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Historical Scientific Standards, or: The Career of the “Varytron” April 14, 2013

Posted by Will Thomas in Commentary Track.
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Alichanian, apparatus

While Robert Millikan thought, circa 1930, that signs of the synthesis of the elements could be gleaned from the energy spectrum of the cosmic radiation, in the late 1940s Armenian physicists (and brothers) Artem Alikhanian and Abraham Alikhanov thought that the way forward in the nascent field of particle physics was by measuring the cosmic radiation’s mass spectrum. It turned out that they were right that unknown particles existed within that spectrum, but wrong that measuring that spectrum was the best path to take to stake discovery claims to them.

Alikhanian and Alikhanov’s work on cosmic radiation dates—remarkably, given that they were Soviet—to World War II, when, like Italians working at the same time (Monaldi, “Life of µ”), they used counter devices to measure the radiation’s properties. In the early postwar years, they (with a third reseracher, A. Weissenberg, on whom I have found little information) assembled counters in tiers (diagram at right*) so that they could make a rough measurement of the deflection of particles in a magnetic field, and make estimates of particle mass. Doing so, they measured a large number of particle masses, which, they argued, were much heavier than the known meson (or “mesotron”, now known as the muon, or µ), and yet lighter than the proton. Because these new particles seemed to have a variety of masses, Alikhanian and Alikhanov gave them the unitary name, “varytron”.

Subsequently, using a larger magnetic field, Alikhanian and Alikhanov were able to resolve the spectrum of varytron masses into discrete clusters, ostensibly representing individual particles. Working high in the Armenian mountains, previously unacknowledged particles, especially pions, probably were passing through their apparatus. However, in those days, when particle physics began to emerge from nuclear physics and cosmic-ray studies, not only were the brothers never credited with the discovery of any new particles, this work seems to have had very little influence at all. To understand why, we need to attend to the intricacies of the sorts of scientific arguments that prevailed at that time—the sort of task I emphasized in my recent series on history-philosophy relations.

Although the question is not an easy one to answer, I feel that under different circumstances, Alikhanian and Alikhanov might have received more credit than they did at the dawn of the era of the rapid discovery of new particles.

One major issue was that at that time experimenters using cloud chambers—a device with more metrical precision than their counter apparatus—were reporting lighter masses than the accepted range for the known muon, leading to suggestions that the particle might have a variable mass. This prospect was struck down by none other than Hans Bethe, who argued that such a radical claim had to constitute an explanation of last resort, and that reported measurements could in fact be reconciled with metrical errors common to cloud chamber experiments. Although Alikhanian and Alikhanov were not proposing a particle of variable mass, their metrical imprecision, and their choice of the term “varytron,” could not have helped their case.

Alikhanian and Alikhanov.  Source: AIP Emilio Segrè Visual Archives, Physics Today Collection

Alikhanian and Alikhanov. Source: AIP Emilio Segrè Visual Archives, Physics Today Collection

Now, it is possible to imagine a history in which experimenters were forced into new particle discoveries through refinements of mass measurements of individual particles. This is certainly the history that Alikhanian and Alikhanov imagined they were participating in. In that history, simply demonstrating the existence of extra particles, without resolving them into discrete discoveries, might in itself have constituted a major step forward, even if Alikhanian and Alikhanov’s particular contribution might not have been regarded as definitive proof due to the imprecision of their apparatus.

Given that their papers attracted little critical attention, it is difficult to say to what extent Alikhanian and Alikhanov’s paper would have been regarded as persuasive evidence that unknown particles existed. In the event, though, the prime strike against them was how little they could definitively say about those particles. This situation contrasts with results being produced by Cecil Powell’s group at the University of Bristol. Using nuclear emulsions, they were able to capture several plates offering visual evidence of a meson producing a “secondary” meson, which clearly indicated the existence of distinct particles.

In my “Strategies of Detection” paper (pdf, 15MB), I argue that the emulsions were not very good at resolving the mass of particles, and that the Powell group was unable to demonstrate how many distinct types of mesons they were seeing in their emulsions. However, using sophisticated arguments from nuclear physics, they were able to make a strong case that secondary mesons were not the same mass, and thus not the same particle, as the primary mesons. Although this did not preclude the theory that the meson had a variable mass, this was enough for theorists Robert Marshak and Bethe to cite their work as evidence in favor of Marshak’s “two meson” hypothesis.

