My task to give a faithful account of the conference is doomed from the start. “Rani Spiegler’s talk was the best” tells me the LSE grad student who I bump into on the way out. Alas, Rani’s was the first talk of the day, and I missed it. I know of his book, of course. Entitled “A curious culture of economic theory” (and freely available online), it’s a witty and rewarding reflection on the style of economic papers and the high-five (general interest journal) incentives that brought it about. Among its contents are polemical beauties such as the “Debraj Ray test”. It’s on many a mind as a grandee list of presenters comes to the LSE to speak, it’s no exaggeration, on the questions Rani has raised in his book.
Theorists are a peculiar bunch. Helplessly eccentric and long seen as the philosopher-kings of the profession, our standing has slowly been fading. The week prior a colleague tells me that many economists think that theory is on the way out. Perhaps we should invite more experimentalists to our seminars he suggests. Another theory colleague shares a graph of the declining share of theory papers in NBER publications. As Eric Eyster points out in his talk, our insights are not understood, merely mentioned but hardly ever used in non-theory research.
I have long felt untroubled by such commotion. Insecurity and anxiety may dominate my field. Yet the fact remains that reflecting about why stuff—inflation, demographics, employment, form of government—changes (and significantly so over the last few decades) will always require a theoretical framework. And with it, researchers who understand and study the framework’s properties rather than bringing it straight to the data.
Trouble is—let’s call this problem #1—theorists do not seem terribly excited about economics. This is not a recent observation. Let me quote from an article mentioned by John Sutton at the conference. It is called “Games Economists Play: A Noncooperative View” by Franklin Fisher, written almost 40 years ago on the theory of industrial organisation. “There is a strong tendency for even the best practitioners to concentrate on the analytically interesting questions rather than on the ones that really matter for the study of real-life industries.” Yet simply mandating that theorists study economic phenomena is not a solution. Truth is, to make progress on understanding economic phenomena, we must understand properties of economic models first (e.g., what are the implications of different ways of modelling search frictions?). Such understanding requires expertise which can only be developed if not all economic models must shed light on economic phenomena (e.g., frictional unemployment). This brings about a dilemma. Research in theory cannot flourish without researcher discretion. But if researchers decide what to study without regard for economics, the research produced is unlikely to be of much value for real-world understanding.
To solve this dilemma, the economic profession has concocted prestigious general interest journals that researchers must publish in to advance their career. Despite the psychological strain this causes for young researchers, there is a welfare case to be made for them: by curating demand (e.g., no to existence proofs, yes to work on redistribution), editors can change researchers’ incentives and thereby steer researchers’ attention towards problems on which progress is deemed more urgent.
Does it work this way?
In his book, Rani professes that “nobody knows” why some papers and topics enjoy success in general interest journals, whereas others remain on the sidelines. Why did Bayesian persuasion take off, yet multi-contracting (to cite work by my advisor that fascinates me) did not? Rani’s best attempt to explain the differential success centres on style and rhetoric. Curation has no part in it. One former Econometrica editor suggested after a seminar dinner that what gets recognized as good theory may simply be a social construct. According to what criteria? There is no consensus. At the conference, Eddie Dekel, another former editor, made an analogy to a supreme court ruling on obscenity: good theory is impossible to define but recognized as such when encountered.
I have a view of my own: Papers take off if they offer other researchers a hammer that they can use. If you subscribe to this view, the genius of Bayesian persuasion was to seduce its readers into thinking of concavification as a tool capable of hammering nails that general interest journals would publish. The unfortunate corollary is an explanation of the observed decline of theorists’ standing within the profession: If the most successful theory papers are merely hammers for other theory papers, why would economists looking for insights read them?
There is one important problem with the hammer view: The prioritization of hammers over insights is longstanding, whereas the decline in the centrality of theory in economics is recent. Something else must have changed, too. The fundamental issue as I see it—let’s call it problem #2—is that theorists have successfully made the case to each other that theory cannot say much about economics.
Two literatures exemplify this: General equilibrium (GE) theory withered, in part, because of a result that was at the same time damning and mathematically too challenging for most: the Sonnenschein-Mantel-Debreu theorem. Any allocation can occur as a general equilibrium of some economy. In other words, there is little predictive power in GE. In came the game theory revolution and a very different practice: the creatively liberating exercise of writing down toy models (usefully referred to as “exemplifying” as opposed to “generalizing theory” by aforementioned Fisher). Some think that this revolution has since met its predecessor’s fate: Being deemed useless for Popperian science, since a clever theorist could write models that would plausibly make about any prediction.
