2013 Pais Prize Lecture: “The Joy of History”

By Roger H. Stuewer, University of Minnesota

Introduction

Physicists and historians of physics share a common goal, the quest for understanding, but their objects are different: Physicists attempt to understand Nature, while historians attempt to understand the past, and as the novelist L.P. Hartley (1895-1972) famously remarked, “The past is a foreign country: they do things differently there.”¹ In 1891 the German polymath Hermann von Helmholtz reflected on his own researches, saying that:

I must compare myself to a mountain climber, who without knowing the way climbs up slowly and laboriously, must often turn around because he can go no farther, discovers new trails sometimes through reflection, sometimes through accident, which again lead him forward a little, and finally, if he reaches his goal, finds to his shame a Royal Road on which he could have traveled up, if he would have been clever enough to find the right starting point.²

This Royal Road, this linear, logical route to the summit, is eschewed by historians, who find both the challenge and joy of history in exploring the byways, uncovering the contingencies of historical events and shaping them into a coherent narrative. To illustrate this, I will draw on my own researches, showing how my analyses were based crucially on three different types of documentary evidence, private laboratory notebooks, unpublished personal correspondence, and the published literature.

The Discovery of the Compton Effect

When I began thinking about the discovery of the Compton effect, the first thing I did was read Arthur Holly Compton’s classic 1923 paper,³ and I soon realized that something important was missing. Nowhere in his paper did Compton mention Einstein’s light-quantum (or photon) hypothesis or cite his famous 1905 paper, or even mention Einstein’s name. I thus asked myself: Was it possible that Compton discovered the Compton effect essentially independently of Einstein’s hypothesis? As we will see, I eventually was able to answer this historical question by analyzing Compton’s laboratory notebooks.⁴

Compton’s Ph.D. research at Princeton and his subsequent research at Minnesota during the academic year 1916-1917 focused on the scattering of X rays from crystals, but he could not pursue it at Westinghouse in Pittsburgh because it had nothing to do with the production of better light bulbs. Nonetheless, he kept abreast of the literature, and in 1917 came across a paper by C.G. Barkla,⁵ in which he reported that X rays passing through aluminum had a mass-scattering coefficient smaller than the classical Thomson mass-scattering coefficient. To explain this, Compton eventually concluded that Barkla’s X rays were being diffracted by ring electrons in the aluminum atom, which meant that the diameter of the ring electron, the diffracting obstacle, had to be comparable to the wavelength of the incident X rays, perhaps about 0.1 Ångstrom. That was a very large electron, but Compton showed that X rays incident on it would have a mass-scattering coefficient smaller than the classical Thomson value.

When Compton left Westinghouse to go to the Cavendish Laboratory in 1919, however, he soon discovered that its new Director, the blunt Ernest Rutherford, would have nothing whatsoever to do with this idea. Thus, Compton recalled that Rutherford once introduced him with the words: “This is Dr. Compton, who is with us from the United States to discuss his work on ‘The Size of the Electron.’ I hope you will listen to him attentively. But you don’t have to believe him!”⁶ Rutherford’s first biographer also recalled that Rutherford once burst out saying, “I will not have an electron as big as a balloon in my Laboratory!”⁷

Compton also rethought his ideas after he carried out γ-ray experiments at the Cavendish and found that scattered γ rays became “softer” or of longer wavelength than the primary γ rays, which he eventually explained by assuming that the incident γ rays were striking tiny electron-oscillators in the scatterer and propelling them forward while they emitted a new type of Doppler-shifted fluorescent γ radiation of longer wavelength. Later, in the summer of 1920, when Compton left the Cavendish to go to Washington University in St. Louis, he took a Bragg spectrometer along with him, used it to produce a monochromatic beam of X rays, and by April 1921 found that when scattered they also excited a similar type of Doppler-shifted fluorescent X rays of longer wavelength.⁸

