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.

Approximation in Physics

Science is all about approximations. The importance of approximation is perhaps most clear in the discipline of physics, which deals with simpler systems than does chemistry or biology. In any case, physics is my discipline so I will focus mainly on approximation in physics. Certainly it is in physics that it is easiest to quantify our approximations, and this may make the role of approximation stand out more clearly in physics than it does in other sciences. Nevertheless, approximation is an important, indeed a fundamental, part of any science.

Let's start by distinguishing two ways that approximation shows up in science (for now I'll focus on physics). One way to make use of approximation is within a model. When I use the word model I mean something a bit broader than what is meant when we talk about "the Bohr model of the atom." I would like to use the term "model" in something like the way that it is used in "the Standard Model of Particle Physics", although without any assumption that the model represents anything fundamental. (For that matter, I have doubts that the Standard Model represents anything fundamental, but that's another story - sort of.) I can make this clearer by describing a specific example. Let's take a model of the solar system. We might posit that each object (planet, asteroid, Sun, etc.) can be represented by a mathematical point in a three-dimensional (Euclidean) space. Each object is also assigned a mass. We then state that these point masses move in such a way that they obey Newton's three Laws of Motion combined with Newton's Universal Law of Gravitation. Now if we specify the initial conditions for each point mass (position and velocity) as some time t=0, then we can determine the state of our model at any future time. In essence, by "model" I mean a description of a system that includes a list of the basic entities of which the system is composed along with the relevant properties of those entities, as well as any rules or laws that dictate the behavior of those entities. I'll leave it open whether or not the initial conditions constitute part of the model.

Now when I talk about using approximations within a model I mean finding the approximate behavior of the entities in the model, rather than the exact behavior according to the rules inherent in the model. For example, in our solar system model we could decide to ignore the gravitational effects of small bodies like asteroids and instead focus only on the gravitational pull of the planets (and perhaps a few larger moons). Note that this approximation can actually take two forms. One way to approach this approximation is to cut the small bodies out of the model entirely. In other words, let's just pretend for the moment that there are no asteroids or small moons in the solar system. This gives us a new, simpler model in which the list of basic entities is different from that of our original model. An entirely different approach to this approximation would be to keep the asteroids and small moons, but ignore the gravitational pull of these objects on the planets, etc. (but not the pull of the planets on the asteroids and small moons). This gives us a new model that has the same list of basic entities, but which follows a different set of laws. In particular, violations of Newton's Third Law of Motion (that objects exert equal magnitude forces on each other in opposite directions) and Newton's Universal Law of Gravitation (that all massive bodies exert gravitational forces on all other massive bodies) abound in this model. There is a sense in which this version of our approximation actually leads to a much more complicated model (sometimes the Third Law is satisfied, sometimes not), but in practice it turns out to be easier to make quantitative predictions in this model than in the original one.

Note that which of these two approaches you take will depend heavily on what you wish to get from your model. For example, if you are trying to predict the motion of Mercury either version of this approximation might do the job nicely but the first version will probably be easier to use. On the other hand, if you are trying to predict possible asteroid impacts on Earth then clearly the first version of the approximation will not do the trick (I can tell you what THAT version will predict right now!). This raises a critical point about how approximations are used in science. The validity of an approximation cannot generally be evaluated on its own. Rather, it can only be evaluated in light of the goals of the scientist. For some purposes the first version of our approximation might be perfectly valid, but for other purposes it will be completely useless. This point may not seem all that striking when we are discussing approximation within a model, but it will also be important for our discussion of the second way that approximation is used in science.

The second way that approximation is used is that our model itself is an approximation of a real physical system (or at least a possible physical system - as a computational physicist I often employ models that likely don't correspond to anything that currently exists in the real world, but give the atom optics people enough time and they'll probably create one). Our solar system model is presumably meant to be a model of the actual planets and other bodies that orbit our Sun. But even the original version of our model was very much an approximation. To begin with, we ignore every property of the objects in the solar system other than their position (and associated time derivatives) and mass. We ignore their chemical composition, their temperature, their albedo, their rotational angular momentum, and on, and on. Furthermore, we ignore the fact that there is a lot of stuff outside the solar system that could, at least in principle, influence the motion of the objects within the solar system. These approximations amount to making cutoffs in our list of basic entities and cutoffs in our list of the relevant properties of those entities. But that's not where the approximations stop. We also make approximations in regard to the laws or rules of our model. Our solar system model ignores all forces other than gravitation. We also chose to use Newton's Laws of Motion, which we know are only approximately correct. Indeed, we completely ignore quantum effects (perhaps justifiably) as well as relativistic effects (that's harder to justify - after all, we know we won't get Mercury's orbit right if we don't use General Relativity).

