The following appendices reproduce additional information, mostly quotes which were too long to be included in footnotes. Although the documentation may appear bulky to some people, I think it is essential that readers see the documentation so that they can form their own judgment.

Appendix 1. Testimony of Wortis (Tufts) to the Dingell Committee.

The following additional quotes, from the testimony given by Wortis to the Dingell Subcommittee on 9 May 1989, p. 255-256, will further help readers evaluate the Tufts investigation and conclusions.

MR. DINGELL. Well, when were you first aware of the existence of the June subcloning data?
MS. HUBER. We did look at subclone data in our first meeting with Dr. Woodland - Dr. Wortis and myself were present.
MR WORTIS. Let me add something on that because I can remember this very specifically. Again, I don't want to go down the road of science, but Dr. O'Toole had raised questions about the existence of the supernatants of the wells shown in Table 2 of some transgene product, and Dr. Imanishi-Kari said yes, but those were wells - those were not yet cloned, and therefore the reason that there is some transgene product is that there are several different cells and one of them is producing transgene and others may not be.
MR DINGELL. Does that mean that the data had been generated at that time?
MR. WORTIS. No, you can't do it then. Let me finish. So, we said yes, but what's important is whether those particular wells have been cloned, and Dr. Imanishi-Kari said yes, I've done those, and we said we would like to see that data, and at that point she began to cry and she said, you didn't believe me? You don't trust me? We said no. We want to see the data and she got out the data and we looked at it then.
MR. DINGELL. Did she get the data out right there?
MR. WORTIS. Right there.
MR. DINGELL. Well, maybe you can tell me when you became first aware of the existence of the June subcloning data. Did that occur at the meeting referred to?
MR. WORTIS. I don't know which June subcloning data you're talking about.

Appendix 2. Testimony of Eisen (MIT) to the Dingell Committee.

The question arises how thorough were the investigations at Tufts and MIT (whatever that means), and to what extent they took into account the possibility of fraud. Within minutes after the Eisen statement quoted in text, in his testimony to the Dingell Subcommittee on 9 May 1989, we have the following exchange with Dingell (p. 291):

MR. DINGELL. ...Did the inquiry ever review the data, Dr. Eisen?
MR. EISEN. I think you really asked me whether the inquiry ever looked at notebooks.
MR. DINGELL. Did you look at the notebooks?
MR. EISEN. I did not look at notebooks.
MR DINGELL. Did you know at the time that you were inquiring into this matter whether all of the experiments which were purported to have been made were in fact made or not made?
MR EISEN. No, I did not know that, and I couldn't have known that, and in fact the question was never raised. That whole question of experiments not having been done was not raised by Dr. O'Toole or until very recently so far as I know.

Compare Eisen's testimony, especially his assertion that O'Toole did not raise questions about experiments not having been done, with Margot O'Toole's memorandum to Eisen dated June 6, 1986. In that memorandum she specifically referred to the fact that the "hybridomas of Table 2 were not checked for isotypes other than mu", contrary to what was claimed in the paper; she also went on: "the statement on page 250 that these hybridomas express gamma 2b is based on an analysis of a number of hybridomas from another fusion". [See Footnote 4 accompanying the Eisen testimony quoted in text.]

Compare Eisen's testimony also with that of MIT's Provost John Deutch, testifying the same day (p. 299):

MR DINGELL. Well, Doctor, we have the situation where at first she didn't even raise a question of fraud, and she found it dangerous. All she said is there's error.
MR. DEUTCH. Her inquiry was treated in a very serious way because it clearly had attention both with regard to whether some mistakes had been made in the paper which hadn't been acknowledged and, in addition, as has been mentioned several times here, it suggested that there was a possibility of misconduct.

Since Eisen stated that he "did not look at the notebooks", the question arises as to what Deutch means when he says that "her inquiry was treated in a very serious way". Also take note of Deutch stating: ". . . as has been mentioned several times here, it suggested that there was a possibility of misconduct" - which gives additional evidence that Baltimore's version in Issues in Science and Technology was misleading.

Appendix 3. The first three NIH reviews of the Stewart-Feder paper.

I quote the three reviews of the Stewart-Feder paper for NIH. These reviews document the refereeing process, and show how the possibility of fraud occurred to the reviewers even though the paper by Stewart-feder was phrased in factual terms. I find the reviews sufficiently important to reproduce them in full.

Reviewer #1. As requested by you, I have reviewed the manuscript by Stewart and Feder and also the paper by Weaver et al. Stewart and Feder claim to have obtained copies of laboratory notebooks containing data which fails to support the published claims of Weaver et al. and to have used this unpublished data to analyze the Weaver et al. paper. If one accepts that the unpublished data is correct, then the conclusions of the Weaver et al. paper appear to be in doubt. However, I have no way of knowing whether or not the unpublished data they claim to have obtained is valid or bogus. Since the Stewart and Feder paper leans heavily on unsubstantiated data, I cannot recommend its publication at this time. However, the Stewart and Feder paper does raise serious issues of scientific fraud. Therefore, they or their colleague who brought them the unpublished data should bring this matter to the attention of the appropriate authorities at M.I.T. and Columbia and/or to the granting agencies that supported the published work.

Reviewer #2. Thank you for the opportunity to comment on the subject manuscript. I believe that it should be approved for submission to an appropriate journal if the authors can show reasonable evidence that the seventeen pages of laboratory records are what they seem to be. That is, I believe your clearance should be withheld until the authors (1) have shared the thrust of their findings with Dr. Weaver and/or Dr. Baltimore (along with copies of the seventeen pages), (2) have received a response, and (3) have made appropriate revisions if any, in the subject manuscript. On the one hand, Weaver et al may have laboratory records or other information that show the subject manuscript to be insignificant, incomplete, or invalid. On the other hand, the comments from Weaver et al may enhance its quality and significance.

