Attention conservation notice: A rant, running to over 6000 words, about the horrors of physicists trying to do economics, by someone who used to be more sympathetic, but has since left physics, and has no credentials in economics. Some may detect an unpleasant sour, musty odor, not entirely due to my having begun writing in June 2006. Includes lots of amateur sociology of science, unsupported by evidence, or, again, any credentials on my part. Even if you care about these fields, wouldn't you rather read science than science criticism?
The occasion for the present rant was being asked by a number of people what I thought about a news piece by Philip Ball, in Nature, on the state of what's come to be called "econophysics". (It lurks behind a pay-wall, without free access, alas.) This in turn was prompted by a paper in Physica A, which sometimes seems like the house organ of the movement, titled "Worrying Trends in Econophysics", by the economists Mauro Gallegati, Steve Keen, Thomas Lux and Paul Ormerod. (Unfortunately, it's not at arxiv.org, but Keen provides a copy, which is more up to date than others on the web.) What follows is some discussion of the paper, shading into the wider theme given by my title.
Back in May of 2005, when there was some dispute at Crooked Timber about whether physicists had contributed anything worthwhile to the study of networks, Henry Farrell asked me to comment. Not being one to miss a chance to procrastinate by pontificating, I did so. Afterwards, my physicist friends told me they appreciated my defense of the honor of statistical mechanics, while my social-scientist friends told me they were glad to see physicists put in their place. Somehow, I doubt that this post will pull off the same trick of serving both duck and rabbit in a single dish.
Ball's piece has a lot of "he said, she said" — or rather, the mathematical sciences being what they are, "he said, he said". (It's also a touch misleading about background issues, though not in very consequential ways [1].) Basically, it reports that some of the economists who had been OK with econophysics are saying "enough, already!", and some of the econophysicists are wringing their hands, while others are charging ahead unperturbed.
The charges made in the "Worrying Trends" paper are reasonably summarized in the abstract:
Econophysics has already made a number of important empirical contributions to our understanding of the social and economic world. These fall mainly into the areas of finance and industrial economics, where in each case there is a large amount of reasonably well-defined data.More recently, econophysics has also begun to tackle other areas of economics where data is much more sparse and much less reliable. In addition, econophysicists have attempt to apply the theoretical approach of statistical physics to try to understand empirical findings.
Our concerns are fourfold. First, a lack of awareness of work that has been done within economics itself. Second, resistance to more rigorous and robust statistical methodology. Third, the belief that universal empirical regularities can be found in many areas of economic activity. Fourth, the theoretical models which are being used to explain empirical phenomena.
The latter point is of particular concern. Essentially, the models are based upon models of statistical physics in which energy is conserved in exchange processes. There are examples in economics where the principle of conservation may be a reasonable approximation to reality, such as primitive hunter-gatherer societies. But in the industrialized capitalist economies, income is most definitely not conserved. The process of production and not exchange is responsible for this. Models which focus purely on exchange and not on production cannot by definition offer a realistic description of the generation of income in the capitalist, industrialized economies.
Before we gone on, it's worth noting that the authors of the "Worrying Trends" paper are, in fact, coming from positions which make them about as predisposed to favor econophysics as possible. While they are economists, none of them, so far as I can tell, has much time for orthodox, neo-classical economics. (Ormerod, for instance, has written at least one popular book about how it's junk, and Keen's personal website is debunkingeconomics.com.) In fact, they have been, as it were, fellow travelers, publishing in Physica A, etc. (E.g., Ormerod, whose work I happen to know better than the others, has several papers arguing that the distribution of the duration of recessions follows a power-law, and that this reflects a kind of critical cascade of failures among firms. Paul Krugman made a similar suggestion in his book The Self-Organizing Economy, but doesn't seem to have followed it up.) So, the people lodging these complaints are not just very familiar with econophysics, they have public commitments which should, if anything, bias them in its favor.
All of their charges seem fair to me; I would only say that they do not go far enough. Some of these remarks from the abstract are amplified in the body of the paper. E.g., the first sentence of the paper proper repeats the first sentence of the abstract, but the second sentence adds "Many of these were anticipated in two truly remarkable papers written in 1955 by Simon and in 1963 by Mandelbrot, the latter in a leading economic journal." Nonetheless, they do give a fair-minded summary of what econophysics has actually positively achieved, so I'll quote that, too (omitting references).
