Models and modelling practices in science were once ignored in philosophy of science; however, in the past fifty years they have been anything but. From Mary Hesse’s pioneering work in the 1960s, to the writing of Ron Giere, Uskali Maki, Nancy Cartwright, Mary Morgan, and Margaret Morrison in the 80s and 90s, to today’s contributions from Michael Weisberg, Mauricio Suarez, Wendy Parker, and too many others to mention, scientific models are now studied left and right. This work is no longer quirky or marginal, and it spans many scientific fields. There are detailed and intricate accounts of what models are, of the variety of different models, and of the epistemic and social roles played by models. But we would like to suggest that in one respect, more should be done.
One of the most useful distinctions to have come out of this work is that between theoretical and phenomenological models, or targeted and targetless models to use the language of Cartwright and Weisberg respectively. For our purposes here, the two distinctions amount to the same thing: phenomenological or targeted models are evaluated on their ability to represent or predict certain features of the phenomenon in question. They are widespread in engineering, applied econometrics, meteorology, and other fields where accurate forecasting matters. Theoretical or targetless models, by contrast, explicitly eschew directly empirical criteria. They are for the most part minimal representations of a single causal factor or mechanism, and their goal is to study the relation between variables in the absence of complications introduced by the real world. Cellular automata models of complexity, Ising models of phase transitions, and rational choice and game theory models in economics and theoretical biology are all examples of targetless modelling. Provocatively, let us call it armchair modelling. It is these models that we need to get tougher on.
By and large, philosophers’ contribution has been to specify the various roles these models play: they isolate causal factors, construct credible worlds, structure research agendas, explore possible explanations, provide understanding, and finally they are playgrounds for creativity. We urge that philosophers should be more than just interpreters of these armchair models; they should also be evaluators of them. But evaluation of what sort?
E. O. Wilson has written:
[In biology] factors in a real-life phenomenon are often misunderstood or never noticed in the first place. The annals of theoretical biology are clogged with mathematical models that either can be safely ignored or, when tested, fail. Possibly no more than 10% have any lasting value. Only those linked solidly to knowledge of real living systems have much chance of being used.
Notice the terms in which he couches his critique: of course, some armchair models have eventually led to genuine explanatory successes while others have gathered dust in the drawers. Wilson is not dismissing the success cases, but he is implying that there are not enough of them.
In our view, this is the key question: has too much been invested in armchair models? Take a particular scientific problem; take a range of methodologies that scientists could be using to make progress on it; take the human, intellectual, and economic resources available to them; and ask ‘what is the rational way of apportioning these resources across the methodologies?’. Just as a community can plan more or less rationally which problems their scientists should tackle—that’s the ideal of a well-ordered science that Philip Kitcher formulates—so can this community make rational decisions about which methodologies to pursue. A methodology has to be an efficient one, given the task and the available resources. Let’s call that ‘efficiency analysis’.
Like E. O. Wilson on biology, we suspect that economics, to take one example, is not practicing well-ordered science. Intricate and sophisticated armchair models are central to the education of students, to publishing in top journals, to getting hired by top departments, and in general are the main currency of prestige in the discipline. This has been true for roughly 50 years. In economics at least, armchair science has had plenty of opportunity to prove itself. Has it? That’s a big empirical question. From a number of case studies by philosophers and historians of economics, including some of our own, our initial verdict is ‘not so much’. Armchair models can do a lot in economics, but not nearly enough to justify the level of investment they receive.
Philosophers of science are particularly well qualified to carry out efficiency analysis because they have the right distance and level of knowledge to question an ‘armchairist’ status quo. But to carry it out properly, we need to move on from our own status quo. Many papers have roughly the following structure: ‘scientists in a discipline X cannot conduct controlled experiments, so they build armchair models. I present a possible justification of this practice’. But there are many other methods available besides building armchair models: process tracing, case studies, observational studies, natural and quasi-experiments, small-N causal inference, and more.
We are all for naturalism and the so-called practice turn in philosophy of science. Engaging with the details of science is crucial. But this should not mean that we just look at what scientists do and then use our ingenuity to rationalize it. Sometimes naturalism calls for being more critical and asking what scientists could be doing instead.