The Davisson Germer Experiment

In 1927, at Bell Telephone Laboratories in New York, a beam of electrons was fired at a plate of nickel and the scattered electrons were counted at different angles. The experiment was designed to answer a question about metals, and it did answer one — but only after a liquid-air bottle exploded and a cooling failure turned the polycrystalline target into a few large single crystals, and after a summer spent in Oxford where Louis de Broglie’s hypothesis was explained to an audience that included the experimenter. This is the story of a wrong question, an accidental change of specimen, and an idea that arrived too late to be useful and exactly in time to be decisive^[1].

The Wrong Question

The laboratory was the Bell Telephone Laboratories, and the men were Clinton Joseph Davisson and his colleague Lester Germer, working in room 7B of the West Village site in Manhattan. The apparatus belonged to Western Electric, the manufacturing arm of the Bell system, and the programme it belonged to was an industrial one: to understand the behaviour of electrons as they struck metal surfaces, because every piece of vacuum equipment in the telephone system depended on that behaviour and nobody had a satisfactory account of it. The question was not about waves. The question was about engineering^{[8, 2]}.

The programme was not chosen for its own sake. Vacuum tubes and electron tubes were at that moment the basis of long-distance telephony, of broadcasting and of the whole of the electronics industry, and the reliability of such a device depended on what happened to the electrons that bounced around inside it. Metallic surfaces were everywhere: the cathode, the anode, the grid. A beam of electrons hitting a metal and scattering in a complicated way was a daily engineering nuisance, and the angular distribution curve was the sort of thing an industrial laboratory wanted explained because a good explanation would make the devices better. Nothing in that brief pointed towards a foundational discovery, and that is exactly why the discovery was available to be made^{[8, 2]}

The first results came out between 1919 and 1923, from work with C. H. Kunsman. When a metal target was bombarded with electrons of a given energy, the secondary electrons coming off it were found to have a distribution in angle with two maxima, and the pattern was found again with platinum and with magnesium. The result was published in 1923 and it was, in the phrase used afterwards, a loose thread. The two maxima were real, they were reproducible, and they had no explanation. Two maxima is not smooth. Two maxima is a signature, and the secondaries in question carried the same energy as the primaries that had produced them, which is to say that they were being reflected rather than knocked loose. An electron that has been scattered inside a metal should have lost energy on the way out. These had not, and that was what made the result so hard to wave away. The ordinary expectation was that the secondary electrons should come off in a smooth distribution, more or less according to how the incident electron happened to be scattered in the material^{[9, 2]}.

The mechanism is worth describing because it explains why the effect was so dramatic. A polycrystalline metal surface is a mosaic: millions of small crystals, each with its own lattice orientation, so that a beam passing through many of them meets a great many different diffraction conditions, and the individual patterns blur together into a smooth average. Annealing a metal slowly produces large grains, and large grains with a single orientation preserve the diffraction pattern instead of averaging it away. The liquid-air bottle had done exactly that. In one accident the target was converted from an averaging device into a resolving device, and an experiment that had been running for six years acquired, without anyone intending it, the specimen it needed^{[2, 3]}

Something was offered in explanation, and it was offered early. In 1924 and 1925 the physicist Walter Elsasser suggested that the two maxima should be read not as a scattering effect at all but as diffraction, that is, as the interference pattern produced when a beam of particles behaved like a wave, in accordance with the hypothesis Louis de Broglie had put forward in his doctoral thesis in 1924. Davisson knew of the suggestion. He did not find it persuasive, and the usual explanation is that he regarded de Broglie’s hypothesis as too strange to be worth building an experiment around, and perhaps also that it did not seem to connect obviously to the particular effect under study. Either way, the suggestion was set aside, and it stayed set aside for a year^{[3, 2]}.

Then, in 1925, the apparatus was damaged. A bottle of liquid air, part of the cooling system that kept the target at a low enough temperature to stay clean, exploded. The heat of the explosion and the failure of the cooling that followed exposed the nickel target to temperatures it was not designed to withstand, and the nickel, which had been a surface of many small crystals, recrystallised into a new crystal structure. The change was permanent and it was enormous. Where there had been a jumble of crystallites in every orientation, there were now a few large single crystals, each with its own well-defined lattice direction and its own lattice planes, and the angular distribution of the scattered electrons, which had been smooth and featureless, developed sharp structure that depended strongly on where in the crystal the beam happened to strike. The accident had turned a piece of metal into a grating^{[2, 3]}.

