects of the published paper that Dr. O'Toole had challenged, comparing them with the 17 pages of laboratory records by Dr. Moema Reis -- one of the coauthors of the Cell (1986) paper, a copy of which O'Toole had provided to them. They became convinced, as she had. that major claims in the published paper were incompatible with the original laboratory records, even though the 17 pages, in a distorted form, clearly formed the source for much of the disputed material in the paper. Lang (1993, pp. 13-22, 31-34) described in detail the ultimately successful efforts of Feder and Stewart to persuade NIH to let them submit the resulting paper for publication and the later decisions by the editors of Cell, Science, and Nature to decline the paper. Lang (1993, p. 31) sharply criticized these adverse editorial decisions as "a closing off what should have been the natural channels of scientific criticism and exchange," and I must essentially agree. In particular. the editor of Cell had a special responsibility in these matters because it was in his journal that the paper with the original claims appeared. If competent referees could not produce clear evidence that the claims of Stewart and Feder were wrong. then publishing their paper and letting the scientific community judge the evidence would have been the sound thing to do. I should add that at that time I was not paying close attention to these events and did not try to influence what was going on. One must note, of course, that their paper, somewhat shortened, eventually found publication in Nature (Stewart & Feder, 1991), but that was after so much else had come to light that its added impact was comparatively small.
Baltimore (1989) set forth in detail his own outlook on these and other matters. He made important comments on some of the problems of scientific researchers today, which deserve attention and thought. However, as I point out later, I must disagree with him on central matters that lie at the heart of this case.
Two days before the Dingell hearings, on the evening of Sunday, April 10, 1988. David Baltimore -- with whom I was on friendly terms, though we were not close friends -- called me in a state of intense indignation. Peter Stockton, an important member of the Dingell subcommittee staff, had been in Boston earlier in the week and had talked to several reporters about the case. This resulted in an article on the upcoming hearings that appeared that day in the Boston Globe. It drew on Stockton's statements and included strong intimations that fraud might be involved. David's outrage was understandable to me, for even Margot O'Toole herself had not charged fraud at that time. He asked me to help set matters straight (as he saw them) when I was at the hearings. I promised nothing but understood his concern.
In retrospect I note that if I had indeed planned to testify on behalf of Margot O'Toole at the hearings, it would have been my moral obligation to inform David of that fact as soon as I realized what he was calling about. Because I had no such intention, that issue did not arise. In view of Lang's perfectly natural misunderstanding of the implications of what I said at the hearings, I emphasize my concern on this point.
At the hearings, as I have indicated above, I made no attempt to discuss the Baltimore case. I did continue to ponder what had occurred. A few weeks later, on May 23, 1988, I wrote to John Dingell, with a mixed message. First, I gave strong praise to his efforts toward exposing fraud, with emphasis on his hearing on the case of Robert Sprague, who had exposed the false claims of Stephen Breuning in the face of formidable obstacles (as discussed later in this article).
Regarding the testimony of Margot O'Toole, I wrote to Dingell:
At the time I found Dr. O'Toole very difficult to hear; she spoke in a low voice, and I am slightly deaf. l have now seen the written transcript of the testimony. She impresses me as a person of scrupulous honesty I do not read her testimony as involving any charge of fraud. The issue as she states it is a question of error in the published findings, and of unwillingness to admit error on the part of Dr. Imanishi-Kari.In this same letter I expressed particular concern because none of the authors of the Cell paper were invited to attend the hearings or given the opportunity to testify or answer questions. Only the two critics, O'Toole and Maplethorpe, were present and testified, and only Maplethorpe was actually charging fraud. I asked: "Were any of them [the authors] invited? Even though this was a hearing, not a court case, it [i.e. the failure to invite them] seems like a violation of due process." That matter still troubles me. I should add that I never received a reply from John Dingell to this letter. In May 1989, as we all know, he did invite David Baltimore to speak on behalf of the authors, and Baltimore -- as the scientific world knows -- responded vigorously.