The evidence for the fat-tailed distribution of asset prices changes noted [by Mandelbrot] has now been established beyond doubt as a truly universal feature of financial markets. A genuinely original and very important contribution of econophysics, using the technique of random matrix theory, has been the discovery that the empirical correlation matrix of price changes of different assets or classes of assets is very poorly determined. [This finding] undermines Markowitz portfolio theory and the capital asset pricing model, still regarded as powerful and valid theories by many economists. There have been very few extensions of the random matrix approach outside financial markets, though there are many potential applications....(For reasons to be skeptical of the extinctions stuff, however, see Newman and Palmer.)Another active area of empirical investigation for econophysics has been industrial structure and its evolution. As with financial markets, large amounts of generally reliable data are available in this area, too. It should be said that some of the econophysics literature is perhaps less original and/or well established than physicists might appreciate. Decisive evidence on the right-skew distribution of firm sizes, for example, has been both available and well known in industrial economics for many years. Plausible candidates in the economics literature to represent the empirical size distribution are the lognormal, the Pareto and the Yule. The main problem is in capturing the coverage of small firms. Recent attempts to do this ... lend support to a power-law distribution... However, this may well be an as yet unexplained outcome of aggregation... A more decisive finding by econophysicists is that the variance of firm growth rates falls as firm size increase, although this too was anticipated in the early 1960s. A further discovery is that the size-frequency relationship, which describes the pattern of firm extinctions, appears to be very similar to that which describes biological extinctions in the fossil record.
From here on, the "Worrying Trends" authors imply, it's all down hill, and I have to agree. When you are dealing with a very, very large amount of very high quality data, you can get away with using sloppy, not-too-reliably means of analysis, because your data will save you unless your analytical procedures are actively malicious. (That goes double if the data are generated by active processes over which you have considerable control, as in real physics experiments.) It also helps if you are merely trying to describe patterns in the data, without framing serious hypotheses about the mechanisms which produce them. Note, also, that none of the genuine accomplishments really draw on any of the distinctive concepts or mathematical structures of theoretical physics, as opposed to the more elementary reaches of probability and stochastic processes. In other words, these are things economists could have done themselves, if they'd read better books on random processes (e.g.) early in their training.
If econophysicists were content to stick to this sort of thing, to the phenomenology of financial time series (etc.), the situation would be almost OK. Almost, because even there it is far too common to see (for example) claims that such-and-such a distribution is a power law, because there's a straightish bit on a log-log plot. I have discussed that particular fallacy ad nauseam elsewhere, and will just note in passing that even here, the refusal to do statistics dooms people to talk nonsense. The real point is that econophysicists are not content with phenomenology based on overwhelmingly large data sets, but want to get at mechanisms, in all kinds of social and economic systems, and there things get really ugly. There is a large literature in econophysics, for instance, on agent-based models of financial markets and (supposedly) other forms of collective behavior, including the formation of public opinion, but not even the authors of "Worrying Trends", who are about maximally sympathetic to the movement, list it as a success. (I will return to the minority game and why I'm so down on it below.) This is a shame, because it's actually in the area of mechanistic models that one might imagine (as I have) that physicists could make a distinctive contribution.
So then: why oh why don't we have better econophysics?
The first reason which occurs to me, now that I'm a dues-paying, card-carrying statistician, is that almost all econophysicists are theoretical physicists, and moreover statistical physicists. (I'm one myself, or at least was through my Ph.D.) Modern physics began, in the 17th century, by fusing mathematical theorizing and artisanal craft, but one result of our progress has been to impose a specialized division of labor, sharply separating theory and experiment; Fermi was probably the last physicist to be both a great theorist and a great experimenter. (Perhaps this is connected to his invention of Monte Carlo?) This means that it is very rare for a theoretical physicist to analyze actual empirical data (say, measurements of magnetic susceptibility), which is what the experimentalists do. Theorists instead deal with experimental results (say, that the susceptibility depends on temperature in such-and-such a way). In high energy physics, theorists are actually so remote from contact with experimentalists that a separate guild of interface specialists ("phenomenologists") has arisen to mediate between them. As a natural consequence of this division of labor, theorists receive no instruction at all in data analysis, let alone statistical inference.
