Category The Enigma of. the Aerofoil

I want to dwell for a moment on the significance of this transition from the­ory to fact. It is a phase-change that has often taken place in the history of science. Assertions to the effect that, say, the blood circulates in the human body, or that water is made of hydrogen and oxygen, may once have been speculations but today can be taken as matters of fact. It would be a question­able use of language to keep calling them theories. How is this change of sta­tus, from theory to fact, best described? One attractive answer was provided in the form of a striking metaphor used by the Cambridge mathematician William Kingdon Clifford.34 Clifford, who had been a second wrangler in 1867, a fellow of Trinity, and a friend of Rayleigh, had wide-ranging interests in mathematical physics. In a lecture he gave in Manchester (some fifty years before the experiments that concern us), Clifford took as his example not hydrodynamics but the wave theory of light. This conception of light, he said, must now be accepted as fact. The difference between a theory and a demon­strated fact, he went on, “is something like this”:

If you suppose a man to have walked from Chorlton Town Hall down here say in ten minutes, the natural conclusion would be that he had walked along the Stretford Road. Now that theory would entirely account for all the facts, but at the same time the facts would not be proved by it. But suppose it happened to be winter time, with snow on the road, and that you could trace the man’s footsteps all along the road, then you would know that he had walked along that way. The sort of evidence we have to show that light does consist of waves transmitted through a medium is the sort of evidence that footsteps upon the snow make; it is not a theory which merely accounts for the facts, but it is a theory which can be reasoned back to from the facts without any other theory being possible. (117)

The thought is that if you can track a process in great detail, and see it de­velop step by step, then you can reach a stable understanding that is unique, unchallengeable, and enduring. Such an understanding, said Clifford, deals with facts, not theories.

Clifford’s metaphor may be a tempting one, but it cannot be wholly right, and it led Clifford himself astray. The development of physics showed that what he thought of as a demonstrated fact was actually a theory. The alleged impossibility of any alternative to the wave theory was refuted by the emer­gence of an alternative. In Clifford’s time the wave theory had superseded an older particle theory, but in 1905 Einstein once again postulated light par­ticles. These new-style particles or “photons” were invoked to explain the photoelectric effect, something that was proving difficult to understand in terms of waves. The photoelectric effect takes place when light is incident on a metal surface and releases electrons from the surface. How could the energy spread across a wave front be concentrated in the way necessary to release a charged particle? This was the problem Einstein’s theory was designed to answer. The light energy, he argued, was concentrated because light consists not of waves, but of particles, albeit particles with unusual properties.35 These developments took place after Clifford’s death. He cannot be blamed for not anticipating them, but they amount to a counterexample to Clifford’s argu­ment and show the need to introduce qualifications into his overconfident picture.

What was Clifford’s error? It was that of assimilating fundamental scien­tific inquiry to commonsense knowledge. While there are many similarities and connections, Clifford ignored a crucial difference. Everyone has seen, or could see, a man creating footprints in snow. The cause and the effect can be conjoined in experience, and both are open to inspection. This is the basis of subsequent inferences from footprints to their human causes and the basis of the conclusions that can be drawn about, say, the route someone had taken from Chorlton Town Hall to the location of Clifford’s lecture. The physicist, on the other hand, did not come to the wave theory of light by seeing light waves creating diffraction patterns or rainbows. The two things were not con­joined in experience in the way people and footprints have been conjoined. The inference to light waves did not have the same inductive basis as the com – monsense inference with which Clifford was comparing it.36

Clifford’s metaphor may have broken down for light waves, but it might still be applicable to Fage and Simmons’ achievement. It could be argued that Fage and Simmons were confronting the vortices and observing them bringing about their effects. Was not this conjunction precisely what the ex­periment was designed to expose? Even if the experimenters could not actu­ally see the flow of air, they could have made it visible, and others had done exactly that. In any case, the diagrams showing the streamlines of the vortices and the contour lines of equal vorticity allowed them to follow the path and development of the postulated vortices. The experimenters could set these diagrams side by side with the measured lift forces on the wing. Causal con­nections and correlations of phenomena that were originally speculative had, in a sense, been exposed to view, and the step-by-step progress of the cir­culation had been traced. Perhaps tracking the vortices through the pattern of measurements registered in Fage and Simmons’ diagrams was, after all, similar to tracking footprints in the snow.

If Clifford’s metaphor is applicable to the aerodynamic work, does this mean that the question “How does a wing produce lift?” can now be answered with the same level of certitude as the question about the man walking down the Stretford Road? In a sense, yes, it does. The phenomena of circulation, vortices, and lift had been made, or were on the way to being made, part of the routine and reality of daily life. At least, this was true for the laboratory life of some of the experimentalists working in this area. They were becoming increasingly familiar with the patterns in the data and the range of effects to be accounted for. Expectations were crystallizing, and experimenters were learning what they could take for granted. Techniques of calculation and pre­diction were becoming more confident and refined. What was once strange was becoming familiar and part of predictable, daily experience—like getting to know a new town. Learning to live with the theory of circulation was like learning to live in a new environment with new architectural styles and a new street plan. You want to get to Prof. Clifford’s lecture starting out from Chor – lton Town Hall? Then go down the Stretford Road! You want to calculate the induced drag? Then use Prandtl’s formula!37

Significantly, this was not yet how some of the most influential British experts saw the issue. They acknowledged that Fage and Simmons’ results represented a triumph of sorts for Lanchester, Prandtl, and Glauert, but they did not accept that the answer was now known to the question How is lift produced? On the contrary, they maintained that, despite the experimental advances and the increase in empirical knowledge, the answer to this ques­tion remained wholly unknown. Many questions, they acknowledged, had now been answered, but not this one. These experts were not simply being stubborn or blind in the face of mounting evidence, and their reaction un­derlines just how careful one must be in applying Clifford’s metaphor. It must be accepted that what looks like demonstrated fact from one point of view may appear less compelling or revealing from another point of view. This skeptical response to the mounting experimental evidence was articu­lated with great clarity by Richard Vynne Southwell (fig. 9.10). Southwell has already been mentioned in connection with the postwar contact with Prandtl and Gottingen, but it is appropriate to look more closely both at the man and at his response to the growing experimental literature.

In 1954 Philipp Frank published an article in the Scientific Monthly called “On the Variety of Reasons for the Acceptance of Scientific Theories.”50 He drew the striking conclusion that “the building of a scientific theory is not essentially different from the building of an airplane” (144). I will use Frank’s argument to comment on the theories developed in fluid dynamics and aero­dynamics, but first I should say a little about Frank himself.51 From 1912 to 1938 he was the professor of theoretical physics at the German University of Prague. A pupil of Boltzmann, Klein, and Hilbert, Frank had taken over the chair from Einstein when Einstein received the call to Zurich and then to Berlin. He had attended Einstein’s seminars in Prague, and Einstein strongly supported his appointment.

In their student days, before World War I, Frank and von Mises talked philosophy in their favorite Viennese coffeehouse and together played a seminal role in the formation of the Vienna Circle.52 In the interwar years, as established academics, Frank and von Mises jointly edited a book on the differential and integral equations of mechanics and physics, Die Differential – und Integralgleichungen der Mechanik und Physik,53 which brought together a range of distinguished contributors. Von Mises edited the first volume on mathematical methods, while Frank handled the second, more physically oriented, volume which included chapters by Noether, Oseen, Sommerfeld, Trefftz, and von Karman, who wrote on ideal fluid theory.54 The Frank-Mises collection, which was an update of a famous textbook by Riemann and Weber, established itself as a standard work in German-speaking Europe.55 In 1938 Frank was forced to leave Prague because of the threatening political situation in Europe, and he went to the United States. During and after World War II, he taught physics, mathematics, and the philosophy of science at Harvard.

Like that of von Mises, Frank’s philosophical position was self-consciously “positivist” in the priority given to empirical data and the secondary, instru­mental role given to theoretical constructs. Frank admired Ernst Mach as a representative of Enlightenment thinking, though his admiration was not uncritical, and he did not go along with Mach’s rejection of atomism.56 Much of Frank’s philosophical work was devoted to the analysis of relativity theory, quantum theory, and non-Euclidian geometry.57 He was a firm believer in the unity of science and rejected the idea that there was a fundamental divide between the natural and human sciences.58 He also insisted on the need to understand science as a sociological phenomenon. The sociology of science was part of “a general science of human behaviour” (140)—a theme central to the Scientific Monthly article.59

Frank asserted that most scientists, in their public statements, assume that two, and only two, considerations are relevant when assessing a scientific the­ory. These are (1) that the theory should explain the relevant facts generated by observation and (2) that it should possess the virtue of mathematical simplic­ity. Frank then noted that, historically, scientists (or those occupying the role we now identify as “ scientist”) have often used two further criteria. These are

(3) that the theory should be useful for technological purposes and (4) that it should have apparent implications for ethical and political questions. Does the theory encourage or undermine desirable patterns of behavior, either in society at large or in the community of scientists themselves? Such questions are often presented in a disguised form, for example, Is the theory consistent with common sense or received opinion or does it flout them? Common sense and received opinion, Frank argued, typically fuse together a picture of nature and a picture of society. The demand for consistency then becomes a form of social control that can be used for good or ill.

