May 19, 1988

Dear colleague:

I have recently become embroiled in a controversy over some of the data used in a paper* (*Weaver, D., Reis, M., Albanese, C., Costantini, F., Baltimore, D. and T. Imanishi-Kari. Altered Repertoire of Endogenous Immunoglobulin Gene Expression in Transgenic Mice Containing a Rearranged Mu Heavy Chain Gene. Cell, Vol. 45, 247-259, April 25, 1986.) published in the journal Cell in April 1986. The paper resulted from a collaboration among three laboratories: mine, that of Dr. Thereza Imanishi-Kari (then at the MIT Cancer Center but now at Tufts University) and Dr. Frank Costantini at Columbia University. Dr. David Weaver was from my laboratory; the other two authors were from Dr. Imanishi-Kari's.

The controversy has generated widespread press coverage, much of it inadequate and some of it downright wrong. I believe that it is of critical importance that I set the record straight, not just to clear my own name and the names of the other authors who have been compromised by this attack, but for another, more compelling reason:

A small group of outsiders, in the name of redressing an imagined wrong, would use this once-small, normal scientific dispute to catalyze the introduction of new laws and regulations that I believe could cripple American science.

My explanation of these events, necessarily long, is spelled out here in four parts: 1) The science; 2) Dr. Feder and Mr. Stewart; 3) Congress and the press; 4) Aftermath.

I. The science

A number of years before this Cell paper, I initiated a collaboration with Dr. Frank Costantini to create transgenic mice using a rearranged p immunoglobulin heavy chain gene. The major reasons for making the mice were to investigate the regulation of the p heavy chain gene and to examine whether a rearranged gene would affect the rearrangement of endogenous genes. We chose, however, to use as the rearranged gene one that encodes the heavy chain of a particular BALB/c idiotype. We injected the gene into a C57BL mouse, a mouse that does not make the idiotype, largely as a convenience for using specific nucleic acid probes. But there was a long-range possibility that by putting a new idiotype into the C57BL background there might be interesting immunologic consequences.

After completing the initial molecular biological work, it was evident that the transgene was being expressed and I entered into a collaborative study with Dr. Imanishi-Kari to study the immunologic questions. The types of methodology involved in doing the immunologic characterization were not then available in my laboratory and she had many years of experience with this system. In fact, I had originally gotten the BALB/c idiotype gene in a collaborative study with her because she had defined the idiotypic X relationships.

The experiments rapidly turned up an apparent anomaly. Although there was a lot of idiotype-positive antibody evident in the serum, it appeared to exceed the amount of product that had the characteristics of the transgene product. To examine the question more closely, hybridomas were made and they, too, showed that there could be cells that were idiotype-positive but did not express the constant region of the inserted p transgene. All of these analyses involved the use of sera that were specific either for constant regions or for idiotype. Dr. Weaver, a postdoctoral fellow in my laboratory - who was involved early in this study undertook to sequence the heavy chain genes expressed in the hybridomas. From the sequence work it became evident that in one case there was expression of a variable region very close in sequence to that of the transgene, but in association with an endogenous constant region. In other cases, it appeared that totally endogenous genes were being expressed, but the hybridomas showed idiotypic characteristics. One heavy chain variable region ("81X") predominated among the hybridomas expressing idiotype-positive, endogenous gene products.

Dr. Imanishi-Kari and I had somewhat different interpretations of these experiments. She felt that there was strong argument for network interrelationships causing the endogenous genes to selectively express idiotypic cross-reactivity. I felt that the explanation probably lay elsewhere. In the case of the one gene that contained the transgene variable region and endogenous constant region, the explanation of trans-switching or gene conversion seemed most likely. In the other cases, I had no particularly good explanation. We wrote the discussion of the paper reflecting the various opinions and indicating that more studies would be necessary to fully understand what was going on.

