Duhem, Brody, Hubble: Approximation and the Scope of Theories

In this essay I'd like to highlight some similarities between the ideas of two physicists who have written extensively on the philosophy of physics. The first is Pierre Duhem, author of The Aim and Structure of Physical Theory. The second is Thomas Brody, author of The Philosophy Behind Physics. In reading these two books I have been struck by some remarkable similarities that I think are worth pointing out. This is somewhat surprising since Duhem was primarily a phenomenalist (though he makes concessions to realism with his idea that science approaches a "natural classification") while Brody seems to be a realist (but one who makes concessions to phenomenalism in his insistence that science is necessarily approximate). It is also surprising because Brody makes no reference to Duhem's work, even though Duhem's book was published in 1906 (in French, an English translation has been available since at least 1954) and Brody 's philosophical work was published mostly in the 1970's and 1980's. These ideas have also given rise to some thoughts about some of Edwin Hubble's work, which I have been studying recently (Hubble's The Realm of the Nebulae is a good introduction to his work).

One similarity between these two is their emphasis on approximation in physics. Both Duhem and Brody recognize that all measurements are approximate and all theoretical predictions are approximate as well. Duhem makes this point the basis for his famous thesis that any experimental measurement outcome is necessarily consistent with an infinite number of theories and any theoretical prediction is consistent with an infinite number of experimental measurement outcomes (a thesis, often known as underdetermination, which was later expanded by W. V. O. Quine, but with somewhat different emphasis). Brody emphasizes the fact that approximations are generally valid in some circumstances in invalid in others. The approximate nature of scientific theories then becomes the basis for his idea of the scope of a theory. The scope of a theory is the range of phenomena for which the theory is valid. The theory is not expected to be valid for phenomena that lie outside its scope. Brody argues that one of the main goals of science is to delimit the scope of theories (as well as to create new theories).

The concept of a limited scope for physical theories is common to Duhem and Brody. Indeed, they both find it quite acceptable for a physicist to use two completely incompatible theories in the course of her work. Duhem quotes Poincare to state that one can use logically incompatible theories as long as one takes care not to mix them or to "get to the bottom of things." Brody presents a somewhat subtler view based on his idea of scope. It is acceptable even to mix theories that are logically incompatible provided that one doesn't use any theory to describe phenomena that are outside of its scope. He cites as an example molecular physics in which the nuclei are treated as classical Newtonian point masses, while the electrons are treated as relativistic quantum particles. Perhaps an even better example he uses is that of studying the influence of the Moon's gravity on a pendulum by first calculating the Moon's orbit (treating Earth as a Newtonian point mass for this purpose) and then treating the gravitational force between the Moon and the pendulum bob as a perturbation on the pendulum's "normal oscillation" (treating Earth as an infinite plane and Earth's gravitational field as uniform). Here within a single problem the physicist uses to logically incompatible models of the same object, but for different phases of the problem. Perhaps Poincare would not consider this "mixing" the two models - but the main point is that each model is used to predict a phenomenon that is within the scope of that particular model. I'm well acquainted with this type of work, since my own research has largely focused on the interaction of quantum particles with oscillating classical electric fields, so I mix classical electrodynamics and quantum physics all the time.

An important consequence of the fact the scientific theories are approximate and have limited scope is that scientific theories are not about truth.
Both Duhem and Brody insist that scientific theories cannot be evaluated on a logical basis. Theories are neither true nor false in a logical sense. The concept of a theory of everything (a theory that explained all phenomena) would be meaningless for both Brody and Duhem. Duhem would view such a theory as a "cosmology" (in the ancient meaning of this term) and thus not a scientific theory at all. Indeed, his chief goal in Aim and Structure was to separate science from, and make it independent of, cosmology.

One more similarity between Duhem and Brody is their insistence on the evolutionary nature of science. Duhem seems to disdain the very idea of scientific revolutions. In part this is based on his extensive historical study of medieval physics which illustrate the origins of many of the ideas that eventually reached maturity in Newton's physics. It should be noted that Duhem wrote his book around 1905, so he was unaware of the coming quantum and relativistic "revolutions" (though I doubt these would have changed his views). Brody seems to accept the idea of revolutions, but rejects Kuhn's idea that between revolutions physicists only solve problems using an established paradigm. He points to the extensive development of mechanics after Newton, pointing out that Newton might very well be unable to understand things like Hamilton-Jacoby theory and the geometrical mechanics of Poincare even though these are supposedly the result of "problem solving" within the paradigm that Newton himself created. I intend to write more about evolution versus revolution in science at a later date.