In Frank’s opinion it is naive to believe that theory assessment can be confined to the two, internal-seeming criteria. He offered three reasons. First, he noted that no theory has ever explained all of the observed facts that fall under its scope. Some selection always has to be made. Second, there is no unproblematic measure of simplicity. No theory has “perfect” simplic­ity. Simplicity will be judged differently from different, but equally rational, perspectives, depending on background knowledge, goals, and interests. Third, criteria (1) and (2) are frequently in competition with one another. The greater the number of facts that can be explained, or the greater the ac­curacy of the explanation, the more complicated the theory must be, while the simpler it is, the fewer are the facts that can be explained. Linear functions are simpler than functions of the second or higher degree, which is why phys­ics is full of laws that express simple proportionality, for example, Hooke’s law or Ohm’s law. “In all these cases,” wrote Frank, “there is no doubt that a nonlinear relationship would describe the facts in a more accurate way, but one tries to get along with a linear law as much as possible” (139-40). What is it to be: convenience or truth? Nothing within the boundaries of science itself, narrowly conceived, will yield the answer. This is why scientists have always moved outside criteria (1) and (2), and, consciously or unconsciously, invoked criteria of types (3) and (4).

These unavoidable choices and compromises tell us something about the status of any theory that is accepted by a group of scientists. “If we consider this point,” said Frank, “it is obvious that such a theory cannot be ‘the truth’” (144). But if the chosen theory is not “the truth,” what is it? Frank’s answer was that a theory must be understood to be “an instrument that serves to­ward some definite purpose” (144). It is an instrument that sometimes helps prediction and sometimes understanding. It can help us construct devices that save time and labor, and it sometimes helps to mediate a subtle form of social control. “A scientific theory is, in a sense, a tool that produces other tools according to a practical scheme” (144), he concluded. Like a tool, its connection to reality is not to be understood in terms of some static relation of depiction but in active and pragmatic terms. Its function is to give its us­ers a grip on reality and to allow them to pursue their projects and satisfy their needs—but it does so in diverse ways. It was at this point that Frank produced his comparison between assessing a theory in science and assessing a piece of technology, such as an airplane. Writing, surely, with the perfor­mance graphs of von Mises’ Fluglehre before his mind, he argued:

In the same way that we enjoy the beauty and elegance of an airplane, we also enjoy the “elegance” of the theory that makes the construction of the plane possible. In speaking about any actual machine, it is meaningless to ask whether the machine is “true” in the sense of its being “perfect.” We can ask only whether it is “good” or sufficiently “perfect” for a certain purpose. If we require speed as our purpose, the “perfect” airplane will differ from one that is “perfect” for the purposes of endurance. The result will be different again if

we chose safety. . . . It is impossible to design an airplane that fulfils all these purposes in a maximal way. (144)

It is the trade-off of one human purpose against another that gave Frank his central theme. Only by confronting this fact can the methods of science be understood scientifically. It is necessary to ask in the case of every scientific theory, as one asks in the case of the airplane, what determined the policy according to which these inescapable compromises are made and how well does the end product embody the policy? We must understand what Frank called, in his scientistic terminology, “the social conditions that produce the conditioned reflexes of the policy-makers” (144).60

In Frank’s terms, Lanchester’s metaphor of playing chess with nature as well as my sociological analysis are ways of describing scientific “policies.” Just as there were policy choices made over the relative importance of stabil­ity and maneuverability, and policy choices about how to distribute research effort between the theory of stability and the theory of lift, so within the pur­suit of a theory of lift there were policy decisions to be made. My analysis identifies one policy informing the Cambridge school and another policy guiding the Gottingen school. Again using Frank’s terms, the members of the respective schools constructed different technologies of understanding, that is, different theoretical “instruments.” Their policies, when construct­ing their theories, maximized different qualities and furthered different ends. The British wanted to construct a fundamental theory of lift, whereas the Germans aimed at engineering utility. Who were the “policy makers”? One might identify, say, Lord Rayleigh as the “policy maker” in Britain and Fe­lix Klein as the “policy maker” in Germany, but there is no need to assume that policy is made by individuals. Such a restriction would not correspond to Frank’s intentions; nor is it part of my analysis. Policies can emerge col­lectively. They can be tacitly present in the cultural traditions and research strategies of a scientific group. One could then say that everyone is a policy maker by virtue of their participation in the group, or one could say that the policy maker is the group itself. In my example the “social conditions” that determine the “conditioned reflexes of the policy-makers” reside in the divi­sion of labor between physicist and engineer.

One implication of Frank’s “policy” metaphor is that a stated policy need not correspond to an actual policy. The devious history of aircraft construc­tion in post-World War I Germany provides some obvious examples. Is this large aircraft really meant as an airliner or is it a bomber? Is this an aero­batic sports plane or a disguised fighter? Is all this enthusiasm for gliding just recreation or a way of training a future air force—and keeping the nation’s aerodynamic experts in a job?61 The difficulty of distinguishing a real from an apparent policy comes from the problematic relation between words and deeds. Sometimes the self-descriptions and methodological reflections of members of the Cambridge school could sound similar to those of German engineers. Both Lamb and Love occasionally invoked the ideas, and some­times the name, of Ernst Mach, but that did not make Lamb into a positivist, nor turn Love’s work on the theory of elasticity into technische Mechanik. Their real policy lay elsewhere.

In an address to the British Association in 1904, Lamb acknowledged that the basic concepts of physics, geometry, and mechanics were “contrivances,” “abstractions,” and “conventions.”62 But Lamb soon left behind this unchar­acteristic indulgence in philosophizing and turned the discussion back to the work of his old teacher, G. G. Stokes. He spoke warmly of “the simple and vigorous faith” that informed Stokes’ thinking.63 Lamb then raised the metaphysical question of what lay beyond science and justified faith in its methods. Why, as Lamb put it, does nature honor our checks? He gave no explicit answer, but the theological hint was obvious. Lamb also distanced himself and the Cambridge school from the “more recent tendencies” in ap­plied mathematics. He deplored the fragmentation of the field and regretted the passing of the large-scale monograph, which was a work of art, in favor of detailed, specialized papers. What differentiated the Cambridge school, he went on, related “not so much to subject-matter and method as to the gen­eral mental attitude towards the problems of nature” (425). It is this “general mental attitude” that constitutes the real policy.

How is an authentic “mental attitude” to be filtered out from misleading forms of self-description? The answer is: by looking at what is done and at the choices that are made. Words must be supported by actions. Bairstow, Cow­ley, Jeffreys, Lamb, Levy, Southwell, and Taylor not only gave their reasons for resisting the ideal fluid approach to lift, but they acted accordingly. This is why, in previous chapters, I have identified the mental attitude that informed the work of the Cambridge school and its associates as a confident, physics – based realism rather than a skeptical positivism. Stokes’ equations were not only said to be true, but they were treated as true. This was the attitude and policy that Love expressed by invoking the role of the “natural philosopher” rather than the engineer. And this was why Felix Klein, in his 1900 lecture on the special character of technical mechanics, could express admiration for Love’s treatise on elasticity and yet pass over it because it could not be taken as an example of technische Mechanik.64

Simplicity and the Kutta-Joukowsky Law

I now apply Frank’s ideas to the Kutta-Joukowsky law: L = p LT, where the lift (L) is equated to the product of the density (p), the speed (U), and the circulation (Г). The law is certainly simple, but what is the meaning of this simplicity? Is it a sign of the “deep” truth of the law and hence a quality that should command a special respect? The idea that nature is “governed” by simple mathematical laws is a familiar one—it goes back to the origins of modern science—but positivists have no time for this sort of talk.65 Frank could have pointed out that the simplicity, and apparent generality, of the Kutta-Joukowsky law derives not from its truth, but from its falsity and from everything that it leaves out of account. The law says nothing about the rela­tion between the shape of the aerofoil and the amount of lift. It contributes nothing to the problem of specifying the amount of circulation and (when used in conjunction with the Kutta condition) gives predictions for the lift that are consistently too high. The law cannot, in any direct or literal way, represent something deep within reality because its individual terms do not refer to reality. They refer to a nonexistent, ideal fluid under simplified flow conditions.

Frank would predict that if an attempt were made to repair the law, and make allowance for some of the factors that have been ignored, then the re­sult would no longer possess the impressive simplicity of the original. This was precisely what happened when, in 1921, Max Lagally of the technische Hochschule at Dresden, produced an extension of the Kutta-Joukowsky for­mula.66 Lagally exploited a result arrived at previously by Heinrich Blasius, one of Prandtl’s pupils, and this result needs to be explained first in order to make sense of Lagally’s formula. Blasius had developed a theorem, based on the theory of complex functions, that allowed the force components X and Y on a body to be written down as soon as the mathematical form of the flow of an ideal fluid over the body had been specified.67 In these terms, for a uniform, irrotational flow U along the x-axis, with a circulation Г, the Kutta – Joukowsky theorem takes the form

X – iY = ipU Г.

Here X, the force along the x-axis, represents the drag, while Y is the force along the y-axis and represents the lift. The letter i is a mathematical opera­tor. The right-hand side of the equation economically conveys the informa­tion that the drag is zero (because X = 0) and also that the lift obeys the Kutta-Joukowsky relation (because Y = pU Г). Blasius’ derivation of this re­sult depended on there being no complications in the flow. Lagally added some complications in order to see what effect they would have. In Lagally’s analysis the main flow has a horizontal component U and a vertical compo­nent V. More important, he assumed that there were an arbitrary number of sources and an arbitrary number of vortices in the fluid around the body. He specified that there were r sources located at the points ar where each source had a strength mr, and s vortices located at points cs where each vortex had vorticity Ks. When the formula was adjusted to allow for these conditions, it looked like this:

X — iY = —ipK(U — iV) + 2np^mr (u r — iv r + U — iV) — ip^Ks (us — ivs +U — iV),

where ur and vr are the components of velocity at ar (omitting the contribu­tion of mr) and us and vs are the velocity components at cs (omitting the con­tribution of Ks). The original Kutta-Joukowsky formula can be seen embed­ded in Lagally’s formula on the immediate right of the equality sign.68

If the original Kutta-Joukowsky relation could be admired for its elegance, like the sleek lines of a modern aircraft, can this be said of Lagally’s formula? I doubt if it attracted much praise on this score. But if the long formula really is an improvement on the short one, why shouldn’t it be seen as more beautiful? If we do not find it beautiful is it because we can’t imagine such complicated mathematical machinery “governing” reality? Frank and his fellow positivists would not want the question to be pursued in these metaphysical terms. They would say: If there is something important about the simplicity of the origi­nal formula L = p UT, then look for the utility that goes with simplicity. What does it contribute to the economy of thought? This question will expose the real attraction of simplicity and explain what might have been lost, along with what has been gained, by Lagally’s generalization.

