Honduras village cohort
We performed our trial in Honduras’s Copán Department, covering more than 500 km2 of challenging mountainous terrain. We started with a census in 176 villages (Extended Data Fig. 1). Recruitment was strong, with government data indicating that approximately 32,800 individuals were eligible. A total of n = 30,422 (93%) of these individuals participated in our census. From this population, 24,702 (81.2%) individuals (in 10,031 households in the 176 villages) enrolled in our longitudinal study. They committed to randomization, a 22-month intervention (with monthly visits from health workers, if selected), annual or biannual surveys and other data collection.
In the parent randomized controlled trial with all 176 villages, the primary objective was to evaluate a strategy to foster social contagion based on the ‘friendship paradox’, to which 66 villages were assigned1. In the present study on network structural dynamics, we use data from the 110 villages that were assigned to the random-targeting arms of the randomized controlled trial, including data from 66 villages that were ‘partially treated’, at dosages of 5%, 10%, 20%, 30%, 50% and 75%; 22 villages that were fully treated (100% dosage); and 22 villages that were assigned to a control arm of no treatment (0% dosage).
From the individuals in these 110 villages, all residents aged 12 years or older in the study villages at baseline were eligible. No statistical methods were used to predetermine sample size; the analysis includes all eligible residents of the 110 villages in the random-targeting arms of the trial. The community health workers who delivered the intervention belonged to a separate organization and were blinded to the purpose of the study and to its randomization scheme; participants could not be blinded to receiving home visits. For the main analyses, we included respondents who (1) were enrolled and surveyed in both wave 1 and wave 3, and (2) did not change household or village between these waves. As a result, we analysed 8,331 individuals who resided in 4,513 households (for robustness checks, see Supplementary Information). For the mediation analyses that use wave 2, we also required survey completion at wave 2. For the wave-4 persistence analyses, we required eligibility and completion at wave 4 in 56 exogenously chosen villages. Full details are provided in the Supplementary Information.
Exogenous intervention
The maternal–neonatal–child health (MNCH) educational intervention was delivered by trained community health workers. The MNCH intervention included 15 educational modules aimed at maternal, child and neonatal practices that are typical of public-health or development-economics interventions, and it was delivered through the ‘Timed and Targeted Counselling’ method over 22 months (November 2016–August 2018). Content spanned folic acid use, prenatal care, birth planning, immediate and exclusive breastfeeding, neonatal thermal and cord care, diarrhoeal and respiratory disease prevention and management, paternal involvement, and modern family planning and delaying first pregnancy, among other topics. There were up to 22 1–2-h home visits tailored to family circumstances. Overall, 83% of targeted households received at least one visit. The median was 18 and the mean was 14 completed visits. Further details are provided in the Supplementary Information.
As part of the trial, the villages were randomized to several dosages (fractions of households receiving the educational intervention) and, according to the assigned dosage in each village, there was random assignment of households to the intervention. Here, exogenous intervention refers to treatment assignment being randomized and independent of existing social ties, which is essential for isolating causal effects. For the present analyses, we are explicitly contrasting low and high dosages (involving random targeting in 88 villages); that is, non-zero dosages are categorized into low (5%, 10%, 20% and 30%) and high (50%, 75% and 100%). Although the 100% dosage scenario could be examined separately, because there are no untreated individuals, we have grouped it with the 50% and 75% dosage arm for two reasons: (1) the behavioural patterns in these high-dosage arms are similar, and (2) grouping them increases the statistical power of our results. This stratification is grounded in preliminary exploratory analysis using non-linear models (Loess regression and smoothing). A detailed explanation is provided in Extended Data Fig. 3.
For clarity, we categorize individuals on the basis of their treatment status and the treatment distribution in their villages. We merge treated individuals in fully treated villages (100% dosage) with treated individuals in partially treated villages (5%, 10%, 20%, 30%, 50% and 75% dosages) under the single term ‘treated individuals’. We retain distinct categories for ‘untreated individuals in partially treated villages’ (5%, 10%, 20%, 30%, 50% and 75% dosages) and ‘untreated individuals in fully untreated villages’ (0%).
Network ascertainment
Using name-generator questions, we recorded diverse social relationships, including health advice, friendship, and financial relationships within each village in waves 1, 3 and 4 (the full list of name generators is provided in Supplementary Table 10). For the main analyses, we first analysed the health network (which consists of two questions: “Who would you ask for advice about health-related matters?” and “Who comes to you for health advice?”), and we allowed for directional ties.
In addition, we analysed multiplex layers, namely: (1) the friendship network (which consists of three questions: “Who do you trust to talk to about something personal or private?”, “With whom do you spend free time?” and “Besides your partner, parents or siblings, who do you consider to be your closest friends?”); and (2) the financial network (which consists of two questions: “Who would you feel comfortable asking to borrow 200 lempiras from if you needed them for the day?” and “Who do you think would be comfortable asking you to borrow 200 lempiras for the day?”). The analysis allows us to attribute the changes of friendship and financial networks to the changes of health network. To ensure the validity and robustness of the changes in the friendship and financial networks, we also performed a complementary analysis examining the residual networks by removing the multiplex health ties from waves 1 and 3 from the friendship and financial networks (Supplementary Tables 57–60).
