Suppose you believe in theory X. You want to do research in theory X. But all the interesting ideas in theory X have already been well-researched. You can't think of anything interesting and new to say about theory X. There might be some unresolved problems in theory X that need to be tackled. But you can't think of any way to tackle them.
Then theory Y suddenly appears. Theory Y is new, and has lots of unexplored areas that you have the skills to work on. You don't believe in theory Y, but you could make a useful contribution to theory Y in your research.
What would you do?
If you are an ambitious economist, especially an ambitious young economist who needs a thesis topic or publications, you would have a very strong incentive to do your research on theory Y. Even if you weren't ambitious, and just needed something to work on to stay busy, or needed to publish anything to stay respectable, you would have an incentive to work on theory Y.
And it's not necessarily always a bad thing that economists might have an incentive to do research developing theories they don't personally believe in.
We believe theory X is better than theory Y, but we don't know for certain that X is better than Y. Other people may think the opposite. We might be wrong. Making a contribution to theory Y would be better, in expected value terms, than making no contribution to theory X.
Even if we are absolutely convinced that theory X is better than theory Y, maybe the only way to convince others that theory Y is a dead end is to join them in developing theory Y to its conclusion. So that everyone else learns it is a dead end, and we can post a big sign at the entrance to theory Y telling future economists that they shouldn't waste their time exploring this path, because we have already explored it thoroughly and it leads nowhere.
And who knows, we might even pick up a few clues and techniques along the way to the dead end that could be useful in following other, more promising paths.
What we research, and what we believe, aren't necessarily the same thing. What gets published in the journals is a survey of what we are currently researching. It isn't an accurate survey of what we currently believe. The whole point of a journal is not to publish what everybody already believes. The journals are a map of where we are currently exploring for gold. They are not a map of existing gold deposits. They are not a map of where we think gold might be found in places we can't currently explore.
It's not necessarily wrong to believe in theory X but work on theory Y. But there are three dangers we need to be aware of.
The first danger is that others, seeing us working on theory Y, might mistakenly think we believe in theory Y. They don't realise that the journals are not a survey of what we believe. Or, if you treat them as a survey, they are a very biased survey.
The second danger is that we start to believe in the theories we are working on, just because we are working on them, and making progress. We want to believe that our work and progress in theory Y is useful, and will lead to discovering truth. If we can only hammer nails, we really want to believe that all nails need hammering.
The third danger is that we mislead our students. Graduate students need to be taught about "cutting edge" research. Because that's probably where they too will most profitably be swinging machetes in the near future. We will teach them a lot about theory Y. They will probably be taught by professors who themselves are working on theory Y. Those professors may have succumbed to the second danger. The third danger is that the students may think that theory Y is believed to be best, just because they are being taught it.
I think that real business cycle theory is theory Y.
Update: in response to Frances' comment. What I meant to say is that Real Business cyle theory has been one theory Y over that last few years. It won't always be theory Y in future. There have been other theory Y's in the past. Outside of macroeconomics, there are other theory Y's right now.
Worthwhile Canadian Initiative 
White Rabbit: Again, in defence of RBC: When RBC first started, it was very easy to reject their models. Indeed, the RBC guys were themselves rejecting them. But they kept working away, changing this, changing that, trying (and as far as I know at least partially succeeding) in getting successive models to work better. It is (or, perhaps, has become) more of a research program than a theory.
There are (almost certainly) RBC guys building crashes into their models right now. That’s how it goes.
Plus. look at early Keynesian models, with sticky wages and flexible prices, competitive markets and diminishing returns to labour. They predict counter-cyclical real wages. We knew that was false back in the…1960’s? But instead of rejecting the whole Keynesian research agenda, we kept at it (or, some did).
Kuhn, Lakatos, whoever. We don’t reject a theory just because it’s got a contradiction with some facts. We keep tweaking the theory, and re-checking the facts, or hoping someone will eventually come up with a way to reconcile it. Or, until some better theory comes along.
I wouldn’t call this a problem. I like string theory. To “test” string theory does not mean that you have to see strings, just as discovery of the electron was indirect. It just means that there are specific falsifiable predictions that can be tested. That could be of the form, if you do X, then Y will occur, whereas current theory predicts that Z will occur. There is no a priori reason that the tuple (X,Y) requires a particle accelerator the size of the solar system, as string theory has dualities that relate high energy effects to lower energy effects. I think that string theory, if it comes to be accepted, will be done based on conforming to predictions arising from dualities rather than from direct observation, just as most phenomena are indirectly observed. I’m all for freedom of inquiry. You can’t say that a collider of the size of the solar system is needed. That reveals a lack of imagination.