Theorists have adopted different attitudes to cope with their perceived Popperian shortcomings. Let me sketch the polar opposites. On one end, there is the narrative approach: As Ariel Rubinstein likes to say, a model is just a story (albeit without, it seems to me, the surprise and moral dimension) that does not offer a straightforward link to observed economic behaviour. On the other end, there is the design approach where a model is an austere and faithful description of real world markets or mechanisms. The end is concrete optimization of institutional rules, not abstract insight.
I am personally sceptical of both approaches. Neither the narrative nor the design approach comes with a convincing way of selecting its object of study. Which classes of models are worthy of our attention? No definition exists. Only a few austere environments meet the realism demanded by market designer. As a result, we know far too much about school choice in Boston, a topic few people (other than parents in Boston) ought to be passionate about. In the narrative realm, most models are in fact sequels of (often worthwhile) earlier stories that have entered the canon long ago when theorists may have felt surer about themselves. Adding elements that would make these stories more realistic (or at least bring them in line with empirical work, e.g., discrete choice) is not a priority.
When theory loses confidence
The current equilibrium pains me. I chose theory over macro-finance because I believed that to understand the macroeconomy one must study what happens at the micro level first. Not because I wanted to avoid thinking about the economy. My becoming a theorist was a disciplined choice, and in part motivated by what the Toulousain understanding of theory entailed.
Back then, I was interested in inefficiencies in bank lending due to asymmetric information over project quality. It felt like a big thing. Many now successful entrepreneurs, e.g., the inventor of Red Bull as I recently learned, were outright shunned by the banks. I believed then and do now that the extent of distortions was impossible to understand without a convincing theory of bank lending under asymmetric information. To understand macroeconomic implications, (i) market power, (ii) screening via different contracts and (iii) the option to borrow from several banks would have to be part of such theory. To date, no unified theory exists. Writing one is bloody hard. This does not prevent policy from being implemented of course: Is it sensible to lend to entrepreneurs directly (e.g., the EIB in the EU or the Department of Energy in the US)? If so, at what interest rate? Above or below the market rate? Or is government money better spent on securing loans (e.g., as is done for exporters)? Theorists have close to a monopoly on the tools to write such a theory. Why don’t they get going?
In 2002, Rochet and Stole wrote on the classical topic of competition and price discrimination: “We are struck by the fact that, in this instance, econometric practice is ahead of the theoretical literature.” In 2025, this sentence warrants repeating without the dependent clause. The gap between empirical and theoretical work has only been growing. Just consider that economists were surprised that healthcare exchanges in the US kept functioning as before when the individual mandate was repealed. And our best explanation for why inflation surged was that people expected inflation to surge. Having a theory of monetary policy that includes money or models of insurance markets that account for market power may have helped. It would seem only natural that the best-trained mathematical economists work on these questions.
The real tragedy is not the decline of the standing of theory but the dearth of economics in theory. The philosopher-kings with scant interest in economics are doing just fine and should not change course. My concern is that too many of the economists have left. This is a problem of selection (cf. Problem #1) that an invented epistemological crisis (cf. Problem #2) has made worse: If leading practitioners blur the link between theory and observed economic phenomena, mathematically gifted students with an active interest in economics naturally look elsewhere for insights. The publishing process is not kind to those who stubbornly try. Having dared to propose applications of theorems in my theory papers, I can report that these are politely ignored in the submission process or requests are made to excise them. Many of the toy models that I have written in the past few years will likely never be published as there is no hammer, only insight.
Does this make me a pessimist? Hardly so. First, theory cannot possibly vanish. In my view the theoretical approach to economics continues to hold the greatest potential for true discovery. I strongly believe that a mature field of economic theory is conceivable where theoretical predictions precede identification of patterns in the data (e.g., how does an increase in search frictions impact assortative matching). Second, our ignorance is our asset. The changeability of beliefs in the profession on about every topic of major economic importance is a measure of our ignorance. Why do beliefs change so dramatically? I think: For lack of theory as an organising principle of economics. Current theory is mostly exemplary (something can happen). Good theory, by contrast, generalises (something will happen) and in so doing brings clarity that empirical work cannot. This theory is not far afield: I share John Moore’s sense that much can be learnt, still, by studying ‘the old stuff’. Third, and on a more practical note, there is real demand for economic theory. In the words of one conference participant complaining about past theory seminar series: “I don’t request that every theory seminar be about prices and markets. But at least once in a while, that would be nice.”
