Category The Enigma of. the Aerofoil

Knowing the predicted pressure distribution along a specified aerofoil opens up the possibility of subjecting the circulation theory of lift to a demand­ing empirical test. Does the predicted distribution correspond to the real

distribution in as far as it can be measured? In 1915, two years after Blumen – thal’s theoretical analysis, a detailed experimental study was published in the Zeitschrift fur Flugtechnik that was designed to answer this question. The pa­per was by Albert Betz, Prandtl’s close collaborator in Gottingen (fig. 6.10). It was called “Untersuchung einer Schukowskyschen Tragflache” (An investiga­tion of a Joukowsky wing).60

Betz used one of Blumenthal’s profiles and worked with a model wing that had a span of 50 cm and a chord of 20 cm. It had a curvature (f/l) of 1/10 and a thickness ration (8/l) of 1/20 and so corresponded exactly to the second of the four profiles described by Blumenthal (that is, the one shown in fig. 6.9). Betz’s aim was to use wind-tunnel data to test Blumenthal’s predicted lift and pressure distribution.

The model wing-section was manufactured from metal plate in the form of an airtight, hollow body and made to conform as precisely as possible to the theoretical, Joukowsky profile. Following Fuhrmann’s work on model airships, the wing was fitted with bore holes and the hollow interior was connected by a thin pipe leading from the wingtip to a manometer. This enabled pressure measurements to be taken at a number of points on the surface along the chord of the wing. Measurements were taken with one hole at a time exposed while the other holes were smoothly plugged. The line of bore holes was not positioned at the center of the span but was displaced a few centimeters to one side. This was to avoid interference to the flow of air over the holes from the strut that had to be attached to the wing in order to hold it rigidly in place in the wind tunnel. As well as the pressure, Betz also needed to know the overall lift and drag of the wing. For this the wing had to be suspended on a balance so that force measurements could be made. Dur­ing this phase of the experiment, the pipes leading to the manometer were disconnected and all the bore holes plugged.

It was necessary to make sure that the experimental arrangement pro­vided a good approximation to the infinite wing presupposed in the math­ematics. Joukowsky had simply made his wing section run from the top to the bottom of the shallow Moscow wind tunnel. This is the basis of all attempts to realize a two-dimensional flow, but Betz put a lot of effort into refining the technique. His aim was to make the test section as free as possible from disturbing effects produced by the walls of the tunnel and the join between the walls and the ends of the wing. An elaborate system of auxiliary sidewalls, gaskets, and seals was designed and tested to ensure a uniform flow across the experimental cross section of the wing. Once he had an acceptable approxi­mation to two-dimensional flow, Betz’s apparatus gave him two sets of data: (1) direct measurements of lift and drag and (2i) pressure measurements dis­tributed over the surface of the wing.

The direct measurements of lift and drag showed the familiar pattern, which partially conformed to, and partially violated, theoretical expectations. The observed lift increased in the predicted, linear fashion with angle of in­cidence, but only from about -9° up to about +10°, at which point the wing stalled. Even over this range the predicted lift was significantly higher than the observed lift. In fact, the observed lift was only about 75 percent of the predicted value. And, of course, there was an observed drag when, theoreti­cally, it should have been zero. There was also another general feature of the flow that Betz observed. Theoretically each angle of incidence should cor­respond to one, and only one, value of the lift. Betz found that if he took a sequence of readings in which the angle of incidence was increased in a stepwise fashion, and another sequence in which it was decreased, a given angle might correspond to one value of the lift in one sequence and another value in the other. There were two values of the lift corresponding to each of these angles, not one. This effect was particularly noticeable above the stalling angle. Thus, at +15°, the coefficient of lift had the values of 0.68 and 0.55. Such a phenomenon fell wholly outside the scope of the theory.

The most important results, however, were those relating to the distri­bution of pressure. Here Betz’s graphs of the manometer readings showed a definite similarity to the theoretical graphs prepared by Blumenthal and his colleagues at Aachen. Betz’s results are shown in figure 6.11. Note that

Betz used a convention different than Blumenthal’s when drawing his dia­grams, and the data for the upper side of the wing are now placed below the base line. Significantly, the general shape of the graph derived from theory and that of the graph derived from experiment were the same. Betz, how­ever, pressed the comparison into greater detail. He was interested in getting information about the residual deviations between theory and reality, “die Abweichungen der Theorie von der Wirklichkeit” (173). This was the stated purpose of the experiment. He therefore drew attention to where the empiri­cal distribution differed from the theoretical distribution. The areas under the empirical graphs were clearly not the same as those under the theoretical graphs. These areas were proportional to the lift, and the theoretical area was significantly greater than the observed area. This was consistent with the fact, mentioned earlier, that the directly measured lift was less than the theoreti­cally predicted lift. What was the cause of the difference, and what should be done in response to it?

