by Has economics — really — become an empirical science? In Economics Rules (Oxford University Press, 2015), Dani Rodrik maintains that ‘imaginative empirical methods’ — such as game theoretical applications, natural experiments, field experiments, lab experiments, RCTs — can help us to answer questions concerning the external validity of economic models. In Rodrik’s view, they are more or less tests of ‘an underlying economic model’ and enable economists to make the right selection from the ever-expanding ‘collection of potentially applicable models.’ Writes Rodrik: Another way we can observe the transformation of the discipline is by looking at the new areas of research that have flourished in recent decades. Three of these are particularly noteworthy:
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Has economics — really — become an empirical science?
In Economics Rules (Oxford University Press, 2015), Dani Rodrik maintains that ‘imaginative empirical methods’ — such as game theoretical applications, natural experiments, field experiments, lab experiments, RCTs — can help us to answer questions concerning the external validity of economic models. In Rodrik’s view, they are more or less tests of ‘an underlying economic model’ and enable economists to make the right selection from the ever-expanding ‘collection of potentially applicable models.’ Writes Rodrik:
Another way we can observe the transformation of the discipline is by looking at the new areas of research that have flourished in recent decades. Three of these are particularly noteworthy: behavioral economics, randomized controlled trials (RCTs), and institutions … They suggest that the view of economics as an insular, inbred discipline closed to the outside influences is more caricature than reality.
I beg to differ. When looked at carefully, there are in fact not that many real reasons to share Rodrik’s optimism on this ’empirical turn’ in economics.
Field studies and experiments face the same basic problem as theoretical models — they are built on rather artificial conditions and have difficulties with the ‘trade-off’ between internal and external validity. The more artificial conditions, the more internal validity, but also less external validity. The more we rig experiments/field studies/models to avoid the ‘confounding factors’, the less the conditions are reminiscent of the real ‘target system.’ You could of course discuss the field vs. experiments vs. theoretical models in terms of realism — but the nodal issue is not about that, but basically about how economists using different isolation strategies in different ‘nomological machines’ attempt to learn about causal relationships. I have strong doubts about the generalizability of all three research strategies because the probability is high that causal mechanisms are different in different contexts and that lack of homogeneity/stability/invariance doesn’t give us warranted export licenses to the ‘real’ societies or economies.
If we see experiments or field studies as theory tests or models that ultimately aspire to say something about the real ‘target system,’ then the problem of external validity is central (and was for a long time also a key reason why behavioural economists had trouble getting their research results published).
Assume that you have examined how the work performance of Chinese workers A is affected by B (‘treatment’). How can we extrapolate/generalize to new samples outside the original population (e.g. to the US)? How do we know that any replication attempt ‘succeeds’? How do we know when these replicated experimental results can be said to justify inferences made in samples from the original population? If, for example, P(A|B) is the conditional density function for the original sample, and we are interested in doing an extrapolative prediction of E [P(A|B)], how can we know that the new sample’s density function is identical with the original? Unless we can give some really good argument for this being the case, inferences built on P(A|B) are not really saying anything on that of the target system’s P'(A|B).
As I see it this is the heart of the matter. External validity/extrapolation/generalization is founded on the assumption that we could make inferences based on P(A|B) that is exportable to other populations for which P'(A|B) applies. Sure, if one can convincingly show that P and P’are similar enough, the problems are perhaps surmountable. But arbitrarily just introducing functional specification restrictions of the type invariance/stability /homogeneity, is, at least for an epistemological realist far from satisfactory. And often it is – unfortunately – exactly this that I see when I take part of mainstream neoclassical economists’ models/experiments/field studies.
By this, I do not mean to say that empirical methods per se are so problematic that they can never be used. On the contrary, I am basically — though not without reservations — in favour of the increased use of experiments and field studies within economics. Not least as an alternative to completely barren ‘bridge-less’ axiomatic-deductive theory models. My criticism is more about aspiration levels and what we believe that we can achieve with our mediational epistemological tools and methods in the social sciences.
