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Jim Levinsohn on the scope for doing work with industrial organization and development

David McKenzie's picture
Late last year I posted several posts on why we don’t see more work combining industrial organization and development. I just received some thoughts on this question from Jim Levinsohn, Professor of Economics and Management at Yale, and a long-time leader in this area. He kindly agreed to let me share them here:
On why we don’t see more work
I agree there are real opportunities for the researcher willing to delve into the mix of IO and development. As IO has become more empirically focused, this means getting micro data from developing countries— either at the plant, product, or consumer level.   But some of that data are out there.   I think the bigger problem is the two fields have, in my view, each gone overboard in terms of a particular methodological bent.   In development, the much discussed rise of the Randomnistas has held sway while in IO very methodologically driven forays into often very policy-irrelevant questions has held sway.    A grad student who has been trained in one field is likely to find the other pretty foreign. 
I think this gulf is likely to narrow.  I think the RCT pendulum has swung about as far as it’s likely to go and we’ll move back to a reconsideration of what one can learn from non-experimental data but with an enhanced (and helpful) focus on the looking for the sort of clean identification that the RCTs provided.    In IO, I think researchers are starting to step back from ever more structural approaches to ever less interesting questions and are instead starting to re-examine some interesting issues.   So there’s hope.

On where there is scope for bridging the two fields
I think that one of the real avenues for productive work is using RCTs to nail down key behavioral parameters that can then be used in a more structural approach to investigate interesting policy issues.    This represents the sort of melding that I suspect is going to be fun and productive. 

Does it matter for doing this research that there are few big firms in many developing countries?
You are absolutely right that there are lots of developing countries in which “there just aren’t that many bigger firms.” I see this as a huge opportunity for really understanding what drives entry, how incumbent firms react to entry, and other related questions that are central to IO.  In this sense, developing countries are a fantastic case study in ways that, say, big developed countries are not.    There are also great opportunities to better understand and measure the benefits of enhanced competition in this setting.

On how applicable standard IO tools are for developing countries
I couldn’t agree more that one shouldn’t use off-the-shelf methodologies (you cite LP on Productivity) which might be appropriate in a developed country but are inappropriate in a developing country.   Again, this is an opportunity for enterprising researchers— amend the methodologies, many of which are quite dependent on the specific underlying structural assumptions, to better fit a developing country context.   

On whether field experiments being cheaper and sometimes easier to pull off in developing countries makes for interesting opportunities to make major contributions to IO
I am not very hopeful when it comes to more field experiments in IO.   You’re right that it’d be cheaper to pull off, but I don’t think cost is the constraining reason we don’t see RCTs in IO.