Why the microfoundations hegemony holds back macroeconomic progress

When David Vines asked me to contribute to a OXREP (Oxford Review of Economic Policy) issue on “Rebuilding Macroeconomic Theory”, I think what he hoped I would write on how the core macro model needed to change to reflect macro developments since the crisis with a particular eye to modelling the impact of fiscal policy. That would be an interesting paper to write, but I decided fairly quickly that I wanted to say something that I thought was much more important.

In my view the biggest obstacle to the advance of macroeconomics is the hegemony of microfoundations. I wanted at least one of the papers in the collection to question this hegemony. It turned out that I was not alone, and a few papers did the same. I was particularly encouraged when Olivier Blanchard, in blog posts reflecting his thoughts before writing his contribution, was thinking along the same lines.

I will talk about the other papers when more people have had a chance to read them. Here I will focus on my own contribution. I have been pushing a similar line in blog posts for some time, and that experience suggests to me that most macroeconomists working within the hegemony have a simple mental block when they think about alternative modelling approaches. Let me see if I can break that block here.

Imagine a DSGE model, ‘estimated’ by Baynesian techniques. To be specific, suppose it contains a standard intertemporal consumption function. Now suppose someone adds a term into the model, say unemployment into the consumption function, and thereby significantly improves the fit of the model. It is not hard to think why the fit significantly improves: unemployment could be a proxy for the uncertainty of labour income, for example. The key question becomes which is the better model with which to examine macroeconomic policy: the DSGE or the augmented model?

A microfoundations macroeconomist will tend to say without doubt the original DSGE model, because only that model is known to be theoretically consistent. (They might instead say that only that model satisfies the Lucas critique, but internal consistency is the more general concept.) But an equally valid response is to say that the original DSGE model will give incorrect policy responses because it misses an important link between unemployment and consumption, and so the augmented model is preferred.

There is absolutely nothing that says that internal consistency is more important than (relative) misspecification. In my experience, when confronted with this fact, some DSGE modellers resort to two diversionary tactics. The first, which is to say that all models are misspecified, is not worthy of discussion. The second is that neither model is satisfactory, and research is needed to incorporate the unemployment effect in a consistent way.

I have no problem with that response in itself, and for that reason I have no problem with the microfoundations project as one way to do macroeconomic modelling. But in this particular context it is a dodge. There will never be, at least in my lifetime, a DSGE model that cannot be improved by adding plausible but potentially inconsistent effects like unemployment influencing consumption. Which means that, if you think models that are significantly better at fitting the data are to be preferred to the DSGE models from whence they came, then these augmented models will always beat the DSGE model as a way of modelling policy.

What this question tells you is that there is an alternative methodology for building macroeconomic models that is not inferior to the microfoundations approach. This starts with some theoretical specification, which could be a DSGE model as in the example, and then extends it in ways that are theoretically plausible and which also significantly improve the model’s fit, but which are not formally derived from micofoundations. I call that an example within the Structural Econometric Model (SEM) class, and Blanchard calls it a Policy Model.

An important point I make in my paper is that these are not competing methodologies, but instead they are complementary. SEMs as I describe them here start from microfounded theory. (Of course SEMs can also start from non-microfounded theory, but the pros and cons of that is a different debate I want to avoid here.) As a finished product they provide many research agendas for microfoundation modelling. So DSGE modelling can provide the starting point for builders of SEMs or Policy Models, and these models when completed provide a research agenda for DSGE modellers.

Once you see this complementarity, you can see why I think macroeconomics would develop much more rapidly if academics were involved in building SEMs as well as building DSGE models. The mistake the New Classical Counter Revolution made was to dismiss previous ways of modelling the economy, instead of augmenting these ways with additional approaches. Each methodology on its own will develop much more slowly than the two combined. Another way of putting it is that research based on SEMs is more efficient than the puzzle resolution approach used today. 

In the paper, I try to imagine what would have happened if the microfoundations project had just augmented the macroeconomics of the time (which was SEM modelling), rather than dismissing it out of hand. I think we have good evidence that active complementarity between SEM and microfoundations modelling would have investigated in depth links between the financial and real sectors before the financial crisis. The microfoundations hegemony chose the wrong puzzles to look at, deflecting macroeconomics from the more important empirical issues. The same thing may happen again if the microfoundations hegemony continues.

