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GiveDirectly just announced a basic income grant experiment. Here is how to make it better.

Berk Ozler's picture

In an article in Slate yesterday, co-founders of GiveDirectly announced that they will provide at least 6,000 people in Kenya with a basic income grant (BIG) for a period of 10-15 years, which will cost about $30 million. The proposal is scant in details at the moment, but this article in Vox suggests that dozens of villages will randomly be selected in an already selected region of Kenya for this exercise and everyone within will be given roughly a dollar a day per person for a decade.

GiveDirectly lays out three principles for the study: the study will be an experiment, which means random assignment of villages into treatment. Second, the intervention will let people know that the income is guaranteed for at least a decade for them to fully optimize. Finally, the transfers will be universal within each community.

This is certainly ambitious and welcome, but, believe it or not, I don’t think it goes far enough. Here is some more ambition to learn a lot more, by spending (quite a bit) more money:

Would targeted government cash transfer programs reduce poverty even more? I get the attraction of guaranteeing everyone money and the fact that non-poor Kenyans, i.e. about 50% of Kenyans above the official poverty line, are still poor by developed world standards. But, at the same time, we don’t have unlimited resources for antipoverty programs and the value of the marginal dollar does decrease even in Kenya as we move up the income ladder. Any standard model would suggest larger transfers to the poor will improve social welfare rather than equal transfers across the board. Of course, the world likes to defy standard models (plus targeting can be costly), so the question of whether a long-term BIG would be more or less effective in reducing poverty and inequality than a targeted government program of the same cost is an empirical question. Why not put that to the test?

The articles above suggest an investment and an insurance role for cash transfers: lump-sum transfers up front work best for the former, while smaller frequent guaranteed transfers are good for the latter. If we were to save 50% of the program funds (minus targeting costs) by excluding the non-poor, we could give that money up front to poor families to spur investment, while still keeping them on monthly transfers for a decade. Might that not work better? It’d be nice to know. There are really many other ways to go once you start thinking about targeting or varying the transfers based on where households are in the distribution.

Are unconditional cash transfers really our best bet for sustained exits out of poverty? Cash transfers are simple to implement and are utterly reasonable as the numeraire antipoverty intervention. But, are they our best hope to pull millions out of poverty? Looking at the landscape of interventions, some might argue that BRAC’s targeting the ultra-poor (TUP) model looks more promising for reducing poverty (and even transforming village economies) than cost-equivalent cash. In fact, Abhijit Banerjee, who is reported to be the lead PI for this study, seemed to suggest as much with his co-authors in the six-country study using this approach published in Science last year: in an apples to oranges comparison of GiveDirectly and TUP in different countries with different budgets, they suggested that while the short-term consumption gains seemed higher in GiveDirectly’s previous study in Kenya, the effects seemed to decline over time while the TUP effects were sustained. That article did suggest that it would be good to compare the long-term evolution of impacts to gauge relative cost-benefit analysis of the two approaches. Why not do that right here right now?

Why have a pure control group? I am sure there are arguments to justify a pure control, but we have a pretty good idea that any of these programs will have some effects. The interesting comparison is not against “no support” (or the usual government support): it’s against cost-equivalent alternative efforts. Plus, the government, local or federal might be tempted to remove business as usual from the treatment villages and focus more effort on the unlucky randomized out. If three groups of villages were getting cost-equivalent programs trying their best to reduce poverty, then the temptation to help one group would be much less. (If still curious about program effects against business as usual, we could employ a non-experimental method, such as synthetic control...)

So, here is what I propose a more ambitious study, which would teach us a lot more, would look like:

The World Bank/Government of Kenya v. GiveDirectly v. BRAC

Each group gets $30 million for its program and gets randomly assigned N villages. They agree on the goal posts, i.e. what we’re aiming for, or the social welfare function: presumably, this gives higher weight to gains among the poor, reductions in inequality, etc. but not necessarily zero weight to the non-poor. Performance of each group gets assessed using this function in all of the N villages assigned to it.

Treatment 1 (BIG): GiveDirectly’s Basic Income Grant Proposal.

Treatment 2 (targeted cash transfers): The World Bank, with the government of Kenya, devises what it considers the most cost-effective cash transfer program to reduce poverty. It could allocate money differently across the villages (based on geographic targeting) and within villages (based on within village targeting). It could have cheap or expensive targeting: the more expensive this is, the less money it would have for actual transfers to households.