Frank called a theory a tool that produces other tools according to a practi­cal scheme. He meant that the simple law provides a pattern, an exemplar, and a resource that is taken for granted in building up the more complex formula.69 This is how Lagally built his generalization, and if Frank is right, other scientists and engineers, interested in a different range of special condi­tions, will follow a similar path. This pattern fits what I have found. Recall the way Betz experimentally studied the deviations between the predictions of the circulatory theory and wind-tunnel observations. He sought to close the gap between theory and experiment by retaining the Kutta-Joukowsky law while relaxing the Kutta condition, that is, the understanding that the circula­tion is precisely the amount needed to position the rear stagnation point on the sharp trailing edge. Again, recall the later episode in which, prompted by the work of G. I. Taylor, the condition of contour independence was relaxed so that a “circulation” could be specified for a viscous flow. In both these examples the development exploited the same resource as Lagally, that is, the simple law was retained as a basic pattern. Simple laws are a shared resource and an accepted reference point. They are used when a group of scientists are striving to coordinate their behavior in order to construct a shared body of knowledge. They are salient solutions to coordination problems, which may explain the obscure “depth” attributed to them. The depth is a social, not a metaphysical, depth.70

What was the scheme of work that was drawn up in the meeting at the Ad­miralty mentioned by Glazebrook? Some indication was given in the House of Commons when questions were taken on the founding of the commit­tee. More details, however, can be gleaned from a document titled “Prelim­inary Draft for Programme of Possible Experimental Work,” dated June 1, 1909, and used as the basis for an interim report during the first year of the committee’s activities.46 The program of work was divided into six sections: I, “General Questions on Aerodynamics”; II, “Questions Especially Relating to Aeroplanes”; III, “Propeller Experiments”; IV, “Motors”; V, “Questions

Especially Related to Airships”; and VI, “Meteorology.” For our purposes, only the first two sections are of interest; within them, some fourteen distinct topics were identified. They repay scrutiny and call for some comment. The list of topics was as follows:

I. General Questions on Aerodynamics

1. Determination of the vertical and horizontal components of the forces on inclined planes in a horizontal current of air, especially for small angles of inclination to the current.

2. Determination of surface friction on plates exposed to currents of air.

3. Centre of pressure for inclined planes.

4. Distribution of pressure on inclined planes.

5. Pressure components, distribution of pressure for curved surfaces of various forms.

6. Resistance to motion of bodies of different shapes = long and short cylinders &c.

7. Combination of planes: effect on pressure components of various ar­rangements of two or more planes.

II. Questions Especially Relating to Aeroplanes

8. Resistance components of aeroplane models.

9. Resistance of struts and connections.

10. Resistance of different stabilising planes both horizontal and vertical.

11.Problems connected with stability.

(i) Mathematical investigation of stability.

(ii) The stability of aero curves of different section and plane.

(iii) Effect of stabilising planes.

(iv) Effect of sudden action.

(v) Effect of gusts of wind.

(vi) Investigations as to stability of models for different dispositions of weight etc.

12. Materials for aircraft construction.

13. Consideration of different forms of aeroplane: monoplane, biplane, etc.

14. Other forms of heavier than air machines, helicopter, etc.

The list conveys the range of problems confronting the committee but also something of its priorities and preferences. The emphasis to be placed on sta­bility stands out clearly in the degree of definition accorded to the problem, which is carefully divided into six subsections. Likewise, the scientific style of the approach is clear. Experimentally, a significant amount of the work was to be done with models while, theoretically, the complexity of the real flying machine was replaced by simplified concepts such as planes and cylinders and centers of pressure.47 The operation of an aircraft was being assimilated to the abstract categories familiar to the committee from their Tripos text­books on mechanics and hydrodynamics.

Something was badly wrong with the picture of air behaving and moving as an ideal fluid. It was mathematically impressive but empirically defective. What exactly was wrong? Was it the assumption of zero viscosity itself that should be dropped or were there perhaps other, unnoticed, assumptions at work in the picture of the flow that might be the cause of the trouble? What about Laplace’s equation and the assumption of irrotational motion?

This question was addressed by a number of late nineteenth-century ex­perts whose investigations greatly deepened the understanding of ideal fluid theory. They began to explore some possibilities that previously had been neglected. But why did they not simply abandon ideal-fluid theory as em­pirically false and turn directly to the analysis of viscous fluids? Attempts were made to do this but with very limited success. The reason was that the mathematics of viscous fluids was so difficult. It was possible to write down the equations of motion of a viscous fluid by taking into account the trac­tion forces along the surface of the fluid element, but it was another matter to solve the equations. The full equations of viscous flow are now called the Navier-Stokes equations, though in Britain they used to be called just the Stokes equations. Of course, they contain a term involving the symbol Ц standing for the coefficient of viscosity. If the value of this coefficient is set at zero to symbolize the absence of viscosity, that is, Ц = 0, the Navier – Stokes equations turn back into the Euler equations that have been described earlier in this chapter. In a later chapter I look more closely at the status of the Navier-Stokes equations and the different responses to their seemingly intractable nature. For the moment it is only necessary to appreciate the problem they posed. No one could see how to solve and apply the equations except in a few simple cases. Because of their intractability, any attempt to avoid the impasse thrown up by the zero-resultant theorem had to be one that stayed with the Euler equations and thus within the confines of ideal- fluid theory.

The crucial insight that permitted the further development of ideal-fluid theory was provided by Helmholtz and Kirchhoff in Germany and Rayleigh in Britain. These men realized that the solutions to the Euler equations that gave the streamlines around an obstacle were not unique. More than one set of streamlines were possible and consistent with the equations. More than one kind of flow could satisfy the equations and meet the given boundary conditions. What is more, some of these flows could generate a resultant force. There were in fact two very different kinds of flow that might have this desired effect and, in principle, allow the zero-resultant outcome to be evaded. Rayleigh contributed to the study of both. Both approaches involved the limited introduction of fluid elements that possessed rotation and vor – ticity. The strict condition of irrotational motion was dropped. On one ap­proach this involved the introduction of just one singular point in the flow that rotated and constituted the center of a vortex. On the other approach a sheet or surface of vorticity was postulated. In both cases the remainder of the flow was still irrotational. These two approaches provided, respectively, the basis for the two different theories of lift that I mentioned in the introduction and called the circulatory or vortex theory of lift and the discontinuity theory of lift. Historically, the first of the two approaches to be developed in detail was the one that led to the discontinuity theory. I now introduce the ideas underlying this approach. The other approach and the other theory of lift are introduced in chapter 4.

In chapter 2 I introduced the idea of describing a flow by means of a stream function. What is the stream function for a vortex? From the definition of a vortex, the flow is in concentric circles of radius r so there is no veloc­
ity component u’ along the radius, but there is a tangential velocity com­ponent V along the circumference of the circles. It will be recalled that the speed of flow is given by the rate of change of the stream function y. In polar coordinates the two relevant equations relating v’ and u’ to the stream func­tion are

1 dy

—-— = u = 0 and r дв

ду = ,= Г dr Inr

Integration of the second of these equations answers the question posed ear­lier and gives the stream function for the vortex as

w = —— logr.

2n

Both Lanchester and his critics made repeated references to flows with circulation but that were also described as “irrotational.” The flow around a simple circular vortex of the kind I have been describing is an example of circulation without rotation. It may seem puzzling to say that the air in such a vortex is not rotating. The problem lies with a divergence between technical and common usage. The difficulty is resolved, at least in part, by distinguishing between the overall path of the fluid element, that is, its cir­cular orbit around the vortex, and its behavior while going round that path. The distinction is sometimes illustrated in textbooks by reference to a Ferris wheel, where the chairs are carried around but always hang vertically and so maintain the same orientation, that is, the chairs “circulate” but do not “rotate.” Circulation is also compatible with an absence of rotation when a vortex exists as one component in a flow. Thus the combination of a uniform wind and a vortex motion, of the kind assumed in the circulatory theory of lift, can also be conceived as an irrotational motion with circulation.

