One way or reading the microfoundations debate is as a clash between ‘high theory’ and ‘practical policy’. Greg Mankiw in a well known paper talks about scientists and engineers. Thomas Mayer in his book Truth versus Precision in Economics (1993) distinguishes between ‘formalist’ and ‘empirical science’. Similar ideas are perhaps behind my discussion of microfoundations and central bank models, and Mark Thoma’s discussion here.
In these accounts, ‘high theory’ is potentially autonomous. The problem focused on is that this theory has not yet produced the goods as far as policy is concerned, and asks what economists who advise policy makers should do in the meantime. But the presumption is generally that theory will get there as soon as it can. But will it do so of its own accord? Is it the case that academics are quite good at selecting what the important puzzles are, or do they need others more connected to the data to help them?
There is a longstanding worry that some puzzles are selected because they are relatively easy to solve, and not because they are important. Like the proverbial person looking under the street light for their keys that they lost somewhere less well lit. This is the subject of this post. A later post will look at another concern, which is that there may be an ideological element in puzzle selection. In both cases these biases in puzzle selection can persist because the discipline exerted by external consistency is weak.
The example that reminded me about this came from this graph.
|US Savings Rate|
The role of the savings rate in contributing to the Great Recession in the US and elsewhere has been widely discussed. Some authors have speculated on the role that credit conditions might have played in this e.g. Eggertsson and Krugman here, or Hall here. But what about the steady fall in savings from the early 1980s until the recession?
Given the importance of consumption in macroeconomics, you would imagine there would be a huge literature, both empirical and theoretical, on this. Whatever this literature concluded, you would also imagine that the key policy making institutions would incorporate the results of this research in their models. Finally you might expect any academic papers that used a consumption model which completely failed to address this trend might be treated with some scepticism. OK, maybe I’m overdoing it a bit, but you get the idea. (There has of course been academic work on trying to explain the chart above: a nice summary by Guidolin and Jeunesse is here. My claim that this literature is not as large as it should be is of course difficult to judge, let alone verify, but I’ll make it nonetheless.)
It would be particularly ironic if it turned out that credit conditions were responsible for both the downward trend and its reversal in the Great Recession. However that is exactly the claim made in two recent papers, by Carroll et al here and Aron et al (published in Review of Income and Wealth (2011), earlier version here), with the later looking at the UK and Japan as well as the US. Now if you think this is obvious nonsense, and there is an alternative and well understood explanation for these trends, then you can stop reading now. But otherwise, suppose these authors are right, why has it taken so long for this to be discovered, let alone be incorporated into mainstream macromodels?
Well in the discovery sense it has not. John Muellbauer and Anthony Murphy have been exploring these ideas ever since the UK consumption boom of the late 1980s. As I explained in an earlier post, there was another explanation for this boom besides credit conditions that was more consistent with the standard intertemporal model, but the evidence for this was hardly compelling. The problem might be not so much evidence, as the difficulty in incorporating credit effects of this kind into standard DSGE models. Even writing down a tractable microfounded consumption function that incorporates these effects is difficult, although Carroll et al do present one. Incorporating it into a DSGE model would require endogenising credit conditions by modelling the banking sector, leverage etc . This is something that is now beginning to happen largely as a result of the Great Recession, but before that it was hardly a major area of research.
So here is my concern. The behaviour of savings in the US, UK and elsewhere has represented a major ‘puzzle’ for at least two decades, but it has not been a major focus of academic research. The key reason for that has been the difficulty of modelling an obvious answer to the puzzle in terms of the microfoundations approach. John Muellbauer makes a similar claim in this paper. To quote: “While DSGE models are useful research tools for developing analytical insights, the highly simplified assumptions needed to obtain tractable general equilibrium solutions often undermine their usefulness. As we have seen, the data violate key assumptions made in these models, and the match to institutional realities, at both micro and macro levels, is often very poor.”
I do think microfoundations methodology is progressive. The concern is that, as a project, it may tend to progress in directions of least resistance rather than in the areas that really matter – until perhaps a crisis occurs. This is not really mistaking beauty for truth: there are plenty of rather ugly DSGE macro papers out there, one or two of which I have helped write. It is about how puzzles are chosen. When a new PhD student comes to me with an idea, I will of course ask myself is this interesting and important, but my concern will also be whether the student is taking on something where they can get a clear and publishable result in the time available.
When I described the Bank of England’s macromodel BEQM, I talked about the microfounded core, and the periphery equations that helped fit the data better. If all macroeconomists worked for the Bank of England, then that construct contains a mechanism that could overcome this problem. The forecasters and policy analysts would know from their periphery equations where the priority work needed to be done, and this would set the agenda for those working on microfounded theory.
In the real world the incentive for most academics is to get publications, often within a limited time frame. When the focus of macroeconomic analysis is on internal consistency rather than external consistency, then it is unclear whether this incentive mechanism is socially optimal. If it is not, then one solution is for all macroeconomists to work for central banks! A more realistic alternative might be to reprise within academic macroeconomics a modelling tradition which placed more emphasis on external consistency and less on internal consistency, to work alongside the microfoundations approach. (Justin Fox makes a similar point in relation to financial modelling.)