Reviewer #3. This is a very unusual manuscript. The authors state at the outset that it represents an "internal audit," but they never state where they obtained the "internal" information. Since neither of them is an author on any of the papers involved, one must assume that the laboratory data examined was obtained from someone else in the laboratory (presumably O'Toole). However, in the absence of a specific statement concerning the source of the data analyzed, it is impossible to assess its authenticity. In this regard, the reader is placed in the same position as the receiver of an anonymous phone call! I would not expect any reputable journal to accept the paper under these circumstances.

If the data are authentic and correct, they indicate that mistakes were made in the analysis and interpretation of data, and that the validity of the conclusions in the resulting paper may have to be called into question. For example, Tables 1 and 2 in this manuscript are said to represent the published and the raw data versions of the same experiment, but are clearly discrepant. Numerous other discrepancies are also pointed out by the authors. However, there is no way for the reader to know that there are not valid reasons for these discrepancies. For example, one alleged discrepancy involves the reactivity pattern of a reagent (Bet-1). The data shown as "notebook data" indicate no difference in the binding of this reagent to mu-a and mu-b. But since the specificity of this reagent has apparently been confirmed in other laboratories, I would imagine that a more likely explanation for the failure to report this data would have been that the authors repeated the experiment elsewhere in their notebooks and found that the experiment in question had been the subject of an interpretable experimental error.

All of these discrepancies and mistakes are specified out of context in the present manuscript, and I would hesitate to evaluate any of them without first hearing the explanation offered by the original authors. I feel that it is impossible to adequately review the science of this manuscript without such considerations.

Appendix 4. Baltimore's position: testimony to the Dingell Subommittee.

Baltimore repeated his position in his testimony to the Dingell Subcommittee, 4 May 1989 (p. 102). He also stated:

The proceedings here today indicate that the Subcommittee wishes to do away with the standard criteria and substitute a whole new standard for judging science. They have chosen a prosecutorial style. The message is to do your science with an eye towards facing prosecution of the style of your science. The order of pages in your notebook will be a primary concern. Never overwrite a date or add a page or the Secret Service will catch you. We could call this the Sovietizing of American science except that the Soviet Union has seen the errors of its past and is moving to a more American style. If the hearing here today represents the Congressional view of how science should be done, then American science is in trouble. Science will become an enterprise based on form, not substance. Young people will be afraid to be audacious for fear that they will be prosecuted for transgressing orthodoxy.
Having said that the appropriate form of judging science is replication and the foundation of further progress, how well has the 1986 Cell paper fared in the 3 years since it appeared? Very well! No result of the paper has been proved wrong, a number have been replicated and there has been significant progress building on the foundation of its results. Because this is the heart of the matter in question, in an appendix I show how five papers published since the Cell article appeared have supported its conclusions.
Why has a Congressional Committee tried to define this new and pernicious form of scientific verification? The answer, I believe, lies in the presence of one man on the Subcommittee staff, Mr. Walter Stewart. In his paper on the Darsee affair he first developed the notion of an "internal audit" of scientific records and in his first letter to me, in December 1986, he said that his goal was to use this paper as a test case of his methods. In May of 1989 we are seeing just what he meant and it makes me proud that when I first saw his request, I resisted it as a destructive interference in the scientific process." [The testimony continues as in footnote 6.]

Appendix 5. Second set of NIH reviews
of the Stewart-Feder paper.

I quote below a large portion of the second set of reviews of the Stewart-Feder paper for NIH.

Reviewer X. I have studied the extensive documentation provided by Feder and Stewart in support of their request for approval to submit their manuscript. The same discrepancies between laboratory notebook data and published data are pointed out, and this time supported with copies of the original notebook pages. However, I still find it impossible to determine from the information provided whether or not there may be valid reasons for these discrepancies. Such reasons would include additional experiments elsewhere in the notebooks, and only a detailed analysis of the notebooks along with the authors who made the interpretations would permit an evaluation of whether or not those interpretations were justified.
Regardless of the possible validity of the arguments raised by Feder and Stewart, I do not think that the scientific literature is an appropriate forum for the resolution of such issues. The entire matter should be referred to an appropriate impartial committee at the institution in question (it is unclear to me whether or not this is what has already been done at MIT). The authors and the scientific community should then be willing to accept the judgment of such a committee. If a further publication clarifying the issue is deemed necessary, it should come from the authors and not from a third party.
I hope these comments will be useful to you in your deliberations.

Reviewer Y. ...The manuscript by Stewart and Feder makes several valid points concerning the manuscript by Weaver et al. that was published in the journal Cell... [Follow several such technical points.]
Having said that certain valid points are made in the Stewart and Feder manuscript, I still cannot recommend its publication. It must be asked what positive purpose would be served by exposition of these possible lapses in a manuscript from the laboratory of a famous scientist. What actions would follow publication of such a manuscript?...
It is my opinion that the possibility is remote that anything more than some misguided enthusiasm on the part of junior staff and sloppy editorial procedures on the part of senior staff is involved here. It is not worth the time or the expense to expend more effort on cataloging the flaws in the Weaver et al. manuscript. It would seem that better examples of fraud than those given in the present manuscript could be found by those interested by such pursuits.

