For the past dozen years or so, any-one even vaguely interested in sci-ence has followed the Baltimore case with all the fascination of witnessing a slow-motion pileup of cars on a foggy freeway. Headlines have alternated between declaring that the Nobel laureate David Baltimore and his co-worker Thereza Imanishi-Kari were either guilty of scientific fraud or cleared of all charges. Federal oversight committees also alternated between finding Baltimore and Imanishi-Kari innocent and guilty. Congressional hearings claimed to expose a rot that was affecting science at its very roots. Baltimore’s colleagues joined in defending or attacking him. Such controversies in science puzzle the general public. Why are these scientists behaving so badly? Scientists are supposed to be dispassionate seekers after truth. Why all these charges and countercharges?
Quarrels in science are chiefly of two sorts—those that concern credit and those that concern accuracy. In the early days of science, all that scientists could hope to receive for their years of work was the acknowledgment of their contributions by their peers, the people who know most about the value of their work. In science the first person to make a discovery public gets the credit—all the credit. There are no silver medals in science. This system was devised to force scientists to publish their findings so that others could use them. A scientist might postpone publishing a crucial result so that he could mine it for additional discoveries, but only at the peril of being scooped. This system has worked well; but in the rush to publish, too much gets published too quickly.
In most cases of disputes over priority, only the people working in the relevant scientific community decide who gets credit for which discoveries. However, once in a while claims of priority become of more general interest because the discovery is so momentous or because large amounts of money are involved. The dispute between Robert Gallo and Luc Montagnier over who first discovered the AIDS virus combined both factors. When hundreds of thousands of people are dying, how could these two scientists take up so much time and so many resources bickering over who discovered the virus first? Of course Gallo and Montagnier want credit for their contributions. But in the face of the newest and probably most lethal plague human beings have ever known, mightn’t these two scientists have bent their individual ambitions and lust for money a bit for the greater good?
To many people quarrels among scientists over credit appear a bit unseemly. Quarrels over empirical matters such as the accuracy of data strike us as more important. That is what science is all about—finding out what causes AIDS, deciding the role that genes play in alcoholism, working out the implications of “strings” in physics, etc. When scientists and students of science claim that science is self-policing, this is what they mean. Scientists use each other’s work. If it helps them with their own research, well and good, but if it contains faults, scientists try to find out why. If they trace the error back to you, you are in real trouble. The worst thing that one scientist can say about another is that you can’t trust his results. The reason that scientists police each other as well as they do is that it is in their own best self-interest to do so.
Numerous disputes over alleged faults in science have become very nasty down through the years, but I think that what has come to be known as the Baltimore affair has blown up into the biggest controversy over fraud and accuracy that we have ever known. The controversy grew out of a paper published in 1986 in Cell by David Weaver, Moema H. Reis, Christopher Albanese, Frank Constantini, David Baltimore, and Thereza Imanishi-Kari.1 In 1986 the immune system was the hottest topic in biology, not just because of AIDS but because of its inherent interest. Nobel prizes seemed to be lying in wait for anyone making a major contribution to unraveling the complexities of the immune system.
The experiment that produced all this controversy was conducted by Imanishi-Kari and her co- workers, in particular Moema Reis, in one of the labs supervised by David Baltimore at the Whitehead Institute of the Massachusetts Institute of Technology. The immune system produces vast numbers of antibodies and, in certain strains of mice, antibodies display a distinctive chemical feature called an idiotype that is akin to a birthmark and can be used to tell one antibody from another and to study the inheritance of genes that produce the antibody. All but a small number of antibodies are reabsorbed in the body without ever having encountered an antigen, but very rarely the binding site of an antibody matches some part of an antigen. Immediately this particular antibody is reproduced in huge numbers and attacks the antigen. In most cases, the attack is successful, the organism survives, and the immune system returns to its former quiescent state.
The experiments performed by Imanishi-Kari and Reis started with two strains of mice, one black, one white, that were so highly inbred that they had lost most of their genetic heterogeneity, although quite obviously not all of it because the genes for coat color differed from one strain of mice to the other. Moreover, the genes in their immune systems that coded for particular antibody types were different. A gene that codes for a particular antibody missing in the black mice was extracted from white mice and transplanted into the fertilized eggs of black mice; it was thereafter termed the transgene, and the mouse that now carried the gene in every cell of its body was called a transgenic mouse.
To the surprise of Imanishi-Kari and her co-workers, the antibody normally produced by the transgene appeared in the newly born black mice. How come? Although several explanations presented themselves, the one that was emphasized in the ensuing paper was “idiotypic mimicry.” The transgene itself, Imanishi-Kari said, did not turn on and produce these foreign antibodies but somehow caused the immune system of the black mice to produce antibodies that mimicked those of the white mouse. Although this paper was only one small step toward understanding the immune system, its implications for treating damaged immune systems looked promising. The results of this research were published in the April 25, 1986, issue of Cell.
