DECEIT IN HISTORY

"Through experimental science we have been able to learn all these facts about the natural world, triumphing over darkness and ignorance to classify the stars and to estimate their masses, composition, distances, and velocities; to classify living species and to unravel their genetic relations. . . . These great accomplishments of experimental science were achieved by men .. . [who] had in common only a few things: they were honest and actually made the observations they recorded, and they published the results of their work in a form permitting others to duplicate the experiment or observation."

So says The Berkeley Physics Course, an influential text that has been used across the United States to impress college students with both the substance and the tradition of modern physics.¹ As with nonscientific systems of belief, however, the elements insisted on most strongly are often those with the least factual reliability. The great scientists of the past were not all so honest and they did not always obtain the experimental results they reported.

・Claudius Ptolemy, known as "the greatest astronomer of antiquity," did most of his observing not at night on the coast of Egypt but during the day, in the great library at Alexandria, where he appropriated the work of a Greek astronomer and proceeded to call it his own.

・Galileo Galilei is often hailed as the founder of modern scientific method because of his insistence that experiment, not the works of Aristotle, should be the arbiter of truth. But colleagues of the seventeenth-century Italian physicist had difficulty reproducing his results and doubted he did certain experiments.

・Isaac Newton, the boy genius who formulated the laws of gravitation, relied in his magnum opus on an unseemly fudge factor in order to make the predictive power of his work seem much greater than it was.

・John Dalton, the great nineteenth-century chemist who discovered the laws of chemical combination and proved the existence of different types of atoms, published elegant results that no present-day chemist has been able to repeat.

・Gregor Mendel, the Austrian monk who founded the science of genetics, published papers on his work with peas in which the statistics are too good to be true.

・The American physicist Robert Millikan won the Nobel prize for being the first to measure the electric charge of an electron. But Millikan extensively misrepresented his work in order to make his experimental results seem more convincing than was in fact the case.

Experimental science is founded on a paradox. It purports to make objectively ascertainable fact the criterion of truth. But what gives science its intellectual delight is not dull facts but the ideas and theories that make sense of the facts. When textbooks appeal to the primacy of fact, there is an element of rhetoric in the argument. Finding facts in actuality is less rewarded than developing a theory or law that explains the facts, and herein lies an enticement. In making sense out of the unruly substance of nature, and in trying to get there first, a scientist is sometimes tempted to play fast and loose with the facts in order to make a theory look more compelling than it really is.

It is difficult for a nonscientist to appreciate the overriding importance to the researcher of priority of discovery. Credit in science goes only for originality, for being the first to discover something. With rare exceptions, there are no rewards for being second. Discovery without priority is a bitter fruit. In the clash of rival claims and competing theories, a scientist often takes active measures to ensure that his ideas are noticed, and that it is under his name that a new finding is recognized.

The desire to win credit, to gain the respect of one's peers, is a powerful motive for almost all scientists. From the earliest days of science, the thirst for recognition has brought with it the temptation to "improve" a little on the truth, or even to invent data out of whole cloth, in order to make a theory prevail.

Claudius Ptolemy, who lived during the second century A.D. in Alexandria, Egypt, was one of the most influential scientists in history. His synthesis of early astronomical ideas resulted in a system for predicting the positions of the planets. The central assumption of the Ptolemaic system was that the earth was at rest and that the sun and other planets revolved around it in essentially circular orbits.

For nearly 1,500 years, far longer than Newton or Einstein have held sway, Ptolemy's ideas shaped man's view of the structure of the universe. The Ptolemaic system prevailed without challenge throughout the Dark Ages, from the early years of the Roman empire until the late Renaissance. Arab philosophers, the guardians of Greek science during the Middle Ages, dubbed Ptolemy's writing the Almagest, from the Greek word for "greatest." He came to be regarded as the preeminent astronomer of the ancient world. It was not until Copernicus in 1543 put the sun instead of the earth at the center of the planetary system that Ptolemy's 1,500-year reign as the king of astronomers began to come to an end. Yet this titan of the heavens had feet of clay.