Reviewer Z. This is in response to your request for comment on the subject manuscript.
1. Despite oral claims by Feder and Stewart to the contrary, the subject manuscript alleges serious misconduct by Weaver et al. Assessment of the validity of the allegations is complicated by (a) the uncertain significance of 17 pages of Weaver's laboratory records, of which Feder and Stewart have a copy and (b) Feder's and Stewart's failure to gain the cooperation of Weaver et al regarding the issues raised in the subject manuscript. On the other hand, the specificity of the allegations and the detailed supporting rationale suggest that Feder's and Stewart's adverse findings are readily testable.
2. In view of the seriousness and specificity of the allegations and the fact that the subject manuscript, in various drafts, already has been shared with many scientists outside the NIH, action by the Office of Extramural Research (OER) is indicated to resolve the matter, if possible, in an equitable and publically [sic] visible way. At the least, this means some fact finding to establish the relevance of the 17 pages of laboratory records and the view of the responsible scientists and institutional officials. At most, OER may need to conduct a formal investigation.
3. While the OER inquiry/investigation is in progress, no further action seems warranted regarding the request by Feder and Stewart to submit the subject manuscript for possible publication. Once the OER process has been completed and its findings made a matter of public record, an appropriately revised or updated version of the subject manuscript might merit your clearance for submission to a journal.

Appendix 6. Testimony of Joseph Davie to the Dingell Committee.

I quote an exchange from the testimony of Joseph Davie at the Dingell hearings, 4 May 1989 (p. 16).

MR. CHAFIN. So they described an experiment that was not done.
MR. DAVIE. That's correct.
MR. CHAFIN. Is that misconduct?
MR. DAVIE. I believe it is misconduct. I believe that we also recommended that that be corrected in a subsequent --
MR. CHAFIN. Was it corrected?
MR. CHAFIN. Did you say misconduct in your report?
MR. DAVIE. We called it a serious error.
MR. CHAFIN. In an earlier draft, it said that there was no fraud, misconduct, and, I believe several other things. I think you actually struck out the word misconduct. You were saying there was no fraud and, I guess, saying there was misconduct. What happened to that? You were the chairman of the panel.
MR. DAVIE. We obviously discussed how to describe these problems.
MR CHAFIN. I understand.
MR. DAVIE. In English. And while I believe everybody understands what was done or what wasn't done, how you describe it is not so easy. You may call it misconduct. I cannot argue with that. Yes it's misconduct. Any time one describes something that's not accurate, that's not right. That's misconduct.
MR. WYDEN. Mr. Chairman?
MR. DAVIE. But we called it a serious error. It is a subtlety. I'm not sure I can defend it at this juncture.
MR. WYDEN. Dr. Davie, if you believe it was scientific misconduct, why wasn't it described as scientific misconduct in the report?
MR. DAVIE. If you call misconduct an intent to deceive or to do wrong, that's a problem. That's clearly misconduct. It was not possible for us to be sure that they intended to deceive in that way...
MR CHAFIN. Were you ever asked to look at intent by Dr. Wyngaarden or as part of your charter?
MR. DAVIE. Part of our charter was to deal with whether there were data in the data books that fit the data in the Cell paper and whether the conclusions were correct.
MR CHAFIN. Right. So there wasn't any look for intent--
MR. DAVIE. Right.
MR CHAFIN. So you're saying then that you conduct an investigation and, in terms of putting it into a certain category, you need to know the intent, but you're not asked to look for the intent. It's an interesting catch-22.
MR. DAVIE. That's correct...

[The above exchange occurs on page 16 of the hearings; but on page 28 we find:]

MR DAVIE. We talked about that before when Mr. Chafin was addressing that issue. I really gave misinformation. Part of the charge of the Committee was to come forward with an opinion of whether misconduct has been perpetrated in generating that information. So we were asked by the NIH to come forward with our opinions of whether misconduct was involved. Our impression that is misconduct means intent.
MR. WYDEN. Was it your opinion that there was misconduct in this area, Dr. Davie?
MR. WYDEN. Pardon me?

Appendix 7. Minority Opinion of the OSI Draft Report.

The Minority Opinion stated that some of the major conclusions are "not justified" in their judgment. They stated: "In each of these sections [to which they object] the findings are open to several alternative interpretations, and depending on what scenario one considers most likely, the interpretations can be radically different. While the inconsistencies which are cited in these sections are certainly disturbing, and are compatible with the conclusions given in the report, alternate scenarios are sufficiently plausible that we cannot agree with the conclusions as stated in the report." However, as Margot O'Toole wrote in a reply to OSI (printed in Nature, 16 May 1991, p. 182), they "do not describe a single alternative scenario that could explain away any of the evidence compiled by OSI. I therefore consider it imperative that the minority opinion be amended to include the scenarios that Drs. McDevitt and Storb believe are plausible explanations."

The Minority Opinion also objects to the "statistical analyses" as "new and untried", and they do not agree with conclusions based on such analyses. They do, however, state: "The second line of evidence presented in Sections IV A&B [of the OSI Draft Report] is much more convincing." [This evidence concerns forensic analyses.] They express one reservation about not having been given "access to the actual chromatograms which led the secret service to make the conclusions referred to above", but "with this reservation, the findings as stated, combined with the other inconsistencies found on the pages referred to above, make it seem likely that the data on these pages are not the result of experiments performed at or near the time stated, but in fact are data from other experiments performed as much as three years earlier. The significance of these data, their relevance to the initial and subsequent investigations, and the corresponding reasons why these data are legitimate targets for the present investigation, are all well described in the report, and we are in agreement with that description. "

Finally, the Minority Opinion states that the general conclusions concerning David Baltimore, David Weaver, and Margot O'Toole "do not accurately reflect our own conclusions", but they do not state specifically in what respects, and they do not state "their own conclusions". In her reply to OSI, Margot O'Toole requested that the Minority Opinion be amended to give reasons for their dissent.