Before discussing the controversy, I should say that further work on this system by Drs. Leonore and Leonard Herzenberg at Stanford University has indicated that in all probability the animals are making relatively few conventional B cells, but have a high fraction of "Ly-l B" cells, a rare type of B cell whose relationship to conventional B cells is controversial. Dr. John Kearney, however, has evidence that the products of the Ly-l B cells often display idiotypic cross-reactivities with other antibodies and my personal explanation now, as reflected in a paper* (*Herzenberg, Leonore A., Stall, A., Braun, J., Weaver, D., Baltimore, D., Herzenberg, Leonard A. and R. Grosschedl. Depletion of the predominant B-cell population in immunoglobulin p heavy-chain transgenic mice. Nature 329: 71-73, 1987.) written with the Herzenbergs, is that much of the idiotypic reactivity is a consequence of the high expression of the Ly-l B cells. There is also evidence that autoreactive antibodies often use the 81X V region and can be cross reactive with the idiotype. I do not believe that the question is at all closed and there may well yet be other surprises and other interpretations.

Early in 1986, after the Cell manuscript had been submitted, Dr. Margot O'Toole, a postdoctoral fellow in Dr. Imanishi-Kari's laboratory, questioned the interpretation of some of the data emanating from that laboratory. Dr. O'Toole was not directly involved in the work that led to the Cell paper. On June 6, 1986, shortly after it appeared, she wrote a critique of the paper to Professor Herman Eisen of MIT.

Dr. O'Toole's criticisms, as described by her, were based on certain experimental attempts of hers involving some of the reagents used in the study described in Cell. A part of her criticism was based on 17 pages of selected laboratory notes, a small fraction of the notes compiled during this project. She summarizes her criticisms in the first paragraph of her letter to Dr. Eisen:

"The central thesis of this work is that, in transgenic mice, there is an elevated expression of endogenous Ig which share idiotypic determinants with the transgenic (exogenous) antibody. In my opinion, the data do not show that the expression of endogenous antibodies bearing the exogenous idiotype is higher in transgenic than in normal mice. I believe that the data indicate that the observed phenomena are best explained by low level expression of the transgene in many of the selected hybridomas and by heterodimer formation."

Basically, Dr. O'Toole is arguing that an alternative interpretation of the data is possible that postulates a series of low level events that together bring about the results. She then provides four arguments why the published interpretation of the results is inappropriate. Reviews by Dr. Eisen and by a panel formed by Dr. Henry Wortis, an immunologist at Tufts, dealt with these four points. The Tufts review was impaneled because by that time, Dr. Imanishi-Kari had planned to move to Tufts. The reviews concluded separately that, although alternative interpretations are possible for most data, there was no compelling reason to believe that any one of Dr. O'Toole's four points represented a serious misinterpretation. Only further experimentation, the reviewers said, could properly resolve the differences between Dr. O'Toole's and others' interpretations.

The investigation did turn up one clear overstatement in the paper. In one sentence it is implied that the Bet-l monoclonal antibody used to detect the constant region of the exogenous gene is absolutely specific. It should rather have said that the reagent, Bet-l, is relatively specific. It could, however, do the job, as had been shown by Dr. William PauI of NIH, in whose laboratory the monoclonal antibody was made. A more precise reagent now available is corroborating the data from the earlier study (Stall, A., Kroese, F., Grosschedl, R., Gadus, F., Herzenberg, L.A. and L.A. Herzenberg. PNAS, in press).

The Bet-l monoclonal antibody has provided much of the controversy and misunderstanding about the data in the Cell paper. It was used in an iodinated form and the iodination can damage the antibody so that some preparations are better than others. Also, because Dr. Imanishi-Kari's native language is not English, at times her oral discussion is difficult to understand precisely. Thus, for a short period in September, 1986, a misunderstanding led Dr. Eisen and I to doubt the specificity of the Bet-l reagent whereas it was only the case that occasional preparations were not specific.

In the data of the Cell paper there is a clear contradiction to the hypothesis of Dr. O'Toole. Some idiotype-positive hybridomas had completely lost the transgene, presumably by segregation during hybridoma formation and stabilization. For these, a: least one of which expressed the 81X V region, there can be no doubt that the idiotype positivity was due to expression of an endogenous gene.

