The Heuristics of War: Scientific Method and the Founders of Operations Research

Jun 19, 04:38 AM

Current Headlines: By Thomas, William

Abstract. This paper explores the relationship between operations research (OR) as practised during the Second World War and the claims of many of its proponents that it constituted an application of scientific method. It begins with an examination of the pre-war work of two of the most notable leaders in wartime OR, the British experimental physicist Patrick Blackett and the American theoretical physicist Philip Morse. Despite differences in their scientific work, each saw science as an essentially creative act relying on the skill and judgement of the individual scientist in the deployment of rational methods for the development of legitimate conclusions. When scientists began to study military operations, their investigations were defined by the technically sophisticated heuristic practices already surrounding military planning. They did not seek to replace these practices with their own rational methods. Rather, they became scholars of the military's methods and adapted their pre-war experience by shifting their self-disciplined attitude to their own work to bodies of military knowledge. Thus scientists learned so well to navigate an alien heuristic system that investigations they conducted within it took on the characteristics that they judged defined scientific work.

During the Second World War the British and American militaries contracted outside scientists to study military operations in order to recommend improvements to senior officers. These scientists worked in teams known as operational research groups within the British services, and as operations research or operations analysis groups in the United States. It was not long before these names (here referred to collectively as OR) began to signify not only scientists' location within the military hierarchy closer to planning operations than to equipment procurement, but also a particular sort of activity with its own methodology. Identification as an activity allowed OR to escape its original wartime and military contexts and continue to exist until the present by becoming a profession and, according to many of its proponents, a science unto itself. The exact contents of its methodology, however, have never been clearly defined. Some of the most vague and perhaps therefore most enduring definitions of OR have referred to it simply as the deployment of scientific methods in the analysis of managed activities.1 The purpose of this paper is to gain a clearer understanding of the relationship between OR as an activity performed by scientists and its ultimate redefinition as a scientific activity during the Second World War.

Heretofore historians of OR have not seen fit to explore this issue in any great depth because of a historiographical preoccupation with the significance of scientists' involvement in military decision-making.2 Whether the primary interest has been the deployment of scientific methodologies in new sorts of problems or else the cachet of scientific knowledge as key to scientists' entry into new arenas of authority, a strong theme in the historiography is that 'scientific' methodology was a foreign entity introduced into the military by outsiders. This notion, originally present in histories written by scientists anxious to show how their work served as a corrective to inadequacies in military thinking, has echoed throughout more recent histories. Andy Pickering, for instance, views OR as a 'polyp' injecting science into the military sphere of activities, thus forming what he calls a postmodern hybrid 'cyborg'.3 Erik Rau has described OR as a successful negotiation between scientists anxious to 'colonize' military affairs and military patrons anxious to benefit from scientific methodology.4

David Edgerton actively resists the tendency to view science and the military as exclusive realms, rightly pointing out that the military boasted a thriving culture of technological specialists. He castigates early British OR proponents and other scientific intellectuals as 'anti-historians' for portraying the military as 'unscientific' in their accounts of the war, suggesting that they harboured contempt for military methods.5 The wartime 'dean' of OR, Patrick Blackett, figures prominently, and is quoted to the effect that many military decisions were often made based on 'gusts of emotion'. But Blackett's observation that military conclusions proved robust nine times out of ten remains unreported.6 British scientists' post-war rhetoric was indeed often icy towards that country's military and political leadership. Yet it should still be understood at the outset that wartime relations between the military and OR scientists were characterized by respect for each others' methods and abilities.7

My own approach to OR places an understanding of its methodology and heuristics before the question of its importance to the scientific-political or scientific-military relationship. While scientists' pre-war scientific work was important to their wartime contributions, following Edgerton I argue that these contributions should not be seen as the Promethean introduction of scientific methods into an otherwise non-scientific or irrational context. Rather, I will show how they were rooted in the creative yet disciplined skills that were honed in the construction and defence of scientists' own scientific arguments, and adapted to scrutinize and augment existing military heuristic practices. Although these skills were certainly associated with science, they were not unique to scientific activity.

I demonstrate my argument by examining the relationship between wartime OR work and the pre-war practices of two of OR's most notable early practitioners, the experimental physicist Blackett, and American theoretical physicist Philip Morse. I choose these figures because they are well known to historians of twentieth- century physics and also because they were well-respected leaders of groups of OR scientists, charged with ensuring the scientific quality of studies done under their supervision. Because they did not perform the bulk of actual work done within their groups and because I do not believe they had any notable influence on the shape of OR methodology, it is important to bear in mind that their specific skill sets and biographical experiences are not of direct concern.8 It is not even of major concern that both were physicists. It would also be possible to focus on a non-physicist OR administrator such as the American chemist George Kimball or the British embryologist and geneticist Conrad Hal Waddington, both of whom shared Blackett's and Morse's attitudes to OR.9 Because my object here is not to isolate OR methodology as a product of individual agency, but to show it as the translation of a trained ability to scrutinize and augment bodies of knowledge into foreign heuristic systems, and because Blackett's and Morse's groups were universally considered quite successful in this respect, their activities should suit this analysis well.

Thus when I examine Blackett's pre-war experimental work and Morse's theoretical work, my primary interest lies in how they felt legitimate scientific arguments could be constructed. The first section shows how the legitimacy of Blackett's cloud chamber work depended on obtaining a reliable narrative understanding of the processes by which his chamber produced all manner of relevant, irrelevant and confusing phenomena, thereby allowing him to devise reliable methods of extracting useful information from it. He was extremely sensitive to the many ways his finicky chamber might fool the careless scientist into arriving at an illegitimate result. The second section demonstrates that Morse's work was also dependent upon narrative understanding of phenomena, but as a theoretician he concentrated on using mathematics to formulate rigorous mathematical representations of experimental phenomena. Morse believed that such representations, if used judiciously, could help the scientist infer knowledge about closely related phenomena or draw creative and instructive analogies between topics as diverse as quantum mechanics, acoustics and mechanical engineering.

