Psychological, Historical, and Ethical Reflections on the Mendelian Paradox

Evidence that Mendel's reported data are too good to be true: By 1911, R. A. Fisher sensed some statistical irregularities [1] in Mendel's classical paper [2]. Twenty five years later, Fisher published an analysis of Mendel's experiments, concluding that "the data of most, if not all, of the experiments have been falsified so as to agree closely with Mendel's expectations." [3, p.164] In private, Fisher referred to his discovery that Mendel data had been "faked" as "abominable" and a "shocking experience" [4, pp. 296-7]. Fisher's dispassionate analysis created a storm [1] which, fifty-seven years after the event, shows no signs of subsiding. Fisher's indictment has received the closest possible attention from a great number of scholars, second only, perhaps, in the genetics literature, to Mendel's own paper. Despite this considerable attention, the subject remains every bit as controversial today as it had been in 1936.

By now, the charge that Mendel's paper does not faithfully report his data stems from four lines of evidence:

1. A cursory look at Mendel's various observations soon makes a statistically literate person notice that they come, over and over again, uncomfortably close to Mendel's expectations. As Edwards put it, "one can applaud the lucky gambler; but when he is lucky again tomorrow, and the next day, and the following day, one is entitled to become a little suspicious" [5]. The precise calculations are still under dispute, but the best current estimate suggests that results as close as or closer to expectations as the ones reported by Mendel would occur in only 1 out of 33,000 replications [6, p. 921]. In other words, it is virtually inconceivable that Mendel obtained his "good" results by pure chance.

2. In one subset of the experiments discussed above, Mendel tested the genetic make-up of F2 plants showing the dominant characteristic. His theory led him to the correct expectation that the actual ratio of heterozygotes (Aa) to homozygotes (AA) in such cases is 2:1. However, because he only tested 10 progeny per plant, a small fraction of the heterozygotes would have been missed, leading to incorrect misclassification of Aa plants as AA and to an observed ratio of 1.7 Aa to 1 AA. Mendel apparently overlooked this, wrongly expecting a 2:1 observed ratio. Amazingly, his reported results agree closely with the naive expectation of a 2:1 ratio. The overall discrepancy from the correct 1.7 to 1 ratio in this subset of the experiment "is strongly significant, and so low a value could scarcely occur by chance once in 2000 trials" [3, p. 162).

Fisher sums up the evidence here:

A serious and almost inexplicable discrepancy has, however, appeared, in that in one series of results the numbers observed agree excellently with the two to one ratio, which Mendel himself expected, but differ significantly from what should have been expected had his theory been corrected to allow for the small size of his test progenies [3, p. 164].

3. Mendel obtained all 128 (27) possible pair combinations of his seven pea characters and reported that each character segregated independently of all the others. This assertion presents two complications. First, it is possible that two of Mendel's seven characters were in fact linked [7, 8]. In that case, Mendel's claim/that all possible permutations "gave approximately equal results" [2, p. 22) as the ones he reported for independent assortment/is questionable.

Second, even if all his seven characters were unlinked, there is still the question of his failure to report linkage. It seems unlikely that by 1865 Mendel would not have encountered linkage in any of his extensive experiments on species other than peas (see below). It seems even less probable that Mendel would not have stumbled upon linkage in peas. Dunn estimates the a priori probability that Mendel would have not encountered linkage in peas as 1 out of 163 [9, ([9, p. 12). Even a lower estimate would still raise the possibility that Mendel encountered exceptions to his law of independent assortment, but that he chose not to report them in his classical paper [8]. Fisher perceived this difficulty. Mendel, he wrote, "may have known of other factors in peas in addition to those with which his experiments are concerned, which, however, could not have been introduced without bringing in an undesirable complication" [3, p. 165).

4. Mendel's biographer tells us that Mendel may have ordered the posthumous "destruction of his scientific notebooks. He had grown weary of the struggle, and did not wish to be exposed to misinterpretation after his death" [10, p. 281). Given Mendel's vast data, his personality, and his conviction about the importance of his work, a decision to condemn his records to the flames is not incompatible with the possibility that he was aware of some irregularities in the records. Evidence for Mendel's integrity and fastidiousness: Apart from the statistical and circumstantial evidence above, everything we know about Mendel suggests that he was unlikely to engage in either deliberate fraud or in large-scale, unconscious, adjustment of his observations.

