Who Benefits From Childhood Deworming? Heterogeneous Treatment Effects by Age and Gender on Long-Run Human Capital and Labor Market Outcomes
Note: This project was implemented using the ML Platform for Trustworthy Human-Agent Research Production.
School-based deworming programs have reached hundreds of millions of children across sub-Saharan Africa and South Asia, scaling up from a landmark randomized trial in Kenya. Whether benefits from these programs are concentrated among specific groups (younger children who were treated during more critical developmental windows, or girls who face steeper labor market barriers) has direct implications for program design. We apply double/debiased machine learning (DoubleML) and causal forest estimation to the Kenya Life Panel Survey follow-up of the Miguel and Kremer (2004) deworming trial, estimating long-run effects of childhood deworming on adult BMI, underweight prevalence, educational attainment, and employment, and characterizing heterogeneity by age at treatment and gender. The developmental-window hypothesis is not confirmed by formal inference: no estimated heterogeneity survives Romano-Wolf multiple testing correction (minimum adjusted p = 0.29). We show that the null is unlikely to be an artifact of attrition or methodological choices. The design is, however, underpowered for plausible nutritional effect sizes at the 20-year horizon. Against this primary null, we document three directionally consistent but fragile findings that motivate further investigation at scale.
The Primary School Deworming Project (PSDP), conducted in western Kenya between 1998 and 2001, randomly assigned 75 primary schools to receive deworming at different times. Miguel and Kremer (2004) found substantial reductions in school absenteeism. Hamory et al. (2021) followed the same cohort two decades later and found significant gains in earnings and consumption. Evidence from this trial informed the Kenya National School-Based Deworming Programme, which scaled to millions of children from 2009, and programs like the Deworm the World Initiative (Evidence Action), which now operates across Kenya, India, Ethiopia, and Pakistan.
A natural next question for program designers at these scales is whether benefits are concentrated in ways that could guide targeting. Two hypotheses have theoretical grounding. First, the developmental-window hypothesis: children who were younger at the time of treatment were dewormed during more critical periods of physical and cognitive development, so effects on adult human capital should be larger for them. Second, a gender-differentiated labor market pathway: girls in rural Kenya face competing demands (household labor, early marriage pressure) that make the school attendance and eventually the employment margin more binding. If deworming eased the health constraint on attendance, the downstream effects on labor market participation may be larger for women.
These questions are exactly the kind that standard subgroup analysis handles poorly. Splitting a sample by age tercile or gender and comparing means pre-commits to a particular partition, is sensitive to the choice of cutpoint, and does not adjust for the correlation between moderators and other baseline covariates. Double/debiased machine learning with causal forest estimation offers a more principled approach. The causal forest estimates a conditional average treatment effect (CATE) for each individual as a flexible function of baseline covariates, without pre-committing to a partition. The best linear predictor (BLP) of the CATE then provides valid inference on pre-specified moderators, accounting for the uncertainty in the forest estimates themselves. Together, the two methods are strictly more informative than a table of interaction terms and, crucially, control the false discovery rate across the full set of heterogeneity tests via Romano-Wolf stepdown correction.
This repository applies that methodological apparatus to a question where the answer matters for operational program design. The honest answer, as it turns out, is a carefully characterized null.
The analysis makes use of two waves of the Kenya Life Panel Surveys:
Kenya Life Panel Surveys (KLPS). The KLPS tracked the cohort of the PSDP trial (Kremer and Miguel, 2004), which enrolled 75 schools and approximately 30,000 pupils, into adulthood across four waves. This analysis makes use of the most recent two waves: KLPS-3 (2011-2014, approximately 10-15 years post-treatment) and KLPS-4 (2017-2022, approximately 17-22 years post-treatment). The analysis sample consists of the 7,527 PSDP-enrolled pupils with confirmed treatment assignment, excluding the Girl Sponsorship Programme subsample. Attrition to the tracked sample is roughly 33% for nutritional outcomes and employment and 44% for education (see Figure 1).
PSDP baseline (1998). The KLPS builds on the original trial, evaluated in Kremer and Miguel (2004). 75 schools were randomized into three groups: full treatment (deworming beginning in 1998), partial treatment (beginning in 1999), and comparison (no treatment during the study period). For the present analysis, the baseline data provide school identifiers, treatment assignment, and limited pupil-level covariates.