Moving on to wartime OR work, the argument of the third section makes no concerted attempt to connect specific practices either with Blackett's or with Morse's prewar practices. Rather, it indicates how OR activities earned the descriptor 'scientific' by taking on the familiarity of the pre-war heuristic practices that scientists controlled entirely and knew intuitively. These included the design, construction and use of an apparatus; the interpretation of data; and the formulation of theories. To become comfortable with military heuristic practices that were beyond their immediate control, scientists became scholars of them. They learnt how field personnel established narratives of operations, how technical experts deployed equipment and interpreted data brought back from the field and, above all, how military executives consolidated this information into an acceptably coherent body of knowledge. By working actively with these military figures, these scientists became specialists at critiquing their practices: identifying topics for scrutiny, designing operational tests, interpreting data, devising useful measures and checking cursory reasoning against statistical argument in order to improve the effectiveness of military operations. Of course, none of these activities depended on the presence of OR scientists. In fact they occurred constantly in their absence. Nevertheless the rapid spread of OR groups in both the British and the American militaries and their continued existence today should indicate that the introduction of scientifically trained OR personnel as critical specialists was widely recognized as a valuable addition to military planning practices. The question of whether or not OR methods were themselves scientific - insofar as they can be meaningfully distinguished from traditional military methods - should ultimately seem beside the point. Patrick Blackett and the methodology of cloud chambers

Mary Jo Nye's recent biography of Patrick Blackett includes some account of his approach to science, arguing convincingly that his work on OR and his Nobel Prizewinning research with cloud chambers were united by a commitment to a phenomenological view of science. He was able to advance studies in the physics of elementary particles and cosmic rays based upon experimental observation before theory generated any expectations of what should be found. Throughout the 1930s and beyond, this approach lent itself well to the study of a host of unexpected new particles. Similarly, during the war, he and other scientists often arrived at expedient analyses of wartime operations that, if lacking in ontological conclusiveness, were at least well argued and therefore acceptable to military executives, thereby leading to improved tactics and procedures. With respect to Blackett's day-to-day scientific practice, Nye briefly describes his commitment to voluminous data collection and his predilection for the continuous adaptation of his scientific apparatus: 'The integrity of the results rested in the maximum input of data in order to refine and eliminate alternative causal hypotheses. "[degrees] But in order to gain a better appreciation of the connection between Blackett's pre-war and wartime work it is important to take a more detailed look at his working methodology.

In peace and war Blackett insisted upon an interpretation of data based on the formulation of a clear narrative understanding of the mechanisms that produced it, a rough but revealing explanatory chain of causal events combined with a sceptical attitude towards the data's basic validity. The process was akin to the plot of a detective novel, with constant interplay between suspicion and confirmation of the steps of the crime. In the cosmic ray physics of the early 1930s, an untrained observer could not simply look at a cloud chamber photograph and casually identify an often inchoate trail of mist with a particular kind of particle, especially if that particle's existence was barely established, as was then the case with the positron. One had to gather evidence with great care in order positively to identify the perpetrator by the ionized footprints left as it crossed the chamber.11

Even if the reliable operation of a cloud chamber were taken for granted, a far from benign assumption, the simple separation of the wheat from the chaff in the yielded data required a studied expertise. Figure 1 is a usable photograph of a cloud chamber expansion. This chaotic image, Blackett informs us, includes several positrons 'plainly bent to the right'. Among the irrelevant phenomena, he tentatively identifies the large white blob as a contaminating alpha particle with no relation to other reactions. The large swathe of white on the right is not vapour at all, but a reflection from the photographic flash.12 Appropriate candidates for analysis were picked out from these other phenomena. Then they had to be measured. Through his own knowledge of the apparatus, Blackett was fully conscious of potential metrical errors and their sources. It was important to keep in mind not just relevant events, but all possible events that could happen within the actual chamber rather than an idealized version of it. For instance, he noted it was best to measure the arc by projecting trails onto model arcs 'due to any departure of the track from a true circle such as might be caused by small nuclear deflections. Experience has shown that such deflections are difficult to recognize and may cause serious error'.13 Other distortions might be caused by fluctuations in the gas that filled the chamber.14 If a particle were moving so quickly that it did not bend appreciably in the magnetic field generated by a solenoid surrounding the chamber, or its path were distorted by the glass window of the chamber, the event could not be conclusively measured at all.15

Identification of a particle by its measured trail was another difficult task, especially when discussing novel particles such as the positron. The charge, energy and velocity of particles could generally be identified by observing, respectively, the direction, tightness and thickness (a measure of ionization) of the arc traced through the magnetic field. Untested assumptions could lead to error. For instance, because a positron only differed from an electron in the sign of its charge, it was therefore most important to know whether a particle was crossing the chamber upwards or downwards. Most cosmic rays travelled downwards. Suspected positrons were often part of a 'shower' of particles apparently originating in the solenoid surrounding the chamber. Such evidence could yield the probability, 'but no certainty', according to Blackett, that particles were really moving in the suspected direction. He felt it was unreasonable to assume that in aggregate all positron suspects were merely deviants. More satisfyingly, though, the direction of individual particles could be confirmed by inserting a metal block into the chamber, thereby robbing incident particles of energy and tightening their arcs as they emerged on the other side. In this case the possibility of a particle having gained energy as it passed through the block was deemed so low as to be negligible.16 Once individual particles were measured and identified, Blackett preferred to repeat the process a number of times to justify his conclusions, even though theoretical claims (in the positron's case Paul Dirac's pair-production theory) might presuppose his experimental results. As he, Giuseppe Occhialini and James Chadwick wrote in their paper elaborating on Carl Anderson's positron discovery, 'The experiments were ... continued until about 4000 tracks of electrons and about 400 tracks of positrons had been obtained, giving a body of evidence sufficient to justify quantitative conclusions.'17

As Nye points out, Blackett was already quite conscious in a 1933 essay of how the interpretative process described here was predicated on the development of a close personal knowledge of the scientific apparatus, forged over the weeks, months and years spent building, modifying, maintaining and using it.18 Diligent work with the instrument could not be substituted by diligent study of publications. But publications might aid others in fostering their own critical skills with a similar chamber set-up. This is doubtless one reason why Blackett provided detailed explanations of his apparatus and methods in his own articles. Peter Galison has also directed our attention to cloud chamber 'atlases' that were later printed to familiarize scientists with typical cloud chamber trails and distortion effects-to train their scientific eye. According to Blackett, in the foreword he wrote to one such atlas in 1952, 'to acquire skill in interpretation, a preliminary study must be made of many examples of photographs of the different kinds of known events. Only when all known types of event can be recognized will the hitherto unknown be detected.'19

