Reprinted from the journal
Ethics and Behavior
Vol. 3 No. 1 (1993) pp. 3-72

Serge Lang
Mathematics Department
Yale University

In 1991, I was invited by the Division of Professional Relations of the American Chemical Society to participate in and give a talk at a symposium, "Whistelblowers, Advocates, and the Law", at their annual summer meeting. Although I could not go, Grace Borowitz (who chaired the Symposium) invited me to publish an article in a monograph containing the proceedings of this symposium, to be published by the ACS.

I submitted my paper in September 1991. However, ultimately, the ACS decided not to publish the book. Grace Borowitz then tried to have the book published by the American Association for the Advancement of Science (AAAS), which also rejected the proposed book, after prolonged correspondence and three reviewers.

I updated the paper throughout the subsequent year, for possible publication elsewhere. The scientific community is indebted to Gerald Koocher for publishing the article in Ethics and Behavior. I also thank him personally. I submitted a table of contents for the article, but the publisher and editor did not allow it. This table of contents has been reinserted here.





§1. How the Baltimore case arose: Margot O'Toole
§2. Conflicting versions: The Tufts Ad-Hoc Committee, Herman Eisen at MIT, and David Baltimore
§3. The "17 pages" and the intervention of Stewart-Feder. The issue of publication


The responsibility of answering questions about one's work
The responsibility whether to submit to authority


§1. The NIH panel
§2. The OSI Draft Report


§1. Attacks on the Dingell Subcommittee
§2. Congressional responsibility and scientific responsibility


§1. Failures of the establishment press
§2. Closing ranks
§3. The legalization of scientific responsibility?
§4. The panelization of scientific responsibility?
§5. Some scientists speaking out





A number of cases of questionable behavior in science have been extensively reported in the media during the last few years. What standards are upheld by the scientific community affect the community internally, and also affect its relations with society at large, including Congress.

Here I wish to address questions of scientific responsibility, using the Baltimore case as a concrete instance where they came up. The first part containing historical background is necessary to provide readers with documentation so that they can have some factual basis on which to evaluate respective positions and my conclusions that follow - based on further but more succinctly summarized documentation.

I have reproduced many quotes because I firmly believe people are entitled to be represented by their own wording. Conversely, I hold people accountable for their official positions. Some of these are reproduced in footnotes, and some longer ones are reproduced in appendices. I also do not ask to be trusted. By providing numerous references, I hope that readers who find my documentation insufficient can follow up by looking up these references.

To address questions of scientific responsibility does not necessarily imply that one needs technical competence in a particular field (e.g. biology) to evaluate certain technical matters. The evaluation of scientific responsibilities can legitimately be done without such technical competence. For example, at no point do I take a position whether certain experiments validate a theory or not, or whether the theory is valid or not; but I do take a position about the ways scientific responsibilities were exercised in raising questions or answering questions about those experiments.

The article is in six parts:

Part I gives mostly a historical background of the early phases of the Baltimore case.
Part II presents a discussion of certain scientific responsibilities based on that background, specifically: the responsibility of answering questions about one's work, and the responsibility whether to submit to authority.
Part III summarizes the two NIH investigations.
Part IV deals with the responsibilities of a Congressional Committee vis a vis science.
Part V goes into an open ended discussion of many issues of responsibility facing scientists, vis a vis themselves and vis a vis society at large, including Congress. The list is long, and readers can look at the section and paragraph headings to get an idea of their content.
Part VI deals with the factor of personal credibility and the shift at the scientific grass roots.

The conclusion is an appeal to the scientific community to reassert the traditional standards of science.


BALTIMORE, David: Co-author of the Cell paper; Director of the Whitehead Institute (MIT) until 1989; then President of Rockefeller University until 1991
CAIRNS, John: Professor of Cancer Biology, Harvard School of Public Health
CULLITON, Barbara: Editor for Science until 1990; then moved to Nature
DAVIE, Joseph: President for Research and Development at Searle; Chair of the investigative panel for NIH
DAVIS, Bernard: Emeritus Professor of Molecular Biology, Harvard
DINGELL, John (D-MI), Chair, House Subcommittee on Oversight and Investigation
DOTY, Paul: Emeritus Professor of Biochemistry, Harvard
EDSALL, John: Emeritus Professor of Biochemistry, Harvard
EISEN, Herman: Emeritus Professor of Biology, Center for Cancer Research, MIT; he did the MIT inquiry on O'Toole's complaint
FEDER, Ned: Scientist at NIH; co-author with Walter Stewart of a paper critical of the Cell paper
GILBERT, Walter: Professor of Molecular Biology, Harvard
GOULD, Stephen J.: Professor of Geology, Harvard
GREENBERG, Dan: Editor, Science and Government Report
HADLEY, Suzanne: OSI Deputy Director, forced to resign in 1991 by NIH incoming Director Bernadine Healy
HUBER, Brigitte: Professor of Pathology, Tufts Medical School; Member of the Tufts Ad-Hoc Committee looking into O'Toole's complaint
IMANISHI-KARI, Thereza: Co-author of the Cell paper
LEWIN, Benjamin: Editor of Cell
MADDOX, John: Editor in Chief, Nature
MARCUS, Steven: Editor, Issues in Science and Technology (NAS)
McDEVITT, Hugh: Professor and Chairman, Dept of Microbiology, Stanford University School of Medicine; member of the Davie panel investigating for NIH
O'TOOLE, Margot: Postdoc who originally questioned the Cell paper
POLLACK, Robert: Dean, Columbia College
RALL, Edward: NIH Deputy Director for Intramural Research
ROWE, Mary: Special Assistant to MIT's President; ombudsperson
SHARP, Philip: Director of the Center for Cancer Research, MIT
SINGER, Maxine: Editorial Board Chairman, NAS
STEWART, Walter: Scientist at NIH; co-author with Ned Feder of a paper critical of the Cell paper
STORB, Ursula: Professor of Molecular Genetics and Cell Biology, University of Chicago; member of the Davie panel
WEAVER, David: Co-author of the Cell paper
WOODLAND, Robert: Professor of Molecular Genetics and Microbiology, U. Mass. Medical School; Member of the Tufts Ad-Hoc Committee looking into O'Toole's complaint
WORTIS, Henry: Professor of Pathology, Tufts Medical School; Chair of the Tufts Ad-Hoc Committee looking into O'Toole's complaint
WYNGAARDEN, James: NIH Director (later Deputy Director of the White House Science Office)


§1. How the Baltimore case arose: Margot O'Toole

In April 1986, the prestigious journal Cell published a paper cosigned by several authors, among which the three main authors were Thereza Imanishi-Kari, David Baltimore, and David Weaver. In May 1986, Margot O'Toole, a postdoc working in the lab, was reviewing the records for some experiments, and became convinced that the experimental data for that paper had been presented in a misleading fashion. She studied especially 17 pages of these records. As she testified to the Dingell Subcommittee on Oversight and Investigation in Congress later (HEARINGS, 9 May 1989, p. 181 and also p. 191): (1)

After I had studied the 17 pages, I knew that the published paper contained false statements. There was another related experiment reported in the paper to support the same point called into question by the 17 pages. I decided that if the data for this experiment was solid, the finding could still be supported by data and that I could justify doing nothing. Without telling Dr. Imanishi-Kari about my concerns or the reasons for them, I asked her if I could study the data for the other experiment. Dr. Imanishi-Kari told me she could not find the records and she did not know where they could possibly be. I decided to go to a more senior scientist for advice.

Margot O'Toole then contacted Drs. Huber and Wortis of Tufts University, as well as Dr. Woodland of the University of Massachusetts. Meetings were arranged with them and Imanishi-Kari on May 16 and May 23. Answers to Margot O'Toole's scientific objections were unsatisfactory, and I find it extraordinarily important that the scientific community should be informed of what it was like to raise a scientific challenge. Consequently, I shall quote extensively from Margot O'Toole's own words, for which there are no substitutes. She testified (p. 193):

I asked to see the original data, meaning the results of the experimental steps that would have had to precede the results she [Imanishi-Kari] was now showing me. Dr. Imanishi-Kari did not reply. After a long silence, Dr. Wortis told me to deal with the data I was being shown. We reviewed the data but they did not answer my objections. Drs. Huber and Wortis agreed with me that the problems were very serious. A large series of experiments, described in the paper and on which the central claim relied, had not even been performed. Dr. Imanishi-Kari said that all the problems were the results of inadvertent errors, and I did not question her explanation. She said she would never forgive me for the way I had handled the matter -- embarrassing her in front of her colleagues and raising questions that could reflect on her integrity. I left the meeting thankful that the unpleasant situation had been resolved, albeit at a high price for me. I was relieved that the paper would be corrected under the agreement I had made with Dr. Wortis. These are the events as they occurred. I should add that both Drs. Huber and Wortis have stated that my account is false.

The next day, Dr. Huber called me and told me that there was no doubt I was right scientifically. However, she and Dr. Wortis were convinced there was no fraudulent intent. She said that a correction would have a devastating effect on Dr. Imanishi-Kari's career. They had therefore decided that no correction would be submitted. I was shocked. I said the paper had to be corrected because others were relying upon it. Dr. Huber replied that there were so many faulty papers in the literature, that one more did not matter. She said that no matter what I did, she and Dr. Wortis would back Dr. Imanishi-Kari and that her "strong advice" to me was to drop the matter. I said that I would have to speak to Dr. Wortis and make sure there was no misunderstanding. Dr. Wortis and I then went through the problems with the paper and he acknowledged them point by point, but restated Dr. Huber's position - no correction would be submitted. I persisted but Dr. Wortis then said that my insistence was calling my motives into question. This was almost more than I could bear from my own thesis advisor with whom I previously had a good relationship.

As advised by Dr. Flax, the chairman at Tufts, I had kept an MIT official, Dr. Mary Rowe, informed of these developments. I had assured her that I felt the matter could be resolved through the informal process at Tufts. After my conversation with Dr. Wortis I had to admit that I was wrong. Dr. Rowe pressed me to bring formal charges at MIT. I told her that I did not wish to challenge Dr. Imanishi-Kari's explanation that the misstatements in the paper were the result of a series of errors and not due to deliberate fraud. I added that Dr. Imanishi-Kari and I had not been getting along and that I felt that my motives were being unfairly questioned. I did, however, feel a strong professional responsibility that the false statements be corrected. Dr. Rowe assured me that MIT could handle the matter in an ethical way without the formal charge of fraud we both knew could have devastating consequences. I also stated my strong belief that a formal charge of fraud was not warranted by the information available to me at the time.

I discussed at length with Dr. Rowe the professional consequences to me if I did as she recommended. I pointed out that upsetting as the experience of the Tufts review had been, the matter had been kept among friends. I had a non-tenure track appointment at Tufts, and I had an opportunity to apply for grants as a Tufts researcher; and I intended to do this. If I pursued the matter further, I felt certain Dr. Wortis, who was very influential at Tufts, would seek to prevent my return. Dr. Rowe assured me that coming forward was the right thing to do and that she would speak to the Dean and the Chairman and enlist them in making sure that a position would be found for me in an MIT lab. This kind of position was very much less attractive to me, because the Tufts position offered independence and scientific freedom. I had been a post-doctoral fellow for over six years and I felt ready for more independence. However Dr. Rowe pressed, saying that I had a professional obligation to come forward.

Having assured me that MIT could deal with the matter in an equitable way without a formal charge of fraud, Dr. Rowe called Dean Brown and arranged for me to talk to him. I described my concerns to Dean Brown. He said the serious nature of the problems sounded like fraud to him. He told me to charge fraud or drop the matter entirely. I told him that neither of those options were acceptable, but that of the two I would choose the latter. After I left, Dean Brown evidently rethought his position and arranged for Dr. Eisen to call me.

Dr. Eisen invited me to come and discuss my concerns on May 30. When I showed him the records he became very uneasy and said that by merely showing him the records I was charging fraud. I said that Dr. Imanishi-Kari said the discrepancies were errors. I said I was willing to accept this explanation but that I did not agree that the misstatements could be ignored simply because they did not occur with fraudulent intent. Dr. Eisen chided me for having placed him in a difficult position and told me that my concerns would have to be put in writing before he would address them.

I prepared a memo. Dr Eisen gave it to the authors and arranged a meeting with Drs. Baltimore, Imanishi-Kari, Weaver and myself. Dr. Rowe advised me to bring someone to represent my interests to the meeting. I asked Dr. Eisen if this would be all right, but he said no, it would be intrusive on the science. I asked if I could bring a scientist, but Dr. Eisen said this, too, would be intrusive.

