9-15-16

Thoughts on “The Trouble with Macroeconomics”

Paul Romer has written an engaging and wide-ranging critique of the last thirty-plus years of macroeconomics. It’s a must-read for anyone concerned who’s interested in the past and future of the field.

Romer makes a methodological criticism and a sociological criticism. I largely agree with the former but I am considerably less persuaded by the latter.

In terms of the methodological criticism, I’m going to strip it down to the following simple statement: Many of the most essentiall features of macroeconomic models have little grounding in evidence. For example, most of the models presume that:

agents have rational expectations.
product markets are purely competitive or are monopolistically competitive
labor markets are purely competitive, entirely union-based, or based on fairly structured one-on-one bargaining.

All of these modeling assumptions matter for key macroeconomic questions, like the effect of monetary policy on inflation and unemployment. But they are based largely on theoretical introspection (done thirty or forty years ago!), not data.

I want to be clear that this comment is related to, but distinct from, the oft-heard complaint that macroeconomic models don’t include the financial sector. There is, in fact, a financial sector in virtually every macroeconomic model. The problem is that this financial sector differs in essential ways from the actual financial sector. My point is that macroeconomists’ comfort level with these differences is symptomatic of an overall methodological shortcoming: macroeconomists are pretty comfortable with non-evidence-based approaches to modeling. (This is what Romer means, I think, when he uses the term “post-real” to describe current macroeconomics.)

And to my younger readers: models with heterogenous agents that exploit administrative data will not save you from this methodological problem. As you add richer forms of data, you will need to make choices about how these agents differ, how they interact (in markets and otherwise), form expectations about their careers and macroeconomic policies, and generally lead their lives. Those choices are either going to be largely based on ad hoc reasoning or on evidence. The incentives in academic macro are currently such that many of you will choose the former approach.

I think that the above short summary largely lines up with what Romer was saying about methodology (although with his references to phlogiston and trolls, he’s a lot more colorful and fun-to-read than I could ever hope to be).

Let me turn then to the sociological issue. Here, again, I’m going to oversimplify Romer’s argument to: macroeconomists have been content to stick with a bad modeling approach because they so deeply admire Bob Lucas, Tom Sargent, and Ed Prescott, and these leaders have been unwilling to explore new directions. I find this personalization of the problem to be extremely misleading. I say this for a couple of reasons. First, I can think of more than a few research agendas that have flourished in macroeconomics in the past thirty years without strong support - and at times active opposition - from these particular economists. Second, over the past thirty years, all of them have pushed their own research at various times in interesting directions that have (as of yet) not been adopted by the mainstream.

So, I think Romer’s formulation of the sociological problem takes us in the wrong direction. I would submit that the problem instead lies with how we (macroeconomists? economists? academics?) think about research. We tend to view research as being the process of posing a question and delivering a pretty precise answer to that question. In this process, machines that can be used by many scholars to generate answers to wide ranges of questions are highly prized. The King-Plosser-Rebelo real business cycle model was one such machine. The New Keynesian three-equation model is another. The Bewley-Aiyagari-Huggett incomplete markets model is yet another. And people who have the mathematical and computational skills to make machines even more powerful, so that they can answer even more questions, are naturally highly valued.

The research agenda that I believe we need is very different. It’s hugely messy work. We need to encourage those who are trying to build a more evidence-based modeling of financial institutions. We need to encourage those who are trying to learn more about how people actually form expectations. We need to encourage those who are using firm-based information about residual demand functions to learn more about product market structure. At the same time, we need to be a lot more flexible in our thinking about models and theory, so that they can be firmly grounded in this improved empirical understanding.

The good news is that this kind of shift away from introspection to evidence has taken place in many other fields of economics (industrial organization, labor economics, public finance, etc.). Can this same kind of change happen in macroeconomics? I’m not sure. It certainly won’t come from me writing blog posts! It will require a group of dedicated scholars - likely relatively early in their careers - who are willing to take some big risks to make macroeconomics different and better along the lines that I’ve described. Back in the ‘70s, Lucas, Sargent, and Prescott (and, of course, many others) were exactly such a group. Will we see their like again?

N. Kocherlakota

on the road in DC

September 15, 2016