Daniel Kevles’s The Baltimore Case is an immensely detailed chronicle of the people and politics surrounding the genesis of this paper and its eventual fate. No one in the future is likely to match Kevles’s scholarship, let alone surpass it. Kevles begins his book with objective, disinterested descriptions of who did what to whom, but as the injustices to Baltimore and Imanishi-Kari begin to pile up and the behavior of some of their opponents becomes tawdry, he cannot even pretend to be a detached observer hovering above the battlefield. Increasingly he describes contradictions in testimony, lapses in memory, the hypocrisy of some of Baltimore’s critics, and the duplicity of the politicians and bureaucrats who became involved in the case. His heroes are not the whistle-blowers who criticized the research for the Cell paper but the two scientists who stood their ground against unrelenting and increasingly powerful persecution.
Kevles begins by introducing his three main characters, along with several others who played less important parts. David Baltimore taught himself molecular biology while an undergraduate at Swarthmore College and earned a doctorate at Rockefeller University in 1964, when he was twenty-six. His first job at the Salk Institute was cut short after he became politically active in opposing the Vietnam War. In 1967, Kevles writes, “when several pieces of art were removed from an exhibit…because they were said to use the American flag improperly, he quit, protesting censorship”; and he then went to work at the Massachusetts Institute of Technology. In 1970 both he and Howard Temin published papers in the same issue of Nature reporting the discovery of reverse transcriptase, a crucial enzyme in the process by which a certain kind of virus—a retrovirus—invades a cell and commandeers its molecular mechanism to make hundreds of copies of itself.
The “simultaneous” discovery of this enzyme independently by two different researchers might have led to a nasty dispute over priority. Even though Temin had anticipated Baltimore by a matter of days, neither man attempted to take sole credit for himself. Instead they published their findings simultaneously, and both received the Nobel Prize for their joint discovery in 1975. One wonders whether had Gallo and Montagnier behaved in a similar way they too might have won the Nobel Prize long ago, instead of battling over who stole what from whom. Once they realized that this behavior was ruining any chances that either man had for being awarded the prize, they published a joint paper, but by then the damage had been done in the eyes of the Nobel Committee, and no prize was forthcoming.
Imanishi-Kari’s journey to MIT was as circuitous as Baltimore’s was direct. Her parents were Japanese immigrant tenant farmers who worked a plot of land near São Paulo, Brazil, and ran a small fleet of rickety trucks. They opposed further schooling, beyond college. Eventually, however, Imanishi-Kari was allowed to go to Kyoto University to do graduate work in biology. While completing her graduate training in Finland, she married a Finnish architect, Markku Tapani Kari. Next she moved to Cologne, Germany, for her postdoctoral work. In 1981 she was hired by MIT as an assistant professor. By then she had a daughter and her marriage was beginning to unravel. When Imanishi-Kari first took the job at MIT’s Whitehead Institute, she was warned that it was a “sea full of sharks” and that getting tenure would prove to be quite difficult. In fact, in 1985 she was informed that she would not be awarded tenure at MIT, but by then she already had the promise from Tufts University of a job that could lead to tenure.
The person who was central in transmuting Kevles’s story into a tragedy is Margot O’Toole. In 1973 O’Toole graduated from Brandeis University with honors in biology. Instead of proceeding directly to graduate school, she worked as an assistant to a young immunologist at Harvard University for a year. She then began her graduate training in 1974 at Tufts University Medical School, working with the respected immunologist Henry Wortis. In 1978 O’Toole married Peter Brodeur, one of Wortis’s graduate students, and in 1979, after receiving her Ph.D., O’Toole and her husband began postdoctoral studies at the Fox Chase Cancer Research Center in Philadelphia. Her work in Donald Mosier’s labs did not go well, and she moved on to work with Melvin and Gayle Bosma. In a story that is all too familiar, O’Toole had a baby and followed her husband back to Tufts when he was offered a tenure-track job. Wortis got her some temporary space at Tufts until her postdoctoral fellowship ran out. It was at this point that O’Toole was introduced to Imanishi-Kari, who offered her a one-year “postdoc” at MIT. As O’Toole remembers their conversation, Imanishi-Kari also promised to help her get a tenure-track position at Tufts when her postdoc job came to an end.