That fall Compton then used his Bragg spectrometer to compare the primary spectrum of MoKα X rays of wavelength λ = 0.708 Ångstrom to their secondary spectrum when scattered through an angle of about 90˚ by pyrex and graphite. And this is precisely where my analysis of Compton’s laboratory notebooks was crucial to understanding the further development of Compton’s thought. Thus, Compton reported that the wavelength of the scattered X rays was about 35 percent greater than the wavelength of the primary X rays. I could not understand that claim—until I plotted Compton’s data directly from his laboratory notebooks. My plots for a pyrex scatterer showed that the prominent line in the secondary spectrum is shifted to a slightly higher wavelength than that line in the primary spectrum. In other words, I knew what I was looking for, but Compton did not, so when he reported a huge 35-percent increase in wavelength it was clear to me that he had taken the primary spectrum to be the prominent high-intensity lines—which he took to be a single line at 0.708 Å—and the secondary spectrum to be the low-intensity lines—which he took to be a single line at 0.95 Å, and which we recognize today as the secondary MoKα spectrum. To Compton, however, the ratio of the primary to secondary wavelengths was λ/λʹ = 0.708 Å/0.95 Å = 0.75.

But how did Compton explain this huge shift in wavelength? It seemed clear to me that he must have invoked his Doppler-shifted fluorescent-radiation hypothesis, so I carried out the simple calculation that Compton had omitted: As seen at 90˚, the ratio of the primary to the secondary wavelengths is λ/λʹ = 1 - v/c, where v is the velocity of the electron-oscillators that were emitting his new fluorescent X rays. But what was the velocity v? By “conservation of energy,” that is, by setting ½mv2 = hν, we have that λ/λʹ = 1 - v/c = 1 - (2hν/mc2)½ = 1 - [2(.017 MeV)/(.51 MeV)]½ = 1 - 0.26 = 0.74. Who could ask for better agreement between theory and experiment? I have called this the first phase of Compton’s classical-quantum compromise, which to me it is a splendid historical example of a false theory being confirmed by spurious experimental data.

One year later, by October 1922, Compton realized that he had misread his experimental data, and that the shift in wavelength between the primary and secondary X-ray spectra was only a few per cent. He now reported that the ratio of the primary to the secondary wavelength was λ/λʹ = 0.708 Å/0.730 Å = 0.969. But how did he now explain this new experimental result? Again by his Doppler-shifted fluorescent-radiation hypothesis. Thus, at a scattering angle of 90˚ we again have that λ/λʹ = 1 - v/c, but how did Compton now determine the velocity v of the electron-oscillators? By “conservation of momentum,” that is, he set mv = h/λ to yield λ/λʹ = 1 - v/c = 1 - h/mcλ = 1 - 0.034 = 0.966. Again, who could ask for better agreement between theory and experiment? I have called this the second phase of Compton’s classical-quantum compromise, which to me it is a splendid historical example of a false theory being confirmed by good experimental data.

Within a month, Compton put everything together.⁹ He set up the correct vector diagram for conservation of momentum, invoked both conservation of energy and conservation of momentum, used the correct relativistic expression for the mass of the electron, and derived a formula equivalent to his famous expression for the change in wavelength, which at a scattering angle of 90˚ reduces toΔλ = λʹ - λ = h/mc = 0.024 Å, which he compared to his experimental value of 0.022 Å. This, however, was precisely the same experimental data that he had reported one month earlier, in October 1922—he merely changed his formulas by substituting his new theoretical expression for his old one. Every physicist knows that good experimental data lasts forever, while theories come and go.

In sum, Compton followed no Royal Road to his discovery of the Compton effect. His thought evolved—over a period of six years—only as fast as his own experimental and theoretical researches progressed. His motivation never was to carry out an experiment to test or confirm Einstein’s light-quantum (or photon) hypothesis, so we now can understand why Compton never cited Einstein’s 1905 paper or even mentioned Einstein’s name in his 1923 paper.

In complete contrast, Peter Debye at the Federal Institute of Technology (Eidgenössische Technische Hochscule, ETH) in Zurich, Switzerland, did follow a Royal Road by directly adopting Einstein’s light-quantum hypothesis and discovering the same effect, seemingly virtually simultaneously. That, however, illustrates the contingency of the publication process. Compton submitted his paper to The Physical Review on December 13, 1922, where it was published in May 1923, while Debye submitted his paper to the Physikalische Zeitschrift on March 14, 1923, where it was published on April 15, 1923, that is, one month before Compton’s paper was published in The Physical Review. Fortunately for Compton, Arnold Sommerfeld was just then a visiting professor at the University of Wisconsin, and when he returned home to Munich he spread the word that Compton had priority in both theory and experiment. Debye himself later insisted that it should be called the Compton effect, and not the Compton-Debye effect, because, he said, the person who did most of the work should get the name.

