O'TOOLE'S TESTIMONY TO THE DINGELL SUBCOMMITTEE 9 MAY 1989

Statement of Margot O'Toole
to the
Subcommittee on Oversight and Investigation
of the
House Committee on Energy and Commerce

May 9, 1989

My name is Margot O'Toole. I was a post-doctoral fellow in Dr. Imanishi-Kari's laboratory at MIT from June 1985 to May 1986, and I was the first to challenge the Cell paper. These hearings are the extraordinary result of that challenge. The reaction of the scientific community to me and to the events surrounding my challenge clearly indicates that most scientists do not understand what happened or why it happened. I hope that the scientists especially will listen and evaluate the factual basis for what I say. Only then can we as a community come to terms with the important issues raised by this case.

This dispute is over a single paper, and the scientific community is clearly at a loss to understand how it reached such proportions. Members of the Subcommittee have stated repeatedly that they are not trying to determine if I am right scientifically. They are concerned about the process and the adequacy of safeguards. The scientists remain focussed on the science, Mr. Chairman, and many do not seem receptive to your criticisms of process. My case should demonstrate to them that the current process of adjudicating disputes of this nature just simply does not work, and this is bad for science and scientists.

The scientists tell me that I have to show that I am right scientifically before they accept outside criticism of the process I have gone through. I say to them: My knowledge of the facts of this case makes me absolutely confident that I will eventually prove my points beyond all shadow of a doubt. By that time there will be a clearly documented history of just how hard it was to make the facts known. The scientific community will then be left with a record of conduct that will not make it proud. It makes more sense for scientists to take seriously the Subcommittee's concerns about the process right now, before all the scientific issues of this case are settled.

I would like to comment on the role you, Mr. Chairman and the Members of this Subcommittee, have played in this process. Your decision to become involved before the case was settled was courageous and has placed you under intense political pressure and public criticism. The scientific community has told you to stand aside while they decide whether I am right or wrong scientifically before you scrutinize their conduct. I thank you for your strong response that whether I am right or wrong the process should be fair and thorough, and the issues should be settled on the basis of the facts, not on the basis of who says I am wrong. By following and overseeing this case during the past year you have discovered and righted serious inadequacies that would otherwise have been ignored.

This case has been extremely painful for all involved. All of us wish it out of our lives. But events make this case one which will have a profound influence on process. For this reason it is important to see the case through to the end. I stand for all those who raise questions about research practices. My battle now is to make sure that those who follow me will get a fair and thorough hearing, that they will be allowed to examine the evidence and see the reports. Most of all I want to see a process that does not require three years and five investigations before a report can be issued that does not fall apart on the basis of the available evidence. This is the situation in which both the authors and myself find ourselves enmeshed. This situation is intolerable.

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 thorough 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 why this whole branch of the self-correction process must be blocked.

To my fellow-scientists who are outraged by the intervention of Congress in affairs controlled solely by scientists up until now, I say the following. Please remember that only friends and allies take the time, trouble, and considerable risk to point out when something is amiss. Those who really do not care stand aside and let the problem get worse. Scientists have had three years to settle this matter. On one point we are now all in agreement -- the matter is still not settled.

Mr. Chairman, your staff has asked me to tell again of my experiences, and I will. I will then take this opportunity to do away with the widely held misconception that I challenged the Cell paper because my interpretation of the data differed from that of the authors. This is not the case, and the sooner scientists understand this, the sooner they can deal with the issues that concern the Subcommittee.

When I joined the laboratory, a very exciting finding had been made in collaboration with Dr. Baltimore's laboratory and had just been announced. This finding was submitted to the journal Cell in December 1985 and published in April 1986. In early May 1986, I was reviewing the records for the mouse colony. I ran across the records for one of the crucial experiments in the Cell paper. I knew it was the data for the published table because of the agreement of numbers in the records and the published paper. An examination of these records convinced me that the findings had been presented in a misleading fashion, and that a central claim of the paper might not be supported by experimental evidence. I copied these records and some preceding them that were also related to the published claims so that I could study them and decide what to do.

As an aside here I wish to address Dr. Baltimore's comments made here last week concerning the data I copied. Dr. Baltimore said that the records were selected to support my arguments. This is not the case. I copied the records for an already published experiment. The repeated statements that it was I who selected these data are false and extremely damaging.

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.

