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Schaffer Turns to Practice April 7, 2009

Posted by Will Thomas in Schaffer Oeuvre.
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The two articles we are looking at today are among the best-known works of Simon Schaffer:

(1) “Astronomers Mark Time: Discipline and the Personal Equation,” Science in Context 2 (1988): 115-145.

(2) “Glass Works: Newton’s Prisms and the Uses of Experiment,” in The Uses of Experiment: Studies in the Natural Sciences (1989), edited by David Gooding, Trevor Pinch, and Simon Schaffer.

19th-century glass factory

19th-century glass factory

The articles stand at an important turning point in Schaffer’s oeuvre, and their style should be very familiar to history of science professionals working in the last 20 years, because both depart from Schaffer’s early concern with the construction of systems of ideas, and both put a specific epistemic practice under the microscope, in this case: striving for precision in observation, and replicating experimental results.  At the time, though, these kinds of studies were reasonably novel.  The Uses of Experiment volume, in particular, was an important follow-up to Leviathan and the Air Pump in the turn toward making instruments and experimental practice a central concern in developing an historicized understanding of the nature of scientific work, as well as in developing a history of science less dominated by the development of theoretical knowledge and philosophical accounts of scientific progress (see also, for example, Peter Galison’s How Experiments End, 1987).

Both pieces can be understood as deploying sociologist Harry Collins’ work on the social problems of “calibration” and the acceptance of standard kinds of observations and apparatus in the fostering of experimental consent (see Collins’ Changing Order: Replication and Induction in Scientific Practice, 1985).  Since the results of one experiment can only be judged as valid by comparison with the results of another experiment (i.e., the instrument is calibrated), one must always refer implicitly back to the credibility accorded to some prior experiment—a situation Collins refers to as the “experimenter’s regress”, and that is fraught with problems of authority.

Let’s go in the chronological order of history, rather than the works.

Isaac Newton’s (1643-1727) initial experiments with prisms and light from the 1660s (well prior to his writing of the Principia) found that sunlight could be decomposed using glass prisms into constituent “primitive” rays of different colors, which could not be further divided.  Newton took his experiment to be a “crucial” demonstration of his natural philosophical argument concerning the differing “refrangibilities” and (sometimes) the immutability of colors.

Newton assumed that his experiment constituted a definitive demonstration of his claims, but, following his publication of his work in 1672,  others were not so easily convinced by his generic descriptions of the crucial experiment.  Robert Hooke denied that the experiment was definitive, and supposed his “hundreds” of trials could support his own vibration theory of light: “it is not that, which he soe calls, will doe the turne, for the same phaenomenon will be salved by my hypothesis as well as by his.”  Jesuit critics likewise disputed Newton’s experiments, indicating that their own experiments did not accord with his: as far as they could see, colors were not differently refrangible, and could be further divided.

The attacks on Newton’s theories caused Newton to elaborate on his specific experimental procedures, to criticize the quality of glass used by his opponents, to change what he claimed the experiment decisively demonstrated, and, by 1678, his frustration motivated him to withdraw from the disputes altogether.  Later, in the 18th century, the validity of the experiment would be taken for granted by Newton’s supporters, and would continue to serve as a point of attack for his opponents.

The history of Newton’s experiments and the disputes surrounding them had previously been well-covered in works such as Richard Westfall’s Newton biography.  Schaffer’s piece demonstrated how and why acceptance or denial of the specific experimental set-up became an ongoing pressure point in the anatomy of disputes over knowledge and method.  It can be easily read in tandem with Schaffer’s 1986 piece on the construction of histories of moments of discovery at the time of the turn to disciplined science.

Both works should be read alongside “Astronomers Mark Time”, which revisits the validity of the observational set-up in the context of the carefully refined practices of 19th-century astronomy.  By the early decades of the 19th century, astronomical work revolved around making very precise observations of the location of celestial objects at very precise moments of time, yielding data that could be used to construct accurate maps, and to calculate the paths of objects in the solar system.

In fact, the practice had become so precise that, to coordinate the results between observatories, it was necessary to develop elaborate means of making sure that all observatories and all observatory staff members made standard and consistent measurements (the “disciplining” of professional astronomy).  In astronomy, the invention of specialized observing equipment, precise time-keeping and recording devices, hiring and training dedicated and skilled observers, and recording differences in individual reaction times—the “personal equation” associated with Friedrich Bessel (1784-1846)—all competed as means of creating a new standard for astronomical observation.

Schaffer emphasizes that developing new means to create standard practices in astronomy, not only in observation but in calculation, were at the heart of international competition and the development of a distinctly professional (versus amateur) culture in astronomy.  This entailed a mishmash of efforts to discipline work, including the personal equation, and even to discipline discipline, as in British Astronomer Royal George Biddel Airy’s efforts to chart changes in an individual’s personal equation over time.

Beginning in the 1860s, quantitative psychologists, most notably Wilhelm Wundt, adopted the personal equation as part of their project to create a new experimental science of the mind.  However, the historical tradition developed by psychologists took it that astronomical observers discovered psychological phenomena as they ran up against the boundaries of their own discipline—a point of view expressed, for example, by experimental psychologist Edwin Boring in the 1960s.  Schaffer takes pains to emphasize contrary to this story that the personal equation was part and parcel of the disciplinary ambitions of astronomy, not a result of discovering its limits leading to the need for extra-disciplinary rescue.