What later troubled me even more than the exclusion of the authors was that the transcript of the hearings, when it appeared, bore at the top of its cover page, in large letters, the heading Fraud in NIH Grant Programs. The hearings involved two major cases: the Baltimore case and the case of Professor Robert Sprague, who had charged his former coworker, Stephen Breuning, with fraud in publications concerning the use of drugs in the treatment of retarded children. In this case there was a clear verdict, after a thorough investigation by an appointed panel of the National Institute of Mental Health, that Breuning had made false claims in these papers-claims that, in fact, had probably misled at least some clinicians who were caring for retarded children. Indeed, Breuning had actually confessed to fraud in at least one instance.
At that time there was a sharp contrast between the status of the Sprague case and the Baltimore case. In the former, there had been a thorough investigation by an appointed panel and a clear verdict, as well as Breuning's confession. In the latter there had been as yet no such investigation; the authors of the Cell paper had had no opportunity to testify, and Dr. Maplethorpe was the only witness who actually charged fraud. To bring these two cases together under the general heading of "fraud" was in my opinion decidedly improper.
Dingell's actions forcefully aroused David Baltimore. He and his supporters soon went into action, calling on the scientific community to mobilize and fight the threat to its autonomy presented by the aggressive Dingell subcommittee. A great number of scientists joined the attack and wrote letters vigorously protesting the subcommittee's conduct, as Lang (1993, pp. 26-29) described. I could understand why David responded as he did, though I thought he was making a serious mistake. Increasingly, I fell out of sympathy with the ferocity of his challenge and with the organized outpouring of letters of protest to the Dingell subcommittee from scientists who did not really understand the complexities of the case.
When I look back on John Dingell's conduct in this whole affair, my verdict is mixed. After the inadequacy of the attempts at Tufts and MIT to come to grips with Dr. O'Toole's call for a correction to the published paper, I believe that Dingell performed a great service in making a forum available in which she could set forth her case and receive a public hearing. Yet Dingell's failure to enable the authors of the disputed paper to respond, and his use of the term fraud where no fraud had yet been established served to polarize the debate and made the backlash more intense. Of course, Dr. O'Toole herself had not sought any such confrontation; I think she behaved with admirable dignity, both then and later. Still, part of the hostility toward John Dingell that his procedure had aroused among many scientists spilled over onto her and made her, too, seem like an enemy to some of them.
Thus my total judgment on Dingell's behavior is complex. On balance I think he did a major service in saving Margot O'Toole from scientific oblivion, but part of the gain from this important action was undone by actions that increased the polarization between the contending sides. However, the later intense attack on the Dingell subcommittee by a considerable fraction of the scientific community, including some of its eminent members, increased the polarization even more. I felt it to be a decidedly misguided response.
A major turning point in my outlook came when I read Dr. O'Toole's testimony in the May 1989 hearings (U.S. Congress, 1989 pp. 180-188, 189-202, 203-208, and later passages). I was not present at those hearings, and I did not read the transcript until some time later, when Professor Lang reprinted it along with David Baltimore's statement (already cited) of his views on the case (Baltimore, 1989). To me, O'Toole's words carried conviction, even more powerfully than in her testimony of the year before. When I looked up the full text of the 1989 hearings and read the testimony of her critics and the questioning that followed, I concluded that her words carried greater weight and authenticity than those of her critics. It became clear to me that her original call for a published correction to the Cell paper came only after Dr. Imanishi-Kari admitted to her that the original records supporting the data in the challenged table simply did not exist. O'Toole asked her if she had other records of experiments that would establish the findings in question. If so, she said, she would withdraw her call for a correction; but Imanishi-Kari could not produce such data. So Dr. O'Toole persisted in her call, and was met by the stubborn rejection of senior investigators at Tufts and MIT.
All of them told her that her objections were trivial and hardly worth even a footnote of correction. They advised her, for her own good, to drop the matter. To me, looking back on the case today, it seems obvious that what was lacking was a thoughtful review by outside independent experts who would look closely at the data in the published paper and at the corresponding evidence -- or lack of evidence -- in the laboratory records. They could report on the validity, or invalidity, of Dr. O'Toole's criticisms, free of personal involvement. That sort of review was to be provided later by NIH, as I note below, but only after the Dingell subcommittee hearings.
Here I come to the fundamental issue, which puts me squarely on the side of Dr. O'Toole. I believe that if you have published accounts of experiments that you later find good reason to doubt, it is your responsibility to inform the scientific public of that fact. Otherwise, other researchers may waste their time following false leads. Of course, you may want to repeat the experiments first. If you do so promptly, and if they confirm the earlier work, you need do nothing further. But in this case there was a very serious reason for corrective action. The supporting evidence in the laboratory records did not exist! At least, Dr. Imanishi-Kari could not produce such evidence.
