Whose questions are we trying to answer?
On the macro vs micro development debate. It doesn’t have to be either-or. And it depends on whose questions we’re trying to answer.
For those not on Twitter, over the weekend there has been a wide-ranging debate on the questions development economists should be working on, sparked by this tweet.
Having caught up as best I can, and having also written about this recently (The development economics I’d like to see), I’ve summarised some additional thoughts I’ve had on this topic, spurred by the interesting feedback I received and some reflections on the Twitter debate. Ultimately, I think a lot of this boils down to whose questions we are trying to answer.
The micro and macro caricatures
If I were to caricature what each side of this debate says about the other:
Micro on macro: Your methods suck and can’t answer the big questions.
Macro on micro: Your methods only answer small questions that don’t matter.
These are caricatures, so only represent the views of a few people. Naturally, I disagree with both. I think we’ve learned a lot of useful lessons about questions that do matter from micro development research. I also don’t think we should ignore, or give up, on the big questions that macro development tries to answer, even if the answers are harder to reach, and less ‘clean’.
I think this point by Jesús summarises best how I think about this debate (plain English translation below for non-academics).
To summarise, it’s not that micro development papers are somehow bad in and of themselves. It’s that we’ve allocated too much research effort and funding to answering narrower questions using the causal identification toolkit relative to macro development work on the bigger, thornier questions.
If funding, career and publication incentives had been more equally distributed in recent decades, and not so skewed to micro, we’d likely have a deeper understanding of the important growth-related questions, and better methods to answer them.
An aside: I would love to see actual data on the research funding breakdown across development economics. Anecdotally, the research I see overwhelmingly falls on the micro side, of which RCTs are actually a relatively small part. But then again, RCTs are more expensive than the typical research project. Anyway, I have a strong prior on how funding breaks down overall between micro and macro in development, but would love to see the data.
Big questions, for who? Donors vs governments
I’ve found myself using the phrase ‘the big questions’ a lot recently. It’s worth unpacking that a bit.
Ultimately, a lot of this debate boils down to whose questions we are trying to answer. You can probably trace a lot of the micro bias of recent years to the questions that donors are grappling with.
To simplify, donors had (and some still have) billion-dollar+ budgets, which are typically spent on programmes, and they wanted to know how to spend it more effectively. So, it makes sense that they funded micro development research to help them answer those questions – the tools of micro are better suited to establishing the impacts of their programmes, things like expanding access to microfinance, distributing deworming medication, or improving teaching in LMIC classrooms.
These are certainly big questions in the sense that there are billions of dollars of funding involved. So even if you can influence a small percentage of that funding to be spent more effectively, then the research will have been worth the cost.
But donors and their programmes, despite their many successes and the millions of lives they’ve saved, are actually a very small part of the most important development story of recent times – sustained economic growth in China, India and elsewhere, which is responsible for the vast majority of people moved out of poverty in recent decades.
Given that donors came to represent a large chunk of those who were funding research in development economics, this skewed the overall discipline in the direction of answering their programmatic questions, rather than the type of questions a government would be asking if they were looking to grow their economies, which is ultimately the best way of alleviating poverty at scale.
There are two things to consider here:
The total potential impact of research (Macro wins)
The likelihood that research has an impact (Micro wins)
I know, this is a gross simplification, as there is no guarantee that a given piece of macro research actually sheds light on replicating the economic success stories of recent decades, nor is there a guarantee that micro research actually shapes policy to be more effective or kills an ineffective aid programme.
But given that micro has dominated development economics, it does feel reasonable that the discipline shifts more attention to macro. Even with a lower chance of impact, the potential impact is so much bigger that it feels important to do this as well. And I imagine some of that rebalancing will come naturally, given that there is less aid funding to influence these days.
The wrong questions?
This links to a separate but related point I made in my recent blog, that there is a serious mismatch between policy questions and research questions.
One point that was missing from my blog, which I think is important to highlight, is that it’s certainly possible that policymakers are asking the wrong questions.
I guess I’m still not sure how to deal with this. There is clearly an important role for research to play in helping to independently shed light on the types of questions policymakers should ask. But it’s unclear to me how feasible it is to influence these, particularly in the short to medium term.