One final feature of vorticity and circulation should be mentioned before introducing Lanchester’s own use of these ideas. In 1869 Kelvin established a remarkable theorem about circulation in an ideal fluid. He proved that it does not and cannot change with time.9 In an ideal fluid obeying the Euler equations the value of the circulation cannot change as a result of any pro­cesses such as the movement of a body through the fluid. Circulation can exist, but once in existence it can be neither augmented nor diminished. Thus if the circulation starts as zero, it stays zero. If the amount of circulation is symbolized by Г, then Kelvin’s theorem is expressed by saying that the rate of change of Г with time is zero. In mathematical symbols,

d г

The proof of Kelvin’s theorem depends on the condition that the con­tour of integration used to establish the circulation is one that moves along with the fluid. The contour must be made up of the same elements of fluid at all times. Such a contour is sometimes called a material loop and stands in contrast to the kind of contour mentioned previously, which is a purely geometrical entity and can be selected on grounds of mathematical or ex­perimental convenience. This restriction of the theorem to the circulation around material loops has consequences that are both important and subtle. It made the precise implications of the theorem difficult to decide. Later we see that Kelvin’s theorem was interpreted in different ways by different groups of experts. The divergence of opinion had a significant impact on the discus­sion of how (or whether) a wing can generate lift by generating circulation. The generation of circulation by the movement of a wing through the air would involve a variation of circulation with time. Is it ruled out by Kelvin’s theorem? If it is, then what does this mean for the circulation theory of lift? I shall come back to these questions, but now, having laid the foundations, I turn to Lanchester’s pioneering statement of the circulation theory.

All real fluids are viscous, but not all viscous fluids are real. A mathematician may construct a model of a fluid which makes provision for viscosity, but it remains an open question whether any real fluid satisfies the specifications of the model. Lamb was very clear on this matter. He raised it in connection with the derivation of Stokes’ equations. All such derivations must start from assumptions, and these typically involve simplifications. A few years before Stokes’ work, Navier in France had arrived at these same equations and so they are often known as the Navier-Stokes equations.23 Navier, however, worked from assumptions about the supposed forces operating between the particles that made up fluids. Stokes is generally considered to have improved on this account by finding a way to avoid speculating about the ultimate particles of a fluid. He treated a fluid as a continuum and confined himself to considering the tangential stresses and shear forces on the sides of a fluid element. This modification avoided Navier’s assumptions but inevitably introduced others. What laws were obeyed by the stresses and forces? Stokes made the assump­tion that there was a linear relation between the shear force and the rate of shear. Lamb was careful to point this out to the reader.24 The assumption of linearity, he said, was exactly that—an assumption. He hastened to add that the assumption was plausible and the success of the equations, where they had been tested empirically, gave every reason to believe it was correct.

It will be noticed that the hypothesis made above that the stresses. . . are linear functions of the rate of stress. . . is of a purely tentative character, and that although there is considerable a priori probability that it will represent the facts accurately in the case of infinitely small motions, we have so far no assurance that it will hold generally. It was however pointed out by Reynolds that the equations based on this hypothesis have been put to a very severe test in the experiments of Poiseuille and others. . . . Considering the very wide range of values over which these experiments extend, we can hardly hesitate to accept the equations in question as a complete statement of the laws of viscosity. (571)

Assumptions had been made, but it turned out that the assumptions were correct. The Stokes equations were not approximations in competition with other approximations. Evidence, said Lamb, shows that the equations are to be accepted as a “complete statement” of the laws of the real-world phenom­enon of viscosity. In a word, the Stokes equations were true.

Given the immense authority behind this judgment, it can be difficult to realize that it was not necessitated by the facts. Lamb could have drawn a different conclusion. He was making a methodological choice and did not have to choose as he did. Others adopted a different stance toward Stokes’ equations and the experimental evidence that Lamb cited.25 I illustrate this point by reference to the work of the applied mathematician Richard von Mises (fig. 5.4). As well as his broad literary and philosophical interests, von Mises made important contributions to aerodynamic theory by generaliz­ing the mathematical technique for creating aerofoil shapes by conformal

transformations.26 He also corresponded extensively with Prandtl about fluid dynamics and contributed to boundary-layer theory.27 Von Mises had lec­tured on aerodynamics to military aircrew in Berlin as early as 1913 and had himself learned to fly at Adlershof. Before the war von Mises held a chair at the University of Strassburg, where he published Elemente der technischen Hydromechanik (The elements of technical hydrodynamics).28 On the title page von Mises was styled as a Maschinenbau-Ingenieur, or “mechanical en­gineer.” During the Great War he returned to Vienna, served as a pilot and an instructor, and then worked on the design of a giant aircraft for which he had provided the wing profile.29 Toward the end of the war he published his military lectures in the form of a textbook, Fluglehre.30 The little book was warmly welcomed by Prandtl because it was written by someone who could handle both the scientific and the technical sides of the aeronautics.31

In 1909, in an article on the problems of technical hydromechanics, von Mises had made a proposal that was designed to rationalize the relation be­tween perfect fluid theory and the theory of viscous flow.32 He called it the “hydraulic hypothesis” and claimed that it was implicit in many of the practi­cal applications of hydrodynamics, even if it was not usually made explicit. Rather than emphasizing the fundamental difference between viscous and inviscid theory (for example, by saying that one referred to something real while the other referred to something unreal), the hydraulic hypothesis em­bodied the view that they were intimately connected. Von Mises still used the hypothesis many years later in his advanced textbook on aerodynamics, the Theory of Flight, first published in English in 1945.33

According to von Mises, so-called ideal fluids represent a process of av­eraging out the statistical fluctuations always present within real fluids. The implied relation between the ideal fluid and real fluid may be illustrated by an analogy. An element of an ideal fluid stands to the elements of a real fluid, that is, the molecules, in roughly the way that, say, the average taxpayer stands to the array of real taxpayers. The behavior of an element of perfect fluid mathematically encodes real information about a specified collection of real things, without itself constituting a further item in the collection. The only fluids are real fluids, just as the only taxpayers are real taxpayers. The concept of an ideal fluid is an instrument by which we talk about, reason about, and refer to real fluids. Indirectly, equations that involve ideal fluids have a real reference, just as statistical data about taxpayers have a real reference. The Euler equations capture the mean values of a statistically fluctuating reality.34 In one formulation von Mises put it like this:

the flow around an aerofoil in a wind tunnel is doubtless a turbulent flow of a viscous fluid. But if the small oscillations are disregarded, the remaining steady velocity values agree very well with those computed from the theory of perfect fluids. . . . The hydraulic hypothesis does not contend that the viscosity effects are negligible. On the contrary. . . the viscosity is responsible for the continual fluctuations or for the turbulent character of the motion. It is left undecided whether the instantaneous (fluctuating) velocities of the real fluid follow the Navier-Stokes equations or not. The hydraulic hypothesis states only that the mean velocity values satisfy, to a certain extent, the perfect-fluid equations. (84-85)

This wording comes from Theory of Flight and therefore dates from 1945, but it is entirely consistent with the original formulation of the hypothesis.

What, on this view, is the relation between Euler’s equations and Stokes’ equations? Von Mises’ answer is interesting. He insists that both are idealiza­tions. In neither case do their concepts have objects that are to be simply or directly identified with real fluids. Both have an indirect relationship. “It should be kept in mind that the ‘viscous fluid’ as well as the ‘perfect fluid’ are idealizations. In introducing the viscous fluid the presence of shearing stresses is admitted, and thus a broader hypothesis is used, which can be ex­pected to give a better approximation to reality. However, we are not entitled to call ‘real fluid’ what is still only an idealization” (76-77). The term “real fluid,” said von Mises, should only be used, “when reference is made to ob­served facts” (77). Real fluids are encountered in experiments and practical engineering. They always stand in contrast to the equations of the mathe­matician—a point that holds whether the equations describe a perfect or a viscous fluid. Both are idealizations, approximations, and constructions, and neither can be identified with reality.35 This was a very different position from that adopted by Lamb and his colleagues. Although Lamb acknowledged the idealization that entered into the construction of Stokes’ equations, he con­cluded that experiment had confirmed their truth. Such confirmation lifted the equations out of the realm of conjecture and put the stamp of reality on them. The idea that, formally, Stokes’ equations stood in the same relation­ship to real fluids as the equations of Euler would have blurred the funda­mental distinction that Lamb and his British colleagues wanted to make.

For certain purposes, some idealizations may be better than others. Von Mises acknowledged that, by taking into account the shearing stresses in the fluid, Stokes had offered a “broader hypothesis” and a “better approxima­tion” than that provided by a perfect fluid. This point must be handled with care. It is surely correct but it does not follow that Stokes’ equations will al­ways give a more accurate answer than that given by the Euler equations. It does not follow that a viscous fluid idealization will always outperform an inviscid idealization. Calling one a “better approximation” than the other may create a certain presumption to that effect, but, given that they are both idealizations, this should not be taken for granted. Von Mises’ own discus­sion of Poiseuille’s results provides a salutary reminder.

Poiseuille’s experiments concerned the uniform flow of a viscous fluid down a straight tube of circular cross section. The fluid will travel more quickly along the middle of the tube than it will closer to the perimeter, and it will be stationary on the walls of the tube itself. Of course, the fluid will have an average velocity, and this will depend on the pressure gradient. The velocity vector will always be parallel to the axis, so the flow is “laminar.” In these simple conditions it can be deduced from Stokes’ equations that the velocity will be distributed over the diameter of the tube in the form of a parabola. The shape of the parabola is determined by the result that the maxi­mum velocity, on the axis, turns out to be exactly twice that of the average velocity. Poiseuille established these facts experimentally, and it was Stokes’ ability to deduce them theoretically that Lamb cited as the grounds for the truth of his equations. But the deductions only hold good if the velocity of the flow is below a certain critical speed. Von Mises reported that, for air in a one-inch pipe, the critical speed is a little below 4 feet per second. Above that speed the analysis fails because the flow ceases to be laminar and becomes turbulent.