In the nineteenth century, astronomers re-examining Ptolemy's original data began to notice some curious features. Back calculations from the present-day position of the planets showed that many of Ptolemy's observations were wrong. The errors were gross even by the standards of ancient astronomy. Dennis Rawlins, an astronomer at the University of California, San Diego, believes from internal evidence that Ptolemy did not make the observations himself, as he claims to have done, but lifted them wholesale from the work of an earlier astronomer, Hipparchus of Rhodes, who compiled one of the best star catalogs of ancient times.

The island of Rhodes, where Hipparchus made his observations, is five degrees of latitude north of Alexandria. Naturally there is a five-degree band of southern stars that can be seen from Alexandria but not from Rhodes. Not one of the 1,025 stars listed in Ptolemy's catalog comes from this five-degree band. Also, every example given in the Almagest of how to work out spherical astronomy problems is given for a latitude the same as that of Rhodes. "If one didn't know better," says Rawlins in an ironic comment, "one might suspect (as did even Theon of Alexandria, Ptolemy's most placid, tireless admirer in the 4th century) that Ptolemy took the examples from Hipparchus."²

Not only questions of theft hang over the head of antiquity's great astronomer. Ptolemy is also accused of a more modern scientific crime―that of having derived the data that he cites to support his theory from the theory itself instead of from nature. His chief accuser is Robert Newton, a member of the applied physics laboratory at Johns Hopkins University. In his book, The Crime of Claudius Ptolemy, Newton has assiduously collected scores, of instances in which Ptolemy's reported result is almost identical with what the Alexandrian sage wanted to prove and greatly different from what he should have observed.³ A striking example is that Ptolemy claimed he had observed an autumnal equinox at 2 P.M. on September 25, A.D. 132. He stressed that he had measured the phenomenon "with the greatest care." But, says Newton, back calculation from modern tables shows that an observer in Alexandria should have seen the equinox at 9:54 A.M. on September 24, more than a day earlier.

In giving his date for the equinox, Ptolemy was trying to show the accuracy of the length of the year as determined by Hipparchus. Hipparchus too had measured an autumnal equinox, 278 years earlier, on September 27, 146 BC.. Newton shows that if 278 times Hipparchus' estimate of a year (which is excellent but not quite right) is added to the Hipparchus equinox, then the time arrived at is within minutes of the time reported by Ptolemy. In other words, Ptolemy must have worked backward from the result he was trying to prove instead of making an independent observation.

Defenders of Ptolemy, such as historian Owen Gingerich, claim that modern scholars are being unfair in applying contemporary standards of scientific procedure to Ptolemy. Yet even Gingerich, who calls Ptolemy "the greatest astronomer of antiquity," concedes that the Almagest contains "some remarkably fishy numbers."⁴ But he insists that Ptolemy chose merely to publish the data that best supported his theories and was innocent of any intent to deceive. Whatever Ptolemy's intent, his borrowing of Hipparchus' work won him nearly two millennia of glory before being detected.

The feature that supposedly distinguishes science from other kinds of knowledge is its reliance on empirical evidence, on testing ideas against the facts in nature. But Ptolemy was not the only scientist to neglect an observer's duties; even Galileo, a founding father of modern empiricism, is suspected of reporting experiments that could not have been performed with the results he claims.

Galileo Galilei is perhaps best remembered as the patient investigator who dropped stones from the Leaning Tower of Pisa. The story is probably apocryphal but it captures the quality that allegedly set Galileo apart from his medieval contemporaries―his inclination to search for answers in nature, not in the works of Aristotle. Galileo was persecuted by the Church for his defense of the Copernican theory and his trial is held up by today's scientific textbooks as a heroic object lesson in the battle of reason against superstition. Such textbooks naturally tend to stress Galileo's empiricism, in contrast to his opponents' dogmatism. "After Galileo," says one, "the ultimate proof of a theory would be the evidence of the real world."⁵ The textbook approvingly cites how Galileo painstakingly tested his theory of falling bodies by measuring the time it took for a brass ball to roll down a groove in a long board: in "experiments near a hundred times repeated," Galileo found that the times agreed with his law, with no differences "worth mentioning."