Millikan and the Photoelectric-Effect

No physicist to my knowledge was more concerned with trying to establish his priority than Robert A. Millikan. Thus, in his Autobiography, which he published in 1950 at the age of 82, he included a chapter entitled “The Experimental Proof of the Existence of the Photon,” in which he wrote that at the April 1915 meeting of the American Physical Society in Washington, D.C., his experiments on the photoelectric effect constituted a “complete verification of the validity of Einstein’s equation,” adding that:

This seemed to me, as it did to many others, a matter of very great importance, for it ... proved simply and irrefutably I thought, that the emitted electron that escapes with the energy hν gets that energy by the direct transfer of hν units of energy from the light to the electron [Millikan’s italics] and hence scarcely permits of any other interpretation than that which Einstein had originally suggested, namely that of the semi-corpuscular or photon theory of light itself.¹⁰

In other words, he, not Compton, had first established the validity of Einstein’s light-quantum (or photon) hypothesis. It seems, however, that Millikan never dreamed that someday some historian might actually read his 1915 paper. Thus, in 1915, at age 47, he had indeed established the validity of Einstein’s equation,¹¹ which achievement, however, he clarified in his 1917 book, The Electron, writing that:

Despite...the apparently complete success of the Einstein equation, the physical theory of which it was designed to be the symbolic expression is found so untenable that ... we are in the position of having built a very perfect structure and then knocked out entirely the underpinning without causing the building to fall. It [Einstein’s equation] stands complete and apparently well tested, but without any visible means of support.... Experiment has outrun theory, or better, guided by erroneous theory [my italics], it has discovered relationships which seem to be of the greatest interest and importance, but the reasons for them are as yet not at all understood.¹²

Millikan’s quest for priority thus led him to completely revise history. By then, however, he already had had some experience with that. Thus, in 1899 J.J. Thomson was photographed sitting in his study in Cambridge, England, in a chair that once had belonged to James Clerk Maxwell.¹³ Seven years later, in 1906, Millikan and Henry G. Gale published their textbook, A First Course in Physics, in which Millikan reproduced this picture of J.J. Thomson, but with a noticeable difference: He etched out the cigarette in J.J.’s left hand.¹⁴ He evidently wanted his students to admire J.J. as a great experimentalist, but not to mimic his bad habit. I confess that I found some satisfaction, even a little joy, in catching Millikan out here. In any case, these two episodes beautifully illustrate what I like to call Millikan’s philosophy of history: If the facts don’t fit your theory, change the facts.

The Cambridge-Vienna Controversy on Artificial Nuclear Disintegration

In the late 1970s, I turned to the history of nuclear physics, building on my graduate research in nuclear physics and on the proceedings of a symposium I organized on the history of nuclear physics in the 1930s.¹⁵ In one of my studies, I focused on a long controversy between Ernest Rutherford and James Chadwick at the Cavendish Laboratory in Cambridge and Hans Pettersson and Gerhard Kirsch at the Institute for Radium Research (Institut für Radiumforschung) in Vienna.¹⁶ As we will see, its resolution would have remained unknown if I had not uncovered crucial correspondence between the protagonists.

A few months before moving from Manchester to Cambridge in the middle of 1919, Rutherford discovered that RaC (83Bi214) alpha particles could disintegrate a nitrogen nucleus, expelling protons that produced scintillations—tiny flashes of light—on a “scintillation screen.” Rutherford knew from long experience that the observation of such scintillations was difficult and tedious, and also depended on the observer’s optical system, training, experience, physical health, and psychological state.¹⁷

Rutherford and his right-hand man Chadwick found by 1921 that RaC alpha particles could disintegrate the nuclei of various light elements. In 1923, however, Pettersson and Kirsch in Vienna reported that RaC alpha particles could expel protons from many more nuclei. Moreover, they also challenged Rutherford’s interpretation of the disintegration process. Rutherford and Chadwick, however, were undeterred. In 1924 they published a bar graph showing that protons could be expelled from many light elements, but not from carbon or oxygen, contrary to what Pettersson and Kirsch had claimed.