At the meeting, Dr. Imanishi-Kari did not present any new relevant information. She immediately conceded that Figure 1 did not accurately represent the specificity of the Bet-1 reagent. Dr. Baltimore asked where the data for the figure came from, and Dr. Imanishi-Kari said that Dr. Reis must have obtained "this result once". Dr. Baltimore replied that "this was not good enough" and added later that he would deal with this matter in private with Dr. Imanishi-Kari. I then went over my concerns about Table 2, the principal support for the central claim of the questionable paper, and I showed a copy of the original data to Dr. Baltimore. He gave them a short examination and said that the claims could not be based upon them. This was precisely my point.

Dr. Imanishi-Kari and Dr. Baltimore acknowledged that some necessary experiments had not been done and they discussed how this error had been made...

Dr. Baltimore acknowledged that the finding I challenged did not have the claimed experimental support. However, he suggested some experiments that Dr. Imanishi-Kari could now do to find out what was really going on. He stated that there were portions of the paper that were sound. I have always agreed that parts of the paper are not false. He then said that as long as parts of the paper were true, he felt no obligation to issue a retraction. I disagreed and he said that I could attempt to submit a correction on my own, but that he would submit a note challenging my corrections...

A day or two later, I called Dr. Eisen and protested his failure to insist that false claims be corrected. I discussed specific scientific issues we had covered at the meeting, but Dr. Eisen said he could not remember them. He said that my continuing pursuance of the matter indicated vindictiveness. I called Dr. Rowe and she indicated that Dr. Eisen had made a verbal report to her and indicated that there were no problems with the paper. I reminded Dr. Rowe that she had said that she would help me to secure another laboratory position. I felt that I needed her assistance to explain why I was suddenly without a job or a recommendation. Dr. Rowe replied that I should have arranged the position before I had handed in my memo and that the time during which she could have helped me had now passed. I asked if I would receive a copy of the report Drs. Baltimore and Eisen had agreed Dr. Eisen would submit. Dr. Rowe said she had told Dr. Eisen that it was better not to submit a report, that reports were usually not filed in cases like this. She said this was in my interest. I presumed she meant that the report, if filed, would be unfavorable to me. She said that the matter was now in the hands of God and she wished me well.

Among other things, the above quotes document the extent to which higher ups were forcing Margot O'Toole and themselves into extreme alternative positions: either deal with a charge of fraud, or there is no necessity to do anything about a scientific challenge. I shall return later to my own objections to alternatives phrased or conceived in this way.

§2. Conflicting versions: The Tufts Ad Hoc Committee, Herman Eisen at MIT, and David Baltimore

I have quoted at length from Margot O'Toole because for several years the establishment press (as we shall see below) represented her position and the issues improperly.
As Margot O'Toole reports, officials at Tufts and MIT investigated her complaint. At Tufts, this investigation was carried out by an Ad Hoc Committee chaired by Henry Wortis, with Brigitte Huber and Robert Woodward as the other members. I quote from their conclusions:



These conclusions are from the Minutes of the Ad Hoc Committee at Tufts, dated 4 June 1986. The document is appended to the Dingell Subcommittee hearings, 9 May 1989, p. 303. For testimony at these hearings which will help readers evaluate the Tufts investigation, see Appendix 1.

Herman Eisen at MIT came to similar conclusions. I quote from a memorandum by Eisen: (2)

Re: Allegations of misconduct by Thereza Imanishi-Kari in a research study...

The allegations of misrepresentation were brought by Dr. Margot O'Toole...
Dr. O'Toole cited four issues, three of which challenge the conclusions drawn in the paper on grounds that some assays were not sufficiently sensitive or that they were misinterpreted. The issues raised by these three objections seem to be matters of judgment and could not be described as evidence of misconduct. . . But one of O'Toole's allegations was disturbing because it raised a serious question about deliberate misrepresentation of data. The allegation concerns a monoclonal antibody termed "BET-1". . .
My conclusion is that O'Toole is correct in claiming that there is an error in the paper; but it is not a flagrant error...The correction would be too minor to rate a letter to the journal; it certainly does not warrant a retraction, especially because the paper contains a substantial body of other data that is clear and impressive.
The other issues raised by O'Toole, which are largely matters of interpretation and judgement, are best dealt with by allowing the scientific process to take its course. Other laboratories are trying to extend the findings. In this way we will know if the interpretations are right or wrong.

David Baltimore himself presented matters differently when he published an article describing his point of view, and when he wrote: (3)

At the outset, the substance of the dispute was not unlike others that occur regularly in biology labs. It was simply a disagreement over scientific matters between two scientists [Imanishi Kari and O'Toole]...
In these reviews [at Tufts and MIT] completed by early summer of 1986, all the issues were scientific. No one had accused anyone of unethical or criminal behavior; O'Toole simply said she thought the conclusions of the paper were not borne out by the data generated in the Imanishi-Kari laboratory. After the second review, I thought that the matter was closed.

All three accounts are misleading, and in some ways are incompatible. Of course O'Toole's complaints dealt with scientific matters. However, she made factual assertions, whose evaluation was not a matter of "interpretation", but of determining correctness or incorrectness. As Margot O'Toole stated in her testimony to the Dingell Subcommittee (9 May 1989, p. 200): "My opponents in this dispute have convinced the scientific community that my differences with them involve alternative interpretations of data. This is not the case. I did not challenge the paper because I felt I had a better interpretation. We scientists discuss alternative interpretations every day. All authors are free to present their own interpretations...I challenged the paper because it represented evidence that simply did not exist, period. This is not a complicated concept. It is one thing to believe that something is true. It is another to present experimental evidence in support of the claim. This is the crux of my dispute with the authors."

Furthermore, although Margot O'Toole did not write down charges of "misconduct", "falsification" or "misrepresentation", the factual evidence (4) she was bringing to the attention of various officials at Tufts and MIT immediately brought to their mind such possibilities, as evidenced by the quotes reproduced above, and by the following testimony by Eisen himself, testifying to the Dingell Subcommittee (9 May 1989, p. 290), when he acknowledged:

In dealing with her charges -- Dr. O'Toole's charges of error -- I was not unaware of the possibility that she had in mind fraud and was unwilling to say so, and in carrying out my evaluation, this concerned me. [However, compare with Appendix 2.] This was one of the reasons it took a long time. I couldn't rush through this. I wanted to do a lot of talking to people and thinking about it and thinking about the science, and I was aware quite distinctly of the possibility that it deserved a fair consideration without her having to charge it or without having to - or without triggering off the full-scale investigation until some preliminary evidence was found that would suggest it merited such a detailed investigation.

Such possibilities were also on Baltimore's mind when he wrote to Herman Eisen a letter dated September 9, 1986, and marked "confidential" (but the letter is reproduced in the public hearings, 4 May 1989, p. 164). I quote from this letter:

After much thought about the situation brought on by my collaboration with Thereza Imanishi-Kari, my opinion has gelled around the following analysis.
1. The evidence that the Bet-1 antibody doesn't do as described in the paper is clear. Thereza's statement to you that she knew it all the time is a remarkable admission of guilt. Neither David Weaver nor I had any idea that there was a problem or an ambiguity with the serum. Why Thereza chose to use the data and to mislead both of us and those who read the paper is beyond me.
2. Given that the analysis is meaningless, does this change the paper? Not really and certainly not in a fundamental sense...
3. A retraction would be difficult because David Weaver would be identified as senior author and he really had nothing to do with those data. All authors do have to take responsibility for a manuscript, so all of us are in a sense culpable, but I would hate to see David's integrity questioned for something he accepted in good faith and where his contribution is what makes the paper strong.
...In summary, I think that a retraction would harm the innocent and raise doubts about quite solid work. I think we should, however, acknowledge to colleagues that the Bet-1 results are not reliable and I, for one, will be skeptical of Thereza's work in the future.

Thus Baltimore himself on 9 September 1986, "after much thought", had on his mind that Imanishi-Kari "chose to use the data and to mislead...". Baltimore stated subsequently at the hearings: "Mr. Dingell, I've gone to great lengths to apologize for that letter, to explain the conditions under which that letter was written...That letter was completely inoperative in its significance within a couple of days of its writing...It was known to me in a day or so that there was nothing wrong with it [the mu analysis] and therefore absolutely no reason to retract it." (5) Compare this explanation with the first sentence of the letter: "After much opinion has gelled...The evidence that the Bet-1 antibody doesn't do as described in the paper is clear."

In the next section, we shall see that possibilities of fraud or misrepresentations were also brought to the mind of scientific reviewers for the National Institutes of Health (NIH).

§3. The "17 pages" and the intervention of Stewart-Feder -- The issue of publication

We shall now deal with the issue of the 17 pages of notebooks on which Margot O'Toole and subsequently other people's objections were based. I start with an account from Baltimore's article in Issues in Science and Technology (p. 49):

Meanwhile, Charles Maplethorpe, who received his Ph.D. for work done with Dr. Imanishi-Kari but who had left her laboratory before the paper was published and had not been involved in the study, got himself involved. Maplethorpe contacted two scientists at the National Institutes of Health (NIH), Walter Stewart and Ned Feder, who had made reputations for themselves by publishing papers analyzing cases of previously demonstrated fraud in science. They received from O'Toole copies of 17 pages of laboratory notes taken from the Imanishi-Kari laboratory. Those pages, of more than a thousand pages collected during the study, included data from a number of failed experiments. On the basis of the 17 pages, plus conversations with O'Toole and Maplethorpe, Stewart and Feder mounted a challenge of their own.
The Stewart and Feder challenge soon developed into a cause celèbre because of the manner in which they conducted it. First they wrote a lengthy manuscript clearly charging that our paper was consciously misleading. The Stewart-Feder manuscript was submitted to a number of journals, all of which rejected it. Frustrated by their inability to publish what journal editors told them was not a scientific article that could be refereed, Stewart and Feder went public. They circulated the manuscript widely to scientists, asking for comment. They also began speaking about their "investigation" on university campuses and at scientific meetings and offered to send a complete file of correspondence to anyone asking for it... (6)

Stewart-Feder, upon receipt of the 17 pages, did write a paper dealing with the possibility that some of the Cell paper findings were not borne out by the primary data. At no point did Stewart-Feder make allegations of "misconduct", and they repeatedly emphasized that they did not. They were dealing with factual accuracy and scientific analyses of data. On the other hand, just as it happened with the Wortis Committee and Herman Eisen, NIH administrators chose to use the word "misconduct" to characterize what Stewart-Feder were objecting to. In addition, they were inclined to see the matter as a case to be handled according to certain quasi-legal procedures. (7)

Stewart-Feder had to ask NIH for permission to submit their paper for publication. Permission was at first refused. But every one of the three referees to whom NIH sent the paper for reviewing expressed the thought that if the 17 pages on which the Stewart-Feder paper was based were authentic, then these data raise serious doubts about the validity of some results in the Cell paper. One reviewer explicitly stated that the Stewart-Feder paper raised "serious issues of scientific fraud". All three reviewers suggested that Stewart-Feder contact the authors of the Cell paper to get their evaluation and explanations. [See Appendix 3 for the text of these reviews.]

Stewart-Feder followed the reviewers' suggestion. Baltimore wrote them his position in a key letter dated January 21, 1987 [see also Appendix 4 for more on Baltimore's position]:

I have been aware for some time that a discontented post-doctoral fellow previously at MIT has raised questions about some of the data in that paper...
Your notion of doing an "internal audit" of the data is not one I can accept. Such a principle, if established, would tie up the scientific community in continuous wrangles...External reviews of data are only relevant when probable causes of fraud have been established. In this case, a number of respected immunologists not involved in the work examined the situation and did not find probable cause.

Baltimore thus raised a fundamental issue concerning the responsibility of scientists to address criticisms of their work. I shall deal with this issue specifically later. Here, I continue with the account of the Stewart-Feder intervention. They also heard from Henry Wortis in a letter dated March 2, 1987: "It would not be useful to pursue the questions you have about the published results in Cell 45:24, 1986...No doubt you are curious about the relationship between the information you have been given and the published material. But there is no social or scientific gain in satisfying your curiosity." Thus although Stewart-Feder were following the recommendations of the reviewers, the principals involved stonewalled attempts to confirm or invalidate the data on which the Cell paper was originally based, and on which the Stewart-Feder paper was based.

In light of the fact that Stewart-Feder requested material from the groups at MIT and Tufts who reviewed the work originally, but complained about not receiving such material, Baltimore then wrote on 17 March 1987 to Edward Rall (NIH Deputy Director for Intramural Research), giving ground on having a "further review of the data". However, he formulated conditions for that review as follows.