We can thus gain a greater appreciation of what Blackett had in mind when he declared in 1960 that

the actual operations of modern war are so complicated and change so fast that the traditional training of the serving officers and personnel is inadequate. In fact, many of the operational problems which arise when new equipment comes into service require for their solution the aptitudes of the scientific research worker: for he is trained to apply scientific methods to elucidate hitherto unknown and complex phenomena.20

For Blackett, the ability to reveal the 'hitherto unknown' in cloud chambers and in warfare was in both cases rooted in study of how interpretations of data were derived from observed phenomena and how the mechanisms under study produced those phenomena. It was his responsibility to be aware of processes that could produce both relevant and misleading data and to be carefully aware of the possible existence of unexpected processes even within a machine he himself had designed and built. Before examining how Blackett adapted these principles to his wartime work, however, it is useful to survey a different but complementary conception of the scientific method.

Philip Morse and the methodology of physical theory

Philip Morse was a theoretical physicist trained within the American university system of the 1920s. In Morse's case, there was an emphasis not on the intelligible reconstruction of events through a rigorous examination of physical evidence, but rather on the formulation of mathematical models that satisfactorily accorded with the known mechanics of observed phenomena. For him and nearly all American theorists of the pre-war era, the barrier between mathematical theory and the sort of experimental physics practised by Blackett was quite permeable. In his youth Morse worked in a radio and electronic parts store started by his friends, before receiving his bachelor's degree from the case School of Applied Science.21 He later described case as 'a training school for engineers and applied scientists, in the American traditioacticality'.22 While at Princeton for graduate training, he worked one summer assisting in a series of experiments on gaseous conduction at the University of Michigan for the Detroit Edison Company, and the next summer carried out theoretical work in an office at Bell Laboratories in New York.23 With Edward Condon he co- authored the first American textbook on quantum mechanics, which emphasized the interplay between experimental result and explanatory theory.24 Once he gained a position at MIT he found that his office in the institute's physics department was 'just around the corner' from the electrical engineering department. The two departments had been one and the same until 1902.25 Despite the close links of Morse and other American theorists with experimental physics, they maintained a healthy respect for the more philosophically oriented theorists of the European continent then dominating progress in the field. Pilgrimages to Europe to learn from the masters there were common. Morse was no exception. He spent the first half of the 1930- 1 academic year studying under Arnold Sommerfeld in Munich and the second half at Cambridge, where he became acquainted with Blackett.26 When he arrived at MIT in the spring of 1931 he was part of an effort by the new president, Karl Compton, to turn the engineering-dominated school into a centre for original scientific research. Compton contested what he saw as the prevailing wisdom that 'pure science could be learned only in Europe'.27 Not long after arriving, Morse also began teaching a course on acoustics and soon became an expert in that field in his own right.

In Morse's thinking there was no set heuristic relationship between pure and applied work, nor between the experimental and the theoretical. Mathematical techniques required for understanding the quantum mechanics of subatomic particles, for instance, could be turned around and applied to the propagation of sound waves in a room with walls of a certain material,28 just as experimental phenomena could provide rich fodder for new quantum theories. For Morse theory was not an independent construct, wherein mathematics predicted new fundamental physical principles, the approach that had produced many of the recent glories of quantum mechanics. Rather, Morse's theoretical methods were tempered by a close familiarity with experimental investigations. His attitude towards theory development is rather well illustrated in a paper he co-wrote with Harry Schlechter and R. H. Boden, based upon work done primarily by Boden at the Sloan Automotive Laboratory at MIT on behalf of the National Advisory Committee for Aeronautics.29 The paper studies the behaviour of gas pressure waves caused by a combustion engine's operation. These pressure waves resulted in a direct, albeit complicated, correlation between the length of the engine's intake pipe, the pipe's inherent resonance frequency and the performance of the engine.

Morse acquired a thorough narrative understanding of the functioning of the engine from his collaborators in the automotive laboratory so as to form a useful theoretical description of the correlation. The crux of the problem was that the generation of large standing waves within the intake pipe resulted in a situation wherein

if the portion of the cycle when the intake valve is just closing happens to coincide with the time when the pressure is less than average, then the waves will reduce the power output; hut if the valve is just closing when the pressure is greater than atmospheric, then the waves will have a supercharging effect and will produce an increase in power.30

But this narrative, the production of which should be familiar from Blackett's work, was only the point where the theoretician's work began. Morse fitted mathematical functions to measurements of the material characteristics of the engine and the motions of its parts and thus the gas moving within it. However, these functions had to balance utility with ontological precision. Theorists had to make their own judgements as to when to employ approximation without losing vital information. Morse notes at one point that it is possible to derive a simultaneous solution both for the displacement of air through the valve intake into the cylinder and for the pressure at the valve intake due to waves in the intake pipe, but that 'this solution is exceedingly complicated and impractical for general use'. It does not appear in the paper. He continues,

A little consideration of the magnitudes of the quantities involved, together with a knowledge of the experimental results, will show the possibility of an approximate solution which will he much more tractable than the exact solution, and which will he accurate enough for our purposes.31

Ultimately Morse's mathematical analysis arrives at a formulation yielding a number of distinct optimal intake pipe lengths that result in the supercharging effect of a 15 to 20 per cent increase in engine performance. The experimental work of the automotive laboratory could produce the optimal lengths as well, but a deeper, even if not perfect, understanding of just how these lengths resulted in enhanced engine performance could provide scientists and engineers with an instructive example that might offer approaches to analogous problems. A combustion engine with a different configuration from the ones studied would only be the most immediate application.