For now what I'd like to do is apply the framework of a theories scope to an idea that is a key part of Edwin Hubble's work, an idea he refers to as "The Principle of the Uniformity of Nature." Now this phrase is often used to denote an essentially metaphysical statement that is supposed to justify induction, but I don't think that's what Hubble means by it. He means something more like a methodological principle, and I think it can be clearly explained in terms of Brody's idea of scope. What Hubble is saying is this: when an empirical law has been found, we should assume the widest possible scope for this law. For example, Henrietta Leavitt found an empirical law relating the apparent brightness (and thus, essentially, the intrinsic brightness) and the period of Cephied variables in the Large Magellanic Cloud. Hubble applied the Principle by assuming that ALL Cepheid variables (as identified by the shape of their light curves) follow this law, even those in distant galaxies and in various parts of our own galaxy. This turned out to cause problems because it led to inconsistent results. But Hubble was never trying to say that these empirical laws really did have universal scope, but only that we should assume that they do until we have reason to think otherwise (i.e. until that empirical law leads to contradictions with another empirical law, or with directly observed data). When such contradictions occur the scope of one of the laws involved must be reduced. In the case of Cepheids, the contradictions were resolved by proposing that there are two types of Cephieds with different period-luminosity relations (one type resides in the galactic plane, the other type in the halo).

Of course, if two empirical laws contradict it may be hard to determine which one should have its scope reduced. In some cases we may be able to carry out an experiment or observation that will clearly favor the modification of one law over the other. But in many cases we may need to guess, and our guess will be guided by how the modification fits with all of our other theories. This view actually ties in well with Duhem's other famous thesis: that we never test a theory in isolation, but rather we test the entire system of current theories. When a predictions is contradicted by a measurement we never know which theory (or assumption, etc.) is to blame, but we must make a choice of what to modify. That choice will be made with a consideration for the impact it will have on our system of theories and its fit to all previously known data. For example, we will be unlikely to modify a foundational theory that explains a wide range of phenomena. Instead, we will probably choose to modify (or delimit the scope of) a theory which if of lesser importance to the entire structure of our theoretical system. This is essentially Lakatos' idea of modifying the "protective belt" rather than the "hard core" of our theoretical system.

Note that the Principle of the Uniformity of nature is a methodological assumption with no logical basis. Logically we have no reason to suppose that the scope of an empirical law or theory extends beyond the data already known to fit it. It is interesting, though, that Hubble's methodological assumption can be recast in terms of Popper's fundamental methodological assumption to always choose the most falsifiable theory. Certainly, we make any theory more falsifiable by assuming it has a universal scope rather than a limited scope. The difference in Hubble's proposal is that he suggests limiting the scope of the empirical law rather than discarding it as Popper (at least in his early work) would have it. I think Hubble's perspective on astronomy fits in very well with the scheme that seems common to both Brody and Duhem.

An analogy that Brody uses can help make sense of all this. He says that science is rather like a map. A map is always approximate. The idea of a map that depicted its subject exactly down the finest detail (i.e. showing blades of grass in Central Park, and the ant crawling on the blade of grass, and the crumb of bread in the ants mandibles, etc.) is ridiculous. Not only that, but such a map would be useless. Moreover, as we make our way around a city we may use multiple incompatible maps. For example, we may have a street atlas, a subway map, and a restaurant guide. These maps are not logically compatible because they will indicate different relative distances between supposedly identical locations (subway maps, in particular, are always schematic and do a poor job of depicting geographical relations between stations). However, in going from a hotel on Fifth Avenue (why not?) to the Statue of Liberty we might make use of a street map to find the nearest subway stop, the subway map to get us to the station closest to the ferry terminal, the street map again to find the ferry terminal, then the ferry map to make sure we get on the correct route. None of these maps embodies the "truth" of New York City, but they all provide a useful depiction of certain structural relations within the "real" New York City. They are incompatible in a logical sense, and yet we can use them together to get where we want to go. In a similar way, none of our scientific theories embody the "truth" of the world, but they do provide useful depictions of certain structural relations within the "real" world. We can use incompatible scientific theories to solve problems and make predictions about the physical world, provided we know which structural relations are accurately depicted by a given theory and which are not.