From Stewart and Feder's "manuscript", it is clear that only someone familiar with immunologic procedures and concepts can provide a review. Therefore I suggest that you appoint a couple of immunologists to do an examination of Stewart and Feder's charges. If you decide that this is the right action, please tell Stewart and Feder that we have suggested this review. For the review to be meaningful, they must agree to abide by whatever decisions are reached. This means that they must promise to cease all discussion of this issue and to send an apology to all concerned if the review group finds that the norms of scientific research were not transgressed. The apology is absolutely necessary to counter the publicity that the issue has already received. The reputations of young scientists (never mind an older one) have been impugned by Stewart and Feder's activities and this wrong must be righted by them.
I should emphasize that by this request for a review, I am in no way suggesting that any of Stewart and Feder's allegations have a basis in fact. In reality, to my knowledge, there has been no official charge of fraudulent behavior made. This request to you is only made in the interest of clearing the air of what I consider false allegations made in a privately, but widely circulated form, so as to remove any tarnish from the reputation of the involved scientists.

It is no surprise that Stewart and Feder refused to accept Baltimore's proposal.

Rall still decided not to allow Stewart-Feder to submit their paper for publication. As a result, they wrote to Rall once more on 9 April 1987. They recounted the past events, and they first asserted that "the arguments for approval of our manuscript are clear and convincing." They summarized these arguments as follows.

(a) They pointed out that they followed the referees' suggestions to contact the authors of the Cell paper and to ask these authors for their comments.
(b) They pointed out that none of the referees had questioned the accuracy of their analysis.
(c) They pointed out that none of the letters they had received from Baltimore or other coauthors questioned the authenticity of the data in the 17 pages on which they based their analysis. For this and other reasons stemming from their correspondence, they concluded that the data were authentic.

As for the deeper problems of scientific responsibility, they asserted among other things:

-- The arguments against prior restraint on publication have a sound basis, particularly as applied to publication of comments on the accuracy of scientific papers. NIH should not embark on the unproductive and dangerous course of censorship of scientific publications...
-- Free and open communication on issues of scientific importance has a long tradition in the scientific community in general and at NIH in particular...
-- It is NIH policy to "Restrict writing and speaking by its employees only to the extent required [emphasis added]by law or regulation or to assure compliance with established NIH and DHHS policy" (NIH Manual, chapter 1184, 3/8/81, "Dissemination of Scientific and Professional Information by NIH Employees," page 2, part E).
We are not aware of any law, regulation, or established policy that requires NIH to prevent our paper from being submitted in the normal way to the scientific public.
Accordingly, prompt approval of our manuscript is clearly required by chapter 1184...

In the same letter of 9 April 1987, Stewart-Feder also addressed a fundamental question of scientific responsibility for themselves:

...Your directive poses a dilemma.
As we have noted, we believe it is generally accepted by almost all scientists that a scientist such as Dr. O'Toole or ourselves with unique knowledge showing that a published paper is probably wrong has an affirmative obligation to ensure that the knowledge is made public...
The problem with your recent directive is that it requires us to violate accepted standards of conduct. If we abide by your decision, we are in a position of covering up poor science, a position that is arguably similar to that of Dr. Baltimore, with the difference that his actions are active and ours would be passive. Either way, the damage to science and the public welfare are the same.
Naturally we will have to consider as a matter of professional conscience whether in light of our unique knowledge and our belief that damage is occurring, we are justified in continuing to remain silent. In reaching this difficult decision we shall seek the advice of senior scientists known for their accomplishments in research and for their integrity. We request that you furnish us with any reasons which in your opinion would justify us in agreeing to the course of conduct you propose.

Rall's reply was to resubmit the Stewart-Feder manuscript to reviewers once again. One of them wrote clearly supporting publication:

Reviewer R. I have reviewed the set of papers submitted by Drs. Stewart and Feder. I cannot interpret the data xeroxed from the original notebooks. One possible solution is to allow publication of their manuscript with a disclaimer that relieves NIH from formally approving the contents of the manuscript since it is not a traditional research document.

Three others recommended against allowing Stewart-Feder to submit their paper for publication, for various reasons. [For extensive quotes, see Appendix 5.] Typical is the following comment:

Reviewer Y: I do not believe that their paper should be published nor do I believe that this investigation should continue. I do not deny the possible validity of the raw data included with their paper, however, as you know pages from notebooks taken out of context can be quite misleading. At any rate I do not see what useful purpose can be served by extending this investigation.
I hope my opinion is of some use to you. I do not envy you your position in this conflict.

The scientific community will have to evaluate these reviewers' reports, which constitute documentation and primary sources (as the historians say) on how the scientific community reacts. (8) I regard such primary sources as exceedingly important, and that is the reason I have quoted so extensively from them.

These reviewers' reports also document the extent to which the scientific data were immediately perceived by some scientists as implying more than error, including possibly misconduct or fraud.

The NIH continued to refuse permission for Stewart-Feder to submit their article for publication. Then the ACLU intervened. In a letter dated 14 July 1987, the law offices of Morrison & Forrester representing the ACLU wrote to Robert Lanman, Legal Advisor to the NIH, "that NIH has no reasonable basis for denying publication, particularly as it is NIH's professed policy to encourage and assist its employees in disseminating information about their scientific research and professional activities. NIH Manual, Chapter 1184(A) and (E), Dissemination of Scientific and Professional Information by NIH Employees (3/18/81). In fact, we believe that NIH's continued refusal to allow Dr. Feder and Mr. Stewart to seek publication of their article constitutes an unlawful prior restraint..."

In a Memorandum dated 17 July 1987, the NIH Deputy Director for Intramural Research J. E. Rall then wrote to Stewart and Feder in a way compatible with the recommendation of Reviewer R and the ACLU request and gave permission for Stewart-Feder to submit their article for publication.

At that point, Stewart-Feder submitted their paper successively to Cell, Science and Nature. All three scientific journals rejected the paper.

Rejection of the Stewart-Feder paper by Cell. The rejection by Cell is noteworthy because Cell editor Benjamin Lewin iterated Baltimore's way of answering scientific challenges in his letter to Stewart dated October 19, 1987. First he asserted that the Stewart-Feder paper "claims fraud" (as opposed to error). He did not document that assertion, which is false. Lewin did not answer Stewart's request to document his assertion. (Of course, like others before him, Lewin interpreted the factual documentation of the Stewart-Feder paper as evidence of fraud -- which is something else.) Second, he proposed the creation of "an impartial committee of immunologists to investigate the allegation, on the basis of full access to the original laboratory notebooks"; however, Stewart-Feder or others would not have access to such data. He also asked that Stewart-Feder abide by the decision of such a committee, by writing:

If it should find that the original data are acceptable within the norms of experimental work, then of course the matter will have been resolved, and you will want to state so directly to those people with whom you have been corresponding about the work.


We now pause in the development of the historical account to comment more extensively on the problems of scientific responsibilities which have arisen, and which involve:

bulletthe responsibility of answering questions about one's work;
bulletthe responsibility whether to submit to authority.

Both these problems of responsibility are raised by the positions taken by Baltimore, Wortis and Cell Editor Benjamin Lewin. I find Baltimore's position and Lewin's letter to Walter Stewart remarkable, and going against the traditional standards of science:

-- Baltimore and Lewin's position goes against the open discussion of claimed scientific results.
-- Baltimore and Lewin improperly ask scientists to abide by the decisions of a committee of experts without the scientists having access to data. They thereby ask scientists to take scientific results on authority.
-- Finally, Baltimore and Lewin's proposals do not deal with the scientific factual questions raised by Stewart-Feder, but with whether "the norms of scientific research were not transgressed", and with whether "original data are acceptable within the norms of experimental work". By such a formulation, considering only transgressions of the norms of science, authorities may arbitrarily redefine whatever norms are convenient to prevent factual questioning concerning the bases and justifications for the conclusions of a paper reporting on an experiment.

According to the norms of science as I have always known them, the determination of correctness and significance of results in science cannot be done under the authority of a committee or a single person or organization. It can be arrived at only by open discussion, based on publicly available data that anyone can check. Experiments must be reproducible, based on the data of the experimenters. These norms require that scientists answer questions about their works; and that data (in the case of experimental sciences) or proofs (in the case of mathematics) be supplied on demand, if for some reason they were not part of the published paper announcing scientific results. (9)

I claim that the Cell editor's letter to Walter Stewart is a prima facie case of intolerable scientific conduct. Baltimore expressed himself even more strongly when he wrote directly to Stewart and Feder on 24 March 1987:

I made two suggestions: that you either accept the judgements of Eisen and Wortis or have other, independently chosen, immunologists consider the question.

If you do not wish to take the words of Drs. Eisen and Wortis, it merely shows how far removed you are from the ordinary behavior of scientists who look to each other for judgement and critical evaluation. If you consider that you want more than a statement that the paper in question is viewed by independently chosen immunologists as within the norms of scientific communication, then you are asking to judge by a criterion you have established for yourselves. [Bold face added for emphasis.] Although that is your right, there is no reason for the rest of the scientific community to go along with your particular desires.

...I am tired of this and convinced that it serves no purpose. Please leave me out of your further attempts to enjoy yourselves at the expense of others.

I think there is every reason for the scientific community to decide very clearly whether it goes along with Baltimore's position that the ordinary behavior of scientists is "to take the words" of experts or authorities, rather than to arrive at independent judgments, based on freely available data. Baltimore's position represents a profound disagreement concerning standards for making scientific criticisms. If Baltimore's view, that scientists who do not take the words of authorities are far removed from the ordinary behavior of scientists, prevails in the scientific community, then something fundamental, very serious, and very disturbing is happening to the scientific community.

The traditional view, which is completely opposite to Baltimore's, was well expressed by Feynman: (10)

Other kinds of errors are more characteristic of poor science. When I was at Cornell, I often talked to the people in the psychology department. One of the students told me she wanted to do an experiment that went something like this -- it had been found by others that under certain circumstances, X, rats did something. A. She was curious as to whether, if she changed the circumstances to Y, they would still do A. So her proposal was to do the experiment under circumstances Y and see if they still did A.
I explained to her that it was necessary first to repeat in her laboratory the experiment of the other person -- to do it under condition X to see if she could also get result A, and then change to Y and see if A changed. Then she would know that the real difference was the thing she thought she had under control.
She was very delighted with this new idea, and went to her professor. And his reply was, no, you cannot do that, because the experiment has already been done and you would be wasting time. This was in about 1947 or so, and it seems to have been the general policy then to not try to repeat psychological experiments, but only to change the conditions and see what happens.
Nowadays there's a certain danger of the same thing happening, even in the famous field of physics. I was shocked to hear of an experiment done at the big accelerator at the National Accelerator Laboratory, where a person used deuterium. In order to compare his heavy hydrogen results to what might happen with light hydrogen, he had to use data from someone else's experiment on light hydrogen, which was done on different apparatus. When asked why, he said it was because he couldn't get time on the program (because there's so little time and it's such expensive apparatus) to do the experiment with light hydrogen on this apparatus because there wouldn't be any new result. And so the men in charge of programs at NASL are so anxious for new results, in order to get more money to keep the thing going for public relations purposes, they are destroying -- possibly -- the value of the experiments themselves, which is the whole purpose of the thing. It is often hard for the experimenters there to complete their work as their scientific integrity demands.

What would Feynman say about the Baltimore position, which goes so much further than what Feynman describes in corrupting the traditional norms of science! And it isn't just Baltimore or Wortis, or Lewin individually. Their position was backed up by the scientific establishment at Tufts, MIT, and elsewhere, for instance by the reviewers who recommended against the publication of the Stewart-Feder article.


§1. The NIH Panel.

In late 1987 or early 1988 the NIH started investigating matters more formally. The NIH first formed a committee, against which Stewart-Feder and Dingell (among others) raised objections because some members of this committee might have a conflict of interest, having been closely associated with Baltimore. Although the first official position of the NIH was that "peer review procedures do not invariably exclude all co-authors and former associates", (11) the NIH in May 1988 created another investigative panel. Three scientists served as members: Joseph Davie (President for Research and Development at Searle); Hugh McDevitt (Professor and Chairman, Department of Microbiology and Immunology, Stanford University School of Medicine); and Ursula Storb (Professor, Department of Molecular Genetics and Cell Biology, University of Chicago). The charge to the panel was to determine if the Cell paper was accurate, as judged by the existing laboratory data. The panel was also asked to describe the nature and extent of inaccuracies, if any, and to state whether misrepresentation or other misconduct was involved. The report of this panel was submitted to NIH 18 January 1989 (and is obtainable through the Freedom of Information Act). In that report, they wrote:

...The Panel found significant errors of misstatement and omission, as well as lapses in scientific judgment and interlaboratory communication. However, no evidence of fraud, conscious misrepresentation, or manipulation of data was found...
With regard to Table 2, the following conclusions were made by the Panel. First, isotyping was not done, but was claimed to have been done. Second, the data are for wells, not clones...