Like Fuhrmann, Betz located the source of the difference between the the­oretical and empirical flow in the tail region. Theoretically, if the Kutta condi­tion is satisfied and the wing profile is that of a pure Joukowsky contour, and if the air acts like an ideal fluid, then the flow along the upper surface will meet the flow along the lower surface in a smooth way at the trailing edge. In reality, however, the air did not behave in this way at the trailing edge, so Betz made a conjecture. It was a characteristically Gottingen conjecture (see fig. 6.12).

Betz suggested that, although the flow of air along the lower surface runs smoothly along the common tangent, the flow along the upper surface does not. Rather, it detaches from the upper surface before reaching the trailing edge, and this leaves a gap between the two flows. The intervening space be­tween the flows, said Betz, constitutes a turbulent wake filled with “Karman vortices” (177).

Betz argued that the effect of this separation is twofold. First, it disrupts the pressure relations in the vicinity of the trailing edge and disturbs the equi­librium between the forward-pointing and backward-pointing components of the pressure distribution. Since it is this equilibrium that generates the zero drag of an (ideally) efficient aerofoil, the disturbance must be a contributory cause of the observed drag. Second, the vortices in the wake draw off energy, and this has the effect of lowering the circulation around the aerofoil and hence diminishes the lift. Betz conceded that it was difficult to analyze these processes rigorously but suggested a simple (and intriguing) way to model the situation using the resources of inviscid theory. He proposed rejecting the Kutta condition and relocating the stagnation point. Whereas Kutta had used the position of the stagnation point to fix the amount of circulation, Betz reversed the process. He used the amount of circulation to fix the stag­nation point.

Betz began with the value for the lift at a given angle of attack that he had found in his experiment. He then inserted the value into the basic Kutta-

Joukowsky theorem L = p V Г. Because he knew the density and velocity of air in the wind tunnel, the formula allowed him to deduce the value of the circulation. He then used this empirical value of the circulation to tell him where the rear stagnation point must be relocated according to the theory of inviscid flow. (Betz was working with a Joukowsky profile, so this point could be calculated by transforming the flow around a circular cylinder.) Given that the empirical value of the circulation is lower than the theoretical value, the stagnation point is on the top surface of the aerofoil, rather than precisely at the trailing edge. It was then possible to replot the theoretical speed and pres­sure distributions and compare them afresh with the empirical curves. The question was whether the revised location of the stagnation point brought the empirical and theoretical graphs onto closer accord. The method automati­cally equalizes the areas under the empirical and theoretical curves but the question remains: do the distributions agree? Betz’s revised graph, superim­posed on the empirical curve, is shown in figure 6.13. The improvement is clear. The graphs are now almost identical. Betz pronounced the agreement to be “extraordinarily good.” As he put it,

Sehen wir von der nachsten Umgebung der Hinterkante ab, fur die ja Voraus – setzungen der theoretischen Stroming vollstandig andere sind wie in Wirk – lichkeit, so mussen wir die Ubereinstimmung der beiden Kurven aufieror – dentlich gut bezeichnen. (177)

If we disregard the vicinity of the rear edge, where indeed the presuppositions of the theoretical flow wholly differ from reality, then we would have to char­acterize the agreement of the two curves as extraordinarily good.

Betz had thus brought theory and experiment into closer accord. His proce­dure involved interweaving them in an interesting way, and the methodologi­cal principles implicit in the process are worth looking at with some care.

The Kutta condition had become established as one of the central as­sumptions of the circulation theory. Could Betz really afford to modify its role in this way? The overriding advantage of the Kutta condition was that it avoided the need for the ideal fluid to move around the trailing edge at an in­finite, and physically impossible, speed. How did Betz justify the reintroduc­tion of infinite speeds given that the need to avoid them was routinely cited whenever the Kutta condition was invoked? The point was addressed explic­itly in the paper. The argument was as follows: Since perfect fluid theory is known to be unrealistic from the outset, said Betz, one more piece of unreal­ity hardly matters. The entire approach is an artifice, so this should not be disturbing. The infinite speeds are just the way that the complicated, physical

processes at the trailing edge receive some manner of recognition within the terms of the theory. Their presence in the analysis simply indicates that fur­ther assumptions need to be introduced to mediate between reality and the idealized picture. Outside the wake, the flow can be reasonably modeled by ideal-fluid theory, and the presence of the wake can be taken into account by lowering the value of the circulation. This approach can be seen as the first step toward a better account of the phenomenon. As Betz put it,

Dafi dabei ein Umstromen der scharfen Hinterkante stattfinden mufite, was praktisch unmoglich ist, braucht uns nicht zu storen, da ja die Stromungen. . . bis zu dem gemeinsamen Ablosungspunkt nur ein theoretischer Ersatz sind fur die in Wirklichkeit vorhandenene Wirbelbewegung. (177)

That this would have to result in a physically impossible flow round the sharp trailing edge need not disturb us. This is because the flow. . . up to the com­mon point of separation is only a theoretical substitute for the vortex motions that exist in reality.