Even though it involved a greater degree of mathematical formality than that of Blackett and was less concerned with the intricacies of data interpretation, Morse's approach was similar in its reliance on an interplay between speculation and confirmation of representations of processes. The manufacture of generalized knowledge was always the province of the theoretician, but in America it was seldom the definitive goal of scientific work. Rather, experiment and theory were complements, much more so, at any rate, than on the European continent or even, perhaps, in Britain. Formal theoretical knowledge provided a firm foundation for the application of knowledge between analogous physical systems, but such foundations did not present themselves spontaneously. Scientists were expected to exercise both discipline and creativity in identifying legitimate analogies between such systems. It was through this approach that Philip Morse was able to defy disciplinary boundaries and move freely between quantum mechanics, acoustic theory, the performance of combustion engines and, ultimately, the dynamics of war.

Science and military heuristics

At a little after half past one in the afternoon of 22 March 1943, Second Lieutenant H. C. Jackson of the United States Army Air Forces, copilot of a B-24 bomber with a non-operational radar on anti-submarine patrol eighty miles off the west coast of Africa, spotted a wake five miles away on his starboard beam. The pilot, First Eieutenant W. L. Sanford, turned to investigate. The vessel was quickly identified as a German U-boat. Sanford guided the plane into a nearby cloud on the approach and dived into attack two minutes after first sighting. The U-boat, apparently taken by surprise, made no attempt to submerge even as a man on deck attempted to arm an antiaircraft gun. The plane dropped four depth charges and a little over a minute later the U-boat was sunk. Nine survivors were spotted clinging to a cylindrical object left floating on the surface. The bomber dropped a life raft and departed the scene half an hour later. Much to the delight of the analysts at the Navy's Anti-Submarine Warfare (ASW) Unit, the crew, in addition to sinking the U-boat, photographed the entire scene in exquisite detail.32

Figure 2 is one of a number of images from what was labelled incident 2737. Between the narrative of the incident provided by the bomber's crew and analysis of the photographs brought back, the attack was dissected. The U-boai pictured is of the 740-ton variety, revised from an initial 500-ton estimate on the basis of 'subsequent interrogation and photographic evidence' that identified the larger type's characteristic features. According to crew reports, the attack was made at an altitude of two hundred feet at a speed of two hundred miles per hour. The large splashes seen in this photograph are from Mk 29 depth charges set to a depth of twenty-five feet spaced at sixty feet entering the water. It was determined that they fell 1.30, seventy and ten feet short of, and fifty feet beyond, the U-boat. The small splash is from a machine gun bullet fired by the tail gunner. The attack was unusual in that U-boats typically would attempt to crash dive to evade attack. The good fortune of attacking a surfaced U-boat was accomplished, according to the crew, by the unexpectedness of attacking so far from base, by the lack of radar use (which might have been detected), by the use of the sun and cloud cover to hide the plane's approach, as well as by the use of the 'British Coastal Command Mediterranean Type' camouflage scheme on the plane. The incident also raised new questions for future discussion. It was the third report of the unknown cylindrical object and the second report noting the appearance of a brown paint- like liquid amid the usual oil patch from damaged and sunken U- boats.33

Incident 2737 was, of course, very nearly an ideal attack. The bomber's unit commander showered praise on the crew for their teamwork and the quality of the evidence they brought back, mentioning both the 'straddle' of the submarine with depth charges shown in Figure 2, and pictures taken of the floating survivors. The squadron commander remarked, 'Having evaluated quite some number of submarine attacks in the year and six months of Anti-Submarine patrol, this is the first of which I have felt so sure of the total destruction of the U/B [U-boat].' The Atlantic Fleet ASW officer even wrote to the Commander-in-Chief of the Fleet, 'It is possible that these photographs would be good propaganda if and when propaganda is needed.'34 Other attacks, of course, were not typically carried out so well or under such ideal conditions and very few produced such good pictures by which to corroborate crew reports. ASW analysts often pored over crew narratives and confused photographs of splashes, watery explosions, swirls left behind by submerged U-boats, oil slicks and surface debris, attempting to ascertain the likelihood of damage or destruction. They sometimes disagreed in their conclusions of whether to congratulate a crew for a job well done or to push for better training. U-boat attack evaluations were often accompanied by report cards on which a variety of analysts provided their own letter grade for the attack. Incident 2737, of course, got all As.35 This process of photographic interpretation recalls Patrick Blackett's cloud chamber work. Figure 2 should suggest an exemplary image of attack-related phenomena that might find its way into a photographic atlas, but the evaluation process described here had little to do with OR teams such as the ones Blackett led. It was usually carried out by military experts. The Columbia University chemist George Kimball, then one of Philip Morse's main assistants at the US Navy's ASW Operations Research Group (ASWORG) did, however, come into possession of the incident 2737 file several months later. He was part of a project to determine whether it would be fruitful to construct an Optical analyser' in order to gather quantitative data from oblique photographs quickly. This was to follow a method proposed by the Royal Air Force Coastal Command OR Section. Kimball pointed out that analysts could more accurately determine bombing error with better quantitative data : the distance between the hull and detonation points, which could be combined with damage estimates to determine the depth charge's range of lethality; actual, as opposed to set, depth charge spacing; U-boat dimensions; the altitude of the attack; and forward travel and dispersion of bombs. Pilots and post-mission evaluators often estimated such figures inaccurately due to the rapid fire conditions of combat and the awkward optical geometry from the view of the bomber.

However, in order for such an analyser to work properly, photographs would need to have precise points of interest (since spray from large depth charge explosions frequently obscured such points), the horizon would need to be visible and a precise dimension such as U-boat length or plane altitude would need to be known, as would the optical axis of the print (ordinarily simple, but impossible in cropped prints), the degree of enlargement of blown-up prints and the focal length of the camera. Kimball added that it would be helpful if photographs were taken at regular intervals and if the plane flew straight and level during the several seconds in which photographs were taken. These were strict requirements, and Kimball concluded that under current conditions it would not be useful to construct an analyser.