To begin with, in his classical paper, Mendel reports some observations with beans which he was barely able to reconcile with his new theory. Later, Mendel published a paper on hawkweeds which seemed to disprove his theory of inheritance [11], for he reports there the "exactly opposite phenomenon" [12, p. 55). Needless to say, it is in precisely such cases that a person of questionable integrity would be tempted to falsify data or withhold information.

Iltis [10, p. 225] tells us that Mendel also kept records of sunspots and that, like all his other observations and records, "these are extremely neat and precise." Another Mendel biographer writes that:

Studying various original documents written by Mendel, especially such documents as a cash book, one is surprised what a pedant Mendel was in recording every numerical item. He was extremely careful of recording financial items in the cash book although he could have left that chore to the procurator of the convent. Mendel was also highly accurate in noting and summarizing his data from meteorological observations and from the measuring of the water level in the monastery well. He kept the data in this way himself until his death [11, p. 777]. Mendel unmistakably loved science. He would often refer to his plants as his wards and "children" [10, p. 108]. Shortly before his death, he reportedly told a colleague that "scientific work has brought me a great deal of satisfaction" ([13, p. 93). He had endured hunger, illnesses, and lifelong financial and spiritual debts in an effort to adequately prepare himself for a scientific career.

Proposed solutions to the Mendelian paradox:
Taken together, the situation seems paradoxical. On the one hand, we have evidence that "the data of most, if not all, of the experiments have been falsified so as to agree closely with Mendel's expectations" [3, p. 164). We also have good reasons to believe that Mendel encountered linkage but failed to report it and that he may have taken the somewhat unusual step of having his scientific records destroyed shortly after his death. On the other hand, everything else we know about him/in addition to his undisputed genius/suggests a man of unimpeachable integrity, fine observational powers, and a passion for science. In other words, Mendel was as unlikely a candidate for scientific misconduct as can be imagined.

This contradiction, the paucity of available records, and Mendel's key role in the history of genetics, prompted many attempts to resolve the Mendelian paradox:

1. The most inviting way of solving this paradox is to show that Mendel's reported data are statistically sound, and hence that no tampering or injudicious selection of data need to be invoked. As far as I am aware, such statistical refutations have never tried to address the totality of the situation, focusing instead on one or another statistical aspect of Fisher's paper. They make no effort, for example, to address the linkage issue. Even for those who believe that statistics can somehow resolve the glaring irregularities in Mendel's data, no fresh review of this subject is called for because it has received the attention of competent statisticians. In 1966, Sewall Wright came "out with substantially the same result as Fisher. There is no question that the data fit the ratios much more closely than can be expected from accidents of sampling" [14, p. 173). Twenty years later, another statistician had this to say about subsequent efforts to refute Fisher's analysis:

My overall impression from reading all the commentaries since Fisher . . . is that a good deal of special pleading, not to mention downright advocacy, has failed to make any substantial impact on Fisher's conclusion. . . . In spite of many attempts to find an explanation, Fisher's suggestion that the data have been subjected to some kind of adjustment must stand. A fresh analysis . . . confirms this conclusion in two separate ways. . . . Mendel's results really are too close ([15, pp. 302, 310].

Franz Weiling is noted for his quarter-century-long struggles to resolve the Mendelian paradox through statistical arguments. His most recent attempt led him to assert that Fisher's conclusion is inapplicable to Mendel's data, and hence, that Mendel faithfully reported his observations (reviewed in 16]. This is not the place to take up this argument, so let me just say that, in my view, this well-intentioned attempt utterly fails "to make any substantial impact on Fisher's conclusions" ([15].

Given the commonsense quality of Fisher's critique, and the failure over the past fifty-seven years to refute it, it seems highly improbable that the Mendelian paradox can be resolved through an appeal to statistics.