The assumptions behind this talk of a “theoretical substitute” (“theoretischer Ersatz”) can be clarified by noting what Betz had said about d’Alembert’s paradox. Notoriously, the theory developed by Kutta and Joukowsky pre­dicted that a wing will have zero resistance. Betz, however, defended the use of an inviscid theory as an approximation, “even though it does not permit any statements to be made about the resistance” (“trotzdem sie uber den Widerstand nichts auszusagen vermag”; 173). What did Betz mean by this? Surely, the theory does permit a statement to be made about resistance. In­deed, it requires that a statement should be made: namely, the false statement that the resistance is zero. Betz knew this, so what he must have meant was that the theory does not permit any useful statement to be made. The theory doesn’t shed any light on the resistance. His question was: To what practical purpose can the theory be put? The theory was being viewed as a tool rather than a body of propositions. Perfect fluid theory is a useful tool for certain purposes but not for others. Betz was telling his readers that questions about the utility of the theory, rather than its literal truth, should be uppermost in their minds. That is why they should not be unduly disturbed by theoretical deductions that entail infinite speeds.

A number of significant changes, both organizational and personal, took place in the higher reaches of British aeronautics at the end of the war. The size of the aeronautical section at the National Physical Laboratory had grown considerably during the conflict. Starting from three or four active workers in 1909, the section had expanded to around forty by the time of the armistice.39 Predictably, the return of peace meant that the budget was now to be cut back. Lord Rayleigh had died in 1919, and the Advisory Committee he had guided for a decade was formally dissolved and reconstituted as the Aeronautical Research Committee (ARC). The new committee held its first meeting on May 11, 1920.40 Glazebrook was given the job of restructuring it and preparing it for its new peacetime role. The National Physical Laboratory and the Aero­nautical Research Committee now came under the aegis of the newly formed Department of Scientific and Industrial Research (DSIR).41 Horace Lamb had been appointed to the Aerodynamics Sub-Committee in July 1918 and later joined the full committee.42 In an attempt to avoid the old hostility between the scientists and the manufacturers, there were now to be representatives of industry on the committee. J. D. North, of Boulton Paul, was appointed to the Aerodynamics Sub-Committee to represent the Society of British Aircraft Constructors. Bairstow left the National Physical Laboratory in 1917 and took up a post with the Air Board, the precursor to the Air Ministry, though he continued to serve on the new committee.43 Bairstow then moved again and become the Zaharoff Professor of Aviation at Imperial College, London. Sir Basil Zaharoff, who financed the chair, was an international arms dealer.44 Shortly afterward Emile Mond provided the money to set up a chair in aero­nautics at Cambridge in memory of his son killed flying on the western front. This chair was taken by Melvill Jones.45 Bairstow’s post as superintendent of the Aerodynamics Department at the NPL was taken over by Southwell, who moved from Farnborough to Teddington. Lanchester, who sometimes felt that Rayleigh was the only sympathetic member of the committee, left a year after Rayleigh’s death. Lanchester had been assiduous in his duties but had al­ready resigned from the Aerodynamics Sub-Committee in December 1918.46 Now that the emergency of the war was over he felt able to cite pressure of work as a basis for leaving. In his letter to the chairman of the Aerodynamics Sub-Committee he expressed “great pleasure in having been able to serve the committee,” but the retrospective account he gave of his departure from the full committee was very different in tone. He complained that he had been sidelined, snubbed, and deliberately edged out by Glazebrook.47

At the moment that Lanchester left the Whitehall scene feeling, justi­fiably, that his ideas had been ignored, moves were under way that would eventually lead to the triumph of the circulation theory he had pioneered. Two things happened. First, on November 13, 1920, Southwell received a let­ter from Prandtl, who sent him some up-to-date papers on wing theory and material from the Technische Berichte. Prandtl explained that his action had been prompted by his meeting with William Knight. Knight had apparently told Prandtl that Southwell wanted to get hold of information about develop­ments at Gottingen. Southwell replied on November 29 with thanks and ten­tatively asked Prandtl for details about his wind tunnel and the techniques for keeping the flow steady. He also stressed that the exchange with Prandtl had to be considered personal rather than official because of the British govern­ment’s policy of restricting formal contact with German institutions. Prandtl sent Southwell the required data about the air flow and said that more in­formation would soon be published in a volume to be titled Ergebnisse der Aerodynamischen Versuchsanstalt zu Gottingen.48

The second development was that two Farnborough scientists, Robert McKinnon Wood and Hermann Glauert, both members of the Chudleigh

set, were sent to Germany to report on the situation. McKinnon Wood, a product of the Cambridge Mechanical Sciences Tripos, was deputy director of the Aerodynamics Department at Farnborough and worked on propel­lers and the experimental side of aerodynamics.49 Hermann Glauert (fig. 8.3) had studied mathematics at Trinity College, Cambridge, where his circle of friends included David Pinsent, G. P. Thomson, and Ludwig Wittgenstein.50 He graduated with distinction in the first class of part II of the Tripos in 1913 and won an Isaac Newton studentship in 1914 and the Rayleigh Prize for mathematics in 1915.51 Glauert was born in Sheffield. His mother was an Englishwoman who had been born in Germany, while his father, a cutlery manufacturer, was German but had taken British citizenship. Originally spe­cializing in astronomy, Glauert published a number of papers on astronomi­cal topics at the beginning of the war and then, through a chance meeting with W. S. Farren, he was appointed to the staff of the Royal Aircraft Factory in 1916.52