It only becomes a problem when you start asserting outcomes based on untested theories. That’s when the attraction to elegance becomes harmful. You build bridges that fall down. Physics has a lot of natural immunity to that sort of harm that economics does not. People do build economies that fall down, based on adherence to untested theories, in a way that engineers do not.
Gregory: “Nick, haven’t your missed a fourth danger: that over time Theory X stops being taught by some of the more avid practitioners of Theory Y?”
Hmmmm. Yes. I did miss that. It’s something I hadn’t thought about. I can’t make my mind up about it. Could theory X disappear completely? My immediate hunch is “no”. It will still be taught at undergrad. But maybe it’s a danger if students skip undergrad, and go straight into grad skool? I don’t know. I’m still thinking about that.
RSJ wrote:
Cosmologists are not subject to a 6 sigma threshold either – there’s just so many clusters of galaxies to work with.
I do agree that the statistical nature is not helpful, and I agree with you that most economists do not act in bad faith – the intellectual corruption IMO does not happen at the individual level, it happens at the phase where normally ‘scientific consensus’ forms.
In “non controverial” topics of science consensus forms when new evidence overwhelmingly supports (or undermines) existing theories. (Paradoxially it is not really a scientific process but a social one: people get convinced gradually and new talent choses the proven-reliable theories to work with.)
In “controversial” topics of science effective consensus cannot form, because the social process is corrupted: there’s political polarization with a loud chorus of ‘supporters’ which makes it all too easy for the individual scientist to ‘re-calibrate’ his model with a new dimension of parameters, instead of just conceding that the other model worked better, etc.
There’s also, frankly, enough bad-faith research money that keeps bad science afloat. I don’t think you can call most of the “think-tanks” to be acting in good faith.
Nick Rowe wrote:
Calibration is used widely in science – but at least in physics it’s considered “ugly” because it adds an arbitrary number that is not really intrinsic. Most failed theories of dark energy and dark matter tried to explain away surprising telescope data by modifying existing laws and adding an extra parameter, and calibrating the parameter to the data. The ‘gut response’ to surprising new data is to ‘recalibrate’ – not to re-examine your assumptions.
If there’s two theories, one of which has a ‘magic parameter’, and both fit the data, then by Occam’s Razor we prefer to pick the simpler, non-calibrated one.
Calibration also makes it arguably somewhat easier to engage in pointless or dishonest arguments: if there’s enough parameters then calibration can make pretty much any model fit the data pretty well. The question is, what is the meaning of the parameters and are the parameters fixed? If every new shock in the world needs serious ‘recalibration’ of a model then it’s not really good at prediction, is it?
Nick: You see…the discussion has suddenly turned much more interesting! š In reply, I do not read Krugman’s piece as explaining anything. Perhaps I suffer, as Mark Thoma claims (with some justification) from “Krugman Derangement Syndrome.” I can literally make no sense of the guy, except when I interpret what he says from his obvious political agenda.
Peter Dorman: I offer you this as an example of some people are trying to interpret depression episodes via the lens of RBC theory: http://www.aeaweb.org/articles.php?doi=10.1257/jel.46.3.669
You also ask: That is, are people working on RBC primarily because there are a lot of publishing opportunities in tweaking the model, because of ideological motives (they want to rehabilitate noninterventionist macro), or because they are motivated to actually provide convincing explanations for economic phenomena?
You really need to define what you mean by RBC. I don’t think that (political) ideology has very much to do with anything, as it is easy to construct RBC models with a welfare-enhancing role for government. I think that for the most part, people are just trying the best they can to come up with plausible interpretations of important economic events.
Darren: Always nice to hear from former students.
There’s a tendency for economists to refer to physics when they want to compare themselves to “real” scientists. This makes sense, since there is some overlap between the two populations: a strong orientation to math, a desire to locate laws that reduce the dimensionality of the perceived universe (in economics, with an error term). There is historical borrowing and all the rest.
Nevertheless, the explananda in economics far more closely resemble what biologists and geologists have to cope with. I think a lot could be learned by observing the day to day work of practitioners in these fields. There are moments when a particular theory is hot, and reputations are made by people who add a crucial piece to a model, but most work is object-of-study-driven, and theories are tools. (OK, ambitious researchers dress up essentially descriptive work with hints that their results will alter how theories are understood or what their field of application can be, but this is mostly about merchandising. One of my jobs has been teaching grad students in ecology how to do this.)
White Rabbit; interesting. What you describe is (almost) the exact opposite of what I understood by “calibration” in economics. As I understand it, the ideal of calibration, as used in RBC, is to take all the parameter values from elsewhere (independent sources), so there are no free parameters that can be adjusted to fit the data.
