Chronic disease accumulation was measured as the change in disease count (ΔChronic) between 2015 and 2018. The CHARLS assesses 13 physician-diagnosed chronic conditions, including hypertension, diabetes, and cardiovascular disease (see the CHARLS Harmonized D manual for the full list). Positive values indicate disease accumulation, negative values indicate improvement, and zero values indicate stability.

Self-reported disease counts were used as the primary outcome for three reasons: (1) the 2018 CHARLS wave lacked biomarker measurements, precluding longitudinal biomarker analysis; (2) self-reported diagnoses were consistently collected across waves, enabling robust temporal comparisons; and (3) validation studies demonstrated acceptable concordance between self-reports and medical records in similar populations [37]. Although this approach may conflate true disease incidence with improved detection resulting from increased healthcare access, the 'detection effect' is considered an important early signal of successful policy implementation rather than a limitation.

Changes in activities of daily living (ΔADL) scores were designated secondary outcomes to assess the impact of policy exposure duration on functional status among older adults. This selection is justified primarily by the well-established correlation between chronic disease burden and functional impairment [17], suggesting that improved disease management may delay functional decline. Furthermore, ADL serves as a validated proxy for quality of life and independence, representing a critical dimension for evaluating the comprehensive benefits of health policies [38].

The policy exposure duration was operationalized as the cumulative number of months from provincial HC2030 implementation to the 2018 CHARLS follow-up, ranging from 0–21 months across provinces. Provincial implementation dates were defined as the dates when provincial governments officially released "Healthy China 2030" implementation plans or equivalent documents (see the complete provincial policy implementation timeline in Appendix I Table S7).

HC2030 implementation enhanced healthcare service accessibility and quality through the following mechanisms: (1) financial accessibility, i.e., expanding insurance coverage and increasing reimbursement rates for outpatient and inpatient services; (2) service capacity, i.e., strengthening primary healthcare infrastructure and establishing standardized chronic disease management protocols; (3) human resources, i.e., increasing medical workforce training and deployment, particularly in underserved rural areas; and (4) system integration, i.e., developing integrated health information systems to improve care coordination and referral networks.

Provincial variation in implementation timing (0–21 months) provided natural variation in exposure to these service delivery improvements, enabling identification of when health system strengthening translates into measurable health outcomes. To examine the nonlinear dynamic characteristics of the association between policy exposure duration and chronic disease progression, continuous policy exposure duration (tml) was divided into three mutually exclusive groups on the basis of quartiles: the short-term exposure group (≤ 25th percentile, approximately 0–15 months), the medium-term exposure group (25–75th percentile, approximately 15–18 months), and the long-term exposure group (> 75th percentile, approximately ≥ 19 months). As a single linear trend or simple intergroup mean comparison might mask heterogeneity in disease progression rates within different exposure stages, a piecewise linear regression strategy was employed. Specifically, interaction terms between group dummy variables and continuous time variables (Group × Time) were introduced into the model. This design allows for simultaneous estimation of differences in baseline levels across exposure stages (intercept effects) and differences in rates of change over time (slope effects). Significant interaction terms indicate that chronic disease accumulation trajectories undergo structural changes as the duration of policy exposure increases, thereby validating the marginal benefits of the policy at different stages. This grouping strategy maintains adequate sample sizes for statistical power in each group while enabling the detection of potential nonlinear associations [39, 40]. Notably, this grouping design employs a grouped-comparison analytical strategy rather than estimating continuous dose‒response relationships.

Covariate selection followed the framework of Andersen's behavioral model of health services use [41], which includes the following: (1) predisposing factors: individual-level demographic characteristics (age, sex, marital status); (2) enabling factors: socioeconomic status (education level, household income or assets), health insurance coverage; (3) need factors: health behaviors (smoking, alcohol consumption), functional and mental health indicators (ADL scores, depression scale scores), baseline chronic disease burden and health service utilization (hospitalization frequency, outpatient visits); and (4) contextual factors: provincial time-varying macroeconomic and health resource indicators extracted from the China Statistical Yearbook, including per capita regional gross domestic product (GDP) and health resource allocation indicators.

