Mr. Chairman and members of the subcommittee, my name is Margot O'Toole and I am appearing here today at your direction. I would not wish to volunteer this testimony as it involves many people I have admired all my professional life and some who were my friends.

I have broken with these people over what I perceive as a major disagreement on matters of ethically acceptable professional practices and our responsibilities as publicly supported scientists. My dispute has halted my career, disrupted my social milieu and had a devastating effect on my life. I know that it has also been extremely upsetting for those who disagreed with me. We scientists should have been able to resolve our differences by ourselves in the academic tradition. I deeply regret that the matter has come to such an impasse. I would like to be able to forget my ordeal entirely and get on with other things.

I received my Ph.D. in immunology in 1979 from Tufts University in Boston. My thesis work was done in the laboratory of Dr. Henry Wortis. From 1981 to 1985, I worked at the Institute for Cancer Research in Philadelphia, first as a postdoctoral fellow of the NIH and then as a fellow of the National Arthritis Foundation.

In January of 1985, my husband and I moved back to Boston and he assumed a position at Tufts University in the same department as Dr. Wortis, my former thesis advisor.

My plans were to continue my project as an Assistant Research Professor at Tufts also in the laboratory of Dr. Sidney Leskowitz. However, my application for funding was turned down. The review of my grant indicated that a more favorable decision was more likely if I reapplied after I had more preliminary data to prove the feasibility of my proposal.

Dr. Theresa Imanishi-Kari of The Massachusetts Institute of Technology, heard of my funding situation through others and approached me with an offer. She needed someone of my expertise to perform a certain set of experiments suggested by her latest findings. If I would postpone assuming my assistant research professorship for 1 year, spend one more year as an NIH postdoctoral fellow and help her with her project, she would allow me enough time to do the preliminary work required for my reapplication. I was delighted by this offer and accepted. I provide here a summary of my experiences. As you have directed me, I attach a detailed chronology of these events.

Soon after I went to MIT, Dr. Imanishi-Kari told me that she would be moving to Tufts in July of 1986. Her appointment would be in the same department as my husband. Within a few months, I had done a number of experiments whose results conflicted with hers. I naturally believed that the differences were the result of error and continued to repeat some of my experiments in an effort to find the source of the discrepancies This took up a lot of time and expensive laboratory supplies and Dr. Imanishi-Kari became very impatient.

She insisted that the discrepancies were the result of my incompetence and that I should accept as valid the findings as she presented them. This would have meant ignoring my own controls and was therefore unacceptable to me for scientific reasons. Some of these experiments were very simple to perform and were absolutely essential for my own project. I could find no reason that I could not get them to work as expected. Communication between Dr. Imanishi-Kari and me deteriorated steadily.

In the fall of 1985, I received a manuscript describing the study that had suggested the project for which I was hired. I had already done experiments that disagreed with some of the findings but Dr. Imanishi-Kari dismissed my results. I should mention in passing that the manuscript was authored by three people from our lab, Dr. Imanishi-Kari, Dr. Reis and Mr. Albanese, and two from Dr. Baltimore's lab, himself and Dr. Weaver. The other author, Dr. Constantini, was from Columbia University. The paper eventually appeared in press in April of 1986.

I found my many discussions with Dr. Imanishi-Kari difficult and unproductive. She did not present her records for comparison as I did. She maintained that I had done the experiments exactly the same way but that she had obtained the opposite result. As my knowledge of the available procedures in the laboratory increased, I began to doubt that certain other experiments could have been performed as claimed in the Weaver et al paper

As my results continued to disagree with those she told me to expect, Dr. Imanishi-Kari became so displeased with me that she told me to stop experimenting altogether and take care of the mouse breeding. I reported my problems to Dr. Herman Eisen, the Director of my training program, Dr. Mary Rowe, the Assistant to the President at MIT, a large number of my peers and Dr. Henry Wortis, my former thesis advisor. Dr. Wortis is a very close friend and professional associate of Dr. Imanishi-Kari's and I had hoped that he would help resolve our differences. However, he stated that he could not become involved.

Dr. Imanishi-Kari instructed me to prepare certain of my experiments for publication in a manner I considered misleading. Eventually, near the end of my time in the lab, she told me that at least for some of the discrepant results, her actual data agreed with mine and not with her published claims. She also confirmed that some of the experiments were not done as presented in the paper. On careful review of her paper, in light of this new information, I began to doubt the validity of some of the assertions.

Soon after these disclosures, I ran across the data for some critical experiments published in the Weaver et al study. These records were from experiments done by Dr. Reis and were among the mouse breeding records that had been left in my care. These records caused me to doubt that the underlying data supported the main conclusions of the now published study. In fact, it appeared that a number of the conclusions were actually contradicted by the records. In an effort to find out if there was any possibility that other records superseded or negated the records I had found, I asked Dr. Imanishi-Kari to show me the records for some other critical experiments she had performed herself. She was unable to find any of these records.