It is worth being precise, too, about how nearly the whole thing was missed. The peaks had been in the data from 1925. The apparatus that produced them had been in use since 1919. The physicist who had the data and the apparatus and the training to interpret them had, in the accepted account, walked past the peaks for a year because he was looking for a scattering effect and not a diffraction effect. Nothing about the discovery required a new instrument, a new laboratory or a new idea about nature. It required an accident, a conversation at a meeting, and the willingness to look at a familiar curve and ask whether the bumps in it meant something^{[2, 3]}

It is worth being precise about what the accident did and did not do, because the popular version usually inflates it. The explosion did not produce diffraction. It produced a specimen capable of showing diffraction, which is a different and much more modest claim, and one that depended on the fact that the experiment was already looking at the angular dependence of scattered electrons with an instrument sensitive enough to see a narrow peak. If the original polycrystalline target had been capable of showing a sharp pattern, the accident would have been unnecessary. What the accident did was remove the averaging that had been hiding the structure. Davisson and Germer went back to work with the recrystallised target, and the peaks they found in it were the peaks they should have been finding all along^[3].

The paper of 1927 makes the point almost in passing, in the discussion of why the earlier results did not show the same structure. The experiment had been done, and it had been done well; what it had lacked was a specimen with a regular lattice rather than a soup of them. Between the accident of 1925 and the recognition of what the data meant in 1926 lay the most consequential summer in the history of the subject, and it was spent not in New York but in Oxford^[1].

The Apparatus

The experiment is best understood as a single curve. Everything the apparatus produced came down to one measurement: the current collected by a detector, plotted against the angle at which that detector was placed, for a given accelerating voltage. The apparatus existed to make that plot accurately, and it is worth describing because the constraints it imposed shaped what could be concluded from it^{[4, 1]}.

The source was an electron gun: a filament heated to release electrons, which were then accelerated through a known voltage — typically of the order of tens of volts, so that the electrons were slow by the standards of the nuclear physicists but fast enough to have a wavelength short enough to be comparable with the spacing of atoms in a crystal. They struck a target of nickel, which could be rotated so that the beam hit it at different angles and at different points on the crystal face. The vacuum was essential rather than decorative: a residual gas molecule in the path would scatter electrons in all directions and wash out the very structure the experiment was looking for^{[8, 4]}.

The detector was a Faraday box: a small collector, shaped rather like a deep cup, which could be swung around the target on an arc so that it could be placed at any scattering angle. Electrons entering the box deposited their charge on it, and the resulting current was measured with a galvanometer. The method was a nineteenth-century one, and it was chosen because it was sensitive and because it was not selective: unlike a photographic plate or a screen, the box responded to electrons coming from anywhere within its acceptance, so the plot it produced was a genuine intensity distribution rather than an image. The scattering angle, the accelerating voltage and the collector current were the three numbers that came off the bench for each setting^{[4, 1]}.

The shape of the collector was not incidental. A plain flat plate facing the target would have measured the current arriving at one angle but would also have been shadowed and biased by its own edges. The deep cup solved this: it admitted electrons over a wide range of directions while presenting almost none of its own surface to the incident beam, so that what it collected was very nearly the whole flux arriving within its acceptance. The measurement was therefore an integral of the angular distribution rather than a sample of it, and the curve it produced could be compared directly with a theory of the distribution rather than needing a correction for the shape of the detector. The same cup design was used for half a century afterwards^{[4, 1]}

The result of any one setting was a single point on the curve. What made the experiment decisive was that the whole curve could be taken at several voltages, and that the Bragg condition could then be tested against it. If the scattered electrons were being diffracted by the crystal lattice, then peaks should appear at angles that satisfied a specific geometrical relation involving the spacing of the lattice planes and the wavelength of the electrons, and the wavelength should itself change with the accelerating voltage in a known way. The measurement was therefore over-determined: a single peak could be fitted to almost anything, but a family of peaks taken at several voltages could not^{[4, 1]}.