I remind readers that McDevitt and Storb were the two members of the first NIH (Davie) Panel, besides the Chair. Words of praise for Margot O'Toole were deleted from a draft of the Davie Panel Report, and did not appear in the final version. Dingell inquired about this at the hearings of 4 May 1989. I reproduce most of the relevant exchange (pp. 39-42):

MR DINGELL. Now, Dr. Wyngaarden [Director of NIH], why was it in the NIH final report that there was no mention of your views with regard to the behavior of Dr. O'Toole, expressed here this morning by you and your associates, [that] her behavior throughout this matter was entirely correct?
MR. WYNGAARDEN. Well, I can't answer for you the sequence of that comment being in an earlier draft and not in the final, but it was not with - I'm sorry?
MR DINGELL. Well, in an early draft of the NIH report, there were such comments about Dr. O'Toole, but they appear to have been excised before the report was finished, because they do not appear in the final draft. You are aware of this, are you not?
MR. WYNGAARDEN. Yes, I've heard that. I -
MR DINGELL. Why were those comments with regard to Dr. O'Toole's behavior excised from the report?
MR. WYNGAARDEN. All I can say is that I did not excise them. I do not know.
MR. DINGELL. [To Joseph M. Davie, Chairman of the investigating panel] ...Why were they excised?
MR. DAVIE. I cannot answer that. I do not know.
MR. DINGELL. ...Were those kinds of comments incorrect or inappropriate in a report of this kind?
MR. DINGELL. No, but they got removed. Did the removal occur after these matters left the panel or before?
MR. DAVIE. I believe it occurred before. Again--
MR DINGELL. ...So the panel then removed them?
MR. DAVIE. I believe that's correct.
MR. DINGELL. As Chairman of the panel, why were these remarks removed?
MR. DAVIE. ...We're saying that we do not have a good explanation for why that specific reference was removed.
MR DINGELL. Did anybody on the panel take them out? Did you take them out? You were the chairman. Did you taken them out, Doctor?
MR. DAVIE. I'm not sure.
MR. DINGELL. Well, did you take them out or not? Obviously, if you did, you would know.
MR. DAVIE. This was a report, a draft that was --
MR. DINGELL. Did you take them out? Yes or No?
MR. DAVIE. I do not know, sir.
Mr. DINGELL. [To panel member Ursula Storb] Dr. Storb, did you take them out?
MS. STORB. I do not - I did not take it out. I'm quite sure.
MR DINGELL. Do you know who did?
MS. STORB. I was actually - I heard yesterday about this statement is -
MR. DINGELL. Do you know who did?
MS. STORB. [continuing]. Not in the report. It's a surprise to me, but, I'm sorry, I cannot offer any explanation as to how it was -
MR. DINGELL. [To panel member Hugh McDevitt] How about you, Doctor, do you know who took them out?
MR. McDEVITT. I did not take them out and it was my oversight and I guess all of our oversight that we did not notice they were taken out and insist that they go back in.
MR. DINGELL. Did anybody take them out?...
MR. McDEVITT. Since the whole thing was done in the central NIH office, it could have been done by any one of a number of people who...
MR. DINGELL. Could it have been done by some person other than a panel member?
MR. DINGELL. That's a curious way for a panel to work. Did the panel write the report or did somebody else write the report?
MR. McDEVITT. We clearly wrote the report.
Mr. DINGELL. ...The early drafts had laudatory remarks about Dr. O'Toole and subsequent reports lacked them. Now, why?
Mr. DAVIE. You're simply asking questions that we really did not address in our review of this. You're talking about early drafts of the substance. We can't really recall.
Mr. DINGELL. You were an independent panel, but the NIH staff then edited your work, is that what you're telling me?
Mr. DAVIE. They helped us in the editing of the final draft....
Mr. DINGELL. Dr. Wyngaarden, how is this an independent panel which has its work edited by the NIH staff? Is that the way your independent panels function out at NIH?
Mr. WYNGAARDEN. The drafts were reviewed internally, and there were some editorial suggestions. I have a list of them, if you're interested in them.
Mr. DINGELL. Well, none of the panel remembers getting this editorial suggestion. None of them knows who made the change. They've indicated to me that this whole report was edited by NIH's staff.
Mr. DINGELL. ...Now, I'm trying to figure out if this is the way you function with your independent committees which are assigned specific responsibilities at NIH...
Mr. WYNGAARDEN. ...I'm not aware that any of the NIH staff changed any of the content of the report.
Mr. DINGELL. Well, nobody knows who changed it. They say that the NIH staff reviewed. They don't remember doing it. That means that it must have been the NIH or some other person, perhaps somebody in the dark of night. I'm just trying to find out how, and what is the integrity of these panels that you set up.

Appendix 8. Further statements by Dingell.

I reproduce here some more technical aspects of Dingell's statement opening the hearings of 14 May 1990. Part of his statement ran as follows (p. 92).

The key notebook furnished by Imanishi-Kari was indeed a curious sight. It contained pages bearing counter-tapes that had obviously been moved from their original positions, sliced into small pieces, and remounted. The pages showed a number of careful alterations that changed the meaning of the experiments and a number of carefully altered dates. Finally, the notebook purported to document some extraordinary experiments -- experiments far better than those the authors had chosen to publish.
To clarify the meaning of these suspect records, the Subcommittee asked the Secret Service to conduct an objective analysis of the key notebooks. Their results indicated that the records had not been created at the time claimed...
Confronted with the Secret Service evidence in May of 1989 that the inks, the paper, and the impression analysis of her laboratory notebooks established convincingly that many pages were prepared in 1986, after the challenge to the paper, Dr. Imanishi-Kari admitted for the first time that much of the key notebooks had, in fact, been prepared in 1986. However, she continued to assert that the counter-tapes were strictly contemporaneous with the experiments...
Dr. Imanishi-Kari and her attorney have repeatedly claimed that they have not been informed of the NIH's allegations against her. These statements are simply false. In a letter of February 1, 1990, from Dr. Hadley, then Acting Director of NIH's Office of Scientific Integrity, to Dr. Imanishi-Kari, Dr. Hadley detailed three charges that constitute the focus of the OSI investigations:
(1) The possibility that substantial portions of the claims related to the immunological aspects of the Cell paper were not supported by proper experiments and reliable data at the time of the paper's submission;
(2) the possibility that after the problems with the paper were brought to light, there was systematic fabrication and falsification of data to support the pages; and
(3) the possibility that falsified and fabricated data regarding immunological aspects of the paper were included in representations to the National Institutes of Health and in published letters of correction to the 1986 Cell paper.