He recommended, though, that proper procedures for photographs be established and that their potential value be made better known so that original negatives would not be lost and simple facts such as focal length would be regularly reported. He also recommended that to improve the utility of photographic evidence, fixed, rear- facing, automatically triggered cameras be attached to bombers and that hand-held cameras be used on approach. Kimball pointed specifically to the quality of the hand-held photographs from incident 2737 and the one featured in Figure 2 in particular. He deemed these excellent for analysis, except for the fact that they were unusable because the focal length was unknown and that the photographs in his possession were enlargements of portions of the negatives, thereby rendering the camera axis indeterminable.36 It had been the excellent quality of the photographs that had prompted their cropping and enlargement in the first place.37 There was no reason, however, that practices amenable to successful attack, presentation and measurement could not be established.

There is no straightforward line dividing scientific from non- scientific work in this story. Although military heuristic practices could sometimes appear very different from scientific practices, they were similarly based on logical argumentation and rigorous observational foundations. When military officers planned missions, when they chose combinations of personnel, materiel and tactics, they did so with specific notions of how their choices would affect the outcome. An aspect of military knowledge would generally present itself for scrutiny as a result of a disparity between the performance of an operation and expectations of how it should have proceeded. These expectations were based on knowledge of one's own capabilities as well as those of the enemy. Knowledge of one's own capabilities was based on technical tests of equipment, reports on the efficacy of training exercises and reports of how crew and equipment performed in tandem under combat conditions, all of which could be measured with some precision. Knowledge of the enemy was, of course, less certain, but it was still possible to gather high- quality data from military intelligence through reconnaissance, espionage, signal interception, interrogation of captured enemy personnel, examination of captured equipment, analysis of enemy tactics and so forth.38

Expectations of how one's own plans would actually play out against the enemy could not be directly calculated a priori as a function of one's own and the enemy's capabilities.39 Instead, they were often expressed in terms relating to what we might identify as two heuristic constructs: the ideal mission and the typical mission. The ideal mission was, by definition, a mission that unfolded in close accord with plans informed by knowledge of the capabilities of crews and equipment. Incident 2737 was clearly one such mission. Data from experience and tests suggested that crews could bomb from a certain height and at a certain speed with so much accuracy, and that depth charges of certain explosive power could theoretically rupture the hull of a U-boat from a certain distance. Indeed, in the nearly ideal scenario that unfolded, technical preparations and tactics conspired to catch a U-boat by surprise, attack it by straddling it with depth charges of a certain spacing, and even obtain definitive evidence of its sinking. Although ideal missions did not necessarily occur frequently, it was desirable that some missions unfold ideally to prove the theoretical validity of mission plans.

In typical missions, however, things did not always go according to plan and success was often attenuated or indeterminate. It was found useful to obtain a thorough understanding of individual elements of such missions' narratives because they suggested ways in which combat experience tended to deviate from ideal plans and also metrics by which success could be measured. Typical deviations and measures of success so obtained defined a reasonable outcome for a mission given a set of circumstances. For instance, when planning a bombing operation, one could connect knowledge of capabilities with typical results to form reasonable expectations by saying, 'we are sending so many planes in so many groups flying at such an altitude, equipped with a certain kind of bomb with a radar of certain known capabilities as well as a welltested countermeasure, and, given that we know the enemy has fortified this location heavily, based upon typical outcomes to such missions we can reasonably assume that we will lose a certain number of planes depending on how things play out and expect to accomplish our mission within a given degree of effectiveness.'40 To make an analogy with science, the ideal of a mission and the ways a mission might be reasonably expected to deviate from that ideal formed a military theory.

Then there was actual performance and analysis of a mission. Call this an experiment. Whether or not a mission were successful, the goal of post-mission analysis was to understand how various factors played out during its course in order to make adjustments for future missions. If a mission came short of expectations in some way, it was important to determine if it was because field personnel did not follow the plan, if the plan was faulty or if something unexpected was amiss. Such a determination could be made by comparing actual mission results with an ideal mission using sets of expectations derived from typical missions as a guide. If a plane got lost from a formation, for example, it could be on account of bad flying conditions, failure of the plane's crew to follow procedures, failure of the procedures to lay out an effective means for keeping planes together, failure of the plane's navigational equipment or some combination thereof. Typical experience with problems of these sorts could suggest the appropriate choice from a number of different responses to such a scenario: training crews harder in navigation techniques, training of ground crew on equipment maintenance, revision of tactical doctrine or training methods, calls for improved technology or dismissal of the incident as attributable to a unique set of circumstances or as an expected cost of flying under certain conditions.41

Sometimes analysis would prompt further attention to and study of a subject. The analysts' reports from incident 2737 indicate that the repeated appearance of the floating cylindrical object and the brown liquid caught their attention. If mysteries could catch attention, though, persistent threats to mission success demanded further investigation. If missions consistently failed to meet expectations, if a debate ensued over appropriate tactics or if operations started inexplicably demonstrating peculiar behaviour, mission experts would begin to seek out additional intelligence and data that might offer some illumination. Problems with technological hardware, for instance, might cause inquiries to go back to the technical personnel who were the most familiar with its functioning, or even the original manufacturer, to call for a solution. If enemy behaviour did not match expectations, intelligence personnel might be consulted to see if there were any indication of a change in enemy technology or tactics. If there were some question as to how crew performed under certain conditions, drills could be established to test them. In a war with quickly shifting technologies and tactics, the need for such research arose frequently.42 Military knowledge was distributed between various branches of the military. The liaison between these branches required for operational planning united them into a more-or-less coherent body. If this body of knowledge failed to represent operational expectations accurately, it was subject to scrutiny, investigation and modification. Yet until the establishment of OR groups, there were no military organizations exclusively dedicated to across-the-board scrutiny of the conclusions reached by military planners and the heuristic methods they used to arrive at them.43 Freed from the burden of mission-planning, OR scientists could ask questions that might not have so swiftly become the object of scrutiny in the course of ordinary planning. They could uncover the 'hitherto unknown', as Blackett would say. Then they could design investigations to attempt to answer those questions, activities in which, as scientists, they were seen as especially skilled.44 There are, however, no steadfast rules to be found in the nature of OR investigations that can be used to distinguish them from investigations prompted directly by military planning. Military and OR investigations could be on the same topic and use the same methods. In fact, OR scientists frequently worked in tandem with military specialists.