Based in the Hotel Hessler in Charlottenburg, Glauert wrote on Janu­ary 21, 1921, to make contact with Prandtl and ask if was possible to arrange a

visit to Gottingen.53 The approach could not have been more different from Knight’s. Knight had sent a typed letter, in English, on elaborately headed NACA notepaper. The letter was replete with office reference numbers and subject headings and was introduced with a flourish of (questionable) diplo­matic credentials.54 Glauert penned his note in German on a modest sheet of unheaded paper. He introduced himself as a fellow of Trinity who worked at Farnborough and explained that he was very interested in the reports shown to him by his friend Herr Southwell. Could he and his friend Herr Wood, also of the Royal Aircraft Factory, come along next Monday? The visit duly took place but cannot have been an extended one because on February 2 Glauert was writing from Farnborough (again in German) to say that he and Wood were safely home after a thirty-six hour journey. All of the technical material that Prandtl had given them, he reported, had been carried over the border without difficulty. In return Glauert sent Prandtl a copy of Bairstow’s new Applied Aerodynamics.55 It was, he said, currently the best English book on aerodynamics.

Bairstow’s Applied Aerodynamics, published in 1920, offered a massive com­pilation of design data from the aerodynamic laboratories which, for Bair – stow, primarily meant from the National Physical Laboratory. It was com­prehensive and detailed but, as far as lift and drag were concerned, heavily empirical. The circulation theory of lift was placed on a par with the dis­continuity theory and rapidly dismissed. Both theories were said to be based on “special assumptions,” that is, ad hoc devices designed to get around the fatal zero-drag result. Kutta’s work, according to Bairstow, offered no more than a “somewhat complex and not very accurate empirical formula” (364). No account, he complained, was given by Kutta or Joukowsky of the critical angle of stall. Bairstow admitted that Joukowsky had found a way to avoid the infinite speeds at the leading edge of a wing profile, but he spoke of the Joukowsky transformation as if it were little more than a mathematical trick. Bairstow called it a “particular piece of analysis” and did not deem it suf­ficiently important to explain it to the reader. Prandtl must have perused Glauert’s gift with mixed feelings. He would have agreed with all of Bairstow’s facts but none of his evaluations. In particular, he would surely have dissented from Bairstow’s conclusion that it “appears to be fundamentally impossible to represent the motion of a real fluid accurately by any theory relating to an inviscid fluid” (361). Wasn’t this exactly what Prandtl and his colleagues had just done for the flow of air over a wing?

It is clear from the subsequent letters exchanged between Glauert and Prandtl that, during the visit, their conversations had been confined to tech­nical matters. Prandtl was now keen to discuss politics as well as aerodynam­ics. He was distressed by the economic and political situation, particularly the stance of the French and the severe reparations that were being demanded. Glauert expressed agreement with much that Prandtl said on these topics, for example, with the “absurd restrictions that have been placed on the develop­ment of German aviation,” but in his replies he encouraged Prandtl to see things in a less pessimistic light. Glauert explained that not everyone in Brit­ain agreed with these policies, and he thought there were strong economic reasons why, sooner or later, they would be modified. Writing now in English, he drew Prandtl’s attention to the influential arguments of the Cambridge economist John Maynard Keynes and mentioned that opposition to punitive sanctions was also part of the official policy of the Labour party.56 He even in­cluded a reassuring cutting from the correspondence columns of the Times.57 The concern was not just personal; it was also professional. Glauert was wor­ried that Prandtl would become so antagonized by allied policy that he would cease to take part in scientific exchanges. The anxiety was more than justified. The academic atmosphere in the immediate postwar years was a poisonous mixture of bitterness, intransigence, boycott, and counterboycott.58

The immediate result of the Glauert-Wood visit to Germany was the production of two confidential reports. In February 1921 McKinnon Wood produced Technical Report T. 1556, “The Aerodynamics Laboratory at Gottingen.”59 He argued (contrary to government policy) that Gottingen should be included in any future international trials that were envisaged to clarify the discrepancies that existed between the results of different labo­ratories.60 When the results of the British and Germans were compared, McKinnon Wood noted that the Gottingen channel gave the same lift and drag, but always for an angle of incidence smaller by about one degree. He also studied and reported on the complicated “three-moment” balance mechanism used to measure the aerodynamic forces. A blueprint of the bal­ance was included in the report. He judged that the Gottingen balances were “very inferior” in sensitivity to the British but then conceded that “our bal­ances and manometers are unnecessarily sensitive for most of the work for which they are required” (14). McKinnon Wood concluded by saying that “Mr. Glauert discussed Prandtl’s aerofoil theories with him and obtained some further papers. A discussion of these will be embodied in a separate paper (T. 1563) which Mr. Glauert is writing” (21). The “discussion” to which McKinnon Wood alluded turned out to be a piece of brilliant advocacy that was undoubtedly a major factor in undermining resistance to the circulation theory in Britain. Glauert had a gift for clear exposition and for seizing the essentials of the subject. Once he had accepted that Prandtl’s theory repre­sented the path to follow, Glauert produced a notable series of papers and reports explaining, testing, and developing the achievements of the Gottin­gen school. He corrected inadequate formulations and produced important extensions of the theory, as well as confronting the skeptics.

