Confessions of a Complexity Skeptic

I’ve uploaded a forthcoming book chapter to the PhilSci archive. In “Confessions of a Complexity Skeptic“, I discuss some of the methodological difficulties that must be overcome by those who argue that “complexity thinking” of some sort will become, or should become, important in science (see Sandra Mitchell for a philosophical and Melanie Mitchell for a scientific take on the issue).

The paper is not a standalone piece but a commentary on another paper which will appear in the same volume (written by Prof. Max Urchs). Nevertheless, the commentary can probably be read on its own, and I think that the difficulties I discuss have some claim to generality.

My main points are these:

  1. Whenever we claim that the explanation of a phenomenon requires complexity thinking, we must make sure – by looking very closely at actual science – that more traditional explanations cannot handle the phenomenon. Since one of Urchs’s examples is the ineffectiveness of monetary policy during the financial crisis, I show (at only slightly tedious length) that this phenomenon can at least potentially be explained by a standard Keynesian analysis.
  2. When we claim that some area of science will profit from complexity thinking, it is not enough to point to an area where we currently have major gaps in our understanding, such as neuroscience. Our lack of understanding may be due to the fact that we are not sufficiently mindful of complexity. But it is also possible that we lack the appropriate mathematical methods, or that we have not yet grasped the salient aggregate-level causal factors in the system. The argument for complexity thinking requires us to show that actual problems have been solved by the approach. A promissory note is not enough.

That being said, I will follow the continuation of this debate – which, on the whole, is a bit removed from my area of research – with great interest.

Hedgehogs and foxes in scientific epistemology

My paper titled “Modeling Causal Structures: Volterra’s struggle and Darwin’s success” recently appeared in the European Journal for Philosophy of Science. The paper was co-authored with Tim Räz. (A draft version is available on the PhilSci archive.)

In the past, philosophical analyses of how the sciences gain theoretical knowledge have tended toward the monistic. This is most easily visible in authors like Hempel or Popper, who suggested that the entire methodological diversity of science ultimately reduces to just one principle (hypothetico-deductivism in the case of Hempel and falsificationism in the case of Popper).1 On the spectrum laid out by the ancient Greek fragment which says that “the fox knows many things, but the hedgehog knows one big thing”, most philosophers of science have lived on the hedgehogs’ side. This is true even for more recent and on the whole more pluralistic authors such as Peter Lipton, who offered inference to the best explanation as at least potentially an explication of all inductive practices in science.2 And if my impression is correct, then modern Bayesians are among the most committed hedgehogs of them all.

In a stimulating 2007 paper in the British Journal for Philosophy of Science, titled “Who is a Modeler?“, Michael Weisberg asks us to adopt a more fox-like stance. Perhaps the reason why philosophers of science have been unsuccessful in offering a monistic analysis of scientific epistemology is that we must distinguishing between several different inductive practices. Perhaps we can say something philosophically and historically insightful about each of them separately.

As a starting point, Weisberg suggests “modeling” and “abstract direct representation” (or ADR) as two different ways of developing scientific theories. His basic idea is that a modeler investigates the world indirectly by constructing a model, exploring its properties, and checking how they relate to the real-world target system. Weisberg’s main example of this is a famous instance of model-based science: The Lotka-Volterra predator-prey model. In what Weisberg calls ADR, by contrast, scientists engage the world directly, without the intermediation of a model. He thinks that Mendeleev’s periodic table of the elements is of this type. Mendeleev did not start out with a constructed model: He simply arranged the elements according to various properties. He thereby gained theoretical knowledge about them, but without using a model. Weisberg concludes his paper by asking why scientists would choose modeling over ADR or other strategies (or more succinctly, having asked “who is a modeler?”, he concludes by asking “why be a modeler?”).

In our paper, we follow Weisberg’s pluralistic approach to scientific epistemology, but we find his distinction between practices unsatisfactory, and so we suggest a different one. Moreover, we give an answer to the question of why scientists choose the strategy of modeling.

A main problem of Weisberg’s paper is that the concept of ADR remains ill-defined. Perhaps it is a useful category for describing some scientific work, but the case remains to be made. We suggest that the more natural counterpart of modeling is causal inference. We argue for this by looking closely at the original publications relating to Weisberg’s main example: the predator-prey model. In particular, we look at a previously unexamined methodological preface to the Italian mathematician Vito Volterra’s Les associations biologiques au point de vue mathématique, published in French in 1935.3 We find that Volterra’s preferred method for investigating the factors determining population sizes and fluctuations would have been the laboratory physiologist’s causal inference: vary one thing at a time and see what changes with it. But as Volterra explained at some length, various factors make causal inference in natural populations difficult: The populations are too large, the time intervals too long, the environmental conditions too changeable for the method to succeed. We summarize this as insufficient epistemic access for applying methods of causal inference. Volterra stated quite explicitly that this insufficient epistemic access is the reason why he chose the modeling strategy. Thus, the distinction between causal inference and modeling offers a possible answer to the question of why scientists model: They do so if causal inference is not possible.4

Our distinction also permits us to reevaluate Weisberg’s second example of “abstract direct representation”, which is Darwin’s explanation of the origin and distribution of coral atolls in the Pacific ocean. We argue that this, too, should be understood as an instance of modeling. We also use the example of Darwin’s corals to discuss how causal models can be empirically tested if straightforward causal inferences are not possible.

