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 
There is one feedback mechanism, if the research is not useful, it is not read, hence a useless theory may not do much harm when published.
Sometimes I wonder if economics as a whole is theory Y.
Sometimes I wonder if economics as a whole is theory Y.
You are not alone. “The purpose of studying economics is not to acquire a set of ready-made answers to economic questions, but to learn how to avoid being deceived by economists.” Matt Yglesias is doing better economics blogging than most blogging economists. I suspect this is partly because philosophy students are not so likely to assume that currently fashionable ideas are necessarily better than those of the ancients.
I also think people don’t appreciate the extent to which “rival theories” in economics don’t conflict as much as we like to pretend they do – they simply describe different economic processes that operate at some times and don’t operate at other times.
Tom Sargent’s recent interview… I think by the Minneapolis Fed… highlights this nicely. He says emphatically that RE/RBC was simply not intended to deal with crises like this one and that people are wrong to act like it was. Now – Sargent may be wise enough to make this decision, but as you note, others aren’t.
I personally feel a Keyenesianish approach is – as Keynes noted – a quite “general theory” that can be accomodated to a lot of what we see. I don’t think that makes non-Keynesian theories wrong or even rival. I just think of them as various “special theories” of the economy that may or may not apply in certain situations. I think we do ourselves a real disservice as science to tear ourselves apart over these theoretical rivalries.
I was figuring Theory Y was going to the newest trendy thing, e.g. behavioural economics, explaining economic growth using European settler mortality rates circa 1500.
What is the nature of belief? For example, I believe in rational choice theory, which means I think it’s mostly a sort of useful approximation that isn’t always literally true. Now that’s a kind of weaselly position because it’s not falsifiable – even if lots of people act irrationally, rational choice theory can still be a sort of useful approximation.
This sounds a bit like Daniel’s position, too.
Believing, or just suspending disbelief?
Matt: eventually yes. But maybe only when theory Y has run its course, and nobody can think up anything new and interesting to add to theory Y. But not if you are looking for a PhD thesis topic, and Theory Y is still running.
Sina: Hey! Young people aren’t supposed to be that cynical! You must be doing too much math!
But yes. But then maybe all disciplines are theory Y too. It does make sense to look for your keys under the lamp post, if you have no idea where you lost them. And anyway, truth is not like a set of keys. It’s not all just in one place.
But you can’t really talk about whether a theory is theory Y except relative to theory X. So it’s a bit problematic to say that all of economics is theory Y.
Kevin: yep. Any philosophy student knows that philosophers have driven round the block a few times over the years. I expect that’s one of the advantages of learning some history of economic thought, as well. Even if you remember nothing else, you ought to remember that intelligent economists have believed many different things in the past. Theories come and go, and sometimes come back again.
Daniel: Yep. Sargent really went up in my estimation on reading that interview. And similarly, on reading Lucas’ thoughts years ago, I learned that Lucas is much wiser than simply reading Lucasian economics would lead you to believe (which is not to deny the brilliance of some of the latter’s insights). What gets published in the journals isn’t the sum total of what guys like that believe. It’s just what they have been working on. Which is different. But their followers might not realise that.
I should also add that when I first saw RBC theory, I thought it was ridiculous. I had just read Haberler’s Prosperity and Depression at the time http://mises.org/resources/4617 . Haberler, IIRC, starts out by saying “Sure, we know that a bad harvest can lead to a drop in GDP, but that’s not what we mean by a recession”. But over the years, I have to admit that RBC economists have been working hard, with some success, to try to get the theory to fit the facts, and to check it against the facts. I still don’t believe it, but it’s not as ridiculous as I once thought it was. And there’s gotta be some truth in it.
Frances: I had RBC theory in mind as theory Y. For macroeconomists of my vintage, it works well as theory Y. For an earlier vintage, I think Keynesian economics was a bit theory Yish. Outside of macro, there are loads of other theory Y’s.
We ought to be weasels, a bit. I don’t see any sensible alternative. The only alternative is to be a nut who thinks he has found the truth, the whole truth, and nothing but the truth.
I’m also trying to remember what Harry Johnson said about Monetarism, decades ago. I think one of the things he said was that successful research programs have lots of little problems, just hard enough to challenge the grad students, but easy enough to solve.