David Baltimore, however, believed that the results O'Toole had challenged were in fact essentially correct, that they had been published in good faith and with no fraudulent intent. Apparently on this basis he judged that there was no need to publish a correction; the published findings, he said, would be tested in other laboratories, which would either support them or lead to their rejection. Such a process, of course, would certainly go on, but O'Toole believed, as I do, that this attitude constituted an abdication of scientific responsibility because it failed to warn other workers that the findings were in doubt. (On this matter, see the important letter from Paul Doty, 1991, in Nature. )
The NIH, acting through the Office of Scientific Integrity (OSI), had set up a panel, headed by Dr. Joseph Davie, to examine the case. In the spring of 1989 the panel reported its findings. They supported Dr. O'Toole's request, made 3 years earlier for a retraction of the challenged table, but the panel accepted Dr. Imanishi-Kari's offer to replace it by other data that she submitted. This, however, did not settle the case, for O'Toole, on examining these data, raised serious doubts of their validity. This led to the action of the Dingell committee in calling upon the Secret Service to examine ImanishiKari's notebooks for evidence of possible falsification, and to a further investigation by an enlarged committee under the OSI.
This committee produced a draft report in April 1991 that was submitted for comment and criticism to all those involved in the controversy. Drawing largely on data from the Secret Service, it concluded that Dr. Imanishi-Kari had altered a number of laboratory records she submitted, and charged her with fraud. The report also gave high praise to Dr. O'Toole for her courage and steadfastness in maintaining and presenting her conclusions regarding the case over several years and under difficult circumstances. It cleared Dr. Baltimore of any involvement in fraud but criticized him severely for failing to deal, at the beginning and within the group, with O'Toole's charges because an early critical review of the situation, perhaps leading to some further experiments, might have prevented all the later conflicts.
The draft report was intended to be confidential, and was sent to the participants in the controversy for review and rebuttals. If this process had worked as was intended, their comments would have gone back to the OSI committee, which would then have prepared a final report. Unfortunately, the draft was soon leaked to the press, which gave it wide publicity because of the dramatic vindication it would have provided for Dr. O'Toole if it had been a final report.
This leak, of course, was gravely improper. As a result of it, the process of review was brought to a halt. I will not attempt to describe the complicated series of events that followed, but the crucial major event, as it related to the Baltimore case, was the abolition of the OSI and its replacement by a new organization, the Office of Research Integrity (ORI). The ORI was placed outside NIH, though within the Department of Health and Human Services. Although the ORI has had the case under consideration since late 1991, no public action to resolve it has yet been announced. Thus, 8 years after the dispute arose, its outcome remains in limbo so far as the work of official investigative bodies is concerned.
By the summer of 1992 I had concluded that it was time to take an explicit public stand on Dr. O'Toole's behalf and not wait for the completion of the official investigations. Paul Doty joined me in nominating her for the Ethics Award of the American Institute of Chemists (AIC). In due course she received this award at the AIC meeting of March 12, 1993, in New Brunswick, New Jersey. She invited me to accompany her to the meeting and introduce her on that occasion. This I was happy to do. What she and I said on that occasion has been recorded (Edsall, 1993; O'Toole, 1993).
I conclude by noting that 8 years after this controversial case began. it still remains in the hands of the ORI, and no indication of impending resolution is yet apparent. My support remains with Margot O'Toole, but I still express sympathy, though not support, to David Baltimore and Thereza Imanishi-Kari for the long ordeal that all three of them have had to face.
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Edsall, J. T. (1993). Introduction of Margot O'Toole [for her Award Address. American Institute of Chemists], The Chemist, 70, (8). 17.
Greenberg. D. S. (1991). Science's mentality on misconduct, Journal of NIH Research, 3, 32-33.
Lang, S. (1993). Questions of scientific responsibility: The Baltimore case. Ethics & Behavior, 3, 3-72.
O'Toole. M. (1993, March 12). Collegiality among scientists [American Institute of Chemists, Ethics Award Address]. The Chemist, 70, (8), 18-19.
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