Appendix 9. Nature editorial of 9 May 1991.

The series of exchanges in Nature (May to October 1991) started after a journalistically questionable prelude. First on 9 May 1991, Nature printed a statement of contrition by Baltimore. It was accompanied by an unsigned editorial, entitled "The end of the Baltimore saga" (p. 85), followed by the comment:

One of the most corrosive disputes of recent years in the research community should be ended with the open acknowledgment of the errors of an excess of trust by the principal in the case . . . . There is some unfinished business, but one thing is clear: Baltimore has said enough to restore his own reputation as a fine scientist, a man of public spirit and potentially superb and certainly imaginative president of an outstanding and distinctive research university. Some among his colleagues may be tempted to use this public acknowledgement of error by their leader as an excuse for furthering their own narrow causes, but they should instead reflect on what Baltimore's ingenuity may eventually accomplish for their institution. To make an error may reflect on a person's judgement, but to confess it in the circumstances in which Baltimore now finds himself is a mark of courage. He deserves a break...

The Nature editorial is tendentious on several counts, one of them being the innuendo questioning the motivation of those who had specific criticisms of Baltimore's position throughout the affair ("may be tempted..."). Aside from that, Nature had to reverse its position, because the very next week in the issue of 16 May, it printed "Margot O'Toole's record of events" (p. 180), with the comment: "The Baltimore saga continues. These excerpts from Dr. Margot O'Toole's comments on the recent draft report by the US NIH's Office of Scientific Integrity contradict at several points last week's statement by Dr. David Baltimore."

For still another reversal by Nature, see the editorial Baltimore's Defence of 10 October 1991 (p. 484), quoted in Part V, §3, and the comments in Footnote 17; and for other implications of Baltimore's statement, see Part VI and Appendix 16.

Appendix 10. Policing science: the Baltimore position.

In his article "Baltimore's travels" (Issues of Science and Technology, Summer 1989), Baltimore wrote on the policing of science, by describing what he says is being done at the Whitehead Institute of MIT, and he suggests the following procedure as a model (p. 53).

Policing science
-- A question about the possibility of scientific misconduct can be raised by anyone in an entirely confidential manner.
-- Once a question has been raised, the director [of the Whitehead Institute] appoints a committee of inquiry, composed of appropriate and knowledgeable people; selections are made confidentially...
-- Both at the outset of an investigation and after it has been concluded, funding agencies are fully informed.

Baltimore's emphasis on "misconduct" is misleading. I object to Baltimore's way of setting up alternatives, involving "misconduct" and legal terminology as he does ("fraud", "verdict", "accuser", "accused"... see p. 54 of his article). The original questions by Margot O'Toole did not deal with "misconduct" but with the existence of data concerning an experiment, the need to publish a correction, and the refusal to publish a correction. Similarly the paper submitted by Stewart-Feder to Cell dealt with questions of scientific fact and was making a correction, but was not accepted for publication. Baltimore does not address himself to the situation at hand.

Who decides what is "appropriate"? Who is "knowledgeable"? Who determines what constitutes "misconduct" and when? In the Baltimore case, different committees have arrived at different conclusions at different times. For instance, in 1988-1989 the NIH had appointed the Davie panel to look into the objections raised about the Cell paper. That panel came to the conclusion that "no evidence was found of fraud, misconduct, manipulation of data, or serious conceptual error..." It actually turned out that the paper was contaminated by what the subsequent NIH Draft Report did find. Even the minority report accepted the existence of problems.

Why the confidentiality when questioning scientific results? Why inform only funding agencies? The scientific journals are read potentially by all scientists. I think it is entirely legitimate to raise questions about the public availability of data, and to hold scientists accountable to themselves and to the public. Agencies outside the scientific community such as the Dingell Subcommittee got involved because the scientific avenues for resolving scientific questioning turned out to be clogged and could not be trusted by some scientists. As far as I am concerned, only open exchanges within the scientific community can legitimately evaluate conduct.

Appendix 11. A Nature editorial on OSI.

The situation dealt with in the Nature editorial of 15 August 1991 involves a morass of conflicting statements. Culliton, speaking of Suzanne Hadley (former acting director of OSI), wrote (p. 563): "Hadley's organizing principle for OSI has been that if someone sees all of the evidence, he or she is in a better position to explain it away. Better to keep the allegedly damaging data secret, available to the accused only in summary form." On the other hand, Hadley answered in a letter to Nature (19 September 1991, p. 204): "This assertion is flatly incorrect. I always followed PHS Policies and Procedures...which state that subjects of an inquiry or investigation "are provided access to any research data under review...[and] are provided with an opportunity to review and comment on significant investigatory documents...". Culliton also wrote that "...OSI's definition of due process...expressly denies the accused the right to see at first hand all of the evidence against him or her." In her letter to Nature, Hadley replied: "As I have said this assertion is not correct. The only instance of which I am aware in which there was any departure from PHS policy occurred when the OSI did not have possession or control of certain pieces of evidence." Culliton then commented (19 September 1991, p. 204): "Why, if damaging data are so faithfully provided, do so many scientists and their lawyers complain of secrecy?" Such a question is a rhetorical thrust, which is not a substitute for documentation.

On the one hand, Hadley's letter was misleading in one respect. As pointed out in a letter from Philip Siekevitz to Nature (Vol. 353, 17 October 1991, p. 597), the text of the Federal Register does put a limitation on what subjects of an investigation are provided with to review and comment, namely "documents identified by OSI unless such disclosure would violate individual confidentiality or significantly impair the investigation...No opportunity is provided for subjects to confront and cross-examine other witnesses interviewed by OSI."