I am not in macro but in my field I can always find a theory z that I believe more than y.
or I can do some smaller contribution to x but answer a smaller question that I find interesting and get a decent publication out of it.
pat: but is there never a trade-off between what you believe and what you can make a contribution in? Sometimes there isn’t, sure. Which makes life easy. But sometimes there is. And when you get that trade-off, there is a theory X and a theory Y.
Nick:
it happens but I usually have very little motivation working in something I dont believe in. For me it is not the best thing to do.
Another point: it is really not optimal that people work in Y…
Just an example from another field.
For micro theory by example, I think it might be why the JET crowd is doing so well. People get math, math has very little flaws so even if people solve question with very little econ value but with a lot of math value it will get published very well. Even if the math is not generalisable to other problem…
Or the problem is solved under 1000 hypothesis.
Nick –
This “we’re talking about different economic processses, not different schools of thought” thing has been bothering me a lot recently, and so I’ve written about it in several places. You might be interested in these:
– http://factsandotherstubbornthings.blogspot.com/2010/12/if-biology-had-schools-of-thought-like.html
– http://factsandotherstubbornthings.blogspot.com/2010/12/keyneso-austrianism-and-steve-waldman.html
– http://factsandotherstubbornthings.blogspot.com/2010/11/practice-of-macroeconomics-few-rules.html
“Sometimes I wonder if economics as a whole is theory Y.
You are not alone. “The purpose of studying economics is not to acquire a set of ready-made answers to economic questions, but to learn how to avoid being deceived by economists.” agreed! or at least i agree about mainstream economics…
i also really want to second Nick about learning history of economic thought. it is soooooo useful to understanding where ideas come from. even more then that… reading the books yourself! i’ve read keynes’ general theory, minsky’s stabilizing an unstable economy (and john maynard keynes) Galbraith’s the great crash and i’m in the middle of reading the wealth of nations and das kapital. i think these readings have really informed my opinions of modern economics much more then anything else could.
Nick, when I first learned basic RBC, my first reaction was “that sounds really stupid.” Which is another way of saying that I didn’t believe it.
But in our discipline, “I don’t believe the basic assumptions underpinning your model” isn’t considered to be a very sophisticated or intelligent way of criticizing an argument (although it’s an improvement over “that’s stupid”).
You know the rest of the point that I’m going to make – papers are judged more by technique than by content etc.
So it’s not just that people choose strategically to work on Y. It’s that a discussion on the believability of X and Y – like a discussion of the relative merits of alternative religious beliefs – isn’t really acceptable in polite academic circles.
Frances: I completly agree
Consider.
Theory X is accepted, powerful, yet has deeply abstract, deeply difficult mostly NON-MATHEMATICAL conceptual pathologies which need sorting out — you could spend years and make only small progress, of a kind difficult to explain to others working mostly on empirical and statistical issues.
There are masses of endless empirical and statistical studies related to Theory X, and there are all sorts of relatively easily engineered and hypothetically related math constructs available to build and publish in the journals.
What do graduate students and tenure track professors choose to work on? After 20-30 years working on these low hanging fruit, what chance will these people have of taking up the big problems?
What I’ve just describes is the field of Darwinian biology.
Ernst Mayr and a few other top biologists worked on the deep issues in the last 2 or 3 decades. Most others never even try.
Biologists 15 years or so ago even set up a committee to try to help correct the problem — no one was working on fixing the global Darwinian explanatory framework — everyone was doing empirical work or math.
So who does the hard stuff? Philosophers of biology like David Hull, who is working on making sense of the species concept, and Alex Rosenberg, who is working on making sense of how the Darwinian paradigm fits with the micro-biological revolution.
Every journalist should be made to read this post, because — amongst other things — it’s why most science journalism sucks. Most interesting new papers in medicine, for instance, are wrong ( http://www.newscientist.com/article/dn7915–most-scientific-papers-are-probably-wrong.html ), largely because one leading cause of a result being surprising is it simply not being true. The only results worth disseminating outside of the field, much less to the public, are those which have survived several years of scrutiny and follow-up work.