...the panel was impressed by the amount of work done in support of the studies published in the paper in Cell, by the completeness of the records, and by the abilities of both Drs. Imanishi-Kari and Weaver to find, accurately interpret, and present data on experiments that were performed as much as three or four years earlier...


1. The Panel felt that the inaccuracies in Table 2 of this paper are sufficiently serious to merit a letter to Cell informing the editors of this fact...In addition, it should be stated that the data originally presented in Table 2 were not from clones, and that isotype determination was not performed. [This agrees with O'Toole's objection in her memo to Eisen, see Footnote 4.]
2. Clerical errors in Table 3 should be corrected.
3. The Panel recommends that the problems in the relative sensitivity and specificity of the Bet-1 and anti-idiotype reagents and assays be reported to Cell in a brief report...
4. In view of the fact that the panel found no evidence of fraud, misconduct, manipulation of data, or serious conceptual error, the Panel felt that no further action was required, other than those identified above...

The Panel has been provided with a copy of a letter that the coauthors of the Cell paper have submitted to the editors of that journal...However, the corrective action taken by the coauthors does not fully meet with the recommendations of the Panel as identified above.

Therefore in January 1989, NIH was still saying officially that there was found no evidence of "fraud, misconduct, manipulation of data, or serious conceptual error", despite the fact that both from internal NIH memoranda and NIH reviewers' reports on the Stewart-Feder paper cited above, in 1986 and 1987 a number of scientists (including some at NIH) interpreted the situation from the start as involving misconduct or fraud, possibly warranting an investigation. The official report of the Davie Panel should also be compared with the testimony given by Davie himself at the Dingell hearings, 4 May 1989. [See Appendix 6.]

§2. The OSI Draft Report.

Congressional hearings by Dingell and press articles reporting unfavorably on science put pressure on NIH to do more than had been done in the past to clear matters up. The Dingell Subcommittee had asked the Secret Service to make forensic analyses of the Imanishi-Kari lab notebooks to verify the authenticity of the entries relevant to the Cell paper. These analyses were presented at the hearings of 4 May 1989, and they showed that key pieces of evidence relied upon by the Davie Panel had been recorded after Margot O'Toole's challenge to the paper, and one to two years after the nominal date of the experiment. Then in summer 1989 NIH instituted still another investigation via its Office of Scientific Integrity (OSI). The OSI Draft Report was leaked in March 1991, and was widely reported in the press. I quote here from one of the main conclusions (p. 114):

The forensic evidence and the extensive statistical analyses establish that the June subcloning data and the January fusion data are fabricated. It remains unclear if these experiments actually were done...
Dr. Imanishi-Kari repeatedly presented false and misleading information to the NIH and OSI and to the expert scientific panels...
It is probable that a substantial portion of the I-1 notebook, the major source of data provided to substantiate the Weaver et al. Cell paper, was falsified...

The OSI Draft Report in addition to determining that data had been fabricated, also questioned the way Baltimore exercised scientific responsibility. It stated (p. 119):

Dr. Baltimore's most recently-expressed views concerning the investigation are the most deeply troubling. These were the statements Dr. Baltimore made on April 10, 1990, when he was interviewed by the OSI investigation team. Dr. Baltimore disputed the significance of the June subcloning data and he asserted that if they were fabricated, the NIH was somehow responsible for this act of scientific misconduct: "If those data were not real, then she (Dr. Imanishi-Kari) was driven by the process of investigation into an unseemly act. But, it does not go to the heart of any scientific issue..." (p. 65). (Dr. Baltimore apparently was referring to the requirement by the NIH at the conclusion of the first investigation that the coauthors publish the June subcloning data as a correction to the Cell paper.)

Dr. Baltimore went on to say that "...if something is not published, it's in your notebooks and it's not published, that it is not then a matter for those rules to be followed" (p. 66). "...[I]n my mind you can make up anything that you want in your notebooks, but you can't call it fraud if it wasn't published. Now, you managed to trick us into publishing -- sort of tricked Thereza -- into publishing a few numbers and now you're going to go back and see if you can produce those as fraud. But, I think you should see that was a forced situation..." (p. 68).

The OSI found Dr. Baltimore's statements to be extraordinary. They are all the more startling when one considers that Dr. Baltimore, by virtue of his seniority and standing, might have been instrumental in affecting a resolution of the concerns about the Cell paper early on, possibly before Dr. Imanishi-Kari fabricated some of the data later found to be fraudulent.

In addition, the OSI Draft Report had substantial words of praise for Margot O'Toole (p. 120):

Dr. O'Toole suffered substantially for the simple act of raising questions about the accuracy of a scientific paper. The loss of her position in Dr. Imanishi-Kari's laboratory is only the most visible symbol for the price exacted of her after she raised the challenge to the paper. Notwithstanding the losses and costs she incurred, Dr. O'Toole maintained her commitment to scientific integrity throughout the several reviews and investigations that followed her challenge to the Cell paper.
Dr. O'Toole was invaluable to the effectiveness of the OSI investigation...
Dr. O'Toole's actions were heroic in many respects. She deserves the approbation and gratitude of the scientific community for her courage and her dedication to the belief that truth in science matters.

A Minority Opinion was submitted by Drs. Hugh McDevitt and Ursula Storb, NIH panel members on the panel investigating the Weaver et al. 1986 Cell paper, dissenting from some of the conclusions. [See Appendix 7.]

The Draft Report gave rise to extensive press coverage, in the press at large and in the scientific press. This coverage was overwhelmingly supportive of Margot O'Toole. [See Appendix 19.] The New York Times also printed an Op-ed statement by Margot O'Toole, "The Whistle-Blower and the Train Wreck" (12 April 1991, p. A 29).

Baltimore himself issued a statement of contrition (Nature, 9 May 1991. p. 94): "I now recognize that I was too willing to accept Imanishi-Kari's explanations, and to excuse discrepancies as mere sloppiness. Further, I did too little to seek an independent verification of her data and conclusions...I am shocked and saddened by the revelations of possible alteration and fabrication of data." (12) He was also quoted widely in the general press (e.g. New York Times, 21 March 1991, p. B10): "...[the Draft Report], if it stands without major changes, raises very serious questions about serological data in the paper. Therefore I am today asking the other authors to join with me in requesting that the journal [Cell] retract the paper until such time as the questions are resolved. It is up to Thereza Imanishi-Kari to resolve them."

Nevertheless, subsequently, the OSI Draft Report came under attack for having been made and leaked under conditions lacking "due process". The incoming Director of NIH, Bernadine Healy, was a major force in undermining the credibility of OSI during summer 1991. She forced the resignation of Suzanne Hadley, formerly Deputy Director of OSI, from the Baltimore and Gallo investigations. As reported in the Journal of NIH Research (September 1991, p. 35):

Many of the issues being raised by Healy and others are crucial to OSI's investigations -- past, present, and future...Should OSI's procedures be changed? Do they afford whistle-blowers and the accused adequate protection and access to information? (13) Is the office adequately staffed and funded?...Have OSI's previous investigations been conducted appropriately? Will OSI's findings in the cases stand up to tougher scrutiny, for example, in the current criminal proceeding against Imanishi-Kari by the U.S. Attorney's Office in Maryland?
Raising such questions is one thing. Attacking OSI publicly and repeatedly before the questions can be addressed is another. But that is what Healy has done...
Some fear that Healy's criticisms -- whatever her intentions -- may damage irrevocably OSI's investigations of the Baltimore and Gallo cases.
"Dr. Healy is trying to give anyone who wants to attack [Suzanne] Hadley or OSI the ammunition to do it." says a staffer on Rep. John Dingell's (D.-Mich) Subcommittee on Oversight and Investigations...The staffer says that attorneys who represent the defendants in the Baltimore and Gallo cases are "licking their chops," because now they can use the words of NIH's director to challenge the credibility of OSI's investigations.

The staffers' fears appear to be well-founded. In an interview, Baltimore pointed directly to Healy's testimony and used it to defend his own position...

There is no doubt that the uproar over Healy, Hadley and OSI has diverted attention from criticisms of Baltimore that, until recently, seemed an important new trend in the case...

The future of OSI is uncertain. Healy sees the office as being at a "crossroads," Dingell wants to protect it, and Hadley and [OSI Director] Hallum continue to defend it...


§1. Attacks on the Dingell Subcommittee

Hearings on the Baltimore case were held by the Subcommittee on Oversight and Investigations, Chaired by John Dingell (D.-Mich) on 12 April 1988; on 4, 9 May 1989; and on 14 May 1990. At the time of the May 1989 Dingell hearings, Baltimore and his supporters mounted a major campaign attacking Dingell. Their position was that Dingell was improperly interfering with science, that he was hurting science, that he was unable to distinguish "error" from "fraud", and that he was about to legislate against "error". (Cf. Baltimore's testimony quoted in Appendix 4.) Baltimore contributed a preliminary shot to this campaign a year before, in a "Dear Colleague" letter (19 May 1988), and followed it up with his article "Baltimore's Travels" in Issues of Science and Technology, Summer 1989. (14) Among the contributors to the campaign:

(a) Phillip A. Sharp, Director of the Center for Cancer Research at MIT, also wrote a "Dear Colleague" letter dated April 18, 1989, as follows:

I am writing to you to ask your help in countering the continuing activities of Rep. John Dingell's subcommittee in Congress...At a meeting of the subcommittee in April 1988, the authors of the paper were vilified for their "fraudulent" work, even though there was no scientific basis for such a statement.
Since that meeting, an NIH review panel has examined the paper and found no evidence of fraud or misrepresentation. Nonetheless, Rep. Dingell and his staff have continued on the attack...
It seems obvious that the Congressional subcommittee has decided to continue to hassle David [Baltimore] and other authors and this has serious implications for all of us...
Enclosed is a draft of an article that Bernard Davis has written for Science. Also enclosed is a fact sheet that could serve you as a sample for a letter or perhaps an "op-ed" piece. Here's what I'm asking you to do:
If you agree with me, write a letter (please don't use my sample exactly). Send it to: 1) your congressman and, if you can, to members of the subcommittee; and 2) write the editor of your local newspaper with a note asking that it be published before May 1. If you're so inclined, you might ask your colleagues to do the same. If this works, we will have gotten the message out to a large and influential segment of the population in a timely way. [Boldface in the original]
The fight won't end there, but it's a good beginning. Please let me know if you will -- or won't -- join me in this. I'm writing to my congressman and to the Boston Globe.

(b) Robert E. Pollack, Dean of Columbia College, had a New York Times op-ed piece (2 May 1989):

In Science, Error isn't Fraud

Dingell's inquiry is a witch hunt

Prof. David Baltimore of the Massachussetts Institute of Technology is under attack by Representative John Dingell of Michigan...
Dr. Baltimore's reputation is at stake, but the rest of us will be affected by the outcome of these investigations as well. What has come under a legislative cloud for the first time in a very long time, perhaps ever in this country, is the legitimacy of the scientific method itself. This is an immediate and serious threat to science and medicine...the process of scientific investigation itself is at stake...
I fear that science is about to be put to an unfair and dangerous test by Congress. I cannot claim to be an uninterested party: I am a grateful recipient of N.I.H. grant support for my own research, and it would be disingenuous not to acknowledge my deep respect for the peer review processes that define the funding of bio-medical research in this country.
But as dean of Columbia College, I have a second concern. Already, too few young people are choosing to be scientists...If Congress legislates against error in science, there is no chance that a sensible young person will choose to be a scientist, and there will be precious few of us to continue the work...
I would welcome a Congressional initiative to deal with fraud as such, but I fear that the way Dr. Baltimore is being treated means that witch-hunts are in the offing.

(c) Stephen J. Gould published a long article in the The New York Times (30 July 1989, S4 p. 6):

Ideas and Trends

Judging the Perils of Official Hostility

to Scientific error

We all learned that Galileo discovered some of the moons of Jupiter and the phases of Venus. Few people realize, however, that he made a gigantic goof about Saturn...
We also all learned that Galileo was later convicted for defending and teaching the Copernican system, and that he spent the rest of his life under house arrest. We continue to deplore Galileo's fate and rank him first in the noble army of scientific martyrs. And yet, in the light of recent developments in Washington, I'm not so sure that Galileo might not be in more trouble today. Several Congressional Committees have been investigating scientific misconduct and some seem ready to view error as a cause for investigation into the misuse of Federal Funds. On this model, the Medicis of Florence might consider prosecuting Galileo for his misreading of Saturn.
"Scientific misconduct" is the subject under scrutiny by Representative John D. Dingell, Democrat of Michigan, and his Oversight and Investigations Subcommittee. The cause célèbre, a paper written by David Baltimore and colleagues, has been placed under the forensic equivalent of an electron microscope. This paper contains some errors, and some evidence of poor record keeping. The more public charge of fraud cannot be sustained.
Fraud and error are as different as arsenic and apple pie. The first is a pathology and a poison, the second an unavoidable consequence of any complex activity...