What made Glauert special? Why did he, with his impeccable Tripos background, strike out in a direction that had hitherto been unattractive to experts who shared with Glauert the intellectual culture of the “Cambridge school”? The “practical men” had always been divided over Lanchester’s the­ory of lift, but the “mathematicians” had been unanimous in their skepti­cism. Why did Glauert break ranks? No definitive answer can be given to this question, though one fact stands out and invites speculation. The Ger­man name, the German father, the command of the German language may have generated some affinity with the body of German work that was under consideration. These facts distinguished Glauert from British experts such as Bairstow who did not have the command of German that would have enabled them to read the literature or converse with Prandtl.61 (At that time Prandtl had little knowledge of English.) Of course, given the bitterness of the war, personal links to Germany might have had quite a different effect. Such links could be sources of difficulty, and there is evidence that they caused prob­lems, and some inner turmoil, for Glauert. Referring to the outbreak of war in 1914, Farren and Tizard said of Glauert: “His German descent was an em­barrassment to him, and he wisely decided to stay where such trivial matters did not assume the importance that they did elsewhere, and where he could work in peaceful surroundings, though not with a peaceful mind. His friends were far afield, and as time went on he became more and more restless and concerned with the difficulty of his position.”62

Some people in Glauert’s position would have kept their distance from all things German, and even shed their German name.63 One might specu­late that, in Glauert’s case, the balance in favor of the circulation theory was tipped by the opportunity to meet members of the Gottingen group. His visit to Germany enabled him to explore the mathematics of the circulation theory with Prandtl face-to-face. Others had visited Gottingen before the war, but British experts did not have a great deal of direct contact with their Ger­man counterparts.64 Even here it is necessary to be cautious about the im­pact of personal contact. Glauert was impressed by the circulation theory before he went to Germany. Doubts and qualifications dropped away after the visit to Gottingen and his advocacy became more confident, but he had begun to explore the theory through what he read in Southwell’s copies of the Technische Berichte. Farren and Tizard suggest that exposure to engineer’s shoptalk in the Chudleigh mess at Farnborough during the war made Glauert sympathetic to the needs of engineers and hence (one may suppose) to the theoretical approaches adopted by the engineers. Beyond this, little can be ventured in terms of explanation. It must simply be accepted that, equipped with the recent papers, Glauert made it his business to explore the Gottingen theory in great detail. He became committed to it, even when this led him to diverge from such authorities as Leonard Bairstow, Horace Lamb, R. V. Southwell, and G. I. Taylor.65

Glauert would have known that, however cogent he made his book, he could not meet all the demands of his intended audience. The diversity of interests that would inform the response would pull in opposing directions. The struc­tural tensions, present in British aerodynamics from the outset, were still at work. By its very nature, Glauert’s Elements of Aerofoil and Airscrew Theory could not satisfy the prejudices of both the practical engineer and the math­ematical physicist. Indeed, the book was designed to bring about a change of approach in both parties. Until it had worked its effect it was bound to be viewed with a certain reservation from both sides, even if, at the same time, its virtues were acknowledged.

The review that appeared in the Journal of the Royal Aeronautical Society was signed “A. R.L.” With its mixture of bluff praise and barbed comment, the review was such that no regular reader would have failed to recognize it as the work of Major A. R. Low.56 Glauert was identified as one (but only one) of the leading exponents of the Lanchester-Prandtl approach, and the Ele­ments was welcomed as (perhaps) the first full-length book on the subject in the English language. There was the hint that engineers might find Glauert’s discussion too advanced, and Low strongly recommended that students read a work by H. M. Martin “as an introduction to the volume under review, and, as well, for Mr. Martin’s mastery of elementary exposition” (167).57 Low simultaneously praised Glauert for the adequacy of his general references, which would “introduce the reader to the most important German work,” and criticized him for not citing Fuchs and Hopf’s Aerodynamik of 1922, which “quite evidently influenced the author, both as to selection and arrangement of materials” (168). The book by Fuchs and Hopf was broader in scope than the Elements, covering both lift and stability, and Low had reviewed it in the Aeroplane. While he had praised their treatment of lift, he had been scathing about their treatment of stability.58 Low acknowledged Glauert’s originality in using the method of images to arrive at a formula for tunnel interference effects in the case of rectangular (as distinct from circular) tunnels but quib­bled at an “unnecessary reference to Hobson’s Trigonometry” (168) to deal with a mathematical point that Low considered elementary.59 Low concluded his review by describing the Elements as “an important contribution to Eng­lish aerodynamic literature” and (high praise indeed) as a book that “should be of the greatest value to all designers of aircraft” (168).

