Cash Transfers and Consumption Smoothing in a Developing Country Appendix

Appendix A Propensity Scores and Reconstructed Quasi-PMT Scores To estimate the probability that household h receives any UCT disbursements, D, we consider the following specification, which roughly approximates information on household h available to enumerators and local officials in mid-2005,1   house head welfare P r(disbursementsh > 0) = F βXfam + γX + αX + δX + ζ > 0 , h h h h h (A.1) All right-hand variables are observed in at baseline in early 2005: Xfam is a vector of demographic variables h including household age structure, gender breakdown; Xhouse includes variables pertaining to the quality of h the physical structures in which household h lives; Xhead includes characteristics of the head of the household, h welfare Xh includes indicators for employment among household members, prior participation in government welfare programs, and amount of land owned; F is the logistic CDF;2 and ζh captures all variables unobservable to the econometrician but possibly observable to program administrators. We also control for province fixed effects to subsume some of the regional differences in targeting infrastructure (among other things). A full elaboration of the coefficient estimates was reported in Table 2.3 Given our large set of dummy variables, there is little advantage to estimating equation (A.1) nonparametrically.4 As discussed in Section 2.2, although we made every effort to reconstruct the underlying PMT scores using available data, the resulting scores were not discriminating enough to allow for a fuzzy regressiondiscontinuity research design. After transforming applicable questions in Susenas 2005 into the corresponding variable-specific eligibility criteria, we apply the district-specific PMT coefficients corresponding to the given variables to produce a measure Peh , which reflects a data-constrained approximation to the actual PMT scores based on the original eligibility survey.5 According to program guidelines, households with PMT scores above the 70th percentile should qualify for benefits. We take this rule to our estimates Peh in search of a potential discontinuity. Unfortunately, as seen in Figure A.1, no such discontinuity can be found—perhaps unsurprisingly given the evidence on leakage and undercoverage. Moreover, the actual probability of UCT receipt looks quite similar across the distribution of the estimated propensity scores Pbh . Yet, if we predict the probability of program receipt using Peh as the only regressor—effectively fixing (β, γ, δ, α) in equation A.1 at the district-specific PMT coefficients—and accordingly reweight households in the control group, the balance at baseline is much worse than when using our arguably more flexible approach in equation (A.1). This can be seen by comparing the effect of reweighting the control group in Figure A.2, which uses Peh , and Figure 4 discussed in the paper, which uses our estimated propensity scores. This balance differential is intuitive because our propensity score model is based on a richer set of variables plausibly in the information set of local officials engaged in community-based alongside or possibly in defiance of official targeting. 1 Moreover, we pursue an additive specification in keeping with the weighting procedure used to construct the original PMT scores. 2 In unreported results, we find that a probit estimator yields identical results. 3 The official eligibility survey grouped several response categories to questions in Susenas concerning household characteristics. Whether one leaves the individual responses as separate indicators (in a fully saturated sense) or groups them according to the rubric in the original survey does not matter for our key qualitative findings. 4 Doing so using the Klein and Spady (1993) estimator yields an estimated propensity score that has a 0.97 correlation with the computationally simpler parametric logit. 