Permutation tests and causal effects
We performed a two-stage, cluster-randomized controlled trial. Villages were first assigned to dosage arms and, within treated villages, households were randomly selected for the 22-month health-education programme1. We analyse our two-stage randomized saturation design under partial interference (interference allowed within, but not across, villages). An ego’s network in our experiment can change because the ego was treated, or because others in their village (both near and far, geodesically speaking) were treated, or both. Disentangling these effects under the two-stage design depends on proper comparisons. ‘Overall effects’ are determined by comparing all individuals in the 88 partially and fully treated villages (5%, 10%, 20%, 30%, 50%, 75% and 100% dosages) with untreated individuals in the 22 fully untreated villages (dosage 0%). This captures the average effect of assigning different treatment dosages to people in a village on an individual’s network structure, regardless of whether they or others in the village are treated. ‘Total effects’ are determined by comparing treated individuals in treated villages (dosage greater than 0%) with untreated individuals in the fully untreated villages, representing the average effect on changes in the network properties of being treated and being in a treated village versus being untreated in a fully untreated village (dosage 0%). ‘Spillover effects’ are established by comparing untreated individuals in treated villages with untreated individuals in untreated villages. These represent the average effect on network changes of being untreated and being exposed to a village dosage greater than 0%, versus being untreated in fully untreated villages (0%). Finally, the difference between the total effect and the spillover effect results in the ‘direct effect’, which compares treated individuals with untreated individuals in partially treated villages.
For overall, total and spillover effects, we first estimate the pooled effects of dosages higher than 0% versus 0%, and then we focus on the separate effects of low dosage (5–30%) versus 0% and high dosage (50–100%) versus 0%. Similarly, for direct effects, we first estimate the pooled direct effect of being treated versus untreated across all dosages, and then we investigate the direct effects within low-dosage villages and within high-dosage villages, separately. When the estimated total and spillover effects have the same sign as, and are similar in magnitude to, the overall effect, we focus on the overall effect for brevity.
To test whether the intervention altered node-level structure (total degree, in-degree and out-degree), we apply permutation tests designed for experiments with partial interference19, which permits the outcomes—that is, the network connections—for an individual to be affected by assignments within the same village, but not by assignments in other villages. This assumption is reasonable given the villages’ isolation and sparse intervillage ties. The test statistic is the studentized difference between village-level mean changes; effects are reported as percentage-scaled difference-in-differences. For each degree metric and for each causal effect, we take the change from wave 1 to wave 3 in the corresponding treated group, subtract the corresponding change in the corresponding control group and then divide this difference by the wave-3 mean of that metric in the comparison group. The estimated percentage-scaled effects, as illustrated in Fig. 2, are assessed against the randomization distribution using the permutation test. This framework provides exact P values under the sharp null of no treatment effect, while respecting the village-level randomization, the possibility of spillovers and the network’s interference structure43.
The randomization distribution is generated by reassigning treatment labels according to the two-stage experimental design and assigning outcomes under the sharp null hypothesis of no effect, yielding design-based P values that respect interference and avoid the independence assumptions of standard parametric tests. The two-sided P values are computed on the basis of how extreme the observed statistics are relative to their null distribution. We use 10,000 permutations.
For the heterogeneity analysis, we use linear mixed-effects models with degree, in-degree or out-degree as the dependent variable and the treatment status as the key independent variable, including an interaction with the socio-demographic or wave-1 network property of interest. We also include household-level and village-level random effects. The treatment variable is defined as treated villages versus 0% villages (for overall effects); treated in treated villages versus untreated in 0% villages (for total effects); untreated in treated villages versus untreated in 0% villages (for spillover effects); and treated in treated villages versus untreated in treated villages (for direct effects).
We address the possibility of false discoveries using the Benjamini–Hochberg step-up procedure applied to pre-specified families44. Following previous work45,46, we also apply the Westfall–Young step-down procedure, which controls the family-wise error rate while accounting for the correlation among outcomes. We also report an Anderson summary-index analysis that consolidates the correlated graph statistics into one index per estimand (m = 6 within each estimand, and m = 24 across estimands)45,46. The dyadic mechanism survives some of these (family-wise) corrections. Some node-level overall effects at low dosage hold under the FDR criterion but attenuate under family-wise control (Supplementary Information). For node-level and network-level tables, we adjust the six graph-metric P values (degree, in-degree, out-degree, betweenness, closeness and clustering) within each estimand (overall, total, spillover and direct; m = 6 per family). For the dyadic logistic models, each specification forms a family of the four exposure indicators {UU, TU, UT and TT} (m = 4). For the node-level tables, P values < 0.001 were set to 0.001 before adjustment; the dyadic tables use the exact model P values. Adjusted P values are reported in Supplementary Information section 22, and do not alter our main conclusions.
