This past year has seen a flurry of governmental activity concerned with fraud in science. Congressman Albert Gore, Jr., Chairman of the Subcommittee on Investigations and Oversight of the House Committee on Science and Technology, held hearings on this issue March 31 and April 1. Not to be outdone, Senator Orrin G. Hatch, Chairman of the Senate Committee on Labor and Human Resources, held a similar set of hearings on June 2, which were closely followed on June 5 by a special meeting in Boston of the President's Commission for the Study of Ethical Problems in Medicine and Biomedical and Behavioral Research.

Both of these latter hearings focussed on the case of Marc J. Straus, who in 1978 was the principal investigator of a research team at Boston University that submitted falsified data to the Eastern Cooperative Oncology Group as part of a project funded by the National Cancer Institute (1). When the fraud was revealed. ECOG purged all of its B. U. data and expelled the B. U. research unit from the collaborative study.

Although the NCI was notified at the time, it did not begin an investigation of the affair until two years later, after the Boston Globe had already run a five-part series on the Straus case, from June 29 to July 3, 1980. In the meantime, Straus had moved to the New York Medical College in Valhalla, N.Y., and had been awarded a three-year research grant from the NCI for aver 1.3 million dollars, of which he had already received one third.

Senator Hatch has charged the NCI with mismanagement of public funds for failing to debar a researcher known to be connected with a lab scandal from further grants.(Science 212 (1981): 1366-67.) Dr. Vincent T. DeVita, Director of the NCI, expressing concern over wasting tax dollars, nevertheless defended the Institute's decision on the grounds that the investigation of Dr. Straus for the 1978 case was not yet complete, and that he ought to be considered innocent until proven guilty. It was, after all, Straus' assistants who were directly responsible for fabricating patients' records. The new Department of Health and Human Services regulations concerning the debarment of researchers from federal grants unfortunately say nothing explicit about whether or not the principal investigator ought to be held accountable for the actions of his subordinates.

The publicity surrounding this and other cases has raised fears that there is a lot more fraud which goes undetected. In a talk presented at the Annual Conference of the Council of Biology Editors in Boston this April, Frank B. Colley expressed the view that the sensational cases of unethical conduct reported in Science are but the "tip of an iceberg." He holds the lack of interest in repeating experiments to be at least in part responsible for a rise in fraud.

Many of those who testified before Congressman Gore's subcommittee, however, do not share Galley's apprehensions. Philip Handler, former President of the National Academy of Sciences, argued that fraud with respect to significant work will ultimately be disclosed either through repeating experiments or through other developments. He furthermore refused to see undiscovered fraud in less significant work as presenting a serious problem. Even if the experiments in question are not repeated, fraudulent work will be brought to light because of the cumulative nature of science, as Donald S. Frederickson, former Director of the National Institutes of Health, has pointed cut. Questionable research will be revealed when any attempt to build on it creates insuperable difficulties.

The weak point in such arguments is that the self-correcting feature of science is designed to disclose falsity, not fraud. Honest mistakes are revealed and lucky guesses pass muster as genuine science. As Ian St. James-Roberts has reasoned, only the researcher himself knows when he has committed fraud, as only he has access to his intentions. (New Scientist 71 (1976): 481.)

It is also a mistake to argue, as William Raub of the NIH seems to do, that fraud in science is limited to a few nasty individuals in an otherwise well-policed profession. There are simply no statistics on this problem, and the suggestion is controverted by the fact that such great lights in the history of science as Galileo, John Dalton, and Gregor Mendel have been guilty of fraud. (Science 183 (1974): 1165-67.)

I believe that intentional misrepresentation of experimental data may actually be fairly widespread, but at the same time I do not see it as presenting a serious problem. Much of the hubbub has been caused by a misconception of science. It is simply a mistake to believe that scientists are, or should be, objective collec toys of facts. A proper understanding of the work of scientists will do two things: (1) it will explain why scientists have not been especially concerned with developing means of detecting and dealing with fraud, and (2) it will reveal that the extent to which it does present a problem for society, it does so only as part of a much greater problem: sloppiness in science.

The Aims of Science
Deena Weinstein has argued that fraud is a more serious problem for science than for any other institution. Representing what is no doubt a common view that science "has the pursuit of truth as its dominant value," she finds fraud to be "antithetical to the very aims of science." (Social Science Quarterly 59 (1979): 639).

