Robert Waldman has a fantastic critique of Paul Romer’s recent missives on economic science. He’s commenting ultimately on why Lucas’s work isn’t such a breakthrough. In it he highlights something of immense importance. It’s hard to think of many developments in economic theory in recent decades to which his observations do not apply. His point is that ‘advances’ in theory tend to be advances in conventions of professional practice, rather than new insights into the world.
General Relativity explained an anomaly … the precession of the perihelion of Mercury… predict[ed]… how much gravity caused light to curve… has yielded a huge number of predictions which fit the data exactly… was easily modified to correspond to an expanding universe…. Physicists are quite sure general relativity is not the truth (because it is inconsistent with quantum mechanics and therefore a lot of data). But it is a very empirically successful theory.
In contrast, the Dixit-Stiglitz example did not attempt to explain anomalies. … The aim was to make models with imperfect competition tractable… an example…. They made a modelling choice… neither would guess that people might actually have Dixit-Stiglitz preferences…. It meant there was a standard way to handle imperfect competition…. [But] there are no general results…. Together the assumptions of imperfect competition and Nash equilibrium imply almost nothing….[Dixit-Stiglitz] made it possible to have the illusion that economic theorists understood imperfect competition, but this was discovery by assuming we have a can opener. The example was fruitful because, once a lot of people decided to explore the same special case, they could discuss its interesting behavior…. Theory can grow if people agree on core assumptions. This is progress if the assumptions are useful approximations. Once a field of economic theory has developed, its core assumptions are no longer vulnerable to data. I do not think the the development of a new branch of theory is necessarily scientific progress.
I think economic theory was massively improved by the Dixit-Stiglitz example because it made economists outside of industrial organization willing to consider imperfect competition. But… it gave the impression that there were simple elegant results based on assuming imperfect competition similar to those based on assuming perfect competition. There aren’t….
A radically new hypothesis which turns out to be totally false was not a contribution to scientific progress. Finding out that it was false was and such dead ends are inevitable in science. But in science development of new theory is not necessarily progress. OK, what about the Solow growth model and the Lucas supply function?… Solow… made a large number of extreme assumptions yielding a tractable model… that… fit the data surprisingly well… [in spite of] excellent arguments for why one shouldn’t be able to treat capital and labor as scalors…. There was no reason to think that the concept of disembodied technology would be useful. But it helps economists fit the data.
Lucas formalized an argument about price level misperception and fluctuations which had been made many times (for example by Keynes in The General Theory as Tobin explained to Lucas in 1971)…. Lucas definitely did not identify a previous conceptual error of treating the expectations unaugmented Phillips curve as a stable relationship–this is a myth. He added a focus on expectational errors alone and the insistence that economists assume rational expectations….
Unlike Dixit-Stiglitz… in 1972 the Lucas model was obviously grossly false – it implies that output is a white noise and it was well known that economic fluctuations aren’t. It requires that agents have very limited information on the price level when, in fact, they have a lot of information. I think it was clear that Lucas’s new research program would be sterile. I think it was entirely sterile…. I certainly don’t think this of the Solow growth model or imperfect competition with a Dixit-Stiglitz preferences or a Dixit-Stiglitz aggregator. Yes, Lucas 1972 was path breaking, but the new path Lucas blazed lead to a dead end.
It seemed to me that ‘New’ or ‘Strategic Trade’ theory was similarly a dead end. Indeed it was a dead end that John Hicks had warned that assumptions of imperfect competition would be in Value and Capital. Here’s Hicks:
[In the presence of scale economies,] [t]here must be something to stop the indefinite expansion of the firm, but it can just as well be stopped by the limitation of the market as by rising marginal costs. . . . It is, I believe, only possible to salvage anything from this wreck – and it must be remembered that the threatened wreckage is that of the greater part of economic theory – if we can assume that the markets confronting most . . . firms . . . do not differ very greatly from perfectly competitive markets. . . . At least this get-away seems well worth trying. We must be aware, however, that we are taking a dangerous step, and probably limiting to a serious extent the problems with which our subsequent analysis will be fitted to deal. Personally, however, I doubt if most of the problems we shall have to exclude for this reason are capable of much useful analysis by the methods of economic theory.
Given the canonical state of this passage and the book they come from, and the fact that it was these concerns that hung over trade theory and justified the almost ubiquitous assumption of perfect competition in formal models (along with the rider that scale economies were important and should not be ignored, but couldn’t be easily handled using formal theoretic methods) you’d think that the new agenda of strategic trade theory might have addressed Hicks’ concerns. That is you’d think that, in constructing the new field, its pioneers would have addressed this question – would have explicitly argued that what they were doing was not, now a waste of time. Certainly there were new techniques, but you’d hope they’d give some thought to their likely utility. I know this is very verbal and all, not conveyed in an equation, but that’s what you’d expect if their energies were to be deployed rigorously. The alternative is what I call the mountaineer’s approach to the utilisation of theory.
Q: Why did you rebuild trade theory around the Dixit-Stiglitz model?
A: Because it was there.