Under multiple-testing correction, the dyadic mechanism is the most robust. The dissolution of treated–untreated ties and the persistence of treated–treated ties survive some family-wise (Westfall–Young) corrections: friendship persistence for UT and TU ties at both dosages and for TT ties at low dosage; health persistence for UT ties at low dosage and TU ties at high dosage; and friendship tie formation (TT) at low dosage. The node-level summary index confirms a dosage contrast—a selective loss of ties at a low dosage and a broad, spillover-driven increase in connectivity at a high dosage—whereas the low-dosage overall node-level effect nearly holds under the FDR criterion but does not survive family-wise control, consistent with the known conservatism of family-wise correction over mechanically related estimands.
Link analysis
Although we can show a one-to-one correspondence between dyadic effects and statistical causal effects on individual-level network properties (in particular, in-degree from treated individuals, in-degree from untreated individuals, out-degree to treated individuals and out-degree to untreated individuals), in the main text we report results for the link-formation analysis using dyadic mixed-effects logistic regressions, because they might be more intuitive (see Extended Data Tables 4–6 and Supplementary Tables 14–22 for methodological details). Specifically, to study tie persistence and formation, we fit mixed-effects logistic models on directed, within-village ego–alter pairs, with exposure encoded by dyad category ∈ {TT, TU, UT, UU, U0U0 (reference category)} and random intercepts for village, ego and alter to account for dependence:
$$\begin{array}{l}{\rm{logit}}(Pr({Y}_{{ijv}}=1|{M}_{{ijv}}=m))={\gamma }_{0m}+{\gamma }_{{\rm{UU}}m}{\rm{UU}}+{\gamma }_{{\rm{UT}}m}{\rm{UT}}+{\gamma }_{{\rm{TU}}m}{\rm{TU}}\\ \,+\,{\gamma }_{{\rm{TT}}m}{\rm{TT}}+{u}_{i}+{v}_{j}+{\xi }_{v},\end{array}$$
where Yijv is the indicator for the existence of a tie between individuals i and j in village v in wave 3; UU, UT, TU and TT are the indicators for the treatment status of the dyad ijv; ui, vj and ξv are ego-level, alter-level and village-level random effects; and m = 1 if the tie between individuals i and j in village v existed in the wave, and 0 otherwise.
These models provide odds-ratio estimates for each dyad category relative to U0U0 and align with node-level estimands through a mapping between dyadic flows and in-degree and out-degree components. Results from the corresponding permutation tests for the individual-level analysis show similar conclusions.
Mediation analysis
At wave 2, midway through intervention delivery, we surveyed 62 knowledge items (scored correct or incorrect; that is, 1 for correct and 0 for incorrect). For each respondent, we created baseline and midline knowledge scores by summing the items. The mediator is the change in knowledge, defined as the midline score minus the baseline score. Of the 8,331 individuals in the main analytic sample, 7,748 were present in all three waves (1, 2 and 3) and are included in the mediation analyses. The summed scores took values between 0 and 53 in wave 1 and between 0 and 58 in wave 2, with a potential minimum of 0 and maximum of 62.
For individual-level mediation, for each estimand (overall, total, spillover and direct), we estimate natural indirect (NIE) and natural direct effects with the cmest function of the R package CMAverse in a regression-based specification using imputation for the g-formula components and bootstrap inference23. Outcomes and the mediator are modelled linearly, and the exposure corresponds to the individual-level and village-level treatment contrast appropriate for each estimand; for example, being treated versus being untreated in partially treated villages for direct effects. We report in the main text the NIE and the proportion-mediated effects; the natural direct effects are provided in the Supplementary Information. The models include the same covariates as the primary analyses and omit exposure–mediator interaction in the main specification.
For dyadic mediation, with the dyad-level outcomes being the existence of a tie in wave 3 given its existence (tie persistence) or non-existence (tie formation) in wave 1, we specify a logistic model for the outcome and a multinomial model for the mediator. The dyadic mediator is a three-category variable; that is, none, one and both, indicating whether neither, exactly one or both members of the dyad increased knowledge between baseline and midline. The exposure is specified as the categorical variable defining the treatment status of the dyad; that is, TT, UT, TU, UU and U0U0, with the latter being the reference category. We again estimate the natural direct and indirect effects using the cmest function of the R package CMAverse, using a regression-based approach and bootstrap inference, without exposure–mediator interaction. Dyad-level NIEs, summarized as a share of the total effects for TT, UT, TU, and UU links versus U0U0, complement the individual-level results. In Supplementary Information section 18, we provide detailed information on the tuning of the functions and a description of the methods used for the mediation analysis.
Software
All analyses were performed in R (v.4.5.3) using Visual Studio Code (v.1.93.1); the complete package environment, with pinned versions, is specified in the deposited code.
Ethics statement
The underlying field trial was registered with ClinicalTrials.gov under the identifier NCT02694679. The Yale University institutional review board (IRB) and the Honduran Ministry of Health approved all procedures (protocol number 1506016012). The research was performed in accordance with all relevant guidelines and regulations, and all participants provided informed consent.
Reporting summary
Further information on research design is available in the Nature Portfolio Reporting Summary linked to this article.