Statistical physicists haven't gone to the same extreme of separation from experiment as particle physics, but in some ways its theorists are especially badly prepared to analyze empirical data. Despite the name, statistical physicists do not learn any statistics. The founders of statistical mechanics, namely Maxwell and Boltzmann, were influenced by then-contemporary ideas on social statistics, as found in e.g. Quetelet and Buckle, but that was long ago, and the lesson was that small-scale random processes can produce stable, nearly-deterministic patterns at the large scale, which we would now say is probability theory, not statistics. (Not that we do such a good job of teaching or learning probability theory, either.) However, more perhaps than other parts of theoretical physics, statistical mechanics relies heavily on simulations. Interpreting Monte Carlo results is like interpreting empirical data, but with the crucial difference that the volume and quality of the pseudo-data is limited only by your patience. If your results are unsatisfactory, you are almost always better off either refining your simulation, or just running it longer, than you are improving your analytical procedures. Real data is not like this.
(I doubt it helps matters that many statistical physicists are in the grip of sub-Bayesian ideas about maximum entropy, but I can't, honestly, say that this has played a direct role in the development of econophysics. It has, however, contributed to susceptibility to some dubious ideas, like Tsallis statistics, but that is really another story for another time.)
Worse, over the last half century or so, the statistical mechanics community has devoted much of its research energy, and its pedagogy, to the theory of phase transitions, such as those between solids and liquids, or liquids and liquid crystals, or between magnetic and non-magnetic materials. (Onsager, incidentally, contributed fundamentally to the theory of phase transitions for both liquid crystals and ferromagnets.) I don't mean that this is bad for statistical mechanics, because phase transitions are important and the theory developed around them is one of the jewels of the field. But phase transitions have the weird property of "universality". In the vicinity of the critical point, the behavior of the system comes to depend only on a few key parameters, so that any two systems in the same "universality class" are quantitatively similar near the transition, even if they are otherwise as different as chalk and cheese. If what you are interested in is this behavior near the critical point, then, you can get away with analyzing or simulating ridiculously over-simplified models, if only you get their universality class right. The implicit lesson is that details don't matter, and results on toy models should generalize directly to real systems. (Of course, details can matter a lot, even with toy models.) I can't make myself believe it's coincidence that so many of the people active in econophysics come from a background in the theory of critical phenomena.
What statistical mechanics does give its students is a way to approach the "many-body problem", a set of techniques for deducing the macroscopic patterns which are produced by the interactions of large numbers of material bodies. These techniques do not try to exactly find the consequences of all the interactions and feedbacks, but rather make some probabilistic assumptions and then work out the typical consequences at the macroscopic level. Thanks to the laws of large numbers, the odds are overwhelmingly good that the actual behavior of the system will be incredibly close to this typical result, at least, as we say "in the thermodynamic limit" where the number of bodies goes to infinity (but the density stays finite). On a smaller scale, these techniques let us calculate fluctuations around the typical values; one of the things that makes phase transitions interesting is that there the fluctuations dominate. (The probabilistic basis of fluctuation theory is not the law of large numbers, but rather the large deviations principle.) Let me emphasize, as a once and future statistical physicist, that this is a really exceptionally powerful and beautiful body of theory, which is capable of explaining everything from why sugar cubes dissolve in coffee and the machinery of cells to the evolution of the stars, and the heart of it, again, is solving many-body problems, which means calculating the macroscopic consequences of microscopic interactions.
If econophysics is dignified enough to have a tragic flaw, it is this. I have lost count of the number of times I have heard other statistical physicists insist, or explain, or just assume, that ecology, or evolution, or neuroscience, or, social networks, or, yes, economics, "is, after all, just another many-body problem", so of course it must yield to the insights of statistical mechanics. This is why our conquistador spirit leads us to make assaults on these disciplines, and not, say, classical philology. I don't even think that this is wrong. I think the problem is that we have a drastically impoverished notion of bodies, and how they might interact.
Let me illustrate this by talking about the minority game, which I mentioned a while ago. This is a simplification of a problem originally posed by the economist Brian Arthur, called the El Farol Bar Problem, which goes (in my own phrasing) as follows:
There are 100 people who like to go out in Santa Fe, and there is only one bar worth going out to, namely El Farol. Sadly, if more than 40 people show up on any given night, it gets too crowded and fight breaks out, and everyone who went would have been happier staying home and looking up at the stars. How do you decide, on any given night, whether or not you should go, without knowing who has already decided to go?Two econophysicists --- Challet and Zhang --- simplified this into the minority game. There are still only two choices in each round of the game, imaginatively called "0" and "1"; whoever picks with the minority gets rewarded, while the majority gets nothing. The utility-maximizing outcome would be to have fifty-percent-less-one in the minority in each turn, so the collective efficiency can be measured by how far the group departs from this. Arthur's original paper on the El Farol problem included a rather complicated model of inductive learning. Challet and Zhang instead assumed that each agent remembers which action won on the last m rounds, and feeds this sequence of 0s and 1s into a look-up table, which in turn tells it whether to chose 0 or 1. Their original paper had a complicated evolutionary scheme for updating these look-up tables or strategies, but almost all subsequent work on the minority game has just said that agents have k different look-up tables, keep track of which one would have done the best, and use that one.