Late in June, 1986, Drs. Eisen, Imanishi-Kari, O'Toole, Weaver and I sat down and went over in detail the questions raised by Dr. O'Toole. At the conclusion of that meeting, Dr. Eisen wrote a memo that includes the following sentences:

"I do not think that I or anyone else present at the meeting felt that Margot O'Toole's disagreements were frivolous. They are indeed based on pretty carefully thought out ideas of the literature of the analytical methods. On the ocher hand, it is difficult to see that even with these shortcomings that the high frequency of idiotype-positive Igs with transgenic mice can be a reflection of what happens in normal C57BL mice. Nor does it seem too likely that virtually all of the hybridomas that were producing Ids, ostensibly pa minus hi nav also have been expressing low (and overlooked) levels of the transgene's products.

"These kinds of disagreements are, of course, not uncommon in science and they are certainly plentiful in Immunology. The way they are resolved traditionally, and effectively, is by publishing the results and having other laboratories try to repeat and evaluate them. The wonderful transgenic mice that have been prepared for this study are indeed being provided freely to other laboratories, and so within a reasonable period of time we should know the extent to which the authors' interpretations are correct or incorrect. If they are incorrect and require revision, then so be it. This is the way science operates; and in fact it is the kind of contentiousness seen in this dispute that helps drive the science 'engine.' Therefore, it appears to me that the entire exercise is not an unusual one, except for the intensity of the feelings generated and the circumstances concerning Dr. Imanishi-Kari's pending appointment at Tufts."

I agree completely with these comments of Dr. Eisen's.

In a formal report of his review of the complaints of Dr. O'Toole, Dr. Eisen said in part:

"My conclusion is that O'Toole is correct in claiming that there is an error in the paper; but it is not a flagrant error. The sentence that says the muB allotype bound only to the anti-muB antibody should have said that 'the muB allotype bound strongly to the anti-muB antibody but also crossreacted weakly with the anti-muA reagent.' The correction would be too minor to rate a letter to the journal; it certainly does not warrant a retraction, especially because the paper contains a substantial body of other data that is clear and impressive.

"The other issues raised by O'Toole, which are largely matters of interpretation and judgement, are best dealt with by allowing the scientific process to take its course. Other laboratories are trying to extend the findings. In this way we will know if the interpretations are right or wrong."

From all that we had learned so far - including two reviews and a lengthy meeting among all of the central figures in the dispute it was my understanding that it was unlikely that Dr. O'Toole's arguments were valid. It was clear that the only way to go farther was by using new tools of analysis and other transgenic systems.

I should emphasize here that the procedure of investigation followed at MIT exactly accorded with the MIT guidelines for examining charges of improper laboratory procedures. Dr. O'Toole brought no formal accusation and therefore the process was informal. Dr. Gene Brown, Dean of the School of Science at MIT, asked Dr. Eisen to investigate the question and provide his view of whether there was substance to Dr. O'Toole's doubts. He did this and concluded as described above. There never has been any effort by me to discourage Dr. O'Toole from pursuing her questions, nor have I done anything to affect her career.

II. Dr. Feder and Mr. Stewart

The controversy, I thought, was settled. The issues of scientific interpretation raised by Dr. O'Toole had been dealt with by MIT review according to the guidelines then and now in force. But I had not at that time heard about the efforts of a one-time graduate student in the Imanishi-Kari laboratory, Dr. Charles Maplethorpe. Dr. Maplethorpe was not involved in this research; in fact, he finished at MIT in the year before the paper was published. But after he finished he continued to appear regularly in his old lab. We have since learned that he had been meeting with MIT's ombudsman, Dr. Mary Rowe, as had, separately, Dr. O'Toole. Neither Dr. O'Toole nor Dr. Maplethorpe chose to file accusations against Dr. Imanishi-Kari at MIT, although according to their testimony, they were given ample opportunity to do so.