Arguments for ending the microfoundations hegemony

Should all macroeconomic models in good journals include their microfoundations? In terms of current practice the answer is almost certainly yes, but is that a good thing? In earlier posts I’ve tried to suggest why there might be a case for sometimes starting with an aggregate macro model, and discussing the microfoundations of particular relationships (or lack of) by reference to other papers. This is a pretty controversial suggestion, which will appear for many to be a move backwards not just in time but in terms of progress. As a result I started with what I thought would be one fairly uncontroversial (but not exactly essential) reason for doing this. However let me list here what I think are the more compelling reasons for this proposal.

1) Empirical evidence. There may be strong empirical evidence in favour of an aggregate relationship which has as yet no clear microfoundation. A microfoundation may emerge in time, but policy makers do not have time to wait for this to happen. (It may take decades, as in the microfoundations for price rigidity.) Academics may have useful things to say to policy makers about the implications of this, as yet not microfounded, aggregate relationship. A particularly clear case is where you model what you can see rather than what you can microfound. For further discussion see this post.

2) Complexity. In a recent post I discussed how complexity driven by uncertainty may make it impossible to analytically derive microfounded relationships, and the possible responses to this. Two of the responses I discussed stayed within microfoundations methodology, but both had unattractive features. A much more tractable alternative may be to work directly with aggregate relationships that appear to capture some of this complexity. (The inspiration for this post was Carroll’s paper that suggested Friedman’s PIH did just that.)

3) Heterogeneity. At first sight heterogeneity that matters should spur the analysis of heterogeneous agent models of the kind analysed here, which remain squarely within the microfoundations framework. Indeed it should. However in some cases this work could provide a rationalisation for aggregate models that appear robust to this heterogeneity, and which are more tractable. Alan Blinder famously found that there was no single front runner for causes of price rigidity. If this is because an individual firm is subject to all these influences at once, then this is an example of complexity. However if different types of firm have different dominant motives, then this is an example of heterogeneity. Yet a large number of microfoundations for price rigidity appear to result in an aggregate equation that looks like a Phillips curve. (For a recent example, see Gertler and Leahy here.) This might be one case where working with aggregate relationships that appear to come from a number of different microfoundations gives you greater generality, as I argued here.

4) Aggregate behaviour might not be reducible to the summation of individuals optimising. This argument has a long tradition, associated with Alan Kirman and others. I personally have not been that persuaded by these arguments because I’ve not seen clear examples where it matters for bread and butter macro, but that may be my short-sightedness.

5) Going beyond simple microeconomics. The microeconomics used to microfound macromodels is normally pretty simple. But what if the real world involves a much more substantial departure from these simple models? Attitudes to saving, for example, may be governed by social norms that are not always mimicked by our simple models, but which may be fairly invariant over some macro timescales, as Akerlof has suggested. This behaviour may be better captured by aggregate approximations (that can at least be matched to the data) than a simple microfoundation. We could include under this umbrella radical departures from simple microfoundations associated with heterodox economists. I do not think the current divide between mainstream and heterodox macro is healthy for either side.

If this all seems very reasonable to you, then you are probably not writing research papers in the macroeconomics mainstream. Someone who is could argue that once you lose the discipline of microfoundations, then anything goes. My response is that empirical evidence should, at least in principle, be able to provide an alternative discipline. In my earlier post I suggested that the current hegemony of microfoundations owed as much to a loss of faith in structural time series econometrics as it did to the theoretical shortcomings of non-microfounded analysis. However difficulties involved in doing time series econometrics should not mean that we give up on looking at how individual equations fit. In addition, there is no reason why we cannot compare the overall fit of aggregate models to microfounded alternatives.

While this post lists all the reasons why sometimes starting with aggregate models would be a good idea, I find it much more difficult to see how what I suggest might come about. Views among economists outside macro, and policy makers, about the DSGE approach can be pretty disparaging, yet it is unclear how this will have any influence on publications in top journals. The major concern amongst all but the most senior (in terms of status) academic macroeconomists is to get top publications, which means departing from the DSGE paradigm is much too risky. Leaders in the field have other outlets when they want to publish papers without microfoundations (e.g. Michael Woodford here).

Now if sticking with microfoundations meant that macroeconomics as a whole gradually lost relevance, then you could see why the current situation would become unsustainable. Some believe the recent crisis was just such an event. While I agree that insistence on microfoundations discouraged research that might have been helpful during and after the crisis, there is now plenty of DSGE analysis of various financial frictions (e.g. Gertler and Kiyotaki here) that will take the discipline forward. I think microfoundations macro deserves to be one of, if not the, major way macro is done. I just do not think it is the only route to macroeconomic wisdom, but the discipline at the moment acts as if it is.