Category The Enigma of. the Aerofoil

It was not until July 3, 1923 (after the confrontations at the Royal Aeronauti­cal Society and the International Air Congress), that the Aerodynamics Sub­Committee took a formal decision to test the Prandtl theory. The minutes read as follows: “That the investigation of the air flow behind aerofoils of finite and infinite span be carried out to ascertain how far the Prandtl theory of circulation can be substantiated by experiment.” The decision was passed to the full committee and ratified on July 10.13

After some delays the much-discussed experiment went ahead at the Na­tional Physical Laboratory. L. W. Bryant and D. H Williams performed a large number of measurements to build up a picture of the speed and direction of the air at points around a vertically positioned aerofoil that stretched across the full seven-foot depth of the NPL’s largest air channel. They did not use a Joukowsky aerofoil but a thick, high-lift section, chosen by Bairstow, that they positioned at approximately 10° to the air flow, which moved at about 49 feet per second. From a study of the velocity data it was possible to evaluate the circulation around various, selected contours. Some of these were cho­sen to loop round the wing itself, while some were closed contours that did not include the wing but were merely located in the space around it. If the flow was irrotational, the latter contours should yield a zero circulation. By contrast, according to the circulation theory, all contours enclosing the wing should show the same, nonzero circulation whose magnitude was related to the lift by the fundamental equation L = p VT. The lift was established by tak­ing pressure measurements. Inserting this empirical value for L in the equa­tion gave a predicted value for the circulation Г, which could be compared with the circulation computed from the velocity measurements.

In November 1923 the committee received Glauert’s technical report T. 1850 titled “Experimental Tests of the Vortex Theory of Aerofoils.”14 This was a general summary of evidence in support of Prandtl’s approach but began with a preliminary analysis that Glauert had made of data provided by Bryant and Williams. The measurements, carried out at what Glauert called a “rela­tively high angle of incidence,” enabled him to present a graph that showed the circulation plotted against the area of the contour around the wing along which the circulation had been measured. The graph indicated that the cir­culation was roughly independent of the area. Different-sized contours were indicating the same value for the circulation—just as the theory implied.

What is more, the numerical value of this circulation was almost exactly the value predicted from the formula. Things looked promising for the support­ers of the theory. There had yet to be any direct test of the zero circulation in the contours that did not enclose the wing, to check that the flow was indeed irrotational, but the indirect evidence gathered so far seemed to confirm the assumption of irrotational flow.

Taylor set about to show that this evidence was not as good as it looked. In January 1924, he submitted his “Note on the Prandtl Theory.”15 It was meant to block the inference that Glauert was making on the basis of the preliminary data. Taylor argued as follows. If the flow is irrotational, then all the contours around the wing will have the same circulation. This condition was consistent with the experimental results, but no experiment can test all contours and, so far, only a few had been checked. It does not follow that, because some con­tours show the same circulation, the flow must be irrotational. In the present case Taylor was convinced that the flow could not be irrotational. His suspi­cions were aroused by the use of a wing at high incidence, that is, approach­ing the stalling angle. Previous experiments had shown that the wing would be experiencing high resistance, although it should have zero resistance in an irrotational flow. The high resistance means the flow cannot be everywhere irrotational. There would be a significant wake, and the fluid elements in the wake would be rotating—some this way, some that. If the experimental read­ings showed that various contours all had the same circulation, then there must be something peculiar about the contours. “Mr. Glauert’s result would have to be attributed to a fortunate choice of his contour rather than to an irrotational type of flow” (3).

How could contours of different sizes exhibit the same circulation with­out this indicating the irrotational nature of the flow through which the con­tour had been drawn? Taylor gave an example to show how this result might arise. Imagine a wing profile surrounded by two circular contours, A and B, which have a common center on the wing. Both are large compared to the wing, but B has a greater radius than A. (See fig. 9.2, which is taken from Taylor’s report.) Suppose that the wing generates a wake with, say, positive vorticity issuing from the upper surface and negative vorticity from the lower surface. The wake is shown in the diagram contained between the dotted lines. The circulation around the circle A is, by Stokes’ theorem, equal to the total vorticity within the area enclosed by the contour. Here there will be two sources of vorticity: the vorticity along the surfaces of the wing and the vor – ticity provided by the wake. Now consider the circulation around the larger circle B. Any difference between the circulation around A and B must come from the vorticity in the wake that lies in the area between the two circles.

Taylor, however, was interested in the conditions that would make them have the same circulation, that is, the conditions that might lead the unwary into supposing that the contours passed through a flow that was wholly irrota­tional. Such a condition would arise if the amounts of positive and negative vorticity issued into the wake were equal. The flow would not be irrotational, but it would yield the same circulation for the different contours. The con­ditions of this example may be special, but they are sufficient to expose the fallacy of inferring the irrotational nature of the flow simply from the equality of circulation around a number of different contours.

This was the essence of Taylor’s argument but not the end of it. Glauert’s preliminary analysis of the experiment not only suggested that the circula­tion was the same on contours of different sizes, but it also revealed that the circulation’s magnitude was almost precisely that predicted from the basic law relating lift to density, speed, and circulation. Could that be explained by the unwitting selection of a “favorable” contour? Taylor showed that the answer to this question is yes. His argument was based on the equations that, respectively, express the conservation of momentum perpendicular to, and parallel to, the direction of motion of an aerofoil. Consider a body in a stream of fluid of velocity U parallel to the x-axis. Taylor wrote down, in what is now a standard way, the momentum flux equations across an arbitrary con­tour C which encloses the body. After some manipulation, and disregarding small quantities, he arrived at the following two expressions. One concerned the drag forces lying in the direction of motion; the other concerned the forces perpendicular to the motion and defined the relation between lift and circulation:

where D is drag, L is lift, U is the velocity of the free stream and I is the circulation, p is density, p is pressure, q is velocity, and m and l are direc­tion cosines. These indicate the slope of the contour. Thus m expresses the orientation of the contour at a given point by giving the cosine of the angle between the normal at that point and the y-axis, while l functions in the same way but gives the cosine of the angle between the normal and the x-axis. The expression in brackets, under the scope of the integral sign, is proportional to what is called the “total head” and (as explained in chap. 2) is a quantity measured by a Pitot tube facing the oncoming stream of air.16

For Taylor’s immediate purposes it was the second of these equations, dealing with the lift L, that was most important. The equation is obviously similar to the Kutta – Joukowsky equation. The familiar product of density, speed, and circulation (here expressed as p UI) is clearly visible, but with the addition of the integral on the right-hand side. Taylor drew attention to the following features of the equation. If the flow is irrotational, the expression in the brackets, the total head, is a constant, and as a result the value of the integral around the contour is zero. This removes the term from the equa­tion and leaves L = p UI, the basic law of lift. Thus the simple law follows from his analysis, given the assumption that the flow is irrotational. But sup­pose there is a wake. Within the wake the flow is not irrotational. Along the part of the contour that passes through the wake, the total head will not be a constant but will vary in magnitude. In general, under these conditions, the value of the integral will not be zero. The simple proportionality between lift and circulation will then no longer hold. But, Taylor noted, the bracket under the integral is multiplied by m, the direction cosine. If the contour is so chosen that the part of it that cuts the wake is perpendicular to the main flow, that is, perpendicular to the x-axis and parallel to the y-axis, then m will be zero. (The angle between the normal to the contour and y-axis will be 90°, and the cosine of 90° is zero.) This feature of the mathematics makes the integral zero once again. For such a contour, the integral term in the equa­tion will disappear and leave an expression that coincides with the simple law of lift.

It follows that one cannot infer that the flow is irrotational just because the data are related by the law L = pUI. Even though some of the flow is not irrotational, this relation between lift and circulation can hold because of the choice of the contour. Taylor summed up his argument in the following words: “We have now seen that the relation L = pUI may be expected to hold even when the motion is not irrotational provided that the circuit used in calculating I is chosen in a particular manner. If Mr. Glauert’s circuits are in fact chosen in this manner his result though interesting in itself cannot be re­garded as being in any sense confirmatory of Prandtl’s fundamental hypoth­esis that the motion at a great distance from the aerofoil is irrotational” (7).

Taylor’s deduction depended on neglecting small quantities. To justify this step he had assumed that the disturbances caused by the aerofoil declined as l/R, where R is the distance from the aerofoil. Taylor was conscious that this step might hide a problem for his argument. Could the l/R assumption be tantamount to admitting that the flow was irrotational? Taylor seemed un­sure but circumvented the problem by showing that there were other coun­terexamples that would block Glauert’s inference, and these did not depend on the l/R assumption.

Here Taylor produced his piece de resistance. He reanalyzed Rayleigh’s 1876 paper on discontinuous flow around an inclined plate and showed that the circulation in the flow conformed to the law L = pUI, provided the con­tour cut the dead air of the wake perpendicular to the direction of the main motion. (See the contour marked C’ in fig. 9.3, again taken from Taylor’s report.)

Rayleigh flow clearly bears no resemblance to the flow assumed by Prandtl. Although the relevant integral can be specified, the idea that Ray­leigh flow has a “circulation” is not physically well defined because there is no unique value attributable to it. The value will depend on the contour. This was Taylor’s point. With the “right” sort of contour, he was able to show that the value of the integral will tend to the same limit, L/p U, as that derived from the assumption of an irrotational flow with circulation. Armed with these remarkable results Taylor drew his final conclusion: “It appears, there­fore, that if Mr. Glauert’s contours were taken in the special way described his results would be expected whatever the type of flow round the aerofoil may

be. It cannot be taken as confirmation of Prandtl’s hypothesis” (14). Were “Mr. Glauert’s contours” taken in this way? Were they perpendicular to the main flow where they cut the wake? The answer is yes. Bryant and Williams had used just such contours to establish the circulation around the wing, and those were the ones Glauert employed in his preliminary analysis. Taylor had pulled the rug from beneath Glauert’s feet.