2. Fisher conjectured that "although no explanation can be expected to be satisfactory, it remains a possibility among others that Mendel was deceived by some assistant who knew too well what was expected" ([3, p. 164). But lack of viable candidates for the wily assistant puts this explanation in serious doubt [17, p. 254). It also appears entirely out of character for Mendel to trust a portion of each of his critical experiments to a junior assistant and, at the same time, to unwittingly, year in and year out, play the part of Clever Hans's trainer.

3. A more plausible explanation of the Mendelian paradox involves unconscious bias. One variation assumes that Mendel already had formed his expectations before counting the peas, and that every classification, e.g., tall vs. short plants, involves a subjective judgment. Mendel then, in perfect conscience, put questionable items aside during the routine counting process. Once he completed a particular experiment, he classified these items so as to make the data fit as closely as possible with his preconceived notions [18; 19, p. 102 ). Another variation argues that every experimenter must sometimes discard some observations for technical reasons, e.g., contamination. Mendel might have, unknowingly and unintentionally, discarded some perfectly good items to bring his observations closer to expectations ([20]. A similar explanation would have Mendel stop scoring sometime at the end of a particular experiment, just at the moment when the observed ratio came close to expectation [21; 11]. Another variation traces the problem to Mendel's university training/he was taught to reduce experimental error by repeating observations and choosing the one with the least error [22].

But all these explanations throw no light on the linkage problem and on the possibility of intentional destruction of records. They tend to cast doubts about Mendel's competence and integrity. Can we really believe that someone with Mendel's mind and scientific training would consistently and systematically, for instance, stop counting when his expectations had been met, even though he had more data in his hands which begged to be counted? Is it plausible to suppose he felt justified in systematically ignoring disconfirming observations? And, if classification is indeed so difficult, wouldn't it be more sensible and honest to classify first and only then count?

Another variant invokes experimenter effects [23]. But the available evidence suggests that Mendel's close fit can, at best, only be explained in part by the tendency of experienced scientists to see what they expect to see: "Observation is inferential, so that any given observation might be influenced by theory, but the inferential processes in observation are not so loose as to allow us to make any observation we want" [24, p. 151; see also ref. 25 for experimental evidence).

4. His paper, Mendel wrote, was a draft of a lecture, "thus the brevity of the exposition, as is essential for a public lecture" [26, p. 61). It seems reasonable to suppose that Mendel only published data that best illustrated the hypothesis he was proposing [27, p. 288; see also: ref. 28, p. 651; ref. 8, p. 514). Fisher examined this possibility and presented rather convincing arguments against it [3]. Mendel, Fisher concluded, meant his lecture to be taken literally, not as a didactic exposition. At any rate, the proper way of dealing with time and space limitations calls for reporting a representative sample of the data, not reporting data that happen to agree with one's theory. Hence, this alternative fails to remove the suspicion of impropriety.

5. A recent explanation argues that "the pejorative connotations of cooking and trimming may obscure the value of the judicious selection or rejection of data as was practiced by some giants of scientific discovery" [29]. There is ambiguity in discerning what should be labeled scientific impropriety. When data are falsified, an intellectual crime has been committed. But when particular observations are selected from an assemblage, without acknowledgment or unconsciously, we should not conclude that the action was improper. Judicious selection or rejection of information is not improper. "If in time the choices made reveal poor discrimination, one's reputation as a scientist suffers. On the other hand, if one's judgment ultimately proves . . . wise, then one's stature as a scientist blooms" [29].

But like the preceding explanation, this one fails to remove the shadow of impropriety from Mendel. When I read your paper, I trust you to tell me what you saw. I take your facts to be as value-free as possible. And, because we both know the same facts, I can evaluate your explanation. However, if you decide to omit counterexamples from your report, meaningful discourse ends. If widely practiced, "cooking" can bring the scientific enterprise to a halt. So, the suggestion that Mendel systematically eliminated data from his report, knowingly or unknowingly, does not convincingly remove the charge of impropriety.