I brought a copy of the records to Dr. Huber of Tufts University. She became alarmed and said she would have to ask Dr. Woodland of the University of Massachusetts for advice. She reported to me that Dr. Woodland had advised her to bring the matter to Dr. Wortis, also of Tufts University. I immediately told Dr. Huber that I did not think this was a good idea because Dr. Wortis and Dr. Imanishi-Kari were close friends. We discussed this for a few minutes and eventually I agreed that Dr. Huber could bring the records to Dr. Wortis. She returned a little while later and asked me to explain the issues to Dr. Wortis and I did. Dr. Wortis decided that he would handle the matter himself. I told him I did not think he was the right person to be in charge. He disagreed and refused to change his plans, saying that if necessary he would "rehabilitate" Dr. Imanishi-Kari. I went to the Chairman, Dr. Flax, who told me that the right thing to do was to go to the MIT authorities. also said that he did not think it was necessary to interfere with Dr. Wortis's plans.

Over the next few days Dr. Wortis and I had a number of telephone conversations. We worked out an agreement that I felt was acceptable. Dr. Wortis was in the process of writing a grant with Dr. Imanishi-Kari, and so it was natural that he needed to go over the data. He could then raise questions himself without involving me in the process. We agreed that, no matter what data he reviewed, he would ask Dr. Imanishi-Kari for a conference with Drs. Huber and Woodland so that they could assist him in evaluating the data. He assured me that if I was right, he would make sure that Dr. Imanishi-Kari submitted a correction. This arrangement had many advantages as far as I was concerned. It took the professional responsibility away from a junior scientist and placed it on a senior scientist where I felt it rightly belonged. It allowed for the possibility that the paper would be corrected if necessary without exposing Dr. Imanishi-Kari to any official inquiries. Finally, it ensured that Dr. Wortis's judgement could be checked by two other scientists.

I stayed at home on the morning of Dr. Wortis's conference with Dr. Imanishi-Kari. Approximately ten minutes after their conference was scheduled to have begun, Dr. Imanishi-Kari called me. She knew that I had raised concerns with Dr. Wortis, and Dr. Wortis had already left. She threatened legal action against me and ended the conversation by saying that I was not to return to the laboratory. Dr. Wortis had abided by his agreement with me for less than ten minutes and had left Dr. Imanishi-Kari's office without examining the data.

The next evening, May 16, Drs. Huber, Wortis and Woodland met with Dr. Imanishi-Kari. Dr. Huber called me the next day and described the data they had examined. I asked about specific data needed to settle the issue, and she said they had not seen these. She added that Dr. Imanishi-Kari had agreed to another conference where she would bring data that she did not have available at the first meeting. Realizing from the conversation that Dr. Huber did not understand the issues as well as I had thought, I said that I wanted to be present at the next meeting. Dr. Huber consulted Dr. Wortis and they agreed I could be present. Dr. Huber told me they would ask Dr. Imanishi-Kari to bring the relevant data to the conference. Dr. Wortis again agreed that if I was right he would make sure the paper was corrected. I agreed that if I was wrong I would apologize and make sure that Dr. Flax knew that my concerns had been answered.

This meeting took place on May 23 but Dr. Woodland did not attend. In support of the published claim that I was challenging, Dr. Imanishi-Kari presented data on only two sheets of paper. She stated she greatly resented having to take a whole week to generate data to satisfy my scientific objections at a time when she was so busy. I asked to see the original data, meaning the results of the experimental steps that would have had to precede the results she 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 the 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 advised 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 would be 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 that 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 chose 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-l 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 questioned 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. They said that Dr. Baltimore had taken the data over the telephone, misunderstood, and thought the experiments had been done. Dr. Imanishi-Kari said that she had not read the drafts of the manuscript carefully. They decided that these false claims were inadvertent, and therefore did not need to be corrected.

We then turned our attention to the other experiments that supported the basic claim of Table 2, the claim that I was challenging. I described the data I had examined at the Wortis committee meeting, but Dr. Imanishi-Kari said my assertions were not correct. Dr. Baltimore told her that he believed her and that there was no reason to examine the data. (She stated she had not brought it to the meeting.) Dr. Imanishi-Kari and Dr. Baltimore then had a long discussion about data for some other papers published four years previously. This data had been brought to the meeting.

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 correction. I was asked if I was going to pursue this matter with the NIH, and I said no, I felt I had discharged my professional responsibility by informing the authors and the administrators.

After the meeting, Dr. Weaver and I had a discussion. Dr. Weaver commended me for my courage. I asked him how Dr. Baltimore could act as if this was acceptable practice. Dr. Weaver replied that he believed there was a difference between what Dr. Baltimore said and what he thought, adding "He does not think this is OK." I told Dr. Weaver that Dr. Maplethorpe had said he heard Dr. Imanishi-Kari tell Dr. Weaver that the Bet-l reagent was not specific. Dr. Weaver said that he remembered this conversation, but that he naturally had assumed the problems had been worked out before publication.

