I recently criticised contemporary economics in a speech launching Max Corden’s memoirs. Economic theory threatens to become a Tower of Babel, preoccupied with the world within its models and irrelevant to policy. This has crowded out an older style of which Corden was an exemplar, in which economics aspired to be the supremely useful social science, policy-relevant as clarified commonsense.
I cited Paul Krugman’s claim that macroeconomics had actually regressed as a result, but I also pointed out that Krugman had himself been the architect of the same kind of regression. He won a Nobel Memorial Prize for his trouble.
In Krugman’s characteristically vigorous and clear-headed response to my speech, he suggests that this is the ‘money quote’ from my speech.
Krugman [is] about the most brilliant and useful economist we have. But his most brilliant work wasn’t useful, and his most useful work isn’t brilliant”
We’ll get to what I think was the money quote, but first … Krugman and I are in violent agreement about the subject of his response – the differences between the Macro and the Trade Towers of Babel.
In macro, the grand prize was ‘micro-foundations’ in which micro and macroeconomics would be unified into a crystalline structure, not unlike Euclid’s Elements, as macro was rebuilt from an aggregation of perfectly rational optimising agents. As I mentioned, “this mindset gave additional licence to the motivated reasoning of the libertarian right”.
For many, that was the idea all along. Like the misdirection of a master magician, new classical models assumed away all the ‘imperfections’ that stare us in the face and make the macroeconomy such an ornery beast, both to live in and to understand; its frictions in transmitting information and incentives, its ‘animal spirits’ and tendency to self-fulfilling prophecies of gloom and euphoria, its ‘sticky’ prices and wages.
And voila! Unemployment disappears! The great depression was really millions of workers taking a spontaneous holiday. And forget government action to fight the business cycle. It’s misguided, and futile if not actively destabilising. And no, I’m not kidding.
By my lights, new classical macro is the most egregious example, but the pattern recurs in field after field. Including Krugman’s new trade theory. The new models produced a Tower of Babel in which strong, robust predictions or policy conclusions were hard to come by. But, as Krugman replies, here the motive wasn’t to banish aspects of reality that were inconvenient for the modelling (or one’s ideology), but rather to invite them in.
What could possibly be wrong with that?
When the assumptions behind your model are simple and seem to formally capture the essence of something important, it can open up a world of insight. This occurred in the first wave of formalism in economics from around 1870 to World War II. At this stage, it’s easy to think that economics’ job is to simply expand this formal method, forever relaxing assumptions towards greater realism.
That’s what the brilliant and useful Paul Samuelson thought as he pioneered the new, mathematical economics from the late 1940s on, seeking to “accumulate a convergent body of econometric findings convergent on a testable truth”. Forty years on he lamented. “My confession is that this expectation has not worked out”.
We’ve been here before. In fact, Isaac Newton ran into the same problem. The handful of simplifying assumptions he made in his celestial mechanics give us a God-like vision of the heavens that’s intoxicated us ever since. But it turns out that its power degrades quite quickly once more than just two celestial bodies (like planets) enter the analysis.
The early progress of formalism brought forth a vision that was almost as miraculous as Newton’s system and in some ways more intoxicating. Quite standard demand and supply diagrams give you a way to look at the chaos of economic life of such easy power that it feels you’ve got magic goggles. Suddenly, you can see how all manner of policies affect both the economy as a whole and the relevant groups as well. Rent control, tariffs, tax and welfare changes – you name it.
But everything has its price. The price of this vision is a long list of unrealistic assumptions. And a central assumption is that competition determines prices, not firms. And the fact is that, in all markets that aren’t for commodities, scale economies limit the number of competitors and give firms some pricing power – as Apple has over smartphones and McDonalds or even the local milk bar has over its burgers. Now there’s a serpent in paradise.
In my original speech, I quoted Max Corden’s mentor, J.R. Hicks, wrestling with the serpent on our behalf. He was trying to hang onto those goggles. Firms’ pervasive pricing power is modern economics’ ‘three body problem’. As Hicks points out, if firms have some pricing power, you don’t even know if they’ll increase supply when demand rises. They might just raise prices, or even cutsupply to boost prices further. And if your answer to any important question is “it all depends on the circumstances”, you don’t have much of a theory.
Hicks plumps for perfect competition because, although imperfect competition is more realistic, if we “abandon … the assumption of perfect competition … the basis on which economic laws can be constructed is … shorn away”. He concludes:
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..
Hicks’ advice isn’t to ignore scale economies but rather to take them into account either informally, or with ad hoc models fitted to specific policy issues and circumstances, just as a person with a map understands that they might have to work out the detail that it doesn’t cover.