In fact, in her later testimony before a Congressional subcommittee, Dr. O'Toole emphasized that she has never claimed that fraud was involved, but that she was upset because she felt that scientific data was being misrepresented. Dr. Maplethorpe, though, Cold that same subcommittee Chat he thought Dr. Imanishi-Kari falsified data. He told the committee that he became suspicious because he thought Dr. Imanishi-Kari conducted herself in a secret manner and wouldn't share her data with others, including himself. He also reported overhearing a conversation between Dr. Weaver and a colleague and snatches of other conversations that caused him to think something was amiss.

According to Dr. Maplethorpe, Dr.. O'Toole approached him with her complaints and he shared his suspicions with her. Dr. Maplethorpe contacted Mr. Walter Stewart and Dr. Ned Feder. They are scientists who have worked together at NIH for about 20 years. In recent years they have turned their attention largely if not entirely to personal (not official) investigation of issues of scientific fraud. They are best known for their Nature paper on the Darsee affair. Dr. Maplethorpe had heard about them in a New York Tines story. Mr. Stewart and Dr. Feder apparently convinced Dr. O'Toole to provide copies of the 17 pages of laboratory notes from Dr. Imanishi-Kari's notebooks, pages that contained data that appeared to be contradictory to the data published in the Cell paper. Dr. Feder and Mr. Stewart compared the copied data with the paper and agreed that they were at variance. They wrote formal letters to all of the authors of the paper asking for all of the laboratory data so that they could compare them to the published data. We discussed this proposal and declined for the following reasons:

1. Dr. Feder and Mr. Stewart are not immunologists and from the types of questions they raised clearly showed a lack of understanding of the complex serology involved.

2. The two were self-appointed and had no right to the data. We believed then, and still believe, that for random people, scientists or not, to investigate scientific papers would severely disrupt ongoing scientific activities. On the other hand, duly constituted investigative bodies or colleagues in the same field should be provided the data for investigative purposes without question, in our opinion.

Dr. Feder and Mr. Stewart persisted with letters and phone calls, and finally I decided simply to stop responding. They succeeded in raising the interest of the NIH hierarchy, although neither was acting on behalf of the NIH and carefully emphasized this point in all correspondence. I suggested in a letter in March, 1987, to Dr. J. Edward Rall, Deputy Director of the NIH, that a group of immunologists be impaneled to consider whether the paper had been published appropriately. I asked for one condition: that Mr. Stewart and Dr. Feder agree to accept the decision of the panel if the panel found no impropriety. Mr. Stewart and Dr. Feder refused, instead asking that they be part of the panel.

At about the same time, Mr. Stewart and Dr. Feder produced a written manuscript that critiqued the paper on the basis of a review of the 17 pages of laboratory notes that had been made available to them by Dr. O'Toole. They circulated the manuscript widely within the scientific community seeking comments. I have never seen the full range of comments, but a number of scientists have sent me copies of their comments and all rejected the contentions of the Stewart-Feder manuscript. This is not surprising; a critique of a paper based on a selected, random set of data is extremely unlikely to be accurate. Dr. Feder and Mr. Stewart then attempted to publish the manuscript. Cell and Science rejected it. I do not know if they sent it elsewhere. In April, 1988, I learned that they were visiting college campuses and discussing the issue in very explicit and unflattering terms. At this point I realized that I might have to take some action to preserve my own reputation.

III. Congress and the press

Events moved faster than I did. Two Congressional subcommittees became interested in the issue. There have been several cases of scientific fraud in recent years and some have been highly publicized. Many Congressmen believe that the scientific community does not police itself effectively and that NIH has not been as diligent as it might be. One of the subcommittees, chaired by the enormously powerful Representative John Dingell (D-Mich), held a hearing at which the witnesses included Mr. Stewart and Dr. Feder, Dr. O'Toole and Dr. Maplethorpe and certain NIH officials. The authors of the paper were not invited to testify, nor were we even informed that an investigation was underway. Prior to the meeting, Mr. Stewart and Dr. Feder called up certain newspaper reporters and briefed them. They refused to talk to other reporters (from whom we first heard about the hearing), saying they were "already working with other reporters."