Both “Glass Works” and “Astronomers Mark Time” traffic in the relationship between the experimental or observational apparatus, the creation of standard practices, the building of bodies of knowledge and scientific disciplines, and the assembly of prior histories of discovery—the first in the age of natural philosophy, the second in the age of precision technology and disciplined science.  Both stories represent canonical moments in the history of science revisited with a sociologically informed emphasis on the role of certain kinds of practices and with the politics of earlier history-building firmly in mind.  Within five years, these argumentative features would become constitutive of work in the history of science discipline.

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1. Michael Bycroft - March 11, 2011

This is somewhat beside the point of the post, but I think “Glass Works” should be read alongside the response, A. E Shapiro, “The Gradual Acceptance of Newton’s Theory of Light and Color, 1672-1727,” Perspectives on Science 4 (1996): 59–140.

From the abstract of Shapiro’s paper:

“Simon Schaffer has published a constructivist analysis of the acceptance of Newton’s theory of color that focuses on Newton’s experiments, the continual controversies over them, and his power and authority. In this article, I show that Schaffer’s account does not agree with the historical evidence.”

The tussle about historical method going on in the background in Shapiro’s article is rarely explicit in the article but comes through in passages like this:

“Underlying [past approaches to Newton’s optical works] is the implicit assumption that Newton’s theory is obviously true and that opposition had to come from conservatives, reactionaries, and incompetents who were unable to come to grips with the new. Today we are more sophisticated and recognize that only occasionally is a theory and its evidence judged to be so obviously true that the scientific community need not be persuaded to accept it, and so we study rhetoric, experimental replication, and “negotiations.”

On my reading, one interesting move from Shapiro in this article is to accuse Schaffer of failing to meet his (Schaffer’s) own standards ie. the standard of getting a less present-centred view of the optics controversies. After noting (in the quoted passage) the dangers of projecting our present-day scientific beliefs on past actors, he goes on to accuse Schaffer of precisely that ie. of projecting present-day notions of scientific practice onto past actors:

“Applying the model of modern experimental science to Newton’s experiments puts them in an alien context and burdens them with undue complexity…The simplest and most fundamental experiment in Newton’s entire repertory, that of forming a spectrum with a single prism, succeeds so readily that it quickly became uncontested.”

If Shapiro is right about all this then he has scored a triple victory. If he is right, then not only does he beat Schaffer at the present-centredness game, he also beats him at the scientific practice game (Schaffer has the wrong idea about Newton’s practice), *and* he shows that the practice game is not the most important one after all (questions of theory and interpretation, not questions of instruments and materials, were the real sticking points for Newton’s theory of light and colour).

I don’t know whether Shapiro is right about the details of the Newton case. But it does seem odd that the following are (as far as I can tell) both part of HoS orthodoxy.
A) it *is not* OK to think (say) of Newton’s Opticks as an early version of (say) Thomas Young’s optical experiments (since that would confuse science with natural philosophy, and since Newton’s and Young’s enterprises and therefore their intentions were completely different, etc.).
B) it *is* OK to think of just about any experimental episode in the history of science as an earlier version of gravity wave experiments (which is effectively what one does when one draws on Collin’s notion of an experimenter’s regress, since he develops that notion using 20thC experiments on topics like gravity waves).

A cynic might conclude that the maxim “don’t think of past science as an early version of present science” has sometimes been applied selectively to support certain sorts of history of science, and cast doubt on other sorts, when in fact the maxim is neutral with respect to those different sorts of history of science. I think that is too cynical to be true, but sometimes it seems “operationally true” ie. it is sometimes an economical description of the facts of historian’s uses of the maxim in the last few decades.

My hunch is that other recent historiographical maxims are sometimes applied in a similar way eg. the maxim “don’t listen to what the scientist says about the aims of his projects, but try to adopt a neutral, anthropological stance; take a close look at what they *do*.” If this were applied consistently to, say, the Principia, we would ignore the fact that Newton states his project as “natural philosophy” in the title of the book and just focus on the technical contents of the book. Yet there is one strand of historiography which says that the sensitive historian should do precisely the opposite. The historians/sociologists who make a fuss about “neutral stance” maxim or it’s opposite also tend to come up with either a less-than-glowing view about science or a less-than-glowing view about pre-1980s historians of science. Since the maxims contradict eachother (or near enough) one wonders whether the maxims are chosen to suit the less-that-glowing view about science rather than the other way around.

On the other hand, I think the work done by the historians/sociologists who make a fuss about these maxims is in many ways fabulous and innovative. It would be a tough task to work out how much their value is due to rigorous application of historiographical maxims and how much due to something else.

Perhaps the “something else” is just the two rarely-stated maxims: “look for ways in which science and/or past history of science is less-than-glowing.” Funnily enough, I can see why the determined application of these maxims could have resulted in lots of fabulous and innovative work in both history and sociology of science — simply because so much history/sociology of science up to about 1960 had been a result of the determined application of the opposite pair of maxims. Since the truth must lie somewhere between the extremes of these two pairs of maxims, the determined application of the “less-than-glowing” maxims was bound to pick up on things that the determined application of the opposite maxims had neglected. This is mostly speculation, but I’ld be interested to know if anyone else shares my hunch (and apologies if my hunch offends anyone).


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