Despite Taylor’s criticisms, Bryant and Williams’ experiment was written up as a technical report (T. 1885) in February 1924.17 It was eventually pub­lished, in an expanded form, in the Philosophical Transactions of the Royal Society in 1926 along with an appendix from Taylor.18 Taylor’s appendix gave essentially the same mathematical and methodological argument as his “Note on the Prandtl Theory,” described earlier. The combination of paper and ap­pendix makes uncomfortable reading because no attempt had been made to modify the contours in the light of Taylor’s comments. The only significant differences between the original technical reports presented to the Research Committee and the published papers lay in the tone of Taylor’s contribution. He had made two alterations. First, the published version contained none of the sharp words directed at Glauert. Second, Taylor chose to reformulate his methodological point and express it in different words. Instead of saying that the purpose of his argument was to show what type of contour should not be used, Taylor now said his purpose was to show what sort must be used if, that is, one desires to get the result that L = pUI for a flow that is not irrota- tional. Thus, “the object of the present note is to find out which type of con­tour must be chosen in order that the lift-circulation relation may be satisfied when the motion is not irrotational” (238).

Logically, this declaration is equivalent to what Taylor said to Glauert, but it is no longer framed as an objection. In the unpublished note Taylor had uncompromisingly stated that the result of the experiment “cannot be taken as confirmation of Prandtl’s hypothesis.” In the published appendix his conclusion was reexpressed as follows: “The relationship between lift and cir­culation may hold when the motion is not even approximately irrotational, provided that large contours are chosen so that they cut the wake in a straight line perpendicular to the direction of motion of the aerofoil” (245).

An anonymous report in Nature, commenting on the published account of the experiment, correctly summarized the position and noted that Bryant and Williams had used contours of a special type, “so that the accuracy with which the observed lift force agrees with that predicted from measurements of circulation is no indication that the flow is in fact an irrotational motion with circulation.”19 Although Nature got it right, it is not surprising, given the rewording, that the significance of Taylor’s note sometimes proved elusive. For example, von Karman and Burgers, writing in 1935 in their chapter in Durand’s Aerodynamic Theory, appeared to miss this point.20 They correctly noted that, when the contour cuts the wake at right angles, “then the value of the circulation is the same for all curves under consideration” (8). But they went on: “If the condition that the line must cut the wake at right angles were not stipulated, the magnitude of the circulation would become indefinite, as an arbitrary number of vortices, ‘washed out’ from the boundary layers along the surfaces of the aerofoil, and rotating either in one sense or in the other, could be included. The necessity of this condition was pointed out by G. I. Taylor”(8). This is true, but it turns the original argument on its head. What Taylor had sought to prohibit has now become a stipulation.21

If Haldane had not followed the advice of a Trinity mathematician when he set up the Advisory Committee for Aeronautics but had, say, recruited Cam­bridge engineers rather than mathematical physicists, he might have got a very different committee. In principle he could have done this because Cambridge had a distinguished school of engineering.25 Predictably, there had always been a tension between the demands of a practical engineering education and the demands of the traditional, Cambridge mathematical curriculum. There was not time in the day to succeed at both, except for the outstanding few. It was not until 1906 that a satisfactory accommodation was reached when Bertram Hopkinson, the professor of mechanism and applied mechanics, gave a viable and independent structure to the Mechanical Sciences Tripos. This took the engineers out of the competitive hothouse, though inevitably it meant they operated at a somewhat less sophisticated mathematical level. The products of Hopkinson’s department played a distinguished role in the development of British aeronautics. Busk (who made the BE2 stable), Farren (who championed full-scale research at Farnborough), Melvill Jones (who worked on low-speed control and gunnery), Southwell (who worked on air­ship structures), and McKinnon Wood (the experimentalist who went with Glauert to see Prandtl) were all products of the Cambridge school of engi­neering. Hopkinson himself, though of an older generation, learned to fly during the Great War and did important work on aircraft testing at Martle – sham Heath. He met his death at the controls of a Bristol Fighter in a flying accident in August 1918.26

Perhaps a counterfactual Advisory Committee, made up of men like Ber­tram Hopkinson, would have embraced Lanchester and the circulatory the­ory. This is consistent with my analysis, although the conclusion would only follow if Cambridge engineers were significantly different in their judgments and orientation from their Mathematical Tripos colleagues and significantly similar to the German engineers from Gottingen and Aachen. Such a premise is plausible but it cannot be taken for granted, and there is some evidence that calls it into question. In certain respects Cambridge engineers adopted atti­tudes that were similar to those of the more traditionally trained mathemati­cians. This is not surprising in the case of the older products of the Cambridge school of engineering because they too were steeped in the earlier Mathemati­cal Tripos tradition. Bertram Hopkinson’s father, John Hopkinson, had been both an engineer and a senior wrangler. After a fellowship at Trinity he be­come a professional, consulting engineer in London but retained a strongly mathematical bent. He developed a mathematical analysis of the alternating current generator and predicted that it should be possible to run such genera­tors in parallel. Practical engineers knew that, given the available machines, they could not be run in parallel, but none of this blunted the confidence of the mathematically able Hopkinson.27 Bertram Hopkinson himself had also read for the Mathematical Tripos and had been a highly placed wrangler. Al­though more practically inclined than his father, he had worked on topics in hydrodynamics and had written a paper on the theory of discontinuous flow.

He extended the work of A. E. H. Love by making allowance for the presence of sources and vortices.28 None of those who contributed to the mathematical development of the theory of discontinuous flow ever went on to work on the mathematics of the circulation theory of lift.

What about the somewhat younger generation of Cambridge engineers such as Busk, Farren, Melvill Jones, McKinnon Wood, and Southwell? Here, too, the evidence indicates that, although they had some sympathy with Lanchester, that sympathy had its limits. And those limits were character­istic of the milieu of Cambridge mathematical physics. Southwell’s role as a lecturer in mathematics at Cambridge (despite his engineering background), and his commitment to a fundamental physics of lift, have already been de­scribed. McKinnon Wood was perhaps different. He had come round quickly to the side of the Lanchester-Prandtl theory of circulation, though exactly why is unclear. It is possible that he was taking his lead from Glauert. Writing retrospectively, McKinnon Wood recalled that, as a student, he had borrowed Lanchester’s Aerodynamics from the Union library but then, after reading it, had thought no more about it.29 Looking back, all that he could report was re­gret at this “mysterious blindness.” Farren appears to have accepted a version of Glazebrook’s excuse and recalled Lanchester as an almost a tragic figure. He was a man who had clear insights but who could not give them expres­sion. “The vision of Lanchester brooding over the irony of a world which at last understood what he had seen so clearly, but had been unable to explain, will not fade from the minds of those who knew him.”30

Bennett Melvill Jones sought to shed light on these mysteries in a talk he gave at the Royal Aircraft Establishment at Farnborough in 1957.31 He de­scribed how, as a young man, his friend and fellow engineering student at Cambridge, Edward Busk, had introduced him to Lanchester’s work. It had deeply impressed them. After studying Lanchester’s treatise, “Ted and I sol­emnly decided to spend the rest of our lives on aeronautics.” But, Melvill Jones went on, aeronautics in Britain had then developed in an almost en­tirely empirical fashion, that is, without the guidance of Lanchester’s theory. This may seem surprising, he told his audience, “because the theory of ideal fluid, which now forms the basis of all your work, had already been very fully developed by Lamb and others. But in this theory, no body which starts from rest can, when in steady motion, experience any reaction whatever. And to us, whose business it was to study this reaction, this did not seem very helpful.” The source of the trouble, he explained, was the impossibility of accounting for the origin of circulation. This was the very same objection that the young G. I. Taylor had used against Lanchester in 1914. The origin of the circulation and hence the lift could not be deduced within the terms of the theory. If

Melvill Jones’ recollections were correct, then the products of the Mechani­cal Sciences Tripos had been at one on this question with the products of the Mathematical Tripos. Both saw its dependence on the classical hydrodynam­ics of potential flow as a fatal objection to Lanchester’s approach.

Melvill Jones went on to say that now (that is, by 1957) it may seem obvi­ous how this difficulty should have been resolved. He added, ruefully, that perhaps he and his contemporaries had not been very clever in making the response they did, but, he insisted, “our view was, at that time, shared by all engineers.” Here Melvill Jones was making a historical mistake. Even if the negative reaction to ideal fluid theory was shared by all Cambridge aeronau­tical engineers of his generation, or even by all British engineers, the response was not shared by the German engineers who developed the circulatory theory. In an attempt to justify the negative reaction to Lanchester, Melvill Jones said that the theory of ideal fluids, then known as hydrodynamics, “was regarded purely as an exercise for the amusement of students.” Again, while this may have been true in Cambridge it was not how things were seen in Gottingen or Aachen. This is not how ideal fluid theory was regarded by Betz, Blumenthal, Foppl, Fuhrmann, von Karman, Kutta, von Mises, Prandtl, or Trefftz. For them it was more than a source of ingenious examination ques­tions; it was a serious instrument of research and a serious technique with which to gain some purchase on reality.