The figures usually quoted are these. At an accelerating voltage of 54 volts a definite peak appears at a scattering angle of about 50 degrees, and the corresponding Bragg angle of roughly 65 degrees gives a lattice spacing for nickel of about 0.092 nanometres, which is of the right order for the atomic spacing of the metal. The measured values of the square root of the accelerating voltage, 7.36, 14.7 and 22, fall in proportion to the wavelengths predicted by the de Broglie relation, and this proportionality is the part of the evidence that is decisive. A small caveat should be recorded: these numbers come from a standard tertiary compilation of the experiment rather than from the paper itself, which has for decades been difficult to consult in full, and they should be treated as the accepted summary of the result rather than as a fresh reading of the measurements^[4].

That last point matters, because the argument was not made in terms of a single number. The de Broglie relation says that a particle of mass m moving with speed v has a matter wave whose wavelength is given by dividing the Planck constant by its momentum, so that increasing the accelerating voltage increases the electron’s speed and shortens its wavelength. What the experiment showed was that the positions of the peaks moved with the voltage in exactly the way that relation required, and that the geometry of the crystal lattice was consistent with the same relation read the other way round. The electrons were behaving like waves of a calculable length, and the crystal was the ruler against which the length was measured^{[1, 3]}.

Oxford, 1926: The Man Who Heard the Idea

The British Association met at Oxford in the summer of 1926, and Davisson was there with his data and without an explanation for them. He discussed the electron-scattering results with Max Born, with James Franck and with others in the audience, and for the first time in any detail he heard Louis de Broglie’s hypothesis, that a particle of velocity v has a wavelength given by dividing the Planck constant by its mass times its velocity. De Broglie’s thesis of 1924 had made the argument from the symmetry of the electromagnetic wave equations, and it had been regarded as one of the more speculative pieces of physics of its decade. It was, in effect, a wager: if matter waves existed, they would be undetectable in any ordinary circumstance, and only a very precise scattering experiment could show them^{[3, 2]}.

The hypothesis Davisson heard was, in its own terms, extremely bold. De Broglie had noticed that the wave equation for light and the equations of mechanics for matter could be written in a formally similar way, and that if the symmetry were real then a particle of matter must be associated with a wave whose wavelength was fixed by its momentum, through the ordinary constant that relates the energy of a photon to its frequency. The argument was so general that it also predicted that matter waves would be extremely short and therefore almost impossible to observe. De Broglie was explicit about this: the waves existed, but no existing means could show them. A hypothesis that announces its own untestability is not the kind of thing a laboratory in New Jersey is likely to be built around^{[3, 1]}

Davisson did not announce a conversion on the spot. What he did was go back to New York and look at his own curves again with the idea in hand, and this time he was not looking for a scattering effect but for interference. He and Germer began a deliberate search for maxima, sweeping the collector through the angles at which a diffraction pattern predicted peaks, and they found thirty of them. Twenty-nine of the thirty could be accounted for by the diffraction geometry. One could not. And eight peaks that the geometry predicted never appeared at all. The modern assessment of the experiment rests on that balance, and it is a much better assessment than the story usually told: the experiment was not a perfect demonstration, and the imperfections are part of why it reads as an experiment rather than a proof^[3].

The publication itself tells you something about the reception. The note in Nature was short, and it announced the confirmation of a hypothesis rather than the discovery of a new effect, which is why it could be written quickly and why it did not need the full apparatus description. The full Physical Review paper came later in the same year, with the curves and the analysis and the caveats, including the awkward ones: the peak that could not be explained and the peaks that failed to appear. Publishing the awkward ones alongside the convincing ones is what distinguishes a mature result from a lucky one, and it is part of the reason the experiment was still being cited and taught forty years later^{[5, 1]}

The second half of the story is the one that is often garbled, so it is worth stating exactly. The same idea was being tested at the same time, in a different laboratory, by a different route, and by a different generation. In Aberdeen, George Paget Thomson, the son of J. J. Thomson, was sending cathode rays through thin films and photographing the diffraction rings they produced. His collaborator at Aberdeen was Alexander Reid, and the two of them published “Diffraction of Cathode Rays by a Thin Film” in Nature in 1927, some weeks after Davisson and Germer’s own note. Thomson followed it with a second paper on thin films of platinum, and the fuller accounts of the Aberdeen work appeared in the Proceedings of the Royal Society in 1928, including Reid’s own paper on the diffraction of cathode rays by thin celluloid films. There was no single discoverer here: two groups, on opposite sides of the Atlantic, using a crystal and a film, arrived at the same conclusion within months of each other^{[5, 10]}.