09-19-16

Methodology Specifics

I want to follow up on my comments about Paul Romer’s interesting recent piece by being more precise about how I believe macroeconomic research could be improved.

Macro papers typically proceed as follows:

1. Question stated.

2. Some reduced form analysis to "motivate" the question/answer.

3. Question inputted into model. Model is a close variant of prior models grounded in four or five 1980s frameworks. The variant is

generally based on introspection combined with some calibration of relevant parameters.

4. Answer reported.

The problem is that the prior models have a host of key behavioral assumptions that have little or no empirical grounding. In this pdf, I describe one such behavioral assumption in some detail: the response of current consumption to persistent interest rate changes.

But there are many other such assumptions embedded in our models. For example, most macroeconomists study questions that depend crucially on how agents form expectations about the future. However, relatively few papers use evidence of any kind to inform their modeling of expectations formation. (And no, it’s not enough to say that Tom Sargent studied the consequences of one particular kind of learning in the late 1980s!) The point is that if your paper poses a question that depends on how agents form expectations, you should provide evidence from experimental or micro-econometric sources to justify your approach to expectation formation in your particular context.

So, I suggest the following would be a better approach:

1. Question

2. Thorough theoretical analysis of key mechanisms/responses that are likely to inform answer to question (perhaps via "toy" models?)

3. Find evidence for ranges of magnitudes of relevant mechanisms/responses.

4. Build and evaluate a range of models informed by this evidence. (Identification limitations are likely to mean that, given available data, there is a range of models that will be relevant in addressing most questions.)

5. Range of answers to (1), given (4).

Should all this be done in one paper? Probably not. I suspect that we need a more collaborative approach to our questions - a team works on (2), another team works on (3), a third team works on (4) and we arrive at (5). I could readily see each step as being viewed as valuable contributions to economic science.

In terms of (3) - evidence - our micro colleagues can be a great source on this dimension. In my view, the most useful labor supply paper for macroeconomists in the past thirty years is this one - and it’s not written by a macroeconomist.

(If people know of existing papers that follow this approach, feel free to email me a reference at nkocherl@ur.rochester.edu.)

None of these ideas are original to me. They were actually exposited nearly forty years ago.

The central idea is that individual responses can be documented relatively cheaply, occasionally by direct experimentation, but more commonly by means of the vast number of well-documented instances of individual reactions to well-specified environmental changes made available "naturally" via censuses, panels, other surveys, and the (inappropriately maligned as "casual empiricism") method of keeping one's eyes open.

I’m not totally on board with the author in what he says here. I'm a lot less enthralled by the value of “casual empiricism” in a world in which most macroeconomists mainly spend their time with other economists, but otherwise agree wholeheartedly with these words. And I probably see more of a role for direct experimentation than the author does. But those are both quibbles.

And these words from the same article seem even more apt:

Researchers … will appreciate the extent to which … [this agenda] describes hopes for the future, not past accomplishments. These hopes might, without strain, be described as hopes for a kind of unification, not dissimilar in spirit from the hope for unification which informed the neoclassical synthesis. What I have tried to do above is to stress the empirical (as opposed to the aesthetic) character of these hopes, to try to understand how such quantitative evidence about behavior as we may reasonably expect to obtain in society as it now exists might conceivably be transformed into quantitative information about the behavior of imagined societies, different in important ways from any which have ever existed. This may seem an intimidatingly ambitious way to state the goal of an applied subfield of a marginally respectable science, but is there a less ambitious way of describing the goal of business cycle theory?

Somehow, macroeconomists have gotten derailed from this vision of a micro-founded unification and retreated into a hermetically sealed world, where past papers rely on prior papers' flawed foundations. We need to get back to the ambitious agenda that Robert Lucas put before us so many years ago.

(I admit that I'm cherry-picking like crazy from Lucas' 1980 classic JMCB piece. For example, one of Lucas' main points in that article was that he distrusted disequilibrium modeling approaches because they gave rise to too many free parameters. I don't find that argument all that relevant in 2016 - I think that we know more now than in 1980 about how micro-data can be fruitfully used to discipline our modeling of firm behavior. And I would suspect that Lucas would be less than fully supportive of what I write about expectations - but I still think I'm right!)

N. Kocherlakota

Rochester, NY

September 19, 2016