In the following, we define treatment assignment, primary outcomes, and moderators:
Treatment definition. The primary analysis pools full-treatment and partial-treatment schools into a single treated group. At a 15-20 year horizon, the one-year difference in treatment timing has plausibly attenuated. The pooled estimand is a convex combination of what we call direct-early effects (full-treatment schools, dewormed from 1998), direct-late effects (partial-treatment schools, dewormed from 1999), and spillover-late effects (partial-treatment pupils who were untreated in 1998 but exposed to neighboring full-treatment schools). A formal test of equality between the full-treatment and partial-treatment ATEs fails to reject at the 5% level for all four outcomes (p = 0.20, 0.48, 0.055, 0.94 for BMI, underweight, education, and employment respectively). The restriction to full-treatment vs. comparison only is reported as a sensitivity check throughout.
Outcomes. We examine four outcomes organized by the causal chain we hypothesize: adult BMI and underweight prevalence (KLPS-3, nutritional status), years of schooling completed (KLPS-3, human capital), and employment status (KLPS-4, labor market). Earnings are excluded: the KLPS-4 E-Module has 75% attrition relative to the original PSDP cohort, producing a sample too selected for credible causal inference. Education has 44% missingness on the primary variable, non-differential by treatment (p = 0.85), and education has 44% missingness on the primary variable, non-differential by treatment (p = 0.85), and results are treated as suggestive rather than definitive.
Moderators. Two moderators are pre-specified: age at treatment in 1998 (primary, testing the developmental-window hypothesis) and gender (secondary, testing the labor market margin hypothesis). Age at treatment has 14-21% missingness in year of birth and is imputed via multiple imputation by chained equations (MICE) with 20 imputations, using baseline grade, school-level clustering, and parental education as predictors. A cross-wave consistency check revealed that parental education reports are unstable across KLPS-3 and KLPS-4 (Spearman rho: father 0.16, mother 0.29), so parental education is retained as a noisy control in outcome models but excluded from the imputation model. A complete-case sensitivity check restricting to respondents with non-missing year of birth is reported alongside the primary results. Covariate balance across treatment groups is shown in Figure 2 below.
The analysis follows the double/debiased ML framework of Chernozhukov et al. (2018). For each outcome
We use cross-fitting, that is, splitting the sample into folds, estimating nuisance functions HistGradientBoosting) for both nuisance functions.
With 73 schools and unconditional intraclass correlation of 0.023, assigning pupils from the same school to both training and test folds leaks the school-level treatment signal into the nuisance model, biasing the orthogonal scores. This makes cluster-aware cross-fitting essential: we enforce school-level fold boundaries throughout via GroupKFold with five folds.
Treatment effect heterogeneity is estimated via a causal forest (CausalForestDML from EconML), which produces an individual-level CATE
The causal forest output is a high-dimensional object that is useful for visualization but difficult to act on directly. The best linear predictor (BLP) of the CATE projects the forest estimates onto the pre-specified moderators using doubly robust orthogonal scores (LinearDML):
This implementation approximates current best practice in Python, with three known limitations relative to the grf package in R. Trees are not fully honest: they do not use separate subsamples for determining splits and estimating leaf means (Wager and Athey, 2018; Athey et al., 2019). Variance estimates are approximate: the bootstrap-of-little-bags approximates the cluster-robust infinitesimal jackknife (Wager et al., 2014; Kleiner et al., 2014), but with 73 clusters, standard tests over-reject and confidence intervals for heterogeneity may undercover slightly (Cameron et al., 2008). BLP inference via LinearDML is asymptotically valid under Neyman orthogonality but finite-sample coverage is not guaranteed (Chernozhukov et al., 2018; 2017).
With two moderators tested across four outcomes, it is important for p-values to account for the multiplicity of comparisons made. We apply a Romano-Wolf stepdown correction separately within each wave family: the KLPS-3 family covers BMI, underweight, and education (six tests) and the KLPS-4 family covers employment (two tests). The bootstrap resamples at the school level. Because the education outcome has a smaller sample (n = 2,769) than BMI and underweight (n = 5,025), effective sample size for education varies across bootstrap replications, making the Romano-Wolf adjustment for education rather conservative.