When O’Toole began working with Imanishi-Kari, both women were at critical points in their careers. O’Toole had to get a tenure-track job very soon or else she would be stuck forever as a lab assistant. Imanishi-Kari had already failed to get tenure at one university. The next was crucial. The first task that Imanishi-Kari assigned O’Toole was to “extend” the work published in the Cell paper, not replicate it. That is, she was not set the task of redoing the experiments that Imanishi-Kari and her postdoc assistant, Moema Reis, had already performed. She was asked to find out how idiotypic mimicry, the process that was central to the conclusion of the Cell paper, actually occurred. For all the talk about the importance of replication in science, scientists rarely spend much time replicating each other’s work. If a new set of data fits nicely with your own, you incorporate it into your work without using precious resources for checking. Serious tests are reserved for those findings that conflict with others. In general, scientists assume that any errors in earlier papers will show up later when others use the results of these papers.
In order to extend the work of Imanishi-Kari and Moema Reis, O’Toole had to master the complicated techniques that they had used to investigate very intricate molecular reactions. Almost everything of interest was going on at levels far below our perceptual level; all sorts of methods had to be devised to estimate, very indirectly, how the various chemical reactions were proceeding. For example, an antibody called Bet-1 had been developed as a reagent, or active substance, to distinguish between the idiotypes of foreign antibodies and those that the mouse under study produced. O’Toole was having a great deal of difficulty getting Bet-1 to make the distinction. She could not get it to work in the same way that it had for Imanishi-Kari and Reis. By then Moema Reis had returned to her native Brazil. When O’Toole reported her difficulties to Imanishi-Kari, the older woman was dismissive. Perhaps, she implied, O’Toole was not cut out to be a research scientist.
O’Toole was extremely frustrated. Her career in science was at stake. Was she at fault or were the results reported in the Cell paper mistaken? It took a while, but eventually O’Toole decided that she was right and the Cell paper was wrong. What confirmed her in her views was the discovery on May 7, 1986, of seventeen pages of lab notes that Reis had left when she returned to Brazil. They contained the raw data that part of the Cell paper was supposedly based upon. O’Toole discovered significant discrepancies between these data and those reported in the Cell paper. What should a young scientist do in such cases? O’Toole’s earlier protests to Imanishi-Kari about Bet-1 had not gotten her very far. She raised the issue with Henry Wortis, her former adviser, and Herman Eisen, the head of the immunology department at MIT. Both men met with her but concluded that she was over-reacting. O’Toole disagreed.
As a result of O’Toole’s persistent prodding, Wortis formed an ad hoc committee to look into the matter. The members of this committee went over Imanishi-Kari’s data with her. Right away they discovered a minor error. One of the mice that Reis had used had been recorded as a normal mouse when actually it was a transgenic mouse. At this meeting Imanishi-Kari was unable to find some of the data requested, but she produced them the next day. She also complained that her integrity was being questioned. The conclusion of the members of this ad hoc committee was that no serious flaws could be found in the Cell paper. One mistyped mouse did not undermine the entire paper. O’Toole would not accept that conclusion. Another meeting was organized, and this time O’Toole was present. Once again, in spite of her arguments, no one could find serious flaws in the Cell paper. At the end of the meeting, O’Toole offered her hand to Imanishi-Kari, but Imanishi-Kari would not accept it.
O’Toole continued to raise objections to the Cell paper, and Eisen organized a second ad hoc committee. The results were the same: the group found a couple of minor errors, that was all. In the memo that she wrote describing her position at the time, O’Toole not only complained about the inadequacy of Bet-1 and other reagents used in the experiment but also proposed her own explanation of the appearance of the foreign antibodies in the black mice. The transgene, she suggested, actually did turn on and start making antibodies of its own. In fact, she believed, most of the antibodies produced came from the transgenes.
From the beginning, the scientists whom O’Toole approached urged her either to lodge formal charges or to let science run its usual course. Further research would indicate who was right on these issues. O’Toole could not bring herself to lodge a formal complaint, especially if it alleged fraud rather than just error. And here the matter would have rested had it not been for a shadowy figure, Charles Maplethorpe, who appears and disappears at crucial times in the controversy. While he completed his MD, Maplethorpe returned to MIT to earn a doctorate in immunology. Because he did not get along with the junior faculty member to whom he had been assigned, he was transferred to Imanishi-Kari’s lab, but his relations with her disintegrated even more rapidly, in part because he thought that Imanishi-Kari was not giving his work as much credit as it deserved. Relations got so bad that eventually Imanishi-Kari formed a committee with the sole intention of finding some way for Maplethorpe to get a Ph.D. so that she could be rid of him.
Even though O’Toole and Maplethorpe overlapped in Imanishi-Kari’s lab for only a short time, O’Toole remembered him as being sympathetic and helpful. Early in the controversy, she sought out Maplethorpe to complain to him about the trouble she was having. Although he was even more critical of Imanishi-Kari than O’Toole was, he advised caution. Would he come forth with his own charges against Imanishi-Kari? “Yes,” he said, “but only at the appropriate time.”