(d) Barbara Culliton's Science article "The Dingell Probe Finally Goes Public" (12 May 1989, p. 643) was equally tendentious. I quote the beginning and the end.

Congressman John Dingell did his level best to pillory Nobel laureate David Baltimore last week. His principal stratagem: to catch Theresa Imanishi-Kari at fraud and watch her drag Baltimore down with her. He succeeded in neither count...
As the hearing broke up, Baltimore and Imanishi-Kari were deluged with congratulatory hugs. "It was heartwarming to get such support," Baltimore said. "I needed it."
But there was also a sense of caution, even fear. "Dingell now is like a wounded animal," said one. "There's no telling what will come next. "

This is the type of journalism which affected the thinking of the scientific community. (15) Nevertheless, as correctly reported in Dan Greenberg's Science and Government Report 15 May 1989: "Baltimore Wins PR Battle. But Key Issues Remain."

§2. Congressional responsibility and scientific responsibility

A year later, Dingell opened the hearings of 14 May 1990 with a general statement running in part as follows (p. 91):

In exploring the issue of scientific fraud and misconduct, this Subcommittee has focused on the ability and will of major research institutions and the National Institutes of Health to police themselves when concerns about scientific misconduct are raised. We have seen a number of cases of proven misconduct that have been mishandled...[See Appendix 8.]
The distressing fact is that none of today's forensics should have been necessary. Former Director of NIH Wyngaarden put this clearly when he wrote Dr. Baltimore on January 31, 1989: [see the quote in Footnote 9] Significantly, this statement was made over a year ago, and before the reopening of the current NIH investigation. The statement is even more relevant now.
Scientists throughout the United States have claimed that this Subcommittee wishes to conduct a forensic analysis of every notebook involved in a prominent discovery. This is nonsense. They have claimed that the Subcommittee wants to "police" science. That is also nonsense. The Subcommittee expects the community of scientists to police itself. We have, of course, been severely disappointed by the response of the scientific community on a number of occasions...
This disappointment extends particularly to the present instance. A number of prominent scientists, under a promise of confidentiality, examined the suspect notebook and agreed that it was obviously bogus. But these same scientists were unwilling to advance their professional opinions in public for fear of the disapproval of their colleagues. This reluctance by prominent scientists to deal fully and frankly with the problem of scientific fraud and misconduct has greatly complicated not only the present investigation, but others as well. There are signs of hope, however, that the current NIH investigation will resolve the allegations in this case in a factual manner.
The standard in science was, and should always remain, a single thing: truth. It is only when allegations are minimized, data is not examined, and people do not behave in a straightforward manner, that it is necessary to employ forensic methods to settle questions of fact.

To Dingell's statement I add what Margot O'Toole said in her testimony of 9 May 1989 (p. 187):

Critics say that the activities of the subcommittee will make science a less attractive career for young people. Mr. Chairman and members of the subcommittee, the opposite is true. If you succeed in your goal of ensuring that concerns of junior scientists receive a fair and unbiased investigation, you will have provided a service for all scientists, and you will have made the profession more attractive. It seems many scientists believe that investigations of this type are unnecessary, even detrimental, because science itself, through the process of further experimentation is self-correcting.
I submit to them that an integral part of the self-correcting process is actions such as mine, and I challenge them to explain to me why this whole branch of the self-correcting process must be blocked.
This has been a long and agonizing affair. However, thanks to you and your staff, Mr. Chairman, there is now a good chance that a proper examination of the evidence will finally occur. The facts will be established based on the evidence, not based on who says I am wrong. The forensic evidence is now part of the equation, and I hope this issue will be settled soon.
When I appeared before this subcommittee last year, I was somewhat reluctant and very afraid. I knew my account would be labeled untrue by other principals in the case, and it has been. I felt they and not I would be believed and this, too, has been the case. I told of my experiences because the subcommittee requested that I do so. As a result of my testimony and my actions predating it, my competence and motives have been attacked by scientists from all over the world. But I had two very powerful factors in my favor. I knew the facts cold, and I was telling the truth. All I needed was a fair and thorough investigation.
The evidence is now proving that I have been telling the truth all along. For instance, when the scientific panel interviewed me in June 1988, I told them that a data page now dated November 1984 had been shown to me on May 23, 1986. I identified this page as one of the two shown to me in response to my challenge. This page bore notations in my handwriting. I further told them that at that time, May 1986, 5 months after the paper was submitted, it was stated that the data had just been generated. The panel paid no attention when I told them this. I did not know and neither did the panel that the Secret Service would later date this page to May 1986, contradicting the written date of May 1984.
This episode demonstrates a beautiful fact of nature and a basic tenet of science: the only version of events that can fit all the evidence is the true version. All that is required now is that the rest of the evidence be gathered and analyzed without bias.
Mr. Chairman and members of the subcommittee, I know you are under fire for insisting on a fair and thorough investigation, but I ask you to continue your interest in this case during this final stage of the NIH investigation.


§1. Failures of the establishment press

(a) Scientific journals such as Cell, Science and Nature originally turned down the paper by Stewart-Feder, analyzing the article by Baltimore et al which had been questioned by Margot O'Toole. They were thus closing off what should have been the natural channels of scientific criticism and exchange. After the NIH Draft Report, in Nature (28 March 1991, p. 269), Editor John Maddox acknowledged: "It may be of some interest that, in 1987 and 1988, Nature declined to publish two versions of a manuscript in which Feder and Stewart spelt out what they considered to be errors in the published paper [of Baltimore et al], partly because it then seemed probable that the matter would be properly investigated. In retrospect, their arguments are more appealing than they may then have seemed." I regard the argument that "the matter would be properly investigated" as illegitimate. Nature was preventing the scientific community from learning of certain issues first hand at a crucial time. Hence Nature has a substantial (but of course not exclusive) responsibility for the escalation of the whole case.

After the NIH Draft Report, and after being criticized for its original obstructions, Nature then decided to publish an abbreviated version of the Stewart-Feder paper, (16) so that there is now a published record of this paper. Furthermore, almost every week for about five months after the NIH Draft Report, Nature published statements and rebuttals from the principal parties involved, and from scientists commenting on the issues. [For further comments on this series, see Appendix 9.]

(b) The National Academy of Sciences' Issues in Science and Technology published only Baltimore's point of view in "Baltimore's travels" (Summer 1989). They did not publish an opposite point of view, for instance Margot O'Toole's testimony to the Dingell Subcommittee. I wrote to Steven Marcus, editor of Issues in Science and Technology, to suggest publishing that testimony, even after the OSI Draft Report, because I think it is essential that readers should know first hand what was withheld from them. The testimony was not published.

In April 1991 I also submitted a piece for publication: "Aftermath of the NIH Draft Report on the Baltimore Case", (a piece similar to Parts IV and V of the present article, but shorter). The editor refused publication.

John Edsall then wrote to Steven Marcus to suggest that Issues in Science and Technology give Margot O'Toole an opportunity to publish a piece. She did submit one, but in light of fast developing events and the increasing complexities of the Baltimore case, this piece was considered inadequate by a number of people, and Margot O'Toole did not follow up on that one. However, in light of developing events, in September 1992 she asked Issues in Science and Technology to publish her original testimony to the Dingell Committee, which she found still the most appropriate presentation of her point of view. Margot O'Toole has not had a reply from the editor of Issues in Science and Technology, and her testimony has not been published.

(c) The New York Times editorial "A Scientific Watergate" (26 March 1991, p. A22) commenting on the NIH Draft Report and describing past behavior of Baltimore and colleagues, stated:

[Dr. Baltimore] orchestrated a chorus of support from sympathetic colleagues by sending a letter to 400 scientists warning that Congressional intervention could "cripple American science".

What the New York Times does not say is that it itself helped the orchestration when it published the article "Judging the Perils of Official Hostility to Scientific Error" by Stephen J. Gould; the op-ed page piece "In Science, Error isn't Fraud" by Dean Pollack of Columbia University; and other material. The position of the establishment backing Baltimore at the time was that there was no fraud, but only mere scientific error, and that Dingell's interference in science was inappropriate and dangerous. Two years later, immediately after the NIH Draft Report, the New York Times published a series of very informative news articles. My principal objection at this time was that the New York Times failed to reveal its role in having misled the public previously. Specifically, in the article "How Charges of Lab Fraud Grew Into a Cause Célèbre" (26 March 1991, p. C1) the New York Times appropriately recalled what Gould wrote: "For example, Dr. Stephen J. Gould, a Harvard geology professor, wrote in 1989, 'in the light of recent developments in Washington, I'm not sure that Galileo might not be in more trouble today.'" But the New York Times gave no reference for where Gould wrote, and in particular it did not say that Gould's comparison of Dingell with the inquisitors who caused Galileo trouble occurred precisely in the New York Times article "Judging the Perils of Official Hostility to Scientific Error".

As for Dean Pollack, he stated in his op-ed piece: "Science differs from politics, or religion, in precisely this one discipline: We agree in advance to simply reject our own findings when they have been shown to be in error. There is no shame to this." But Dean Pollack's statement reproduced only the rhetoric of science, not the reality. He misrepresented the reality and thereby misled the public, with the full force of a New York Times op-ed piece.

(d) The rhetoric and the reality. Speaking out -- when? Publishing -- when? The reality has been the opposite of the rhetoric especially when questions have been raised about eminent figures in the establishment. The discrepancy between the rhetoric and the reality is partly documented by scientific journals refusing to publish an article critical of the Baltimore paper, and is further documented in the way Nature's editor John Maddox described first hand Baltimore's reaction in his Nature comments of 28 March 1991: "Some of Baltimore's friends (this one in particular) urged him to make some kind of public statement shedding full personal responsibility for the study. But they revealed an angrily defensive person, most offended that work with which he had been associated should be challenged." Maddox also published a New York Times op-ed piece "Dr. Baltimore's experiment in hubris" (31 March 1991, p. E13) after the NIH Draft Report came out, stating in part: "Loyalty to one's colleagues is admirable, but the ferocity of Dr. Baltimore's defense has been arrogant. He angrily rejected suggestions from friends (myself included) that he should publicly allow the possibility of error." So immediately after the NIH Draft Report, influential and powerful people such as Maddox tripped over themselves to dump on Baltimore. Why didn't Maddox write publicly two years before, or a year before, or six months before that "the ferocity of Dr. Baltimore's defense has been arrogant"? I personally object to John Maddox' conduct in not having made his point publicly sooner, and I want the scientific community to evaluate the journalistic responsibility of Maddox and others like him, in this context. The scientific community can also evaluate the journalism of the New York Times, which published Maddox's criticism of Baltimore in 1991, instead of, say, spring 1989 when they serviced the campaign against Dingell.

(e) Parallel sources of information. Throughout the Baltimore case, until the NIH Draft Report, one could not rely on the establishment press for systematic and correct information. One had to look elsewhere. The most notable place for the Baltimore case was Dan Greenberg's Science and Government Report. Greenberg's articles systematically provided extensive documentation. Among other things, in his articles, Greenberg quotes extensively from past and present reports, Congressional hearings and original sources, giving primary references from which readers may form their own conclusion, or may follow up his documentation.

Stewart and Feder also distributed a great deal of information, aside from submitting their scientific paper. All three, Greenberg, Stewart and Feder deserve the appreciation of the scientific and academic community.

(f) Obstructions in general. I entirely agree with the position expressed by Herman Eisen himself, but only after the OSI Draft Report came out, when the New York Times quoted him as saying (26 March 1991, p. C5): "I think there ought to be some instrument to allow a person like Dr. O'Toole who was dissatisfied, to publish her objections. I blame myself very much for not urging Dr. O'Toole to publish. That was a major mistake. Of course, journals might not have published.... "

§2. Closing ranks.

Members of the science establishment mostly backed Baltimore. Besides Phillip Sharp, Dean Pollack, Stephen J. Gould, figures such as Maxine Singer and Bernard Davis contributed to this backing. Maxine Singer is quoted in the New York Times (14 May 1989, p. E6):

"In science, mistakes can be positive and discussing them can move research forward," she says. Most scientists would not have problem with Congress investigating a research paper if there was truly evidence of fraud, Dr. Singer says. But, she said, "These hearings have focused on one paper, the validity of its data, and the errors it contains, with no charge of fraud or misconduct. Most scientists would agree that this is not the proper forum in which to discuss scientific error.