No estimated heterogeneity survives Romano-Wolf multiple testing correction. All BLP coefficients have Romano-Wolf adjusted p-values above 0.28. The minimum adjusted p-value across all moderator-outcome combinations is 0.29, for the age-times-female interaction on employment. The developmental-window hypothesis (that younger children at the time of treatment benefited more) is not confirmed by formal inference for any outcome. This is the headline result and it holds across all specifications examined. BLP coefficients with Romano-Wolf adjusted confidence intervals are shown in Figure 3 below.
The average treatment effect estimates are themselves informative. BMI shows a pooled ATE of -0.19 points (p = 0.008), running counter to the expected direction of nutritional improvement. Underweight probability shows a pooled ATE of +1.5 percentage points (p = 0.017), also positive, meaning slightly more underweight in the treated group, which is consistent across all treatment contrasts and is a separately puzzling pattern. Employment shows no detectable effect (ATE = +0.013, p = 0.19) and education no detectable pooled effect (ATE = +0.01, p = 0.91). Outcome distributions by treatment group are shown in Figure 4 below. ATE estimates under DoubleML and naive OLS are compared in Figure 5.
Null results require robust support to be credible as evidence of no effect rather than a failure of design, insuffiency of data or analysis. In the following, we address six concerns head on: sample selection within a follow-up process spanning 20 years, the imputation method used to buttress reported age, the choice of leaf size to regularize causal forests, pooled vs. unpooled treatment samples andthe role of spillovers, the noisy parental education proxy, and systematic school-level variation in the nuisance residuals:
Sample selection over 20 years. Roughly 33% of the original study cohort are successfully tracked within the KLPS. This given rise to the concern that, if deworming raised incomes and improved labor market outcomes, treated respondents may have been more mobile and therefore differentially difficult to locate, or alternatively easier to locate through formal employment records. Either pattern would mean the tracked sample differs by treatment status in ways that correlate with the outcomes we measure. The standard approach to this problem due to Lee (2009) constructs sharp nonparametric bounds on the treatment effect under the weakest possible identifying assumption: that treatment can only increase, or only decrease, the probability of being tracked. Lee bounds for BMI of [-0.10, +0.08] straddle zero under this assumption, confirming the null is not driven by differential tracking. Lee bounds for all moderator subgroups are robust to attrition-induced uncertainty, as confirmed through Generalized Lee bounds (Semenova, 2025). We note that the monotonicity assumption itself may be violated if deworming-induced labor mobility made treated respondents differentially reachable; this cannot be ruled out but the bounds are informative conditional on the assumption.
Age imputation. Age at treatment, the primary moderator, is missing for roughly one in five respondents. We opt for imputation via MICE, thereby running the risk of inducing spurious correlation between age and treatment assignment such that the null on the age coefficient could reflect noise rather than an absence of signal. Restricting the analysis to the 4,232 respondents with observed year of birth who also have valid BMI data (4,209 total with observed year of birth in the KLPS-3 sample), however, all BLP age coefficients remain near zero and insignificant across all four outcomes. We conclude that the null on age heterogeneity is unlikely to be driven by imputation.
Forest regularization. The causal forest's minimum leaf size of 50 was chosen to prevent within-school overfitting, but it also constrains the forest's flexibility. If over-regularization were driving the null, a more flexible forest would find statistically significant heterogeneity. We re-ran the forest at minimum leaf sizes of 20 and 100. Mean CATE is stable across all leaf sizes, always close to the ATE. Directional patterns, including the BMI gender gap (female minus male CATE: -0.35 at leaf=20, -0.33 at leaf=50, and -0.21 at leaf=100) and the underweight age gradient (+0.019 to +0.020), are stable across the full regularization range. The contention is that, if a leaf size of 20 providing maximum flexibility still does not produce significant heterogeneity, the null is robust to regularization choices.