In May of 1986 Maplethorpe heard about two staff members of the National Institutes of Health who had taken it upon themselves to investigate fraud in science—Ned Feder and Walter Stewart. He called them about O’Toole’s problems but did not reveal her name. Not until the end of July did Maplethorpe inform O’Toole of his actions. Initially, she was angry, but she allowed him to reveal her identity to Feder and Stewart as long as they promised that she would not have to take an active part in the investigations, a promise that they did not and could not keep.
At the time, a husband and wife team at the Stanford School of Medicine, Leonard and Leonore Herzenberg, were conducting experiments similar to those being carried out by Imanishi-Kari. In the fall of 1986 Leonore Herzenberg called Henry Wortis to inform him that they were getting results different from those reported by Imanishi-Kari, and she asked Wortis to pass on this information to Imanishi-Kari. A year later, as part of their ongoing investigation, Feder and Stewart contacted the Herzenbergs. On November 6, 1987, the Herzenbergs wrote Baltimore to inform him that Feder and Stewart had sent them a copy of the report the two NIH investigators were writing about the Cell paper. The Herzenbergs warned Baltimore that they were having a great deal of trouble with Bet-1; in addition, they said, a more plausible explanation of their results was suggested by O’Toole’s hypothesis, not by Imanishi-Kari’s conclusion of idiotypic mimicry. Mightn’t Baltimore, they asked, publish a joint letter with O’Toole in Cell presenting her views? The Herzenbergs also wrote that they might consider inviting O’Toole to Stanford to work with them. In his response Baltimore was less than enthusiastic about both of these suggestions, and the Herzenbergs dropped the matter.
The research for the Cell paper was supported in part by grants from the NIH. No formal committee existed in the NIH at the time to look into charges of misconduct. A staff member, Mary Miers, was in charge of such inquiries. At the prompting of Feder and Stewart, Miers formed yet another ad hoc committee to look into the charges.
In the midst of these deliberations, Congressman John Dingell, the chairman of the House Energy and Commerce Committee, saw Baltimore and Imanishi-Kari as providing an easy target for an investigation. Congress has the right to hold hearings on any topics that they see fit. Unfortunately, the procedures for such hearings in both the House and the Senate can easily be abused and they frequently are, most notably in the late 1940s and 1950s by the House Un-American Activities Committee and by Senator Joseph McCarthy. Whatever the official purpose of such committees may be, they are often more drawn to television theatrics than to sober searching after truth, and Dingell’s hearings about the Baltimore affair were no exception. As chairman of the House Subcommittee on Oversight and Investigations, Dingell could range freely over such issues as $700 toilet seats, $250 shower curtains, and instances of fraud in science.
I must admit that I enjoy the embarassment of bureaucrats when at long last they are called to account for cost overruns of three and four times the original estimates, or of tobacco company CEOs when they parrot the party line that smoking has nothing to do with lung cancer. Of course, when the hearings are over, everyone returns to business as usual, but for a brief moment the general public can see big shots squirm. But how about well-known scientists? Do they deserve the same treatment? Is misconduct in science so prevalent that congressional exposés are called for?
The first congressional hearing on the Baltimore affair took place on April 12, 1988. The only witnesses called were those critical of Baltimore and Imanishi-Kari. In her testimony, under extremely gentle questioning, O’Toole came across as sincere, brave, and only slightly naive. Who could not feel sympathy for this clear-eyed young woman who thought she was only doing her duty and believed her career had suffered as a result. Following her testimony Baltimore sent an open letter to four hundred scientists around the country on May 19, 1988. In this letter he defended the Cell paper and denounced Dingell for trying to determine scientific truth in committee hearings; but he also expressed doubts about Imanishi-Kari’s theory of idiotypic mimicry as an explanation of her results. Later, in a paper that he coauthored with the Herzenbergs, Baltimore reiterated his doubts about idiotypic mimicry.
Baltimore and Imanishi-Kari were not called before Dingell’s committee until a year later, in 1989. To some observers, Baltimore did more than hold his own against Dingell, arguing that the questions raised about the Cell paper did not warrant a congressional inquiry. But others thought that he came across as too arrogant and unbending. In the literature on the Baltimore affair, everyone seems obliged to mention how arrogant Baltimore is. But no one explains the connection between modesty (a Christian virtue) and doing first-rate science. Baltimore was capable of making public corrections in the face of scientific data—as he did in his letter to the four hundred scientists—but not of exhibiting humility before Congressman Dingell. Imanishi-Kari was a much more sympathetic witness as she struggled with the English language. Dingell’s hearings dragged on for five more years.
