Last week I had the pleasure of being on a roundtable on “Transnational Diffusion: Concepts and Mechanisms” at the ISA conference in San Francisco, together with Etel Solingen, Zachary Elkins, Detlef Jahn, and Covadonga Meseguer. In fact, diffusion was the general theme of the conference, which pissed off some
tasteless discerning people.
It was a great occasion to think freely about the future direction of diffusion research. Here is a summary of my contribution to the discussion. A more traditional review of the literature is here, and on Twitter I use #policydiffusion for tweets related to this topic.
1) Concepts are clear, worry about measures
We have reached a consensus on the definition of diffusion. Diffusion is a consequence of interdependence and is not defined exclusively (or even primarily) by the fact that something has spread. This implies that, when studying diffusion, we are interested more in the process than in the outcome. Convergence, for instance, can be a useful complement to a diffusion analysis, or it can motivate the research in the first place, but is not what we are actually studying.
Moreover, there is consensus on three broad classes of diffusion mechanisms: learning, emulation, and competition (some add coercion, but I disagree). For definitions, see this chapter.
This means that, conceptually speaking, it is pretty clear what we talk about when we talk about diffusion. There is definitely room for some improvement, but not much. Most new conceptual distinctions are hairsplitting. Where we have real problems is with operationalization. In this paper (still at draft stage), Martino Maggetti and I have done a meta-analysis of 100+ diffusion studies and have found that there is a lot of confusion on what indicators are appropriate for the different mechanisms. The same indicators are used for different mechanisms, and different indicators are used for the same mechanism. A mess. This has to improve if we want to generate more cumulative knowledge.
2) Learn about diffusion, or use diffusion to learn about something else?
There are two types of research questions that are worth asking at this point.
First, we can try to make a contribution to the diffusion literature itself. It is becoming harder and harder to pull this off successfully. The n-th study showing that a unit is more likely to adopt a policy if its neighbors/competitors/etc. have done so is not going to cut it. What is required is better, more focused questions, which themselves require better, more focused theory. As the building blocks of diffusion are fairly clear, theoretical advances should aim to explain more precisely how they operate in different contexts. For instance, Susan Hyde has been working on how practices diffuse and become norms in virtue of the signals they send. For instance, refusing to invite observers to monitor elections has become an unambiguous sign that a country is not democratic, which is why even clearly non-democratic states do it. In a panel at last week’s ISA conference, Hyde suggested that many other phenomena may fit this argument, such as sovereign credit ratings. In my own work I have tried to move theory forward by, for instance, arguing that different policy makers learn from different policy outcomes (including implications for their re-election) and that socialization attenuates tax competition.
Second, we can try to use the insights of diffusion research to learn something new about other phenomena. Diffusion often gives an original angle to do this. For instance, traditional work on competition focuses on, well, competition, but diffusion research tells us that this is just one type of interdependence among others: there is more to competition than just competition. Or, the literature on women’s representation has identified many types of spillovers, but it turns out that, until women’s participation in politics becomes a well-established norm, the number of women candidates in one unit increases with the number of women elected in other units.
3) We need better research designs
Standard research designs have almost fulfilled their potential. Adoption in one country = f(adoption in other countries, controls) has been done to death. Mostly for good reasons: it is a good approach to show that something diffuses. But if we want to push things forward, at this point we need something new (and better).
First, we need better data. Often this means moving away from cross-national analysis, which is also a trend in political science in general. In many cases sub-national units offer data of higher quality, are more comparable, and are closer to the level at which the action is really going on. We should also think creatively about data sources. Automated text analysis seems an especially promising avenue in this respect.
Second, research designs should be tailored to the specific questions asked. This is a truism that applies to any area, of course, but the problem seems particularly acute in diffusion research. There is a clear template with which we can study almost anything, so there is the temptation to actually do it. Which is fine, except that we cannot expect significant new insights to follow.
Third, we should take causal inference more seriously. This is a big
fad trend in political science right now, but one needs not be an identification Taleban to say that very, very few diffusion studies in political science pay any attention at all to this issue. Although in our context the problem is even thornier than usual (some say there is no hope), the status quo is not OK and we should do our best to improve on this front.
4) So what? Enter the “diffusion multiplier”
If you are into diffusion, you cannot get enough of it. But why should others care?
Well, assume that you are an advocate of marriage equality. Same-sex marriage has already spread a good deal, but it is still by no means the norm. Would it not be useful to know which states or countries one should persuade in order to accelerate the process? We can call this the “diffusion multiplier” (by analogy with the “social multiplier”): if the “right” units adopts a policy, others will be more likely to do the same. Thus, by influencing one unit directly, many more are reached indirectly.
This works also the other way round: if you want to prevent the spread of a policy, it would be useful to know on which units you should concentrate the efforts. For instance, not all states are equally effective as firewalls against the spread of soda bans.
Of course, we first need to know which units are influential and why, which is where diffusion research has something to say. We are nowhere near being able to make such specific recommendations, but this is certainly one of the potential practical payoffs of this literature.