The way to make your reputation in philosophy is to produce a result which is absurd on its face using a set of premises which others use only because they create endless journal articles.
And you’d be amazed how many philosophers will eat the absurd conclusion in order to hang on to the premises that support the publish or perish game.
Example — the work of David Lewis on semantics.
“The way to make your reputation in philosophy is to produce a result which is absurd on its face using a set of premises which others use only because they create endless journal articles.
And you’d be amazed how many philosophers will eat the absurd conclusion in order to hang on to the premises that support the publish or perish game.”
This is a great discussion, and I think it is a pretty accurate description of the way career incentives play out in economic research. Nevertheless, I also think it is symptomatic of a deeper problem with economics relative to the “real” sciences.
In most fields of science, researchers want to explain things. They are looking for the mechanisms by which observed outcomes arise. A theory can be largely “figured out” but still contribute mightily to research as more and more observed phenomena are subjected to it. Very few biologists, for instance, see themselves as “working on theory”, although (of course) biological theory continues to be developed. The bulk of the work is explaining how things work, and there are a lot of things out there (or in there if you happen to be a biologist). The fetish with prediction, the notion that a “good” theory is one that generates a single, falsifiable prediction in a given context, shifts the balance of theory work in directions that have little to do with the research most scientists do. (This sort-of-Popperian approach makes sense in adjudicating rival theories, but such adjudication is not the main activity in most sciences.) The result is that you get the pattern Nick describes in economics, but what governs the use of theories in the scientific literature is how successful they are in generating explanations.
The second big problem is the lack of serious concern for Type I error. Most protocols in empirical economics are conditional: if my model is correct, and if we can make some additional assumptions that people like me have been willing to swallow, I can test for whether I can reject the null hypothesis that my prediction is totally false. Even worse is calibration: the test is whether I can find a set a parameters under which my model can survive an encounter with a data set. This approach has almost nothing to do with rooting out Type I error as most scientists understand it. Theories with a high probability of being false can survive decade after decade in economics, because the protocols are so intrinsically weak. Only now, with the rise of experimental and quasi-experimental methods, is there the appearance of a critical test from time to time, and even so most economists do not recognize the difference between such tests and their normal empirical work.
I don’t want to romanticize science. Theories do blow hot and cold in most disciplines for careerist reasons, and there is a lot of dubious stuff that gets published in the first efflorescence of a new research program, but the process is constrained by a serious commitment to minimizing Type I error over time. People who say something is true when it is later shown to be false suffer large career consequences in the scientific world. Can you say this about economics?
Peter: “People who say something is true when it is later shown to be false suffer large career consequences in the scientific world. Can you say this about economics?”
God, I hope not, or we would all be scr***d!
More seriously, we don’t want to penalise people for trying out new theories. And we don’t want to increase the incentives for people to do anything to defend failing theories to the death. It’s much better if we all just recognise the distinction between what ideas are worth working on and what ideas are probably true.
Yep. This discussion is going really well. I have little to add. I’m just going to let it run.
Peter: “People who say something is true when it is later shown to be false suffer large career consequences in the scientific world. Can you say this about economics?”
No, see my post on missing women and hepatitis b.
In that post, I argue that journals should publish errata notices along the lines of “this research was subsequently found to be wrong.” In the case of missing women and hepatitis B, there is a possibility of the research doing real harm, by drawing attention away from the economic and social causes of China’s gender imbalance.
Would the economics community actually be able to reach a consensus on which ideas had been disproved?
But in our discipline, “I don’t believe the basic assumptions underpinning your model” isn’t considered to be a very sophisticated or intelligent way of criticizing an argument (although it’s an improvement over “that’s stupid”).-Frances
I think there’s a good reason for that. You explained it when giving your thoughts on rational choice theory. The value of an economic theory/model is not determined solely by that accuracy of its underlying assumptions.
The models have consequences. If economists made no policy recommendations, and offered no pronouncements about the effects of economic policies, then these arguments would have a lot more force.