In turbulent flow the velocity distribution in the cross section of the pipe alters markedly. Instead of the parabolic distribution, a much flatter distri­bution prevails where the maximum is only a few percent higher than the average. Did this directly contradict Stokes’ equations? It remained unclear whether this behavior contradicted them or not. The relation to the equations could not be determined, and no one could predict the pattern of turbulent flow from them. But while the equations of viscous flow were no help, it was evident that the flat distribution looked strikingly similar to that predicted on the assumption of an inviscid fluid. A frictionless fluid would not adhere to the sides of the pipe, so the fluid there would not be retarded relative to that near the center. There would be no parabolic distribution of velocities but a uniform march forward on a straight front. And this is very nearly what happens in turbulent viscous flow. As von Mises put it in the Theory of Flight. “This uniform velocity distribution of the perfect fluid flow agrees much better with observations under turbulent conditions than the veloc­ity distribution of a laminar viscous flow” (83). The perfect fluid provided a better approximation to the complicated case of turbulent flow than did the equations of viscous laminar flow.

Nor did this superiority hold just for the case of a fluid in a pipe. Von Mises argued that it applied to other practically interesting flows such as those through curved channels and those with varying cross sections, and, as we have seen, to the flow in wind tunnels. “If the small fluctuations are disregarded and attention is given only to the average values at each point, there appears a marked resemblance to the irrotational flow pattern of a per­fect fluid. The mean values of the velocity are distributed very much like the instantaneous velocities in a perfect fluid” (84).

The hydraulic hypothesis was a particular expression of a more general view that von Mises adopted toward the state of mechanics in the early de­cades of the twentieth century. His understanding of both the Euler equations and the Stokes equations brought them into line with his views on probability theory and his understanding of the modern scientific picture of the world— “das naturwissenschaftliche Weltbild der Gegenwart.” He was impressed by current developments in quantum theory and understood them to mean that behind the differential equations of classical mechanics there lay a reality governed by statistical rather than causal laws.36

Whatever one makes of the hydraulic hypothesis and the ultimate indeter­minism of physical laws, the essential point that von Mises was making about the Stokes equations still holds good. Even if von Mises’ statistical interpreta­tion of the Euler equations were to be rejected, his claim that both the Euler and Stokes equations were idealizations would not be directly threatened and could be defended on independent grounds. The point was forcefully made by the American mathematician Garrett Birkhoff. In his book Hydrodynam­ics: A Study in Logic, Fact and Similitude,31 Birkhoff lists molecular dissocia­tion and ionization at hypersonic speeds, chemical kinetics, and sound atten­uation as some of the physical effects not covered by the equations. He also noted that “the first supersonic wind-tunnels were plagued by condensation shocks due to water vapor in the air—another ‘hidden variable’ ignored by the metaphysics of Navier and Stokes” (31). Impressive though they are, the Stokes equations are not a complete statement of the laws of viscosity. They should be seen, as von Mises saw them, as idealizations covering a very in­complete range of phenomena in a very partial manner.

I now put these divergent responses to perfect fluids, d’Alembert’s para­dox, and Stokes’ equations into context. I identify two divergent traditions of mathematical work, one British, the other German. The tradition with the strong boundary between ideal and real fluids might be called “Cambridge – style mathematical physics.” The other, with the weaker boundary between the real and the ideal, is the tradition of technical mechanics as it was devel­oped in the German system of technical colleges. I start with a characteriza­tion of the Cambridge approach and, again, take Horace Lamb as my refer­ence point.

In 1910 the Society of German Aeronautical Engineers began to publish the Zeitschrift fur Flugtechnik und Motorluftschiffahrt—the journal for aeronau­tics and motorized airship transport.45 The ZFM, as it was called, rapidly be­came the leading scientific publication in the field. There was no precise Brit­ish equivalent. The ZFM was more technical than, say, the Aeroplane or Flight and yet more accessible, and certainly more diverse, than the Reports and Memoranda of the Advisory Committee for Aeronautics. As well as scientific reports it contained general survey articles on the state of aviation, accounts of the latest exhibitions and meetings, and reviews of recent publications. There was, however, no close reporting of political controversies of the kind that was conspicuous in the British aeronautical press. Perhaps the nearest British publication was the Journal of the Aeronautical Society, but unlike the ZFM, this was not a routine vehicle for publishing research results.46 The lack of any British equivalent hints at the different ways aeronautical knowl­edge was integrated into the institutions of the two countries. Those who wrote for the ZFM communicated across boundaries between theorists and practitioners that seemed more difficult to overcome in Britain, while their silence in the domain of politics shows that there were other boundaries that remained higher in Germany than in Britain.

The advisory board of the ZFM was impressive. The journal was edited by the Berlin engineer Ansbert Vorreiter, and the scientific side was under the guidance of Ludwig Prandtl in Gottingen. Alongside Prandtl the board contained Carl Runge, also of Gottingen, along with Finsterwalder of the TH in Munich, Reissner of the TH in Aachen, and von Parseval and Bendemann from the TH in Charlottenburg. The masthead of the journal also carried the name of Dr. N. Joukowsky. His affiliation was given as the University of Moscow and the technische Hochschule of Moscow.

In the issue of November 26, 1910, the ZFM published the first part of a two-part article by Joukowsky titled “Uber die Konturen der Tragflachen der Drachenflieger” (On the shape of the wings of aircraft).47 The article has come to occupy a notable position in the history of aerodynamics. It is cited as the source of an important methodological shift in the mathematics of lift. The shift consisted in replacing Kutta’s complicated conformal transforma­tions with a single, simple transformation, now called the Joukowsky trans­formation. Not only was it simpler, but it produced a more realistic aerofoil shape. Kutta’s method had merely produced a geometrical arc. The arc was an adequate model of Lilienthal’s wing, but it did not capture the increas­ing use of wings with a rounded, rather than sharp, leading edge as well as a slender tailing edge. Kutta had established the logic of the process by which knowledge of the flow around a circular cylinder could be turned into knowl­edge about the flow around a wing. The next step was to refine and improve this method of analysis. It is in this connection that Joukowsky’s paper has, rightly, achieved the status of a classic.

A reader who is aware of its reputation, but who confronts Joukowsky’s paper with fresh eyes, might feel puzzled. Where is the bold simplifying stroke? The inner coherence of the mathematics of the infinite wing, so evi­dent in the textbooks that emerged a few years later, is not to be seen. The argument of the paper lacked clarity, and Joukowsky cited formulas without proof and used them without adequate explanation. There was also an edgy concern with issues of priority, particularly Russian priority, and some dis­tracting typographical errors. The formula in the theory of complex variables that is now called the Joukowsky transformation was not actually stated in the paper, although some of its immediate consequences were given a lim­ited application. But any inclination toward disappointment should be re­sisted. The smoothness of the later analysis is indeed absent from the paper, but that is because the later analysis was the work of others who learnt from Joukowsky and carried his ideas further. It was a collective, not an individual, accomplishment.

What was Joukowsky’s own contribution? I answer this question by giving an analysis of the argument of the 1910 paper. Joukowsky began by stating, without proof, two formulas for the lift, P, of an aerofoil that takes the form of a circular arc. The first was for an arc at zero angle of incidence; the second was for an arc at the arbitrary angle of incidence p. The formulas were

2 a 2 P = 4na sin— pV 2

and

P = 4na sin—sin+ pV2>

where V is the free stream velocity, p the density, a the radius of the circu­lar arc, and a is specified as half the angle subtended by the arc at the cen­ter of the circle. Clearly, the two expressions become the same when P = 0. Kutta published both of these formulas, the first, simpler one in 1902 and the second, more general one in 1910, the same year as Joukowsky’s paper.48 Jou­kowsky, however, said that his colleague Sergei Tschapligin had by this time already discovered the second formula.49

Next came a discussion of the general lift theorem L = p V Г. Here a full proof was provided. Joukowsky approached the problem in terms of the flow of momentum across a control surface. His proof was of a type that has now become standard in modern textbooks. Again, Joukowsky raised issues of priority. He allowed that Kutta discovered this theorem in his unpublished thesis of 1902 but pointed out that he, Joukowsky, in 1906, was the first to publish it.50 He also noted that Finsterwalder had accepted this priority claim.51 Joukowsky granted that Lanchester had been the first to explain the relation between two-dimensional and three-dimensional flow by introduc­ing the trailing vortices. At this point the main business of the paper was announced. In studying the problems of Kutta flow, said Joukowsky, he had found contours of a winglike form (“von flugelartiger Form”) that did not, like Kutta’s arc-wing, give rise to infinite velocities at the leading edge. The aim of the paper was to show how to construct these contours and to test their properties empirically:

Die Beschreibung der Konstruktion dieser Konturen und die experimentelle Untersuchung der ihnen entsprechenden Widerstandskrafte der Flussigkeit stellt den Inhalt dieser Arbeit dar. (283)

The content of the work can be represented as the description of the con­struction of these contours and the experimental study of the corresponding resistance forces of the fluid.

Joukowsky set out, step by step, a geometrical procedure for transforming a circle into the first of his two contours. Whereas Kutta had employed func­tions of a complex variable, Joukowsky took his readers back to the geometry lessons of the classroom. The procedure involved drawing circles and tan­gents, labeling significant points and angles in the figure, carrying out some careful measurements on the diagram, and then adding construction lines. To start the process, said Joukowsky, it is necessary to draw a circle whose center is labeled O and whose radius is a. Some arbitrary point E is then chosen which lies outside the circle, and from E two tangents are drawn. The angle enclosed by the tangents at E is called 2a. It is then required to draw a second, larger circle whose radius is called b. The larger circle does not share the same center O as the smaller circle. Rather, its position is determined by the requirement that it encloses the smaller circle but touches it so that it shares one of the tangents. It is this larger circle that is to be transformed into the aerofoil.