Approaching the Elements from the direction of the mathematician rather than the engineer, R. V. Southwell reviewed it for the Mathematical Gazette.60 He praised Glauert’s “power of concise exposition” (394) and said the book gave “an admirable account of a fascinating theory.” It could be recommended as “indispensable to every student of modern aerodynamics” (395). But, as well as offering praise, it is clear that Southwell was taking care to locate Glauert’s achievement in a particular way. He began by noting that when Mr. Asquith first appointed the Advisory Committee for Aeronautics in 1909, “nothing seemed more certain than that aerodynamics must develop

as a purely empirical science” (394).61 Theoretical hydrodynamics was not sufficiently developed to take account of both inertial and viscous forces. Today, said Southwell, that “difficulty is not yet overcome, but it has been turned” (394). Prandtl’s wing theory is not “an exact theory,” but Prandtl “has supplied what for practice is almost as useful—a theory which can pre­dict” (394).

Southwell then clarified his distinction between exact and predictive theories. Consider Glauert’s chapter 8, which contained an account of skin friction and the origins of viscous drag. Southwell granted that Glauert’s brief treatment was appropriate given the limited purposes of the Elements but ex­pressed the hope that Glauert would produce a follow-up volume to expand the “somewhat slender outline” of the present chapter. The follow-up vol­ume would call for a “slightly altered arrangement” of the material. It appears to me, said Southwell, that

we ought to recognise not one “Prandtl theory,” but two. The first forms the main subject of the present work; its methods are those of the classical theory, and its assumptions, based on Lanchester’s picture of the flow pattern, are justified, ultimately, by its success in prediction. The second, which develops the notion of the “boundary layer” is more fundamental, more difficult, and (probably) less productive of concrete results than the first; its aim is to ex­plain the circulation round a lifting wing in terms of the known equations of viscous flow. (395)

The implication was that Glauert had adopted an “arrangement” of his material that did not adequately recognize the difference between the two theories. Glauert ran these two distinct theories together and aspired to a “combined” presentation. This may help the student, said Southwell, but it cannot do justice to either theory because “their methods are too distinct to permit a really satisfactory blend” (395). He did not believe that they could be combined in the way that Glauert wanted. “For the combined theory seeks to bring phenomena, in their very essence dependent on the viscosity of the fluid and its interaction with the solid boundary, within the scope of analysis which he knows is strictly applicable only to vortex motions existent through­out all time in a fluid devoid of all viscosity” (395). Southwell thus insisted on keeping apart what Glauert had sought to bring together. What the author had aspired to unify, the reviewer saw as incompatible. The themes invoked in Southwell’s review were familiar and characteristic of the British experts: there was the desire for a “fundamental” theory based on Stokes’ equations, a commitment to the “essential” difference between real and perfect fluids, and the appeal to the eternal character of vortices in a perfect fluid, that is, to Kel­

vin’s theorem. That Glauert, like Prandtl, was deliberately trying to overcome the idea that there is an “essential” difference between real and perfect fluids finds no recognition. Southwell acknowledged in Glauert’s unified presenta­tion not a principled methodological stance but a mere pedagogical expedi­ent, an “arrangement” of material to help students—and an arrangement that could not be sustained in the face of reality or in the pages of a more advanced treatise.

Southwell said that the views he expressed “imply no criticism” of Glau – ert’s book. The claim may look disingenuous but I think it should be accepted as authentic. The words would make sense if Southwell were reading Glau­ert’s book as an exercise in technology rather than physics. Once Prandtl’s wing theory was understood as no more than an instrument of prediction, as something that could be assessed using purely pragmatic criteria, then the real business of science could be thought of as proceeding in parallel to the technology. There would be no need for any quarrel between those engaged in the two distinct sorts of activity, provided they were kept apart and not confused with one another. Thus Southwell could honestly declare that he was not criticizing Glauert’s book but simply making it clear what manner of book it was, and what criteria were appropriate for its assessment.