Economics had changed by the late 1970s. The Dixit-Stiglitz model of imperfect competition and variants of it were becoming workhorses in various areas. So it made sense to deploy them in trade theory to see what insights they might turn up. But those models themselves were full of ad hoc assumptions – leaving Hicks’ wider concerns unaddressed, limiting the practical relevance of the modelling results. The culture of economic discourse had changed too. With academic specialisation proceeding apace, Hicks’ style of close, discursive reasoning became rarer and, perhaps more to the point, unnecessary to get journal articles accepted.
Max Planck told us that science progresses one funeral at a time. But that’s how it regresses too. Like lots of intellectual innovators, Krugman had difficulty publishing his early new trade papers. Referees were unconvinced that an “understanding of these issues would be helped by writing down formal models”. Of course the papers deserved publication, but the referees’ concerns weren’t only valid, they were vindicated. In the upshot, as Krugman admits, this journey towards more ‘realism’ in formal trade theory, wasn’t very useful. It showed that:
- scale economies give us more gains to trade (suggesting that traditional models can substantially underestimate the case for free trade) but
- at the same time the models generate a plethora of ‘special cases’ enabling countries to advantage themselves with trade interventions to advantage certain firms.
And we already knew that. As trade theorist Ronald Wonnacott protested after a decade of new trade theory, it “may not yet have even scratched the surface. To identify one of the large number of possible new cases, all that’s required is the combining of one of the many causes of market failure with one of the many mercantilist instruments that could then be used to increase welfare”.
Here’s Krugman’s Nobel acceptance speech:
You may think all this is obvious, and it is – now. But it was totally not obvious before 1980 or so – except for some prescient quotes from Paul Samuelson, you really can’t find anyone describing trade this way until after the theory had been laid out in mathematical models. The plain English version came later.
And you should bear in mind that economists have been thinking and writing about international trade for a couple of centuries; to come along and say, “Hey, we’ve been missing half the story” was a pretty big thing.
Here we get to the nub of my beef with Krugman. Certainly there must be a division of intellectual labour to get anywhere. But formal theory should develop in close dialogue with – indeed to the extent possible should be enveloped by – close discursive reasoning. And theorists must respect the knowledge of others working in areas of relevance. My reaction – I think, were he alive, J.R. Hicks’ reaction – to the way trade theorists ignored scale economies before Krugman modelled them is “shame on them”, or more constructively, “how can we improve the disciplinary incentives that reward this groupish myopia?”.
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For all his brilliance, I’m repeatedly shocked at Krugman’s complacency on this score from his perch in the heights of the academy. As I put it in my speech, Krugman thinks that that “those who smell a rat at the dysfunctionality of all this should just get over themselves”. But it gets worse. What could Krugman possibly mean when he tells his Stockholm audience that “the plain English version” came after his theory? What’s his response to the list I mentioned in my speech?
- Hicks (1959),
- Linder (1961),
- Elkan (1965),
- Vernon (1966),
- Balassa (1966),
- Drysdale (1969),
- Grubel (1967),
- Corden (1970),
- Lloyd (1975)
- Gray (1976),
- Bhagwati (1973),
- Krueger (1978).
I’m genuinely baffled, given Krugman would be familiar with most if not all these authors. In any event, if he wants a ‘money quote’ from me to respond to, that would be my pick.
All this while Krugman laments new classical macro’s bred-in insularity from those pesky facts in the real world.
Theory is a moon buggy for exploring terrain that’s difficult or impossible to explore any other way. We need our wits about us to build and to guide the buggy. The real distinction isn’t between formal and informal methods – they both need each other. It’s between the use of those methods that is skilful and fruitful, rather than just clever, and use that is less so – between good analysis (formal and discursive) and not-so-good analysis.
Formal models will be worthwhile if they raise logical possibilities leading to conclusions that are important and surprising and weren’t otherwise clear. Another kind of usefulness arises when they give us another, better understanding of the mechanisms causing the economic phenomena we observe.
To get back to what Krugman took to be my ‘money quote’, since he’s stopped using his brilliance to rediscover the obvious, his work has focused on real and pressing problems. I think of Krugman’s Nobel for his new trade theory as an Academy Award. He deserves the Nobel for calling the risks of a lost decade long before the reality was upon us and for his economic journalism – the best since Keynes. Though these days he occasionally apologises for the provisional nature of his sketched models on his blog for their falling short of the standards expected in academic publication, their usefulness shines through. So much the worse for academic publications which, in the age of the internet, we’ve made lamentably little progress in reinventing.