According to historian I. Bernard Cohen, however, Galileo's conclusion "only shows how firmly he had made up his mind beforehand, for the rough conditions of the experiment would never have yielded an exact law. Actually the discrepancies were so great that a contemporary worker, Pre Mersenne, could not reproduce the results described by Galileo, and even doubted that he had ever made the experiment."⁶ In all likelihood, Galileo was relying not merely on his experimental skill but on his exquisite talents as a propagandist.⁷

Galileo liked to perform "thought experiments," imagining an outcome rather than observing it. In his Dialogue on the Two Great Systems of the World, in which Galileo describes the motion of a ball dropped from the mast of a moving ship, the Aristotelian, Simplicio, asks whether Galileo made the experiment himself. "No," Galileo replied, "and I do not need it, as without any experience I can affirm that it is so, because it cannot be otherwise."

The textbooks' portrayal of Galileo as a meticulous experimentalist has been reinforced by scholars. According to one translation of his works, Galileo reportedly said: "There is in nature perhaps nothing older than motion, concerning which the books written by philosophers are neither few nor small. Nevertheless, I have discovered by experiment some properties of it which are worth knowing and which have not hitherto been observed or demonstrated."⁸ The words "by experiment" do not appear in the original Italian; they have been added by the translator, who evidently had strong feelings on how Galileo should have proceeded.

Unlike the textbook writers, some historians, such as Alexandre Koyre, have seen Galileo as an idealist rather than an experimental physicist; as a man who used argument and rhetoric to persuade others of the truth of his theories.⁹ With Galileo, the desire to make his ideas prevail apparently led him to report experiments that could not have been performed exactly as described. Thus an ambiguous attitude toward data was present from the very beginning of Western experimental science. On the one hand, experimental data was upheld as the ultimate arbiter of truth; on the other hand, fact was subordinated to theory when necessary and even, if it didn't fit, distorted. The Renaissance saw the flowering of Western experimental science, but in Galileo, the propensity to manipulate fact was the worm in the bud.

Both sides of this ambiguous attitude to data reached full expression in the work of Isaac Newton. The founder of physics and perhaps the greatest scientist in history, Newton in his Principia of 1687 established the goals, methods, and boundaries of modern science. Yet this exemplar of the scientific method was not above bolstering his case with false data when the real results failed to win acceptance for his theories. The Principia met with a certain resistance on the Continent, especially in Germany where opposition was fomented by Newton's rival Leibniz, whose system of philosophy was at odds with Newton's theory of universal gravitation. To make the Principia more persuasive, Newton in later editions of his work improved the accuracy of certain supporting measurements. According to historian Richard S. Westfall, Newton "adjusted" his calculations on the velocity of sound and on the precession of the equinoxes, and altered the correlation of a variable in his theory of gravitation so that it would agree precisely with theory. In the final edition of his opus, Newton pointed to a precision of better than 1 part in 1,000, boldly claiming accuracies that previously had been observed only in the field of astronomy. The fudge factor, says Westfall, was "manipulated with unparalleled skill by the unsmiling Newton."

The hiatus between lofty principle and low practice could not be more striking. As amazing as it is that a figure of Newton's stature should stoop to falsification, even more surprising is that none of his contemporaries realized the full extent of his fraud. Using his contrived data as a spectacular rhetorical weapon, Newton overwhelmed even the skeptics with the rightness of his ideas. More than 250 years passed before the manipulation was completely revealed. As Westfall comments, "Having proposed exact correlation as the criterion of truth, [Newton] took care to see that exact correlation was presented, whether or not it was properly achieved. Not the least part of the Principia's persuasiveness was its deliberate pretense to a degree of precision quite beyond its legitimate claim. If the Principia established the quantitative pattern of modern science, it equally suggested a less sublime truth―that no one can manipulate the fudge factor so effectively as the master mathematician himself."¹⁰

Newton's willingness to resort to sleight of hand is evident in more than just falsification of data. He used his position as president of the Royal Society, England's premier scientific club, to wage his battle with Leibniz over who first invented calculus. What was shameful about Newton's behavior was the hypocrisy with which he paid lip service to fair procedure but followed the very opposite course." It would be an iniquitous judge "who would admit anyone as a witness in his own cause," announced the preface of a Royal Society report of 1712 which examined the question of priority in calculus. Ostensibly the work of a committee of impartial scientists, the report was a complete vindication of Newton's claims and even accused Leibniz of plagiary. In fact the whole report, sanctimonious preface included, had been written by Newton himself. Historians now believe that Leibniz' invention of calculus was made independently of Newton.