Pooled vs. unpooled BMI and treatment spillovers. Given expectations motivated by the developmental-window hypothesis, the pooled ATE on BMI of -0.19 (p = 0.008) appears puzzling. However, when the analysis is restricted to the cleanest treatment contrast of 2-years-treatment schools against no-treatment schools, and excluding 1-year-treatment schools, the BMI ATE drops to -0.08 (p = 0.35), while the partial-treatment effect alone is -0.18 (p = 0.01). This inverts the natural expectation: if childhood deworming genuinely improves long-run nutritional status, the group that received two full years of treatment should show at least as large an effect as the group that received one year. The fact that the opposite is true is the clearest evidence that the pooled BMI result reflects the partial-treatment group's distinct exposure history rather than a genuine nutritional effect of deworming. These pupils were untreated in 1998 while exposed to spillovers from neighboring full-treatment schools. They are a contaminated counterfactual that the pooled estimand cannot separate.
Noisy parental education proxy. The adjustment set includes parental education as a proxy for household socio-economic status, despite evidence for considerable cross-wave instability in how respondents report their parents' education across KLPS-3 and KLPS-4 (Spearman rho: father 0.16, mother 0.29). After correcting a data bug in which raw education codes (100-117 for years 0-14, >=200 for post-secondary) were averaged without conversion to years, parental education now has 70% missingness and a mean of 5.3 years. If the noisy proxy were absorbing treatment-correlated variation rather than genuine confounding, including it could bias scores towards a spurious null. Dropping parental education from the adjustment set leaves ATE and BLP coefficients essentially unchanged: the ATE on BMI shifts from -0.19 (with) to -0.24 (without), a direction that strengthens rather than weakens the result, and no BLP coefficient changes significance. The null is not an artifact of variable selection.
School-level hierarchical nuisance models. The baseline nuisance models treat schools as exchangeable conditional on covariates. However, with a residual ICC of 0.030, some school-level variation remains in the nuisance residuals, which could in principle bias the orthogonal scores. Refitting with school random intercepts via MixedLM and recomputing the orthogonal scores produces directionally consistent but slightly noisier estimates. The BMI ATE attenuates to -0.21 (p = 0.05) under MixedLM nuisance, consistent with the fragility already documented for the pooled BMI result. All BLP coefficients remain null (all p > 0.05). Residual ICC is nearly identical under MixedLM (0.027) and gradient-boosted trees (0.030), confirming that partial pooling provides no material additional absorption of school-level clustering. Substantive conclusions are unchanged.
The school-level minimum detectable effect for this design, with 48 treated schools, 25 comparison schools, average cluster size of 68, and unconditional ICC of 0.023, is 0.41 BMI points (0.13 standard deviations) at 80% power. Under more conservative ICC assumptions of 0.05 and 0.08, the MDE rises to 0.54 and 0.66 BMI points respectively. The 2:1 allocation of schools to treated versus comparison increases the MDE by approximately 15% relative to a balanced design with equal cluster counts per arm: under balanced allocation with 36-37 schools per arm and the same total sample, the MDE at conservative ICC of 0.05 would be approximately 0.45 BMI points rather than 0.54. The observed ATE of -0.24 BMI points falls below the MDE under all but the most favorable assumptions.
The prior expectation was a positive effect: childhood deworming reduces iron malabsorption and caloric competition from worm burden, which should improve nutritional status. Any true effect in the range of approximately [-0.54, +0.54] BMI points is statistically consistent with what we observe under conservative assumptions. The null result on BMI should therefore be read as uninformative about small true effects rather than as evidence against a nutritional pathway. The design was adequate for detecting the large labor market effects documented by Hamory et al. (2021), for which the relevant outcomes have higher signal-to-noise ratios, but not for detecting plausible nutritional effect sizes at a 20-year horizon. The MDE across ICC scenarios alongside the observed ATE is visualized in Figure 6 below.
Against the backdrop of the confirmed null, three patterns are directionally consistent with theory across multiple specifications, though none survives formal inference. We report them here as directions for future work rather than primary results. CATE distributions by moderator tercile are shown in Figures 7a and 7b below. (Note that none of the tercile differences are statistically distinguishable from zero with formal BLP inference.)
Gender and employment under the cleanest treatment contrast. When the analysis is restricted to full-treatment versus comparison schools, the BLP on employment shows a female coefficient of +0.41 (p = 0.03) and an age-times-female interaction of -0.03 (p = 0.03). The direction is consistent with the competing-demands hypothesis: childhood deworming increased employment more for women, concentrated among those who were youngest at treatment. The estimated differential treatment effect by gender is 41 percentage points: conditional on age, childhood deworming is estimated to increase employment by 41 percentage points more for women than for men. Both signals are absent in the pooled sample and rely on 50 schools and 3,406 employment observations, roughly two-thirds of the pooled sample, making these specification-dependent results. They do not warrant a policy recommendation on their own, but they suggest that a larger, better-powered study examining gender-differentiated labor market effects would be worth running.