This argument also seems to confuse the psychological act of discovery and the public act of reporting a discovery. In the former case, it is indeed often the mark of greatness to be captivated by a novel insight and to ignore incongruent details. Likewise, in reporting this insight, one cannot be accused of improper behavior for choosing to ignore the contradictory evidence discovered by others. But when the source of the novel insight is one's data, one is honor-bound to report what one saw.

In 1966, Sturtevant felt that none of the attempted solutions to the Mendelian paradox was "wholly satisfactory, since they seem out of character" [30, p. 16). Despite repeated efforts to unravel this paradox since then, I believe that Sturtevant's conclusion still stands. In fact, it is precisely because none of the available explanations is adequate that there are so many of them; in an unsettling situation, a flawed answer is better than none. This inadequacy probably explains, as well, why so many observers are inclined to adopt the far more economical assumption that Mendel is guilty of outright fraud [31; 32; 33, p. 55]. Here I would like to explore two related solutions to the Mendelian paradox. Put briefly, both proposals involve the contention that Mendel consciously presented biased data, but that in doing so he acted honorably and in the best interests of science. Before presenting these proposals, we shall need to venture farther afield than statistics, scientific methodology, and unconscious thought processes.

The Scientific ethos: Sociologists of science distilled the rules of conduct to which most individual scientists, and the scientific community, subscribe [34, pp. 267-278). I shall briefly present the relevant features of their analysis, modifying them occasionally in light of my own experiences as a geneticist. Among the imperatives comprising this ethos, four deserve special attention here. First, scientific claims ought to be evaluated regardless of the personal or social attributes of their protagonists. This imperative also finds expression in the demand that careers be open to talented individuals, for any other arrangement would harm the advancement of knowledge. Second, scientists ought to communicate their findings. Needless to say, the more important one's discovery is, the more binding the requirement to make it public. Third, scientists ought to have the advancement of scientific knowledge as their primary goal, subordinating all selfish objectives. Fourth, scientists ought to communicate their actual observations as accurately as possible. Any tampering with one's data, any intentional half-truth,any effort to falsify data in an effort to prop up one's theory, is deplorable.

In most cases, one's course of action is unambiguous, for all these strictures can be simultaneously followed. Problems arise in those rare instances where two or more of these strictures are in conflict. What, in particular, does one do when one's peers reject one's valid contribution in part owing to one's social attributes? What is the proper conduct when a conflict arises between the norm of communicating one's findings and the norm of communicating them as faithfully as possible? What is one to do when the only way to communicate a larger truth is to tamper with some inconsequential details?

What, in particular, is one to do when the advancement of scientific knowledge conflicts with presenting a scrupulous account of one's data? Every biologist knows about segregation, but none can cite offhand Mendel's numbers. Without a doubt it is segregation that contains the larger truth. If, by reporting everything you did accurately, this larger truth remains only known to you, would such an uncompromising attitude be considered moral? Or is it more important to compromise on the details so that the larger picture has a chance of reaching the international scientific community?

Such conflicts, if they existed, may shift the blame from Mendel to structural flaws in nineteenth-century science.

Did Mendel sense the significance of his discoveries?

Mendel was probably aware of the extraordinary character of his results. Unfortunately, most of the clues we have here are suggestive at best because they are based on the reminiscences of friends long after his death and the "rediscovery" of his work. In an often quoted statement, Mendel reportedly told a colleague "my time will come" ([10, p. 282]. Shortly before his death, Mendel had reportedly told a fellow monk that "the time will come when the validity of the laws discovered by me will be recognized" ([16, pp. 20-21].

We do have some evidence in Mendel's own writing that suggests that he might have recognized the revolutionary nature of his work: "I knew that the results I obtained were not easily compatible with our contemporary scientific knowledge, and that . . . publication . . . was doubly dangerous; dangerous for the experimenter and for the cause he represented" [26, p. 60].

Although Mendel had undoubtedly encountered exceptions to the regularities he reported for peas, he knew that these regularities applied to many other species as well; that they provided one key to understanding life, not merely the life cycle of peas. In his classical paper, he reports results with three bean characters, two of which behaved exactly like peas. In a subsequent letter to Nageli, Mendel also described confirming experiments with stock, maize, and four o'clock [26, p. 93]. It is also possible that Mendel bred mice but refrained from disclosing his results as animal experiments of this type were frowned upon by the Church ([10].