The next step was the addition of construction lines. These are needed to connect any specified point M on the larger circle to a corresponding point M’which will lie on the aerofoil. Joukowsky specified which lengths and an­gles to measure and explained how to use the results to arrive at the position of M’. By selecting, say, ten or twenty representative points around the circle, and following the instructions, the result is ten or twenty points that form an aerofoil shape. The more points that are transformed, the more accurately the outline of the wing emerges.

Joukowsky’s own finished diagram is reproduced here as figure 6.6. It looks complicated, but it is not difficult to identify the two main circles and the tangents, meeting at E, which were needed to start the construction. The resulting aerofoil shape can be discerned draped over the top of the diagram with its sharp tail at point C, on the left-hand side, and its rounded nose at M’on the right-hand side. The aerofoil that Joukowsky chose to construct for purposes of illustration has a marked camber and is very thick. This makes it look unrealistic, but such a degree of curvature and thickness is not intrinsic to the method. Joukowsky explained that the shape of the wing is determined by the three parameters, a, b, and a. As the circles are made larger or smaller and the point E is moved closer to, or farther from, the circles, so the shape of the wing is modified, and it can be made more rounded or more slender. In the limit, as b ^ a, and the larger circle comes ever closer to the smaller

stretches across the top of the figure, having its trailing edge near the letter C, on the left, and its leading edge near the letter M’, on the right. From Joukowsky 1910, 283. (By permission of Oldenbourg Wissen – schaftsverlag GmbH Munchen)

circle, the profile of the wing becomes so thin that it turns into an arc. In fact, it turns into Kutta’s arc.

Joukowsky then showed how to construct his second contour. He gave another set of instructions, this time involving trigonometry as well as geom­etry. Again the process started from two circles, one of radius a, and one of radius b, with b > a. The circles have their centers on the x-axis, and so their point of contact must also lie on the x-axis. Using the center of the smaller circle as the origin O, each point M on the larger circle can be specified by measuring the length r of the line joining O to M and the angle 0 between the line OM and the x-axis. Joukowsky gave the rules for transforming a point M into the corresponding point M’on the contour that is to be constructed. The rules gave the x – and y-coordinates of M’ in terms of the values of r and 0 that specified M. Thus,

Figure 6.7, taken from Joukowsky’s paper, shows that the larger circle b is transformed into a streamlined, rudderlike shape lying symmetrically along the x-axis. The thickness of the rudder depends on the relative size of the circles. As b ^ a, the rudder gets thinner and eventually turns into a straight line of length 2a lying along the x-axis. The arc and the line that constitute a sort of skeleton for the thicker shapes were referred to by Joukowsky as the “bases” of his contours.

The second, empirical, installment of Joukowsky’s paper was published in 1912, two years after the theoretical part. He focused attention on two, aero­dynamically important properties of his theoretical contours that could be made accessible to empirical testing. The two characteristics were (1) the angle of zero lift, that is, the small (and often negative) angle of incidence at which the wing first begins to produce lift, and (2) the slope of the graph when the coefficient of lift was plotted against the angle of incidence. Both of these angles could be deduced from the basic principles of the circulation theory. Their analysis proceeds in a similar way for all aerofoil shapes derived from a conformal transformation of a circle.52 This approach enabled Joukowsky to derive his predictions using Kutta’s lift formulas and then make experimental comparisons between models of Kutta’s arc-like wing and his own wings and rudders. The predictions applied (approximately) to all the profiles.

To address the angle of zero lift, consider again Kutta’s formula for the lift P on a circular arc at an angle в to a flow of velocity V. Kutta found that

where a is the radius of the circular arc of the wing and a is half of the angle

subtended by the arc. Assuming that the velocity V is not zero, then, if the lift is to be zero, the term sin (a/2 + P) must equal zero. In other words, P must equal – a/2. So – a/2 is the angle of zero lift, and it is determined by the ge­ometry of the wing. When Lilienthal selected a wing based on a circular arc, and decided that it should subtend an angle of 2a at the center of the circle, he was implicitly fixing the value of the angle of zero lift. More precisely, he was fixing the angle of zero lift, provided all the assumptions of the theoreti­cal analysis held true. It is striking that such a significant parameter should emerge so readily from the theory, and it was a consequence of the analysis that could be easily tested.

The other angle that interested Joukowsky was the slope of the lift- incidence curve. Joukowsky simplified Kutta’s formula by supposing that the arc of his wing could be treated as equivalent to two straight lines, one con­necting the trailing edge to the highest point of the arc, the other connecting the leading edge to the highest point. The length of the two lines was desig­nated /, and elementary trigonometry showed that / = 4a sin a/2. Substitut­ing this in Kutta’s formula for the lift P gave

P = np/sm^O. + ej V2.

Joukowsky then made two further changes to the formula. First, he replaced the lift by a coefficient of lift called Ky. This was done by dividing both sides of the above equation by V2 and /. Second, for small angles, the sine of an angle equals the angle itself (measured in radians). The equation then becomes

^+e •

Joukowsky noted that the angle (a/2 + P) represented the angle of incidence as measured from the line of zero lift. If the approximations are reasonable, and if the theory was on the right lines, this formula showed that a graph of the lift coefficient against angle of incidence should have the slope np. Jou – kowsky gave the slope the label K. So here was a second testable prediction. He worked out that for a temperature of 20° and an atmospheric pressure of 760 mm, the slope of the graph should be K = 0.39.

Joukowsky had built a wind tunnel in the TH in Moscow. The tunnel had a rectangular, working section of 150 X 30 cm and could achieve wind speeds of up to 22 m/sec. The wing sections under test were suspended ver­tically, with their ends close to the top and bottom of the tunnel, so that they approximated an infinite wing. The sections were rigidly fastened to a framework, and the forces were measured by the weights that were needed to counterbalance them and keep the framework in equilibrium. The wing and rudder contours to be tested had been constructed so that they accorded with the outcome of the geometrical transformations described in the earlier part of the paper. The wing form had been constructed geometrically using a small circle with radius a = 750 mm and with the larger circle of radius b = 762.5 mm and an angle a = 20°. This gave a much thinner and flatter section than the heavily cambered one shown in the diagram in the first installment of the paper. The more slender of the two rudder shapes was generated from two circles a = 250 mm and b = 260 mm, whereas the fatter model was based on two circles a = 250 mm and b = 270 mm.

Joukowsky’s graphs of his experimental measurements revealed the famil­iar pattern when lift and drag coefficients are plotted against the angle of in­cidence. The lift increased in a roughly linear fashion with angle of incidence up to about в = 15°, while the drag stayed low until about the same point and then increased rapidly. Joukowsky immediately noted that his coefficients of lift and drag had higher values than those reported by Eiffel for comparable shapes. This sort of discrepancy between the wind tunnels in different na­tional laboratories was to plague experimental work for many years. In this case Joukowsky suggested that the Moscow experiment approximated more closely the infinite wing assumed in the theoretical calculations. The impor­tant question, though, was whether his experimental graphs corroborated the theoretical predictions.

Joukowsky found that the angle of zero lift for his theoretically derived wing profile fitted more closely to the predicted value than did the Kutta – like arc that Joukowsky called its “basis” or skeleton. But even the model wings that were meant to conform to the Joukowsky profile did not achieve quite the predicted degree of lift. The wing ceased to give lift at -6°, and the circular arc that was its basis at around -4° compared with a theoretical value of (a/2) = -10°. Some of his computed values of the slope K, however, were very close to the predicted value where K = pn = 0.39. Thus he reported that K = 0.38 for the arc, K = 0.37 for the wing, but only K = 0.30 for the rudder.

The wind tunnel at the Moscow TH was soon to figure again in the pages of the Zeitschrift fur Flugtechnik. In June 1912, Joukowsky’s assistant G. S. Lou – kianoff published graphs showing the lift, drag, and center-of-pressure char­acteristics of the wing contours of seven types of aircraft that were currently flying with success: the Breguet, Antoinette, Wright, Bleriot, Farman, Hen – riot, and Nieuport machines.53 As von Mises observed, these early Moscow experiments gave a slope for the lift-incidence curve that closely corresponded to the theoretical value, though later experimenters found a slightly smaller value. In general, said von Mises, two-dimensional wing theory overestimates the slope by about 10 percent and underestimates the angle of zero lift by one or two degrees.54 But it was the theoretical achievement, rather than the experimental work, that proved most significant. Joukowsky’s aerofoils, the J-wings, as they were sometimes called, aroused an immediate and positive response in Germany. The interest in the theory was not abstract, aesthetic, or otherworldly. Joukowsky’s theoretical profiles became the focal point for a series of developments that brought the mathematical analysis of lift into intimate contact with both physical reality and engineering practice.

When I returned to Cambridge in 1919 I aimed to bridge the gap between Lamb and Prandtl.

g. i. taylor, “When Aeronautical Science Was Young" (1966)1

Oscar Wilde declared that if you tell the truth you are bound to be found out sooner or later.2 There is a corresponding view that applies to scientific theories. Given good faith and genuine curiosity, a true theory will eventu­ally prevail over false ones. These sentiments make for good aphorisms but the epistemology is questionable. Even if it were right, there would still be the need to understand the contingencies and complications of the historical path leading to the acceptance of a theory. My aim in the next two chapters is to describe some of the contingencies that bore upon the fortunes of the cir­culatory theory of lift in Britain after the Great War. I shall come back to the philosophical analysis of theory acceptance in the final chapter of the book, when all the relevant facts have been marshaled. I begin the present discus­sion with some observations about the flow of information between German and British experts before, during, and after the Great War.