By July 1924, Rutherford, who was not famous for his patience, let off some steam to his friend Niels Bohr, writing, in the first of many letters I found in the Cambridge University Library, that:

He [Pettersson] seems a clever and ingenious fellow, but with a terrible capacity for getting hold of the wrong end of the stick. From our experiments, Chadwick and I are convinced that nearly all his work published hitherto is either demonstrably wrong or wrongly interpreted.... It is a very great pity that he and his collaborators are making such a mess of things, for it is only making confusion in the subject.¹⁸

Here was Rutherford, by far the most revered experimental physicist of the period, placing Pettersson, a novice, on notice, as well as Pettersson’s boss and Rutherford’s friend, Stefan Meyer, Director of the Institute for Radium Research.

The battle lines therefore were drawn. By the summer of 1925 the tone of the controversy can be judged from a letter that Chadwick wrote to Rutherford while he and his wife were on an extended trip home to New Zealand and Australia:

Our friend Kirsch has now let himself loose in the Physikalische Zeitschrift. His tone is really impudent to put it very mildly.... Kirsch & Pettersson seem to be rather above themselves. A good kick from behind would do them a lot of good. The name on the paper is that of Kirsch but the voice is the familiar bleat of Pettersson. I don’t know which is the boss but as Mr. Johnson said there is no settling a point of precedence between a louse and a flea.¹⁹

The controversy was clearly heating up. In February 1926 Rutherford proposed an explanation of his and Chadwick’s observational differences with the Vienna team in another letter to Bohr, writing that:

The idea that you can discriminate between slow α particles and H particles [protons] by the intensity of the scintillation is probably the cause of their going wrong.... [Such] a discrimination by eye is terribly dangerous.²⁰

In other words, a low-energy scattered alpha particle could produce a scintillation just as bright as a high-energy disintegration proton.

Only one avenue remained open to resolve the controversy, namely, an exchange of visits between the two laboratories. Pettersson visited the Cavendish first, in May 1927, each evening reporting his experiences to Meyer in long letters I found in the Institute for Radium Research. He told Meyer that Rutherford and Chadwick was treating him well, but nothing convinced him that their observations were correct.

Then the time came for the return visit. Rutherford was far too busy to make the trip, so he dispatched Chadwick to Vienna, where he and his wife arrived on Wednesday, December 7, 1927, and stayed in the comfortable Hotel Regina, about a ten-minute walk from the Institute for Radium Research. Chadwick told Rutherford in his first letter from Vienna that after unpacking he went to the institute and talked with Meyer and “Pettersson’s people.”²¹ He made no progress in resolving the controversy, however, nor did he on Thursday, because it “was a holy day and no work could be done without danger to our future in the world to come.” Friday, December 9, however, was very different. Chadwick told Rutherford that he and Pettersson “ended up with a fierce and very loud discussion.” Nor would Pettersson agree to allow Chadwick to test whether carbon could be disintegrated, which “precipitated a most fiery outburst....” Chadwick wrote that Meyer and others “with no direct interest in the question [were] exceedingly pleasant and friendly but the younger ones [stood] around stifflegged and with bristling hair.”

The atmosphere thus was extremely tense. As Elisabeth Rona, one of Pettersson’s assistants, recalled:

The impression made on us by Chadwick...was not favorable. He seemed to us to be cold, unfriendly, and completely lacking in a sense of humor. Probably he was just as uncomfortable in the role of judge as we were in that of the judged.²²

Rona added that she later understood that Chadwick’s “ordeal” when he was incarcerated in Berlin during the Great War “had much to do with his behavior” now that he again was in a German-speaking city.

On Monday, December 12, everything changed. Rona recalled that:

All of us sat in a dark room [in the laboratory] for half an hour to adapt to the darkness. There was no conversation; the only noise was the rattling of Chadwick’s keys. There was nothing in the situation to quiet our nerves or make us comfortable.²³

Chadwick reported to Rutherford, that:

I arranged that the girls should count and that I should determine the order of the counts. I made no change whatever in the apparatus, but I ran them up and down the scale like a cat on a piano—but no more drastically than I would in our own experiments if I suspected any bias.²⁴

The result was that the counters found “no evidence” of disintegration protons from carbon. Chadwick added that he could see “no reason why the counters should be off colour.”²⁵

The Vienna scintillation counters, in fact, came as a great surprise to Chadwick. In Cambridge he and Rutherford regularly participated in the scintillation counting, but in Vienna, Chadwick told Rutherford,

Not one of the men does any counting. It is all done by 3 young women. Pettersson says the men get too bored with routine work and finally cannot see anything, while women can go on forever.²⁶