Mendel's goal in publishing his paper: Mendel naturally felt some doubts about his observations. He was, as we have seen, anxious to show that they had universal validity. "A number of hybridizations undertaken in 1863 and 1864," he writes to Nageli, "convinced me of the difficulty of finding plants suitable for an extended series of experiments, and that . . . years might elapse without my obtaining the desired information" [26, p. 60). He decided therefore to make his results public, in an effort to get others to replicate them and expand his research program. And, again, in the same letter he repeats the plea that his "experiments should be repeated and verified" [26, p. 63]. Mendel also sent Nageli over 140 seed packets along with detailed instructions, hoping to induce Nageli to test some of Mendel's predictions ([10, p. 195].

In his paper, Mendel says that the "validity of the laws proposed for Pisum needs confirmation," and that a replication seems desirable [2, p. 43). At the beginning of his paper he says that "it requires a good deal of courage indeed to undertake such a far-reaching task; however, this seems to be the one correct way of finally reaching the solution to a question whose significance . . . must not be underestimated" [2, p. 2].

Ethical considerations: Most ethicists would probably agree that, under certain circumstances, lying is a necessary evil. Indeed, sometimes any other action would be improper.

A few unrelated illustrations should make this point clear. Experimental psychologists routinely misinform their subjects about the goals and nature of their experiments. In medicine a similar lie has a well-known name: placebo. In such cases it is taken for granted that the advancement of knowledge and public health take precedence over truthfulness.

Ibsen's The Wild Duck describes the tragic consequences of one man's mistaken notion that the truth must always be told. As a result of this man's crusade for candor, a loving father is made to confront the truth that his daughter is not his. An estrangement follows, leading the child to commit suicide. Ibsen's sentiments, with which most viewers would probably agree, are plain enough: "Life would be quite tolerable, after all, if only we could be rid of the confounded duns that keep on pestering us, in our poverty, with the claim of the ideal" [35, p. 812).

Take the more dubious case of Christopher Columbus. He was convinced that India was just around the corner, that the Earth was round, with a circumference shorter than it actually has [36]. Columbus averted mutiny and a premature return to Spain by deliberately deceiving his crew about the actual distance they traveled. Was his behavior unethical, or did the end in this case justify the deception? Even if Columbus's ships were lost at sea as a result of his action, would we condemn his use of systematic fraud in an effort to overcome his sailors' fears and superstitions?

Johannes Kepler's background and circumstances are reminiscent of Mendel's. Kepler's three laws of planetary motions have been largely based on Tycho Brahe's data, which Kepler stole from Tycho's heirs [37, p. 161). Here the conflict involved, on the one hand, the moral and legal strictures prohibiting misrepresentation and the appropriation of someone else's property, and, on the other hand, the higher value of advancing humanity's conceptions of reality. In this case, Kepler unflinchingly subordinated conventional morality and the law of the land to the scientific imperative of advancing knowledge.

One might disagree about the propriety of conduct in examples such as these, but I believe the principle itself is widely accepted: The telling of lies or half-truths can sometimes be justified on moral grounds.

Cognitive psychology: Experimental psychology provides conclusive evidence that human beings find it hard to abandon strongly held beliefs, even when these beliefs suffer decisive refutations [38]. Of special interest here are recent experiments in which natural scientists served as the subjects and which bring this human failing into sharp relief (39; 25].

In these experiments, all subjects held a Ph.D. in a natural science. All were employed by two major research universities as postdoctoral fellows and professors. These subjects possessed, therefore, exceptional measurement skills and an above-average ability to treasure their exceptions. They were led to believe they were engaged in a professional evaluation of a self-discovery instructional manual. Before they could provide the needed evaluations, they were told, they needed to go through the manual in the same manner prospective students later would.

At a certain critical point in this manual, these scientists were given a plausible but false formula that led them to believe that spheres are 50 percent more voluminous than they really are.