(It may not always live up to that ideal in practice, of course.)
David: It’s possible you have a different understanding of the word “explanation” than I do. Saying that you have a model that would correctly predict a subsequent outcome on the basis of prior data is not explaining by my book. I mean the term in the way it is used by my science colleagues: you show explicitly the process by which the outcome is arrived at. In that respect, I would disagree with Temin’s review: it would be an important contribution to an explanation of the Depression to show how changes in TFP resulted in changes in aggregate output, even if TFP shocks were taken as exogenous. (We might find, of course, that they are ultimately endogenous, but putting a piece of the story in place is a step toward telling the whole story.) But do the contributors to this volume reveal actual mechanisms? Do we see specific productivity shocks working their way through specific markets to, for instance, invalidate specific investment plans? That would be an explanation as I understand it.
Peter: RBC models definitely do have “explanations” in your sense. There is a fully-specified process of how the exogenous shock will affect all the endogenous variables. It’s the same process of all general equilibrium theory. The main strength of RBC is precisely that it does have a fully-specified explanatory process.
I think that’s actually the main attraction of RBC theory to its followers. And the main criticism that they make of people like me is that we don’t have a fully-specified process for price adjustment in our sticky price models.
Nick, there must be something I’m missing here. As I understand it, RBC models (and, as you say, most GE models) do specify a process, and they demonstrate that real world outcomes could have been generated by it (“the data are consistent with”), but what they don’t do is show that the process actually occurred, or that the fingerprints show that the process occurred with a high degree of probability. Am I right here? As I understand it, if, for instance, you had a productivity shock-driven model of the business cycle, and you wanted to say it explained a particular instance, wouldn’t you (according to my definition of “explain”) need to provide the kind of detail I specified in my previous comment? I haven’t seen this in the RBC literature, but I can’t say I follow it religiously, and it’s very possible there are such articles and haven’t seen them.
Peter: ah. I think I see what you mean now. You mean do they trace a very specific shock, to some particular technology, through micro-level markets, following the fingerprints all the way through, in a very detailed reading of the history of a particular episode.
That’s very rare in macro. What comes to mind as closest is the method of Friedman and Schwartz.
“Calibration also makes it arguably somewhat easier to engage in pointless or dishonest arguments: if there’s enough parameters then calibration can make pretty much any model fit the data pretty well. The question is, what is the meaning of the parameters and are the parameters fixed? If every new shock in the world needs serious ‘recalibration’ of a model then it’s not really good at prediction, is it?”-White Rabbit
I agree, but I think any decent model of the economy would have to include parameters that are assigned values based solely on empirical calibration. The way I picture it is that theory lists all of the forces that affect a given event and observation shows us how strong each of them is.
Whatever happened to, “All theories are wrong, but some are useful”?
vimothy: I like that saying. When I said “Suppose you believe in theory X”, you might want to read “Suppose you believe that theory X is useful”. Or, theory X is more useful than theory Y. Of course, you might believe X is more useful than Y for some purposes, but vice versa for others. I didn’t want to get into those complications.
Nick:
I believe you fudge an extremely central point. Namely, by using the phrase “to work on Theory Y,” you elide the difference between advancing a theory you think is wrong, and critiquing that theory.
If you do not believe in a theory, it is still intellectually honest to study it and teach it in order to address your doubts about the theory. My advisor, Miles Kimball, taught me a lot about RBC theory, precisely because much of his research has been devoted to showing that RBC theory does not fit the data.
However, advancing or promulgating a theory about which you have serious doubts is pure intellectual dishonesty. I think Richard Feynman put it best when he said:
“But there is one feature I notice that is generally missing in cargo cult science. That is the idea that we all hope you have learned in studying science in school–we never explicitly say what this is, but just hope that you catch on by all the examples of scientific investigation. It is interesting, therefore, to bring it out now and speak of it explicitly. It’s a kind of scientific integrity, a principle of scientific thought that corresponds to a kind of utter honesty–a kind of leaning over backwards. For example, if you’re doing an experiment, you should report everything that you think might make it invalid–not only what you think is right about it: other causes that could possibly explain your results; and things you thought of that you’ve eliminated by some other experiment, and how they worked–to make sure the other fellow can tell they have been eliminated.
Details that could throw doubt on your interpretation must be given, if you know them. You must do the best you can–if you know anything at all wrong, or possibly wrong–to explain it. If you make a theory, for example, and advertise it, or put it out, then you must also put down all the facts that disagree with it, as well as those that agree with it. There is also a more subtle problem. When you have put a lot of ideas together to make an elaborate theory, you want to make sure, when explaining what it fits, that those things it fits are not just the things that gave you the idea for the theory; but that the finished theory makes something else come out right, in addition.