The problem with this view is that it fails to distinguish among different kinds of truths, not all of which are of equal importance. Scientists are more interested in establishing the truth of theoretical claims than establishing that of claims regarding observations and experiments. Fraud is not a serious problem for science simply because it is not possible to fake a theory, regardless of how easy it maybe to fake an experiment.

At this point I can imagine the reader objecting: "Aren't scientific theories based on observed facts? Won't fraudulent observations then yield false theories?" Not necessarily. It is at least logically possible to draw true conclusions from false premises.

A deeper problem with this objection is that it relies on a distorted view of how scientists work. According to this view, scientists are supposed to begin by collecting facts without any preconceived notions or biases. These facts are then to be recorded, analyzed, and classified in order to allow the scientist to reason to a general theory concerning them. Further experiments are then performed to corroborate this theory.

This narrowly defined inductivist view of science is simply untenable. Potentially, there is a limitless number of facts in nature which a scientist may observe. The philosopher Carl Hempel asks:"Are we to examine, for example, all the grains of sand in all the deserts and on all the beaches, and are we to record their shapes, their weights, their chemical composition, their distances from each other, their constantly changing temperature, and their equally changing distance from the center of the moon? Are we to record the floating thoughts that cross our minds in the tedious process? The shapes of the clouds overhead, the changing color of the sky? The construction and the trade name of our writing equipment? Our own life histories and those of our fellow investigators?."

This problem is compounded by the fact that there will also be an indefinite number of ways to analyze and to classify any given set of facts.

In order to get his research off the ground, a scientist must have some way of distinguishing facts which are relevant to his problem from those which are not. He does this through imagining some tentative solution to his problem, which then serves as an hypothesis which he can test in the laboratory. Steven Brush quotes Einstein on this point: "But on principle, it is quite wrong to try founding a theory on observable magnitudes alone. In reality, the very apposite happens. It is the theory which decides what we can observe." (Science 183 (1974): 1167.)

But even if it is true that scientists begin with hypotheses and not with unbiased observations, the reader may ask, is it not also true that an honest scientist will reject any hypothesis which conflicts with experimental results?

Again, the answer must be "not necessarily." When a researcher confronts an unexpected turn of events in the laboratory, it is not always clear to him where he went wrong. In designing and predicting the outcome of any experiment, a scientist must make a host of assumptions in addition to the hypothesis under investigation. As a simple example, he must take the laws of optics on faith if he is to regard his telescopic or microscopic observations as reliable. In actual experiments, the situation is far more complex than this. As the philosopher-scientist Pierre Duhem has argued, in cases where a scientist has incorrectly predicted the outcome of his experiment, it is not always possible to determine which assumptions are at fault (2).

Kuhn suggests that for these reasons we have always maintained even our most important theories in' the face of anomalous experimental results, in the hope that these will eventually be explained away in such a manner that our favorite theories will not be threatened. Some, such as Steven Brush, are even willing to argue that the history of science reveals that theoretical considerations have generally carried more weight than experimental results in debates over new hypotheses. (Science 183 (1974): 1169.) A scientist is in far more trouble if his ideas conflict with our most cherished scientific theories than if they contradict a mere handful of experiments.

A scrupulous scientist will nevertheless be quite frank about the problems confronting his theory. Indeed, it is only through taking such a critical attitude that science is able to progress at all. Confronted with a troubling experiment, one hopes that through further testing one may be able to weed out those parts of one's theory which are false.

In this weeding-out process, the question of how various scientific beliefs were arrived at is irrelevant. A geneticist confronting an anomalous experiment would not be tempted to throw out Mendel's Laws simply because Mendel may have faked his experiments. (Annals of Science 1 (1936): 115.) Scientists did not revert to a theory of blending inheritance when Mendel's fraud was disclosed because his laws have received support from further experimental work. Indeed it is precisely because the question of how certain results were obtained is not always relevant to that of the truth of one's theories that science has not evolved procedures for detecting and dealing with fraud.

For this reason, when a scientist is absolutely certain that he is right, he may be tempted to represent fictions as experimental facts. This happened in the case of Robert J. Collis of the Max Planck Institute for Biochemistry in West Germany. Gallia had faked certain results concerning the levels of cyclic GMP and AMP in neuroblastoma cells and hybrid cells. He later confessed his crime in the following way:

"I wish to disclose the fact that papers published in several journals with myself as principal author are not reliable. The curves and values published are mere figments of my imagination, and during my short research career I published my hypotheses rather than my experimental results. The reason was that I was so convinced of my ideas that I simply put them down on paper; it was not because of the tremendous importance of published papers to the career of a scientist. (Science News 111 (1977): 150-51.1

Fraud and Science Policy
Although disclosure of fraud may be of little concern to scientists themselves, the reader may now object, it is important to remember that science does not operate in a social and political vacuum. Policy decisions may be based on scientific work, especially in areas concerned with health. energy, and the environment. Furthermore, society supports scientific research through its tax dollars. For these reasons society at large cannot tolerate scientific fraud.