5 Prior to this, we rescale the coefficients to ensure that they sum to 1 after dropping the questions not available in Susenas. Figure A.1: Comparing Propensity Score Estimates and Approximated PMT Scores 1 1 actual Pr(BLT receipt) ideal Pr(BLT receipt) .8 .8 .6 .6 .4 .4 .2 .2 0 actual Pr(BLT receipt) ideal Pr(BLT receipt) 0 0 .2 .4 .6 .8 binned CDF of approximated PMT score 1 0 .2 .4 .6 .8 binned CDF of predicted Propensity Score: Pr(BLT receipt | X) 1 Notes: LEFT—The circles capture the share of UCT (BLT) recipients within the given bin where the bins are 0.05 width slices of the CDF of the quasi-PMT scores approximated using the procedures described in the text. The dashed vertical line constitutes the 30% threshold above which households were (in theory) supposed to receive the program. RIGHT—The circles capture the share of UCT (BLT) recipients within the given bin where the bins are 0.05 width slices of the CDF of the propensity scores obtained from estimating a binary version of equation (A.1) by maximum likelihood where ζh is logistic distributed. Figure A.2: Baseline Expenditure Distributions by Treatment Status 0 .2 kernel density .4 .6 .8 Treatment Control, Reweighted Control 10 12 14 log household expenditure/capita, 2005 (baseline) 16 Notes: All distributions estimated using Epanechnikov kernel and a rule-of-thumb bandwidth. The “Control (Reweighted)” observations are adjusted using inverse probability weights (IPW) based on normalized estimated odds of treatment ω e = Pe/(1 − Pe), where Peh is as described in Appendix A. B Further Empirical Results This appendix provides tables and discussion of additional empirical results mentioned in the paper. B.1 Validating the Exogeneity of Variation in Transfers per Capita Table B.1 shows that the UCT program had no effect on household size over the period from early 2005 to early 2006, and Table B.2 shows that the size of the informal tax levied on UCT recipients is uncorrelated with household characteristics. The results in these tables support the claim in the paper that the residual variation in transfers per capita is exogenous with respect to a number of other factors potentially associated with expenditure growth over the period under study. B.2 Heterogeneity by Age of Household Head In Table B.3, we allow the estimated treatment effects τ to vary by the age of the household head. We do this in columns 1 and 3 by interacting the treatment indicators with a quadratic in age and in columns 2 and 4 by interacting those indicators with three bins comprising roughly the bottom three quintiles of the age distribution. The marginal effects reported in Figure 6 correspond to the quadratic interactions in columns 1 and 3. While we observe an interesting nonlinear age profile in the treatment effects consistent with life cycle behavior, the estimates underlying Figure 6 are somewhat imprecise. B.3 Ruling Out Spillover Effects via Local Informal Redistribution In Table B.4, we consider the effects of informal redistribution of the UCT benefits within villages using the approach described in Section 4.4. As noted there, the results withstand this test, which reassigns all control households to the given treatment group within a village if there are any reports of redistribution. B.4 Using Geographic Fixed Effects as Instruments for Delayed Disbursement In Table B.5, we use geographic fixed effects as instruments for the arrival of the delayed second disbursement by early 2006. As discussed in the paper, this requires the strong and arguably implausible assumption that geographic FE only explain variation in consumption growth across households through their effect on the timing of cash transfers. Nevertheless, in doing so, we find results that are largely consistent with the reduced form approach to geography pursued in the main analysis and preceding specification checks. In particular, we find that the differential treatment effects remain qualitatively unchanged. However, the coefficients increase by about 50 percent in magnitude at the expense of some precision. The increase in coefficients suggests that the reduced form estimates in the paper may be downward biased due to our inability to observe actual dates of transfer receipt (or scheduled receipt for those still awaiting the second disbursement). However, underidentification tests suggest that the instruments may be collectively weak, which might lead to upwardly biased second stage estimates. Overall, though, the instrumental variables estimates in this table support the main reduced form estimates in the paper. Tables Table B.1: UCT Benefits Had No Effect on Household Size Estimator τ10 : disbursement 1 τ21 : disbursement 2 τ20 ≡ τ21 + τ10 : disbursements 1+2 Reweighted Propensity Score Control(s) Xh Controls Number of Households R2 OLS IPW Double Robust (Pbh ) (Xh ) (3) (4) Control Function (5) (1) (2) -0.014 (0.059) 0.014 (0.065) 0.069 (0.127) -0.090 (0.133) 0.069 (0.129) -0.090 (0.135) 0.058 (0.116) -0.045 (0.116) 0.095 (0.117) -0.115 (0.127) 0.0002 (0.030) -0.021 (0.078) -0.022 (0.079) 0.013 (0.075) -0.020 (0.080) No No No Yes No No Yes Yes No Yes No Yes Yes Yes No 9,011 0.006 9,011 0.011 9,011 0.011 9,011 0.131 9,011 0.016 Notes: All columns estimated by linear probability regressions with ∆ log household size between 2005 and 2006 on the left hand side. Columns 2-5 are estimated by weighted least squares where the weights for treatment households equal one and the weights for control households are given by the normalized ω b = Pb/(1 − Pb). All columns include province fixed effects. Standard errors are clustered by village and computed using a block bootstrap with 1000 repetitions. Table B.2: Idiosyncratic vs. Spatial Variation in the “Tax” on UCT Recipients household size, t − 1 Fixed Effects (FE) Xh,t−1 controls p-value joint statistical significance Number of Households R2 (1) (2) (3) (4) -0.001 (0.004) 0.001 (0.002) 0.003 (0.005) -0.000 (0.002) Province Subdistrict Province Subdistrict No No Yes [0.52] Yes [0.99] 2,410 0.113 2,410 0.822 2,410 0.187 2,410 0.827 Notes: All columns are estimated by linear probability regressions of the following specification: P r(transf erh < f ull amount | disbursements > 0) = βXh,t−1 + θF E + eh , where Xh,t−1 includes all the baseline household characteristics used to estimate propensity scores. Standard errors clustered by village. Table B.3: Heterogeneity by the Age of the Household Head Growth Horizon disbursement 1 disbursement 1 × age of HH head disbursement 1 × age of HH head squared 2005-2006 (1) (2) 0.235 (0.231) -0.016 (0.009)∗ 0.000 (0.000)∗∗ disbursement 1 × age of HH head ∈ [13, 36] disbursement 1 × age of HH head ∈ [37, 46] disbursement 1 × age of HH head ∈ [47, 56] disbursement 2 disbursement 2 × age of HH head disbursement 2 × age of HH head squared 0.234 (0.212) -0.005 (0.008) 0.000 (0.000) disbursement 2 × age of HH head ∈ [13, 36] disbursement 2 × age of HH head ∈ [37, 46] disbursement 2 × age of HH head ∈ [47, 56] disbursement 1+2 disbursement 1+2 × age of HH head disbursement 1+2 × age of HH head squared 0.469 (0.191)∗∗ -0.020 (0.008)∗∗∗ 0.000 (0.000)∗∗∗ disbursement 1+2 × age of HH head ∈ [13, 36] -0.086 (0.058) -0.116 (0.055)∗∗ -0.183 (0.062)∗∗∗ 0.025 (0.039) 0.082 (0.050) 0.069 (0.048) 0.075 (0.049) 0.039 (0.037) 0.336 (0.258) -0.014 (0.011) 0.000 (0.000) -0.189 (0.264) 0.007 (0.011) -0.000 (0.000) 0.147 (0.189) -0.007 (0.008) 0.000 (0.000) -0.004 (0.049) -0.047 (0.041) -0.108 (0.050)∗∗ disbursement 1+2 × age of HH head ∈ [37, 46] disbursement 1+2 × age of HH head ∈ [47, 56] Number of Households 0.014 (0.042) 2005-2007 (3) (4) 9,011 9,011 -0.006 (0.056) 0.056 (0.076) -0.013 (0.077) -0.067 (0.074) 0.060 (0.053) -0.081 (0.069) -0.020 (0.069) -0.067 (0.067) 0.054 (0.044) -0.025 (0.062) -0.033 (0.058) -0.133 (0.056)∗∗ 6,992 6,992 Notes: Significance levels: ∗ 10% ∗∗ 5% ∗ ∗ ∗ 1%. The dependent variable in all specifications is ∆log household expenditures per capita between 2005 and 2006/2007. All columns are estimated by weighted least squares where the weights for treatment households equal one and the weights for control households are given by the normalized ω b = Pb/(1 − Pb). All columns include a 5th order polynomial in the propensity scores that is allowed to vary by treatment and control. All columns include province fixed effects. Standard errors are clustered by village and computed using a block bootstrap with 1000 repetitions. Table B.4: Reassigning Control Households to Treatment Groups Estimator τ10 : disbursement 1 τ21 : disbursement 2 τ20 ≡ τ21 + τ10 : disbursements 1+2 Reweighted Propensity Score Control(s) Xh Controls Number of Households R2 τ10 : disbursement 1 τ21 : disbursement 2 τ20 ≡ τ21 + τ10 : disbursements 1+2 Reweighted Propensity Score Control(s) Xh Controls Number of Households R2 OLS IPW (1) (2) Double Robust (Pbh ) (Xh ) (3) (4) Control Function (5) -0.051 (0.030)∗ 0.022 (0.032) Short-Term: 2005-2006 -0.077 -0.076 -0.081 (0.035)∗∗ (0.033)∗∗ (0.033)∗∗ 0.036 0.038 0.042 (0.036) (0.036) (0.033) -0.047 (0.032) 0.034 (0.035) -0.030 (0.015)∗∗ -0.040 (0.020)∗∗ -0.038 (0.020)∗ -0.039 (0.019)∗∗ -0.013 (0.018) No No No Yes No No Yes Yes No Yes No Yes Yes Yes No 9,007 0.045 9,007 0.079 9,007 0.083 9,007 0.153 9,007 0.099 0.005 (0.040) -0.019 (0.043) Medium-Term: 2005-2007 -0.012 -0.016 -0.003 (0.039) (0.039) (0.036) -0.016 -0.015 -0.022 (0.043) (0.041) (0.037) 0.016 (0.040) -0.020 (0.043) -0.014 (0.020) -0.028 (0.022) -0.031 (0.024) -0.026 (0.022) -0.005 (0.022) No No No Yes No No Yes Yes No Yes No Yes Yes Yes No 6,994 0.044 6,994 0.059 6,994 0.062 6,994 0.144 6,994 0.074 Notes: Significance levels: ∗ 10% ∗∗ 5% ∗ ∗ ∗ 1%. This table reproduces the baseline estimates after first reassigning all control households (D = 0) to one of the two treatment levels (D = 1, 2) if recipients in their village report being informally taxed during disbursement rounds one and/or two for the purposes of redistribution to non-recipients. As in Table 5, Columns 2-5 are estimated by weighted least squares where the weights for treatment households equal one and the weights for control households are given by the normalized estimated odds of treatment ω b = Pb/(1 − Pb), where the normalization is over the entire sample for the given time horizon. Using the Crump et al. (2009) procedure, we trim 41 households in the upper tail of the estimated propensity scores, Pb, and do the same in the OLS regressions for comparability. Column 3 controls linearly for the propensity score and column 5 for a fifth-order polynomial in the propensity score allowing it to vary by treatment and control. Column 4 controls for all covariates Xh used to estimate the propensity score. The coefficients on these additional terms in columns 3-5 are suppressed for presentational purposes. All columns include province fixed effects. Standard errors are clustered by village and computed over the entire two-step process using a block bootstrap with 1000 repetitions. Table B.5: Using Geographic Fixed Effects as Instruments for Staggering Estimator τ10 : disbursement 1 τ21 : disbursement 2 OLS IPW (1) (2) -0.072 (0.067) 0.063 (0.087) Double Robust (Pbh ) (Xh ) (3) (4) Control Function (5) Panel A: District FE as Instruments -0.132 -0.143 -0.129 -0.119 (0.080)∗ (0.084)∗ (0.073)∗ (0.077) 0.130 0.147 0.125 0.134 (0.107) (0.111) (0.096) (0.101) τ20 ≡ τ21 + τ10 : disbursements 1+2 -0.01 (0.025) -0.002 (0.036) 0.005 (0.033) -0.004 (0.031) 0.015 (0.032) Number of Households R2 Overidentification Test (p-value) First-stage F Statistic Underidentification Test (p-value) 9,011 0.045 0.506 11.34 0.850 9,011 0.099 0.373 10.28 0.692 9,011 0.102 0.363 10.27 0.861 9,011 0.181 0.213 10.01 0.627 9,011 0.118 0.335 10.36 0.561 τ10 : disbursement 1 τ21 : disbursement 2 -0.099 (0.058)∗ 0.099 (0.074) Panel B: Subdistrict FE as Instruments -0.152 -0.153 -0.145 -0.130 (0.080)∗ (0.076)∗∗ (0.069)∗∗ (0.067)∗ 0.157 0.161 0.146 0.149 (0.103) (0.097)∗ (0.088)∗ (0.088)∗ τ20 ≡ τ21 + τ10 : disbursements 1+2 -0.0002 (0.021) 0.005 (0.032) 0.008 (0.030) 0.001 (0.026) 0.019 (0.027) Number of Households R2 Overidentification Test (p-value) First-stage F Statistic Underidentification Test (p-value) 9,011 0.044 0.493 8.012 0.988 9,011 0.098 0.434 7.737 0.984 9,011 0.102 0.433 7.728 0.973 9,011 0.180 0.406 7.506 0.765 9,011 0.118 0.442 7.742 0.437 Notes: Significance levels: ∗ 10% ∗∗ 5% ∗ ∗ ∗ 1%. The dependent variable in all specifications is ∆log total monthly household expenditures per capita between 2005 and 2006. Panel A instruments for the receipt of disbursement 2 using 297 district fixed effects, and Panel A uses 589 subdistrict fixed effects instead. All columns control for province fixed effects in the second stage. Standard errors are clustered by village and computed using a block bootstrap with 300 repetitions. The overidentification test is a Hansen test of the null hypothesis that the exclusion restrictions are valid. The underidentification test is a Kleibergen-Paap Lagrange multiplier test of the null hypothesis that the system of equations is underidentified. See the notes to Table 5 in the paper for further details on the estimators and specifications. C Data Construction Merging Across Survey Waves. The main panel dataset is constructed by merging household identifiers across the three waves of Susenas enumerated in early 2005, 