In summary, the idea is to try to give all of the information to help others to judge the value of your contribution; not just the information that leads to judgment in one particular direction or another.”
I think that the field of economics, which is not culturally steeped in the scientific tradition that took physics centuries to cultivate, and which is plagued by inaccurate data and high causal densities, should be more, not less, careful to cultivate intellectual honesty. I suspect the success of RBC models, in terms of publication and classroom curriculum, as involving gross breaches of intellectual honesty, especially when its leading proponents put “theory ahead of measurement” (http://ideas.repec.org/p/fip/fedmsr/102.html) and view theoretical disagreements through a polemical lens (http://ideas.repec.org/p/nbr/nberwo/2982.html).
I think that your post, while highlighting some of the very real problems created by study of RBC theory, largely ignores this need for intellectual honesty, and the paramount imperative of science to match observable data. RBC matches the observable universe about as well as astrology, yet this fact has done little to dent its prevalence in economics journals. Old Keynesian macro was poor science, but at least it was science.
Noah:
Yep, you ought to give all the relevant information. If you know there’s a potential flaw in your argument, that the careful reader might not figure out (like if some of the rats in your experiment might have cheated on the maze) you should mention it. But this argument cuts both ways.
Here’s a counterexample from physics. According to commenter Thomas on this blog: http://rationalitelimitee.wordpress.com/2010/12/06/faut-il-croire-a-la-theorie-sur-laquelle-on-travaille/
two physicists got the Nobel for proving Big Bang Theory. But they themselves believed (or had believed) in steady state theory. I think that’s good.
Suppose you could solve a math problem that the RBC guys needed to solve but couldn’t solve. Suppose you knew of some evidence that would support RBC theory, that the RBC guys didn’t know about. I say it would be quite OK for you to publish that math result or that evidence. I would go further, and say you should do it (or, at least, tell the RBC guys about it so they can publish it).
You could also publish it yourself, but add a disclaimer saying you don’t believe in RBC theory. But then, the evidence ought to be what matters, not what we believe.
Very Interesting discussion. On Harry Johnson, I’m not sure what he said about monetarism, but he whittled as a hobby. He would whittle little elephants and place them in a line with the trunk of each elephant but the first wrapped around the tail of the elephant preceding him in the line. His title for this ongoing sculpture was “The Chicago School of Economics.”
Feynman is not describing actual behavior among the hard scientists — he’s describing a fabled ideal.
There’s a literature on this.
Arnold Kling weighs in:
http://econlog.econlib.org/archives/2010/12/what_was_ration.html
The “Theory X” which isn’t taught is Hayek’s disaggregated monetary / finance explanation of the trade cycle, a modelnwhich rejects a causal explanatory role for pure math equilibrium constructs.
Arnold also notes that what matters is the value of additional research at the margin. That’s an important point I missed. Even if theory A is more promising than theory B, if everyone else is working on theory A, the value marginal product of working on theory B could be higher.
The link to Arnold: http://econlog.econlib.org/archives/2010/12/theory_x.html
“what we believe” is religion. It has nothing to do with science. Economics based on beliefs is religion. There is nothing there to research.
String theory in physics is an attempt to find a unified theory of physics. It is a quest for knowledge and not to satisfy beliefs.
Researchers should believe in what they are doing if they want to go past the limits. Otherwise they are wasting time. Discoveries do not happen only because researchers research and know how to run eviews.
Back to the original question, what I did amounted to pursuing an alternate career path as a programmer. Aside from comments on economics blogs, I make very little use of my graduate training in economics.
I think David gave away the game when he said: “That’s very rare in macro. What comes to mind as closest is the method of Friedman and Schwartz.”
You simply cannot read Friedman and Schwartz and not come away convinced that the Depression was mostly due to really bad monetary policy. It had nothing to do with RBC-style explanations. That’s the sense in which Nick is correct, theory X (Friedman and Schwartz, “money matters”) is clearly correct and RBC theory is just wrong. There was no mass outbreak of laziness, nor were the advanced technologies of 1929 somehow lost in the mists of time.
But, as Nick says, the incentives in the profession are to work on theory Y, or even better, to invent theory Z. For Bernanke, Z was the credit view, and it worked out great for him. He had a great career until he got the chance to put Z into practice. Wall Street was bailed out at great cost to the taxpayer, but the recession goes on. If you want to know what Friedman would have said about that, read what Scott Sumner writes. More than anyone else, I think he comes closer to saying what Friedman would be thinking if he were still around.