Immediately after, they generated experimental evidence that dramatically discredited this formula. While the formula was leading them, for instance, to expect that a given sphere would contain three quarts of water, direct measurements yielded only two. They were then asked whether, in light of the experimental evidence they had just obtained, the formula they were given was valid. To the experimenters' astonishment, not one scientist flatly rejected the formula. They were also given a paper-and-pencil question about the volume of a sphere of the same dimensions as the sphere for which they had obtained the discrediting evidence. All subjected chose the discredited value.

In view of this unexpected results, an additional segment was added to the instructional manual. This time the goal was to make the discrepancy between the false formula and observations so absurd as to enable all scientists to break away from the formula. Even though this segment tried in every possible way (short of telling these scientists that they had been deceived) to help them break away from the spurious belief, over 90 per cent still failed.

Surveys suggest that these results are counterintuitive/neither natural scientists nor psychologists were able to predict these subjects' striking reluctance to let go of an established belief.

The history of science: The history of ideas can be viewed as the struggle of the originators of new ideas to overcome, first, their own resistance to conceptual shift and, second, the resistance of their colleagues. Papers by obscure authors, especially, run a great risk of either being refused publication or being overlooked. A great number of examples could be cited, but the present discussion is best confined to individuals whose work is closely connected to Mendel's.

At the start of his career, R. A. Fisher encountered great difficulties publishing papers that are now considered classic [4; 1]. Fisher's 1918 paper was rejected, allowed to languish for more than two years, and was eventually published only thanks to the intervention of Leonard Darwin, an amateur biologist and a nonmathematician with a very famous father and a strong believed in the genius of this "obscure schoolteacher" whose contributions were largely rejected by the professionals [4, p. 50). Later, and in dire financial circumstances, Fisher was offered a job by Pearson, but on the condition that he only publish what Pearson approved [4, p. 61). On a few other occasions in his early career, Fisher again experienced publishing difficulties [4, pp. 82-3, 87] which might have proven insurmountable without Darwin's help.

Among early hybridizers, Mendel singled out especially Gaertner and Koelreuter. Gaertner failed to achieve recognition in his lifetime, even though he had money and was the "son of a world-famous botanist. In 1849, despairing of getting a willing publisher for his great book, he paid for the printing himself" [21, p. 25]. Koelreuter's "book never achieved a wide circulation. . . . Sad to relate, the records of all these experiments were passed over by almost all his contemporaries and forgotten. . . . Koelreuter . . . was frustrated and bitter to the end of his days" ([21, p. 5].

It was no easy task to get your papers published in those days. According to one observer,

"to have a paper published in the Archiv fur Entwicklungsmechanik was a great distinction for any biologist" [33, p. 50). Pearson and Weldon attacked Bateson and other Mendelians, but did not allow them to reply in the columns of Biometrika." Bateson/the co-discoverer of linkage and inventor of the word "genetics"/was thus forced to resort to fraud: "He had his reply privately printed and bound in a cover which was an exact replica of the cover of Biometrika."

Pearson had also used his considerable influence with the editors of Nature to successfully prevent publication of Bateson's letters [33, p. 54). One could fill volumes with such anecdotes, but enough has been said to illustrate the empirical generalization that "the history of science abounds in instances of basic papers having been written by comparatively unknown scientists," only to be rejected or neglected for years [34, pp. 456-457; see also ref. 40].

We are now in a position to translate the various threads of this essay into two possible solutions to the Mendelian paradox.

An editorial roadblock? Mendel's biographer states that the data Mendel had accumulated by 1866 would have provided sufficient material "for a stately tome." "We may suppose," Iltis goes on to say, "that the editor of the 'Proceedings of the Brno Society for the Study of Natural Science' is likely to have warned Mendel not to let his pen run away with him.

Such a hint seems to have been common form, and was natural enough in view of the scantiness of the Society's funds" [10, pp. 193-4).