Chadwick also later recalled in an interview that Pettersson said he believed that women were more reliable than men as scintillation counters because they would not be thinking while observing, and that Pettersson preferred women of “Slavic descent” as counters because he believed that Slavs had superior eyesight.²⁷ We do not know in what tone of voice Pettersson made these remarks. We do know, however, that he respected his women scintillation counters, and they him, and that they in fact were remarkably talented scientists with outstanding careers ahead of them.*

Chadwick emphasized that the Vienna scintillation counters were not being dishonest; he suspected no cheating. Rather, they were deluding themselves. They knew that their bosses, Pettersson and Kirsch, believed that scattered alpha particles could be distinguished from disintegration protons by the brightness of their scintillations, while Rutherford and Chadwick knew that was impossible. Moreover, the Vienna scintillation counters were informed of the nature of the experiments, and they knew that Pettersson and Kirsch believed that carbon could be disintegrated. They therefore saw what they were expected to see. They had fallen prey to a psychological effect, much as in the famous earlier case of René Blondlot and his N Rays.

When Chadwick confronted Pettersson with these troubling results he become “very angry indeed,”²⁸ and when they met in Meyer’s office on Wednesday morning, December 14, Meyer became “very upset indeed” and offered to do anything necessary to set the record straight, such as make a public retraction. Chadwick refused this suggestion, however, because he knew that Rutherford was adamantly opposed to public controversy, and also that Rutherford would not wish to do anything that might cause his friend Meyer pain, which a public retraction certainly would. Chadwick therefore told Meyer that the Vienna experiments should simply be dropped, and nothing further should be said about them.

In sum, the progress and resolution of the Cambridge-Vienna controversy would never have been known if the above correspondence had not been preserved. In fact, its resolution was kept so secret that not even those close to it but outside of the innermost circle permitted to know about it. Elisabeth Rona, for example, later wrote that, “As far as I know, the discrepancies between the two laboratories were never resolved.”²⁹

The Meitner-Frisch Interpretation of Nuclear Fission

My final story began when I asked myself, How did it happen that Lise Meitner and her nephew, Otto Robert Frisch, were able to propose their novel and correct interpretation of nuclear fission when they met in Kungälv, Sweden, near Göteborg, over the Christmas holidays of 1938?³⁰ The answer, I found, emerged from a careful analysis of the published literature and supports, I believe, Arthur Koestler’s analysis of the act of creation, namely that:

the more original a discovery the more obvious it seems afterwards. The creative act is not an act of creation in the sense of the Old Testament. It does not create something out of nothing; it uncovers, selects, re-shuffles, combines, synthesizes already existing facts, ideas, faculties, skills.³¹

To Koestler the creative act thus constitutes the synthesis of what he called two previously unrelated “matrices of thought.”³²

I knew that to understand Meitner and Frisch’s creative act I had to understand the origin of the liquid-drop model of the nucleus, which, contrary to what many physicists seem to believe, was not invented by Niels Bohr in 1936 but was invented by George Gamow eight years earlier, at the end of 1928, while he was at Bohr’s institute in Copenhagen.

Gamow imagined that the nucleus consists of a collection of alpha particles with short-range attractive forces between them that balance their Coulomb repulsion, and that they exert an outward pressure owing to their kinetic and potential energy but are held inside the nucleus by its “surface tension.” He calculated the total “drop energy” of the nucleus in terms of the number of alpha particles in it, and found that a plot of the resulting mass-defect curve has a distinct minimum in it. Five years later, in 1933, after Chadwick’s discovery of the neutron, Werner Heisenberg recalculated the total energy in terms of the number of neutrons and protons in the nucleus and again found that the mass-defect curve has a distinct minimum in it. Then, in 1935, Heisenberg’s student, C.F. von Weizsäcker, extended his mentor’s work, introducing his famous semi-empirical mass formula, and again finding the same distinct minimum in the mass-defect curve. His result thus constituted the culmination of the line of development that Gamow had inaugurated in 1928.

A second phase in the history of liquid-drop model began in February 1936 when Niels Bohr published his theory of the compound nucleus. He argued that a neutron incident on a heavy nucleus interacts with many neutrons and protons in it, producing an excited, long-lived compound nucleus, which then decays by the emission of a proton, neutron, gamma ray, or by any process consistent with conservation of energy. Bohr went on to claim that if the energy of the incident neutron were increased more and more, even up to 1000 MeV, then many charged or uncharged particles would be expelled and the entire nucleus would eventually explode. Otto Robert Frisch drew a picture for Bohr that illustrated the early stage of this process, showing an incident neutron transferring energy to the target nucleus, causing the excited compound nucleus to first heat up, and then to cool down by the evaporation of a single particle from its surface. Bohr and his assistant, Fritz Kalckar, developed this idea further in 1937.

