Oct 20 JDN 2458777
The beauty and clearness of the dynamical theory, which asserts heat and light to be modes of motion, is at present obscured by two clouds. The first came into existence with the undulatory theory of light, and was dealt with by Fresnel and Dr. Thomas Young; it involved the question, how could the earth move through an elastic solid, such as essentially is the luminiferous ether? The second is the Maxwell-Boltzmann doctrine regarding the partition of energy.
The above quote is part of a speech where Kelvin basically says that physics is a completed field, with just these two little problems to clear up, “two clouds” in a vast clear horizon. Those “two clouds” Kelvin talked about, regarding the ‘luminiferous ether’ and the ‘partition of energy’? They are, respectively, relativity and quantum mechanics. Almost 120 years later we still haven’t managed to really solve them, at least not in a way that works consistently as part of one broader theory.
But I’ll give Kelvin this: He knew where the problems were. He vastly underestimated how complex and difficult those problems would be, but he knew where they were.
I’m not sure I can say the same about economists. We don’t seem to have even reached the point where we agree where the problems are. Consider another quotation:
For a long while after the explosion of macroeconomics in the 1970s, the field looked like a battlefield. Over time however, largely because facts do not go away, a largely shared vision both of fluctuations and of methodology has emerged. Not everything is fine. Like all revolutions, this one has come with the destruction of some knowledge, and suffers from extremism and herding. None of this deadly however. The state of macro is good.
The timing of Blanchard’s remark is particularly ominous: It is much like the turkey who declares, the day before Thanksgiving, that his life is better than ever.
But the content is also important: Blanchard didn’t say that microeconomics is in good shape (which I think one could make a better case for). He didn’t even say that economics, in general, is in good shape. He specifically said, right before the greatest economic collapse since the Great Depression, that macroeconomics was in good shape. He didn’t merely underestimate the difficulty of the problem; he didn’t even see where the problem was.
If you search the Web, you can find a few lists of unsolved problems in economics. Wikipedia has such a list that I find particularly bad; Mike Moffatt offers a better list that still has significant blind spots.
Wikipedia’s list is full of esoteric problems that require deeply faulty assumptions to even exist, like the ‘American option problem’ which assumes that the Black-Scholes model is even remotely an accurate description of how option prices work, or the ‘tatonnement problem’ which ignores the fact that there may be many equilibria and we might never reach one at all, or the problem they list under ‘revealed preferences’ which doesn’t address any of the fundamental reasons why the entire concept of revealed preferences may fail once we apply a realistic account of cognitive science. (I could go pretty far afield with that last one—and perhaps I will in a later post—but for now, suffice it to say that human beings often freely choose to do things that we later go on to regret.) I think the only one that Wikipedia’s list really gets right is ‘Unified models of human biases’. The ‘home bias in trade’ and ‘Feldstein-Horioka Puzzle’ problems are sort of edging toward genuine problems, but they’re bound up in too many false assumptions to really get at the right question, which is actually something like “How do we deal with nationalism?” Referring to the ‘Feldstein-Horioka Puzzle’ misses the forest for the trees. Likewise, the ‘PPP Puzzle’ and the ‘Exchange rate disconnect puzzle’ (and to some extent the ‘equity premium puzzle’ as well) are really side effects of a much deeper problem, which is that financial markets in general are ludicrously volatile and inefficient and we have no idea why.
And Wikipedia’s list doesn’t have some of the largest, most important problems in economics. Moffatt’s list does better, including good choices like “What Caused the Industrial Revolution?”, “What Is the Proper Size and Scope of Government?”, and “What Truly Caused the Great Depression?”, but it also includes some of the more esoteric problems like the ‘equity premium puzzle’ and the ‘endogeneity of money’. The way he states the problem “What Causes the Variation of Income Among Ethnic Groups?” suggests that he doesn’t quite understand what’s going on there either. More importantly, Moffatt still leaves out very obviously important questions like “How do we achieve economic development in poor countries?” (Or as I sometimes put it, “What did South Korea do from 1950 to 2000, and how can we do it again?”), “How do we fix shortages of housing and other necessities?”, “What is causing the global rise of income and wealth inequality?”, “How altruistic are human beings, to whom, and under what conditions?” and “What makes financial markets so unstable?” Ironically, ‘Unified models of human biases’, the one problem that Wikipedia got right, is missing from Moffatt’s list.
And I’m also humble enough to realize that some of the deepest problems in economics may be ones that we don’t even quite know how to formulate yet. We like to pretend that economics is a mature science, almost on the coattails of physics; but it’s really a very young science, more like psychology. We go through these ‘cargo cult science‘ rituals of p-values and econometric hypothesis tests, but there are deep, basic forces we don’t understand. We have precisely prepared all the apparatus for the detection of the phlogiston, and by God, we’ll get that 0.05 however we have to. (Think I’m being too harsh? “Real Business Cycle” theory essentially posits that the Great Depression was caused by everyone deciding that they weren’t going to work for a few years, and as whole countries fell into the abyss from failing financial markets, most economists still clung to the Efficient Market Hypothesis.) Our whole discipline requires major injections of intellectual humility: We not only don’t have all the answers; we’re not even sure we have all the questions.
I think the esoteric nature of questions like ‘the equity premium puzzle’ and the ‘tatonnement problem‘ is precisely the source of their appeal: It’s the sort of thing you can say you’re working on and sound very smart, because the person you’re talking to likely has no idea what you’re talking about. (Or else they are a fellow economist, and thus in on the con.) If you said that you’re trying to explain why poor countries are poor and why rich countries are rich—and if economics isn’t doing that, then what in the world are we doing?—you’d have to admit that we honestly have only the faintest idea, and that millions of people have suffered from bad advice economists gave their governments based on ideas that turned out to be wrong.
It’s really quite problematic how closely economists are tied to policymaking (except when we do really know what we’re talking about?). We’re trying to do engineering without even knowing physics. Maybe there’s no way around it: We have to make some sort of economic policy, and it makes more sense to do it based on half-proven ideas than on completely unfounded ideas. (Engineering without physics worked pretty well for the Romans, after all.) But it seems to me that we could be relying more, at least for the time being, on the experiences and intuitions of the people who have worked on the ground, rather than on sophisticated theoretical models that often turn out to be utterly false. We could eschew ‘shock therapy‘ approaches that try to make large interventions in an economy all at once, in favor of smaller, subtler adjustments whose consequences are more predictable. We could endeavor to focus on the cases where we do have relatively clear knowledge (like rent control) and avoid those where the uncertainty is greatest (like economic development).
At the very least, we could admit what we don’t know, and admit that there is probably a great deal we don’t know that we don’t know.