If a policymaker comes to you and says ‘here’s what I’m doing, how do I do it well?’, good luck telling them that, actually, it would be better if they did something else entirely. Instead, the most fruitful route to impact in these circumstances is likely, regardless of the policy, making sure it is done effectively. This is the Stefan Dercon art of ‘second-best’ policymaking. But where you draw the line, that is which economic policies are so bad that you choose to play no part, even if you could improve them on the margin, is murky.
Who’s leading the charge
One glaring problem with this debate is that it’s being led by academics at US and European institutions. Ultimately, it should be led by academics at universities in Latin America, Africa, and Asia. But development economics has failed to empower them, and they are often forced to focus on the questions they can get funded, rather than the questions they know are most important for their local context.
Some progress has been made, and it’s now more common to see local academics added as a co-author to a US or Europe-led project. But a more fundamental change is needed. The ideas phase should instead be led by those closer to the questions that need answering, who can then add other academics if they have methodological expertise to bring to bear, or funding networks they can tap into.
Progress is being made in macro development
I also wanted to emphasise that macro development is not starting from scratch, and progress has been underway in recent years.
As I discussed in my recent post on AI – There is no randomising a technological revolution – there are bright spots in the discipline, with tools emerging that are suited to this class of questions. The Structural Transformation and Economic Growth (STEG) programme, run by Doug Gollin and Joe Kaboski, stands out as one. STEG coordinates and funds research on macro questions in developing countries, including structural change, productivity and growth, often drawing on micro data. This goes beyond just industrial policy and looks at how a range of policies on human capital, financial markets, and agriculture, could ultimately lead to economic growth.
And this did not happen by accident, but was a result of funders pushing the growth research agenda at a time when the randomistas dominated. So, it’s worth highlighting the work of those at DFID, now FCDO, like Andy Hinsley and John Piper, who funded PEDL, and then STEG. I read a lot of development economics, and research originating from these two programmes consistently feels closer to the big questions on growth.
(It’s worth noting my conflict of interest here, as the same FCDO team funds VoxDev, and I’m based at CEPR which manages both PEDL and STEG, but I stand by the points I’ve made above).
And it’s not just STEG, Oliver Kim, for instance, has a number of relevant papers here.
And this thread also identifies a range of useful research on these types of questions.
So, overall, I’m glad this debate is being had, and I’m hopeful that we are on the way to a renewed focus on, and understanding of, the ‘big questions’ in development.
To help this effort, I think we’d benefit massively from a much more systematic attempt to collect policymakers’ questions, as it often feels like we are shooting in the dark when trying to establish what really are the most important questions – or, at least, those with the most interest from policy audiences. Funding that type of effort would seem to be a great guide for the discipline, both in terms of matching the body of evidence we already have to existing questions, and acting as a north star to guide future research agendas.
Keen to continue the conversation in the comments, or on Twitter.
Oliver, this is exactly the debate the field needs. Also worth calling out is Lant Pritchett's work and also that of Growth Teams as a recent attempt to operationalise the government-question side of this: i.e., what would it look like to actually embed researchers within the policy process, oriented around growth diagnostics, rather than studying it from outside?
Even so, there's a question one level upstream that's also worth including. An earlier generation of scholarship did try to ask not just what policies countries such as Korea adopted, but also what created the political space for those choices to be made at all, and what organisational alignment throughout the state made them executable rather than aspirational. That literature, including the likes of Evans, Amsden and others, feels somewhat unfashionable now. Nonetheless, the questions they were asking haven't been fully answered. There are those of us trying to bring it back. Think of Dercon's Gambling on Development as one strand of this.
So, to be fully satisfying, I think that the renewed macro agenda needs to go upstream from policy identification to the political and organisational conditions that make those policies achievable and sustainable. Korea's Economic Planning Board wasn't just technically competent; it was the product of a specific moment and a cadre-formation process that preceded it by years. The policy was the visible layer. But the underlying machinery was a different and much slower thing.
Whether the macro tradition now re-emerging has better tools for that prior question than the developmental state scholars did is genuinely unclear, and probably the most important methodological challenge for the agenda you're describing here. But one well worth tackling. Keep up the encouragement!