As reported in the Washington Times article "Scientists' empire strikes back at one who dared to challenge it" (16 June 1989):

Ms. O'Toole has tried to respond to the avalanche of what she believes to be misleading information by contacting individual scientists who speak out publicly on the affair.
Her experience with Maxine Singer is typical. In an unpublished letter to The Washington Post circulated among scientists, Ms. Singer, editorial board chairman of the National Academy of Sciences, replied to a Washington Post editorial that mentioned Ms. O'Toole's role as whistleblower in the Baltimore affair: "Whistleblowers' integrity is compromised," wrote Ms. Singer, "when they confuse scientific criticism with allegations of fraud."
Margot O'Toole responded in a private letter: "Since the editorial you mention identifies only one whistleblower by name, me, you have publicly impugned my integrity." She went on to request that Ms. Singer "support your damaging statements about my integrity with actual evidence and publicly withdraw your assertions."
Nearly a year later, after Ms. O'Toole left a phone message, Ms. Singer replied in writing: "You must have read a copy of my letter. However, because the Post never published my letter, there seemed (and seems) no purpose in responding to your comments."

Maxine Singer did indeed write her letter as described above on official NAS stationery, bearing her identification as Editorial Board Chairman, and her letter was indeed circulated among scientists (I have a copy). The Washington Times continued by describing the role of Bernard Davis, who had been invoked by Phillip Sharp in his "Dear Colleague" letter:

Bernard Davis, a professor at Harvard Medical School who has criticized Congress for launching "a paralytic legislative crusade for an unattainable degree of purity," expresses a sentiment shared by many scientists: "Whose judgment am I to take more seriously? I have to look at the fantastically productive record of Dr. Baltimore, not only before, but since he won the Nobel Prize [vs.] a postdoc [Ms. O'Toole]. You can call that a ganging up, or covering up, but whose judgment am I to take more seriously?"
While having written on the subject he hasn't examined the data personally. "I felt with so many experts close to the field going over it, it would be presumptuous of me to think that I could shed any new light."

Here we behold a scientist going against one of the basic tenets of science by relying on authority and big time certifications such as the Nobel prize, thinking it "presumptuous" to engage in his own independent analyses.

In his New York Times piece of 31 March 1991, John Maddox had this to say about the responsibility of scientists and the damage to science due to closing ranks (p. E13):

When the Dingell inquiry was announced, he [Baltimore] circulated a letter to the scientific community warning of the dangers of Congressional interference in science. That danger is one of dark consequence. Another is the damage to O'Toole, who behaved properly throughout. She was without a job for three years. Those who have carried out the investigations at Tufts, M.I.T. and the N.I.H. have been made to look foolish, dupes of Dr. Baltimore's glittering reputation. It has taken the Secret Service to show that the disputed data were fabricated.
The damage to the scientific community's reputation will also be considerable, after a decade's anxiety about laboratory fraud...
But this case will seem proof that the scientific community can cover up the errors of eminent insiders at the expense of unestablished whistleblowers. The disputed article would not have survived had not Dr. Baltimore been its champion.

§3. The legalization of scientific responsibility?

Questions have arisen about the policing of science. Who is responsible for the policing? My answer is: all of us. I object to a legal approach when settling questions of science or scientific behavior. In policing science, I favor applying the norms of science, which require scientists to answer criticisms of their works openly and publicly. What may start as scientific objections may evolve into questions of fraud or misconduct. I object to the attempt which has been made to drive someone from the start into the position that either there is only "error", in which case there is no need for investigation, and corrections need not be made; or there is an allegation of "fraud" or "misconduct", and then one must establish legal or quasi-legal procedures, as described in "Baltimore's travels". [For a specific quote, see Appendix 10.]

Some editorials in Nature have been phrased in terms of the legalization of investigations, for instance the unsigned editorial "Even misconduct trials should be fair" (Nature 28 March 1991, p. 259). Of course I am not against being "fair", but the word means different things to different people, especially lawyers. I do not agree that the OSI investigation was a "trial". I disagree with the conclusion: "Because OSI is a quasi-legal office, it should in fairness adopt the safeguards of the legal system." The legal system safeguards can only too easily be used to put constraints on the open confrontations of ideas and challenges which form part of the traditional norms of science. On the other hand, the editorial takes OSI severely to task for not giving "due process" to the "accused". Similar charges were repeated in an editorial "NIH need clear definition of fraud" by Barbara Culliton (Nature, 15 August 1991. p. 563). The validity of such charges was not documented in the Nature editorials. [More details will be given in Appendix 11.] In any case, I do not agree that NIH needs a "clear definition of fraud". Scientific responsibilities traditionally transcend a legal approach. I do not know of any clear definition of "fraud": some extreme cases are universally accepted as "fraud", but there is no agreement on all cases. As far as I can judge, any such definition will simply reinforce a point of view currently supported by some scientists that if what one does is not "illegal", then it's acceptable; and it will contribute to the legalistic morass. Such a point of view undermines the exercise of scientific responsibilities, as distinguished from legal responsibilities. I share Feynman's view of scientific responsibilities, which I shall quote further below.

The 28 March Nature editorial also stated (p. 260): "Investigations of scientific misconduct should be subject to the 'sunshine' laws that apply to many areas of government business. NIH should develop a system whereby the prosecutor -- OSI -- and the defendant could present their respective cases to an appropriately constituted panel of peers in an open hearing." I object to the first phrase, viewing OSI as a "prosecutor" and certain scientists as "defendants". However, in the present circumstances, I agree that the NIH investigations should have proceeded in open hearings, in full view of the scientific community, which should have had documentation immediately available as a basis for independent judgment. The function of OSI would be not so much a "prosecution" but would be more to provide an open forum in cases when scientists refuse to answer other scientists' challenges about their work or provide insufficient answers, and when scientific journals refuse to publish such challenges. [For an opposite view by OSI Director Jules Hallum, see Appendix 12.]

I also object to the part of the 15 August 1991 Nature editorial where Barbara Culliton asserts (p. 563):

A fundamental point needs to be resolved in this debate. Is it the government's job to ferret out and punish scientists who commit fraud in the course of conducting federally funded research, or should the government's official fraud office extend its reach to matters that are properly defined as error and carelessness? A logical response is that the government should stick to the former, leaving judgements about the adequacy of footnotes, perfection of data presentation in published tables or handling of students to editors, tenure committees and the bodies that award prizes to people whose behaviour is so exemplary that it sets them above the average.

Culliton phrases the alternatives in a tendentious manner. (In the Baltimore case, did the NIH "ferret out", or did it respond to complaints by scientists, or what?) I do not find her response "logical". Who is to evaluate what constitutes "exemplary" behaviour? What does "average" mean? At the start of a scientific challenge, one does not know whether a problem is due to the adequacy of a footnote, sloppy data, fabricated data, or worse. One traditional view of scientific responsibility is that one cannot rely on any one's authority to determine the merits of a case, but that full documentation must be publicly available, to provide the possibility of independent judgment. After ordinary scientific channels have shown themselves to be clogged, I don't see what is so illogical for a government agency such as NIH via OSI to provide an independent open forum for the presentation of scientific challenges, which is not "to punish". Fundamentally, if Baltimore and co-authors accepted to answer publicly and through scientific channels questions raised about their work; and if the editors of scientific journals (Nature, Science, Cell) allowed papers such as the one submitted by Stewart-Feder to appear and to form a basis for public scientific discussion, then the whole problem of whether to "investigate" and under what conditions would be moot as far as the responsibilities of the scientific community were concerned. The responsibility for a granting agency whether to make or continue a grant might require them to make an investigation, but that would be a separate matter. However, nowhere do the two Nature editorials consider the fundamental problem of scientists not answering scientific criticisms of their work, not allowing publication of criticisms, or requiring other scientists to submit to various authorities. The effect of such editorials is to draw attention away from this fundamental problem, while discrediting attempts by government agencies to prod scientists to maintain certain standards, when the scientific community itself is failing.

Two months later, subsequent to a fundamental point raised by Paul Doty (quoted in §5 below), Nature (10 October 1991, p. 484) finally had a very different editorial (unsigned) facing the problem head-on:

Baltimore's defence

Although the final decision of the Imanishi-Kari case is some way off, one issue in the case is already clear...But there is one issue, raised by Professor Paul Doty (Nature 352, 183; 1991) which requires a decision by the scientific community rather than by an office of the US National Institutes of Health (NIH): what are the responsibilities of the authors of a published research report?
The issue is simply stated. Dr David Baltimore, the most celebrated although not the principal author of a disputed paper (Cell 45, 247; 1986) has from the outset taken the view that it is for the scientific community at large, and for others working in the field concerned, eventually to demonstrate the validity or otherwise of the disputed data and the conclusions drawn from them. It is a point of view, but hardly a defensible one, especially when the authenticity of the data on which the disputed paper's conclusions were supposedly based has been sharply questioned...The plain truth is that the authors of all published research reports have a personal responsibility for their aftercare...So much has hitherto been generally accepted. Were it otherwise, science itself would be undermined. For the presumption would be falsified that what appears in the literature can be regarded, at least provisionally, as authentic...

This editorial provides still another instance of a pattern, whereby the editors of Nature write up "the plain truth" only after someone such as Paul Doty comes out; and only years after others have been on the line to uphold the traditional norms of science, and when those on the line needed "the plain truth" about scientific standards to be expressed in the establishment press. (17)

The norms of science as I have always known them hold that the evaluation of experiments or data cannot be done confidentially, and that it is highly improper to have the ultimate verification entrusted to the authority of a single agent, be it a person or a committee. The scientific community is entitled to have full information on which to base an independent judgment.

Again I share the Feynman position (loc. cit. p. 341):

But there is one feature I notice that is generally missing in cargo cult science. That is the idea that we all hope you have learned in studying science in school -- we never explicitly say what this is, but just hope that you catch on by all the examples of scientific investigation. It is interesting, therefore, to bring it out now and speak of it explicitly. It's a kind of scientific integrity, a principle of scientific thought that corresponds to a kind of utter honesty -- a kind of leaning over backwards. For example, if you're doing an experiment, you should report everything that you think might make it invalid -- not only what you think is right about it: other causes that could possibly explain your results; and things you thought of that you've eliminated by some other experiment, and how they worked -- to make sure the other fellow can tell they have been eliminated.
Details that could throw doubt on your interpretation must be given, if you know them. You must do the best you can - if you know anything at all wrong, or possibly wrong - to explain it. If you make a theory, for example, and advertise it, or put it out, then you must also put down all the facts that disagree with it, as well as those that agree with it...In summary, the idea is to try to give all the information to help others to judge the value of your contribution; not just the information that leads to judgment in one particular direction or another.

The scientific community is again faced with a choice: to uphold the legal concept of scientific responsibility as in "Baltimore's Travels" and in the Nature editorials of 28 March, 9 May, and 15 August, or the traditional concept of scientific responsibility represented by the Nature editorial of 10 October and Feynman.

§4. The panelization of scientific responsibility?

Throughout the Baltimore affair and in other cases, we have met with one panel after another. In the Baltimore case, this panelization started with the panels at MIT and Tufts. Then we had the Davie Panel at NIH. Benjamin Lewin, Editor of Cell proposed constituting an "impartial committee of immunologists" instead of publishing the article by Stewart-Feder, who of course refused to accept such a proposal since they would have had to surrender their independent judgment as scientists and would not themselves have had access to the laboratory data. After that, we had the Office of Scientific Integrity and its Draft Report.

Finally in late 1990, the NAS Committee on Science, Engineering, and Public Policy (COSEPUP) appointed a panel (still another one!) chaired by Edward David, with the following charge:

1. To review modern research practices and analyze factors that could affect the integrity of research.
2. Examine the advantages and disadvantages of explicit guidelines to strengthen scientific standards for scientists and their institutions.
3. Clarify roles for public and private institutions in promoting responsible research practices, and assess institutional experience with current procedures for handling allegations of misconduct in science.

In the article "Panel Urges Independent Body to Set Ethical Standards in Science", the New York Times of 28 March 1991 quoted an interview with the chairman Edward David: "It is terribly important for the country that the science community keep its ability to self-govern. That is what is being called in question now - the ability of universities and laboratories to govern themselves. And if we don't perform well to maintain that, we are in trouble." In that same article, the New York Times also quoted Robert Rosenzweig, President of the Association of American Universities: "Our main concern is to keep the universities' feet to the fire."

But it's not only a question of the universities.

(a) The NAS. The David-COSEPUP Panel might also keep the NAS feet to the fire. After all, the NAS was part of Baltimore's orchestra when it published only Baltimore's point of view in Issues in Science and Technology, and when Maxine Singer wrote to the Washington Post on NAS editorial stationery. It would be quite appropriate for the David-COSEPUP Panel to bite the hand that feeds it.