This left just “one small detail” (395) that Southwell certainly wanted to criticize in an explicit way. He was worried about the imaginary roller bear­ings that Glauert interposed between a fluid and a material body or between two layers of fluid moving in different directions or with different speeds. References to roller bearings cropped up at a number of points in Glauert’s book, for example, on pages 95, 100, and 117, and were represented diagram­matically on page 131. Southwell thought such talk was misguided, and he implied that Glauert should know better. Vortices don’t behave like roller bearings, and it won’t help the beginner to understand “the purely math­ematical concept of vorticity” (395), that is, the technical definition of the rotation of a fluid element. Southwell’s point was that “vorticity,” as the term is used in fluid dynamics, can be present when nothing in the flow behaves like a “vortex,” as that term is used in common language, that is, nothing is swirling, rolling, or rotating. For example, mathematically, “vorticity” is pres­ent when two immediately adjacent layers of ideal fluid move horizontally with uniform but different speeds. All the fluid in the respective layers moves in straight lines, but for the mathematician, this phenomenon is equivalent to an infinitely thin sheet of vorticity between the layers. Talk of “roller bear­ings,” however, will produce an incorrect picture in the mind. The begin­ner “will misunderstand either the vortex sheet, or the action of roller bear­ings” (395). The harshest criticism was thus directed at Glauert’s engineering imagery. Southwell was not, in general, against visualization.62 The complaint was against the way that viscous processes and the viscous boundary layer were represented in nonviscous terms.63

Despite these reservations, the publication of Glauert’s Elements in 1926 represented the de facto victory of the circulation theory of lift among Brit­ish experts. The theory and references to Glauert’s exemplary account of it found their way into all subsequent treatises and textbooks, such as Lamb’s Hydrodynamics and Ramsey’s Treatise on Hydromechanics. The victory was, of course, underpinned by the steady accumulation of evidence from experi­mentalists such as Fage.64 The increasingly secure position of the circulation theory was, however, of a qualified kind. The victory was no simple rout of the opposition. The situation might be described with the use of political metaphors by saying that territory was conceded and new spheres of influ­ence agreed on. The power of the circulation theory had been demonstrated, and a certain zone of occupation was now recognized—though not the full legitimacy of what had taken place. The task now was to get on with life under the new dispensation. In the Great War, Germany may not have prevailed, but in the field of practical aerodynamics a new respect was accorded to the circulation theory and Prandtl’s wing theory. In 1927 Prandtl was invited to London to deliver the Wright Memorial Lecture to the Royal Aeronautical Society and to receive the Gold Medal of the society.65

There had been a previous suggestion that Prandtl might give a talk, which had been conveyed via Glauert in 1922. Prandtl had felt compelled to turn down the invitation, however, because of his lack of English.66 The Wright Lecture was a much grander affair, and Prandtl, who clearly appreciated the invitation, now felt better equipped to cope, though he still had some anxie­ties. In the preparatory exchange of letters with the chairman and the secre­tary of the society he fussed over what he should wear. Should he be in Frack, that is, tailed coat? In hesitant English he announced that “I have at this time English lessons and believe to be able up to the date of the lecture, to read the paper myself.”67 In the event, despite displaying the recommended tails, white tie, and white waistcoat, he only delivered the opening passages of the lecture and then called on the help of Major Low. Low, who had worked with Prandtl to translate the text, read the remainder.68

Those opening passages, however, touched on a matter of some delicacy. They concerned the origin of the theory of the aerofoil and the relative con­tributions of Prandtl and Lanchester. Who invented the theory and who should get the credit? Prandtl was diplomatic but forthright. He said that Lanchester had worked on the subject before he, Prandtl, had turned his at­tention to it and that Lanchester had independently obtained an important part of the theory. Prandtl insisted, however, that the ideas he used to build up his theory had occurred to him before he read Lanchester’s 1907 book. This prior understanding, he argued, may explain why “we in Germany were better able to understand Lanchester’s book when it appeared than you in England” (721). The truth, Prandtl went on, is that “Lanchester’s treatment is difficult to follow.” It makes “a very great demand on the reader’s intuitive perceptions,” and “only because we had been working on similar lines were we able to grasp Lanchester’s meaning at once” (721).

Is Prandtl here corroborating Glazebrook’s excuse for the British neglect of Lanchester? Surely not, though he certainly shared some of Glazebrook’s ideas about Lanchester’s work. Like Glazebrook, Prandtl did not countenance the possibility that it was the understanding of Lanchester, rather than the failure to understand him, that lay behind the British response. But, while go­ing along with part of Glazebrook’s story, Prandtl’s comments actually serve to accentuate the tensions between the different parts of Glazebrook’s excuse. They made it even more necessary to explain why the Germans were in a po­sition to grasp Lanchester’s meaning when, allegedly, the British had not been able to rise to the occasion. Glazebrook had excused one failure by citing another failure, and what Prandtl had to say aggravated rather than alleviated this logical weakness.69

My example of trailing vortices depended for its force on the difference be­tween the understanding of two groups of agents, the scientists and the pilots—the one group believing that trailing vortices had no practical sig­nificance, the other group knowing in a tacit and practical way that they did. What happens to the arguments for relativism when all parties know the same thing? This question is important because the universality of scientific under­standing is often taken to provide an adequate response to relativism. There is only one real world; the laws of nature are the same in London and Berlin; a true theory applies everywhere, and science knows no bounds of nation or race. “It is transnational and, despite what sociologists claim, independent of cultural milieu.”86 If science is independent of cultural milieu, then it cannot be relative to cultural milieu. Granted the premise, the conclusion follows, but my case study shows that the premise is false. The understanding of the phenomenon of lift was not the same in London and Berlin or Cambridge and Gottingen.