Newton having set the standards, it is perhaps not so surprising to find other scientists using the truth to support their own theories in ways that make a mockery of the scientific method. Historians have raised substantial questions about the experiments of John Dalton, a towering figure in early nineteenth-century chemistry and a founder of the atomic theory of matter. From his belief that each element is composed of its own kind of atoms, Dalton developed his law of simple multiple proportions. The law holds that when two elements form a chemical. compound they do so in fixed proportions because the atoms of one element combine with a precise whole number-one, two, or more-of the atoms of the other element. Dalton supplied major evidence for this law from his study of the oxides of nitrogen, stating that oxygen would combine with a given amount of nitrogen only in certain fixed ratios.

Modern inquiry raises considerable doubts about Dalton's data. For one thing, historians are now sure that Dalton first speculated on the law and then made experiments in order to prove it.¹² For another, he seems to have selected his data, publishing only the "best" results, in other words those that supported his theory. His best results are distinctly hard to duplicate. "From my own experiments I am convinced that it is almost impossible to get these simple ratios in mixing nitric oxide and air over water," says historian J. R. Partington.¹³

Scientists' cavalier attitude toward data in the nineteenth century was sufficiently widespread that in 1830 the phenomenon was described in a treatise by Charles Babbage, inventor of a calculating machine that was the forerunner of the computer. In his book Reflections on the Decline o f Science in England, Babbage even categorized the different types of fraud that were prevalent.,, "Trimming," he wrote, "consists of clipping off little bits and there from those observations which differ most in excess from the mean, and in sticking them on to those which are too small." Though not approving of the practice, Babbage found that at times it might be less reprehensible than other types of fraud. "The reason of this is, that the average given by the observations of the trimmer is the same, whether they are trimmed or untrimmed. His object is to gain a reputation for extreme accuracy in making observations; but from respect for truth, or from prudent foresight, he does not distort the position of the fact he gets from nature."

Worse than trimming, in Babbage's view, was what he described as "cooking," a practice known today as selective reporting. "Cooking is an art of various forms," wrote Babbage, "the object of which is to give ordinary observations the appearance and character of those of the highest degree of accuracy. One of its numerous processes is to make multitudes of observations, and out of these to select those only which agree, or very nearly agree. If a hundred observations are made, the cook must be very unlucky if he cannot pick out fifteen or twenty which will do for serving up."

Most pernicious of all, wrote Babbage, is the scientist who pulls numbers out of thin air. "The forger is one who, wishing to acquire a reputation for science, records observations which he has never made. . . . Fortunately instances of the occurrence of forging are rare."

As the number of scientists increased throughout the nineteenth century, new varieties of deception came into being. Out of competitive zeal and the battle for scientific glory grew an altogether novel scientific sin, that of omitting to mention similar work that had preceded the unveiling of a new theory. Because of the importance of originality in science, tradition requires that a scientist acknowledge in his publications those whose work in the field preceded his. The mere absence of such acknowledgment constitutes a claim for originality. But even Charles Darwin, author of the theory of evolution, was accused of failing to give adequate acknowledgment to previous researchers.

According to anthropologist Loren Eiseley, Darwin appropriated the work of Edward Blyth, a little-known British zoologist who wrote on natural selection and evolution in two papers published in 1835 and 1837. Eiseley points to similarities in phrasing, the use of rare words, and the choice of examples. While Darwin in his opus quotes Blyth on a few points, notes Eiseley, he does not cite the papers that deal directly with natural selection, even though it is clear he read them.¹⁵ The thesis has been disputed by paleontologist Stephen J. Gould.¹⁶ But Eiseley is not the only critic of Darwin's acknowledgment practices. He was accused by a contemporary, the acerbic man of letters Samuel Butler, of passing over in silence those who had developed similar ideas. Indeed, when Darwin's On the Origin of Species first appeared in 1859, he made little mention of predecessors. Later, in an 1861 “historical sketch" added to the third edition of the Origin, he declineated some of the previous work, but still gave few details.Under continued attack, he added to the historical sketch in three subsequent editions. It was still not enough to satisfy all his critics. In 1879, Butler published a book entitled Evolution Old and New in which he accused Darwin of slighting the evolutionary speculations of Buffon, Lamarck, and Darwin's own grandfather Erasmus. Remarked Darwin's son Francis: "The affair gave my father much pain, but the warm sympathy of those whose opinions he respected soon helped him to let it pass into well-merited oblivion."¹⁷