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

I telephoned Dr. Flax and discussed my situation. He confirmed for me what I had already heard from people at MIT. Dr. Imanishi-Kari, who was now in his department at Tufts, had asked for his assurances that I would not be allowed to return to my position at Tufts. He told me that he had assured her he understood how she felt.

My husband, who works in Tufts in the same department with Drs. Wortis, Huber and now Imanishi-Kari, told me not to worry. He said to take some time to recover and then to come and work in his lab for a while. If things went well I could rebuild my career. However, Dr. Wortis told my husband that this was not a good idea. It would make Dr. Imanishi-Kari uncomfortable, and it would inhibit free and open discussion. My husband and I discussed this conversation, and he suggested some professional restrictions for me. In the end, however, I decided that I could not accept these restrictions and he also could suffer isolation from his colleagues if he accepted me into his laboratory. We decided to protect the one job we had between us, and I suggested that he offer the position to someone else.

I have made some attempts to clear my reputation among scientists. In October 1986, after I had taken a job outside science, I protested to Dr. Huber that the Wortis Committee's handling of the matter, especially their false report on the matter to the other members of the Tufts department, had left my reputation unfairly damaged. She replied that she was "sure I could get a job somewhere doing something if I tried hard enough". She treated my predicament as if it had nothing to do with her. I wrote to Dr. Eisen about false statements about me in his report. I asked him to correct the false statements and thereby correct the damage he had done to my reputation. He has not replied.

I consulted a lawyer who told me that I should formally request that Dr. Flax reinstate my appointment as a research assistant professor in his department. However, both my husband and I felt that if I put the Chairman in this position, a position that my previous conversations with him indicated he wished to avoid, a battle with Drs. Wortis, Huber and Imanishi-Kari would ensue. My husband and his career would be caught in the middle. Neither of us doubted that as a result, my husband's colleagues would begin to wish he look elsewhere for a job so that their problems would be solved. Again we decided to protect the one career that was still intact.

I learned that the top administrators at Tufts had been briefed on the case, but that the description of my actions was false and damaging. In an interview with a magazine, Dean Lasagna told of the case, identifying it with specifics but without names. The Dean said, in effect, that the case involved a charge of fraud that had been made without justification. This was devastating to me. I had been so careful to make my concerns clear and to make sure that it was understood that I had not charged fraud. Moreover, every allegation I had made about inaccuracies in the paper was true.

I tried to get a copy of the report filed by the Wortis committee so that I would be able to reply. Dean Banks refused, saying that it would not be appropriate to let me see the report. I heard via the grapevine that MIT faculty were accusing me of "purloining" or stealing laboratory notes. I has never done such a thing, but I have since confirmed that this is how they described my attempts to behave in a professionally responsible manner. A number of eminent scientists have attacked me publicly. I have tried to learn the basis for their objections in two cases, but have received no reply.

Mr. Chairman and Members of the Subcommittee, scientists told you last Thursday that I could still have a career in science. I hope so and I am currently negotiating for a position. If, however, any scientists doubt that I have been damaged as the result of my challenge to this paper, I ask them to answer the following questions. When was the last time they hired someone who eminent scientists have described as one who purloins data and lies under oath? Who among them has ever hired anybody who reputable people say selectively copied notes to make trouble or support a particular point of view? Who would want in a laboratory someone who can not accept an alternative interpretation of data, who can not distinguish important issues from trivial issues, does not accept the reviews of eminent and qualified reviewers, and who has unfairly besmirched the public's view of research? All these things are being said about me, and all these things are false.

I sat in this room last Thursday as scientists here actually snickered when the issues of my concerns were raised. If my job negotiations are successful, I will need to apply for funding. I will have to go through a peer review process that is controlled by those who laugh at my concerns and are nothing short of furious about the results of my actions. The people who might hire me are well aware of this. Mr. Chairman and Members of the Subcommittee, anyone who tells you my career has not been badly damaged, even irrevocably damaged, is insulting your intelligence.