The Cambridge ethos seems to have enveloped its engineers as well as its mathematicians. It therefore cannot be assumed that a counterfactual committee of Cambridge engineers would have responded as the German engineers did and welcomed the circulatory theory.32 This answer obviously depends on the range of factors that are allowed into the imaginary picture. If engineers had been given a dominant position on the ACA, they might have gained greater independence of mind. They might then have been less influ­enced than they actually were by the older Tripos tradition of mathematical physics. No one can know. The fact remains that these were not the men who initiated the research program into the theory of lift, and they did not have a dominant role on the committee that Haldane actually created.33

The political pressures that originally prompted Herbert Asquith’s Liberal ad­ministration to set up the Advisory Committee for Aeronautics can be epito­mized by the reaction to the first cross-channel flight from France to England, made by Louis Bleriot on July 25, 1909. Newspaper headlines declared that Britain was no longer an island. Bleriot’s heroic feat was greeted with sport­ing cheers, but the depressing military implications of the flight were evident. The nation’s basic line of defense had been breached. The channel was no longer a moat that made the island an impregnable fortress. Bleriot’s flight dramatically confirmed the warnings that had been voiced since the incep­tion of “aerial navigation.” These reactions have been described in detail by the historian Alfred Gollin, who documents the atmosphere of alarm and the fear of invasion that gripped the country during the early years of the cen­tury, particularly with regard to the emerging power of Germany.7 There was anxiety, assiduously cultivated by the press, that Britain was falling behind in the race to exploit the military potential of the new flying machines: the airship and the airplane. The anxiety was expressed in newspaper reports of mysterious (and almost certainly nonexistent) Zeppelins lurking in the night skies over Ipswich and Cardiff.8

The government, represented by Richard Burdon Haldane (fig. 1.1), the secretary of state for war, did not participate in this sort of unseemly clamor. Haldane was a patrician and highly intellectual figure who combined his poli­tics with philosophical writing and a successful legal career. Educated at the universities of Edinburgh and Gottingen, he was fluent in German, translated Schopenhauer, and had a passion for Hegel.9 To the fury of his critics the portly Haldane proceeded at his own steady pace. Much preoccupied with the long-overdue reform and rationalization of Britain’s major institutions, from the army to the universities, Haldane always insisted that a cautious and “scientific” approach was needed.10 Critics of the government policy on aeronautics called for the immediate purchase of foreign machines. Airships could be bought from France, and aircraft were on offer from the American

Wright brothers, who had been the first to master powered flight. Haldane thought that Britain should go more cautiously, even if it meant going more slowly. He was disinclined to rely on the results of mere trial-and-error meth­ods developed by others. In fact he looked down on those who proceeded in a merely empirical manner, devoid of guiding principles to broaden and deepen their understanding.11

Haldane met the Wright brothers in May 1909 when they came to Europe touting for government contracts. An editorial in Flight, on May 8, hinted at inside information and expressed confidence in the outcome of the meeting: “On Monday, Messers Wilbur and Orville Wright paid a visit to Mr. Haldane, and, while naturally it is needful and fitting to preserve secrecy as regards offi­cial matters, it may be taken as assured that our Government will duly acquire Wright aeroplanes and the famous American brothers will themselves in­struct the first pupils in England.”12 In fact it was not assured. Despite much pressure and lobbying, Haldane declined to do a commercial deal with the Wrights. Rather, the minister concluded, Britain should follow the German example—or what he took to be the German example. The National Physi­cal Laboratory at Teddington, outside London, had been founded in 1900 on the model of Helmholtz’s great, government-funded institute of physics in Berlin, the Physikalisch-Technische Reichsanstalt, and this was the pattern that Haldane wanted to see developed.13 The government must locate the best scientists that were available and set them to work on the fundamental problems of flight. The pioneers had got their machines into the air, but how and why they flew remained obscure. The working of a wing, for example, the secret of its lift, remained an unsolved problem, as did the basis of stability and control. Furthermore, it was unclear whether the future lay with heavier – than-air flight or airships. Like many others, Haldane was more impressed by airships, but scientists must address these issues in all their generality and then, with scientific theory leading practice, the best technology would be able to progress on sound principles. As Haldane put it, “the newspapers and the contractors keep clamouring for action first and thought afterwards, whereas the energy which is directed by reflection is the energy which really gives the most rapid and stable results.”14 The issue of the Wright brothers and their rebuff deserves comment. To Haldane’s critics the refusal to buy these aircraft seemed a gross error of judgment on the government’s part. In fact it was grounded in a defensible line of reasoning. The Wright machine was known to be clumsy and unstable. It could only take off along specially constructed rails, and the subsequent flight demanded great skill and cease­less intervention by the pilot. As a British test pilot put it a few years later, in a report to the ACA on the flying qualities of different machines, it needed an “equilibrist of the first order” to keep the Wright machine in the air.15 (This judgment is corroborated by modern aerodynamic research conducted on the Wright machine.)16 The pilots of such aircraft would (1) require extensive training, (2) become exhausted on long flights, and (3) be so preoccupied that they could hardly perform any military task such as map reading, recon­naissance, or photography. The need was for aircraft that were easy to fly and would leave their pilots with spare mental and physical capacity. The British government’s view was that power in the air would go to the nation that pos­sessed stable aircraft.17

Even before he met the Wrights, Haldane had sanctioned secret tests to be carried out at Blair Atholl, in the Scottish highlands, on a machine de­signed by a British inventor, J. W. Dunne.18 Dunne was a friend of H. G. Wells and later in life became well known for his metaphysical speculations on the nature of time.19 After his early military career had been terminated by ill health, Dunne turned to aviation and won the confidence of the super­intendent of the Army Balloon Factory at Farnborough. Dunne’s airplane, unlike the Wrights’, was meant to be stable and, to achieve this he used a novel, swept-wing configuration. The tests, however, which took place in the summer of 1907 and 1908, were a failure, and the machine did not maintain sustained flight.20 A retrospective report of the episode in the journal Aero­nautics contained the fanciful claim that, after an indiscrete mention of the trials in the press, the Scottish estate where they took place was alive with foreigners who, it was implied, must have been German secret agents. “In two days the place was buzzing with Teutons.” Fortunately, the article continued, loyal local citizenry misdirected the unwanted foreign visitors so that the na­tion’s secrets remained secure.21 Flight even hinted that some of these alleged spies had been disposed of by the Scotch gillies, who acted as lookouts for the trials.22 Haldane’s worst suspicions about empirics and inventors, and every­thing to do with them, were confirmed by such goings on.23 Dunne and his supporters were dismissed. It was time to bring in the scientists and develop a serious policy. Haldane had no intention of being deflected from this course just because the Wrights turned up in London.

Haldane had already laid out his ideas of a sound policy at the first meet­ing of a new subcommittee of the powerful Committee of Imperial Defence on December 1, 1908.24 The prime minister had formed the subcommittee to report on three questions: (1) the military problem that aerial navigation posed to the country, (2) the naval and military advantages of airships and airplanes, and (3) the amount of money that should be spent and where that money should go. The chairman, Lord Esher, invited Haldane to open the proceedings. Haldane said it was important to have the navy and the army working together on these issues in order to provide the preconditions for real progress. Haldane meant by this the preconditions for developing a genuine, scientific understanding of aerial navigation and the problems it posed. He went on: “I was at Cambridge on Saturday, and I spent Sunday talking over some of these questions with Sir George Darwin, the mathematician. Some of them there have given a good deal of attention to this matter, and what strikes them—certainly what has struck me—is the little attempt which has been made, at any rate as far as the War Office is concerned, to answer these ques­tions.” Nobody in the navy, he said, would think of building ships without testing models in water, but if there was ever a need for model work it was in aeronautics. Darwin had told him that the French had experimental establish­ments using artificial currents of air. In reply to a direct question, Darwin had also told him that there was a great deal of mathematical work that needed to be done. Haldane therefore asked the subcommittee to consider appointing a further committee of experts to advise them on technical questions. The advisory body might have “somebody presiding over it like Lord Rayleigh or Lord Justice Fletcher Moulton, or Sir George Darwin.” This, concluded Haldane, was “a very important preliminary to any real progress.”

Esher’s committee went on to take evidence from a number of expert wit­nesses, such as the aviator the Hon. C. S. Rolls and, to appease Churchill, the bombastic businessman, arms dealer, and aviation enthusiast Hiram Max­im.25 The Esher committee did not succeed in bringing the interests of the army and navy into alignment and became bogged down in complicated dif­ferences over policy. Overall, it backed airships over airplanes and even rec­ommended stopping research on heavier-than-air machines, although later this policy was quietly dropped.26 In the course of the protracted discussions, Haldane was challenged by the navy representative over the desirability of his proposed committee of scientists. Should not scientists be on tap rather than on top? Eventually Haldane got his way but, perhaps as a result of this challenge, made sure that his projected advisory committee of experts would report directly to the prime minister.

After introducing Laplace’s equation, Cowley and Levy made the following observations about its centrality to the mathematics of ideal-fluid flow: “The real key to the solution of any problem in the irrotational motion of a non­viscous fluid lies in the determination of the appropriate expression that sat­isfies this equation and at the same time gives the requisite boundaries to the fluid” (44). If this is the “real key,” then where and how is the key to be found? I have just indicated that some flows can be built up by combining the
stream functions of existing flows, but how does the process get started? How were these stream functions arrived at? Apart from the simplest possible of all flows, the primordial straight-line, steady flow, how does the mathema­tician determine which expressions satisfy Laplace’s equation and meet the requisite boundary conditions? Cowley and Levy acknowledge that it is not easy and draw attention to the expedients that have been used to cope with the difficulty.

One expedient is called the indirect method. Instead of beginning by stating a problem (for example, what is the mathematical description of the flow around such-and-such a given object?) the researcher starts with some known piece of mathematics and asks what flow it might be used to describe. Various mathematical functions are investigated to determine which bound­aries might be fitted to them. The difference between the direct and indirect approach is like that between the carpenter who wants to put up a shelf and looks for a suitable piece of wood, and the carpenter who finds an interesting piece of wood lying around and looks for an opportunity to use it. As Cowley and Levy put it, “it will be clear that this indirect method of attack does not furnish a method of obtaining the solution of any proposed problem but rather furnishes the solution from which the problem is obtained” (51-52). This method works because there is a rich field of possible candidates. There is (so to speak) a lot of interesting wood lying around. In this and the next section, I show why there are so many solutions in search of problems. I then look at some more direct lines of attack on the problem of arriving at a mathematical description of a desired flow. The survey will reveal what is, at first sight, an almost uncanny relationship between pure mathematics and the physical world. This feature is one of the most intriguing in classical hydrodynamics.

