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Exemplary Episodes: The N-Rays January 19, 2010

Posted by Will Thomas in Uncategorized.
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Photographic evidence of N-rays

The N-ray research program, led by respected French physicist Prosper-René Blondlot (1849-1930) and followed by many others, was of substantial significance, generating about 300 papers in the period between 1903 to 1906.  N-ray researchers not only argued for the existence of N-rays, but detailed their physical properties.  Their work is routinely included in the history of the new radiations of x-rays and Henri Becquerel’s radiation, and is often paired with psychologist and sociologist Gustave Le Bon’s “black light” (here not the same as UV light) as part of the discoveries of “spurious” forms of radiation.   Notably, cosmic rays, discovered around the same time, were also initially very slippery to detect, and would remain in limbo for well over a decade before being fully accepted as a phenomenon of extraterrestrial origin (never mind further disputes over their composition).

Traditionally, the N-ray research program has been of interest as an exemplary episode—an instrumental use of history that imparts a lesson or principle.  Because the rays do not actually exist, the historical flourishing of a research program dedicated to studying them becomes a cautionary tale to scientists.  Unless the lessons of the “affair” are heeded, you, too, could end up like Blondlot, needlessly wasting research effort on a chimera.  Unlike Blondlot, your follies probably won’t become a legend that lives on long after you (and after your legitimate achievements are forgotten), but it nevertheless wouldn’t do to acquire a reputation as methodologically reckless.

As an exemplary episode, the historical context of the N-ray program is typically analyzed in order to explain how it could have been allowed to exist at all, rather than to properly characterize its place amid contemporaneous research programs. Mary Jo Nye’s key contribution: “N-rays: An Episode in the History and Psychology of Science,” Historical Studies in the Physical Sciences 11 (1980): 125-156, notably, provides a self-standing history of the N-ray research program, as well as a detailed explanation of its existence.

Nye’s piece works well, because, even though it doesn’t judge the significance of the N-ray program in comparison to the x-ray program, it does offer a compact assessment of the research’s support and lack thereof, from its conception as an offshoot of Blondlot’s attempts to measure the polarization properties of x-rays, to its denouement following visiting Johns Hopkins physicist Robert Wood’s tampering with an experiment in-progress unknown and undetected by Blondlot.  In particular, it accounts for the suspicions and criticisms that surrounded the N-ray program throughout its existence, delineating the program’s arguments, objections to those arguments, and the defensive strategies deployed by the program’s adherents.

Without mentioning any theoretical or methodological framework (except, as we will see, Kuhn’s), Nye’s work essentially incorporates historiographical insights that would later be presented as methodological products of the social studies of science program.  Where nine years later Schaffer would essentially write “Glass Works” around Harry Collins’ sociology of calibration, this article, already in 1980, contains a robust description of how faith in the apparatus—here the ability to visually detect changes in the brightness of sparks and phosphorescent dots—became a site of contention as those unable to detect the phenomena could be dismissed as not having sufficiently acute vision.  She also describes how photographic evidence was invoked to bolster the claims to objectivity of N-ray researchers by overcoming physiological variability (only to meet criticism that the photographs were subconsciously rigged), how the social status and experimental talent of Blondlot’s assistant were implicated in criticisms, and how the novelty and mysteriousness of the N-rays themselves could be invoked to overcome criticisms of their seemingly contradictory behaviors.

Nye also discusses anxieties of decline in French science, a professional tendency to close ranks around its celebrated members, the prevalence of interest in paranormal phenomena at that time, the premium the scientific community placed on bold new results, and so forth.  She places especial emphasis on the characteristics of the period.  Invoking the Kuhnian model, she emphasizes that it took place “at the margins of normal science”; in other words at a moment when physics was “experiencing a conceptual crisis”.  At this time, “Traditional methods did not always suffice when the rapid pace and sheer bulk of reported data for chemical, heating, and electrical effects made difficult quick decisions about apparently contradictory observations.”  These circumstances “may help explain the exaggerated importance assumed by social and psychological forces in the discovery and confirmation of N-rays.”

The paper should not, however, be understood as an entry in the “sociology of error”.  Far from reinforcing the lesson of the exemplary episode, she takes the analysis to blunt those lessons: the research “was not ‘pathological,’ much less ‘irrational’ or ‘pseudo-scientific'” (155).  Furthermore, despite the delineation of particular “social” forces, there is no indication that Nye takes more ordinary scientific work to be un-social.  Rather, in this case ordinarily accepted social rules, such as the refusal of requests by non-members of the program to collaborate in observations, “were suspended longer and more broadly in France than elsewhere” (my emphasis).  According to Nye, this suspension of ordinary modes of conduct does indeed require some special socio-psychological explanation.

As an exemplary episode in the history of science, the N-ray program would continue to attract attention, particularly as the sociology of knowledge grew in importance.  Notably, Malcolm Ashmore would revisit Wood’s role in the N-ray program’s decline in “The Theatre of the Blind: Starring a Promethean Prankster, a Phoney Phenomenon, a Prism, a Pocket, and a Piece of Wood” Social Studies of Science 23 (1993): 67-106, in which he undertook a professedly radical extension the “social studies of science” tradition to bring “justice” (this is a Latour reference) to the case of N-rays.  The methodological argument is that a just analysis is, following Bloor, a properly  “symmetrical” one, which, according to Ashmore, is successfully achieved by screwing up one’s mind to the point that episodes appear differently, even if this means actually inverting rather than resolving prior asymmetries.  In this case an “even-handed” treatment “largely fails to go far enough in its efforts to disturb the cognitive consensus” (70).  Instead, Ashmore takes on the role of “relativist as defence lawyer” (fn. 26).