Now after thinking hard about all the approximations that are intrinsic to our model of the solar system, we might begin to question whether the model is actually good for anything. It seemed pretty good at first (after all, we were prepared to keep track of a point mass to represent every object in the solar system). But now it seems like a joke. How can we convince ourselves that it is not? In other words, how can we convince ourselves that this model is valid? Well, we saw in that in the case of approximations made within a model the question of validity hinged on our purpose in using the model. The same is true here. Suppose we want to predict what the Moon will look like from Earth on a given night in the future. Well, if all we want to know is the phase of the Moon then our model may do the trick since it can predict (approximately) the location of the Moon relative to Earth and the Sun. If, on the other hand, we want to be able to say something about how bright the Moon will appear then we are lost since that will depend on the nuclear reactions that produce the Sun's luminosity, the albedo of the lunar surface, as well as local atmospheric effects on Earth. None of that is in our model, so we have no hope. So in some cases we can show that the model is invalid for a particular purpose without even making a prediction. For example, if we want to predict properties of objects that are not included in the model (either the properties or the objects or both) then the model will not be valid for that purpose. But if we cannot invalidate the model that way, the best way to test it is to make predictions with the model and see how they stand up against the actual behavior of the physical system we are trying to model. If we wanted to predict Earth's orbit around the Sun for the next one hundred years we would probably find that our original solar system model would do a bang-up job.

There may be other ways to validate our approximations, particularly if they can be quantified. For example, we can justify ignoring quantum effects in our solar system model because they simply won't show any noticeable effect at the scale we are examining. We can justify ignoring the gravitational forces exerted on the planets by stars other than the Sun because those forces are negligibly small. Again, though, whether or not these approximations are acceptable will depend on our purpose for using the model (just how precisely do you want to predict Earth's orbit?).

Now we're getting close to the main point I want to make. I hope it is clear that approximations pervade everything we do in physics. Approximations are such a fundamental part of doing physics that physicists tend to forget they are there. But all of physics is an approximation. It is simply not possible to do any physics without making some approximations. We must truncate the list of basic entities in our model (otherwise we would have to include everything in the Universe - and I don't just mean the visible Universe). We must truncate the list of properties that the basic entities possess (otherwise we must consider all possible properties - and who can say what unknown properties might be possessed by some object in the Universe?). Ideally we will make use of our best physical laws, but even these are almost certainly approximations.

I probably wouldn't get much argument from other physicists about what I've said so far, but now I'd like to claim something more controversial. I am convinced that understanding the role of approximation in physics makes it impossible to believe in a "final theory" (or at least impossible to believe that we will ever find the final theory). If we are willing to acknowledge that everything we now call physics is, at some level, an approximation then we must accept that any new theories must potentially be approximate as well. How would we be able to determine that a new theory was not an approximation, that it was in fact the "final" theory? Presumably we would use the theory (or model) to make predictions and then see if those predictions match our observations or experimental results (and I'll pretend for the moment that we can do this in some obvious way and actually know whether or not the predictions match the observations - reality is much trickier than this). But even if the match was perfect that would only validate the theory for that prediction (or at best for some class of predictions). We can only test the validity of an approximation in the context of some particular purpose. To show that a theory is universally valid (i.e that it is a final theory) we would have to show that it is valid for all possible purposes. I simply don't think that it is possible to do this. I'm really not even sure what it would mean to make the claim that a theory is valid for all possible purposes.

So I don't believe in a final theory. I believe that all of physics as it currently exists is an approximation, although an astoundingly good approximation for most of the purposes for which we have used it. I believe that all future physics will still be an approximation, although it will likely be a better approximation for some of our old purposes and a valid approximation for some purposes of which we have yet to conceive. But physics will always have a limited scope (I'll save a detailed discussion of the idea of scope for a later essay - or just read Thomas Brody). The only argument I can see against this point of view is that if we find a theory that works well for all purposes that we can think of now, then it will probably work well for all purposes we devise in the future. But evaluating a theory based on its "logical probability" does not work well (I'll try to write about this later, but Karl Popper has already made the point pretty well). I am convinced that any "Dreams of a Final Theory" will remain just that (with or without the Superconducting Supercollider).

P.S. Yes, I've read the book by Stephen Weinberg whose title I quote above. No, I am not trying to criticize that book or Weinberg himself. In fact, I had two semesters of quantum field theory from Weinberg when I was a grad student. The man clearly knows a lot more about physics than I do, and he has thought a lot more about philosophy than the vast majority of physicists. Even if, as a pond minnow, I wished to pick a fight with one of the great Leviathans of the sea, I would not choose to pick a fight with Weinberg!