The abandonment of fiscal policy as a demand management tool has real effects, in terms of millions of unemployed people. When a philosopher decides to publish a counterintuitive result based on somewhat implausible assumptions, then that’s one thing. But when economists take crowding out arguments based on implausible assumptions seriously, then that’s another matter — the economy remains mired in a slump for much longer than is necessary. So a simple little fudge, such as assuming that government debt must be zero in long run equilibrium, though it might make solving the model easier, ends up contributing the depravation of millions of people, if your conclusion can shift the conventional wisdom into believing that fiscal policy is ineffective.
At that point, you can’t defend a certain theory purely on grounds of intellectual curiosity, as this debate is not happening in isolation of the political debates.
Economics is constrained in a way that philosophy is not.
That’s why Samuelson was under political pressure to not include too many Keynesian effects when publishing his textbook. That’s why the census bureau stopped collecting input/output data in the 1950s, as this was seen as too “Soviet”. There is and has always been lots of political pressure in this field, going back to the very beginning; pretending that we are just talking about curious people following their own idiosyncratic research paths is not an honest description of what’s happening, although it may be an honest description of the experience of a single researcher.
A slow day, Nick?
What if I told you that in my view, Y = the incoherent, static, reduced-form macro models of the 1950s and 1960s? I could blog about it, but what would be the point? You have your Y (or is it Krugman’s Y?) and I have my Y. And the point of this is?
PS. Your link to the Krugman article needs to be fixed.
Andolfatto charms us all yet again.
Patrick: Twas the rum speaking, not I! 🙂
actually david, that was a comemnt a la Krugman…
Good old Max Weber started the the model building faze of modern economics rolling with his ideal types. Types that he called fiction.
Economist should keep in mind that their models are fictionalized representations of reality. There is no absolute truth in economics. The best that economist can hope for in their models is an approximate representation of an ever changing and complex reality.
For instance Larry Summers thought that a cataclysmic unraveling of the financial sector was unlikely because that community had achieved a wider risk sharing, but it was this wider risk sharing that caused the whole system to implode in upon itself. Not a very good approximation of reality.
David: different people believe in different theories. That’s OK. Some people believe RBC is the better theory. That’s OK. We can argue about that. But that’s not the point of this post. I’m talking about the incentives to do work on a theory, whether or not one believes it. When RBC theory first came out, there were a lot of incentives to work on it. A lot of areas within RBC theory hadn’t been explored, and could be explored. So people explored them. I’m not even saying it’s bad that people explored them.
RSJ: “At that point, you can’t defend a certain theory purely on grounds of intellectual curiosity, as this debate is not happening in isolation of the political debates.”
You most certainly can defend a theory on the grounds of intellectual curiosity. And we can learn a lot from e.g. counterfactuals, like the Modigliani-Miller theorem. And if you really want to understand whether and under what conditions fiscal policy works, you had better understand the Ricardian Equivalence Theorem too.
The solution is not to ban intellectual curiosity. And certainly not to have some sort of political oversight committee, even if it exists only in our own minds. The solution is to be much clearer about the distinction between what we are working on and what we believe. We shouldn’t be wedded to our theories.
Models are just models. It takes judgment to decide which model to use where.
Must try to fix link to Krugman, but I’m not home right now, and I’m working on a borrowed computer.
If theory ‘Y’ is the real business cycle model then the choice is not really between a “well established” and a “new/underdeveloped” field of research – but the choice is whether to work on and support a theory that has been demonstrated to be wrong and false, because it’s based on invalid assumptions – as your instincts are telling it you already.
By doing that you would actually hinder scientific progress, for the sake of a better career position. No doubt it is a working business model that many are using, just make sure you are aware of that and make sure that you don’t consider yourself a scientist after that point.
In other words, working on something that’s been proven factually wrong in the past, with the goal of ‘advancing’ it against other, better working theories – while from the very beginning having the impression that the basic assumptions of RBC are unfixably wrong (which they are IMO), is as anti-science as it gets.
You can do more interesting and more useful things than to work with bogus models.
For example there’s a marked lack of agent based models that actually work in practice and which converge to mainstream macro models.
When it comes to economic forecast we are still in the dark ages, compared to other sciences.
Well, supposing that theory Y and X have some different implications, there is whole lot of work to figure out where the data support Y or X, how important this is, and how Y (or X) can be adapted to deal with anomalies. (cf. Keynesian => RBC => NKE) You say it as if there is no talking possible between X and Y, and while for some people that is a correct statement, this is not true overall.