If you’re interested in the details, please go and read the paper. I will argue on another occasion that the distinction between modeling and causal inference can do a good bit of philosophical work. For example, the debate about scientific realism should probably pay more attention to the distinction, since arguments for inductive skepticism with regard to model-based science may not go through with regard to causal-inference-based science (I’ve started to develop the idea in this talk).

Since this is an ongoing project, I will attempt some crowdsourcing. Our thesis about the motivation for modeling – insufficient epistemic access for causal inference – would be challenged by episodes from the history of the sciences where causal inference is possible and modeling is nevertheless chosen as a strategy. If you can think of such episodes, please send them my way.


  1. Hempel’s views are accessibly summarized in his Philosophy of Natural Science, originally published in 1966 and still available. The best primary source for Popper’s views remains his Logic of Scientific Discovery, either the German edition of Logik der Forschung published by Mohr Siebeck or the English translation published by Routledge. Popper’s Conjectures and Refutations (also by Routledge) is another good point of entry. For a textbook-type introduction, I recommend chapters 2–4 in Peter Godfrey-Smiths’s Theory and Reality (2003 by The University of Chicago Press).
  2. Lipton’s Inference to the Best Explanation (1993/2004, Routledge) is a challenging but rewarding read.
  3. Philosophers of science have not yet paid much attention to Volterra’s explicit methodological discussion. This is probably explained by the fact that the relevant publications were written in French. This was after Volterra left Rome for Paris because of Mussolini’s rise to power.
  4. For an episode where causal inference dominates, see my Semmelweis paper.

 

My review of “Philosophy of Biology: An Anthology”

My review of Philosophy of Biology: An Anthology (edited by Alex Rosenberg and Robert Arp) has appeared online at the journal Acta Biotheoretica.

In brief: A nice volume that will be useful to many people, but it has one substantive and one formal failing. The substantive failing is that there is no sign in the volume of the more recent directions in philosophy of biology (mechanisms, experimental biology, and so on). The formal failing is that some papers are not reproduced faithfully. For example, the classic “Spandrels of San Marco” paper by Gould and Lewontin is reproduced without photographs, and so readers never get to see any spandrels (or “pendentives”, which I read is the correct term for three-dimensional spandrels). For a paper that relies so heavily on its central architectural metaphor, that’s a problem – especially since the full paper is freely available online.

Nevertheless, this is a useful volume, and reviewing it has given me an opportunity to think in earnest about the function of anthologies in academic disciplines.

My Semmelweis paper has appeared in SHPS

My paper on Semmelweis’s discovery of the cause of childbed fever has appeared in Studies in History and Philosophy of Science.

Semmelweis’s discovery has been used by philosophers of science for many decades as a a case study of scientific method. For example, Carl Hempel used Semmelweis as a “simple illustration” of the hypothetico-deductive method in his Philosophy of Natural Science (1966, p. 3). Peter Lipton used it as an extended case study of Inference to the Best Explanation in his book of the same name (1991). Donald Gillies has argued that the episode needs a Kuhnian (in addition to the Hempelian) reconstruction if we are to make sense of it. And this philosophical work on Semmelweis is merely in addition to the work  of medical historians, who have long been interested in Semmelweis as a pioneer in the modern study of infectious diseases.

So what more is there to say about Semmelweis’s work? I show in the paper that the philosophical debate has neglected much material that is relevant to Semmelweis’s methods – and if we take this material into consideration, then a reconstruction of his methodology in terms of causal inference and mechanisms suggests itself very strongly.

The argument is partly historical. I show that the passages of Semmelweis’s Etiology of Childbed Fever (published in 1861) which relate to causal inference and mechanisms were omitted from the most widely available English-language edition of the book (K. Codell Carter’s otherwise excellent translation from 1983). This concerns mainly Semmelweis’s numerical tables and the description of his animal experiments.

However, the argument has a philosophical component. In the past decade, causal philosophies of science (for example of the mechanistic or interventionist type) have become prominent. One of the promises of these approaches is an accurate description of much work in biology and the biomedical sciences – but it is up to careful historical scholarship to find out how widely and how straightforwardly these new approaches can be used to make sense of actual science. In this context I find it very promising that one of the classical case studies of confirmation follows, on close inspection, such a clear causal and mechanistic logic.

On a meta-level, my paper raises a question which I think should receive more attention from the HPS community: On what grounds do we prefer one philosophical account of the case to another? After all, it would be a mere finger exercise for a philosopher to take my new historical material and incorporate it into an account of Semmelweis’s work in terms of hypothetico-deductivism, inference to the best explanation or what have you. So while it is clear that philosophers have not taken sufficient account of the historical material, historical scholarship on its own also cannot take us all the way to an understanding of the episode.