A champion of Darwin's evolutionary cause during the late nineteenth century, Thomas Henry Huxley, made a remark in a letter to a friend that well sums up the complexities in the struggle for recognition.¹⁸ "You have no idea of the intrigues that go on in this blessed world of science. Science is, I fear, no purer than any other region of human activity, though it should be. Merit alone is very little good; it must be backed by tact and knowledge of the world to do very much." Moreover, as Darwin himself admitted, the sheer approbation of his peers was not an irrelevant factor.¹⁹ "I wish I could set less value on the bauble fame, either present or posthumous, than I do, but not, I think, to any extreme degree." Though Eiseley's charges of theft are undoubtedly overstated, it is clear that Darwin was laggard in giving credit to earlier authors of theories of evolution.

More serious than a mere breach of scientific etiquette is the charge raised against that other pillar of modern biology, the Abbé Gregor Mendel. By breeding plants and noting that certain traits were inherited in a discrete fashion, Mendel discovered the existence of what are now called genes. His analysis of inheritance in peas allowed him to identify what he called dominant and recessive characters, and the proportions in which these would be expected to appear in the offspring. The elegance of his insights, culled after many years of tedious experiment, earned Mendel a reputation in the twentieth century as the founder of the science of genetics.

The extreme precision of his data, however, led the eminent statistician Ronald A. Fisher in 1936 to closely examine Mendel's methods.²⁰ The results were too good. Fisher concluded that something other than hard work must have been involved. "The data of most, if not all, of the experiments have been falsified so as to agree closely with Mendel's expectations," wrote Fisher. He politely concluded that Mendel could not have "adjusted" the outcome himself but must have been "deceived by some assistant who knew too well what was expected." Geneticists who later looked at the problem were not so kind, deciding that Mendel must have selected data in order to make the best case. "The impression that one gets from Mendel's paper itself and from Fisher's study of it," wrote one historian of genetics, "is that Mendel had the theory in mind when he made the experiments. He may even have deduced the rules from a particulate view of heredity which he had reached before beginning work with peas."²¹ In 1966 geneticist Sewall Wright, in a brief but often quoted analysis, suggested that Mendel's only fault was an innocent tendency to err in favor of the expected results when making his tallies of peas with different traits: "I am afraid that it must be concluded that he made occasional subconscious errors in favor of expectation," concludes Wright.²²

Wright's exculpation of the father of modern genetics did not win universal conviction. "Another explanation would be that Mendel performed one or two more experiments and reported only those results that agreed with his expectation," wrote B. L. van der Waerden in 1968. "Such a selection would, of course, produce a bias toward the expected values." But van der Waerden apparently saw nothing wrong with such methods: "I feel many perfectly honest scientists would tend to follow such a procedure. As soon as one has a number of results clearly confirming a new theory, one would publish these results, leaving aside doubtful cases."²³

Academics may debate the precise nature of Mendel's misdeeds, but horticulturists have long since arrived at a verdict, if the following anonymous comment is anything to go by.²⁴ Entitled "Peas on Earth," it appeared in a professional journal: "In the beginning there was Mendel, thinking his lonely thoughts alone. And he said: `Let there be peas,' and there were peas and it was good. And he put the peas in the garden saying unto them `Increase and multiply, segregate and assort yourselves independently,' and they did and it was good. And now it came to pass that when Mendel gathered up his peas, he divided them into round and wrinkled, and called the round dominant and the wrinkled recessive, and it was good. But now Mendel saw that there were 450 round peas and 102 wrinkled ones; this was not good. For the law stateth that there should be only 3 round for every wrinkled. And Mendel said unto himself 'Gott in Himmel, an enemy has done this, he has sown bad peas in my garden under the cover of night.' And Mendel smote the table in righteous wrath, saying `Depart from me, you cursed and evil peas, into the outer darkness where thou shalt be devoured by the rats and mice,' and lo it was done and there remained 300 round peas and 100 wrinkled peas, and it was good. It was very, very good. And Mendel published."