So, I consider this X or Y choice a strawman.
What we are talking about here is the politics of a science, not the science itself. Virtually every science has its politics, and the politics often control the direction that the science takes over a considerable period. That is why significant change must sometimes wait for a new generation, since politics equals power and is dominated by those with the greatest influence and strong vested interest.
Nick,
I’m sorry, but this post just rubs me the wrong way, and in every which way possible! To be fair, you begin with a given supposition: suppose you believe theory X, but are somehow drawn to do work in theory Y. As a young researcher, you somehow already “believe” in theory X. Evidently, there is nothing much left to learn about theory X, but you really want to work on it anyway. And then you hear the siren call of theory Y. You don’t “believe” in theory Y. But you work on it anyway, since evidently there is much to explore about the nature of this theory.
But this is a rather strange and unfamiliar story, in my view.
Who actually “believes” in a theory? When I first started working on RBC theory, I did not “believe” in it. Nor did I “believe” in any of the theories that preceeded or coexisted with it. Theory, in my view, constitutes a body of tentative hypotheses (assumptions) leading to a set of conclusions (predictions) via a mapping of deductive logic. What does it mean to “believe” or “not believe” in such objects? We are supposed to be scientists, not priests. What sort of scientist says to him or herself “I really believe in X, and I don’t believe in Y–even though I haven’t really explored Y that much.” Really?
And then you go and associate Y with RBC theory, linking to Krugman’s foolish post asserting that “RBC theory is wrong.” Krugman is clueless. Nay, beyond clueless…I would say, appallingly ignorant, especially with respect to the body of macroeconomic research produced since 1982.
What is “RBC theory” anyway? I suspect that when most people think of “RBC theory,” they are thinking of maximizing agents operating in a world of complete markets where the primary impulse mechanism constitutes a random arrival of events that alter the economy’s production possibilities frontier (e.g., technology shocks).
Is RBC theory, in the narrow way I just defined, “wrong?” What does one mean by “wrong?” Bad assumptions? Bad predictions? Implausible interpretations? Or is the theory “correct” in the sense that it appears to offer a plausible interpretation of the forces behind at least some component of the business cycle (certainly consistent with Schumpeter, and Robertson before him)?
Of course, RBC theory has evolved far beyond the narrow characterization I described above. Distortionary taxes, externalities, search frictions, heterogeneous agents, financial market imperfections, etc., etc. etc. Not that Krugman has ever acknowledged this.
But the lasting legacy of RBC theory extends, I think, beyond any specific model. RBC theory, more than anything else, represents a methodological approach to understanding or interpreting aggregate phenomena. It is a method that accommodates many different schools of thought. Indeed, I believe that it may even accommodate behavioralists, since any given behavioral rule can be thought of as the solution to a highly constrained problem (e.g., a decision-making unit constrained in information processing).
So there you have it, a few Sunday morning thoughts. I realize that your post has more to do with the incentives to do research. But then, if so, there would have been no need for you to take that gratuitous swipe at RBC theory and then link up to a foolish Krugman post.
David: So in your world, being rational scientists, we all come to the field with the same vague prior. We all envision the same set of all possible worlds, i.e. our priors have the same support. And we have the same measure.
If this was physics, it wouldn’t matter that much which vague prior you start with. But the system being enormously chaotic, the measurements being few and abysmal, and experiments being next to impossible to construct, the choice of prior is everything. That’s why we disagree.
David: when RBC theory first appeared, it was complete markets and technology shocks etc. Yes, it has changed a lot since.
We don’t (or shouldn’t) believe that any theory is the truth, whole truth, nothing but the truth, with 100% certainty. (Nor, as some above seem to think, that any theory is 100% conclusively false, etc.). But we do have beliefs about which theory comes closer, or is better than another theory.
For economists of my vintage, RBC fits what I’m saying. I think people worked on it because there was stuff to be done. I don’t think everybody worked on it because they thought “I believe RBC more than other theories”. Your description of your own experience does not, so far, contradict my hypothesis.
My guess is that in the 1940’s some economists started work on Keynesian macro, for the same reason. Because there was stuff to be done. It was theory Y.