Many ‘experimentalists’ claim that it is easy to replicate experiments under different conditions and therefore a fortiori easy to test the robustness of experimental results. But is it really that easy? If in the example given above, we run a test and find that our predictions were not correct – what can we conclude? The B ‘works’ in China but not in the US? Or that B ‘works’ in a backward agrarian society, but not in a post-modern service society? That B ‘worked’ in the field study conducted in the year 2008 but not in the year 2014? Population selection is almost never simple. Had the problem of external validity only been about inference from sample to population, this would be no critical problem. But the really interesting inferences are those we try to make from specific labs/experiments/fields to specific real-world situations/institutions/ structures that we are interested in understanding or (causally) explaining. And then the population problem is more difficult to tackle.
The increasing use of natural and quasi-natural experiments in economics during the last couple of decades has led, not only Rodrik, but several other prominent economists to triumphantly declare it as a major step on a recent path toward empirics, where instead of being a deductive philosophy, economics is now increasingly becoming an inductive science.
In randomized trials the researchers try to find out the causal effects that different variables of interest may have by changing circumstances randomly — a procedure somewhat (‘on average’) equivalent to the usual ceteris paribus assumption).
Besides the fact that ‘on average’ is not always ‘good enough,’ it amounts to nothing but hand waving to simpliciter assume, without argumentation, that it is tenable to treat social agents and relations as homogeneous and interchangeable entities.
Randomization is used to basically allow the econometrician to treat the population as consisting of interchangeable and homogeneous groups (‘treatment’ and ‘control’). The regression models one arrives at by using randomized trials tell us the average effect that variations in variable X have on the outcome variable Y, without having to explicitly control for effects of other explanatory variables R, S, T, etc., etc. Everything is assumed to be essentially equal except the values taken by variable X.
In a usual regression context one would apply an ordinary least squares estimator (OLS) in trying to get an unbiased and consistent estimate:
Y = α + βX + ε,
where α is a constant intercept, β a constant ‘structural’ causal effect and ε an error term.
The problem here is that although we may get an estimate of the ‘true’ average causal effect, this may ‘mask’ important heterogeneous effects of a causal nature. Although we get the right answer of the average causal effect being 0, those who are ‘treated'( X=1) may have causal effects equal to – 100 and those ‘not treated’ (X=0) may have causal effects equal to 100. Contemplating being treated or not, most people would probably be interested in knowing about this underlying heterogeneity and would not consider the OLS average effect particularly enlightening.
Limiting model assumptions in economic science always have to be closely examined since if we are going to be able to show that the mechanisms or causes that we isolate and handle in our models are stable in the sense that they do not change when we ‘export’ them to our ‘target systems,’ we have to be able to show that they do not only hold under ceteris paribus conditions and a fortiori only are of limited value to our understanding, explanations or predictions of real economic systems.
Real-world social systems are not governed by stable causal mechanisms or capacities. The kinds of ‘laws’ and relations that econometrics has established, are laws and relations about entities in models that presuppose causal mechanisms being atomistic and additive. When causal mechanisms operate in real-world social target systems they only do it in ever-changing and unstable combinations where the whole is more than a mechanical sum of parts. If economic regularities obtain they do it (as a rule) only because we engineered them for that purpose. Outside man-made ‘nomological machines’ they are rare, or even non-existent.
I also think that most ‘randomistas’ really underestimate the heterogeneity problem. It does not just turn up as an external validity problem when trying to ‘export’ regression results to different times or different target populations. It is also often an internal problem to the millions of regression estimates that economists produce every year.
Just as econometrics, randomization promises more than it can deliver, basically because it requires assumptions that in practice are not possible to maintain.
Like econometrics, randomization is basically a deductive method. Given the assumptions (such as manipulability, transitivity, separability, additivity, linearity, etc.) these methods deliver deductive inferences. The problem, of course, is that we will never completely know when the assumptions are right. And although randomization may contribute to controlling for confounding, it does not guarantee it, since genuine randomness presupposes infinite experimentation and we know all real experimentation is finite. And even if randomization may help to establish average causal effects, it says nothing of individual effects unless homogeneity is added to the list of assumptions. Real target systems are seldom epistemically isomorphic to our axiomatic-deductive models/systems, and even if they were, we still have to argue for the external validity of the conclusions reached from within these epistemically convenient models/systems. Causal evidence generated by randomization procedures may be valid in “closed” models, but what we usually are interested in, is causal evidence in the real target system we happen to live in.
