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  • Reply to: GiveDirectly Three-Year Impacts, Explained by the Authors   5 hours 19 min ago
    Hi Dan,

    Thanks. It is a puzzle, isn't it? I first thought it was thatchd vs. ALL, but that's not it. It cannot be baseline controls, because pure controls don't have them. So, while I have not figured it out yet, I can offer a tidbit from the paper. "In addition, the magnitudes and significance levels obtained in this within-village analysis are broadly similar to those found when comparing treatment to pure control households (Online Appendix Table 38), with three exceptions. First, the treatment effect on assets is larger when estimated across villages than within villages." So, it looks like they prefer the 104.56 to the zero...

    I'll let you know if I figure it out. I'll also forward your question to Johannes to see what his answer is...

    Berk.
     
  • Reply to: GiveDirectly Three-Year Impacts, Explained by the Authors   19 hours 50 min ago

    I want to start by thanking Berk, Jeremy, and Johannes for hosting this incredibly interesting analysis over the last few posts. I can say that it's spurring a lot of really interesting debate at IDinsight and among the rest of the cozy SF development community.

    I've been spending some time poring through the papers myself, and I was hoping that someone here could answer what I think is a more straightforward technical question on measurement of spillovers. In H+S '16 Table 3 (which is also Table 37 in the appendix), Column 1 reports spillover effects for the entire sample. Table 38, Column 4 in the appendix also reports spillover effects for the entire sample, so I would have expected the estimates to be exactly the same. And indeed they are for most outcomes, making it seem like they are running an identical specification.

    However, there is one critical difference: the estimate of spillovers on assets. For this, the point estimate in Table 3/37 is 1.00, while in Table 38 it is 104.56. Yes, that is a massive difference, going from a precisely-estimated zero to a big positive spillover. Quite possible I'm missing something, but does anyone else pouring through these tables understand this?

    Then, fast-forward to H+S '18, Table 7, column 5. Here the point estimate for spillovers on assets is 1.34. So I'm not really sure how to interpret this compared to H+S '16. Does this mean that whatever is happening with asset spillovers, it's staying pretty constant (as suggested by Table 3 in H+S '16), or am I to believe that there were initially positive spillovers that have disappeared 3 years later?

    Happy if someone has this figured out and can enlighten me. Thanks!

  • Reply to: GiveDirectly Three-Year Impacts, Explained by the Authors   23 hours 49 min ago
    Hi Sean,

    Answers inserted between your questions below:

    Why do we have to assume that the negative spillovers WITHIN the within-village sample apply more broadly?

    BO: We don't have to assume that. We simply don't know.

    If we don't have to assume that -

    a. what is the best PLAUSIBLE guess as to what happened to those households that (may have) experienced spillovers?

    BO: I don't know. But, for one example, you could imagine that poor people are engaged in similar small enterprises in these villages and removing the credit constraint to some allows them to enter the market (and perhaps even grow a bit), but at the cost of losses to existing enterprises.

    b. is there available data on what happened to the other households WITHIN the village, who were neither the a) treatment group, b) spillover group?

    BO: Not in this study. Some studies do this, some don't. I'll have a post on this tomorrow...

    Thank you, again.

    BO: No problem,

    Berk.
  • Reply to: GiveDirectly Three-Year Impacts, Explained by the Authors   1 day 29 min ago

    That's really interesting, Berk. Thank you for the response!

    Final question - to anyone, really, but Berk would welcome your thoughts. Of course if Jeremy or Johannes want to jump in - please do!

    Berk, I was interested in your response to the chart in the CGD blog post that looked at 235 vs 217 vs 188, and its accompanying interpretation, which I think you disagree with. But ... how DO we make sense of the negative spillovers - both a) technically and b) substantively?

    Technically, let me just make sure I have it right.

    Treatment - 235
    Within-village Control (Spillover Group) - 188
    Across-village Control (Should be used used to measure ITT) - 217

    Let's cross out the "across-village control."

    Now left with -

    Treatment - 235
    Within-village Control (Spillover Group) - 188

    Why do we have to assume that the negative spillovers WITHIN the within-village sample apply more broadly?

    If we don't have to assume that -

    a. what is the best PLAUSIBLE guess as to what happened to those households that (may have) experienced spillovers?

    b. is there available data on what happened to the other households WITHIN the village, who were neither the a) treatment group, b) spillover group?

    Thank you, again!

  • Reply to: GiveDirectly Three-Year Impacts, Explained by the Authors   1 day 1 hour ago
    Hi Sean,

    Thanks. On (1), yes. On (2), my statement is just about HS(18), while the quote from HS' guest blog post is more generally about cash transfers. So, they don't really need to be reconciled per se.

    There is too solid evidence, true, on consumption, mental health, nutrition, but they're all contemporaneous with transfers (or measured soon afterwards), and may not last after transfers stop (Sandefur covered this bit well in his CGD blog post last wee). To me, that's not really news - the protection role is proven: and, some people think that's all you should expect from cash transfers. Some, however, were hoping for more: one-off programs should get you over a hump, to a much better equilibrium...

    My feeling on the latter is that we have a recent, still small, body of evidence that suggests that UCTs to general populations (rather than selected ones, such as microenterprise owners, etc.) may speed convergence to a slightly better steady-state equilibrium, but perhaps will not get them over a poverty trap by removing credit constraints. There may be exceptions (target population being suitable, adding intensive training to cash a la TUP programs, etc.), but we don't have the evidence that they have sustained, long-term effects that are large.

    Berk.