I linked to PK’s post precisely because I am giving a different interpretation than he is. He gives his explanation of the rise of RBC/equilibrium BC theory; I give mine. Which do you prefer? Or do you have a third explanation?
Italics fixed.
can’t get rid of these italics!
Economic italicisation
Italics fixed – White rabbit left a tag open.
As a causal science providing sound causal explanation of design-like order, there is nothing “fictional” about the central causal components of the science — entrepreneurial learning in the context of changing relative prices and local conditions, systematically shaped by the logical structure of marginal valuation.
Economists has got to stop being truly pathetically horrible philosophers right at the core of their “science” with all other there instrumentalism and “its all false but lets it lets us make scientific predictions” stuff.
Get the foundations right, get the explanatory strategy right, and you can abandon the bad philosophy — and stop being in the first instance bad philosophers rather than good scientists.
Even in macroeconomics we can identify sound causal facts and structure — unsustainable structures of malinvestment, changes in monetary demand and velocity, mismatches between consumption and production plans across time — which are causal features of the world and have nothing “fictional” about them.
The “precision” and mathematical tractability of the “models” is a bogus precision, and a bogus standard of “scientific” validity.
And I think Nick is right about what is driving all this — and it ain’t the demands of “science” or explanatory success.
Nick @8:35
I agree, but I’m saying you can’t have it both ways.
Mathematicians can have any priors that they want and are only bound by logical consistency. All that matters is their proofs. An elegant proof is rewarded.
Physicists can pick any prior that they want, if their conclusions are backed by rock-solid empirical support in the form of reproducible experiments. But economists are not mathematicians or physicists, they are social scientists. They can’t get rock solid empirical support and they can’t do falsifiable hypotheses, since the field is filled with limited data and observational equivalences.
In that case, they are constrained by the plausibility of their priors in a way that mathematicians or physicists are not.
The problem is in operating as if they were mathematicians, and having the influence of physicists (i.e. if you do X, then Y will occur).
Ricardian equivalence was not adopted because of strong empirical support in the same way that General relativity has been adopted. Neither was CAPM, or the Expectations Hypothesis, or RatEx. All of these were adopted in spite of the evidence, not because of it. They were adopted because the elegance of the result outweighed the lack of data for the hypothesis. This resistance to data is why it takes a complete and public failure such as a global depression in order to get economics to abandon elegant results. And even then, the results are not really abandoned, and as soon as the depression fades from memory, the elegant results are believed again.
And if that’s the mode in which you want to operate — i.e. as mathematicians — then you cannot give policy advice, or pretend that what you are studying is the actual economy.
But given that economists will be giving policy advice and they are studying the actual economy, then it means you have to have less freedom than mathematicians or physicists in picking your priors, and more self-discipline in terms of not taking the results too seriously when giving policy advice.
David: Can you provide an example or two of specific economic episodes for which RBC (in any flavor) supplied an important part of the explanation? I’m thinking of a particular macroeconomic event which researchers sought to understand, and where RBC was part of the “aha” moment. As a well-known exemplar, I offer the late-30s dip in US output, which is generally seen as reflective of a Keynesian fiscal mechanism. Needless to say, “explanation” is a rather higher bar than “is consistent with”.
I don’t mean this rhetorically. I think economics suffers from insufficient tools of explanation, and if RBC can do the job in some contexts, fine.
Also, I don’t mean to be getting off on the what-do-you-think-about-RBC tangent. My question is intended to be in the spirit of this thread. 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?
This sounds nice and plausible, but it’s a myth …
Firstly, a lot of physics is statistical in nature. In fact most of modern physics is that – and often involves processes that are a lot less observable than economic processes …
Secondly, the problem with economics is not that there’s not enough good data to build good theories. The problem is not that there are no good scientists or that there are no good predictions.
The problem is that while in physics there’s little interest in misinterpreting measurements of the Higgs boson or misinterpreting the results of cosmological models, in economics there’s a lot of vested interest in “misinterpreting” economic and social processes for political gains.
This kind of conflict of interest poisons economics the same way politics poisons climate research. Those who have no interest in finding scientific truth can easily create the appearance of truth, and given big enough research grants there will always be people who follow those false leads. The “general public” is not a scientist to decide one way or another so outstanding doubts will never be settled in a satisfactory way.