Such a response, based upon mere historical fact, is unlikely to satisfy the critics of relativism. It will be said that my study deals with a passing phase. Isn’t the important thing what happened after the episode that I described— when the truth emerged? The transnational character of science may take time to reveal itself, and progress may be inhibited by unfavorable social con­ditions, but universality triumphs in the end. It will be insufficient for the relativist to object that the antirelativist has shifted the discussion from what was the case to what ought to be the case or to what will be the case. The pic­ture of universal knowledge has force because there is, here and now, much science that is indeed transnational. This fact cannot be denied, so what can the relativist say?

Frank argued that relativism is consistent with universality. He said that the conditions leading to the spread of scientific knowledge were the very ones that ought to encourage a healthy relativism. As experience is broad­ened, the tendency to treat a belief as absolute will be undermined. Dogmati­cally held theories will encounter challenges, and a growing appreciation of the complexity of the world will undermine their apparently absolute status. Absolutism is parochialism—the cognitive equivalent of parish-pump pa­triotism. But the central reason why universalism is no threat to relativism is that the extent of a cultural milieu is purely contingent. In principle, a culture could be worldwide. The universal acceptance of a body of knowledge could only serve as a counterexample to relativism if universality indicates, or re­quires, absolute truth.

Let me explain this by an example. By the early 1930s Hermann Glauert had become a fellow of the Royal Society and the head of the Aerodynamics Department at Farnborough. He was at the height of his powers and had just finished a lengthy contribution on the theory of the propeller for William Durand’s multivolume synthesis of modern aerodynamic knowledge. Then tragedy struck. On August 4, 1934, a Saturday, Glauert took his three chil­dren for a walk across Laffan’s plain near Farnborough. The party stopped to watch some soldiers who were arranging an explosive charge to blow up a tree stump. The party stood, as required, at a safe distance some two hundred feet away, but the instructions they had been given were based on a misjudg – ment. Glauert was struck by a piece of debris from the explosion. No one else was hit, and his children were unhurt, but Glauert died instantly.87 In a dignified letter to Theodore von Karman, who had now moved from Aachen to the California Institute of Technology, Glauert’s wife (Muriel Barker) re­called the last time she and her husband had met von Karman. Along with G. I. Taylor they had all sat together, in the garden of Taylor’s Cambridge house, having tea and making plans for the future.88 Von Karman replied, in English: “The few people really interested in theoretical aerodynamics always felt as one family, and I am very proud to say that I had the feeling that your late husband and I were really friends, also beyond the common scientific interests.”89 Von Karman’s metaphor of the “family” to describe the relation­ship between leading members of the profession is striking. It resonates with, and lends support to, the theme of the transnational or universal character of science, though of course allowance must be made for the circumstances in which the expression was used. Perhaps it is the exchange of letters itself, rather than any particular choice of words, that should be considered the salient point. Former enemies in a bitter war are now consoling one another and affirming their solidarity. This epitomizes the increasingly cosmopolitan nature of the scientist’s world, at least as it was emerging, in the interwar years, in the field of aerodynamics.90

How is this emergence of a transnational science to be interpreted? There is a methodological choice to be made. In framing a response the choice lies between (1) invoking some form of inner necessity governing scientific progress and (2) settling for mere contingency. On the first approach it will be tacitly supposed that a “natural tendency” or telos is at work guiding the development. This idea will not recommend itself to an empirically minded analyst, who would therefore choose the second approach. Internationalism is to be analyzed strategically, not teleologically. The relevant comparisons are with the globalization of markets or the spread of the arms race.

Any move toward transnational knowledge should be interpreted in a wholly matter-of-fact manner. Sometimes scientists will reach out across na­tional boundaries, and sometimes they will not. It will depend on opportuni­ties and on perceived advantages and disadvantages and will vary with time and circumstance. (Recall Prandtl’s ambivalent reaction to cooperation in the immediate postwar years.) There will be no inner necessity at work, and references to the “transnational” character of science should not be accompa­nied by starry-eyed sentiments about Universal Truth. Why was von Karman in the United States? What was he doing at Caltech, and who was support­ing his research? 91 Each case needs to be examined by the historian for its particular features and causal structure. Thus in my study I found there was a phase when the reports of German work prepared for the Advisory Com­mittee for Aeronautics lay gathering dust, and there was another phase when copies of the Technische Berichte were sought with urgency. Both should be counted as equally natural. The universality of science and technology, or the absence of universality, depends on familiar, human realities. Some of these will be the brutal realities of war, power politics, and military and diplomatic strategy. Others will be the softer and more agreeable realities of the kind recalled in the exchange between Glauert’s young widow and von Karman— such as taking tea on a Cambridge lawn. These two levels, so different and yet so intimately connected, need to be brought together and linked to the calculations and experiments carried out at the research front. This is what I have sought to do.92