The Scope of a Scientific Theory

In this essay I want to follow up my discussion of Lakatos' conception of scientific research programmes by describing Thomas Brody's conception of the scope of scientific theories. Brody's views, as set forth in his The Philosophy Behind Physics (a book which he did not complete before his death, and which includes some essays written by him that were never intended for the book), seem to have been largely ignored by the philosophy of science community. It may be that his ideas are fundamentally flawed, and have been ignored for good reason. I'm not enough of an expert to judge that. However, I find his concept of scope quite compelling. In particular, it seems to me that Brody's approach can be viewed as another way of keeping Popper's basic approach to scientific methodology while simultaneously addressing some of the problems that beset Popper's views (see my previous essay for a brief discussion of some of these problems).

Brody's understanding of scientific progress sees the evaluation of scientific theories as divided into two stages. In the first stage, a nascent theory gains support by accumulating confirming evidence (corroboration, in Popper's terminology). A newly proposed theory that fails to be supported by empirical evidence will likely be discarded. However, once a theory has survived this early stage it moves on to a phase in which the focus is on trying to find situations in which the theory fails (just as in Popper's falsification approach). The purpose of finding these failures, though, is not to falsify the theory in anything like an absolute sense. The theory will not be discarded simply because a few failures occur. Rather, these failures of the theory are used to delimit the theory's scope.

The scope of a theory, as Brody presents it, is something like the set of circumstances in which the theory will produce successful predictions. This definition, though, is probably too vague. If the successes and failures of the theory follow no apparent pattern then it is probably impossible to define the scope of that theory. But a theory's scope can become well defined if we can translate the "circumstances" in which the theory is used into something like a parameter space. If we then find that the theory produces successful predictions for some region of this parameter space, but fails to produce successful predictions outside this region, then the region of success effectively defined the scope of the theory. Brody seems to assume in his writing that we should expect theories to behave in this way. He does not address pathological cases in which the points in parameter space at which the theory is successful are intimately intermixed with the points at which the theory fails. I think this is because his concept of scope is largely derived from his view that all theories are approximations (see my essay on approximations in physics for my take on this). Mathematical approximations (such as truncating a Taylor series, for example) are generally valid for some range of values for the relevant variables and invalid outside of that range. Brody seems to think the scope of a theory can be determined in much the same way.

Now I find this idea compelling because it avoids the assumption that I have claimed lies at the heart of naive falsificationism, namely that there is one "true" theory that is capable of predicting everything in the Universe. Brody's sees scientific theories as human inventions, inventions that can at best approximate reality. Science, from this point of view, is not about pursuing absolute truth but about finding approximate truths and understanding when those approximate truths hold and when they do not. Brody finds it perfectly acceptable to have one theory that describes a phenomenon in a certain parameter range and another logically incompatible theory that describes the same phenomenon in a different parameter range. He discusses the various models used in nuclear physics in this context. It is possible that one could even view wave-particle duality (of photons, electrons, etc.) in this way, although it is not clear how one could define parameters such that wave behavior manifests for one range of parameter values and particle behavior for a different range.

Another reason I find Brody's idea compelling is that it seems to reflect some important parts of scientific history. When a well-established theory is falsified, historically scientists have not tossed the theory aside and moved on to something else. Certainly, there is a desire to formulate a new theory that will work where the previous theory failed. But quite often the "falsified" theory is kept on. If one can clearly determine the scope of the theory then it is rational to continue using the old theory in those situations which fall within its scope. Classical Newtonian mechanics is an excellent example of this. Newtonian mechanics has been falsified over and over, yet we have not tossed it aside (I teach a two-semester sequence on intermediate classical mechanics and I don't think I am wasting my student's time!). We still use Newtonian mechanics in those situations where we are confident that it will work. There may be a sense in which physicists are convinced that quantum mechanics and relativity are "truer" than Newtonian mechanics, and that we are only still willing to use Newtonian mechanics because it accurately approximates those "truer" theories in certain situations. But in the case of quantum mechanics, showing that the "truer" theory reduces to Newtonian mechanics in the appropriate circumstances has proved to be challenging (particularly in the case of chaotic systems). The same may be true for general relativity, although I know much less about that case. I think Brody would claim that we need not worry so much about this issue. As long as we know when it is okay to use Newtonian mechanics, then it is fine for us to do so. We don't have to convince ourselves that we are really using quantum mechanics and general relativity in an approximate form.