At some point during the summer of 1986 I learned that Dr. Maplethorpe, a former graduate student from Dr. Imanishi-Kari's laboratory, had called Dr. Feder before the first meeting of the Wortis committee. He had then kept him and Walter Stewart informed of developments. A few months later, when I thought it was all over, I received a phone call from Mr. Stewart. He asked if I was satisfied that my concerns had been adequately addressed. I said no, they had not been, but that there was nothing else I could do or cared to do. Mr. Stewart then said he wanted to analyze for himself the scientific basis for my challenge and asked me to send him the 17 pages of laboratory records I had copied. I refused for quite some time, but he was persistent. Over a period of weeks, Mr. Stewart made clear to me that I had only one of two choices. I would have to become part of the problem, or I would have to become part of the solution. He told me that if I sent him the laboratory records, he would inform the appropriate NIH authorities if he felt such a move was warranted. I eventually sent him the records. At Mr. Stewart's request, I told him about the science and the investigation in detail. I described the data examined at each of the meetings and the reasons I felt that I had never received an adequate response to my challenge.

As everyone now knows, Mr. Stewart and Dr. Feder analyzed the records that I had copied, and then they too challenged the findings of the Cell paper. The impasse between the authors and Stewart and Feder resulted in a very open dispute. The NIH decided to settle the matter officially, and I have co-operated fully with their efforts. Two members of the panel had to be replaced when, last year, this Subcommittee highlighted obvious conflicts of interest. A new panel began work in June 1988, and the NIH issued its report on January 31. The NIH has now reopened its investigation.

I would now like to comment on the status of my scientific challenge to the paper. I quote from the NIH Panel's report. "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, and offering in replacement, the data obtained from the subclones of the wells represented in this table." It was precisely the Table 2 data that caused me to challenge the paper. The Panel finds that I was correct about these data, but describes subcloning experiments that do support the Table 2 claims and recommends that these data be published instead. However, at the time of my initial challenge I asked Dr. Imanishi-Kari if these subcloning experiments had been done. If the experiments had been done and supportive results obtained, I would have withdrawn my challenge. Dr. Imanishi-Kari stated that the experiments were not done.

The scientific panel has confirmed the legitimacy of my concerns about the published data and has recommended that other data that do support the claims be substituted. In November 1988, I told the NIH that the Panel had relied on data that I was told did not exist at the time of my challenge, and they disregarded what I said. The evidence uncovered by the Secret Service calls much of the unpublished data into question. The authors reply that none of the questioned data was published. What is crucial to remember is that, although the questioned data were not published, the Panel relied on them in deciding there was experimental evidence in support of the central claim. I note that some have said that parts of the paper have been confirmed. In fact, however, the central claim of the Cell paper, the claim that I challenged, has not been repeated.

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. It has hurt me greatly that the entire scientific community is apparently convinced that I do not understand this most basic tenet of the scientific endeavor. 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.

From my perspective the NIH investigative process has been flawed in a number of important respects. Most importantly, when the facts of the case were in dispute, the NIH relied on statements made by the Wortis committee to justify dismissing my statements. NIH knew before the investigation began that the other participants were saying publicly that I had not told the truth under oath. There was clearly no point in conducting an investigation if issues were to be decided on the basis of their word against mine. When I showed the scientific panel the evidence examined during the previous investigations and told them what had transpired, they stated clearly that they were not interested in this information. The approach of the Subcommittee is much more in keeping with the principles of the scientific process. The Subcommittee asked for an expert analysis of the evidence. I am confident that when all the evidence has been analyzed, all my statements will be shown to be truthful. Without the oversight of this Subcommittee this would have been impossible.

Another flaw in the NIH process is that does not allow for challengers to see evidence. The person most likely to understand the basis for a challenge is the challenger. It is not in the interests of science or the investigation to keep the evidence secret until after the report is released. The scientific panel can judge if the analysis of a challenger has merit and I see no reason why a panel should not have the benefit of the challenger's comments. 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. Thus the NIH denied itself the benefit of useful information I could have given. The NIH treats scientific data for publicly supported published work as one would a personal diary. I think the policies that emanate from this attitude should be changed.

We are scientists and we should examine data. In his testimony, Dr. Baltimore indicated that it is not appropriate for collaborators to examine each other's data carefully. He said such examination would imply a lack of trust. This may be the case at the present time, but it should not be. 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 collegian 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.

This has been a long and agonizing dispute. Thanks to you and your staff, Mr. Chairman, there is now a good chance that a proper examination of all 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 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 that my account would be labeled untrue by other principles in the case, and it has been. I felt that they, 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 action 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 dated 11/30/84 had been shown to me on May 23, 1986. I identified this page as one of 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, five 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 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. I take this opportunity to thank you for your concern and for tenacity in the face of criticism. I will be happy to any questions.

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