On the other hand, Marshak and Bethe observed in a footnote, that Alikhanian and Alikhanov’s paper, while pertinent, was “less convincing,” and did not warrant detailed discussion. In a later interview with Charles Weiner, Marshak elaborated:

The Russians were constantly finding lots of intermediate mass particles… Alikhanian and his group—but they had small numbers of particles with all kinds of masses. Maybe some of the heavier mesons are pions but they had many more than are known even now. It was pretty poor stuff. But in the case of the Bristol work, these were nuclear emulsion events, and they looked very good, although they made a very serious mistake in the estimate of the mass of the heavier meson.

In an early draft** of my paper, I argued that this situation is not well described by Harry Collins’s celebrated “sociology of calibration,” because the Powell group’s emuslions were not exactly considered reliable (as Marshak’s quote illustrates). Rather, the crucial issue seems to have been more pointed disagreements about what sorts of tentative claims could be supported by what sorts of results. The kinds of claims that Alikhanian and Alikhanov could make were simply not ones that were valued.

As experienced historians of science will know, disagreements about the value of claims are rarely resolved cleanly. And indeed, in late 1948 Alikhanian and Alikhanov wrote a letter to Nature complaining that their work had been ignored. They further claimed that their ability to resolve numerous particle masses suggested that ascribing any particular identity to the particles that the Powell group detected in their emulsions might “lead to erroneous results.”

As it would happen, it soon transpired that there were a lot more particles than Marshak’s two mesons, but Alikhanian and Alikhanov’s results could not speak reliably to how many particles there were, or what their masses might be. In Powell’s reply to their letter, he lamented the political difficulties that made communication of results with the Soviets difficult (Powell, incidentally, was a political radical). He, however, felt that the Soviet claims to numerous particles were not well substantiated due to the “statistical fluctuations” in their data, though he did allow that their work was suggestive and looked forward to receiving additional results.

As I argue in “Strategies of Detection,” the analysis of “decay modes,” of which the Powell result was an early example, was soon to become a crucial way of staking claims to the discovery of new particles, though it was by no means clear at that precise moment that that would be the case. At a time when mass measurements remained deeply unreliable, the only even remotely reliable way to pick out novel particles was by capturing the transformation of particles into other particles, thus providing a limited set of tracks to identify as belonging to known or unknown entities. (Particle accelerators, however, would soon make other means of precision experimentation possible as well.)

Alikhanian and Alikhanov’s varytron did, however, claim one adherent at the observatory on Pic du Midi in France: physicist Jean Daudin, who published on varytrons as late as 1953. Strategies of detection aside from rough mass estimates were proving very productive and reasonably reliable by that late date. However, a commemorative website on Daudin, assembled by his daughter, offers us a clue, albeit not a definitive one, to his sympathies. According to her, Daudin was a committed communist who “ne sépare pas son activité de chercheur de sa reflexion politique et rédige des écrits sur la place de la Science dans la Société…” (did not separate his research activities from his political thought, and wrote about the place of science in society…). Unfortunately, Daudin suffered from tuberculosis, and died in 1954 at the age of 41. I have found no information on the “varytron” concept after this point.

Alikhanian and Alikhanov’s varytron occupies a strange place in scientific knowledge—it was a suggestive concept that was eclipsed less because it was wrong, than because it did not conform the most productive heuristics that existed in cosmic ray physics at that time. Experimental analyses of cosmic rays were constantly producing spurious results. Progress was made not by being right, but by producing tentative conclusions, which could serve as a constructive presupposition in further analyses. It was, if I may be permitted to stretch the concept, a field that was experiencing lots of small Kuhnian revolutions every couple of years. Understanding this mode of work and argumentation in this field at that time is instrumental to understanding why some concepts proved influential while others did not in that milieu.