The literature on this little model is immense. Considerable effort and ingenuity have been put into deriving all manner of supposedly "universal" results, about the length of memory (m) which maximizes global efficiency, for example, the formation of "crowds and anti-crowds", etc., etc. Some of this work is actually quite clever, and worthy of approbation. Much less worthy are the claims that these findings apply to financial markets, congestion problems, and even a general theory of what all systems of multiple adaptive agents must be like. (The latter claim actually exists in several different versions, at least one of which is simply a rediscovery of the first elements of large deviations theory.) Much of the appeal of the model has rested on the particular form of the decision rule, which is comparatively easy to analyze if you know a lot about disordered spin systems, one of the core topics of modern statistical mechanics.
What appears to have entirely escaped the notice of everyone working on the minority game is that way people make choices and predictions in competitive situations has been extensively studied in experimental psychology and experimental economics (which has existed for some time now). The results look nothing at all like their chose-a-look-up-table models. If there was some kind of result saying that any plausible model of human choice was in the same universality class as these models, and we only cared about scaling relations near the critical point, this wouldn't matter, but of course no one has any such theorem, nor do we only care about critical scaling. No one has even looked into whether these sorts of look-up tables produce behavior which is even remotely similar to more realistic models. There is exactly no reason to believe that they do — if anything there's evidence that they don't — and every reason to suspect that this whole sub-sub-field is at best a mathematical curiosity. The closest thing we have to a study of the statistical mechanics of even vaguely-realistic adaptive agents is, in fact, the work of economists. So the fact that something is, or can be treated as, a many-body system doesn't mean that the bodies are of the kind we know from our elementary textbooks.
At this point, if I have any readers left (which I admit is unlikely), the economists among them will be nodding complacently, especially the smug neo-classical ones. (To be clear, it is the smugness which causes complacency, not neo-classicism.) "After all", they are saying to themselves, "we've been building a science of 'micromotives and macrobehavior' ever since 1776. How arrogant of these physicists to ignore our works, and how unsurprising that their own have come to nothing." (The math of neo-classical economics is different from that of statistical mechanics, but it's not harder. If you can learn how to do renormalization group calculations, you can learn the Arrow-Debreu model, or game theory.) The arrogant, cultivated ignorance of physicists is indeed reprehensible, but I don't want to give the economists a pass.
To begin with, mainstream economics is clearly false. I don't say this just because perfectly competitive markets aren't the only economic institution in this world; the neo-classical framework now includes very sophisticated theories of imperfect competition, imperfect information and non-market institutions, and these developments are mainstream enough to result in Nobel Prizes (in, e.g., 1993, 1994 and 2001). The foundation on which the neo-classical framework is raised, though, is an idea about rational agents: rationality means maximizing expected utility, where expectations come from maintaining a coherent subjective probability distribution, updated through Bayes's rule; moreover, the utility function is strictly self-regarding. This is a very well-specified idea, readily formalized in clean and elegant mathematics. Moreover, there's pretty much only one way to formalize it, which makes the mathematical modeler's life much easier. All of this appeals to certain temperaments, mine very much included. Alas, experimental psychology, and still more experimental economics, amply demonstrate that empirically it's just wrong. We are boundedly rational, and, for good or for ill, we give a damn about others. Moreover, there are very general reasons, having to do with the computational intractability of optimization problems, and the severe limitations of computationally feasible Bayesian learners, to think that no creature could ever be a "rational agent" in the neo-classical sense. Bounded rationality is the only kind we encounter, and the only kind we are going to encounter. (Yes, yes, there are selectionist arguments a la Friedman or Alchian: they fail. But this post is supposed to say mean things about physicists, not the Chicago School, so another time. Also, I'd say it's an abuse of the language to describe our deviations from the impossible neo-classical ideal as "failures of rationality", but, again, another time.) But, as I said, all the rest of the neo-classical framework rests on this conception of individual decision-making; remove it and all the models are standing on air. So: neo-classical economics is false.