When does a conclusion established in population X hold for target population Y? Only under very restrictive conditions!
‘Ideally controlled experiments’ tell us with certainty what causes what effects — but only given the right ‘closures.’ Making appropriate extrapolations from (ideal, accidental, natural or quasi) experiments to different settings, populations or target systems, is not easy. “It works there” is no evidence for “it will work here”. Causes deduced in an experimental setting still have to show that they come with an export warrant to the target population/system. The causal background assumptions made have to be justified, and without licenses to export, the value of ‘rigorous’ and ‘precise’ methods — and ‘on-average-knowledge’ — is despairingly small.
So, no, I find it hard to share Rodrik’s and others’ enthusiasm and optimism on the value of (quasi)natural experiments and all the statistical-econometric machinery that comes with it. Guess I’m still waiting for the export warrant…
Taking assumptions like utility maximization or market equilibrium as a matter of course leads to the ‘standing presumption in economics that, if an empirical statement is deduced from standard assumptions then that statement is reliable’ …
The ongoing importance of these assumptions is especially evident in those areas of economic research, where empirical results are challenging standard views on economic behaviour like experimental economics or behavioural finance … From the perspective of Model-Platonism, these research-areas are still framed by the ‘superior insights’ associated with early 20th century concepts, essentially because almost all of their results are framed in terms of rational individuals, who engage in optimizing behaviour and, thereby, attain equilibrium. For instance, the attitude to explain cooperation or fair behaviour in experiments by assuming an ‘inequality aversion’ integrated in (a fraction of) the subjects’ preferences is strictly in accordance with the assumption of rational individuals, a feature which the authors are keen to report …
So, while the mere emergence of research areas like experimental economics is sometimes deemed a clear sign for the advent of a new era … a closer look at these fields allows us to illustrate the enduring relevance of the Model-Platonism-topos and, thereby, shows the pervasion of these fields with a traditional neoclassical style of thought.
Re game theory, yours truly remembers when back in 1991, earning my first PhD with a dissertation on decision making and rationality in social choice theory and game theory, I concluded that
repeatedly it seems as though mathematical tractability and elegance — rather than realism and relevance — have been the most applied guidelines for the behavioural assumptions being made. On a political and social level it is doubtful if the methodological individualism, ahistoricity and formalism they are advocating are especially valid.
This, of course, was like swearing in church. My mainstream neoclassical colleagues were — to say the least — not exactly überjoyed. Listening to what one of the world’s most renowned game theorists — Ariel Rubinstein — has to say on the rather limited applicability of game theory in this interview (emphasis added), I basically think he confirms my doubts about how well-founded is Rodrik’s ‘optimism:’
Is game theory useful in a concrete sense or not? … I believe that game theory is very interesting. I’ve spent a lot of my life thinking about it, but I don’t respect the claims that it has direct applications.
The analogy I sometimes give is from logic. Logic is a very interesting field in philosophy, or in mathematics. But I don’t think anybody has the illusion that logic helps people to be better performers in life. A good judge does not need to know logic. It may turn out to be useful – logic was useful in the development of the computer sciences, for example – but it’s not directly practical in the sense of helping you figure out how best to behave tomorrow, say in a debate with friends, or when analysing data that you get as a judge or a citizen or as a scientist …
Game theory is about a collection of fables. Are fables useful or not? In some sense, you can say that they are useful, because good fables can give you some new insight into the world and allow you to think about a situation differently. But fables are not useful in the sense of giving you advice about what to do tomorrow, or how to reach an agreement between the West and Iran. The same is true about game theory …
In general, I would say there were too many claims made by game theoreticians about its relevance. Every book of game theory starts with “Game theory is very relevant to everything that you can imagine, and probably many things that you can’t imagine.” In my opinion that’s just a marketing device …
So — contrary to Rodrik’s optimism — I would argue that although different ’empirical’ approaches have been — more or less — integrated into mainstream economics, there is still a long way to go before economics has become a truly empirical science.