In June of 1988 a reconstituted NIH panel looked into the case against Imanishi-Kari and, indirectly, Baltimore, who continued to support his more junior and more vulnerable collaborator as having acted with integrity as a scientist, whether she was right or wrong in her conclusions. Even though Imanishi-Kari had tried to organize her laboratory notes in preparation for testifying, the members of this panel were dismayed by how sloppy they were. Instead of bound notebooks in which daily activity is recorded and dated, the image that the term “laboratory notebook” brings to mind, Imanishi-Kari presented pages torn out of spiral notebooks, scraps of paper stuffed into folders, and bits and pieces of “counter tapes.” These last were crucial to her case. In molecular biology and biochemistry, the numbers involved are so huge that human beings often cannot record each reading of experimental results by hand. To determine whether specific antibodies were present in a mouse’s body, and in what quantity, Imanishi-Kari used a complex laboratory apparatus to measure the intensity of the radiation given off by the radioactive reagent, Bet-1, which was bound to the antibodies. The radiation counter was hooked up to a teletypewriter that printed a record of the results on rolls of paper—the counter tapes.
Imanishi-Kari had many tapes to show the committee, but in her testimony she admitted, “I am not a neat person.” She often left her counter tapes in file folders or drawers, or even on windowsills, for months until she could no longer stand the mess. After the hearings were over, the members of the panel requested that Baltimore and his coauthors write a letter to Cell correcting the errors that the panel members found in their original paper. According to Kevles, Baltimore was not happy about this, but he knuckled under and sent a note to Cell mentioning, among other technical errors in the original paper, the problems that had subsequently arisen with the Bet-1 reagent. (Baltimore did not include any reference to the mistyped mouse; it was too trivial.) In July of 1988 Dingell subpoenaed all of Imanishi-Kari’s laboratory records and turned them over to the Secret Service for investigation.
Baltimore’s letter appeared in Cell on November 18, 1988, the same day that the NIH misconduct office mailed out copies of its draft report. Although the members of the panel discussed various problems with the Cell paper, they concluded that “no evidence of fraud, conscious misrepresentation, or manipulation of data was found.” Needless to say, O’Toole and her supporters were not happy about this statement, but the Baltimore camp was also displeased when the panel members subsequently complained that the letter to Cell had not gone far enough. Baltimore, the panel members said, should send yet another correction to Cell. In spite of protests from both sides, the panel declined to change anything in its original draft report, which was published in January 1989.
As Dingell continued his hearings, he leaked to the press the results of the Secret Service investigation. The findings were devastating. Imprints of dates on later pages of Imanishi-Kari’s notebooks could be discerned on earlier pages. Analyses of the ink and paper on various counter tapes also showed that they were seriously out of sequence. On the basis of such evidence, the Secret Service concluded that at least 20 percent of the material in one crucial notebook was “forensically questionable.” In view of the evidence being uncovered by Dingell, the NIH reopened its investigations in April of 1989, this time under the newly created Office of Scientific Integrity (OSI). With all the publicity that the Dingell hearings were getting, the NIH had to show that it, too, was capable of policing the scientists whom it was supporting.
In November of that year, Suzanne Hadley became acting director of the OSI with every expectation of eventually becoming director. However, in 1990 Jules Hallum was appointed director, and Susan Hadley had to settle for deputy director. It was also at this time that Baltimore learned that he was a candidate to become president of Rockefeller University. In spite of all the criticism that he had received with respect to the Imanishi-Kari case, he was offered the position and was installed as president on July 1, 1990.
As deputy director of the OSI, Hadley took on the two most visible cases then under investigation—the priority dispute between Gallo and Montagnier and the case involving Baltimore and Imanishi-Kari. It did not take long for Hadley to decide that Gallo did not deserve credit for discovering HIV and that Baltimore and Imanishi-Kari were guilty. In the case of Imanishi-Kari, Hadley wrote a draft report of the NIH panel’s deliberations. Even though two of the five members of the panel dissented, Hadley found Imanishi-Kari guilty of two charges of fraud as well as other lesser offenses. Baltimore, according to Kevles, was deeply upset by this development. It is one thing to have politicians accuse a scientist of misconduct. It is quite another to have a panel of one’s peers make similar charges. In the face of the forensic evidence and the OSI report, Baltimore withdrew his support of Imanishi-Kari and stated publicly that he retracted the Cell paper. He even made overtures to O’Toole, but by now she was implacable. No longer was she content to charge error; she had now become convinced that Imanishi-Kari had committed outright fraud. By the end of 1991, the criticism of Baltimore became so intense that he resigned his job at Rockefeller and planned to return to MIT.