The debate over whether Mendel consciously or unwittingly improved upon his results cannot be resolved with certainty because many of his raw data do not exist. With twentieth-century scientists, it is more often possible to compare their published work with the raw material on which it was based. The comparison is necessary because it often reveals serious discrepancies between appearance and reality in the laboratory. As biologist Peter Medawar observes: "It is no use looking to scientific `papers,' for they not merely conceal but actively misrepresent the reasoning that goes into the work they describe. . . . Only unstudied evidence will do―and that means listening at a keyhole."²⁵

Consider the case of Robert A. Millikan, a U.S. physicist who won the Nobel prize in 1923 for determining the electric charge on the electron. He became the most famous American scientist of his day, winning sixteen prizes and twenty honorary degrees before his death in 1953. In addition he was an adviser to Presidents Hoover and Franklin D. Roosevelt, and president of the American Association for the Advancement of Science. A careful study of Millikan's notebooks has brought to light some bizarre procedures in the methods by which Millikan climbed to scientific fame and glory.

As an unknown professor at the University of Chicago, Millikan published his first measurements of e, the electronic charge, in 1910. The measurements, which depended on introducing droplets of liquid into an electric field and noting the strength of field necessary to keep them suspended, were difficult to make and subject to considerable variation. In strict accordance with the ethos that demands full disclosure of data, Millikan used stars to grade the quality of his thirty-eight measurements from "best" to "fair," and noted that he had discarded seven entirely.

The candor did not continue for long. Millikan's rival in measuring electric charge, Felix Ehrenhaft of the University of Vienna, Austria, immediately showed how the variability in Millikan's published measurements in fact supported Ehrenhaft's belief in the existence of subelectrons carrying fractional electronic charges. Battle was joined between Millikan and Ehrenhaft, and the question of subelectrons was discussed around the scientific world by leading physicists such as Max Planck, Albert Einstein, Max Born, and Erwin Schrodinger.

To rebut Ehrenhaft, Millikan published an article in 1913 full of new and more accurate results favoring a single charge for the electron. He emphasized, in italics, that "this is not a selected group of drops but represents all of the drops experimented upon during 60 consecutive days."

On the face of it, Millikan had achieved a brilliant rejoinder to Ehrenhaft and had proved beyond a doubt the correctness of his measure of the electron charge―all through the sheer power of scientific precision. However, a look through Medawar's keyhole shows a quite different situation. Harvard historian Gerald Holton went back to the original notebooks on which Millikan based his 1913 paper and found major gaps in the reporting of data.²⁶ Despite his specific assurance to the contrary, Millikan had selected only his best data for publication. The raw observations in his notebooks are individually annotated with private comments such as "beauty. publish this surely, beautiful!" and "very low, something wrong." The 58 observations presented in his 1913 article were in fact selected from a total of 140. Even if observations are counted only after February 13, 1912, the date that the first published observation was taken, there are still 49 drops that have been excluded. ²⁷

Millikan had no need to worry that his deceit would be exposed, for, as Holton notes, the "notebooks belonged to the realm of private science. . . . Therefore he evaluated his data .. . guided both by a theory about the nature of electric charge and by a sense of the quality or weight of the particular run. It is exactly what he had done in his first major paper, before he had learned not to assign stars to data in public."

Across the Atlantic, meanwhile, Ehrenhaft and his colleagues assiduously published readings, good, bad, and indifferent. The picture that emerged from their work did not support the notion of a single, indivisible electronic charge. This view was contrary to prevailing theory at the time and, as Holton notes, "from Ehrenhaft's point of view it was, for just this reason, to be regarded as an exciting opportunity and challenge. In Millikan's terms, on the contrary, such an interpretation of the raw readings would force one to turn one's back on a basic fact of nature―the integral character of e―which clearly beckoned."