On the other hand, what precisely was withheld and by whom? Nature itself reported more accurately (2 January 1992, p. 6): "Imanishi-Kari has refused to comment on the draft report (beyond an attack on the overall process) until she is allowed to see the original laboratory notebooks on which OSI and other federal investigators carried out the forensic analysis that led them to conclude that data had been fabricated. Many of those notebooks, however, are in the hands of the US attorney, who has declined OSI's repeated request to turn them over to Imanishi-Kari. If a grand jury reaches an indictment, a legal process known as 'discovery' will allow Imanishi-Kari and her lawyer to examine the data. Until then, OSI considers its hands tied." This sort of concrete information partly answers Culliton's rhetorical question, and puts a different light on OSI, confirming Hadley's assertions.

With respect to open hearings, Margot O'Toole gave the following testimony to the Dingell Subcommittee concerning the Davie Panel investigation, not the OSI investigation (9 May 1989, p. 201): "From my perspective the NIH investigative process has been flawed in a number of important respects....Another flaw in the NIH process is that it does not allow for challengers to see evidence...In my case I asked to be allowed to examine certain data, but the NIH released the report before the data was sent to me... We are scientists and we should examine data...A scientist is one who analyzes facts in order to reach conclusions. We should always examine the evidence to support our claims, and we should be able to do so in a collegial fashion. That we have lost the ability to do this indicts us all. In my opinion, it is for this reason, and this reason alone, that these hearings have become necessary."

Appendix 12. OSI Director Jules Hallum on open hearings.

For comments on OSI procedures from the point of view of OSI people, and the problems of what constitutes "protection" of subjects on whatever side of an issue in such an investigation, I recommend an interview in Dan Greenberg's Science and Government Report (1 October 1991), with OSI Director Jules Hallum, Deputy Director Clyde Watkins, and Senior Scientist Alan Price. Hallum states, among other things (p. 6):

What some of them are asking for, and they don't know the consequences, is an open hearing kind of investigation. That's this due-process consideration. I think that's going to be very dangerous to science...There will be no protection for the whistle-blower, no protection for the reputation of the respondent. And another thing they haven't thought about is that if we're forced to that, then our procedures are the same as practically all the university [misconduct] procedures in the country. And then will less be expected of the universities, or will they have to go to an open court-like hearing, as well? I suspect they will. The criticism that makes me the most angry was the charge that we inhibit creative, new, and innovative research. That was a damned lie. I challenge the head of that society to show me one case where we have inhibited research. He said we're teaching the young scientists to do only safe science, because they're so terrified of being investigated by us for doing something original. Why aren't they terrified of the local organization?...

Appendix 13. The NAS pamphlet On Being a Scientist.

Under the heading "Upholding the Integrity of Science", the NAS pamphlet states:

Perhaps the most disturbing situation that a researcher can encounter is to witness some act of scientific misconduct by a colleague. In such a case, researchers have a professional and ethical obligation to do something about it. On pragmatic grounds, the transgression may seem too distant from one's own work to take action. But assaults on the integrity of science damage all scientists, both through the effects of those assaults on the public's impression of science and through the internal erosion of scientific norms...
Responses by the accused person and by skeptical colleagues that cast the accuser's integrity into doubt have been all too common, though institutions have been adopting policies to minimize such reprisals...
Accusing another scientist of wrongdoing is a very serious charge that can be costly...A person making such a charge should therefore be extremely careful that the claim is justified. One of the best ways to judge one's own motives and the accuracy of a charge is to discuss the situation confidentially with a trusted, experienced colleague.

Readers can compare this rhetoric with the reality of attacks on Margot O'Toole by scientific big shots and the closing of ranks behind Baltimore. After she brought up her objections to the Cell paper, she was dismissed from the laboratory, did not get the position she was promised at MIT, and could not get letters of recommendation. Cf. her testimony to the Dingell Committee quoted in I §1. In practice, she could not rely on "a trusted, experienced colleague", namely her own thesis advisor or Mary Rowe at MIT.

The NAS pamphlet is also questionable in suggesting that one should "judge one's own motives" when raising questions about scientific claims. As far as I am concerned, what matters is the accuracy of the science, and the scientific responsibility, not the motives.

Appendix 14. The "mentor system" and the "corruption" of unearned authorship.

Concerning the "mentor system", brought up in Part V, §4, I quote from a letter to Nature (12 September 1991, p. 104) by Louis DeFelice, Division of Biology, Caltech:

John Maddox (Nature 350, 269:1991 [28 March 1991]) asks why a scientist like David Baltimore should have so vigorously defended what has now proved to be a false position...As a scientist saddled with the aftermath of a parallel scandal, the Darsee affair, I wish to suggest a possible answer: researchers routinely accept a certain level of dishonesty and therefore defend larger transgressions that involve the same vice. The particular corruption that I speak of is unearned authorship.
...Because of administrative or monetary relationships between senior and junior scientists, marginal contributions may be elevated to authorship.
Earned authorship in scientific papers means doing the experiments, analysing the data, working out the theory, writing the paper, reading the literature...Merely encompassing the work under the umbrella of one's interest and ideas does not.
Why do scientists expose themselves in this way? For one thing, putting one's name where it does not belong is rewarded by granting agencies and tenure committees...
At Emory University, during the investigation of the Darsee affair, the argument was made that junior scientists cultivate senior co-authorships in order to get their work published...Regardless, this argument puts the blame on the privates and lets off the generals. Established scientists, under pressure to obtain extramural funds, are burdened with the baggage of success: leadership in national societies, membership of editorial boards and grant review panels, travel and lectures, committees and administration. These activities drain the time and the energy of every established investigator, and they make bench research nearly impossible. Yet the pressures to present oneself as being at the vanguard of research are greater than ever.
By accepting or insisting upon unearned authorship, much of the scientific community has forfeited the right to bear witness. Thus when investigations reveal unbecoming conduct that involves the same crime, scientists close their ranks, because many are guilty of far less spectacular but similar infractions.