We therefore see that the liquid-drop model of the nucleus developed in two stages, first from 1928-1935 with the work of Gamow, Heisenberg, and von Weizsäcker, who calculated the nuclear mass-defect curve by focusing on static features of the model, and second, from 1936-1937 with the work of Bohr and Kalckar, who calculated nuclear excitations by focusing on dynamic features of the model. I showed that the first stage persisted in Berlin into 1938, and that the second stage persisted in Copenhagen, also into 1938. And just at that time, in the middle of 1938, Lise Meitner, who had been thoroughly embedded in the Berlin tradition, was spirited out of Berlin and eventually made her way Stockholm, while her nephew, Otto Robert Frisch, had been thoroughly embedded in the Copenhagen tradition since 1934 while working in Bohr’s institute.

Based on Frisch’s published recollections, I concluded that the Berlin and Copenhagen traditions merged in his and Meitner’s minds during their memorable walk in the snow in Kungälv, Sweden, over the Christmas holidays of 1938. I reconstructed their conversation as follows: First, Meitner rejected the idea that Otto Hahn had made a mistake when he and Fritz Strassmann reported finding barium, an element of intermediate atomic weight, when neutrons bombarded uranium. Both Meitner and Frisch then sensed that this could not be explained by a chipping off or cracking up of the uranium nucleus. Meitner, it seems, then thought of the liquid-drop model of the nucleus in this connection, while Frisch probably suggested the possibility that an incident neutron would induce oscillations in it, since he had sketched just such a picture for Bohr. Meitner then drew a large circle with a smaller circle inside it, which Frisch immediately interpreted as an end-on view of a dumbbell—as an elongated liquid drop with a constriction between its two halves. Meitner, whom Frisch recalled “had the mass-defect curve pretty well in her head,” then estimated from it that about 200 MeV—an enormous amount of energy—would be released if the heavy uranium nucleus were split up into two nuclei at the middle of the periodic table. Meanwhile, Frisch had realized that the repulsive surface charge of a heavy nucleus like the uranium nucleus of atomic number about 100 would offset its attractive surface tension. He also calculated that two nuclei in the middle of the periodic table, if initially in contact, would fly apart under their mutual Coulomb repulsion with an energy of about 200 MeV—in agreement with Meitner’s figure. As Frisch said, “We put our different kinds of knowledge together.” I think Koestler would have said that a synthesis of their two different “matrices of thought” occurred.

When Frisch returned to Copenhagen and told Bohr about his and Meitner’s interpretation, Bohr burst out, saying,”Oh, what fools we have been! We ought to have seen that before.” Bohr now immediately saw that he had missed this Royal Road to the summit, while by exploring its byways I saw that he had been missed it, at least in part, by proposing a very different picture, that a neutron of increasing energy incident on a heavy nucleus would eventually cause it to explode. Meitner and Frisch, by contrast, had climbed to the summit by following two different routes that were contingent on their different personal trajectories and scientific knowledge.

The Human Factor

In closing, I note that besides sharing the common goal of understanding, both physics and history of physics are human endeavors, and nothing has given me more joy over the years than working with many physicists, historians, and others in a variety of activities, for example, in founding and directing Minnesota’s Program in History of Science and Technology, in organizing the 1977 Minnesota symposium on the history of nuclear physics in the 1930s and the annual Seven Pines Symposia, in editing the Resource Letters of the American Journal of Physics and co-editing Physics in Perspective, and in contributing to the professional activities of the History of Science Society, American Physical Society, American Institute of Physics, and American Association of Physics Teachers. I am deeply grateful to my many students, colleagues, and friends who have joined and supported me in these richly rewarding endeavors.

End Notes

1. L.P. Hartley, The Go-Between (London: Hamish Hamilton, 1953), p. 9.

2. Hermann von Helmholtz, Ansprachen und Reden gehalten bei der am 2. November 1891 zu Ehren von Hermann von Helmholtz veranstalteten Feier (Berlin: Hirschwald’sche Buchhandlung, 1892), p. 54 (my translation).