As in Victorian novels, when the night becomes darkest a savior appears. As Kevles sees it, this role was played by Bernadine Healy, who became head of the NIH in 1991. According to Hallum, oversight committees are engaged in scientific, not legal, investigations and scientists therefore do not have or need the protection of due process. Healy changed all that. She was under pressure to do so, since more and more scientists who had been criticized by scientific panels were taking their cases to court and having their condemnations reversed because of total lack of due process. Before Healy arrived as director of the NIH, Hadley left the OSI for an assignment in another section of the NIH. However, she continued as chief investigator for the Gallo and Imanishi-Kari cases. Hadley tried to remove one of the dissenting members of the NIH panel, but the other panel members came to her rescue. Because of rumors that Hadley maintained too close a relationship with O’Toole, Healy asked for Hadley’s telephone logs. When Robert Lanman, a legal adviser to the NIH, showed up at Hadley’s office to ask for her notes, Hadley protested that her integrity was being questioned, the same protest that Imanishi-Kari had made five years earlier.
On July 1, 1991, Hadley resigned her responsibility for the two cases and took a leave of absence. At the end of 1991 she returned to the NIH, taking what she termed “a nothing job” developing science education projects. Kevles writes that an informant had told Hallum that Hadley was leaking documents to the Dingell subcommittee. When Healy found this out during the weekend of March 7, 1992, she had the locks on Hadley’s office changed so that she could enter only under supervision. To say the least, Dingell was displeased. One of the few bureaucrats who was willing to take a strong stand was being silenced. He asked that Hadley be reassigned to his subcommittee, but Healy refused. When Dingell went all the way to the Secretary of the Department of Health and Human Services, she relented, and Hadley was assigned to work with Dingell’s subcommittee for a period of six months. Dingell then turned his attention to Healy.
In 1990, while Healy was director of the Cleveland Clinic research institute, a junior scientist at the institute accused a more senior scientist of misrepresenting data on a grant application. Healy formed a committee to look into the allegations, which concluded that the senior scientist was guilty of sloppiness, not fraud. Later, when additional documents became available, Healy set up another inquiry which nevertheless reached the same result. Because the accusations concerned the use of NIH grant money, she forwarded the results of her inquiries to the NIH. When she became director of the NIH, Healy recused herself from all matters dealing with the OSI’s investigations into the Cleveland Clinic affair. In response to Healy’s treatment of Hadley, Dingell began a probe of the Cleveland Clinic affair and called Healy as a witness. According to Kevles, a high official of the Department of Health and Human Services urged Healy to grovel before Dingell if she wanted to avoid trouble. She refused. In late 1992 the NIH found the senior scientist at the Cleveland Clinic guilty of misconduct.
Finally, in 1992, six years after the controversy began, Imanishi-Kari’s lawyers were able to cross-examine her accusers and gain access to her original notebooks. They turned all the forensic evidence over to their own experts, who proceeded to challenge the highly circumstantial conclusions produced by the Secret Service. The pages may have been presented in confused order, but no longer did the counter tapes seem all that convincing as evidence of fraud. In July 1992, the US prosecutor, Richard D. Dennett, announced that he would not seek a criminal indictment against Imanishi-Kari because he thought that the case was essentially scientific and too complicated for a jury to understand. Baltimore promptly retracted his earlier retraction. The case, however, was not over. It still had four years to go.
One month before Dennett declined to prosecute Imanishi-Kari, the Office of Scientific Integrity was removed from the NIH and reconstituted as the Office of Research Integrity (ORI) within the office of the assistant secretary for health. The ORI promptly turned the case over to a three-member committee—John D. Dahlberg, an immunologist; Barbara Williams, a geneticist; and James Mosimann, a statistician. By this time in his account Kevles has convinced his readers that Imanishi-Kari was basically innocent of all charges. However, two years later, in October 1994, the Dahlberg committee produced a report for the ORI. In the earlier draft report, Imanishi-Kari had been convicted of only two instances of misconduct. The Dahlberg committee concluded, to the contrary, that she was guilty on almost all counts—nineteen in all. For example, in the early draft report Imanishi-Kari had been accused of only two counts of fraud—one involving her data on subcloning, the other concerning data on hybridomas (hybrid cells that fuse a normal cell with a cancerous cell). To these the Dahlberg committee added seventeen others, including the fabrication of the data showing the specific action of Bet-1. How could two committees come up with such different conclusions? The Dahlberg committee employed much less stringent standards of proof. As punishment, Imanishi-Kari was barred from receiving NIH funds for ten years.
The controversy had now been going on for almost nine years and had cost untold millions of dollars. Tufts responded to Dahlberg’s report by suspending Imanishi-Kari from her tenure-track job, although they allowed her to continue to work in her lab while she appealed the decision. To hear her appeal, the Department of Health and Human Services appointed a three-person board made up of an immunologist and, for the first time, two lawyers. The ORI desperately needed to win this case because it had suffered a series of humiliating defeats with respect to the Gallo case. Then, in the May 27, 1996, issue of The New Yorker, Kevles published a fourteen-page article defending Baltimore and Imanishi-Kari. One month later the appeals board presented its findings.
