underlying all matching studies is to explain why, if these two groups are so similar, only one group ended up taking the intervention. Our rich data and experiment help in addressing both concerns. We have up to 18 months of pre-intervention financial data for these clients, so can match not only on current financial behavior, but on the monthly trajectory of this behavior over many months. This helps alleviate concerns about dynamic selection. Moreover, by only matching to individuals in the control group (and not those in the treatment group who did not take up treatment), we have a plausible reason why some individuals do not take up treatment – they were not invited to under the random invitations.

Difference-in-differences further enables us to difference out any time-invariant unobservable differences between the two groups. Thus, if those who participate in training or coaching always tend to be better re-payers than those who do not, we can difference this out. The underlying assumption for difference-in-difference analysis is that of a common trend, so that the two groups would follow the same time paths as each other in the absence of an intervention. This assumption is more credible if the individuals are more similar to begin with (which is where matching helps), and if we see the two groups have the same dynamics prior to the intervention. Researchers relying on survey data typically do not have multiple rounds of pre-intervention data with which to test this assumption. In contrast, the monthly administrative data enables us to not only test whether the two groups follow similar linear trends prior to the intervention, but also to test whether they follow the same non-linear trend. To test this, we estimate over the pre-intervention period: And test that all the β’s are jointly zero.

As we move away from the pure experiment, there is no one universally agreed control group. We examine several different plausible ways of choosing this control group. We then view the resulting estimates as more credible if these different methods give similar results, even though they end up choosing different individuals from the control group to match to those who actually take up treatment in the treatment group.

We begin by estimating the difference-in-differences estimator using the full control group. If there is self-selection into treatment, those receiving training or coaching will differ in levels, and potentially trends, from this full control group. A first step towards refining the control group to more comparable individuals is to restrict the analysis to individuals in the common support of the propensity score. For this approach, we estimate the propensity score as a function of gender, and pre-treatment monthly levels of all five outcomes. This involves matching on 73 variables in total, and eliminates 38% of the control group and 22% of the treatment group for coaching. We then go further by choosing the nearest neighbor within this common support for each client who received treatment. Using all the outcomes simultaneously to form these matches has the advantage of making clients similar on average in terms of existing financial behavior, but, because it is attempting to match on so many variables, may not match especially well on any particular single outcome. We therefore also consider two alternatives to forming the propensity score and then matching on the nearest neighbor. The first is to use Lasso to choose a parsimonious set of variables to match on. This chooses 8 of the 73 variables to use in forming the match. The second, and our 13