Why then is it not totally crazy to pursue mainstream economics, and why do I fault physicists for not bothering to learn it? Well, classical physics is false, too: the combination of Newton's laws of motion with Maxwell's equations for electromagnetism straightforwardly predicts that ordinary atomic matter, composed as it is of moving charged particles, should be unstable. The theory predicts that every material body should rapidly collapse in an ultraviolet flash; manifestly, the theory is false. [2] Nonetheless, physicists know very well that classical physics is an extremely good theory in the right limits, and that a lot of the situations of practical or intellectual interest in the world are in those limits.
In a similar way, I think, the neo-classical ideal is a tolerable approximation in certain limits. Since I am writing a blog post, and not a treatise on economic methodology, I will be vague about specifying those limits, but one aspect ought to be low computational complexity, relative to the cognitive capacity of the decision-maker. (It's no accident that Herbert Simon combined general arguments about bounded rationality with both experimental studies of choice and expertise and computational models of cognition.) A lot of the organization of society, especially modern society, can be usefully seen as ways of drastically simplifying and restricting decision problems, so that bounded human rationality can cope with them. (This, at least as I understand it, is a big part of Hayek's argument in "Economics and Knowledge" and "The Use of Knowledge in Society".) Homo economicus would would also easily solve these problems, so neo-classical models don't do a bad job, provided we also don't have to worry about other aspects of human motivation. (All over the world, neo-classical predictions fail in the ultimatum game not because the game is hard but because people care about fairness.) It's possible, I think, to get a glimpse of what a real economics, going beyond neo-classicism in both its assumptions about individuals and about institutions, would look like; to get that glimpse, one reads Sam Bowles's Microeconomics.
So much for all of the ways in which there isn't enough "econo-" in econophysics. Let me also complain that there isn't enough physics: the repertoire of ideas taken from physics is very impoverished. Basically, we see random walks, power laws, and spin systems over and over again. These are important ideas, but they're just a small part of theoretical physics! To give an example, Eric Smith and Duncan Foley have a fun paper working through detailed mathematical analogies between the axiomatic versions of utility theory and thermodynamics, leading to a reversible "engine" that runs on credit. (Disclaimer: Eric is a friend.) Or: it's obvious, once pointed out (by K. Ilinski ), that prices and discount rates form a gauge connection, a mathematical object we study to death in field theory. These ideas have met with, so far as I can tell, absolute indifference from econophysicists.
Or again: a large part of modern statistical physics is concerned with pattern formation (in no small measure inspired by Turing, though anticipated by the great, semi-crazy Nicholas Rashevsky [3]). There are now very interesting models of urban morphogenesis, explicitly drawing on this work, and at the same time grounding these large-scale patterns in the market interactions of individual decision-makers. These are not, however, due to econophysicists, but to economists, notably Fujita, Venables, and Krugman. (This is from the forgotten days before Krugman's encounter with the eldritch horror that is the mendacity, malevolence, incompetence and disconnection from reality of the Bush Administration turned him into the Grand Heresiarch of the Ancient and Hermetic Order of the Shrill.) So far as I can tell [June 2006], this work has been cited exactly three times on the arxiv (once by an economist, and once by me).
In fact, the most interesting physics-inspired idea now going in economics is due to a rather orthodox, if imposingly erudite, economist, namely John Sutton. In his work on industrial organization since the mid-1990s, he's actually come up with a genuine innovation in economic methodology, explicitly inspired by an analogy with thermodynamics. Consider, he says, trying to calculate the efficiency of a heat engine. One way would be to set up a very detailed mechanistic model, incorporating condensation, combustion, friction, etc. You'd have a huge number of parameters, but if you could estimate them you could, in principle, solve the model and calculate the efficiency of the engine. The thermodynamic approach is instead to come up with a result which is valid for any heat engine, and depends on only a few (two) parameters — but is only an inequality, an upper bound on the efficiency. This is the lesson Sutton takes from thermodynamics, not a desire to find an enthalpy. In his work on the evolution of industrial structure, accordingly, he avoids the usual econometric path of specifying a detailed model, fitting all the parameters, etc.; instead he finds simple inequalities which must hold across large classes of models, if certain basic assumptions are right, and then show that those inequalities are in fact satisfied. It is, if a non-economist can say so, brilliant stuff. (If you want to know more, at great length, with abundant historical and technological detail, apt yet obscure quotations from R. A. Fisher, etc., read his Technology and Market Structure; if you want to know more, with methodological reflections and amusing anecdotes, read Marshall's Tendencies; and if you just want a review paper, read this.) Naturally, this has made no impact at all on econophysics, though Sutton has published a paper in Physica A, which sometimes gets cited as a reference for Gibrat's Law.