Appendix 15. More of Bernard Davis' position.

In a Commentary (The Scientist, 13 May 1991), entitled "Is the Office of Scientific Integrity Too Zealous?", Bernard Davis also wrote (p. 12):

While it is necessary to strengthen the NIH mechanisms for dealing with fraud, the existence of two offices, for a function that could well be performed by one, wastes both money and time. More disturbing than their structure is the broad mandate of these new offices, which instructs them not only to monitor and conduct investigations of misconduct but also to "promote high standards of laboratory and clinical investigations in science through a prevention and education program." This phrasing is fraught with possibilities for encouraging the government to mix problems of misconduct with problems of quality in the conduct of research...Another concern is that the mission of these offices is now being pursued with excessive zeal...I conclude that the new offices have become grotesque in their evident aim of purifying science root and branch, without recognition that the cure would do more harm than the disease...Though NIH enjoys a respected and even affectionate relationship with the scientific community, its overreaction to political pressure in combating fraud threatens the welfare of science on a much wider scale.

Bernard Davis has also published elsewhere in the press at large, as in the piece "More than a test-tube tempest", Los Angeles Times (10 December 1991, p. B5), where he iterates his distrust of government intervention "in dealing with scientific fraud", and casts aspersions on the credibility of OSI and Margot O'Toole. For instance, he writes: "Excessive reliance on O'Toole's sincere but often-contradicted testimony certainly contributed to the conclusion by the Office of Scientific Integrity of the National Institutes of Health that Baltimore's collaborator, Thereza Imanishi-Kari, had committed fraud..." Readers of the present article can compare the documentation with the tendentious phrase "sincere but often-contradicted".

Appendix 16. Baltimore's statement of contrition in Nature.

I quote several passages from Baltimore's statement of contrition in Nature (9 May 1991, p. 94).

Dr Baltimore says "sorry"

Dr. Baltimore says he had no knowledge of the fabrication of data in a paper in Cell of which he was a co-author, says he will work to develop new guidelines for misconduct and apologizes to Dr. Margot O'Toole.

...I wish to state at the outset that my defence of Imanishi-Kari was not due to any lack of regard for Dr. Margot O'Toole, the postdoctoral fellow who first uncovered certain discrepancies in Imanishi-Kari's research. I have tremendous respect for O'Toole, personally and as a scientist, and I have consistently maintained that I believe that her analyses were insightful, her expressions of concern were proper and appropriate, and her motives were pure. Rather, my defence of my co-author was fuelled by my respect for Imanishi-Kari's demonstrated abilities as a scientist, by my belief that the paper's scientific conclusions were sound, and by my trust in the efficacy of the peer review process...
Those experts [at Tufts] concluded in June 1986 that there was no evidence of deliberate falsification or misrepresentation and characterized the availability of alternative interpretations of the data as "the stuff of science". A later review at MIT reinforced that conclusion. The expert there found that O'Toole had correctly identified a minor error, but explained that the error was too insignificant to warrant a retraction in the light of "a substantial body of other data that is "clear and impressive". The MIT report echoed the sentiments of the Tufts reviewers and noted that "other issues raised by Dr. O'Toole, which are largely matters of interpretation and judgment, are best dealt with by allowing the scientific process to take its course...
In good conscience I feared a rush to judgement, and I accorded my colleague the benefit of every doubt. 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 acknowledge that, for too long, I focused narrowly on the question of whether the paper could stand...
...I am shocked and saddened by the revelations of possible alteration and fabrication of data...Science must be an objective search for truth. It was my belief in science and faith in my fellow scientists which led me to set my threshold of suspicion so high...
For their work scientists are entrusted with public funds. I have come better to appreciate the legitimate role of government as the public sponsor of scientific research and to respect its duty to protect the public interest and hold the scientific community accountable for its stewardship of public funds. Such accountability can be entirely consistent with the essential objectivity of scientific inquiry...
I have learned from this experience that the accountability to ensure the responsible use of public funds rests not only with each individual scientists but with the scientific community as a whole...
In conclusion I commend Dr. O'Toole for her courage and her determination, and I regret and apologize to her for my failure to act vigorously enough in my investigation of her doubts. I recognize that I may well have been blinded to the full implications of the mounting evidence by an excess of trust...This entire episode has reminded me of the importance of humility in the face of scientific data.

Baltimore's statement in Nature should also be compared with the statements of some of his supporters, such as those of Bernard Davis quoted in Appendix 15. These are incompatible. Baltimore's statement was also contradicted at several points in a response by Margot O'Toole in Nature, 16 May 1991. Then Baltimore replied that her comments "create a misleading impression...I feel that it is necessary to demonstrate publicly that her charges lack substance". Herman Eisen also replied that he found Margot O'Toole's "extreme be inaccurate or grossly to misrepresent the true events". (Nature 30 May 1991)

Appendix 17. What Baltimore and his lawyers were aware of.

Here is a quote from the NIH Draft Report (pp. 7 and 8), showing what Baltimore and his lawyers were aware of.