Item by item and point by point, the panel concluded that, according to legal standards of proof, the allegations against Imanishi-Kari had not been proven. In particular, they could not see why Imanishi-Kari, if she had made up the data published in the Cell paper, would set O’Toole the task of discovering the mechanism that produced these faulty data. On July 21, 1996, the appeals board concluded that for none of the nineteen charges against Imanishi-Kari had the ORI proved its case by a “preponderance of the evidence.” Tufts promptly returned her to her tenure-track job and at long last promoted her to associate professor with tenure in June of 1997. For over a decade committees of scientists and bureaucrats had been wrangling over the Baltimore affair, and now she was not far from where she had started.
What of the others? In 1990 Mark S. Ptashne, a prominent Harvard biologist who had criticized Baltimore’s work, got O’Toole a job as a technician in the Genetics Institute, which he had founded in 1981. She took a leave of absence to have another baby and then returned to work as a full-fledged research scientist. In 1993 the NIH abolished Feder and Stewart’s laboratory, prohibited them from doing further work on scientific misconduct, and assigned them administrative jobs. In 1994 Dingell lost his chairmanship of the House Energy and Commerce Committee as well as of the Subcommittee on Oversight and Investigations when the Republicans became the majority party. Healy was forced out of the NIH in 1993, ostensibly because of her abrasive manner. She ran for senator in Ohio and lost. She is currently Dean of the Ohio State College of Medicine. In 1997 Baltimore was named president of the California Institute of Technology.2
Are there any lessons to be learned from this monumental fiasco? The most important is that rather than resorting to committees to resolve disputes, science should, where it is possible, be allowed to run its usual course of continued experiment. Certainly university committees have not shown themselves to be all that effective or fair in adjudicating cases of alleged misconduct. Federal oversight committees seem even more inept. People who have very little training and relevant experience are often asked to make decisions way beyond their abilities. Just because you are a psychologist or an immunologist does not mean that you can sit in judgment over every kind of scientific conduct and can evaluate the intricate experiments of other scientists, any more than first-rate experimentalists automatically make good administrators. The only sort of training that members of committees tend to receive is on-the-job training, and the specific history of federal oversight committees during the Baltimore case justifies serious general skepticism about them. The response of the federal bureaucracies in this case to their own repeated failures at policing science is also all too familiar. They changed the name of the Office of Scientific Integrity to the Office of Research Integrity and moved it from one place in the federal hierarchy to another.
Although Baltimore was not very good at defending the autonomy of science, I agree with him and other scientists cited in Kevles’s book that the members of the relevant scientific communities should decide the value and accuracy of scientific research. Scientists are certainly not infallible in making such judgments, but so far they have proved far superior to anyone else who has tried. If so much attention had not been drawn to the Cell paper, science would have proceeded in its usual fashion. Within a year of its appearance, scientists were questioning the article’s claims. Some of the later work supported parts of the Cell paper but, just as frequently, doubts were raised about it. As far as the paper’s central thesis is concerned, the results are by now reasonably clear. It seems that in 1986 Imanishi-Kari chose the wrong hypothesis and that, so far as we now know, idiotype mimicry does not occur. If science had been allowed to proceed as it usually does, the Cell paper would have shared the fate of most scientific papers; partially owing to the work of the Herzenbergs, among others, it would have disappeared from scientific discourse. A few references in later papers might have indicated the problems with it, but eventually even these citations would have ceased. There would have been no retractions, no breast-beating, just a silent sinking from view.
Letting scientists themselves decide the accuracy and value of their own work seems to give scientists a unique freedom. No one else lives so comfortably isolated from external checks and balances; but until those who would sit in judgment on science begin to show even minimal competence, I see no other alternative. In cases involving priority, governments have become involved, especially when money is at stake. The governments of France and the United States agreed to joint priority with respect to the discovery of the AIDS virus and, more importantly, joint profits with respect to tests for HIV. But scientists do not feel in the least bound by such decisions. An analysis comparing articles written by Montagnier and by Gallo found that in the early years following their work on the AIDS virus, Gallo’s paper was cited more frequently than the paper by Montagnier’s group, but by 1986 Montagnier surpassed Gallo in frequency of citation and has held the lead ever since.3 The relevant scientific community has decided which of the two papers should take precedence, regardless of what governments may or may not have done.
