surveyors were fairly successful at maintaining respondent consistency. In the observational data the primary respondent accounted for 79.8 percent of all reports at the weekly level and the fraction drops somewhat to 77.5 percent in the monthly reports. Despite the qualitatively similar averages, the difference between the two is significant at the 90 percent level of confidence. We therefore estimate recall effects with an additional indicator variable that takes the value 1 if the respondent was the designated primary respondent (for weekly reports aggregated to the monthly level this becomes the fraction of weeks that the primary respondent answered). For the reported number of acute illnesses and total self-medication we find small respondent effects (when the respondent was the primary respondent, reports increase) with significance at the 90 percent level of confidence. In these cases, the estimated recall impact decreases from 0.57 to 0.55 (number of acute illnesses) and from 0.95 to 0.947 (total self-medication) and the declines are not statistically significant. For the other outcome variables considered here, we are unable to detect respondent effects in these specifications (with p-values on respondent identity ranging from 0.32 to 0.76) and there is no impact on the estimated size of the recall effects.

_Income or Education?_ Finally, heterogeneity in the recall impact by PCE could be driven by covariates correlated with PCE rather than PCE itself. Although most naïve estimates of income-elasticity used in the health literature suffer from similar interpretational issues, it is possible that education (which is highly correlated with PCE) rather than PCE drives the greater recall impacts among the poor. We re-estimate the heterogeneous impact of the recall period with PCE at the household-level with an additional interaction between the education of the household head and the recall period. These regression results are reported in Appendix Table 2. Across the outcomes considered here, we find two consistent patterns. First there is a small drop in the size of the recall impact and in its interaction with PCE, suggesting that part of the heterogeneous impacts could indeed arise from differences in education. However, for all our outcome variables, the qualitative (and quantitative) finding that recall impacts are higher for the poor remains robust to the inclusion of the additional interaction. Second, for all specifications, the interaction with education is in the expected direction—the impact of the recall period is lower for more educated households—but the effect sizes are small and generally lack precision (except for the labor impact of acute illness, which is significant at the 90 percent level of confidence).

# **Conclusion**

Common sources of information concerning health conditions—the National Sample Surveys in India and the Living Standards Measurement Surveys of the World Bank—use between 2 weeks and a month as a standard recall period for illnesses. Ordinarily, we assume that decisions about recall length don‘t bias results. In this paper, we find that they do; the choice of recall period has substantive implications. With shortened 17