Underweight age gradient across all specifications. The BLP coefficient on age at treatment for underweight prevalence is consistently negative across the pooled analysis, the full-treatment-only analysis, and the complete-case analysis (p = 0.12-0.13 in all three). A consistently negative coefficient means that children who were younger at treatment show lower adult underweight prevalence, the direction predicted by the developmental-window hypothesis for nutritional outcomes. This pattern never reaches conventional significance but its consistency across specifications that use different samples and make different imputation choices is the most stable directional signal in the project. A study with larger cluster counts would be well-positioned to test this hypothesis with adequate power.
Education under the cleanest treatment contrast. Full-treatment versus comparison schools shows a positive education ATE of +0.29 years (p = 0.015 uncorrected; note this is a subsample analysis not factored into the pre-specified Romano-Wolf correction, n = 1,909). This result is absent in the pooled sample and relies on a subsample of 50 schools with wide standard errors, so it should be treated as potentially reflecting sampling variability. We note it here because it is in the expected direction and the magnitude (roughly one additional third of a year of schooling) appears consistent with what the long-run returns literature would predict from an effective early health intervention.
We see several limitations present in this analysis that go beyond the first-order constraints discussed in the main body of the write-up.
Intention to treat versus treatment on the treated. The estimates throughout are intention-to-treat effects of school assignment to deworming, not effects of deworming receipt. Compliance varied across schools, while spillovers from treated to neighboring comparison schools mean that comparison-group pupils were not entirely unexposed to the intervention.
Heath versus education pathway. Without baseline health data for the comparison group (stool examination and hemoglobin data are available only for treatment schools), we cannot decompose the total effect into health-mediated versus education-mediated pathways. The finding of a negative age gradient on underweight prevalence is consistent with a critical-period mechanism operating through early nutritional improvement, but we cannot rule out alternative pathways operating through schooling quality, peer effects, or labor market entry timing.
KLPS's primary focus and sample size constraints. Later instalments of the KLPS were designed primarily to measure long-run economic outcomes, not to serve as a heterogeneity study. Adult anthropometric outcomes were added to a survey with a different primary focus and the sample is not powered to pick up meaningful effects in that domain. A study designed from the outset to detect nutritional heterogeneity by age and gender would require substantially larger cluster counts than the 73 schools available here.
Intergenerational effects. The KLPS-4 Kids modules contain cognitive assessments, teacher evaluations, and birthweight data for the children of original PSDP respondents. These open a natural extension to intergenerational effects: did childhood deworming affect the next generation? The heterogeneity framework developed here is directly suited to that question: who among the original respondents transmitted the largest gains to the next generation, and whether the age-at-treatment gradient persists into the intergenerational channel.
Bayesian hierarchical nuisance models. A fully Bayesian hierarchical specification of the nuisance functions — placing a prior over school-level random effects and propagating posterior uncertainty through the orthogonal scores — is the natural next step beyond the MixedLM sensitivity check reported above. In this dataset, however, the MixedLM results make a material difference unlikely: residual ICC is nearly identical under partial pooling (0.027) and flat nuisance models (0.030), and substantive conclusions are unchanged. The Bayesian extension would be more consequential in settings with higher residual ICC, stronger school-level treatment effect heterogeneity, or fewer clusters than the 73 available here — conditions under which the frequentist partial pooling approximation would be less reliable. For a worked treatment of Bayesian hierarchical shrinkage in a related heterogeneity context, see the companion bayesian-segmentation repository.
All raw data files are verified against SHA-256 hashes before any analysis runs. Every dataset transformation is logged with a content-addressed hash. Every specification choice is recorded in impl-log.jsonl before the relevant analysis runs, providing a verifiable audit trail rather than a reconstruction from memory. Before fitting any estimator to the data, nuisance model hyperparameters were set and logged; no choices were made after seeing results.
The analysis is fully reproducible from the raw data files via make all (as of 05/28/2026). Dependencies are pinned in pyproject.toml and managed via uv for easy replication.
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