(b) Students and young scientists or established scientists? Despite the fact that it is established scientists who have transgressed the rhetoric of scientific conduct, there have been repeated suggestions laying blame on young scientists, or on the lack of courses in ethical matters for students.

-- The NAS Committee on the Conduct of Science put out the pamphlet "On being a scientist". NAS President Frank Press wrote in his preface: "This booklet is written primarily for students who are beginning to do scientific research... The mechanisms that operate within science to maintain honesty and self-correction must therefore be honored and protected..." There is the rhetoric. We have seen the reality. Phillip Sharp, who orchestrated the campaign against Dingell, is one of the coauthors of this NAS pamphlet. [For more on this pamphlet, see Appendix 13.]

-- Francisco Ayala chaired the NAS Committee that put out the pamphlet. He also published the article "For Young Scientists, Questions of Protocol and Propriety Can Be Bewildering" (Chronicle of Higher Education 22 November 1989, p. A36) in which he invokes the pamphlet. In the title of his article and elsewhere, Ayala makes it appear as if the problem is for "young scientists"; but one thing bewildering to Margot O'Toole was that Baltimore did not immediately and routinely make a correction. What do the big time generalities of the NAS pamphlet mean in practice? What steps have Frank Press, Phillip Sharp, Francisco Ayala and the NAS taken to protect scientific whistleblowers?

Ayala also brought up "mentors" in his article: "The mentor system, in which a university faculty member serves as adviser and laboratory director for a group of graduate students, is the centerpiece of what always has been an oral tradition of passing on the values, ethics, and practices of science. " The article by Ayala is hypocritical and revealing in light of the performance of established scientists during the Baltimore case. Given the repeated failures of senior scientists, and in the Baltimore case of a large part of the scientific establishment, one might conclude more legitimately that the "mentor system" might push young scientists away from scientific values. [See Appendix 14 for further documentation on the mentor system.] Ayala's centerpiece has shown itself to a large extent to be a centerpiece of misrepresentations, subservience to authority, intimidation, and arbitrary power (scientific and journalistic).

-- A Boston Globe article titled "Rep. Dingell asks scrutiny of MIT, Tufts over handling of fraud probe" (22 March 1991) reports that in a letter to MIT faculty and researchers, the university's president, Charles M. Vest, called for development of a program "to provide career guidance and mentoring" and to communicate the values of science, which "demand the pursuit of truth with integrity and ethical rigor." The irony of Vest's program "to provide career guidance" would be laughable if it were not so sad, in light of what Baltimore and higher ups at MIT and Tufts did to Margot O'Toole's career.

-- The New York Times article of 28 March 1991 on the David-COSEPUP Panel states: "Another recommendation of the draft report [of this panel] is to have required courses in ethics and conduct within the regular curriculum for science students."

-- Dr. Judith P. Swazey (of the Acadia Institute) is quoted in the same Times article as stating: "In our survey we found that deans felt it was terribly important for their students to learn about ethical issues, but most said they had no courses that taught the subject and no expectation that they would. There is a major gap between good intentions and practices." How does Swazey know what "intentions" are? Has Swazey surveyed Dean Pollack at Columbia University about Pollack's charge of "witch-hunts" in his New York Times op-ed piece? What about the deans at Tufts and MIT?

In fact, the problems have not been with students; there has been no evidence in the recent cases of public notoriety (Baltimore, Gallo, Darsee, Breuning, Freeman, Braunwald,...) that students need to learn about ethical issues. Problems have arisen with established scientific figures whose teaching may consist of questionable examples. As I have pointed out repeatedly, problems in the Baltimore case (and others) have not been with "young scientists" either (e.g. Margot O'Toole); but I have seen problems with Imanishi-Kari, David Baltimore, Dean Pollack, Stephen J. Gould, Phillip Sharp, Bernard Davis, Maxine Singer, and S. Marcus, established scientists all. Who would determine the content of courses in scientific ethics? On what examples would these courses be based? With what choice of material? Would it be exclusively the quoted views of the above scientists, or of Bernard Davis and the 143 scientists who published "An open letter on OSI's methods" in Nature (27 June 1991, p. 693), stating:

As scientists, we are deeply disturbed by the way in which the charges against Dr. Thereza Imanishi-Kari...have been handled by the Office of Scientific Integrity of the National Institutes of Health. The need for formal, thorough and fair investigations of possible scientific fraud is clear. However, it is apparent that the procedures followed by the OSI have serious shortcomings, and have not permitted Imanishi-Kari the opportunity to defend herself by a public examination of the evidence against her...Under the circumstances, we reserve judgement about the facts of this case until Imanishi-Kari has had an adequate opportunity to defend herself. It is not clear to us that the current procedures will allow this to occur.

Bernard Davis was among the signers. He also published a scathing attack on Margot O'Toole in the Wall Street Journal (22 July 1991), entitled "Dingell's Witness for the Persecution". Aside from a direct personal attack, he wrote:

It is hard to avoid the suspicion that the OSI -- recently created in response to congressional criticisms -- has been excessively eager to establish fraud in this case . . . . The scientific community has been split into passionate defenders and equally passionate critics of Margot O'Toole. But all would agree that Rep. Dingell's choice of this case was tragic and the costs have been excessive. These include a great deal of time and money, serious damage to reputations and to the public image of science, and the possible impairment of the future contributions of David Baltimore as an exceptional scientist and administrator. Even more serious, however, is the danger that we may end up imposing on science the kind of bureaucratic system of policing familiar to legislators. After all, it is asked, are scientists entitled to any more autonomy than bankers?
But this is the wrong question. The issue is not entitlement: it is the value of autonomy in promoting creative research. (18)

Bernard Davis writes tendentiously (e.g. "It is hard to avoid the suspicion..."), and he also writes presumptuously that "all would agree...". The "costs" have indeed been great, but what does "excessive" mean? Did the scientific community's failures deserve the costs? Was the damage to reputations (whose?) deserved? Not all would agree with the judgments of Bernard Davis that Dingell is the one responsible for the "costs", or that Dingell was undermining the "autonomy in promoting creative research". I, for one, do not agree. I do not recognize being an "exceptional scientist" as a license to throw one's weight around to avoid answering scientific criticisms.

§5. Some scientists speaking out.

John Edsall's opinions concerning the Baltimore case evolved over several years. I shall describe them here more extensively and more accurately than I did in the published article, because of information which he communicated to me in September 1993, and because I know other scientists who underwent evolutions. John Edsall testified at the Dingell Subcommittee hearings of 12 April 1988, with a "prepared statement". The statement does not deal specifically with the Baltimore case, but with some other cases. It contains praiseworthy sentences about Stewart-Feder, for instance concerning the Darsee case, when Edsall states: "Drs. Stewart and Feder have made serious sacrifices of their research program in order to carry on and publish their enquiry into these matters, and they have paid a penalty for doing so by losing much of their research space and equipment to others. I greatly respect what they have done; I think they have performed an important public service."

Edsall's statement also contains general statements concerning the possibility of scientific misconduct or fraud, including the statement (p. 149): "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 whistle-blower 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."

On the other hand, although Edsall "commended" Dingell for his "concern for scientific honesty, and for exposure of scientific fraud and misconduct", he also was troubled because at the hearings, "none of the coauthors of the paper being criticized was present". [Letter to Dingell, 23 May 1988] In a letter to the Boston Globe (20 June 1988), he iterated his criticism of Dingell for not inviting these authors to testify. Although Dingell did not reply to the letter, he took into account such criticisms (not only by Edsall), because Baltimore and others were invited to testify at the hearings a year later, when Baltimore won a public relations victory. Subsequently, Edsall summarized the evolution of his position in the Journal of NIH Research (August 1991, p. 31) as follows:

For some time I was confused and misled by the orchestrated attack on Rep. John Dingell's (D.-Mich) subcommittee by many members of the scientific community. This was also inevitably, in effect, an attack on Dr. O'Toole. In retrospect, I consider that Rep. Dingell made some mistakes at the beginning, which understandably infuriated David Baltimore, and increased the polarization of the debate. My net conclusion is that, on balance, Mr. Dingell has served well the cause of truth and justice, and thus the cause of science also.
Dr. O'Toole's later testimony, followed by the recent draft report of the NIH Office of Scientific Integrity, has convinced me that she was telling the truth from the beginning...

In the late eighties, an important part of the scientific establishment was taking a complacent attitude toward the cases of questionable scientific conduct which arose. This attitude was exemplified in an editorial by Science editor Daniel Koshland (9 January 1987), concluding: "Having acknowledged that, we must recognize that 99.9999 percent of reports are accurate and truthful, often in rapidly advancing frontiers where data are hard to collect. There is no evidence that the small number of cases that have surfaced require a fundamental change in procedures that have produced so much good science. To continue the great advances that are being made, we must accept that perfect behavior is a desirable but unattainable goal. Vigilance? Yes. Timidity? No."

Edsall's article in the Journal of NIH Research concluded by addressing itself to this attitude as follows:

Serious attention to misconduct is still lacking. The Panglossian Koshland was reflecting the complacency of the managers of science when he proclaimed that science has a purity that even exceeds Ivory Soap's. My estimate is that another Baltimore case or two must occur before the mandarins recognize that a problem exists, and that if science doesn't clean house, politics will.

In an article "Cover up charge puts scientists under microscope", the Detroit News of 29 October 1989 quotes one scientist: "Harvard's Walter Gilbert, who won a Nobel Prize in 1980 for DNA research, told The Detroit News the implication of the Secret Service findings to date is that 'those experiments weren't done at that time -- or they were not done at all.'" After the OSI Draft Report came out, Walter Gilbert was further quoted in the New York Times (22 March 1991, p. B6):

The whistle-blower herself did not want to call this fraud in the beginning, but she reported it to people who should have known better. The people in authority, and in my opinion that means at M.I.T and Tufts, failed to investigate properly. Neither of them seriously entertained the question of whether there had been fraud and what should be done.
That is the greatest failure of the institutions. There is a canon of the establishment which says that when someone objects, that person must be a malcontent and be badly motivated and that science is holier than anyone or anything. This is the issue: what happens when a scientist is called upon to be unsure of his or her work.

In Science and Government Report of 15 October 1989 (p. 6), Dan Greenberg had quoted some scientists similarly, but anonymously:

...a number of highly respected scientists are just plain dismayed about Baltimore and the Cell paper. One of them, a Nobel laureate, told SGR on a non-attributable basis last June that "I have reservations about the [Baltimore] paper. Lots of people think, I too, that the broad claim of the paper is wrong." He said he agreed with another scientist's characterization of the paper as "sloppy," and added that "a set of experiments were done, probably sloppily, and others maybe were not done" -- which is one of the allegations under investigation by NIH and the Dingell committee. The same scientist also said he felt Baltimore and allies had sought to obscure the dispute about the paper by raising the "issue of Congress attacking science." He said he deplored this as "a misrepresentation on the public".
Another scientist, a member of the National Academy of Sciences who is on the faculty of a major university, told SGR -- also on a non-attributable basis -- that "Baltimore's extraordinary claim (in the Cell paper) is almost certainly wrong. The tragedy," he added, "is David's refusal to admit what anyone else would admit." Asked about assertions by Baltimore and several colleagues that the "central claim" of the paper has been replicated, this scientist said: "It's a goddam lie."

How come these anonymous scientists did not speak on the record? By definition, the anonymity they required at the time reflects a certain intimidation and even fear in the world of science. Other scientists (how many?) did not even allow such anonymous quotes from them, even though they might agree (contrary to those on the roster named above). Panels and courses cannot deal effectively with cases of intimidation, and in some cases panels have actually contributed to intimidation or to covering up. As Nature quotes Imanishi-Kari herself (27 September 1990, p. 317): "If OSI reaches the conclusion that there was misconduct on my part, then you have to conclude that MIT covered up and Tufts covered up." The OSI has now reached that conclusion in its Draft Report, and in this instance I agree with Imanishi-Kari.

On the other hand, after the NIH draft report, more scientists did come out on the record. I quote from two of them.