Southwell entered Trinity in 1907 to read mechanical sciences. He was an engineer, but an engineer with impressive mathematical skills.38 In 1909 he was placed in the first class of part I of the Mathematical Tripos and in 1910 graduated with first-class honors in the Mechanical Sciences Tripos. He was coached by Pye and Webb, two of the best mathematical coaches of the time. On graduation he began research on elasticity theory and the strength of ma­terials and in 1912 became a fellow of Trinity. In 1914 Trinity offered Southwell the post of college lecturer in mathematics but he did not take up the offer because of the outbreak of war. He volunteered for the army and was sent to France. In 1915, however, he was brought back to work on airships for the

navy. In 1918 he was transferred to the newly created Royal Air Force, with the rank of major, and was sent to Farnborough in charge of the aerodynamic and structural department. After demobilization, and a brief return to Trin­ity, in 1920 he went to the National Physical Laboratory as superintendent of the Aerodynamics Department. He stayed at the NPL for five years and then returned again to Cambridge, where (unusual for an engineer) he was a fac­ulty lecturer in mathematics.

It was in the field of applied mathematics, rather than practical engineer­ing, that Southwell made his outstanding contribution. He developed novel mathematical techniques for the analysis of complex structures of the kind used in the building of airships. The technique was called “the relaxation of constraints” and depended on replacing the derivatives in the equations and boundary conditions by finite differences.39 Though the technique was initially developed to deal with engineering problems, Southwell later dem­onstrated its power as a general method of solving differential equations. Referring to the unavoidable complexities of practice, and the uncertainties

in data of whatever kind, he called his own Relaxation Method “an attempt to construct a ‘mathematics with a fringe.’”40 He was not only interested in elasticity and the strength of materials but also worked on viscous flow. Like Bairstow, Southwell started from Oseen’s approximation to the full equations of viscous flow and the developments provided by Lamb.41 In 1929 Southwell was offered the chair in engineering at Oxford, which he accepted after some hesitation but where he stayed until his retirement. Southwell had a lively sense of the different demands confronted by engineers and mathematical physicists, but it may be revealing that Glazebrook said of him that, although he was an Oxford professor, he was still a Cambridge man.42

As superintendent of the Aerodynamics Department at the NPL, South­well played a prominent role in the discussions that took place in the Aero­nautical Research Committee after the war when plans for future work were thrashed out. Southwell always placed great emphasis on fundamental scien­tific research. It was the long term, not the short term, that counted. Though an engineer by training, he defended the value of academic research of the kind so often attacked by the practical men. This came out clearly in the pol­icy discussions that took place in February 1921, devoted to the topic of “The Aeroplane of 1930.” The participants were invited to anticipate the character and needs of aviation in ten years’ time. Southwell wittily subverted the discussion by posing the question If we could know where we would be in ten years’ time, why wait? His point was that fundamental advances could not be predicted. He suspected that, whatever we said, we would be wrong.43 The most we can do is to be conscious of the gaps in existing knowledge and try to fill them. Consider, he said to the committee, the fundamental cause of the lift and drag on an aircraft wing: “We have much empirical data in regard to aerofoils, but our ignorance of the mechanisms by which their lift and drag are obtained has hitherto been almost absolute.” Here was a worthy focus for research: the true mechanisms of lift and drag must be identified.44

One might assume that Bryant and Williams’ experiments, as well as those of Fage and Simmons, were performed to identify the mechanisms that Southwell had in mind. But if this were so, we would expect that the results of the work (give or take Taylor’s reservations) would have been seen by South­well as furnishing the desired account of lift and drag. This was not how he saw them. The same sense of ignorance about fundamental causes still per­vaded Southwell’s thinking after this experimental work had been completed and after Glauert had begun to provide his superbly clear exposition and de­velopment of the circulation theory. The same pessimism that was expressed privately in committee in 1921 was expressed again, and publicly, some four years later in two lectures that Southwell gave in 1925. One of these lectures, on January 22, was to the Royal Aeronautical Society; the other, on August 28, was to the British Association meeting in Southampton.

The lecture to the RAeS was titled “Some Recent Work of the Aerodynam­ics Department” and was meant as a summary of the achievements of the department during the years of Southwell’s superintendence.45 His return to Trinity was an opportunity to take stock. Southwell began by welcoming the change from ad hoc wartime experimentation to programs of research guided by theory. Two main lines of theoretical concern were identified. First, there was the classical theory of stability, and Southwell described in detail the re­cent work of Relf and others. This had taken the experimental determination of the damping coefficients for roll, yaw, and pitch to new levels of sophistica­tion. The second set of theoretical concerns dealt with the fundamentals of fluid flow. For aerodynamics, said Southwell,

I suppose no problem is so fundamental as the question—why does an aero­foil lift? We can hardly rest satisfied with the present position—which is, that we have next to no idea. To answer the question completely would involve no less than the solution of the general equations of motion for a viscous fluid, and attacks on these equations have been made from all angles. Considering the energy expended, the results have been very small; but then, these are about the most intractable equations in the whole of mathematical physics. (154)

Southwell mentioned the role played in this (so far fruitless) endeavor by Bairstow, Cowley, and Levy and then moved on to the approach adopted by Prandtl, namely, using the inviscid theory of the “hydrodynamic textbooks” informally conjoined with the idea of a viscous boundary layer. In this way the “once discounted” classical theory of the perfect fluid had been “rein­stated” and could provide a close approximation to the truth when used “un­der proper control, and aided by assumptions based on physical intuition” (156). At the NPL, said Southwell, every opportunity had been taken to check the validity of Prandtl’s theory, and “in the main one must say, I think, that it has passed the ordeal with flying colours” (156). The most important tests “are those which Messrs. Fage, Bryant, Simmons and Williams have made” (156). Southwell explained that at the time of his lecture this work had not yet been published but it had confirmed the most important result, namely, “the theoretical relation between lift-coefficient and the circulation” (156).

At this point Southwell’s audience might have been puzzled. They were being told that Prandtl’s theory had passed the tests to which it had been subject with “flying colours,” and yet a moment before, Southwell had de­clared that experts had “next to no idea” how a wing produced lift. Didn’t these claims contradict one another? The answer is that Southwell’s argument was consistent but depended on a suppressed premise. For Southwell, the experiments of Fage and Simmons only justified the use of inviscid theory as a way of representing the real flow. They did not show that it truly described the flow. As far as Southwell was concerned, Fage and Simmons were not tracing footprints in the snow. In their experiments the imprint of reality had not been made in some familiar and reliable medium. Their analysis had used ideal fluid theory. The nature of the beast that left the footprints was still under discussion. The inviscid approach left it an open question whether the “actual flow” corresponded to the representation, and the most plausible answer was that it did not. The no-slip condition was violated by the inviscid representation, and Prandtl had assumed that the flow was steady. The eddies in the wake were neglected. The place to look to resolve these issues, Southwell concluded, was the boundary layer. It was this aspect of Prandtl’s work that really engaged Southwell. As he put it, “the conditions in this layer are the ultimate mystery of aerodynamics: somehow or other, in a film of air whose thickness is measured in thousandths of an inch, that circulation is generated which we have just seen to be the essential ingredient of ‘lift’” (158). Research should concentrate on the boundary layer. Theoreti­cally this required a deeper understanding of the equations of viscous flow; experimentally it called for the development of special instruments such as microscopic Pitot tubes to probe the boundary layer. Southwell mentioned that Muriel Glauert was working mathematically and experimentally on the calibration of such an instrument.46

Here was the explanation of Southwell’s apparently conflicting claims. Prandtl’s theory of the finite wing “worked,” but it could not be true because the mathematical analysis depended on false boundary conditions. This was the suppressed premise, which rendered the argument consistent. Although Prandtl’s wing theory could pass many tests, and even pass them with flying colors, it could not, by its very nature, answer the question that Southwell wanted to answer. In a very British way, he wanted to know how a viscous fluid generates lift. In the discussion after the lecture, in response to Major Low, Southwell said: “The really interesting part of Prandtl’s work was the work he had been doing subsequently in his study of the ‘boundary layer,’ because that work might ultimately explain why the assumptions which could not be correct could make such amazingly true predictions” (166).

In a lecture titled “Aeronautical Problems of the Past and of the Future,” delivered later in the same year, Southwell insisted that the aim of research was “not so much to achieve, as to understand.”41 Scientists should not be content with “achievement,” “unless it be the result of understanding’—something of which the “practical man” would never be persuaded (410). Understanding meant understanding based on a sound theory. Southwell identified three triumphs of British aeronautics that, in his opinion, met this condition. They were (1) the ability to build stable aircraft, (2) the analysis of the dangerous maneuver of spinning and its avoidance, and (3) the achievement of control in low-speed flight even after the aircraft had stalled. In all three cases, he argued, the end result had enormous practical value but the driving force had been the aim to understand. And it was mathematical analysis that had furnished the understanding.

The theory of lift was conspicuous by its absence from this list of tri­umphs. For Southwell, Prandtl’s wing theory was an achievement that was not yet informed by an adequate theoretical understanding. Bryant, Wil­liams, Fage, and Simmons were mentioned by name, and Southwell used diagrams taken from their papers. The role that he accorded the work, how­ever, was that of showing that the effects of viscosity can be ignored as far as the sliding of air on air is concerned but cannot be ignored very close to the surface of a wing or in the wake behind the wing. It is what happens in these regions that constitutes “the ultimate problem of hydrodynamics” (417). It was this “ultimate” problem that Southwell had in mind when he asked: Why does a wing generate lift? He was not denying the role of circulation, nor was he belittling the insights of Lanchester, Prandtl, or Glauert as they continued to develop the inviscid theory of lift. His point was that no one, following this route, could hope to explain the origin of circulation.48 Within inviscid theory, circulation had to be a postulate not a deduction.

