Before we get into the back-and-forth, there's the interesting question of who you should believe, an experienced insider or a bomb-throwing outsider. Chris is a successful macroeconomist at an excellent university. I am not a macroeconomist at all; my experience is limited to two years of grad school macro and a number of academic conferences. Insiders tend to be biased, because people go into fields that they enjoy and believe in, and they also have a vested interest in promoting the field. But outsiders tend to be ignorant. So after I respond to Chris' points, I'll bring in a recent critique of macro from an accomplished insider in the field.
Anyway, on to the point-by-point. Chris:
Noah Smith really has it in for macroeconomists.
Shouldn't have assigned so much homework, prof...
Ha. I kid. Actually I do not have it in for macroeconomists. A lot of the economists I admire most are macroeconomists - Markus Brunnermeier, for example, or Martin Eichenbaum, or Ricardo Caballero. Miles Kimball and Mark Thoma and David Andolfatto, who are among my favorite bloggers and are awesome people besides, are macroeconomists. All of my favorite classes at UMich were taught by macroeconomists. I enjoy going to macro conferences much more than I'd enjoy going to a game theory conference or a labor econ conference. There are certain macroeconomists who do annoy me, of course, but that will be true in any field.
What annoys me (warning: pretentious phrasing ahead) is the intellectual culture of macro. Which lots of macroeconomists are working to change from the inside (which of course is more admirable than simply running away and throwing bombs over their shoulder, as I did). By helping to focus popular annoyance away from econ as a whole and toward macro in particular, my hope was to help the internal critics make headway toward reform.
Anyway, back to Chris:
Macro is quite productive and overall quite healthy. There are several distinguishing features of macroeconomics which set it apart from many other areas in economics. In my assessment, along most of these dimensions, macro comes out looking quite good.
First, macroeconomists are constantly comparing models to data...Of course it is a problem that the theories are so soundly rejected...In many other areas in economics the theories aren’t rejected because...the theories simply don’t exist. There are many purely empirical studies in which there is little theory to speak of.
Sorry, but I fail to see why "purely empirical" studies with "little theory to speak of" are worse than "theories [that are] soundly rejected." That just doesn't make any sense to me. What is wrong with looking at the world without first trying to force it into some mental framework that you came up with?
And what are macroeconomists doing with all those rejected theories? Are they throwing them away? Are they keeping them on the shelf in case they're needed? Do people go on believing and using them anyway because they seem cool? (Actually Chris partially answers this later on...)
Also, Chris is overstating his case when he says that macroeconomists are "constantly comparing models to the data". Sometimes these comparisons are not particularly impressive. For example, many macro models are compared with the data by "moment matching", which is just about the lowest possible bar for models to pass. But lots of macro papers are satisfied with "moment matching".
Chris also mentions that in some branches of econ, theories are rarely compared to data. I assume he's talking about pure game theory. But pure game theory is really a branch of mathematics, not an empirical science, so it doesn't need to test itself. Applied game theory is continually tested against data, and many applied game theory models have been so successful that they have found widespread application in industry. And other than pure game theory, I'm pretty sure all branches of econ compare their theories to data.
Back to Chris:
Second, in macroeconomics, there is a constant push to quantify theories. That is, there is always an effort to attach meaningful parameter values to the models...This is again one of the ways in which macro is quite unlike other fields.
So, theories that are "soundly rejected" by data, but which have very well-quantified parameter values? What is the point of precision without accuracy? I mean, it's nice, why not be precise, but what's the point of measuring the 5th decimal place of a parameter that probably doesn't even represent any real thing?
It's kind of like "Oh, if this theory were right, you could boost growth by 1% a year by cutting taxes to 20%, but according to our data this theory is nowhere close to right." So who cares if the 1% number is big? Again, I kind of don't get it.
Back to Chris:
Third, when the models fail (and they always fail eventually), the response of macroeconomists isn’t to simply abandon the model, but rather they highlight the nature of the failure. This is again a good research habit because mistakes and rejections have value – knowing the nature of the mismatch between the model and the data helps you to refine the theory. There are many “puzzles” in macroeconomics (the excess sensitivity puzzle, the risk-free-rate puzzle, the equity premium puzzle, the international comovement puzzles, and so on, …). At a superficial level one might be tempted to conclude that the prevalence of such puzzles shows that the field is in a constant state of disarray. In fact, these mismatches between theory and data serve as an important guide to how to modify the theories.