The Baltimore case also raises the question of how sloppy a scientist can legitimately be in conducting research and recording the results. Melodramatic as allegations of fraud can be, most scientists would agree that the major problem in science is sloppiness. In the rush to publish, too many corners are cut too often. Both the ease with which Imanishi-Kari admitted to being a messy person and Baltimore’s defense of this sloppiness strike me as cavalier. Baltimore grudgingly admitted that scientists must maintain more orderly notebooks, but he did not want to “straitjacket science with a preconceived notion of how notebooks should be kept.” As Kevles describes it, many others working in the same building at MIT’s Whitehead Institute kept records no more accurate and orderly than those of Imanishi-Kari.
If that institute is typical of university research, it differs very sharply from industries where possible patents are at stake. In general, scientists in such industries cannot leave the laboratory until their research is recorded and dated; they do not tuck slips of paper containing important data here and there, or submit sheets torn out of looseleaf notebooks as evidence of experiments. If scientists in industry can keep proper records, then so can university-based scientists.
Shouldn’t Baltimore or Imanishi-Kari have repeated the experiments that they reported in the Cell paper when O’Toole, the Herzenbergs, and others raised doubts about them? In retrospect, the answer is certainly yes. If they had only known how much time, money, and energy that investigation of their Cell paper was going to waste, they certainly would have taken the few weeks necessary to have done so. What if they had attempted to replicate their experiments in 1987? In view of what we know now, they surely would have come up with quite different findings. A new Cell paper would have described in detail the “improvements” that they had made in their earlier work. The new paper might also have raised doubts among scientists, and in that case the procedures described would have been repeated. Such sequences of papers are what science is all about. An unresolved issue is what contribution Baltimore and Imanishi-Kari might have made to future research on the effect of transgenes on the production of antibodies. Although Baltimore stopped working on this matter, Imanishi-Kari continued doing so. However, partly because of all the furor over misconduct in science, her papers went all but unnoticed.
I began this review by noting that anyone even vaguely interested in science has followed the Baltimore case. I must admit that throughout the course of events, I was on the side of O’Toole, Hadley, and even Dingell. I thought that problems with Imanishi-Kari’s original findings were probably the result of sloppiness. Just possibly, in the face of federal investigations, she may have “organized” her lab reports in ways that were questionable. Who knows? But it was the counter tape evidence, as first set out, that convinced me. I thought that Baltimore and Healy were trying to cover up Imanishi-Kari’s misconduct. It also did not help that in 1993 a popular book by Judy Sarasohn appeared that supported the generally held suspicions of Imanishi-Kari and her work.4 But Kevles’s meticulous scholarship has now convinced me that I had been misled by the articles published by science reporters in some of the most prestigious journals and newspapers. If you can’t depend on Science, Nature, The Wall Street Journal, and The New York Times, who can you depend on?
In the future, those interested in the Baltimore case will have to begin by reading Kevles’s book, and they probably will read no further—and that would be unfortunate on at least one count. Kevles repeatedly states that Baltimore and Imanishi-Kari were in the last analysis “exonerated.” In my dictionary “exonerate” means to “clear, as of a charge; free from blame; exculpate.” But the Appeals Board of the Department of Health and Human Services did not “clear” or “exonerate” Imanishi-Kari. The members of the board concluded that the ORI “did not prove its charges by a preponderance of the evidence.”
Kevles is so meticulous throughout his book that it is a shame that he passes so quickly over this point. In our system of law, a person is considered innocent until proven guilty, but not being able to prove that someone is guilty is not the same as their being innocent. O.J. Simpson is not innocent of killing two people. Throughout the Baltimore controversy, one of the main confusions was the use of at least three different standards of proof: those implicit in the decisions made by professional scientists working in immunology, the partially formalized standards used by governmental oversight committees, and standards of proof used in courts of law. These three standards of proof result in very different decisions. But whether Imanishi-Kari is innocent or guilty, rarely has any scientist been punished more severely. If she is largely innocent, she has suffered an egregious miscarriage of justice; but even if she is guilty on some counts, her punishment has far exceeded the significance of any of her purported crimes.
December 3, 1998
David Weaver, Moema H. Reis, Christopher Albanese, Frank Constantini, David Baltimore, and Thereza Imanishi-Kari, “Altered Repertoire of Endogenous Immunoglobulin Gene Expression in Transgenic Mice Containing a Rearranged Mu Heavy Chain Gene,” Cell 45 (April 25, 1986), pp. 247-259. ↩
Kevles, a professor of humanities at CalTech, comments, “The selection of Baltimore was as much news to me as it was to the rest of the CalTech community.” ↩
Alison Rawling, “The AIDS Virus Dispute: Awarding Priority for the Discovery of the Human Immunodeficiency Virus (HIV),” Science, Technology, & Human Values, Vol. 19 (Summer 1994), pp. 342-360. ↩
Science on Trial: The Whistle-Blower, the Accused, and the Nobel Laureate (St. Martin’s, 1993). ↩