Ashmore goes on to show that it is indeed possible to think of the episode in a different light, provided you pick your historical evidence extremely selectively, are willing to accept that Wood was an out-and-out liar,  and systematically misrepresent the sociology and epistemological standards of scientific communities, and the instrumental functions of history therein.  The exercise sets up Wood’s story as a sort of crucial experiment in the debunking of the N-rays and then applying a “sceptical” analysis to the story’s ability to function as a definitive means of achieving a thorough debunking.  This essentially means analyzing the narrative structure in Wood’s story, then poking holes in its consistency, mainly by noting discrepancies in the 1904 and 1941 versions of it, and finally using the resulting blows to Wood’s credibility to assert that maybe Wood made the whole thing up.

My feeling is that the paper misconstrues the instrumental uses of history, taking Wood’s story to function as a proper justification of any refusal to revisit the possible existence of N-rays.  I would argue that the instrumental function of the story, the reason it is compelling, is that it conveys a very general lesson or principle about possible sources of illegitimacy in scientific work.  In the face of any serious pressure to reopen the N-ray case specifically in the face of accusations about Wood’s honesty, one would be obliged to revisit the story in more detail, wherein one would encounter the full scale of the program’s difficulties and the criticisms of those difficulties.  A fuller examination of the arguments and counter-arguments as presented at the time would lead to a fuller appreciation that what Ashmore (and Nye) present as a reasonably legitimate research program (Ashmore goes further: it is “proper science, correct procedure, [and] positive results”, 90) was not dismissed cavalierly on the basis of a single incidence of debunking.

Beyond the basic point that you can deny anything if you restrict and manipulate your argumentation in the proper ways, I’m not sure what Ashmore’s paper is supposed to demonstrate.  Beyond this disappointment, though, Ashmore compounds the problems with the paper by claiming he hoped it would “provoke some reassessment” of the “socially achieved” dismissal of such research programs as cold fusion and infinite dilution (70).  That was at least as reckless as any of the claims made in the course of N-ray research.



1. Jed Rothwell - January 19, 2010

I assume you are saying the dismissal of cold fusion was socially reckless. It was indeed. As Schwinger said, regarding the rejection of his cold fusion papers:

“The pressure for conformity is enormous. I have experienced it in editors’ rejection of submitted papers, based on venomous criticism of anonymous referees. The replacement of impartial reviewing by censorship will be the death of science.”

However this rejection had nothing to do with scientific content of cold fusion research. After 1989 hundreds of mainstream, peer-reviewed papers showed that “there are undoubtedly overwhelming indications that nuclear processes take place in metal alloys” (Gerischer). The rejection was caused by academic politics alone.

For much more about cold fusion, including about a thousand papers, see:


2. Will Thomas - January 22, 2010

My point was that I don’t think Ashmore’s paper had much to say about the merits or demerits of the academic process with respect to N-rays, and had still less to say about the case’s implications for more contemporary public controversies. These are numerous and fascinating, often involving some very elite figures, Linus Pauling’s support of vitamin c as a cancer treatment, for example.

3. Jed Rothwell - January 22, 2010

You are right; there are many fascinating controversies, and it is easy to draw the wrong conclusions from them. There are more controversies than we realize because they are sometimes swept under the rug after being resolved.

Polywater was more interesting and complex than people realize. I recommend the book Felix Franks, “Polywater,” (MIT Press, 1981). One researcher told Franks she had a wonderful time working on polywater, and she considers this work the high point of her career, even though her results were all negative and polywater later became disreputable. Good for her!

Of course there are many examples of breakthroughs there were considered highly controversial when they were made, which everyone now takes for granted today, and few remember were controversial. The laser is good example. See Charles H. Townes, “How the Laser Happened — Adventures of a scientist” (Oxford University press, 1999)

4. Will Thomas - January 22, 2010

Or indeed plate tectonics, though it’s worth noting that Naomi Oreskes has shown how the degree and unanimity of opposition to that program has often been exaggerated to exemplify the against-the-odds quality of that narrative. On the other hand, some cases were quite noxious, as in transistor co-inventor William Shockley’s arguments about race. Oreskes and Erik Conway have recently done very good research discussing (very very high level physicists’) Fred Seitz’s and William Nierenberg’s 1980s-era opposition to global warming. Nierenberg’s opposition was from an authoritative perch on a National Academy of Sciences committee. Seitz’s contrarian attitude also led him to consult for the RJR Reynolds Tobacco company. Seitz and Nierenberg are both dead, but others, such as Princeton’s William Happer continue on in their stead.

So, here we can see a full range of possible instrumental uses of historical controversies, often employing many of the same themes of academic dogmatism, academic authority, partisan interest, brave contrarianism, stubborn contrarianism, noxious contrarianism, etc. Those wishing to take some intelligent stand on any issue using these postures as a guide will be ill-served by them, and will be forced to explore the terms of the various assertions and objections more deeply, conscientiously, and using a much sharper toolkit.

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