A body of mathematics called the theory of functions of a complex vari­able places a large body of material at the disposal of the student of hydrody­namics. Complex variables are really just pairs of numbers which represent the coordinates (x, y) of a point relative to a standard coordinate system. But instead of a number pair (x, y), the coordinates are expressed in the form z = x + iy, where i = V – 1. Conventionally the symbol x is called the “real” part of the complex number z, and y is called the “imaginary” part. The symbol i is sometimes called an imaginary number.29 Complex numbers obey all the usual rules for manipulating numbers apart from needing the extra rule that і2 = -1. A function of a complex variable is some combination of complex numbers z whose value is arrived at by adding or multiplying the variable z or subjecting it to some other mathematical operation. Thus, to take an example that will play a prominent role in the story, f(z) = z + 1/z is a function of a
complex variable. Insert a value of z into the formula, perform the requisite operations (finding the reciprocal and adding), and out comes the value of the function f(z). Classical hydrodynamics was able to develop as it did be­cause of the fortunate and remarkable fact that every function of a complex variable w = f(z) turns out to represent a possible two-dimensional flow pattern of an ideal fluid in irrotational motion. There are an infinite number of such functions, some simple, some complicated, but they all represent a possible flow of an ideal fluid.30

I illustrate this remarkable fact by a particular case. It is a case used by Cowley and Levy to illustrate the inverse method, that is, to show how one can, for whatever reason, begin by looking at a piece of mathematics dealing with complex variables and then realize its significance as a description of a possible flow. The example also shows how every function of a complex vari­able embodies the formula for both the potential lines and the streamlines of a possible flow. The potential function ф occurs as the real part of the complex function, while the stream function у occurs as the imaginary part. The link between the two sets of lines, the streamlines and the lines of equal potential, can be represented by writing f(z) = ф + iy.

Cowley and Levy invite their readers to “consider” the function f(z) = (z + l/z). What is the flow that could be represented by this function? This flow can be found by explicitly writing out the function in terms of the more familiar x and y notation. Recalling that z = x + iy and that i2 = —1, then sub­stitution in the formula for f(z) gives

Ф + iy = z + — = (x + iy) +– .

z (x + iy)

The numerator and denominator of the last term are multiplied by (x — iy), and then all the terms on the right-hand side can be put over the same de­nominator (x2 + y2). Rearranging and grouping together the real and imagi­nary parts of the expression gives

. . . x — iy x(x2 + y2 +1) ,y(x2 + y2 — 1)

(x + iy) +— — = —————- – + i————– 2.

4 ” 2.2 2.2 2.2

Examination of the right-hand side of the above equation will reveal that it has the formf(z) = ф + iy. It is now easy to read off the formulas for the po­tential lines and the streamlines of a possible flow.

The potential lines ф= c are given by the real part of this expression, thus

x(x2 + у2 + 1)

2 2 x + у

The streamlines, у = c, are given by the imaginary part of this expression, thus

y(x2 + y2 -1) у = —

T 2,2

x + y

The family of curves у = constant gives the equations of the streamlines, and one of these can be interpreted as the outline of the boundaries that constrain the flow, that is, the shape of the body around which, or along which, the fluid is flowing. Consider the streamline represented by у = 0. This equation calls for either of two conditions to be satisfied. It requires that either y = 0 or (x2 + у1 – i) = 0. The first of these conditions is satisfied if the x-axis (that is, the line y = 0) is a streamline. The other condition is fulfilled if x2 + y2 = 1. This condition is met by points that fall on the circle of radius i, whose center is at the origin. Both of these will be streamlines of the flow represented by the function /(z). In other words, the function can be understood as giving the mathematical description of a flow along the x-axis, which then goes around a circular cylinder of unit radius. If the formula had been (z + a/z) rather than (z + 1/z), the flow described would be that around a circle of radius a.

What about the velocity of the flow? Recall that the velocity components of a flow are given by differentiating the stream function. Thus

ду 2xy

~дХ = (x2 + y2)2′

To find the velocity at a great distance from the circular cylinder (which has its center at the origin) one must ask what happens when the values of x and y become very large. Because of the squared term in the denominator, the frac­tional terms in the previous equations will tend to zero. Thus “at an infinite distance,” as Cowley and Levy put it, u = -1 and v = 0. At a large distance from the cylinder, the flow has unit velocity along the x-axis (from right to left) and that is all. On the surface of the cylinder, one point that can be selected for consideration is x = 1 and y = 0, that is, the very front of the cylinder. Here substitution in the previous formulas gives u = 0 and v = 0, so this point is called a stagnation point or a stopping point of the flow. The upshot is “that the circular cylinder is stationary and the fluid is streaming past it with unit velocity at infinity” (46).

This worked example illustrates the way that (given sufficient ingenuity) the mathematical behavior of a function and its geometrical representation can be read, retrospectively, as providing a picture of a flow. The diagram given by Cowley and Levy showing the flow generated by f(x) = z + l/z is reproduced here as figure 2.4. The solid lines represent the streamlines; the dotted lines represent the lines of equal potential. That the two sets of lines form orthogonal sets is evident from the figure. Inspection of the di­agram indicates two further points. First, the general rule that streamlines and lines of equal potential are at right angles breaks down at the stagna­tion points of a flow. Second, when streamlines and lines of equal po­tential are switched in their roles, it is necessary to adjust the boundary conditions.31

The commonly distinctive feature of a modern mathematical treatise, in any branch of physics, is that the investigation of any problem is initially conducted on the wid­est and most comprehensive basis, equations being first obtained in their most gen­eral form. . . . The author has endeavoured to minimise any difficulty on this score by dealing initially with the simpler cases and afterwards working up to the more general solutions.

f. w. lanchester, Aerodynamics, constituting the First Volume of a Complete Work on Aerial Flight (1907)1

By the beginning of the Great War the British experts on the Advisory Committee who were responsible for research in aerodynamics had effec­tively abandoned the discontinuity theory of lift. There was, however, a known alternative: the circulatory or vortex theory that had been developed by Frederick Lanchester. It would be reasonable to expect that this theory would now become an object of some interest even if it had been ignored at the outset of the committee’s work when they had concentrated on Rayleigh’s achievements. But, rather than turning to the circulation theory, the ACA again treated it as if it were of no merit. Lanchester was a member of the committee but his ideas were passed over—for a second time. Given that the circulation theory later came to be accepted as the correct account of lift, this insistent rejection has long been seen as a puzzle. Why did it happen? In this chapter I lay the foundations for an explanation of this negative response. The explanation is developed and tested as the analysis is carried further in subsequent chapters.

I begin by introducing the basic ideas and technical vocabulary of the cir­culatory theory.2 This will give access to the (largely) qualitative version of the theory developed by Lanchester and lay the basis for my discussion in later chapters of the quantitative versions that were subsequently developed in Germany. In this chapter I also have more to say about Lanchester’s treatment at the hands of the so-called practical men. Their opinion of Lanchester was divided. While some recognized him as one of their own, others saw him as selling out to the state-funded academic scientists, theorists, and mathemati-

cians who were so reviled by the spokesmen of industry. Lanchester hit back in a characteristically forthright way and became involved in some bruising, but revealing, encounters with the antigovernment press. While Lanchester was defending the Advisory Committee, the Royal Aircraft Factory, and the National Physical Laboratory, the experts within these bodies were articulat­ing a systematic rejection of the circulatory theory of lift. They were hostile or indifferent to Lanchester’s approach. Lanchester was thus in the unenviable position of being attacked for belonging to a group that, while not actually excluding him, was certainly marginalizing him. It is vital to understand both the external politics and the internal politics that were woven together in this episode. Both are described in this chapter. The first step, however, must be to understand the conceptual basis of Lanchester’s theory.

Sir Horace Lamb’s famous textbook started life in 1879 as A Treatise on the Mathematical Theory of the Motion of Fluids, which was based on the lectures Lamb had given as a fellow of Trinity.11 Lamb (fig. 5.1), who had been taught by Stokes and Maxwell, left his Cambridge fellowship in order to marry. He took a chair at Adelaide and then taught for many years at the Victoria Uni­versity of Manchester. He returned to Trinity in 1920 as an honorary fellow. During this time the small Treatise was renamed Hydrodynamics and grew into the imposing volume known to generations of students in applied math­ematics. It went through a total of six editions between 1879 and 1932. The gap between the third and fourth editions, that is, from 1906 to 1916, covered the pioneering phase of aerodynamic theory and the emergence of the circula­tion theory of lift. Most of this aerodynamic work was too late for inclusion in the 1906 version but found a response in the updated 1916 volume. Here, for the first time, one finds the names of Kutta, Joukowsky, Prandtl, Foppl, von Karman, and Lanchester.