Southwell’s skeptical position was endorsed by H. E. Wimperis, the quiet but influential director of scientific research at the Air Ministry.49 Wimperis had trained as an engineer in London and Cambridge and had sat the Me­chanical Sciences Tripos in 1890. During the Great War he had served as a scientist with the Royal Naval Air Service and had designed a bomb sight that carried his name. After the war he worked at Imperial College in a labora­tory financed by the Air Ministry. Along with Tizard, he was later to play an important role in the development of Britain’s radar defense system. In 1926 Wimperis, in his role as director of research, published a survey article in the Journal of the Royal Aeronautical Society called “The Relationship of Physics to Aeronautical Research.”50 One of Wimperis’ aims was to send the message that the Air Ministry and government were aware of the need for fundamental research. What, he asked, was engineering but applied physics? Government scientists at the National Physical Laboratory and Farnborough must have the freedom to pursue basic, physical problems. A second aim was to argue that this policy had already produced significant results. Here Wimperis cited, among other examples, the mathematical work that had been done on fluid flow and, in particular, the flow around a wing. It rapidly became clear, how­ever, that in Wimperis’ view, the approach based on inviscid theory was not an exercise in real physics but a mere preliminary to a genuine understanding of lift. On a classical hydrodynamic approach, he noted, the circulation must be added in an arbitrary way to the flow, and this only provides an “analogy with the lift force experienced by an aerofoil” (670). Admittedly there have been some successful predictions made “by the employment of this conven­tion” (670), but the theory becomes “somewhat far-fetched” in its account of what is happening on the surface of the wing. “Circulation,” said Wimperis, “must have a physical existence since velocity is greater above the wing than below; though this real circulation is a circulation with no slip, whereas the mathematical circulation has slip. Hence the rather amusing situation arises of adding to the mathematical study of streamlines a conventional motion which could not really arise in an inviscid fluid!” (670). Southwell was right, said Wimperis, in insisting that the real problem lay in discovering what was actually happening in the very thin, viscous layer close to the wing. This was a problem in physics rather than something that could be evaded by the use of mathematical conventions and unreal boundary conditions.

The continuity between Frank’s ideas, developed in the 1930s, and the more recent work in the sociology of scientific knowledge was noted by the phi­losopher Thomas Uebel in his paper “Logical Empiricism and the Sociology of Knowledge: The Case of Neurath and Frank.”71 Uebel concluded (I think rightly) that Frank had anticipated all the methodological tenets of the Strong Program (147), but he insists that there is an important difference: the advo­cates of the Strong Program are “relativists,” whereas Frank “did not accept the relativism for which the Strong Programme is famous” (149). This state­ment is incorrect. The similarity does not break down at this point. Frank was also a relativist. I first want to establish this fact and then I shall use Frank’s relativism to illuminate some examples of aerodynamic knowledge.

Frank’s relativism was implicit, but clearly present, in his paper on the acceptance of theories, for example, in his assertion that there was no such thing as “perfect” simplicity. He meant that there is no absolute measure of simplicity that could exist in isolation from the circumstances and perspec­tives of the persons constructing and using the theory. If there is no absolute measure, then all measures must be relative, that is, relative to the contingen­cies and interests that structure the situation. Recall also the trade-off be­tween simplicity and predictive power. Frank said this meant there was no such thing as “the truth” because there was no absolute, final, or perfect com­promise. The relativist stance is epitomized by Frank’s comparison between assessing a theory and assessing an airplane. Talk about an “absolute aircraft” would be nonsense. All the virtues of an aircraft are relative to the aims and circumstances of the user. If the process of scientific thinking has an instru­mental character, and theories are technologies of thought, then talk about an absolute theory, or the absolute truth of a theory, is no less nonsensical.

Frank made his relativism explicit in a book called Relativity: A Richer Truth.72 Einstein wrote the introduction, and the book contains a number of examples drawn from Einstein’s work, but the book is not primarily about relativity theory. It is a discussion of the general status of scientific knowl­edge and its relation to broader cultural concerns. Frank’s purpose is much clearer in the title of the German edition, Wahrheit—Relativ oder absolut? (Truth—relative or absolute?),73 which poses the central question of the book. Does science have any place within it for absolutist claims? Frank said no. No theory, no formula, no observation report is final, perfect, beyond revision or fully understood. The world will always be too complicated to permit any knowledge claim to be treated as absolutely definitive. In devel­oping this argument Frank draws out the similarities between relativism in the theory of knowledge and relativism in the theory of ethics. Are there any moral principles that must be understood as having an absolute character? The claim is often made, but Frank argues that if close attention is paid to the actual employment of a moral principle, it always transpires that qualifica­tions and complications enter into their use. “For this so-called doctrine of the ‘relativity of truth’ is nothing more and nothing less than the admission that a complex state of affairs cannot be described in an oversimplified lan­guage. This plain fact cannot be denied by any creed. It cannot be altered or weakened by any plea or admonition on behalf of ‘absolute truth.’ The most ardent advocates of ‘absolute truth’ avail themselves of the doctrine of the ‘relativists’ whenever they have to face a real human issue” (52).

The book on relativism was written during the 1940s after Frank had left Prague. It was a response to a systematic attack on science by theological writ­ers in the United States. They blamed science for the ills of the time, such as the rise of fascism, the threat of communism, the decline in religious belief, and the loss of traditional values. The critics said that science encouraged relativism and relativism was inimical to responsible thinking. Frank con­fronted the attack head on. He did not seek to evade the charge by arguing that scientists were not relativists (and therefore not guilty); indeed, he said that scientists were relativists (and should be proud of the fact). The danger to rational thought and moral conduct came, he said, not from relativism but from absolutism. If we try to defend either science or society by making absolutist claims, we will merely find ourselves confronted by rival creeds making rival, absolute claims. If we take the issue outside the realm of reason, we must not be surprised if it is settled by the forces of unreason (21). Relativ­ism, he argued, is the only effective weapon against totalitarianism and has long been instrumental in the progress of knowledge. It has been made “a scapegoat for the failures in the fight for democratic values” (20).

Frank alluded to the many caustic things that critics said about relativism and then added, “this crusade has remained mostly on the surface of scientific discourse. In the depths, where the real battle for the progress of knowledge has been fought, this battle has proceeded under the very guidance of the doctrine of the ‘relativity of truth.’ The battle has not been influenced by the claim of an ‘absolute truth,’ since the legitimate place of this term in scientific discourse has yet to be found” (20-21). Notice that Frank placed the words “absolute truth” in quotation marks because, as a positivist, he would have been inclined to dismiss the words as meaningless. For him they had no real content and no real place in meaningful discourse. The claims of the absolut­ists were to be seen as similar to the claims of, say, the theologian. But if the best definition of relativism is simply the denial that there are any absolute truths, and if relativism is essentially the negation of absolutism, then relativ­ism is meaningless as well. The negation of a meaningless pseudoproposi­tion is also a meaningless pseudoproposition. Relativism would, likewise, be revealed as an attempt to say what cannot be said. This may explain why Frank also placed the words “relativity of truth” in quotation marks. There is much to recommend this analysis. It might be called the Tractatus view of relativism.74 Where, however, does this analysis leave Frank’s book? Does it not render the book meaningless and pointless? The answer is no. The reason is that absolutism, like theology, has practical consequences, and whatever the status of its propositions, the language is woven into the fabric of life. It provides an idiom in which things are done or not done. Even for the strictest positivist this penumbra of practical action has significance.

What is done, or not done, in the name of absolutism? The answer that Frank gave is clear. Absolutism inhibits the honest examination of the real practices of life and science. It is inimical to clear thinking about the human condition. The meaningful task of the relativist is grounded in this sphere. It is to be expressed by combating obscurantism and fantasy and by replacing them with opinions informed by empirical investigation. That is the “richer truth” referred to in the title of the English-language edition of Frank’s book. This down-to-earth orientation also provides the answer to another prob­lem that may appear to beset Frank’s relativist position. What is scientific knowledge supposed to be relative to? The answer is that it is relative to what­ever causes determine it. There are as many “relativities” as there are causes. That is the point: knowledge is part of the causal nexus, not something that transcends it. Knowledge is not a supernatural phenomenon, as it would have to be if it were to earn the title of “absolute.” Knowledge is a natural phenomenon and must be studied as such by historians, sociologists, and psychologists.

Frank’s relativism, and the relativist thrust of the positivist tradition, seems to have been forgotten.75 A number of prominent philosophers paid a moving tribute to Frank after his death in 1966, but they did not mention his relativism.76 In the course of this forgetting, a strange transformation has taken place. In his Kleines Lehrbuch des Positivismus, von Mises spoke of “the phantom of absolute cognition.”77 That phantom still stalks the intellectual landscape, but in Frank’s day it was scientists who were accused of relativism, whereas today it is scientists, or a vocal minority of scientists, who accuse others of relativism. From being the natural home of relativism, science has been polemically transformed into the abode of antirelativism and hence of absolutism. A significant role in this transformation has been played by phi­losophers of science who are today overwhelmingly, and often aggressively, antirelativist in their stance. The involvement of analytic philosophers should have ensured that the arguments for and against relativism were studied with clarity and precision. This has not happened. The philosophical discussion of relativism is markedly less precise today than when Frank addressed it fifty years ago and provided his simple and cogent formulation of what was at stake.