was interviewed using the weekly-recall module. In the second month, the sub-sample was split into two randomly assigned groups. The ―treatment‖ group continued with weekly recall surveys for another 4 weeks, while the ―control‖ group was administered a single survey collecting data on the basis of monthly recall at the end of the month. The randomization was privately completed using STATA and was stratified by locality. To check the randomization, we compared household characteristics for the control and treatment groups and found that the two sets of households similar on all observable criteria.

The two data sources are complementary. In the ―observational‖ data – that is, the data from families that were tracked for two years – many individual characteristics are held constant over time, including general healthiness and innate ability to recall events. The large number of observations leads to greater precision in the estimation of recall effects. However, a drawback to using this type of data arises from its vulnerability to temporal autocorrelation of illness patterns that differ between individuals and could systematically influence individuals‘ recollections of events. This temporal autocorrelation would be particularly problematic if the localities in the two different waves differed in their morbidity and treatment seeking patterns. In our analysis, we attempt to tackle this problem by including individual fixed-effects and a full set of monthly dummies. Nonetheless, we cannot entirely rule out the possibility that our results are biased by this autocorrelation.

In the ―experimental‖ data, the autocorrelation of illnesses is entirely controlled for by the randomization process. On the other hand, the experimental sample is not large enough to produce precise heterogeneous treatment effects. In particular, for the observational data, there are a minimum of 36 weekly observations and 5 monthly observations for 300 households, while in the experimental data the sample size is reduced to 4 weekly observations and 1 monthly observation for 205 households. Therefore, we use the experimental data to verify the average treatment effects from the observational estimates, but we rely on the observational data to further examine heterogeneity in the treatment, particularly across income groups.

Summary statistics for all individuals and households in the observational sample are presented in Table 1. The median age of individuals in our sample is 22, 50 percent of all individuals are either illiterate or have less than primary education and are living in nuclear households with an average of 5.4 members per household. About 50 percent of respondents of age greater than 15 are employed, resulting in 1.5 income earners per household, although only a third of income earners are employed in the formal sector (public and private). Table 1 also presents summary statistics by income group. Per capita income among rich households is more than three times that among poor households. Since both household size and the number of employed adults per household are similar across income groups, variation in income levels is mainly due to differences in the earning capacity of employed adults. As expected, average age and education are higher for the rich, who also 7