The structure of the 1916 edition was very close to that of the previous editions. The new work on aerodynamics was not allowed to upset the pre­existing framework of hydrodynamic theory.12 Consider the relation between the accounts of viscous and inviscid flow. The book was some 700 pages long, and the discussion of viscosity began on page 556 with chapter 11. Viscosity, said Lamb, is a phenomenon “exhibited more or less by all real fluids, but

which we have hitherto neglected” (556). Up to that point all the analysis had concerned an ideal fluid. The Euler equations had been sufficient to solve the problems discussed in the previous chapters, but it was now necessary to con­front the formidable Stokes equations of viscous flow. The equations, which Stokes had arrived at in 1845, were duly derived and set out on page 573. I give a form of the equations below. I have simplified them and changed Lamb’s notation slightly so that they can be compared more easily with the Euler equations for ideal fluids as I gave them in chapter 2. Like the Euler equations, they are partial differential equations that relate together the components of fluid velocity u and v and pressure p, but this time allowance has been made for viscosity represented by |i. Stripping away the negligible effect of external forces such as gravity and treating the fluid as incompressible, and the flow
as both two dimensional and steady, the Stokes equations for a viscous fluid can be written as follows:

dp ( du du і ^2 ,

-^ = ^1 u— + v— — u and dx ^ dx dy)

where

If the coefficient of viscosity, |i, is put equal to zero, the equations lose the terms on the extreme right and they assume the simpler form of the Euler equations for an ideal fluid. This does not mean that any solution to the Euler equations is also a solution to the Stokes equations. The presence or absence of the viscous terms alters the character of the equations. The Euler equations do not have to satisfy all the boundary conditions of the more complicated equations. A solution to the equations of viscous flow must satisfy the condi­tion that the fluid adheres to any solid boundary and thus has zero velocity along the boundary as well as zero velocity normal to it. An ideal fluid is not required to adhere to a solid boundary but can slide along it with perfect smoothness.

After the derivation of the Stokes equations, Lamb considered a num­ber of applications, for example, the flow of a viscous fluid between two flat plates that are very close together, and the motion of a sphere falling through a very viscous fluid. The former case approximates the study of lubrication. It also provided the occasion for Lamb to discuss the intrigu­ing photographs taken by Hele-Shaw. These rendered with great accuracy the appearance of the flow of an inviscid fluid. By introducing a (very thin) cylinder between the plates, and forcing the fluid to flow around it, the flow could be studied even in cases that defied direct mathematical analysis. Lamb recapitulated the mathematical explanation of these photographs first given by Stokes. Stokes had been able to demonstrate why a viscous flow could, under the circumstances of creeping flow, simulate the behavior of an inviscid flow.13

The case of the sphere falling through a viscous fluid was important for the study of meteorological phenomena that involved droplets of water in
the atmosphere.14 Because the drops fell very slowly, it was possible to sim­plify the equations and arrive at a law giving their speed. In 1910 this law had been applied to the oil droplets in Robert Millikan’s famous experiment to measure the unit of electric charge. The oil drops in the apparatus obeyed Stokes’ law, as it came to be called, which gave their speed of fall in terms of their radius, relative density, and the coefficient of viscosity of the fluid.15 Lamb showed how this law was derived from the basic equations. Important as these and similar results were, the introduction of viscous forces into the analysis had to be accompanied by a corresponding limitation in the role played by the inertial forces. The motions under study had to be very slow or the dimensions very small. Without this restriction the Stokes equations were, in general, intractable.

The 1916, fourth edition of Hydrodynamics contained a new section, “Re­sistance of Fluids,” which Lamb added to the end of the chapter on viscosity. It was here that he addressed the aeronautical work. The location and the name of the new section suggest that Lamb saw the problem of lift as falling under the rubric of viscous flow. The position and title carried the message that lift was not to be analyzed on the basis of perfect fluid theory. Resistance, said Lamb, “is important in relation to many practical questions” (664). He mentioned the propulsion of ships, the flight of projectiles, and wind forces on, for example, buildings, and added that although resistance “has recently been studied with renewed energy, owing to its bearing on the problem of artificial flight, our knowledge of it is still mainly empirical” (664).

Lamb then discussed Kirchhoff-Rayleigh flow and drew attention to its empirical failings, particularly the failure to account for the suction effect on the upper surface of a wing. The reader was referred to publications by Stan­ton and Eiffel for information on “the experimental side.” After this came an account of the circulation theory. It was introduced as an explanation of how a body may be supported against gravity that had been “put forward from a somewhat different point of view,” that is, somewhat different from the theory of discontinuous flow (666). A footnote then made reference to Lanchester’s Aerodynamics, but no attempt was made to expound Lanchester in his own terms. Instead the reader was briskly referred to the earlier sec­tion in Hydrodynamics, article 69, which dealt with Rayleigh’s tennis ball. Lanchester’s theory, said Lamb,

is based on the result of Art. 69, where it was shown that a circular cylinder will describe a trochoid path, the motion being mainly horizontal, if the sur­rounding fluid is frictionless, and its motion irrotational, provided there is a circulation (к), in the proper sense, about it. In particular the path may be a

horizontal straight line, the lifting force (which is to counteract gravity) being

then

Y = KpU

per unit length, where U is the horizontal velocity. (666)

Lamb went on to show that the formula held for a cylinder of any cross section, not just for the case of a winglike section. Here Kutta and Joukowsky were mentioned and references given. Lamb then cited the result for an el­liptic cylinder (that is, the 1910 Tripos question) and went on to say that Kutta “had treated the case of a lamina whose section is an arc of a circle.” Lamb’s summary is instructive: “He [Kutta] assumes the circulation to be so adjusted in relation to the velocity of translation that the infinite value of the fluid velocity which would otherwise occur at the following edge is avoided, whilst an infinity remains of course at the leading edge. It is supposed that in this way an approximation to actual conditions is obtained, the ‘circulation’ rep­resenting the effect of the vortices which are produced behind the lamina in real fluids; and a good agreement with experiment is claimed” (667).

All the standard British objections found an expression in this compressed passage. Kutta’s theory was not offered as a description of reality. There was merely the supposition that there was some “approximation to actual condi­tions.” In a real fluid there are vortices in the flow behind a lamina, but these received no recognition in Kutta’s analysis. The circulation (in quotation marks) merely represents the effects of a certain phenomena but (the wording implies) does not correspond to its real nature.

It would be difficult to devise a description of Kutta’s work that was as brief and as accurate as Lamb’s but that contained more qualifications and implied question marks. Perhaps this was to be expected, given that the dis­cussion of Kutta’s inviscid analysis was located in a chapter devoted to vis­cous processes. The message was that Kutta, Joukowsky, and Lanchester were trying to represent essentially viscous processes by an inviscid theory. Lamb was highlighting the artificiality of their analysis and pointing to the need to ground it in Stokes’ equations of viscous flow.

Now it was time to compare the theoretical predictions with the results of ex­periment. Kutta did not perform experiments himself but used existing data. The aim was to see if the predicted relation between lift and angle of incidence was correct. The formula for the circulation shows that the circulation increases with increasing angle of incidence, so lift should likewise grow. Kutta worked out two sets of testable results, one for a flat plate, the other for the curved wing. The two predictions are closely related because the flat plate is just the limiting case of the curved plate. The limiting process greatly simplified the formula and permitted a rough comparison with flat-plate data already pub­lished by Duchemin and Langley. The experimental lift was about two-thirds of that predicted by the theory. Kutta declared this “nicht ganz schlecht” (52), which might be rendered as “not too bad.” In his discussion of the flat plate, Kutta also established that the center of pressure will be at a point one-quarter the width of the chord from the leading edge and that, unlike for the curved plate, the position stays the same even though the angle of incidence changes.

Coming now to the curved wing, Kutta used Lilienthal’s own data, which were generated by experiments on a small model of an arc-shaped wing with a sharp leading edge. Because of the sharp leading edge, Kutta thought that friction effects would be dominant so that the leading-edge suction would be damped down or removed. He therefore compared Lilienthal’s measurements with predictions drawn from two different parts of the theoretical analysis. In one case he computed the lift from the general formula showing that the lift = density X velocity X circulation. In the other he used the pressure lift alone (that is, the theoretical lift minus the leading-edge suction). This latter case created a drag because the resultant was tilted backward. On the basis of cer­tain assumptions about the test conditions, Kutta made his predictions for lift and drag for nine different angles of incidence from -9°, through 0°, to +15°. Overall he found that the theoretical predictions of lift were consistently 10 -20 percent higher than those arrived at by observation. Kutta concluded:

Aus der Tabelle scheint also hervorzugehen, dafi fur die untersuchte gewolbte Flache und fur Luftstofiwinkel unter 15° die beobachtete Hubkraft 80-90 Prozent der errechneten ausmacht—was mit dem Umstande, dafi die theore – tischen Vereinfachungen sicher auf zu grofie Zahlen fuhren mufiten, in Uber- einstimmung steht. Auch fur den Stirnwiderstand ergeben sich einigermafien brauchbare Zahlen. (54)

It follows from the table that, for the curved surfaces that were studied, the observed lift force was 80 -90 percent of the calculated value for angles of incidence below 15°—which constitutes agreement given that the theoretical simplifications were bound to lead to numbers that were too high. Even the values for the frontal resistance are reasonably useful.

In other words, the theory fitted the data tolerably well given the approxima­tions that had been made.

Prandtl took a significant step toward greater realism when he went be­yond the idealization of the infinite wing. But, as von Mises emphasized, Prandtl’s own work rested on numerous idealizations. Prandtl was fully aware of this. He explained, for example, that the lift force was assumed to be small so that changes in the direction of the airflow would also be small. Mathematically this justified the neglect of all but the lowest order of the quantities under consideration and made the theory linear. As we have seen, the wing was replaced by a bound vortex, a lifting line, and was treated as if it had no chord. Central to the process of idealization was the now familiar horseshoe vortex. The metaphor of the horseshoe is strained be­cause the vortices in Prandtl’s model were in the form of straight lines with right-angled bends, whereas horseshoes are curved. How did the schemati – zation acquire this inappropriate name? The answer links together some of the sparse facts about the relation between Prandtl’s work and Lanchester’s book. It also provides material for reflecting more generally on the role played by idealization.