In the case of public policy decisions, however, I submit that the problem again is one of distinguishing the true from the false rather than disclosing fraud. With respect to the testing of new drugs, for example, which the FDA has attempted to regulate since 1962, an honest mistake can have just as disastrous consequences as a deliberately fabricated report. So might an outdated theory. In order to guard against all forms of error, policy decisions influenced by the testimony of scientists ought never to be regarded as a "closed book," but rather ought to remain open to revision in the light of future scientific developments.

Fraud in science does seem to prosent a serious problem with regard to public support of research. We may want to develop some means of distinguishing fraudulent from honest work for the purpose of debarring unscrupulous scientists from receiving further grants. This is in fact one of the ends which the Department of Health and Human Services has tried to achieve through regulations established in the fall of 1980. (See story an p. 9.)

These regulations are vague and ambiguous when it comes to spelling out causes for debarment. Nowhere is the term "fraud" explicitly defined. Instead we find reference to "serious unsatisfactory performance" and to" any other cause . . . of sufficiently serious nature as determined by the Secretary to warrant debarment."

To distinguish fraudulent misrepresentation of scientific results from errors resulting from honest mistakes, as we have said, requires access to the intentions of the scientist in question. For practical purposes this often means that one cannot establish fraud unless a scientist confesses to it. John Long's cell cultures provide a case in point.

Although permanent cell lines of other kinds of human cancer cells have been around for some time, Long, a researcher at Massachusetts General Hospital, enjoyed the distinction of having been the first scientist to establish permanent cell lines from patients with Hodgkin's disease. (Science 211 (1981): 102225.) His research career had been quite successful until 1978 when a junior colleague in his laboratory. Steven Quay, obtained some unexpected results in an experiment on these cells. Quay then left for a two week vacation, and on his return, Long informed him that he had repeated Quay's experiment and obtained the expected results. Long then published these results.

Quay was incredulous, and asked to see Longs laboratory notes. Careful study of these and other records revealed that Lang had fabricated his results. When confronted with the evidence, Long resigned, but insisted that this was the only experiment he had ever faked. Nevertheless, his other work was called into question and an investigation ensued.

A troublesome problem with Longs cell lines, which he had openly admitted in his grant application to the National Cancer Institute, was that they contained a gene for a form of an enzyme found only in black people, although Long claimed to have taken his cultures from white patients. Long accounted for this anomaly by assuming that his patents must have been heterozygous-that is, that they had some genes for both the "black" and the "white" forms of the enzyme in question.

Further tests revealed that Longs cell cultures were not even of human origin, but had come from a brown-footed owl monkey. This monkey contains the enzyme in question in a farm similar to that found in blacks. Longs laboratory records revealed that he had indeed performed experiments on cells from such a monkey, and the conclusion was that cell cultures from patients with Hodgkin's disease were contaminated with monkey cells.

The question then arose as to whether this contamination was doliberate or accidental. Accidental contamination of cell cultures is, as a matter of fact, a very common occurrence. Since Long maintains that he did not intentionally tamper with his cell lines, there is no way to prove that he did.

A more thoroughgoing scientist, however, might have conceived the possibility of contamination as soon as he was confronted with the anomalous gene. Even if Lang was sincere about his cell lines, was he not also negligent in failing to pursue this lead? Should his research have been funded by the NCI to the tune of $750,000 in full cognizance of this problem with his cells?

Cases such as this raise the following question: Is it any less wasteful to support sloppy research than to support fraudulent work? A similar question could be raised in the case of Marc Straus. Even if his honesty is ultimately established, is he not guilty of failing to establish some procedures for validating the results of his research team?

The issue of the degree to which a senior investigator is responsible for the data of junior colleagues was also raised in the case of Drs. Philip Felig and Vijay Soman at Yale. Felig had co-authored a paper with Soman, who, unbeknown to Felig, had fudged some data. Although Felig is not directly responsible for any fraud in this case, is he not guilty of some sort of intellectual negligence for failing to familiarize himself with Somari s experiments? Felig admitted to an investigating committee at Columbia College of Physicians and Surgeons, where he was being considered for a faculty position, that he "was not fully conversant with the methodology of Dr. Soman." (Science 213 (1981): 115.)

