New paradigms in economic theory? Not so fast | E-Axes

Not a member yet? Click here.
Forgot your Password?
Archives - Categories
On Inequality
On the Eurozone Debt Crisis
On Monetary Policy and Central Banking
On Global Economic Growth
On the Greek Debt Crisis
On the Banking and Financial Sectors
On Brexit
On China
On India
On Global Inflation
On Currencies
On the US Debt
On the "Economics" of the Arab Spring
Working Papers
Books suggested by members

New paradigms in economic theory? Not so fast

Author(s): Noah Smith

From Noah Smith's blog:

I've recently read two big-think piece about new paradigms for economic theory - this one by evolutionary biologist David Sloan Wilson, and this one by venture capitalist and activist Nick Hanauer and speechwriter Eric Liu. Is economic theory due for a paradigm shift? Maybe, but I don't think we know what the new paradigm will be yet.

Wilson's piece - grandiosely titled "Economic Theory Is Dead. Here’s What Will Replace It." - claims that evolutionary theory will be the magic bullet that will breathe life into econ. The piece doesn't explain how to incorporate evolutionary thinking into econ, but it does link to a 2013 special issue of JEBO that Wilson edited along with Barkley Rosser about incorporating evolution into economics. In a paper in that volume, Wilson lays out his ideas slightly more explicitly.

But only slightly. Wilson's paper does three things: 1) it references economists who have suggested making use of evolutionary ideas in the past, 2) it discusses some arguments against using evolutionary theory in econ, and 3) it lays out some broad general principles of evolutionary theory. Concrete examples are left to the other papers in the volume (which are all sadly paywalled).

In principle I think evolutionary theory might add a lot to economics, because economies obviously involve things like birth and death of firms, competition, predation, and other features similar to natural ecosystems. 

But the case for using evolutionary theory in econ is not yet a slam-dunk. The big reason is that we don't have much evidence that inheritance of traits occurs in economies. In biological evolution, we have many clear examples of heredity. In econ, to my knowledge, we have none. Evolution needs heredity, so evolutionary theorists who want to change the econ world should focus on demonstrating the existence of traits that are passed from company to company, or person to person, or industry to industry, within economies. Or, alternatively, they should show that companies and/or individuals have traits that change over time in a way similar to the way that biological traits change between generations. They should be very concrete and consistent about how to measure these traits. Then we can start talking about using evolution to create a new economics. 

Would-be evolutionary economists should realize that the measure of their success will be quantitative prediction. Get some numbers right out of sample, and they will win. What won't be useful is for them to simply point at various economic phenomena and say "Hey, this looks kind of like it conforms qualitatively to one or more general principles of evolution!" That sort of vague hand-waving does not really generate any progress in humanity's understanding of our world - it merely creates a feel-good sense of "truthiness" that makes for some good hypey media articles but little else. Evolutionary theorists, like all other researchers in all fields, should focus on predictive power and leave the hand-wavey just-so stories to a minimum.

Hanauer and Liu's piece - similarly titled "Traditional Economics Failed. Here’s a New Blueprint." - is, in my opinion, much more promising, if also pretty vague. It is also much more diverse, specifying many different sweeping changes that they believe need to be made in economic theory. Among these are:

1) The replacement of reductionist models with ones based on "complex adaptive systems"

2) The use of network models

3) The use of disequilibrium models

4) The use of nonlinear models

5) The replacement of "mechanistic" theories with "behavioral" ones

6) The replacement of optimization with something resembling "satisficing"

7) The replacement of forward-looking agents with adaptive agents in econ theories

8) Modeling people as interdependent instead of independent

9) Modeling people as irrational approximators instead of rational calculators

10) Modeling people as caring about reciprocity

11) Modeling win-win situations instead of environments characterized by rivalry

12) Replacing models of competition with models of cooperation

There is a lot to digest here. I'd split these points into three categories:

Category 1: Good points. These include (2), (4), (6), (7), (8), (9), (10), and (12). Hanauer and Liu identify networksnonlinearityincomplete optimizationincomplete forward-looking-nessexternalitiesbehavioral heuristicssocial preferences, andcooperative games as areas needing more attention in economics. I agree with all of this. Good job, guys!