An open letter to an officer of the NAS

by John Cairns, Department of Cancer Biology

Harvard School of Public Health

(Published in Nature, 11 July 1991, p. 101)


(2) Nothing now is likely to stop the affair from progressing to its final disastrous conclusion, and I do not see how the authors of the paper can escape public censure at the very least. About the only question remaining is whether anyone will actually go to jail....
(4) Some of the blame falls on the scientific community - on those who arranged and conducted the initial, perfunctory inquiries - on the National Academy for not demanding a proper investigation - and on the many scientists who did not look at the evidence and, instead, construed the whole business as a Congressional manoeuvre to attack the scientific establishment. (I remember that originally I too felt that the row was probably a political stunt.)
(5) Because the establishment has played such an undistinguished role, we may find it increasingly difficult to maintain the idea that science is a genuine search for truth and that scientists are generally honourable and deserving members of society...
(6) So I believe that, although it [is] now too late to do much good, the Academy should be issuing a statement (a) reaffirming the aims of science and (b) pointing out that if the rules and principles of science had been observed we wouldn't now be in this mess. For most scientists, science is the pursuit of a truth that is external to our wishes. This truth is quite unlike the verdict of a court of law because it does not depend on advocacy. Instead, each of us has to be responsible for the accuracy of our own statements; we cannot simply count on others to correct our mistakes. Each of us knows more about our own experiments than anyone else, and when something goes wrong we have to speak up. If the Academy does not say something like that, American scientists may end up with the same kind of public image as many of the contry's lawyers and politicians - which would do a great disservice to all young scientists.

Commentary by Paul Doty

Mallinckrodt Professor of Biochemistry Emeritus

Harvard University

(Published in Nature, 18 July 1991, p. 183)

...Moreover, until the final OSI report is released, we will not know the extent to which the opposing views of the authors of the Cell paper will have affected final judgements. And the acceptance by the OSI draft report of compelling evidence for falsification of data may not be settled until there has been a court review. But in my view, the case for egregious departure from the usual standards of carrying out and reporting research stand independent of these remaining conflicts. The same applies to the succession of failures of reviews of the paper and the procedures used to address complaints against it once serious questions had been raised...
...Consider first a few of the lapses in scientific standards seen in the actions of various authors. The recording of data, especially by Dr. Thereza Imanishi-Kari, was so sloppy as to insult the scientific method. Reviewing the case strictly from Baltimore's published account reveals at least four lapses from what have been the traditional standards of science. He (1) failed to examine critically the quality and sufficiency of the data before publication; (2) failed to examine the data and report the possibility of error after serious criticisms were made; (3) instead organized an attack on his critics and discouraged publication of their views; and (4) did not subject the conclusions to further tests or check the reproducibility of what had been reported in a timely manner...
Baltimore's attitude towards the responsibility of authors checking the reliability of their own data is a critical departure from common standards...To forgo this obligation -- to leave to others the responsibility of establishing the validity of what you have published -- is not only a fundamental retreat from responsibility but, if it became accepted practice, would erode the way science works...
But the essence of change must come within the scientific community by its reassertion of its ability to police itself...
This challenge to readdress the fundamental tenets of acceptable behaviour in science comes at a time when the traditions of the scientific enterprise are under new threats arising from new stresses and temptations. The growth of the enterprise itself with its accompanying bureaucracy, the near cut-throat competition for grants, the possible corruption, on occasion of peer review, the growing number of cases of deception in scientific papers, scientists' acquiescence in the increasing avoidance of meaningful review in direct congressional grants for research buildings and projects -- all these contribute to the pressure to compromise and erode the high principles of the past. As a result the scientific community may already be experiencing a gradual departure from the traditional scientific standards; this could be abetted by condoning the behaviour seen in this present case. In this way we risk sliding down toward the standards of some other professions where the validity of action is decided by whether one can get away with it. For science to drift toward such a course would be fatal - not only to itself and the inspiration which carries it forward, but to the public trust which is its provider.


I have emphasized fundamental issues of scientific responsibility. However, factors of personal credibility have also been important in the resolution of the Baltimore case (as far as it goes, changing with time). I shall put here together a chain of events from May to December 1991 which led to a disavowal of Baltimore among an important segment of the science community.

Immediately after the NIH Draft Report in spring 1991, Baltimore and some of his co-authors retracted the Cell article, and Baltimore published a relatively long statement in Nature (9 May 1991), in which he praised O'Toole; he attributed his own failures to "an excess of trust" in a co-worker (Imanishi-Kari); he cited the inquiries at Tufts and MIT which had found no "deliberate falsification or misrepresentation" but only different "interpretations"; he mentioned the retraction of the Cell paper "in light of the revelations" of the OSI Draft Report; and he acknowledged the "legitimate role of protect the public interest and hold the scientific community accountable...". [More extensive quotes will be found in Appendix 16.]

Although Baltimore's statement was accepted at face value in some quarters, e.g. in the unsigned Nature editorial accompanying the statement [see Footnote 17 and Appendix 9], it lacked credibility in other quarters. For instance, Paul Doty in his subsequent Commentary in Nature observed that "the apology, although welcome, does not erase from the record the behavior that occurred and was defended over five years and omits mention of many other actions." Baltimore had stated in particular that he was "shocked and saddened by the revelations of possible alterations and fabrication of data". (19) However the New York Times article "Nobelist Apologizes for Defending Research Paper With Faulty Data" (4 May 1991, p. 1) reported: "Dr. Walter Gilbert, a Nobel Laureate in molecular biology at Harvard who has criticized Dr. Baltimore's behavior in the case, said that he found the tone of the report odd and disappointing, adding: "It reminds me of that moment in the movie Casablanca, where Claude Rains stands in the bar and says, 'There is gambling going on here? I'm shocked! I'm shocked!' There is very little admission in it."

Baltimore himself subsequently negated whatever admissions he had made when he replied to Paul Doty's letter in Nature (5 September 1991, p. 9). In that reply, Baltimore reaffirmed earlier positions putting the burden of justifying or verifying a paper not on the authors but on the rest of the scientific community, and in effect he retracted his own retraction of the paper when he said that his "science -- including the Weaver et al. paper -- is done with rigour and criticality...For the Weaver et al. paper, the data have proved more durable than the data in most papers...the science has stood up to the toughest test of all, the test of history." Baltimore also nullified his praise of O'Toole, when he wrote that Doty's judgment did "not depend on complete evidence" but that his "verdicts" were "based mainly on the unsubstantiated, and often refuted, allegations of one participant in events five years old." Baltimore's latest turnaround provoked Doty to question further Baltimore's credibility as follows (Nature, 10 October, p. 495):

Rather than replying in detail to David Baltimore's open letter to me (Nature 353, 9; 1991), I would suggest that interested readers compare his letter with my Commentary article (Nature 352, 183; 1991). The disconnection is nearly total. I stated: "Reviewing the case strictly from Baltimore's published account reveals at least four lapses...". Baltimore counters with: "...your verdicts are...based mainly on the unsubstantiated, and often refuted, allegations of one participant...". My statement is true, his is not... [Doty gives other concrete examples.]
...The part of my Commentary concerned with Baltimore dealt almost entirely with criticizing his behaviour and urging that it should not contribute to debasing past standards of conducting and reporting research. In his reply to me, Baltimore ignores this central theme and insists that he has always abided by the higher standards. This is the ultimate disconnection: alas it shows no sign of being bridged.

The role of Baltimore's personal credibility was especially important in his own institution. Baltimore accepted the Presidency of Rockefeller University in 1989. Even then approximately one third of the faculty, including Anthony Cerami (dean of graduate and postgraduate study), objected to his appointment publicly, and let their objections be known in the press. (20) During the next two years, two important faculty groups (one group headed by Cerami, and another group headed by Gerald Edelman, a Nobel Laureate) left Rockefeller University, and tensions mounted. On the other hand, during that same period, the trustees repeatedly and publicly asserted their confidence in Baltimore, expressing "unconditional support" as late as 25 November 1991. In October this confidence was accompanied by a gift of $20 million from David Rockefeller. However, a number of factors having to do with Baltimore's view of his own responsibilities and the destruction of his personal credibility vis a vis his colleagues led to his resignation as President of Rockefeller University on 3 December 1991.

This resignation was extensively reported in the press [see Appendix 18]. The New York Times described the vanishing of support for Baltimore, including the tendered resignation of Rockefeller's Vice President for Academic Affairs James Darnell. The four page article in Science "David Baltimore's Final Days" (13 December 1991, p. 1576) recounted in some details the final development of an essentially unanimous faculty against his remaining as President of Rockefeller University. The article also described some of the factors which influenced the faculty, especially the exchange with Doty in Nature, as in the following paragraph:

...Yet the exchange in Nature had a telling effect. A Rockefeller professor recently gave a glum summation of how Baltimore's reply influenced the faculty. "He even retracted his retraction...That's what made the faculty upset. They said, 'we can't support those arguments.' No one can defend this position. He was saying 'The paper still stands up as well as any other in the literature.' Do people believe that?..."

Thus finally some of the scientific grass roots reacted.

However, Baltimore persisted and the case did not end with his resignation, but rebounded in Summer 1992. I cannot give a better summary of this development than by quoting Science (17 July 1992, p. 318):

In a dramatic announcement that has brought a celebrated case of alleged scientific fraud back into the headlines, federal prosecutors...announced last Monday that they had decided not to bring criminal or civil charges against Thereza Imanishi-Kari...The prosecutors did not dispute the findings of the NIH investigation, but they said a criminal case based on those findings would have been too difficult to prosecute successfully.
Through her lawyer, Imanishi-Kari immediately declared herself vindicated. And Nobel Laureate and former Rockefeller University president David Baltimore, the Cell paper's most prominent coauthor, announced that he would issue a statement expressing confidence in the original paper, in essence retracting a retraction he issued in the spring of 1991 in the wake of publicity surrounding the NIH draft report...
Last spring, Imanishi-Kari's lawyer Bruce Singal commissioned a second forensic analysis by Albert Lyter, a forensics expert (and frequent expert witness) formerly with the federal Bureau of Alcohol, Tobacco, and Firearms. Lyter wrote an affidavit that the Secret Service conclusions "are not supportable by the test results or available data" because of what he called "a number of serious flaws" in the analysis...
The backlash. While Imanishi-Kari has decided to lie low for now (calls to her were referred back to Singal), Baltimore has taken a more aggressive tack. In an interview with Science, he said Lyter's analysis had "clearly discredited" the Secret Service evidence of fabricated data. "So far as I can tell, the [Cell] paper is a valid contribution to scientific discourse," he says. "The only thing that ever bothered me was that the Secret Service had evidence that purported to show criminal conduct, that [Imanishi-Kari] had somehow attempted to consciously fabricate data. It's now clear from the analysis of the Secret Service information that they have no such evidence." Baltimore says he plans a short letter to Cell that will set forth his new stance on the paper.
In so doing, Baltimore runs a risk of reopening the wounds of a scientific community that was already traumatized by the initial disclosure of the draft report. "My reaction to [Baltimore's unretraction] is probably unpublishable," says Nobel laureate Walter Gilbert..."It's such foolishness I can't believe it."...Gilbert says his reading of the science convinced him that "the paper was correctly withdrawn. Dr. Baltimore would be wiser to put the issue behind him." For better or for worse, however, Baltimore clearly has decided he can't take this kind of advice. (21)


The circumstances of the Baltimore case are extraordinary, involving extraordinary forces and pressures. They include the courage, stamina, and clear-headedness of Margot O'Toole as well as the independence of Dan Greenberg's journalism and Stewart-Feder. They include the influence of Dingell's Subcommittee to force NIH to investigate seriously. They include the Congressional Weiss Report documenting a dozen cases of scientific misconduct or worse. (22) They include an unfavorable press against science in many newspapers and magazines, causing concern in the top science establishment about the public image of science in the country. [For a brief list, see Appendix 19.] But these circumstances have illustrated and exposed problems which exist independently of these circumstances. The Baltimore case has only provided one concrete illustration of such problems. Among those problems is the way the scientific community at large exercises its responsibilities. As documented in the Baltimore case, in certain cases of challenges, some of those in power leave no alternative but to submit to authority or to escalate the challenge. The dynamics of this process are very clearly exhibited in the successive steps: the Tufts proceedings, the proceedings at MIT, the obstructions to publish via standard scientific journals, the first NIH panel, the Dingell hearings with the Secret Service forensic investigations, the OSI Draft Report, and finally the accounts in the press at large. Usually this escalation process stops early because those raising the challenge do not have the resources to engage in such an escalation, or because the circumstances do not afford an opportunity for such an escalation.

What to do about the problems which have been exposed by the circumstances of the Baltimore case? Ultimately, to uphold the traditional standards of science, scientists cannot rely on authority, they cannot rely on panels, they cannot rely on big-time certifications such as those coming from Nobel Prizes or the National Academy of Sciences. They cannot count on the press and they cannot count on Congressional committees to bring the problems of the scientific community to their own attention, or to police the scientific community. They must rely on individual responsibility, and they must create an atmosphere and conditions under which scientists, both young and established, can exercise this responsibility without fear -- fear of retaliation, fear for their careers, fear for their funding, fear for their publications, fear of the tensions which come from a challenge, fear of being uncollegial, whatever. Will they? (23)

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