One further note: investigating the tangential history of the varytron ended up nicely illustrating the point that this or that detail in history is important to someone. Aside from Daudin’s daughter’s website providing handy information on Daudin, it also turned out to be possible to do quick research on Alikhanian and Alikhanov because they are scientific heroes in Armenia, where the Yerevan Physics Institute is also known as the Alikhanian National Laboratory. A recent paper commemorating the 100th anniversary of Alikhanian’s birth offers a brief history of their work and the laboratory they founded. Both Alikhanian and Alikhanov, incidentally, were major players in Soviet physics, even though their varytron work ended up being a bit of a flop.

*Illustration from A. Alichanian, A. Alichanow, and A. Weissenberg, “On the Existence of Particles with a Mass Intermediate between Those of a Mesotron and a Proton,” Journal of Physics (USSR) 11 (1947): 97-99.

**I dropped this point from my final draft because it was extraneous to my overall point, but also because one of the people I had read the draft gathered that I was critiquing Peter Galison’s account of experiment interpretation from the standpoint of SSK, and I didn’t want to create needless confusion.



1. Michael Weiss - April 14, 2013

Interesting. With regard to “many mini Kuhn revolutions every couple of years”, assuming we want to use the Kuhn framework at all, doesn’t this sound more like Kuhn pre-paradigm period?

2. Joachim - April 14, 2013

As I understood Kuhn’s scenario a revolution requires a phase of normal puzzle solving, out of which grows an anomaly, which causes a crisis, and so on…

The premature phase of science is characterized by inchoate and outright contradictory theories and data.

What Will described seems to be neither, maybe puzzle solving of an exceptional kind.

3. Michael Weiss - April 14, 2013

I dunno, it sounded sort of inchoate to me… Variable masses, or maybe two discrete masses, or who knows how many discrete masses, difficulty in evaluating the reliability of experimental results, altogether a very confused situation — but *not* a sharp inconsistency with any established theory (or should I say paradigm), the hallmark of an anomaly, leading to a revolution.

Kuhn’s puzzle-solving really doesn’t seem to fit. This activity, as I read Kuhn, always takes place in the context of normal science, and consists of trying to resolve anomalies by “articulating the paradigm”.

Of course, perhaps this just means that the Kuhn framework doesn’t apply. Applying Kuhn theory self-referentially, we may have an anomaly to the Kuhn paradigm paradigm.

4. Will Thomas - April 14, 2013

Aha, you guys picked up on what was going through my head when I threw that line in there. I’m not at all committed to interpreting this with a Kuhnian model, but I thought it might be fun to give it a try. You could describe the situation as pre-paradigmatic, but there do seem to have been little pockets of normal-ish puzzle-solving work that followed from different sets of presuppositions. Then, as often as not, these presuppositions had to be discarded or substantially revised after a couple of years (i.e., “all positive particles we see are protons” -> “no, wait, they’re all positrons” -> “no wait, I guess they’re a mix of mesotrons and positrons, but fortunately mesotrons penetrate lead, so we can separate them out” -> “no, wait, I guess some protons get through after all” etc.)

Joachim - April 15, 2013

Sounds like discovery, pure and simple, in a new research field, where neither a paradigm has yet been established nor hold outs exist to revolt against.

Joachim - April 15, 2013

Or, if it must be forged into a Kuhnian narrative, it sounds like the establishment of a first paradigm in a new field – neither the pre-mature phase before nor the revolution thereafter.

5. Will Thomas - April 15, 2013

One interesting feature of the history is that prior to about 1950 experimentalists did not seem to expect to have to go through a long period of grasping about before hitting upon solid foundations. Thus, it seems generally as if there was an attitude of “if we can just get past this one obstacle, things will become more clear”. In its own way, even something as apparently radical as the variable-mass meson idea was conservative, in that it created only one problem—integrating a particle of variable mass into existing schemes (and not so radical, perhaps, in view of relativity and variable-energy photon creation, and the like.)

After 1950, and certainly by the famous 1953 Bagneres de Bigorre conference, it had become clear that the variety of particles was a real problem, and that there was, as yet, no underlying physics explaining why they should exist, or what laws governed their behavior. I believe that references to the “phenomenology” of particles arose in that period.

If the Kuhnian scheme had ever evolved into a more sophisticated vocabulary of “anomaly-handling,” it might be of some use as a guide here, but personally I do feel its use is limited, though it is evidently a very good conversation starter!

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