This is a brief follow-up to this post from Noah Smith (see this post for the abstract to the Marco Del Negro, Marc P. Giannoni, and Frank Schorfheide paper he discusses):
So far, we don’t seem to have gotten a heck of a lot of a return from the massive amount of intellectual capital that we have invested in making, exploring, and applying [DSGE] models. In principle, though, there’s no reason why they can’t be useful.
One of the areas I cited was forecasting. In addition to the studies I cited by Refet Gurkaynak, many people have criticized macro models for missing the big recession of 2008Q4-2009. For example, in this blog post, Volker Wieland and Maik Wolters demonstrate how DSGE models failed to forecast the big recession, even after the financial crisis itself had happened…
This would seem to be a problem.
But it’s worth it to note that, since the 2008 crisis, the macro profession does not seem to have dropped DSGE like a dirty dishrag. … Why are they not abandoning DSGE? Many “sociological” explanations are possible, of course – herd behavior, sunk cost fallacy, hysteresis and heterogeneous human capital (i.e. DSGE may be all they know how to do), and so on. But there’s also another possibility, which is that maybe DSGE models, augmented by financial frictions, really do have promise as a technology.
This is the position taken by Marco Del Negro, Marc P. Giannoni, and Frank Schorfheide of the New York Fed. In a 2013 working paper, they demonstrate that a certain DSGE model was able to forecast the big post-crisis recession.
The model they use is a combination of two existing models: 1) the famous and popular Smets-Wouters (2007) New Keynesian model that I discussed in my last post, and 2) the “financial accelerator” model ofBernanke, Gertler, and Gilchrist (1999). They find that this hybrid financial New Keynesian model is able to predict the recession pretty well as of 2008Q3! Check out these graphs (red lines are 2008Q3 forecasts, dotted black lines are real events):
I don’t know about you, but to me that looks pretty darn good!
I don’t want to downplay or pooh-pooh this result. I want to see this checked carefully, of course, with some tables that quantify the model’s forecasting performance, including its long-term forecasting performance. I will need more convincing, as will the macroeconomics profession and the world at large. And forecasting is, of course, not the only purpose of macro models. But this does look really good, and I think it supports my statement that “in principle, there is no reason why [DSGEs] can’t be useful.” …
However, I do have an observation to make. The Bernanke et al. (1999) financial-accelerator model has been around for quite a while. It was certainly around well before the 2008 crisis. And we had certainly had financial crises before, as had many other countries. Why was the Bernanke model not widely used to warn of the economic dangers of a financial crisis? Why was it not universally used for forecasting? Why are we only looking carefully at financial frictions after they blew a giant gaping hole in the world economy?
It seems to me that it must have to do with the scientific culture of macroeconomics. If macro as a whole had demanded good quantitative results from its models, then people would not have been satisfied with the pre-crisis finance-less New Keynesian models, or with the RBC models before them. They would have said “This approach might work, but it’s not working yet, let’s keep changing things to see what does work.” Of course, some people said this, but apparently not enough.
Instead, my guess is that many people in the macro field were probably content to use DSGE models for storytelling purposes, and had little hope that the models could ever really forecast the actual economy. With low expectations, people didn’t push to improve the existing models as hard as they might have. But that is just my guess; I wasn’t really around.
So to people who want to throw DSGE in the dustbin of history, I say: You might want to rethink that. But to people who view the del Negro paper as a vindication of modern macro theory, I say: Why didn’t we do this back in 2007? And are we condemned to “always fight the last war”?
My take on why these models weren’t used is a bit different.
My argument all along has been that we had the tools and models to explain what happened, but we didn’t understand that this particular combination of models — standard DSGE augmented by financial frictions — was the important model to use. As I’ll note below, part of the reason was empirical — the evidenced did matter (though it was not interpreted correctly) — but the bigger problem was that our arrogance caused us to overlook the important questions.
There are many, many “modules” we can plug into a model to make it do various things. Need to propagate a shock, i.e. make it persist over time? Toss in an adjustment cost of some sort (there are other ways to do this as well). Do you need changes in monetary policy to affect real output? Insert a price, wage, or information friction. And so on.
Unfortunately, adding every possible complication to make one grand model that explains everything is way too hard and complex. That’s not possible. Instead, depending upon the questions we ask, we put these pieces together in particular ways to isolate the important relationships, and ignore the more trivial ones. This is the art of model building, to isolate what is important and provide insight into the question of interest.
We could have put the model described above together before the crisis, all of the pieces were there, and some people did things along these lines. But this was not the model most people used. Why? Because we didn’t think the question was important. We didn’t think that financial frictions were an important feature of modern business cycles because technology and deregulation had mostly solved this problem. If the banking system couldn’t collapse, why build and emphasize models that say it will? (The empirical evidence for the financial frictions channel was a bit wobbly, and that was also part of the reason these models were not emphasized. But that evidence was based upon normal times, not deep recessions, and it didn’t tell us as much as we thought about the usefulness of models that incorporate financial frictions.)
Ex-post, it’s easy to look back and say aha — this was the model that would have worked. Ex-ante, the problem is much harder. Will the next big recession be driven by a financial collapse? If so, then a model like this might be useful. But what if the shock comes from some other source? Is that shock in the model? When the time comes, will we be asking the right questions, and hence building models that can help to answer them, or will we be focused on the wrong thing — fighting the last war? We have the tools and techniques to build all sorts of models, but they won’t do us much good if we aren’t asking the right questions.
How do we do that? We must have a strong sense of history, I think, at a minimum be able to look back and understand how various economic downturns happened and be sure those “modules” are in the baseline model. And we also need to have the humility to understand that we probably haven’t progressed so much that it (e.g. a financial collapse) can’t happen again. History alone is not enough, of course, new things can always happen — things where history provides little guidance — but we should at least incorporate things we know can be problematic.
It wasn’t our tools and techniques that failed us prior to the Great Recession. It was our arrogance, our belief that we had solved the problem of financial meltdowns through financial innovation, deregulation, and the like that closed our eyes to the important questions we should have been asking. We are asking them now, but is that enough? What else should we be asking?
This piece is cross-posted from Economist’s View with permission.