For Millikan, the battle ended in a Nobel prize (which also cited his work on the photoelectric effect); for Ehrenhaft, in disillusionment and eventually a broken spirit. But Ehrenhaft, who had the more accurate equipment and made better measurements than Millikan, may yet be vindicated. Physicists at Stanford University using a similar methodology have recently found evidence of a kind of subelectronic charge.²⁸

The example of Millikan and the other adepts of science who cut corners in order to make their theories prevail contains some alarming implications. Scientific history by its nature tends to record only the deeds of those few who have successfully contributed to knowledge and to ignore the many failures. If even history's most successful scientists resort to misrepresenting their findings in various ways, how extensive may have been the deceits of those whose work is now rightly forgotten?

History shows that deceit in the annals of science is more common than is often assumed. Those who improved upon their data to make them more persuasive to others doubtless persuaded themselves that they were lying only in order to make the truth prevail. But almost invariably the real motive for the various misrepresentations in the history of research seems to arise less from a concern for truth than from personal ambition and the pursuit, as Darwin put it, of "the bauble fame." Newton wanted to persuade the skeptics of his ideas in France and Germany. Millikan misreported data in order to defeat a rival, not to make his work mirror more perfectly an ideal of scientific precision.

The twentieth century has seen the development of science from a hobby to a career become almost complete. Galileo was supported in grand style by the Duke of Tuscany. Charles Darwin, born into the well-to-do Darwin and Wedgwood clans, never had to worry about making money from his scientific speculations. Gregor Mendel entered the Augustinian monastery in Brno where he was able to pursue his studies in complete freedom from financial worries. In the twentieth century, the cost of buying instruments and hiring technicians has put science almost entirely out of the amateur's reach. The tradition that kept curiosity about nature divorced from the generation of personal income has been left far behind. Almost all scientists nowadays pursue science as a career. Their vocation is also the source of their salary. Whether supported by government or industry, they work within a career structure that offers rewards for tangible, often short-term, success. Few scientists today can leave it to posterity to judge their work; their universities may deny them tenure, and the flow of grants and contracts from the federal government is likely to dry up quite quickly, unless evidence of immediate and continuing success is forthcoming.

If the luminaries of scientific history would on occasion misrepresent their data for the personal vindication of seeing their ideas prevail, the temptations must be all the greater for contemporary scientists. Not only personal justification but also professional rewards depend on winning acceptance for an idea or theory or technique. Often an extra measure of acceptance can be won by minor misrepresentations. "Tidying up" data, making results seem just a little more clear-cut, selecting only the "best" data for publication-all these seemingly excusable adjustments may help toward getting an article published, making a name for oneself, being asked to join a journal's editorial board, securing the next government grant, or winning a prestigious prize.

In short, careerist pressures are intense and unremitting. Many scientists, no doubt, refuse to let their work be distorted by them. Yet for those who do, the rewards for even deceitfully gained success are considerable and the chances of apprehension negligible. The temptations of careerism, and the almost total absence of credible deterrents to those who would cheat the system, are graphically demonstrated in the meteoric career of that uniquely twentieth-century scientist Elias Alsabti.

Notes

CHAPTER 2

DECEIT IN HISTORY

1. C. Kittel, W. D. Knight, M. A. Ruderman, The Berkeley Physics Course, Vol. 1, Mechanics (McGraw-Hill, New York, 1965).

This passage, together with an interesting analysis of the scientific textbook writers' use of history, is quoted in an article by Stephen G. Brush, "Should the History of Science Be Rated X?" Science, 183, 1164-1172, 1974.

2. Dennis Rawlins, "The Unexpurgated Almajest: The Secret Life of the Greatest Astronomer of Antiquity," Journal for the History of Astronomy, in press.

3. Robert R. Newton, The Crime of Claudius Ptolemy (Johns Hopkins University Press, Baltimore, 1977). For a summary of the argument see Nicholas Wade, "Scandal in the Heavens: Renowned Astronomer Accused of Fraud," Science, 198, 707-709, 1977.

4. Owen Gingerich, "On Ptolemy As the Greatest Astronomer of Antiquity," Science, 193, 476-477, 1976, and "Was Ptolemy a Fraud?" preprint No. 751, Center for Astrophysics, Harvard College Observatory, Cambridge, 1977. See also a news article summarizing an attempt to absolve Ptolemy, Scientific American, 3,90-93,1979.