A good case could be made that such carelessness ought not to be rewarded with tax dollars for further research. I suspect that more money is wasted through sloppy research practices than through outright fraud. In the Straus case, we recall, Dr. DeVita justified the decision to award Straus a new grant on the grounds that it had not been conclusively established that Straus was guilty of fraud.

Senator Howard M. Metzenbaum suggested that the practice of assuming a suspect innocent until proven guilty may not be appropriate in this context. (Science 212 (1981): 1367-69)'I`his point has been elaborated by St. James-Roberts:"No doubt an argument could be made for something along the lines of the legal system to determine sufficient ground for intent and lack of it. Parsimony suggests that a more realistic approach may be to assume guilt unless evidence dictates otherwise. Such an approach may seem odious and may be less than fair on occasion, but it can be justified using the argument that the scientist's first responsibility is to be critical of his work. We may also reasonably ask whether such careless individuals are likely to prove of benefit to science, their colleagues, or themselves by remaining in research. (New Scientist 72 (1976): 469.)

This principle could, of course, be pushed too far. We do not want to debar every scientist who makes a simple mistake. Indeed, it can be argued that we learn through our mistakes. At the June 5 hearings of the President's Commission regarding his case, Straws argued that it would be "unrealistic" to hold a principal investigator accountable for all the results submitted by his research team (3).

Dr. Kenneth J. Ryan of Harvard Medical School, who was present at this investigation, agreed that the accountability of the principal investigator for the actions of members of his research team "should not be absolute." He then attempted to define the investigator's responsibilities as follows:

(1) having proper procedures for the selection of research personnel.

(2) giving proper instructions to the members of his team.

(3) having sound procedures for monitoring or auditing the conduct of the research.

(4) keeping up-to-date on the progress of the research.

(5) protecting him/herself against charges of misconduct.

Although same such provisions as these would be a welcome addition to the present HHS debarment regulations, and might save the tax-payer the expense incurred through erroneous research due to carelessness as well as fraud, these provisions as stated would be difficult to apply. What constitutes "proper procedures and instructions" and "sound procedures?" How would government agencies be able to obtain evidence that a researcher had been careless in any of these ways? In practice, it may prove to be more difficult to sanction a researcher for carelessness than for outright fraud.

Conclusion:
A moral philosopher might object to my analysis on the grounds that it considers fraud strictly in terms of its consequences. Don't we have a duty always to tell the truth, regardless of the casts?

However, one must be careful not to confuse lying with fraud. To maintain that honesty is absolutely obligatory would be to prohibit the socalled "white lie" as well as fraud. Fraud is distinguished from lying in general in so far as fraud is defined as intentional misrepresentation which results in some harm.

For this reason, I have found it necessary to weigh the seriousness of fraud in science on the basis of the damage it may cause. In this regard, carelessness proves to be a more important problem in science than fraud.

Indeed, one of the consequences of sloppiness in science is that it may tempt a scientist to commit fraud. Long and his cell cultures provide a case in paint. The famous "patchwork mouse" affair provides another. Summerlin had successfully transplanted a white patch onto a black mouse. The significance of this result was challenged by Medawar, who suggested that Summerlin had performed this experiment on a heterozygous mouse (Science 184 (1974): 544-50.)

That is, if the black mouse had one white parent and one black parent, a successful skin graft from a white mouse would come as no surprise. On the other hand, if Summerlin could produce a white mouse with a successful skin graft from a black mouse, he would have a significant result, since white mice can only come from two white parents.

In short, Medawar was implying that Summerlin was a careless researcher. Summerlin had no choice but to produce a white mouse with a black patch. Repeated failure led to his desperate painting of two white mice. If he had given more careful thought to his original experiment with black mice, he might have saved himself from this predicament.

Footnotes
1. My information of the Straws case derives from testimony presented to Gore's subcommittee by Alexander Capron and Barbara Mishkin of the President's Commission for the Study of Ethical Problems in Medicine and Biomedical and Behavioral Research.
2. Pierre Detrain, The Aim and Structure of Physical Theory, (New York: Atheneum, 1974).
3. I would like to thank the President's Commission for the Study of Ethical Problems in Medicine and Biomedical and Behavioral Research for making the minutes of their June 5 hearing available to the Ethics Center at IIT.