To sum up my rant so far: our current econophysics is not very good. Nonetheless, we could have a better econophysics, if the physicists in question would bother to learn more about the kind of bodies whose macroscopic behavior they are supposed to be modeling. So why don't we have this better econophysics? This is a very hard question, because it's essentially a causal, counter-factual one: what would have to have been different in order to lead to the better econophysics? At best, I can make semi-informed guesses here, and I shouldn't pretend that they're anything more than that, though my tendency to strident over-statement may make it sound like I think I've got the one true explanation.
I have already suggested some aspects of the disciplinary culture of physics, especially theoretical statistical physics, which contributed to the problem. That is, if statistical physicists knew more about statistics, had fewer presumptions about universality, and were willing to learn more from others, they could do better econophysics. This may go some way towards explaining why they do bad econophysics, but I don't think it explains why they do econophysics. Here I'd speculate that there are two forces at work, one pushing physicists to do things which were not-physics-as-we-know-it, the other pulling them towards doing stuff about financial markets.
The first is the "ecological" crisis of physics as an academic discipline: the rate of production of new physics Ph.D.s has for some time greatly exceeded the rate at which professorial jobs for them arise. The classical Malthusian resolutions of such a dilemma are war, disease, emigration, misery and "vice", i.e., birth control. Physicists have not taken to slaughtering each other to secure faculty positions (outside of Dorothy Sucher's very amusing mystery novel, Dead Men Don't Give Seminars), nor are there many illnesses which reduce our numbers. There are deep institutional incentives which keep us from limiting our reproduction, but physicists who go into industry, as opposed to academia, do not train up new physicists in turn, so they are effectively sterile, and one might regard this as the analog of Malthusian vice.
But what about emigration? That would correspond to entering a new field, where there was less competition. But, once you have gotten all the way through a Ph.D. in one field, retraining yourself in another, starting from the basics, is a deep pain on many levels. (Trust me on this one.) Much easier, emotionally and practically, to decide that the skills and ideas you have acquired, at so much cost, are actually just what's needed to make progress in the other field, the one which seems so attractive. In fact, if those ideas are fairly new ones, which seem very powerful and have been received with a lot of excitement in the field, it is very natural to want to push them even further, to see just how far they can go. ("Too much of a good thing is wonderful".) If they seem to succeed in the new area — either because they really work, or because the people applying them don't know enough about the area to recognize failure (as has been suggested) — then the usual processes of social learning will lead to more "emigration" into the new area. Thus, in part, the rise of "complex systems" within statistical physics, and the many conversations I recall with colleagues on the theme that the appropriate domain of physics was whatever could be studied using our methods, not just "matter and motion".
(Incidentally, a very similar story could be told of the rise of "cultural studies" in literature departments: responding to over-crowding in the original problem-area by deciding that existing, but still newish and cool, tools and ideas should be applied over a much broader domain. Network analyses of super-heroes (1, 2) or of EuroVision are, as it were, our equivalent of the proverbial deconstructions of Batman. But one could argue that classical deconstruction itself was much more like string theory.)
So, we have ecological pressures forcing physicists out of physics and into complex systems. Econophysics is a part of this general movement. But why econo-physics? Why not, say, eco-physics, following the pattern set by Bob May in the 1970s (to say nothing of Lotka in the 1920s)? Well, we have some ecophysics too, of course, but on nowhere the same scale as econophysics, despite the great scientific and practical importance of ecological problems. Something seems to make econophysics more attractive.
This could just be chance. Certainly I haven't constructed a good neutral model of the situation, which would have to include herding, and shown that the growth of econophysics has been greater than it predicts, which is what I ought to do before trying to explain a phenomenon which might need no explanation. (At least, that is what I ought to do according to myself.) But, with that caveat noted, let's suppose that there is something to be explained here.