Treatment 3 (TUP): BRAC (but you can insert any highly competent INGO here if they're unwilling to participate) implements its TUP program optimized for Kenya. Again, the TUP program would make its own choices about how much to spend on transfers vs. other types of support, who to target, etc.

Is it possible? Sure: GiveDirectly has reportedly already raised two thirds of the funds and looking for the rest, which I am sure it will raise in no time. The World Bank could easily put $30 million behind a social protection/ poverty reduction program to fund its arm. We could get another donor for the TUP arm (and give BRAC some time to develop its intervention in Kenya. In fact, we could take this study elsewhere to where BRAC is already comfortable operating and has shown effectiveness, as cash transfers are much more easily transported across the world).

What does this buy us? A number of things: First, by having each organization run its own program in its assigned areas, the incentives are completely lined up: everyone would try to run as lean and optimally-designed a program as possible to maximize the social welfare function in their assigned areas. If we had one organization pitting these models against each other in an experiment, we might worry that they could put more effort into one of the approaches because they are partial to it for whatever reason. The competition aspect makes the horse race real. A transparent operation for a decade with the world’s attention on this experiment would guarantee that there’d be no temptation to cheat, either (say, the WB funding more complementary projects in its assigned villages).

Second, imagine the growth incidence curves that we can draw with these three groups on the same graph: imagine, hypothetically, that growth rate in the mean is higher in the BIG arm, but the rate of pro-poor growth (or the mean percentile growth rate) is higher in another. Support this evidence with improvements in other outcomes, like child health, improvements in test scores, etc.: just wonderful and exciting to think about...

Third, we may not get many more chances at this kind of learning again. Just the BIG proposal will cost $30 million and take the most part of a decade to learn from. Why not spend three times that much to gauge how well a program like Bolsa Familia (or a generous social cash transfer scheme in Africa) stacks up against BIG or TUP. Considering the opportunity cost, it could be justified: plus the $90 million is not really a "cost" as most of this money will go to poor people in a developing country, with many of the best minds in development pitching in to design the programs to be as efficient as they can possibly be.

So, come on World Bank: make an offer to GiveDirectly (jointly with the government of Kenya) to double their experimental funds if they’ll let a good SP program go head to head with their proposed basic income grant. With $60M in hand, I am sure another angel investor (or a multinational donor) would happily back the TUP model for the three-armed study.
 
P.S. While I am solely responsible for this post, the ideas here – particularly the idea of having cost-equivalent programs being evaluated against each other over a sufficiently long period of time using a common target population and an agreed upon goal post – is borrowed from a previous research proposal co-authored with Sarah Baird, Craig McIntosh, Elan Satriawan, and Sudarno Sumarto, submitted to the Development Innovation Ventures and the Global Innovation Fund. None of them are implicated here.

P.P.S. A quick calculation suggests that the proposed BIG is a transfer of about $500 per person per year, which more or less adds up to a little over a dollar a day. However, the sample of dozens of villages does not: how would 6,000 people, which must be about 1,500 households, form the entire population of dozens of villages? I would have guessed the total population of 10 villages would easily add up to 1,500 households. I am sure the detailed plans will clarify...
 

Comments

Submitted by John Quattrochi on

Great post, Berk. Do you believe that within-village targeting is still a reasonable option despite the evidence for negative psychological spillovers? Is the theory that clearly explained targeting criteria would not cause the same resentment or jealousy that random assignment causes?

Submitted by Berk Ozler on
You're right on both fronts. I am a believer that negative spillovers are possible, but, so far, that evidence is from randomized out eligibles. Clearly articulated, transparent criteria, covering a large segment of the population, should do better. After all, I don't see many developing country governments giving up on targeting the poor anytime soon.

Submitted by Ashu Handa on

The Government of Kenya ALREADY has its own very large cash transfer program, reaching 350k households and roughly 1.5m individuals--the Kenya CT-OVC. No need for the WB to come in and re-invent the wheel. [The Kenya CT-OVC has undergone an impact evaluation as well.] Better to compare to a home-grown program which already has been through the political vetting process.

Will the NGOs have to go through the Kenya Central Tender Board, or have to follow the State Personnel Act? Implementation is (almost) everything--to make it a fair fight, all would have to play by the same rules. Governments are accountable in ways that NGOs are not. And ultimately, since I guess the state would be responsible for a scaled-up program, and would have to implement within official rules, all interventions ought to abide by the rules that the GoK Ministry abides by.