5. Cecil J. Schneer, The Evolution of Physical Science (Grove Press, New York, 1960), p. 65.

6. I. Bernard Cohen, Lives in Science (Simon & Schuster, New York, 1957), p.14.

7. Some research has suggested that Galileo could have easily carried out certain experiments, and that historians who claim they were all imaginary are overstating the case. See Thomas B. Settle, "An Experiment in the History of Science," Science, 133, 19-23, 1961. See also Stillman Drake, "Galileo's Experimental Confirmation of Horizontal Inertia: Unpublished Manuscripts," Isis, 64, 291-305, 1973. See also James MacLachlan, "A Test of an Imaginary Experiment of Galileo's," Isis, 64, 374-379, 1973.

8. Alexandre Koyre, "Traduttore-Traditore. A Propos de Copernic et de Galilee," Isis, 34, 209-210, 1943.

9. Alexandre Koyre, Etudes Galileennes (Hermann, Paris, 1966). This is a reprint of three articles published between 1935 and 1939.

10. Richard S. Westfall, "Newton and the Fudge Factor," Science, 179, 751-758, 1973. See also various letters in response in Science, 180, 1118, 1973.

11. William J. Broad, "Priority War: Discord in Pursuit of Glory," Science, 211, 465-467, 1981.

12. J. R. Partington, A Short History of Chemistry (Harper & Brothers, New York, 1960), p. 170. Also see Leonard K. Nash, "The Origin of Dalton's Chemical Atomic Theory," Isis, 47, 101-116, 1956.

13. J. R. Partington, "The Origins of the Atomic Theory," Annals of Science, 4, 278, 1939.

14. Charles Babbage, Reflections on the Decline of Science in England (Augustus M. Kelley, New York, 1970), pp. 174-183.

15. Loren Eiseley, Darwin and the Mysterious Mr. X (E. P. Dutton, New York, 1979).

16. Stephen J. Gould, "Darwin Vindicated," The New York Review of Books, August 16, 1979, p. 36.

17. Francis Darwin, The Life and Letters of Charles Darwin (John Murray, London, 1887), p. 220.

18. L. Huxley, Life and Letters of Thomas Henry Huxley (Macmillan, London, 1900), p. 97.

19. For this and other Darwin quotes on ambition see Robert K. Merton, The Sociology of Science: Theoretical and Empirical Investigations (University of Chicago Press, 1973), pp. 305-307.

20. R. A. Fisher, "Has Mendel's Work Been Rediscovered?" Annals of Science, 1, 115-137, 1936. For reprints of this and several other papers on Mendel see Curt Stern and Eva R. Sherwood, The Origin of Genetics: A Mendel Source Book (W. H. Freeman and Co., San Francisco, 1966), pp. 1-175.

21. L. C. Dunn, A Short History of Genetics (McGraw-Hill, New York, 1965), p. 13.

22. For Wright's analysis see Curt Stem and Eva R. Sherwood, The Origin of Genetics: A Mendel Source Book (W. H. Freeman and Co., San Francisco, 1966), pp. 173-175.

23. B. L. van der Waerden, "Mendel's Experiments," Centaurus, 12, 275-288,1968.

24. Anonymous, "Peas on Earth," Hort Science, 7, 5, 1972.

25. Peter B. Medawar, The Art of the Soluble (Barnes & Noble, New York, 1968), p. 7.

26. Gerald Holton, "Subelectrons, Presuppositions, and the Millikan- Ehrenhaft Dispute," Historical Studies in the Physical Sciences, 9,166-224,1978.

27. Allan D. Franklin, "Millikan's Published and Unpublished Data on Oil Drops," Historical Studies in the Physical Sciences, 11, 185-201,1981.

28. For an account of the Stanford discoveries see "Fractional Charge," Science 81, April 1981, p. 6.

(W. Broad and N. Wade, Betrayers of the Truth ― Fraud and Deceit in the Halls of Science, Simon and Schuster, New York, 1982. ISBN 0-671-44769-6. Chapter 2)