To illustrate the fluidity of the barrier between military and OR practices, before 1941 the RAF Coastal Command made no effort to study the effect of airplane camouflage on anti-U-boat activities before the Coastal Command OR Section began to study the problem in conjunction with military experts. The original studies were quite superficial, measuring spotting distances of black-painted and white- painted bombers in different weather conditions. Soon, though, OR reports on the camouflage problem began to detail complicated paint schemes, noting the benefits and potential drawbacks of using certain colours and glosses of paint on certain parts of the bomber. There was no special reason why the military could not have independently developed airplane camouflage schemes in its own technical establishments. But at that point it was still unclear whether airplane camouflage was even an important enough factor in ASW operations to refer to the technical experts. Prompted by a wing commander's suggestion, the OR team assigned a man to investigate the issue, eventually leading to the more detailed studies.45 By 1943 airplane ASW camouflage was the province of technical experts with no connection to OR, and, as we can see from the crew report from incident 2737, its impact on mission outcome was recognized by flight crews and mission-planners alike. In this case, OR studies simply served to integrate camouflage into the body of knowledge concerning ASW operations.

Regardless of whether investigations were undertaken in the ordinary course of military planning, or initiated as a result of an OR group's scrutiny, investigation was always a creative act within the context of military heuristics surrounding the mission. In this respect, academic science was not much different from military planning. Blackett's and Morse's pre-war work was defined by their ability to understand the possibilities and limits of their own arguments. For Blackett, the crux of scientific investigation was not in the rational act of constructing cloud chambers, but in understanding the ways they represented natural phenomena in order to find effective heuristic methods for interpreting data. Similarly, for Morse, scientific work was not in the rational act of making mathematical arguments, but in finding appropriate and useful ways of mathematically representing experimental phenomena, even if the equations did not arrive at exact solutions. Scientific activities of these kinds were bound within rational frameworks, such as the logic of mathematics or the known design of an apparatus, but they were not in and of themselves rational. Blackett and Morse creatively cobbled together means of comprehending poorly understood phenomena, whether it was a result of an apparatus's interaction with the unknown, such as cosmic rays, or an unintended consequence of the device's design, such as combustion engine supercharging.

When scientists set out to study the problems of war, they began to work within the rational framework of military planning. Within this new framework, it is not especially constructive to discuss scientists' contribution to it in terms of whether they made military methods 'scientific', because military methods defined so much of the work they did. Scientists lobbied to be included in staff meetings in order to view points of uncertainty and disagreement between military planners before they became hidden beneath official policies. OR reports were often couched in the language of military planners, identifying factors impacting the outcome of the mission given certain combinations of personnel, materiel and tactics, and developing expectations for how those factors should play out given the known evidence. Like planners, OR scientists gathered libraries of military reports in order to collate military knowledge into a comprehensive body of knowledge. Both planners and scientists attempted to improve field reporting methods and to squeeze more information out of existing methods to obtain the most detailed information possible.46

It might be better to say that, within the military, scientists ceased to be scholars of scientific heuristics (that is, scientists) and instead became scholars of military heuristics.47 Their goal was to become sufficiently familiar with the means by which the military obtained knowledge from operations and assembled this knowledge into coherent plans. Then the scientists could judge whether the conclusions underlying military planning followed from the evidence gathered by military heuristic methods, much as they judged whether their own scientific conclusions followed from methods they themselves practised in peacetime. No evidence has been found to suggest that military planners, as a rule, either granted this work of scientists a special cachet or received it with undue suspicion on account of scientists' status as scientists. Rather, OR scientists came to be viewed as fellow experts on operations and the quality of their studies was judged on the merit of the evidence they presented and arguments they employed.48

It should not be surprising, however, that many of the problems identified by OR groups for investigation were concentrated in areas wherein traditional scientific strengths complemented weaknesses in the process of military planning. In particular, the notion of a typical mission used to define operational expectations often lacked rigorous quantitative definitions of typicality and expectation.49 Statistical arguments could resolve debates wherein the reasonability of expectations had become a matter of contention. Recall that the crew in incident 2737 partially attributed their surprise of the U-boat to the non-use of radar. The question of whether or not radar helped or hindered in searches wherein U-boats might be equipped with radar detectors had been taken up some months earlier by British Coastal Command OR section. In any given mission it was, of course, unclear whether a radar blip that disappeared was the result of a U-boat having detected a bomber's radar and submerged. There were many potential causes of disappearing blips. It was, therefore, unclear how reasonable it was to expect a blip to disappear a certain percentage of the time without coming to the conclusion that a typical disappearing blip represented an alerted U- boat. It was necessary to perform statistical analysis of instances of disappearing radar blips and to investigate the relative frequency of causes of such instances to determine whether Germans were, in fact, evading bombers by detecting their radars, and, if so, whether lost contacts outweighed gains in search efficacy promised by radar use. The OR section concluded it was not beneficial to use radar at that time.50

To assume that scientists' use of quantitative methods defined their OR activity as 'scientific' and thereby unique, however, would be a mistake. As Blackett himself remarked after the war, 'Collection of statistics for the sake of statistics is no more operational research than collecting beetles is biology.'51 The military was entirely capable of collecting and analysing their own statistics. OR scientists, rather, replaced statistical rules of thumb with new rules that made more rigorous use of available data. Yet remember that Blackett himself remarked that military methods proved sufficiently rigorous nine times out of ten. Are we to define statistical analysis as scientific only where it proved useful to have a more rigorous treatment?52 Rather than concentrate on how OR quantitative methods may or may not have differed from military quantitative methods, we should emphasize the idea that the greatest power of OR investigations was not in their quantitative rigour, hut in their questioning of unsubstantiated assertions.