While the sales pitch was always that new trade theory responded to developments in the world, its real focus was itself. In 1985, Brander and Spencer showed that an export subsidy could advantage a nation hosting one of the two firms in a duopoly where the other was located abroad – think Airbus and Boeing. Apparently, this “idea” generated a “flurry of excitement”.It wasn’t wrong theory. It was bad theory, labouring to rediscover the obvious by imposing crude assumptions to get the maths out. The next year Eaton and Grossman published an analogous model with a slightly different (though equally crude) assumption about how the firms interacted. This reversed the result. Which paper was right? Neither. They both follow long-established conventions in the assumptions and the maths they use. So they look serious and, as we saw, they’re publishable. But, as a way of thinking about the difficult question of Airbus and Boeing’s rivalry, both tell us next to nothing. They’re silly; ‘academic’ in the bad sense.
In this sense, I think the heirs to Corden’s work in trade are those who’ve done the intellectual work to understand the patterns of trade and development we observe and to infer robust, or at least promising and insightful policy conclusions from them: people like Dani Rodrik and Ricardo Hausmann. They’re helping break open another citadel of groupish myopia – the Washington Consensus. They use theory of course, but not merely to rediscover the obvious and then reprove others’ for failing to render their thoughts visible to the high priests.
2018 July 8
 To quote two emails I received from practicing economists – one in the markets and one in an international governmental organisation – in the upshot of this debate
“[Y]our aphorism was a good one. … [I]t is, in a way, a marvellously pithy summary of the the whole of post-1980 economics – macro, monetary, trade (I assume), micro… the lot. When brilliant, a bit useless – when useful, all too often a statement of the bleeding obvious.”
“[You] could easily be describing aspects of health economics”.
 Patterns that emerge robustly with two bodies often break down into non-recurring patterns bogging the analysis down into endless special cases some of which break down into chaotic motion. Though there are multiple bodies in the solar system, stability is assured by the fact that virtually all the relationships exist as one or more small bodies circling a much larger body so the third-body interactions have very marginal effects on the main pair. The planets perturb each others’ orbit infinitesimally.
The presence of three bodies does not produce chaos automatically, but raises the spectre of the same. See this essay for further elaboration. The point is simply that the capacity to understand even a very simple system can break down quite quickly once we move towards greater ‘realism’ or fidelity to the empirical world we can see.
 It gives us a powerful new way of looking at the world. As Australia’s then Opposition leader, Professor of Business, John Hewson observed in 1991: “As soon as you get an equilibrium approach to life, suddenly you realise that a lot of what you’d thought was wrong”. But it threatens to be more intoxicating because, in addition to painting a picture of the way the world really is (if only the world could stop being so messy) it also offers a powerful vision of an ideal. When an anomaly was discovered with Newton’s system, there was no-one arguing that we should change nature’s laws to make it look more like our model. When some grand theory appears to be refuted by experience, there’s usually no shortage of people arguing that we haven’t tried hard enough to implement the theory.
In contrast [to Einstein’s explanation of an empirical anomaly in Newtons system], the Dixit-Stiglitz [model of imperfect competition] did not attempt to explain anomalies. … The aim was to make models with imperfect competition tractable.… [The (unrealistic) assumptions they made] meant there was a standard way to handle imperfect competition…. [But] there are no general results…. [The Dixit-Stiglitz model] 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. … 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….
 Gans, J. G. and Shepherd, G.B., 1994. “How the Mighty are Fallen: Rejected Classic Articles by Leading Economists”, Journal of Economic Perspectives, Volume 8, pp. 165-179 at p. 170.
 All mention the significance of scale economies in driving trade patterns together with plenty of empirical data and theorising in both plain English and ad hoc partial equilibrium models and schematic diagrams. Some I didn’t mention in my speech include:
- Kravis (1956),
- Drèze (1958),
- Posner, (1961),
- Hufbauer, (1965),
- Elkan (1965),
- Kojima (1965),
 I’d add that informal reasoning, of the kind we’re using in this discussion, is the master discourse and formal reasoning its servant, or, to use the image of a marvellous book, it’s emissary. For those who are interested, I recommend the introduction given by Russ Roberts in his recent, characteristically excellent, interview with the author of the 2009 classic, The Master and his Emissary on EconTalk.
 Brander, J. A. and Spencer, B., 1985. “Export Subsidies and Market Share Rivalry”, Journal of International Economics, 18, pp. 83-100.
 Krugman, P., 1993. “The Narrow and Broad Arguments for Free Trade”, American Economic Association, Papers and Proceedings, American Economic Review, 83, pp. 362-371.
 Eaton, J. and Grossman, G. M., 1986. “Optimal Trade and Industrial Policy under Oligopoly”, Quarterly Journal of Economics, 101, pp. 383-406.
 The two papers used ‘Cournot’ and ‘Betrand’ models of duopoly respectively. A Cournot duopolist maximises its profits assuming its competitor’s output as given whilst the Betrand competitor takes their competitor’s prices as given.