Ah, so this is what happens to all those theories that don't match the data! They become "puzzles", which then generate more macro papers.
Look, I can make up any number of theories that don't match reality. I can generate "puzzles" for you all day long. For example, my theory is that recessions are caused by a giant flying mongoose named Skippy that appears whenever investment is low and breathes a magic Breath of Sadness that makes people not want to work for a few years (note that this model matches the negative correlation between investment and unemployment). Sadly, we have not yet managed to observe Skippy the Giant Mongoose, but that's OK; we can spend the next ten years of our lives publishing possible solutions to the Mongoose Deficit Puzzle.
Silly. But only silly because Skippy the Mongoose sounds implausible to you. How about the idea that stocks consist of claims on the output of fruit trees that give a random amount of fruit each year in an i.i.d. normal distribution, and that people care only about the amount of fruit they eat each year? That's the setup in the Equity Premium Puzzle. Sounds a bit more plausible than Skippy the Mongoose, I'll grant you, but not necessarily so plausible that its failure to match reality should have been hailed as a great theoretical triumph.
The Equity Premium Puzzle did get a lot of finance people interested in investigating stuff that eventually proved very interesting, I'll grant it that. And it spurred people to think some very deep thoughts. So it is a very important paper. But if all you ever get are puzzles and puzzles and more puzzles, then at some point maybe the real puzzle is why you're still at it.
Finally, back to Chris:
Lastly, unlike many other fields, macroeconomists need to have a wide array of skills and familiarity with many sub-fields of economics. As a group, macroeconomists have knowledge of a wide range of analytical techniques, probably better knowledge of history, and greater familiarity and appreciation of economic institutions than the average economist.
I agree, that is a reason many macroeconomists are awesome.
Anyway, so I think this argument - which, as you might guess, is basically a replay of discussions Chris and I had in his office back in 2007 - pretty clearly demonstrates my problems with the intellectual culture of macro. The Macro Way of Thinking just values stuff that I don't value very much. I guess that's a matter of taste.
But now it's time for me to point out that a number of actual, practicing, successful macroeconomists are saying stuff similar to what I'm saying (though in more upbeat, polite, and constructive ways). For example, Ricardo Caballero of MIT wrote this comment about "Macroeconomics After the Crisis", which I pretty much agree with 100%. The abstract:
In this paper I argue that the current core of macroeconomics—by which I mainly mean the so-called dynamic stochastic general equilibrium approach—has become so mesmerized with its own internal logic that it has begun to confuse the precision it has achieved about its own world with the precision that it has about the real one. This is dangerous for both methodological and policy reasons. On the methodology front, macroeconomic research has been in “fine-tuning” mode within the local-maximum of the dynamic stochastic general equilibrium world, when we should be in “broad-exploration” mode. We are too far from absolute truth to be so specialized and to make the kind of confident quantitative claims that often emerge from the core. On the policy front, this confused precision creates the illusion that a minor adjustment in the standard policy framework will prevent future crises, and by doing so it leaves us overly exposed to the new and unexpected.
And an excerpt:
To be fair to our field, an enormous amount of work at the intersection of macroeconomics and corporate finance has been chasing many of the issues that played a central role during the current crisis, including liquidity evaporation, collateral shortages, bubbles, crises, panics, fire sales, risk-shifting, contagion, and the like. However, much of this literature belongs to the periphery of macroeconomics rather than to its core...The dynamic stochastic general equilibrium strategy is so attractive, and even plain addictive, because it allows one to generate impulse responses that can be fully described in terms of seemingly scientific statements. The model is an irresistible snake-charmer. In contrast, the periphery is not nearly as ambitious, and it provides mostly qualitative insights. So we are left with the tension between a type of answer to which we aspire but that has limited connection with reality (the core) and more sensible but incomplete answers (the periphery).
Caballero is describing the "precision without accuracy" problem. Macro's current culture values very precise, detailed, deep knowledge about models that have so far given us no reason to believe in them. But that knowledge is not likely to ever be valuable to people outside the field.
(His proposed solution - that macroeconomic theorists should focus more on picking away at the problem, understanding macro-relevant "microeconomic" phenomena instead of trying to swallow the whole business cycle in one big arrogant gulp - seems right to me too. But that is a topic for another post.)
Anyway, so if you really want a critic of macro who is an eminent macroeconomist rather than a disgruntled bomb-thrower who quit the field after two and a half years of grad school, go read Caballero.