Quantitative methods could conceal knowledge as easily as reveal it. What mattered was the investigative skill to properly connect quantitative information with operational facts. Blackett commented on this point after the war, describing a mystery that, he believed, contained 'an element of discovery of the unexpected in the sense in which the words are used by natural scientists'. Early in the war, anti-aircraft batteries along the coast were reporting a night-time kill rate twice that from batteries inland. Many possible explanations for the statistical disparity were considered. But the solution, so it turned out, was to be found in how statistical data were reported. Overland kill reports were checked against reports of wreckage and unconfirmed reports disallowed. Over the English Channel such reports could not be confirmed, so none were disallowed. In the end, it was revealed that overland kill reports were, indeed, found to be exaggerated by 'a factor of about two' before disallowances.53 Just as Blackett had to be familiar with how his cloud chamber produced confusing data, so the OR scientists under his supervision had to understand how operational record- keeping could do the same. Even the most sophisticated theoretical product of wartime OR, search theory, should be viewed only as an aid to topical investigation. Search theory was a geometric and statistical body of theory constructed by mathematicians at ASWORG to yield probabilities of encounter (whether in search, collisions, weapons fire and so forth). However, it should not be construed as a free-standing science of warfare. Like the mathematics of acoustics, Morse's speciality, search theory was a generator of analogies. It could produce theoretical expectations, but only insofar as its formulations could first be made to reproduce verifiable observations. Much like traditional military planning, its power was limited by the quality of knowledge about one's own search capabilities and intelligence on enemy capabilities as well as by the creative skill used in constructing rigorous arguments based upon that knowledge. In this sense, search theory augmented operational reasoning, but it is not what made it scientific.54

The fundamental similarity of search theory and other methods of OR to military heuristics is reflected poignantly in a statement made in Morse and George Kimball's post-war report on ASWORG's activities, later turned into the first book on OR methodology:

Operations research done separately from an administrator in charge of operations becomes an empty exercise. To be valuable it must be toughened by the repeated impact of hard operational facts and pressing day-by-day demands, and its scale of values must he repeatedly tested in the acid of use. Otherwise it may be philosophy, but it is hardly science.55

While the statement is a call always to test the conclusions of OR studies against actual results, it can be read as a sign that, like all other research done under military auspices, its central validity as science was tied inextricably to the act of operational planning. Scientific work could only be conducted within a rational framework defined by planning, but planning itself had already created its own military heuristic practices. Scientists simply proved adept at learning about and improving these practices.

Conclusion

The question of whether OR was a scientific activity or an activity performed by scientists has importance far beyond semantics. It is central to understanding whether or not the introduction of outside analysts fundamentally changed the nature of scientific and military work. Many historians have placed OR squarely within historiographical constructs such as the 'World War II regime', the 'Closed World discourse' and the 'Cyborg Sciences', in which the military provided scientists not only with patronage but with a host of militaristic and mechanistic metaphors, prompting the rise of fields such as cybernetics and game theory. Scientists, in turn, have been judged to have provided the military with the means to centralize control of warfare through the development of the analytical techniques that RAND used to study nuclear warfare in the 1950s and that Robert McNamara employed in his reforms at the Pentagon in the 1960s, as well as through the development of command- and-control technologies that continue to dominate military activity today.56

It is time to refine our notions of the relationship between science and the military by dispensing with the notion that 'science' has had a coherent influence on the military and vice versa. We should begin to understand the differences and relationships between various kinds of scientific activity within military contexts. The exploration of the relationship between OR and the technology of fire control would be an excellent starting point. The two concepts have often been grouped together, but only as two facets of a singular phenomenon.57 The differences between them are crucial. Firecontrol mechanisms automated the process of aiming and firing weapons by anticipating the future location of enemies using target-tracking by humans as an input. They reified knowledge about ballistics and enemy behaviour into a piece of equipment and are widely seen as the prototype of cybernetics, that epitome of post-war rationalism, centralization and control.58 On the other hand, as we have seen, OR was oriented more towards the scrutiny and investigation of existing bodies of knowledge rather than the construction and establishment of new ones.

This role for OR reflected a broad but distinctive view of scientific method held by its most influential early practitioners. Coming from two different branches of physics, Patrick Blackett's and Philip Morse's everyday pre-war scientific experiences held no deep resemblances to each other. Blackett painstakingly manipulated machinery to coax details about the tiniest particles of nature out of misty air. Morse dealt with diagrams, data-sets and equations, attempting to re-create physical phenomena in the abstract zone of mathematics. Yet, in spite of the differences in their practices, both described OR as an application of scientific method. To both, science was simply a creative act that relied on a detailed understanding of the processes that led to the manifestation of physical phenomena in order to assemble effective or appropriate means of interpreting experimental data and thereby obtaining a clearer understanding of them.

When Blackett, Morse and other scientists began working with the military, they found already in place a vast complex of rational planning practices as well as heuristic practices aimed at comprehending and reacting to unexpected and ill-understood operational phenomena that threatened to undermine planned operations. OR scientists did not set out to replace existing military practices with their own scientific methods. Instead they became scholars of them. Once they understood how military heuristics produced knowledge and supported mission-planning, they could scrutinize and critique these practices with the authority of a military expert. Ultimately, they became so adept at making arguments within the rational framework of military operations that OR became recognizable to them as a scientific activity in and of itself. For its own part, the military recognized scientists' investigative talent and found it valuable to retain their services.

It would be very difficult to associate any notion of scientific method that accompanied OR with a particular body of scientific theory such as cybernetics or with the rise of any particular set of technologies such as those that developed around fire control. The fact that research into operations was continuing may well have been more valuable than any individual conclusion that OR scientists might have reached.59 I believe it is, therefore, better to associate OR with the rapid proliferation of the topical military 'study'. The connection between OR and the systems-analysis studies later performed by the RAND Corporation, for instance, has long been recognized, but the nature of the connection has remained shrouded in preconceptions about the post-wnr encounter between science and the military. If we begin to look beyond the most ambitious calculations of systems analyses and see them less as extensions of mathematical theories of combat and more as extensions of wartime OR, as acts of scholarship in a topic of military interest and as interrogations into the assumptions that inform military planning, we can begin to understand 'scientific' studies as something other than extrinsic and antipathetic alternatives to traditional military thinking. If we question what we mean by science and scientific method in relation to the military, what has been seen as the rise of a new monolithic paradigm suddenly fractures and becomes part of a longstanding string of debates in both the military and science about how good our metaphors and models really are. These are debates about the strength and integrity of bodies of knowledge and about what is well understood and what has remained hitherto unknown.