In Lanchester’s Aerodynamics there is a drawing of the vortex system around, and behind, a wing (175). Lanchester’s sketch is reproduced here as my figure 7.14. The likeness is not exact, but Lanchester drew the vortices in a way that looked roughly like a horseshoe. They are certainly much more horseshoe-like than the vortex system made up of the three straight lines that Prandtl used. Although Lanchester himself called the shape a “hoop or half­ring” (174), this description must have been the origin of the “horseshoe” metaphor. The Hufeisen label presumably arose in Gottingen as a natural response to Lanchester’s truly horseshoe-like figure.

Prandtl knew Lanchester’s book, and he knew Lanchester’s drawing. He mentioned it explicitly in one of the few reflective pieces he wrote

about his methods of work. In a talk he gave in 1948, called “Mein Weg zu hydrodynamischen Theorien” (My route to hydrodynamic theory), he re­marked that it was frequently his doubts about existing treatments of a prob­lem that spurred him to new ideas—and he instanced this particular diagram in Lanchester’s book as an example.84 Unfortunately, he did not specify exactly what it was about the figure that struck a discordant note. A probable answer is that the figure looked wrong because Prandtl took it to be a consequence of Helmholtz’s theorems that the trailing vortices would be carried along by the streamlines and, to a first approximation, these would be the straight stream­lines of the free flow. The free-vortex lines would not coincide exactly with a prolongation of the original, straight streamlines (because they would have a slight downward movement), but they would not have the marked, outward curving, horseshoe-like shape attributed to them by Lanchester.85 The defect in Lanchester’s figure was removed in the better, though still approximate, straight-line diagram that Prandtl subsequently used. This showed the trail­ing vortices going straight back from the wingtips.

Was the error in Lanchester’s figure obvious to Prandtl the moment he set eyes on the original diagram, or did it take some time before the problem emerged into view? There are grounds for thinking that the error may not have been immediately obvious. The horseshoe-like diagram was not modi­fied in the German translation of Lanchester’s book made in 1909 by Prandtl’s friends Carl Runge and his wife. Had the diagram seemed obviously wrong from the outset, Prandtl would have mentioned it to his friends, and the mat­ter would have then been raised with Lanchester in the discussions that took place in Gottingen over the translation. The opportunity would have been taken to modify the text in the same way that an opportunity was taken to add a mention of Prandtl’s 1904 boundary-layer paper.

Although Prandtl introduced his quantitative theory in 1910, in the sum­mer semester of 1909 he had already given a series of lectures on the scientific basis of airship flight in which, in addition, he had touched, qualitatively, on the circulation round the finite wing of an aircraft. Some of Otto Fop – pl’s notes of those earlier lectures have survived and are reproduced in Ju­lius Rotta’s beautifully illustrated book Die Aerodynamische Versuchsanstalt in Gottingen.86 Foppl’s lecture notes include a diagram that he presumably copied from one of Prandtl’s own blackboard drawings. The diagram shows the vortices curving out from the wingtips in the way Lanchester had origi­nally presented them. It seems that in 1909 Prandtl had drawn the vortex sys­tem so that it did indeed still look like a real horseshoe. Foppl’s diagram also contains a cross section of the trailing vortices that clearly shows the core of the vortices separated by a distance considerably greater than the wingspan, thus confirming the idea that the vortex lines were not meant to go straight back from the tips. The mere presence of the diagram does not prove that Prandtl had drawn it on the board as an example of truth rather than error, but a probable sequence of events would be this: Prandtl started by accept­ing the (curved) horseshoe picture, as did Finsterwalder, but within a year realized that it was wrong. Henceforth his model had straight lines. Despite this change of mind, the name Hufeisen appears to have stuck and was used, somewhat incongruously, for the simple, straight-line vortex schema that re­placed the original curved horseshoe.87

I shall now comment on the important transition from the simple, straight-line horseshoe schema to the refined version involving an infinite number of infinitesimal horseshoe vortices. The infinity of vortices coming away from the trailing edge creates a “vortex sheet” spread across, and trail­ing behind, the span of the wing. In the simple schema there was a vortex line coming from each tip; now there is something like a continuous train of vor – ticity attached to the rear of the wing. This changes the picture considerably. It also poses a problem. If this picture is right, the earlier picture was wrong, but the supporters of the circulatory theory claimed to have actually seen the simple horseshoe structure. In the first publication to use Prandtl’s theory, Foppl said that the two vortices trailing from the wingtips had been made visible in the wind channel by introducing ammonia vapor. Nor was it just the members of the Gottingen group who claimed to have seen the horse­shoe-like vortices. A similar, though more guarded, claim had been made by Lanchester, who had moved a model aerofoil under water and claimed to have “traced experimentally” the vortices that were postulated in his theory.88 But if these two trailing vortices are now discarded as theoretical fictions, what was it that had been made visible? One possible answer, according to later versions of the theory, was that the phenomenon reported was really

the rolling up of the vortex sheet. Prandtl argued that the sheet was unstable and rolled up at the edges in the way shown in figure 7.15. The rolled-up sheet then decayed into something resembling the two trailing line vortices. Per­haps this is what had been seen.89

There remains a further and deeper question about the move from the single, horseshoe vortex to the infinite number of trailing vortices that now constitute the vortex sheet. I have explained that the single, horseshoe schema could not do justice to what was known experimentally about the distribution of lift along a wing. Greater realism required a non-uniform lift distribution across the span, with zero lift at the tips. Accordingly, Prandtl replaced his single, highly abstract, horseshoe model with an infinite number of similar models. No fundamental principle of the original model was changed in the course of producing the more refined version. In fact, those principles were reproduced an infinite number of times. Can this be right? Can an unrealistic construct be made more realistic by repetition? The refined horseshoe model shows that the answer to this question must be yes.

The earlier discussion of Prandtl’s boundary-layer theory showed that the realism of a theory may be increased even though physically impossible ide­alizations were still present. Now the point can be taken further. Realism may be increased by increasing the number of idealizations. It may sound wrong to say that “realism” is increased, while attributing that increase to the in­creased use of highly “unreal” instruments of thought, such as ideal fluids and infinitesimal vortices, but the discomfiture must be overcome. The essential point is that there is no valid inference from the desirability of greater realism, as that word is normally understood, to the undesirability of idealization. If a theory has been made more realistic, it does not follow that abstractions and idealizations must have been removed or their number diminished. This might, on occasion, be part of the story, but the move to greater realism bears no necessary relation to a reduced number of abstractions and idealizations.

Prandtl and his colleagues were not inclined to be apologetic about the abstractions they deliberately introduced into their theory, nor were they in any doubt that they were grasping reality. As Prandtl insisted to his Ber­lin friend von Parseval, the Gottingen work on vortex theory was successful because of its abstractions, not in spite of them. In discussing a paper that von Parseval had given on the formation of vortices on a wing, Prandtl com­plimented von Parseval on his treatment but contrasted their approaches.90 He put it like this: “Herr Professor v. Parseval hat der Wirbeltheorie, die bei unseren eigenen Arbeiten immer etwas Abstraktes behalten hat (die allerdings gerade durch die bewufit eingefuhrten Abstraktionen zu ihren Erfolgen fuhren konnte), eine anschauliche Deutung gegeben” (63) (Prof. v. Parseval has given an intuitive significance to the theory of vorticity. In our own work it has always been treated rather abstractly [though it is, neverthe­less, precisely because of these consciously introduced abstractions that it has led to success]). Prandtl’s assistant Max Munk surely spoke for the Gottingen group as a whole when he insisted that the formulas of Prandtl’s wing theory represented “die wirkliche auftretenden Vorgange”—“the actual processes that occur.”91 The consciously introduced abstractions were the means by which the real and actuality occurring processes were described.

The stance of Prandtl and Munk, and the striking achievements of the Gottingen approach suggest a bold generalization. Perhaps successful work of this kind will always be based on idealizations and abstractions. If this is cor­rect, then what is really at issue is not whether abstractions are to be used but which abstractions are to be used. Which are to be counted as having a role in the laws of nature and which not? Scientists and engineers themselves, collec­tively, have the responsibility of according or withholding that status and of saying which abstractions and idealizations best describe the actual processes that occur in nature. Different groups may discharge this responsibility in dif­ferent ways. This fact has already been encountered in the different positions adopted by British and German experts with regard to the Stokes equations. Now we have another example. For the German aerodynamic community, unlike the British, the pragmatic success of the circulatory theory of lift, even within a limited technological domain, was evidence enough that the gulf between thought and reality was being overcome.

What is the correct understanding of Taylor’s “Note on the Prandtl Theory” and the mathematical arguments he put forward? What might explain the in­version of its perceived significance? Why did Taylor himself begin that pro­cess when he reworked the conclusion to the original note in his published appendix? Clearly, Taylor was not trying to rehabilitate the old discontinuity theory; he was merely using it to embarrass the supporters of Lanchester and Prandtl. He was showing that there was no unique explanation of the phe­nomena summarized by the Kutta-Joukowsky law.22 Taylor can therefore be seen, at least initially, as putting forward counterexamples in order to make a logical point. He was concerned with what follows, or does not follow, from the standard formulation of the circulation theory of lift. He had caught Glauert out in a hasty inference, but to show that proposition A does not

entail proposition B does not prove that B is false. Taylor’s argument did not establish the falsity of the conclusions that Glauert drew about the results that were emerging from Bryant and Williams’ experiment.