On a side note, a BRAC/TUP program recently closed shop in neighboring Tanzania, too costly and not tailored to local context.

Submitted by Berk Ozler on
Grouchy comment, but thanks. If CT-OVC is what the Kenyan government thought it would be its best foot forward, sure. However, I was thinking of transfers that cover all poor households, not just those with children or other criteria than just being a poor household.

Submitted by Yohanna on

Great post, and really interesting experiment!
The long-term dimension is a key feature, but also brings added risk. For instance, one question that came to my mind is what will happen to people who move out of the village, and the potential consequences. If they lose the BIG, it can become a disincentive to perhaps pursue better opportunities elsewhere. Maybe not a big disincentive if they have some certainty that the new opportunity is better; however, it may be enough to prevent people from pursuing riskier ones. If they keep the BIG, the positive impact will accrue elsewhere (perhaps in a control village, perhaps in another part of the country altogether). And what happens to people moving into the village? I suppose they don't get the BIG (otherwise everyone will move!), but doesn't this somewhat undermine the notion that the BIG must be universal in the community?

With a real national BIG program, this question would not arise because everyone (or everyone entitled) would receive it. However, in an experimental setting with a geographic dimension to it, can we safely ignore the potential impact on outcomes?

Submitted by Berk Ozler on
You're asking the right questions. The details are not out yet, so I don't know the answers for what's being proposed. But, you're right that this would not be an issue in either a nationwide program, or under targeted cash transfer programs with clear rules.

Having said that I would not have an issue with having initially defined beneficiaries carrying their benefits wherever they go. And, you could have rules about eligibility for movers-in...

These are some of the many details that would have to be worked out...

Berk.

Submitted by Vincenzo on

Thanks Berk, this is very interesting! Without additional details on treatment 1 and 3, I'd be very concerned (as another reader implicitly pointed out) about their policy relevance and potential to be scaled up. Even when we do IEs that are fully embedded in Government programs and systems, often results are not used by governments. So what are the chances that intervention that are not built on country systems (or that are explicitly and intentionally by-passing them) are finally adopted by governments? Ideally, one would like to have all 3 treatment arms fully backed by the Government, I don't think thinking of the 3 interventions as a race between 3 different institutions is particularly useful, while I see the learning potential from testing them as 3 different models.

Submitted by Berk Ozler on
About policy relevance: I think these are some of the bigger questions, approaches we are grappling with at the moment -- at least at a global level. There might be many implementation questions that are as interesting and more important, but it's hard to say that these approaches, which are being tried in many settings in one form or another, should not be judged against each other in an "apples to apples setting."

I alos am not worried too much about immediate scale-up in any one country, but what we learn from them could spur a new generationof programs that are better designed and adapted in many settings.

The problem with a government running all three models is that it also has downsides on efficacy interpretations: did one not work because of improper implementation or else? I think you'd organize things so that each intervention is possible for the government to consider implementing and feasible and cost-effective to scale up, but you don't have to have the experiment to be run by it. I think the incentives to do well are important, even though it could lead to hanky panky -- to use a totally scientific term...

But, these are the questions you'd be debating a lot if you were setting up something that ambitious. I do know that the Kenya WB team and their counterparts will likely be talking to GiveDirectly about all of this and perhaps touching on some of these very points. None of this is easy or cheap: that's for sure...

Submitted by Michele on

While I have been a great supporter of Give Directly – if anything because initiatives like it keep us working on cash transfers on our toes, I am having a hard time figuring out the main objective of this experiment.
If I am not mistaken, Give Directly aims to provide about $600 per year/individual for 10 years.
Back of the envelope calculations tell us that $600 per year, with 20+ million poor people in Kenya based on WDIs, amount to a total cost of about $12 billion per year if the program were to be scaled up nationally with some poverty-targeting element. It could be up to $25 billion a year if one were to keep the program universal. Given that the total GDP of Kenya is about $60 billion, the experiment is essentially simulating something that would cost, at best, 20% of GDP. I cannot think of a CCT that comes even close to costing that much. And I am certain that the experiment will show us great results in terms of income, HD indicators, and so on. But then what really? How scalable is this program? What are we going to compare it against? The only similar experiment I can think of is Mongolia late 2000s-early 2010s, and that did not go that well…

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