Also during this time NIH became aware for the first time that Dr. Imanishi-Kari's notebooks had not been compiled contemporaneously with the conduct of the reported experiments. Rather, the notebooks were assembled specifically to respond to the challenges to the paper. Subsequent information provided by Dr. Baltimore and his attorney, Normand Smith, Jr., indicated they were aware of Dr. Imanishi-Kari's having organized the notebooks to respond to the NIH and Congressman Dingell's subcommittee. During the April 31, 990 interview with Dr. Baltimore, Mr. Smith said a meeting was held "where Thereza came with all of her data and there was a to whether we should just dump it on the doorstep of the committee...or should she go through her data, catalog it and put it in order and try and make it as comprehensible as possible." Mr. Smith said "I think I may have been instrumental in advising her to do the latter, which I think was, in large part, her undoing" (Interview Transcript, page 71). Mr. Smith said some data were in folders, some in spiral notebooks, and "there were [sic] a lot of just loose paper." According to Dr. Baltimore, Dr. Imanishi-Kari took the data home and organized it "...entirely on her own...over a weekend" (Interview Transcript, page 72). Dr. Imanishi-Kari herself acknowledged some data were not entered into laboratory notebooks, but directly into figures, as in Figure 1. Dr. James Wyngaarden, testifying before the Dingell Subcommittee in 1989 (see below), referred to these as "unorthodox data handling practices." Based on these discoveries, the NIH decided it would reopen its investigation.

Appendix 18. Some of the press on Baltimore's resignation.

I list a few reports in the press concerning Baltimore's resignation as President of Rockefeller University.

New York Times, 3 December 1991: "Nobelist Caught Up in Fraud Case Resigns as Head of Rockefeller U."; and 4 December: "Science and the Stain of Scandal - Role at Rockefeller U. Fatally undermined by Fraud Case". In its articles and editorial of March 1991 the New York Times had failed to point to its own role in having helped Baltimore's anti-Dingell campaign. (See V, §1(c).) At that time I made my objections known to the Times. In the article of 3 December 1991, the New York Times did report more completely: "Dr. Baltimore led many scientists and others in a campaign of letter-writing, speeches and opinion pieces opposing a Congressional investigation of the paper, which appeared in many magazines and newspapers including the New York Times."
The articles of 3, 4 December were followed by an editorial "Rough Justice for Dr. Baltimore" on 5 December, ending with the statement: "But the deeper judgment is clear: The scientific community must police itself more effectively. It should not take four Congressional hearings, two university inquiries, two investigations at the National Institutes of Health and a Federal grand jury to unravel a case that could have been settled years ago by Dr. Baltimore, had he been less interested in protecting his reputation and more determined to get at the truth."
Washington Post, 3 December 1991: "Nobel Winner Quits as University Chief, Citing Role in Scientific Fraud Probe."
Wall Street Journal, editorial 4 December 1991: "Dingell Gets Baltimore".
Boston Globe, 5 December 1991: "Baltimore's legacy: concern about oversight of scientists".
Nature: a brief article "Baltimore resigns" 5 December 1991, and an unsigned editorial "Baltimore defeat a defeat for research", 12 December 1991;
Science, 13 December 1991: "David Baltimore's Final Days".
Science and Government Report (Dan Greenberg) 15 December 1991: "Baltimore Steps Down from Rockefeller Presidency". Greenberg gives a notably informative one-page-and-a-half account of the context of Baltimore's resignation, starting (p. 4): " 'Dingell Gets Baltimore,' the title of a fulminating Wall Street Journal editorial on December 4, summarizes a widespread interpretation of Nobel laureate David Baltimore's resignation from the presidency of Rockefeller University. In reality, however, Baltimore got Baltimore..."

Appendix 19. Bad press for science.

For articles giving a bad press to science, see for instance:

The Economist: "When science turns nasty" (9 June 1990);
"The Baltimore Affair, Ignoble" (30 March 1991);
"Searching for a bigger can" (5 October 1991);
TIME: "Thin skins and fraud at MIT" (1 April 1991);
Detroit News editorial: "Dingell: He Was Right" (25 March 1991)
The Plain Dealer (Cleveland) editorial: "A sad case of scientific hubris" (27 March 1991)
New York Times (among others, after the OSI Draft Report): "Crucial Research Data in Report Biologist Signed are Held Fake" (21 March 1991);
"Hero in Exposing Science Hoax Paid Dearly" (22 March 1991);
"Upholding a Challenge to the Status Quo" (24 March 1991);
"A Scientific Watergate" (Editorial, 26 March 1991);
"How Charges of Lab Fraud Grew Into a Cause Célèbre"
(26 March 1991);
"Can the Scales of Justice be Calibrated for Scientific Fraud?"
(31 March 1991);
"Rockefeller U. Is Hurt as President Feels Pain of Science-Fraud
Case" (1 April 1991);
TIME, "Science under Siege: Crisis in The Labs" (26 August 1991);
U.S. News and World Report: "The Best of America; Setting wrongs right - Congress's most feared Democrat" (26 August - 2 September 1991)
New Republic: "THE SCIENCE MOB - Fraud, complacency, and secrecy in the scientific establishment", by Philip J. Hilts, (18 May 1992);
Newsweek: "A Plague of Science Fraud" by Robert Bell (15 June 1992)

On the other hand, throughout the Baltimore affair, the Wall Street Journal was systematically against Dingell and pro-Baltimore. See for instance:

"Science in Stripes" ("REVIEW AND OUTLOOK") 18 April 1988 (p. 24). The gist of the article is: "There is no free lunch. Becoming so thoroughly dependent on federal funding leads unavoidably to conflicts with the funders, who are politicians and who behave like politicians. Up to now the research community has been willing to try to paper over fundamental problems created through the funding process by accepting more oversight, more regulations, more review boards. The result over time is likely to be less significant science."
"Latest Chapter in the Fine Science Of the Smear" by Paul Gigot, 5 May 1989;
"Fraud vs. error: The Dingelling of Science", by Bernard Davis, 8 May 1989;
"The Science Police" ("REVIEW AND OUTLOOK"), 15 May 1989;
"Politics and Science" (Editorial), 29 March 1991;
"Dingell Gets Baltimore" (Editorial), 4 December 1991.