As well as measuring the circulation along contours that enclosed the wing, Bryant and Williams also measured the circulation around contours that did not enclose the wing. This part of their argument remained intact. They di­vided the space around the wing into zones, like tiles on a bathroom wall, and then measured the circulation around each zone (see fig. 9.4). The question they posed was the following: Were these local circulations all zero? Zero cir­culation was required for these contours (that is, contours not surrounding the wing) because that would indicate that the main flow was irrotational, namely, an irrotational motion but with circulation around the wing. Not all of these local circulations turned out to be zero. As can be seen in figure 9.4, there were a number of anomalous values particularly among those recorded near the leading edge. Despite this, enough of the readings were sufficiently close to zero for the measurements to be seen as a vindication of the theory. This result had emerged after Glauert’s preliminary analysis and after Taylor’s original note. It was therefore too late to have played any role in the exchange in the Aerodynamics Sub-Committee, but it was acknowledged in the pub­lished version of Taylor’s note attached to Bryant and Williams’ paper in the Philosophical Transactions.

The new data may have contributed, in some measure, to the change in Taylor’s tone between the unpublished and the published versions. Despite limitations in the experimental design, the overall picture that emerged from the experiment favored the circulation theory. Taylor therefore had little choice but to begin the published version of his comments by accepting that, after all, the flow was mainly irrotational. As he put it: “In their paper ‘An Investigation of the Flow of Air Round an Aerofoil of Infinite Span,’ Messrs. Bryant and Williams show that the flow round a certain model aerofoil placed in a wind channel is not very different from an irrotational flow with circula­tion. There are, however, differences which are considerable in the wake, a narrow region stretching out behind the aerofoil” (238).

The acknowledgment that the flow outside the wake was “not very differ­ent” from irrotational gave the supporters of the circulation theory all they really needed. Taylor had himself identified this as “Prandtl’s fundamental hypothesis,” but though he was now conceding the point he did not linger on the concession. Taylor immediately drew attention to the flow inside the wake, which was nonirrotational. This point was the real focus of his interest. The Aerodynamic Sub-Committee discussions of the preliminary data com­ing from Bryant and Williams, in December 1923, had charged Taylor with the task of differentiating “between the effect due to circulation and that due to eddying on the forces as measured on a complete aerofoil.”23 The “Note on the Prandtl Theory” was his response to this request. In the same spirit, when Bryant and Williams gave their technical report to the committee, Tay­lor drew attention to the apparent presence of local areas of significant circu­lation where there should have been none. Glauert, by contrast, wondered if this result could be an artifact produced by the compounding of small errors elsewhere in the data.24

In taking the line he did in his note, Taylor showed that his thinking fell into the familiar pattern that was characteristic of British work—with the exception of Glauert’s. Taylor’s counterexamples were an expression of the old argument that perfect fluid theory must be false because it predicted zero drag for an infinite wing. The wake was the physical source of the drag, and drawing attention to it and exploring the consequences of its presence, merely underlined the standard objection. If, along with a wake and a viscous drag, the Kutta-Joukowsky law of lift turned out to be approximately true of the flow, then some other reason had to be found to explain the law than the one originally advanced. In a real, viscous fluid, there was no well-defined quan­tity that could be called “the” circulation of the flow. The value of the relevant integral would not be contour-independent but would, in general, vary from contour to contour. This was why Taylor stressed the contour dependence of the experimental results. Taylor, however, was not asserting anything that the defenders of Prandtl’s theory had not granted long ago. In 1915 Betz had made a correction to allow for the role of the wake. There was no inconsistency between what Taylor said in the passage quoted earlier, in which he conceded the generally irrotational nature of the flow, and what Glauert had said origi­nally in his technical report “Aerofoil Theory,” in which he had conceded a viscous wake. Both men acknowledged the presence of rotational and irro- tational flow in the phenomenon before them. The difference between them lay in their reaction to this agreed fact. It was a difference of emphasis and preferred method. Taylor wanted to know where the inviscid approach failed, whereas Glauert wanted to know where it worked. Taylor’s eyes were directed to the viscous wake, whereas Glauert’s gaze was on the nonwake.

This concern with the wake may help explain the inversion that took place in the perception of Taylor’s argument, and even why Taylor himself reex­pressed his original, negative point in an oddly positive way. The ideas Taylor used, negatively, to construct the counterexamples to the circulation theory became resources that could be used, positively, to study the wake. This study rapidly became a subject of research in its own right. The ideas Taylor origi­nally advanced as counterexamples found a new use. Perhaps it was the tran­sition to this new role that gave rise to the later misunderstanding. The new studies of the wake did not displace the circulation theory of lift but came to complement it. The viscous flow inside the wake found a place alongside the inviscid flow outside the wake. Nor did the two merely coexist. Rather, the latter could be seen as the limiting case of the former. As the wing increases in efficiency, so the wake gets smaller. In the limit the wake is simply the vortex sheet behind the wing, which was central to Prandtl’s analysis. Taylor’s viscous, rotational wake becomes, to use Glauert’s word, “evanescent.” Un­derstood in terms of Glauert’s methodology, the reality of the wake was not being ignored but was allowed for in the limiting process by making the right choice of the inviscid flow. The counterexample then becomes identical with the phenomenon it was meant to contradict. Perhaps Glauert had begun to convince Taylor that the seeming contradiction between his counterexamples and the theory were not as logically sharp as it first appeared. Glauert would surely have discussed the problem with Taylor in the time between Taylor’s (unpublished) note and his (published) appendix. If minutes had been taken of these discussions, it might have been possible to trace the process by which Taylor came to reformulate his original doubts.

What is a matter of public record is how Taylor’s argument was deployed for the purpose of studying the wake. Recall that Taylor’s analysis of mo­mentum relations concerned not only lift but also drag. The physical basis of Taylor’s calculation of drag was the idea that drag arises from a loss of momentum in the fluid flow behind the obstacle. His analysis showed that this loss implied a pressure reduction in the wake, namely, a diminution of the quantity called the “total head” or the “total pressure.” (These terms were explained in chap. 2 in connection with Bernoulli’s theorem.) This account of drag was taken up by Fage and Jones at the National Physical Laboratory in a paper published in 1926 in the Proceedings of the Royal Society.25 They cited Taylor’s comments on Bryant and Williams’ work, but they did not read them negatively. They understood them as positive suggestions about the na­ture and measurement of drag and proceeded to do the experiments needed to test them. Bryant and Williams, they said, had explored the velocity of the flow in the wake of a model aerofoil spanning the wind tunnel and had shown that, for all practical purposes, it was two-dimensional. They went on: “In an Appendix to the above paper [by Bryant and Williams], Prof. G. I. Taylor shows that there is good reason to believe, on theoretical grounds, that the drag of an aerofoil can be determined with good accuracy from observa­tion of total-head losses in the wake, provided that these observations are taken in a region where the velocity disturbances are relatively small” (592). Fage explained that the drag under discussion was not Prandtl’s “induced drag,” which was a by-product of the lift, but “profile drag” associated with the shape and attitude of the wing section (592).

Fage and Jones’ experiment was to be carried out on an infinite wing with two-dimensional flow for which the induced drag should be zero. Using the symbol H to represent the total head ^p+1 pq2 j and, like Taylor, neglecting small quantities, Fage and Jones rewrote Taylor’s drag equation in a simpli­fied form as

D = pjH. ds,

C

where “the integration is taken along a line passing through the wake at right angles to the undisturbed wind direction” (594). Outside the wake, H will be constant from streamline to streamline but will vary as the line of integration passes through the wake. For a contour that cuts the wake parallel to the y – axis, the value of the direction cosine l is unity, which explains its apparent absence from Fage’s simplified expression. If Taylor’s analysis was right, the experimenter could measure the drag on a two-dimensional or infinite wing by summing up the losses in the total head across the span. This was what Fage and Jones did using a model wing of 0.5-foot chord mounted, with only a small clearance, right across the 4-foot wind tunnel. The wind speed was 60 feet per second. They calculated the drag from pressure measurements taken in the wake and performed the required integration using graphical methods. They found that most of the loss of total head pressure (H) came from a loss in velocity (q) rather than a reduction in the static pressure (p) of the wake. Finally they compared the predicted drag with the result of their di­rect drag measurements when the wing was suspended on wires and attached to scales. The two methods they concluded were “in close agreement” (593).

A further feature of Taylor’s argument that was given a new employment was his picture of the equal discharge of positive and negative vorticity into the wake (respectively from the upper and lower surfaces of the wing). This also helped to integrate the circulation theory into the study of viscous flow.26 The theorem that the circulation in all circuits enclosing the aerofoil had the same value, if the contour cut the wake at right angles, was, as one later re­searcher put it, “of fundamental importance in the calculations of the lift of aerofoils allowing for the boundary layer.”27 An important sequence of pa­pers starting in the mid-i930s was devoted to this theme, and they all traced their approach back to Taylor’s appendix. New ways were sought to general­ize the old Kutta condition in order to quantify the circulation under more complex and realistic conditions.28

As independent evidence in favor of some version of the circulation theory increased, the original significance of Taylor’s analysis, as a source of counterexamples, decreased. The ideas became consolidated in a new con­text. This may explain why von Karman and Burgers expressed themselves as they did. Perhaps they were not misreading Taylor so much as rereading him. That is, they were reinterpreting his original contribution in the light of later concerns and assimilating his ideas to the new preoccupations of a research agenda in which the circulatory theory of lift was taken for granted. Taylor’s line of thought was now being used to supplement rather than undermine the theory of circulation.

The British economy and the character of British culture provide the back­drop to the episode that I have been investigating. I now want to see how the British resistance to the theory of circulation fits into this broad picture. There are two, starkly opposed theories about the economic fortunes of Britain throughout the nineteenth and twentieth centuries and each carries with it a particular image of British society and British science. How does my story bear upon the dispute between the supporters of these two, opposing theories?