One thing which might make econophysics especially attractive among complex systems fields is that, over the last few decades, we've seen a new sink for industrial employment of physicists, in finance. Following the rise of the Black-Scholes formula for option pricing, which is closely tied mathematically to path integrals of Gaussian processes, there has been a lot of demand for physicists as "quants" or "rocket scientists" in the financial industry. (A truly astonishing, and depressing, fraction of the people I went to graduate school with are now working for banks or investment funds.) This may have made physicists interested in complex systems especially apt to think of applications to finance; if so, it's at least a little ironic, because Black-Scholes is all about neo-classical equilibrium, efficiency, Gaussian distributions, etc.
Personally, and on the basis of no systematic studies whatsoever, I tend to discount this in favor of another, even less edifying factor. I have posted about this before, but it bears explicit repetition. Wolfgang Beirl put it very nicely: "cointegration of multi-agent research networks with financial markets and in particular the Nasdaq stock market bubble".
It will be based on a simple search of the word "market" in abstracts of papers stored at xxx.lanl.gov for the years 1998--2004 with the following results:(Extending the series, I get 105 for 2005 and 124 for 2006.) Less formally, the rise of econophysics coincides with a period when the whole damn culture went ga-ga over the financial markets (or at least the relevant stratum of the culture did). As Robert Shiller can explain to you, this was part of the "naturally-occurring Ponzi process" which gave us the bubble, or more accurately bubbles. Physicists began obsessing over the stock market when everyone began obsessing over the stock market; it's just that their obsession took the form of papers rather than day-trading.
1998 25
1999 49
2000 70
2001 108
2002 94
2003 94
2004 79
I don't know about you but it leaves me somewhat depressed. We don't, yet, have a really good general way, or even a decent one, of understanding how the interactions of lots of adaptive agents produce social phenomena. It would be very nice to understand this, both intellectually and because it might (sometimes, a little bit) help to keep us from making such a mess of things. (Do not take that for a plea for social planning, or rule by an enlightened elite of scientists, or some such bullshit.) Economics seems like a good place to start building such a science, largely for reasons of data and concreteness. Physicists have as much right to contribute to such a project as anyone else, and statistical physics really has discovered a lot of useful things about many-body problems. I would love to see a statistical mechanics of social and economic behavior. Even partial solutions of the social problem would drastically transform and improve our mathematical theory of many-body systems. For all these reasons and more, I would really like there to be a good and successful econophysics. Nonetheless, despite a lot of activity by many smart physicists, there isn't. This seems like a waste, but also not something I can do much about, except to hope piously that the usual self-correcting mechanisms of the scientific community will come into play.
[1]: Bachelier's
random-walk
theory of financial market prices actually predates
Einstein's
work on Brownian motion, which was done independently. Bachelier's work
was rediscovered in the mid-20th century by the economists who elaborated the
efficient market hypothesis, since it predicts just this "random character of
stock market prices". For that matter, Ball runs smack into one of the endemic
confusions in this area, which is over the word "equilibrium". In dynamics,
"equilibrium" just means a steady state, or fixed point, where no variables of
the system are changing. (In statistical mechanics, this sense is
strengthened: only steady states
of minimum
free energy, obeying the
principle of detailed
balance, are true equilibria.) The economic concept is related but more
subtle: an equilibrium is a fixed point of strategies, where no agent
would want to unilaterally change its decision rule. Prices can
certainly fluctuate in economic equilibrium, either in response to new
information and external shocks, or without them, along a path which ensures
that at no point would anyone be better off by changing their actions. (More
exactly, no agent would think they would be better off by deviating.)
One can even
build equilibrium
models of economic growth.
[2]: The stability of matter actually
depends on quantum effects, but remains a very hard problem. There is
a nice account in
Krieger's Constitutions
of Matter, with about as little technical detail as possible (which
is still a lot).
[3]: The story
of Nicholas Rashevsky and his "mathematical biophysics" movement, centered at
the University of Chicago in the 1930s and 1940s, is an important subterranean
theme in the development of artificial intelligence, neural networks, social
networks, quantitative modeling in biology and social science, etc., as well as
being a fore-runner of such later movements as cybernetics, general systems
theory and complex systems. Unfortunately, and curiously, I can't find any
full-length studies of the man or his movement, and he doesn't even have a
Wikipedia entry. Dover Books used to publish a reprint of
his Mathematical Biophysics, but that, too, has been out of print
for a long time now.
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Posted at September 15, 2007 16:40 | permanent link