3. Arthur H. Compton, “A Quantum Theory of the Scattering of X-Rays by Light Elements,” Physical Review 24 (1923) 483-502; reprinted in Robert S. Shankland, ed., Scientific Papers of Arthur Holly Compton: X-Ray and Other Studies (Chicago and London: The University of Chicago Press, 1973), pp. 382-401.

4. For a full account, see Roger H. Stuewer, The Compton Effect: Turning Point in Physics (New York: Science History Publications, 1975), Chapters 3-6, pp. 91-285.

5. C.G. Barkla and M.P. White, “Notes on the Absorption and Scattering of X-rays and the Characteristic Radiation of J-series,” Philosophical Magazine 34 (1917), 270-285.

6. Quoted in Arthur Holly Compton, “Personal Reminiscences,” in Marjorie Johnston, ed., The Cosmos of Arthur Holly Compton (New York: Alfred A. Knopf, 1967), p. 29.

7. Quoted in A.S. Eve, Rutherford: Being the Life and Letters of the Rt Hon. Lord Rutherford, O.M. (New York: The Macmillan Company and Cambridge: At the University Press, 1939), p. 285.

8. Arthur H. Compton, “Secondary High Frequency Radiation,” Phys. Rev. 18 (1921), 96-98; reprinted in Scientific Papers (ref. 3), pp. 305-307.

9. Compton, “Quantum Theory” (ref. 3).

10. Robert A. Millikan, The Autobiography of Robert A. Millikan (New York: Prentice-Hall, 1950), pp. 101-107, on pp.101-102.

11. Stuewer, Compton Effect (ref. 4), pp. 72-75.

12. Robert Andrews Millikan, The Electron: Its Isolation and Measurement and the Determination of Some of its Properties (Chicago: The University of Chicago Press, 1917), p. 230.

13. George Paget Thomson, J.J. Thomson and the Cavendish Laboratory in his Day, Nelson (London: Nelson, 1964), facing p. 53.

14. Robert Andrews Millikan and Henry Gordon Gale, A First Course in Physics (Boston, New York, Chicago, London: Ginn and Company, 1906), facing p. 482.

15. Roger H. Stuewer, ed., Nuclear Physics in Retrospect: Proceedings of a Symposium on the 1930s (Minneapolis: University of Minnesota Press, 1979).

16. For a full account, see Roger H. Stuewer, “Artificial Disintegration and the Cambridge-Vienna Controversy,” in Peter Achinstein and Owen Hannaway, ed., Observation, Experiment, and Hypothesis in Modern Physical Science (Cambridge, Mass. and London: The MIT Press, 1985), pp. 239-307.

17. E. Rutherford, “Collision of α Particles with Light Atoms. I. Hydrogen,” Phil. Mag., 37 (1919), 537-561; reprinted in James Chadwick, ed., The Collected Papers of Lord Rutherford of Nelson, O.M., F.R.S, Vol. Two. Manchester (London: George Allen and Unwin, 1963), pp. 547-567, on pp. 550-551.

18. Rutherford to Bohr, July 18, 1924, Rutherford Correspondence, Cambridge University Library; hereafter RC.

19. Chadwick to Rutherford, undated but July-August 1925, RC.

20. Rutherford to Bohr, February 8, 1926, RC.

21. Chadwick to Rutherford, December 9, [1927], RC.

22. Elizabeth Rona, How It Came About: Radioactivity, Nuclear Physics, Atomic Energy (Oak Ridge, Tenn.: Oak Ridge Associated Universities, undated, ca. 1976), p. 20.

23. Ibid.

24. Chadwick to Rutherford, December 12, [1927], RC.

25. Ibid.

26. Ibid.

27. Interview of James Chadwick by Charles Weiner on April 17, 1969, Session III, Niels Bohr Library and Archives, American Institute of Phyiscs, College Park, MD USA, p. 10 of 37.

28. Ibid.

29. Rona, How It Came About (ref. 22), p. 20.

30. For a full account, see Roger H. Stuewer, “The Origin of the Liquid-Drop Model and the Interpretation of Nuclear Fission,” Perspectives on Science 2 (1994), 39-92.

31. Arthur Koestler, The Act of Creation (New York: Macmillan. 1964), p. 120.

32. Ibid., p. 207.

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The articles in this issue represent the views of their authors and are not necessarily those of the Forum or APS.