Now I think that the concept of scope helps resolves some of the problems associated with naive falsificationism, but it certainly doesn't settle all of them. In particular, it seems to suffer at the hands of the Duhem-Quine thesis. If a theory fails to predict the results of an experiment, how can we be sure that the experiment is outside the theory's scope? It could be that the failure is due to an auxiliary hypothesis (thus indicating that the experiment is outside the scope of that auxiliary hypothesis). So just as we can never falsify a theory in isolation, we can never determine the scope of a theory in isolation. We can only determine the scope of an entire network of theories that are used to predict the results of an experiment (and to interpret the experimental data). Another way to state this is that when we test a theory we must inevitably assume the validity of several other theories in the process. This assumption may prove to be correct, or it may not. Whenever we get a negative result, it could be a failure of the theory we are testing or it could be a failure of the assumptions we have made. This makes determining the scope of a theory a complicated process. In practice we must evaluate many theories at once and any failure signifies that we are outside the scope of at least one of the theories. Delimiting the scope of a set of theories thus becomes and endless process of cross-checking. So Brody's view faces some serious challenges - but I think it deserves more attention than it has received.

I'd like to close this essay by trying to tease out some similarities between the approaches of Lakatos and Brody. Both seem to build on Popper's basic premise. Both avoid inductivist ideas. Both attempt to defend the rationality of science (contra Kuhn and Feyerabend, etc.). I think one could even reformulate Lakatos' ideas using Brody's language. When we perform an empirical test of a theory we are really testing a whole network of theories and assumptions. However, based on the details of the experiment we may have different levels of confidence in the various theories that compose the network. We may be very confident that we are well within the scope of many of these theories/assumptions, and therefore we would be very unlikely to blame any failure on these parts of the network. The theories or assumptions in this group would form the "hard core" in Lakatos' terminology. On the other hand, we may be less certain about the where the experiment falls in relation to the scope of other theories and assumptions in the network. We would be much more likely to blame a failed prediction on one of these theories/assumptions. This group of theories and assumptions then forms the "protective belt". This represents a significant change in Lakatos' conception (at least, as far as I understand it) because now theories could move between the hard core and the protective belt depending on the context of the experiment. I think this is a step in the right direction because it provides some much-needed flexibility. In particular, it opens up the door for falsifying (or at least delimiting the scope of) those theories which are part of the hard core. If a theory that is in the hard core is always in the hard core then it would seem to be unfalsifiable, and thus it would become a metaphysical principle or a convention rather than a physical theory. Yet, this idea does allow for the possibility that some theories (or principles, or whatever) could have universal scope and could therefore be "permanent members" of the hard core.

I have actually used Brody's concept of scope in teaching students about the nature of science. I have them perform an experiment to determine the relation between the period of a pendulum's oscillations and it's length. They consider two mathematical models: one in which the period is a linear function of length, and one in which the square of the period is a linear function of length. They generally find that both models work well to fit their data. They then use each model to predict the period of a 16-meter pendulum, and then they actually measure the period of such a pendulum (we have a 16-m Foucault pendulum in our lobby). They find that the second model's prediction is reasonably close, while the first model is way off. We could consider this a falsification of the first model, but I try to lead them toward a different conclusion: that we have really just shown that long pendulums lie outside the scope of the first model. In fact, if we made the pendulum VERY long (say, a significant fraction of Earth's radius) then we would find the second model would fail as well. The basic idea is that all models have a finite scope, so a failure of a model doesn't mean we should discard it or else we would discard everything. However, in evaluating between two models we may find that the scope of one completely encloses but extends beyond the scope of the other. In that case we would clearly prefer the model that has the wider scope. On the other hand, if the two models had scopes that overlapped only partially or else did not overlap at all then it would be quite reasonable to keep both models around so that we can use the model which is most appropriate for the prediction we are trying to make.