The first theory has been called declinism. The declinists hold that, after its initial lead in the industrial revolution, when the country was led by men who were “hard of mind and hard of will,” Britain ceased to be the workshop of the world and, ever since, has been in a steady state of decline both cultur­ally and economically. The main causes of the decline, the argument goes, are to be found in the antiscientific, antitechnological, and antimilitary in­clinations of subsequent generations of the British elite. The entrepreneurial spirit was drained out of British society, and innovation gave way to inertia. An important role in causing this sorry state of affairs is attributed to the universities. Universities are said to have cultivated the arts and humanities at the expense of science and technology. Literary and genteel inclinations were encouraged rather than more robust industrial and military values.34

The historian Correlli Barnett has formulated an influential version of the declinist theory in his book The Collapse of British Power.35 Barnett places great emphasis on national character. He diagnoses a fatal complacency that infected the British character after victory in the battle of Waterloo. Moral principle rather than self-interest became the dominant motive of political activity. Barnett is clear about the causes. The blame lies with the high-flown sentiments of evangelical religion and the ideology of individualism and free trade. Liberal economic doctrines, he concludes, were “catastrophically in­appropriate” for a Britain facing the growing economies of (protectionist) America and Prussia (98). By the 1860s, the misguided British faith in the “practical man,” along with the weakness of the educational system, had made the country dependent on its commercial and military rivals for much of its more advanced technology (96). By 1914 Britain, with its overextended empire, may have looked like a world power, but it was “a shambling giant too big for its strength” (90). In The Audit of War, Barnett acknowledges that the Cavendish Laboratory made Cambridge a “world centre of excellence” in science but insisted that this was “of little direct benefit to British industry.”36 The lack of industrial and commercial relevance was due to the cultural bias of the universities, particularly Oxford and Cambridge, against “technology and the vocational” (xiii): “Here amid the silent eloquence of grey Gothic walls and green sward, the sons of engineers, merchants and manufacturers were emasculated into gentlemen” (221).

Barnett acknowledges the success of the desperate, last-minute efforts that were made during the Great War to overcome the lethargy and inefficiency of British capitalism. In The Collapse of British Power he describes how the

Ministry of Munitions brought about a “wartime industrial revolution” (113) by setting up more than two hundred national factories for the manufacture of ball bearings, aircraft and aircraft engines, explosives, chemicals, gauges, tools, and optical instruments. But the effort was not to last, and the full lesson was not learnt. British economic performance and British power, he asserts, continued their trajectory of decline throughout the 1920s and 1930s. The defects of the British national character similarly bedeviled the coun­try’s struggle during World War II and, to Barnett’s evident disgust, expressed themselves after 1945 in the electorate’s desire to build a “New Jerusalem”—a welfare state.

This pessimistic picture has been widely accepted, but is it true? That it captures something is beyond doubt, but the basis of Barnett’s account has been challenged by the advocates of a rival picture. They may be called the antideclinists. Antideclinists acknowledge that there was an economic slow­down after 1870 but insist that if this counts as a “decline,” it was a relative, not an absolute, decline. It was almost inevitable as new nations industrial­ized and began to play a role in world trade. Thus in the early 1870s Britain produced 44 percent of the world’s steel, whereas by 1914 it produced 11 per­cent, but, as the economic historian Sidney Pollard put it, “It is evident that a small island with only limited resources of rather inferior ores could not go on forever producing almost half the world’s output of iron or steel; that share had to drop.”37

Pollard is by no means uncritical of British economic policy, but he takes the view that in 1914 the British economy was riding high. Decline, he sus­pects, is a political myth: “the statistics are against this argument.”38 With re­gard to the universities, antideclinists draw attention to the significant role of the British educational system in producing large numbers of scientists and technologists, many of whom have gone into government and industrial ser­vice.39 The declinists also tend to overlook the civic universities that emerged in the late nineteenth century and often worked in close conjunction with local industry.40

David Edgerton has presented the antideclinist case in a series of publica­tions that includes Science, Technology and British Industrial Decline, 1870­1970 and Warfare State Britain, 1920—1970.41 He argues that the declinist view rests on the claim that Britain has not spent enough on research and devel­opment (R&D). The declinist premise is that economic growth depends on R&D, but, says Edgerton, this premise is false: economic growth is largely in­dependent of investment in R&D. In any case, British spending on R&D has long been comparable to, or greater than, its competitors. Rather than being in the thrall of an antiscientific elite, Britain has been a scientific powerhouse during the twentieth century. Since 1901 Britain has won roughly the same number of Nobel Prizes as Germany. By 1929 well over half the students at British universities were studying science, technology, or medicine. In War­fare State Britain Edgerton notes that despite this, “The image of Germans as both militaristic and strong innovators and users of high technology in warfare is still a standard one in popular accounts” (274). It would be closer to the truth, Edgerton argues, to invert the usual stereotypes and apply this description to the British. British military policy has been to invest in the high technology of its navy and air force—and use them ruthlessly against the economy and civilian population of the enemy.

Edgerton has also marshaled the neglected evidence about the massive involvement of British scientists in governmental and military roles. The declinists ignore the historical, statistical, and economic data that support the view of Britain as a technological and militant nation. For Edgerton the declinist theory is not detached, historical scholarship; it is an ideology that expresses the partisan claims of a disgruntled political lobby. The unending complaint that British universities ignore technology and shun the scientific – military-industrial complex is actually the expression of an insatiable demand for ever more engagement. As Edgerton puts it: “I take the very ubiquity in the post-war years of the claim that Britain was an anti-militarist and anti­technological society. . . as evidence not of the theory put forward, but of the success (and power of) the militaristic and technocratic strands in British culture” (109).

How does my study fit into this debate? Does the British resistance to the circulation theory of lift provide evidence in favor of the declinist, or the antideclinist, view? At first glance it would seem to support declinism. I have identified an elite group of academically trained scientists who turned their backs on a workable, and technologically important, theory in aerodynamics. They left it to German engineers to develop the idea of circulation that had originated in Britain. This lapse seems to confirm the familiar, declinist story about the weaknesses of British culture. Rayleigh’s strengths lay in research rather than development, and as one commentator has put it, “Rayleigh’s weakness in this direction was an example of the British research and devel­opment effort in general.”42 The way Lanchester was sidelined surely epito­mizes the resistance to modernization. Putting aeronautics in the hands of a committee of Cambridge worthies and country-house grandees reveals the amateurism so characteristic of British culture.43

A closer examination of the episode casts doubt on this declinist read­ing. First, recall how closely the elite British scientists whom I have studied worked with the government and the military. From 1909 they were given a role close to the center of power, and they embraced it readily. The first place that Haldane went for advice, as the government minister responsible for military affairs, was Trinity College. The University of Cambridge provided the mathematical training of a significant number of Britain’s leading aero­dynamic experts, including Rayleigh, Glazebrook, Greenhill, Bryan, Taylor, Lamb, Southwell, and of course Glauert, who later championed the circu­latory theory. The intimate connection between academia and the military evident in the field of aerodynamics does not, in isolation, refute the declinist picture, but it certainly runs counter to it. It exemplifies the policy of high – technology militarism that has long characterized British culture but that is ignored by declinists.44

Second, the initial opposition to the circulatory theory must be put in context. The work of the Advisory Committee covered a broad range of other aerodynamic problems as well as lift. Along with the National Physical Labo­ratory and the Royal Aircraft Factory at Farnborough, the committee was deeply immersed in the theory of stability and control. We should not forget the words of Major Low, who recommended a comparative perspective. He argued that the British and the Germans both had their strengths and weak­nesses, and where one was strong, the other was weak. The British strength was stability.45 In this area the same group of experts who fell behind in the study of lift excelled and led the world. And they did this by using their Tripos, or Tripos-style, mathematics. In this case they did not call on fluid dynamics but on the equally venerable and equally abstract dynamics of rigid bodies. I have described the central role played in this area by the Cambridge-trained G. H. Bryan, who used the work of E. J. Routh, the great Tripos coach.

The conclusion must be that the same cultural and intellectual resources that had failed in the one case, the theory of lift, succeeded in the other, the theory of stability. British experts may have faltered over the theory of lift be­cause they were mathematical physicists rather than engineers, but it was not because they were effete or antimilitary or significantly antitechnological. Sta­bility is as much a technological problem as is lift. Nor did these experts falter over lift because they were torpid and unresponsive in the face of novelty and innovation. On the contrary, they rejected the circulatory theory of lift pre­cisely because it lacked novelty. It was novelty that the British experts wanted, not the old story of perfect fluids in potential motion. They were seeking in­novations in fluid dynamics and looking for new ways to address the Stokes equations. The theory of decline therefore points the analyst in precisely the wrong direction to appreciate the true nature of the British response.

The lesson to be learned is that broad-brush, pessimistic macro­explanations will not suffice. They do not fit the facts of the case I have studied.46 In Barnett’s words, British cultural life is identified as “stupid,” “le­thargic,” “unambitious,” and “unenterprising.”47 Some of it certainly is, but an unrelieved cultural pessimism can shed no light on the specific profile of success and failure that I have been analyzing. Declinist pessimism does not possess the resources to account for the successes of British aerodynamics that went along with the failures. In the event, it cannot even illuminate the failures themselves. Barnett’s contemptuous adjectives do no justice to the clever and ambitious British mathematicians and physicists whose work has been examined. His picture of pacifist tendencies hardly accords with the speed with which young Cambridge mathematicians volunteered for active service in 1914. What is needed, and what I have given, is a micro-sociological explanation that addresses both success and failure in a symmetrical manner. My account of the British resistance to the theory of circulation does not ap­peal to the vagaries of national character or broad, cultural trends. Like other studies related to the Strong Program, it rests on the technical details of the methods used by clearly identified scientific groups and the character of the institutions that sustained them.48