I went for advice to Dr. Huber, a scientist at Tufts University who had agreed to review my data and concerns. She in turn enlisted the aid of two other scientists, Dr. Woodland of the University of Massachusetts and Dr. Wortis, in an attempt to resolve the issues raised by the comparison of the records with the published claims. I informed our Chairman at Tufts of these events and he told me that I should bring the matter to the MIT authorities, since MIT was responsible for the work.

Dr. Huber, Dr. Woodland and Dr. Wortis met with Dr. Imanishi-Kari in an unsuccessful attempt to resolve the issues. Then Dr. Huber and Wortis arranged and attended a meeting where Dr. Imanishi-Kari and I reviewed the data. My assertions that the data did not support the published claims were completely confirmed. I left that meeting under the impression that the paper would be retracted.

The next day, however, I was informed by Dr. Huber that, although she and Dr. Wortis agreed with me scientifically, they felt that fraud was not the cause of the discrepancies. They had decided therefore that since a retraction or correction might be very detrimental to Dr. Imanishi-Kari, it was best for all concerned to drop the matter. I disagreed, saying that other laboratories were relying on the data and that we had a professional responsibility to make the truth known. I also spoke to Dr. Wortis at length, and while he reaffirmed the validity of my objections, I could not change his mind. The Chairman of the Department later told me that both Drs. Wortis and Huber had reported to him that my objections had been easily dismissed.

In the meantime, as advised by the chairman, I had kept Dr. Mary Rowe of M.I.T. informed of the developments. I had refused to comply with her request that I bring the matter to the appropriate authorities at M.I.T., because, as I told her, I believed that the scientific issues could be resolved in a less traumatic, more collegial way by Dr. Imanishi-Kari's supporters at Tufts. I eventually had to admit to her that I had carefully checked and confirmed by assertions and that I was convinced that the published paper contained serious errors of fact. I also informed her that scientists much more senior than I had judged that this matter did not warrant any published corrections.

She cited the damage being done to my reputation by the rapidly travelling rumors that I had falsely accused my supervisor, and of which she and I were both aware. She insisted that I speak to Dean Brown, the Dean of Science at M.I.T., called his office and arranged for me to speak with him that afternoon. Dean Brown told me that I should either bring charges of fraud or forget the matter entirely. I told him that of those two options, I would choose the latter.

Soon after that, Dr. Eisen, the director of my training program, called me, arranged a meeting, went over the notes and told me to put the objections in writing. I wrote him a memo. He gave the memo too and arranged a meeting with Drs. Baltimore, Imanishi-Kari and Weaver, and they are all authors of the papers in question.

At this meeting, no new evidence was produced and I again confirmed by objections. Dr. Baltimore acknowledged some of my major points as valid and said he would speak to Dr. Imanishi-Kari in private. For other parts of the study, he amazed me by maintaining that the total absence of controls did not constitute a significant problem. Dr. Baltimore argued that he had reason to believe that part of the study was valid. For that reason, no correction was necessary. He added that this sort of thing is not unusual in science, that research corrects itself as other scientists attempt to repeat or extend the findings. He said that in this way it would become clear over the next few years which of the assertions of the paper were valid. He strongly advised me to drop the matter for my own good an asked Dr. Eisen to write up a memo saying that the matter had been "aired."

At this point I had brought the matter first to Dr. Imanishi-Kari's friends and supporters, and then to her collaborators and officials at M.I.T. I believed that I had explored all my options and fulfilled my professional responsibilities. I would like to take this opportunity to state under oath that I did not know then, as I do now, that Mr. Stewart and Dr. Feder were being advised of these events as they occurred. I can take neither the credit nor the blame that this matter has come to light. I dropped the matter completely and left science, saddened and disillusioned.

I have had time now to reflect on my experiences. Unfortunately, it is apparently the prevalent attitude among senior scientists that revealing known errors is not worth hardship that might be brought to their careers, that science itself in time will reveal the truth. This attitude was expressed to me by a number of scientists who reviewed my case and I have since seen it in writing. I consider it totally irresponsible and for my own part I have decided that I must reject it. Of course there is trial and error in research. Much of what may at first appear to be an exciting breakthrough is later found to be trivial or false.

It is extremely counterproductive to current scientific investigation, however, that known errors remain published as truths. Funds in this profession are too scarce, the public need too pressing, laboratory work too costly and the time and efforts of scientists too valuable to waste our precious resources discovering errors that were known to others from the start.

While it is probably true that the funding system is much to blame for the unwillingness to correct error, it appears to me that the prevailing attitudes sanction inaccuracy. It is hard to imagine that they do not actually result in increased published errors. Difficult as it may be, I believe scientists should make the commitment to do everything they can to ensure that the literature is as reliable as possible.

For my own part, my troubles began when I refused to compromise a basic rule of scientific investigation, one that is taught in our very first lab courses as children: Experiments must contain valid controls. My evidence for this is irrefutable, yet of the many senior scientists and officials at M.I.T. and Tufts who reviewed my case, not one offered me help or support. In fact, most openly questioned my motives and treated me as if I was behaving in a socially unacceptable manner. Only my peers watched with sympathy and the knowledge that the same thing could have happened to them.

I thank the subcommittee for their interest in these issues.

[A chronology of events follows:]