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.