1 C. Kittel, 'The nature and development of operations research', Science (1947), 105, 150-3, originally offered the definition 'Operations research is a scientific method for providing executive departments with a quantitative basis for decisions' (emphasis in original). This definition was adapted elsewhere before making its canonical appearance, in altered form, as the first sentence of P. Morse and G. Kimball, Methods of Operations Research, New York, 1951.

2 The historiography of OR is vast and includes a substantial and informative group of histories written by OR practitioners. Some of the most recent contributions by historians are also the most comprehensive and contain extensive bibliographies of older materials. See especially M. Kirby, Operational Research in War and Peace: The British Experience from the 1930s to 1970, London, 2003; and K. Ran, 'Combat scientists: the emergence of operations research in the United States during World War II', Ph.D. dissertation, University of Pennsylvania, 1999, UMI number 9926187; as well as two published articles: idem, 'The adoption of operations research in the United States during World War II ', in Systems, Experts, and Computers: The Systems Approach in Management and Engineering, Wttrld War II and After (ed. T. Hughes and A. Hughes), Cambridge, MA, 2000; and idem, 'Technological systems, expertise, and policy making: the British origins of operational research', in Technologies of Power (ed. M. Allen and G. Hecht), Cambridge, MA, 2001. Rau is currently preparing a book on the topic. M. Fortun and S. Schweber, 'Scientists and the legacy of World War II: the case of Operations Research (OR)', Social Studies of Science (1993), 23, 595- 642, is an influential essay on OR history that addresses sundry questions concerning its development, including its relationship with Taylorism and the preponderance of physicists in wartime OR. Also see R. Rider, Operations research and game theory: early connections', in Toward a History of Game Theory: Annual Supplement to Volume 24, History of Political Economy (ed. E. Weintraub), Durham, 1992. A number of other works have commented on the significance of OR to wartime and post-war developments, without offering complete histories. These works will he cited here as appropriate. 3 A. Pickering, 'Cyborg history and the World War II regime', Perspectives on Science (1995), 3, 1-48, 13-18.

4 See both Rau, 'The adoption of operations research in the United States', op. cit. (2), esp. 227; and Rau, 'Technological systems, expertise, and policy making', op. cit. (2).

5 D. Edgerton, Warfare Suite: Britain, 1920-1970, Cambridge, 2006, esp. Chapters 4 and 5. See also idem, 'British scientific intellectuals and the relations of science, technology and war', in National Military Establishments and the Advancement of Science and Technology (ed. P. Forman and J. Sanchez-Ron), Boston, MA, 1996. Edgerton's claims relate mostly to research and development hut can he extended to operational planning as well.

6 Edgerton, Warfare State, op. cit. (5), quoting from P. Blacken, 'Scientists at the operational level', a 1941 memorandum reprinted in idem. Studies of War, Nuclear and Conventional, New York, 1962, 173. Note Blackett's comment two paragraphs above: 'The scientist, in considering an operational problem, very often comes to the conclusion that the common-sense view is the correct one.' The 'nine out of ten' figure is published in 1'. Blacken, 'Recollections of Problems Studied, 1940-45' (1953), reprinted in ibid., 210. Philip Morse, to be introduced shortly, once described Blacken as the 'general dean of OR everywhere', 'Diary of Dr. Philip M. Morse and Dr. William Shockley, Visit to London Commencing November 19, 1942,' Folder 5, Box 39, Edward I.. Bowles Papers, Manuscript Division, Library of Congress, Washington, DC.

7 The figures of the Arrogant Scientist and the Curmudgeonly Officer often appear in histories as colourful examples of tensions between science and the military. For a recent instance, S. Ghamari- Tahrizi, The Worlds of Herman Kahn: The Intuitive Science of Thermonuclear War, Cambridge, MA, 2005, is an excellent account of the method and purpose of Kahn's work, hut Kahn's often arrogant style is implicitly traced back to wartime OR, where we are presented with a Blacken whose 'smugness was intolerable to the services' (46). Stories of conflict between scientists and military officers should not be construed as typifying their relationship. In all of his work. Ran has continually made clear that territorial negotiations between OR scientists and officers were, taken on the whole, quite successful.

8 To clarity the meaning of 'methodology', Blacken and Morse are both viewed as crucial figures in the establishment of a broad methodology of OR, meaning what form OR groups should take, what their relationship should be with the military and some vague notion of their investigative concerns and methods. Blacken, particularly, published two influential wartime memoranda: Blacken, 'Scientists at the operational level', op. cit. (6); and Blacken, cents note on certain aspects of the methodology of operational research' (1943), in idem, Studies of War, op. cit. (6). However, actual analytical methodology was not dictated from administrators such as Morse and Blaekett, but would have been more dependent on the talents of individuals and their OR colleagues.

9 Kimball was Morse's deputy in the Anti-Submarine Warfare Operations Research Group (ASWORG), working for the US Navy, and was co-author of their influential post-war report of ASWORG's activities, which was later turned into a textbook; see Morse and Kimball, op. cit. ( 1). C. Waddington, O. R. in World War 2: Operational Research Against the U-Boat, London, 197.3, was written soon after the war ended, but its publication was delayed by security issues. It clearly conveys a similar attitude to problem- solving that is familiar from Morse and Kimball as well as Blackett's writings on OR.

10 M. Nye, Blackett: Physics, War, and Politics in the Twentieth Century, Cambridge, MA, 2004, quote on 140.

11 On the history of particle detection in cloud chambers see P. Galison, How Experiments End, Chicago, 1987, Chapter 3; and esp. idem. Image and Logic: A Material Culture of Microphysics, Chicago, 1997, Chapter 2.

12 P. Blackett and G. Occhialini, ' Some photographs of the tracks of penetrating radiation ', Proceedings of the Royal Society of London, Series A (1933), 139, 699-726, Plate 21, caption, 720.

13 J. Chad wick, P. Blackett and G. Occhialini, 'Some experiments on the production of positive electrons', Proceedings of the Royal Society of London, Series A (19.54), 144, 235-49, 237-8.

14 On the effects of gas see P. Blackett, On the technique of the counter controlled cloud chamber', Proceedings of the Royal Society of London, Series A (1934), 146, 281-99, 288-9. A good discussion of more subtle distortion ef