Category 2: Points that misunderstand the current state of economics research. These include (3) and (11). Regarding "equilibrium", economists don't use it in the physics sense that Hanauer and Liu cite. Instead, they have redefined the word "equilibrium" to mean "any solution to a system of equations in any model." The term is thus now meaningless. Many, many mainstream economic models include "transition dynamics" or "short-run equilibrium" that is exactly the same as what Hanauer and Liu call "disequilibrium".
As for "win-win" models, most existing mainstream econ models are all about win-win situations. This is the concept of Pareto Efficiency

Category 3: Points that are not very well-defined. These include (1) and (5). "Complex adaptive systems" is a term that gets thrown around a lot but rarely gets a concrete definition. In computer science research, "complexity" basically just means "displaying emergent properties", and progress in that field has been rather halting. I'm still not sure what the term "complex adaptive systems" means in terms of economics. 

Hanauer and Liu assert that "We understand now how whirlpools arise from turbulence, or how bubbles emerge from economic activity." The latter is not the case; we do not actually know what bubbles are, or even whether they are a single phenomenon or several similar-looking phenomena. Are bubbles based on "greater fool" speculation? Rational mispricing? Emotion-based irrational mispricing? Information cascades? Other forms of herd behavior? Bayesian "information overshoot"? Some combination of these? None of these? We just don't know.

As for making economics less "mechanistic" and more "behavioral", Hanauer and Liu do not explain what this means, and merely reference a David Brooks book (which is not encouraging). 

So I agree with about two-thirds of Hanauer and Liu's points. The others need tightening up, but not bad overall. The question is whether these ideas, together, represent a new paradigm in economic theory. Hanauer and Liu argue that they do, but I am not so sure. There seem to be three mini-paradigms here: bounded rationality, interdependence, and holistic analysis. The first two have already been making inroads in economics, though I think they should make more inroads. The latter is kind of an older idea that doesn't seem to have panned out as well as many hoped - there isn't actually going to be a Second Enlightenment replacing reductionist science with holism.  

But I think that more important than any of these theoretical changes - or the evolutionary theory suggested by Wilson - is the empirical revolution in econ. Ten million cool theories are of little use beyond the "gee whiz" factor if you can't pick between them. Until recently, econ was fairly bad about agreeing on rigorous ways to test theories against reality, so paradigms came and went like fashions and fads. Now that's changing. To me, that seems like a much bigger deal than any new theory fad, because it offers us a chance to find enduringly reliable theories that won't simply disappear when people get bored or political ideologies change.

So the shift to empiricism away from philosophy supersedes all other real and potential shifts in economic theory. Would-be econ revolutionaries absolutely need to get on board with the new empiricism, or else risk being left behind.


David Sloan Wilson replies. He laughs at economics for being very very late to embrace empiricism. While the rebuke is very deserved, it's also true that good data is a lot harder to gather in econ, and that technology has made this a lot easier in recent decades.

Wilson also writes:

But there is more to Science 101 than the need to test theories. Let’s imagine that there were ten million cool theories out there. How long would it take to test them? Hundreds of millions of years. ...Does Smith really believe that any old idea that comes into the head of an economist is equally worthy of attention?

Answer: Of course not, but this is another reason empirical results are important. They typically leave a trail of clues that help guide scientists toward good theories. You see electrons making a sort of wavey pattern, and you invent quantum mechanics to explain that - and luckily it turns out to explain a lot of other stuff too. That's a typical progression - you start out with some fact or phenomenon, then you make a theory to fit it, then you test that theory on different phenomena to see if you've got something structural. Of course, sometimes pure intuition gets things right the first time around - general relativity and auction theory are examples of this - but usually we're not that smart, and theorists have to follow the empirical bread crumbs.

Wilson also writes:

The main reason that the so-called orthodox school of economics achieved its dominance is because it seemed to offer a grand unifying theoretical framework. Too bad that its assumptions were absurd and little effort was made to test its empirical predictions.

Well, there has definitely been some of that going on. But "orthodox" econ has achieved a lot of solid results, like auction theory, random utility discrete choice models, and a number of other models in tax, labor, and other areas. Nor are orthodox assumptions always absurd, since some of them hold up well in lab experiments and other micro-level studies. I think Wilson would enjoy learning about these successes, in addition to the well-publicized failures.

© 2011–2017 e-axes. All rights reserved. | Credits | Contact Us | Privacy Statement | Fri 19 Jan, 2018 19:01:33 PM
e-axes is proudly powered by Norder - Creative Solutions