We know that Mendel's contemporaries failed to understand his paper. Most likely, his editor was no exception, especially since at the time Mendel was profoundly obscure, socially and economically. The editor might have insisted that Mendel report only results that, in the editor's ignorant but decisively important opinion, agreed well with Mendel's expectations. If the editor required the type of changes that would later cast a shadow on Mendel's integrity, his demand would have presented Mendel with a conflict. The Proceedings could very well provide Mendel with his only outlet for communicating his findings to the world. He was convinced, as we have seen, that his paper might, if published, make a significant contribution to the advancement of science. The Proceedings permitted him to publish his real important insights, and even some seemingly contradictory cases, such as his results with flower and seed color in beans. His editor might have made publication contingent upon brevity and on selectively underscoring the case for Mendel's theory, not against it. In such circumstances, a scientist, and especially a man who dedicated his life to the pursuit of fundamental natural laws, may feel justified in acceding to such editorial requests.

I have only come across one claim that seems to contradict this reconstruction. One historian mentions in passing that "Mendel had no difficulty in publishing his major paper. He had read it before the Brno Natural Science Society, and the proceedings were ordinarily published" [41, p. 10]. This may indeed be true, but the evidence given earlier suggests that publication in this case could have been problematic.

A conscious adjustment of reported results? As we have seen, Mendel may have sensed the revolutionary and controversial nature of his new theory. By 1865, he probably realized that it was beyond the comprehension of most of his contemporaries. He came to see that his theory required an experimental program which was far beyond the capacity of a single person (the type of program that would indeed be launched in 1900 and that would place the new science of heredity on solid ground within twenty years or so). He was most anxious to have his results replicated and expanded, for even self-possessed people (and he wasn't) entertain occasional misgivings about the accuracy, originality, and significance of their work.

To achieve these goals, his work had to be understood. In comparison to his theories, of whose validity he was sure, the data were of no significance whatsoever. His task was not the one faced by the normal scientist [42] addressing a sympathetic and competent audience, but that of a revolutionary who must break through the cognitive paradigms and social prejudices of his audience [19]. If this larger goal could be best achieved by simplification/deliberately omitting some observations from his report and adjusting others to make them more palatable to his audience/could not such a step be justified on moral grounds?

One historian tells us: good PR work may not be able to sell a bad theory, but a potentially good one may find its acceptance blocked if its proponents cannot play the game of scientific politics. They must adopt a workable strategy for converting others, undermining the influence of opponents, gaining access to journals and research grants, and all the other activities required to ensure an expanding role within the scientific community. The emergence of genetics was a particularly complex process, because it required not a revolution within an existing science, but the creation of an entirely new discipline [19, p. 8].

The obscure monk from Brno may have sensed these realities by 1865 and was perhaps disinclined or unable to play the game of scientific politics. He may have fully understood what twentieth century critics of his integrity so often forget/that data taken by themselves are comparatively trivial. What really mattered was the triumph of his ideas. In this less-than-perfect world, he may have sorrowfully realized, a genuine leap forward can sometime only be purchased with half-truths. Thankfully, innovators such as Columbus, Kepler, and Mendel may have been willing to create gold from base metals, hoping perhaps that a richer posterity would be wise enough to cherish their discoveries and forgive their methods.

Conclusion: Broad and Wade argue that "some who commit fraud do so to persuade their refractory colleagues of a theory they know is right. . . . If history has been kind to scientists such as these, it is because the theories turned out to be correct. But for the moralist, no distinction can be made between an Isaac Newton who lied for truth and was right, and a Cyril Burt who lied for truth and was wrong" [32, pp. 212-213).

This harsh accusation ignores the cognitive and political realities of doing science. In most cases, adjustment of data is rightly frowned upon, for it betrays an important rule of scientific conduct and, at the same time, it retards the growth of knowledge. Fraud undertaken for selfish, ideological, and other extra-scientific reasons, is indeed reprehensible. Sometimes, however, the demand to faithfully report one's data must be sacrificed for the higher value of advancing knowledge. It is, of course, impossible to know whether Mendel (and perhaps also others) faced such a procrustean dilemma. But the information presented in this paper raises the possibility that he may have. In that case, Mendel's choice merits our compassion and thanks, not our disapprobation.


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