If you want to know which economic models are good, just follow the money and see what models the big investment houses are running.
White Rabbit,
re: physics, all I can say is that I disagree. Getting a 6-sigma evidence for a new particle is fairly robust evidence, in my view. Statistical evidence is also evidence. You can argue that string theory is popular because of mathematical elegance, and I would agree. But at the same time, you do not see the standard model being adjusted until the data comes out. So here is an example of a popular research program, in which everyone agrees that the standard model is just an effective theory, but people are not yet drawing conclusions in terms of claiming to be able to predict outcomes until they get robust data. There is a large sense that “we don’t know”. I once attended one a conference in which mathematicians and physicists got together and Ed Witten spent a good chunk of the time explaining that we don’t yet know understand string theory. That’s a constraint that requiring data imposes on you.
But economists are claiming to predict the validity of fiscal stimulus without data.
As to your political poisoning observation, I don’t think that economists generally act in bad faith. They are enchanted by elegance in the same way that string theorists are, but unlike the string theorists, they can’t collect peta-bytes of data in particle accelerators, or from satellites and so they just start making predictions about economic policies based on the elegance of the argument. They are not subject to a 6 sigma threshold before announcing the discovery of a new particle. The elegance of the argument is enough to convince them of the existence of the effect, unfortunately.
David: “Who actually “believes” in a theory?”
In my view, this is a naive view of how most researchers actually think, and indeed, of the reasons that people choose to become researchers in a particular field to start with. Even before future academics taking their first courses become familiar with the weight of evidence (or lack thereof) supporting economic theory, they find the prevailing methodology and assumptions of a field attractive and plausible, something they’d like to spend their lives working on. Those who don’t major in something else. And within their field, they will find some theories, some “stories” about how the economy works, more attractive and plausible than others. Hence comes ‘Theory X’ and ‘Theory Y’.
As an aside, I am one of David’s former students in his intermediate macro class at SFU, and David’s approach to teaching intermediate macro was (as you’d guess) a radical departure from the usual IS/LM approach. It really opened my eyes to the (perhaps unavoidably) primitive state of economic theory relative to the physical sciences; you would NEVER be offered an intermediate organic chemistry course taught by someone from a different “school of thought”.
I recall asking David whether it was plausible that the Great Depression was really due to a technological shock, and he confidently answered that it was. Even then, I found that incredibly unlikely, so much so that I would really be uninterested in exploring such a hypothesis. I gather that most empirical research in RBC is “calibration” (a la Prescott), which strikes me as something of a fraud, since this approach cannot ‘reject’ RBC.
I find what Delong and Krugman have to say on the subject much more compelling. Bring on Theory X!
Darren: “I gather that most empirical research in RBC is “calibration” (a la Prescott), which strikes me as something of a fraud, since this approach cannot ‘reject’ RBC.”
I’m actually going to come to the defence of RBC on that point. As far as I understand it (which is not very far, I admit) RBC introduced calibration into macro. It’s an example of the sort of thing I had in mind when I wrote:
“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.”
To my mind, calibration is just a better way of doing “back of the envelope” calculations to see if the predictions of the theory are roughly in line with what we observe, when we plug in plausible numbers taken from elsewhere for the parameters.
It’s another way of trying to check if the theory fits the facts (or at least, what we think the facts are). Perfect? No. Foolproof? No. But a useful addition to the economics toolbox, and laudable in its purpose? Yes. I admire the way RBC theorists started using calibration.
RSJ wrote:
Well, the problem with string theory is that while it’s elegant, it does not create hypotheses that are testable.
So physicists “don’t know” because we don’t have particle accelerators that have the size of the solar system (yet), which would prove or disprove string theory.
In economics, nobody is arguing that RBC is not testable. It was testable, and it was tested and it failed, numerous times – unless you want to argue that all market action is rational and that there’s no such thing as an irrational market crash fuelled by sheer panic.
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? Krugman and others have lamented the sorry fact that many of the so-called freshwater schools stopped teaching Keynes. And this lead to the uninspiring spectacle of highly credentialed economists making very elementary mistakes when confronted by our current economic crisis.