2006, and 2007. We first construct a balanced two-year panel between 2005 and 2006 by matching along (i) province-district-subdistrict-village-sampling ID-household ID and (ii) household head names in the 2005 and 2006 Susenas panels. While a traditional merge along strict geographic identifiers provides a balanced panel of 9, 797 households, significant discrepancies in household characteristics (including first names of household members) across waves indicate that survey administrators did not ensure the time-consistency of household presence in the physical location of prior enumeration. A name-matching algorithm provided by Robert Sparrow generated an initial balanced panel of almost 8500 households, and through further manual inspection, we added an additional 548 households. We then merged this balanced two-year panel of 9,048 households with the subset of all households enumerated in early 2007 also reporting enumeration in 2005 (in a specific survey question verified by enumerators). This process generated a balanced three-year panel comprising 7,014 households. A number of households are lost between 2006 and 2007 as a result of a change in the sampling rather than direct attrition by households. Attrition. The data structure pose a nonstandard attrition problem. Although attritors appear much more similar to non-recipients than recipients (see Table 1), we do not know which attritors between 2005 and 2006 actually received the UCT. We observe recipient status among the 2,034 attritors between 2006 and 2007, and reassuringly the ratio of recipients to non-recipients remains essentially unchanged across years. Although inter-survey attrition is potentially a non-negligible problem, we ignore its consequences in the main results presented below. Nevertheless, all results are robust to reweighting the sample so as to account for the probability of attrition as a function of all observable characteristics used to predict treatment. The lack of contrast between attrition probability-weighted and unweighted estimates provides evidence against attrition being a source of misspecification that might confound identification of the causal average partial effect of interest (see Solon et al., 2013).1 Variable Construction. We use the Susenas datasets to construct all of the expenditure outcomes, baseline controls (see Table 2), health shocks and participation in other social programs (see Table 10), and information on UCT benefits. The following variables were constructed based on data recorded in the Village Potential or Podes administrative census from April 2005: bank presence in the subdistrict, log travel distance to the (sub)district capital, log travel distance to the post office, village road paved, village accessibility by land, the incidence of natural disasters by type, and the ranking of the President’s political party in the 2004 local village election. We are unable to match the data in Podes to Susenas villages for a small number of households in Papua. However, the main baseline results in Table 5 are robust to dropping these households. Data on rainfall shocks were obtained from NOAA/GPCP sources. The total amount of rainfall during the given growing/harvest season where (i) seasons are 12 month intervals beginning with the first month of the province-specific wet season in a given year, and (ii) rainfall at the village level is based on rainfall levels recorded interpolated down to 0.5 degree (latitude/longitude) pixels between rainfall stations. We obtain data on the regional CPI and the district-specific poverty lines (see Table 10) from the Central Bureau of Statistics. The former measures were mapped to villages based on the great circle distance from the centroid of the village’s district to the centroid of the city in which the CPI measure was taken. The (log) distance to Jakarta was computed as the great circle distance from the centroid of each district to the centroid of Jakarta 1 A similar argument can be made for why we prefer not use the sampling weights provided in Susenas. Although we do not use those weights in the paper, doing so leaves key results are unchanged, and the lack of contrast between weighted and unweighted estimates provides evidence against the sort of misspecification that weighting might help correct in our context.