Thus, in the few days before the hearing there were newspaper articles about the O'Toole-Imanishi-Kari dispute throughout the country, including all of the major newspapers. Although we offered to as many reporters as would listen as complete an explanation as we could, our story was not as "flashy" as that profferred by Mr. Stewart and Dr. Feder. With the exception of the Washington Post and the Los Angeles Times, we fared badly. The most damaging article to me personally was in the Boston Globe, one from which I have not yet recovered. I am personally shocked that the press, with few exceptions, would investigate such a serious matter so carelessly and present such an unfair story.

We have not yet seen the end of this. The Dingell subcommittee continues its investigation and has asked, through NIH, for MIT and Tufts to literally empty their files of everything pertaining to the situation. A letter was sent by the subcommittee counsel, Mr. Michael F. Barrett, Jr., to NIH on May 4, 1988, and demanded that all of the data be supplied the next day. The subcommittee's chief investigator, Mr. Peter Stockton, who was quoted in the Boston Globe making highly inflammatory and condemnatory statements about the authors of the Cell paper, has been aggressively attempting to schedule interviews with some of the authors. For example; he called Dr. Imanishi-Kari at home on her unlisted telephone number at 10 o'clock at night. Meanwhile, I have never been contacted by him or any other member of the subcommittee or its staff on this matter.

We expect further hearings. The announced focus of the subcommittee's concern is the manner in which accusations of fraud or misconduct are handled by the NIH and its grantees. But the actions of the investigators make it clear that Dr. O'Toole's allegations will continue to be a focus of the subcommittee's activities. They appear to plan to judge the science through the hearing process, a totally inappropriate forum for deciding scientific questions. I am advised that I personally am likely to be a target of their questioning, an unpleasant process that will make headlines at my expense.

I believe this is all totally unnecessary. Dr. O'Toole never charged fraud and has avoided that characterization. She believed in the beginning that there were alternative interpretations that should have been given prominence. It is my understanding that only Dr. Maplethorpe claimed "fraud," and he, like Dr. Feder and Mr. Stewart, has little knowledge in this issue. His cry was picked up at the hearing by Congressmen, unfortunately, and the word was used liberally in the press.

IV. The Aftermath

Many friends and colleagues have sent word of their support either directly or through others and I value the sentiments. Many have asked what they can do to help and there is little to recommend except letters to Representative Dingell and his committee and letters to Dr. James B. Wyngaarden encouraging a rapid and complete review by NIH.

It is hard to know when and how this will end. I am inured to the necessity of public testimony in an atmosphere created by the one-sited publicity and proceedings that have gone before. One evidence of the approach of the subcommittee is that Mr. Stewart has become a committee investigator, "on loan" from NIH.

NIH is finally getting a group of immunologists together to review the paper, as I had asked a year ago and repeated recently. But, despite my urging, it seems to be taking a very long time to get off the ground. I firmly believe that this panel - or any other qualified scientists - who look dispassionately at all of the records and experiments will conclude that the published paper appropriately reflected the state of the science at the time it was written.

Whether that point will ever come across to the Congressional subcommittee, or to the public at large, is problematic. But I take solace in the knowledge that the scientific community will know and understand. What we are undergoing is a harbinger of threats to scientific communication and scientific freedom. The halls of Congress are not the place to determine scientific truth or falsity. NIH must put in place procedures that will protect us from such investigations and that will neutralize the activities of such as Mr. Stewart and Dr. Feder by quickly responding to charges of fraud and misconduct.

Several scientific societies have begun to take the issue of scientific misconduct and fraud more seriously; they will perhaps encourage more rigorous NIH procedures. As long as such procedures are effective against fraud and do not impede scientific progress, I would support them. The pressure to deal with fraud directly is too great to resist, but I worry that over-regulation might impede scientific progress or scare off younger scientists, especially those with controversial or progressive ideas.

These are difficult times for those of us who pursue knowledge in the biological sciences. I see this affair as symptomatic, warning us to be vigilant to such threats, because our research community is fragile, easily attacked, difficult to defend, easily undermined. What is now my problem could become anyone else's if circumstances present themselves.



David Baltimore