The physical activity variable exhibited a relatively high proportion of missing values (approximately 50%) in the analytical sample, and missing pattern analysis suggested possible systematic differences. Because including variables with high missing rates can substantially reduce the sample size and introduce selection bias, physical activity control variables were excluded from the main regression model.

To construct comparable reference populations across different policy exposure duration groups, we employed the overlap weighting (OW) method for multinomial treatments [45]. This method reduces selection bias arising from uneven covariate distributions by assigning weights to observations with propensity scores within the common support region, which is particularly important for comparing provinces with different baseline levels of healthcare service accessibility.

For three-category treatment (short-term/medium-term/long-term exposure groups), we first estimate generalized propensity scores (GPSs) via multinomial logistic regression: P(TML = k|X) = exp(X'γk)/Σⱼ exp(X'γⱼ), k ∈ {short-term, medium-term, long-term}. where X includes all baseline covariates. On the basis of GPS, overlap weights are calculated as follows: for individual i in exposure group k, w_ik = Π_{j ≠ k} e_ij, which is the product of generalized propensity scores for all groups except k.

This weighting scheme has the following advantages: (1) it maximizes the effective sample size: compared with inverse probability weighting (IPW), overlap weights are insensitive to extreme propensity scores; (2) it ensures covariate balance: in weighted pseudopopulation, the three exposure groups have identical covariate distributions; and (3) it focuses on the overlap region: the estimated effects correspond to subpopulations where all three groups are adequately represented. Standardized mean differences (SMDs) are used to assess balance, with SMDs < 0.10 indicating good balance and SMDs < 0.05 indicating excellent balance.

To handle missing data, we used multiple imputation by chained equations (MICE), generating 50 imputed datasets [46]. The imputation model included all the analytical variables and relevant auxiliary variables to approximate the missing-at-random assumption. The results were combined via Rubin's rules [47].

Given the limited number of provincial clusters (n = 28), traditional cluster-robust standard errors may underestimate sampling variability and increase Type I error rates. Therefore, we combined wild cluster bootstrapping (WCB) with multiple imputation for statistical inference [48, 49]. Specifically, 10,000 WCB repetitions are performed on each imputed dataset via Rademacher weights; point estimates and variances across imputed datasets are combined via Rubin's rules; and 95% confidence intervals and p values are constructed. The simulation results show that WCB methods can still provide reliable inference when the number of clusters is small (e.g., G between 15–20) under certain conditions [49].

To identify critical time points at which healthcare service improvements translate into health outcomes. On the basis of the marginal prediction curves, we calculate the following:

These calculations use point estimates from the regression model. We focus on trajectory-level inference (testing whether group slopes differ) rather than precise threshold estimation, as our primary interest is in demonstrating that sustained health system exposure produces measurable benefits within a policy-relevant timeframe.

To assess the reliability of causal identification [50], we conducted sensitivity analyses across four dimensions: (1) temporal specificity: prepolicy placebo test (2011–2015), designating 2013 as the "virtual policy start year," testing whether interaction terms between virtual exposure groups and time months are statistically significant in the prepolicy period; (2) treatment specificity: randomized pseudoexposure test, using random number generators to generate provincial random exposure durations (0–21 months), testing whether random grouping produces significant effects; (3) outcome specificity: placebo outcome test, using measured height as a negative control, testing whether policy exposure is associated with height changes; and (4) heterogeneity testing: including three-way interaction terms of the policy exposure group with age, sex, urban‒rural residence, and education level.

Main findings: Policy effects depended critically on exposure duration (Table 3, Appendix I Table S3). Compared with short-term exposure, long-term exposure (≥ 19 months) significantly slowed chronic disease accumulation (β = -0.325, SE = 0.116, p = 0.005, 95% CI: -0.552–0.098).

Clinical significance: This effect is substantial. The average population experienced 0.45 additional chronic conditions over the observation period due to natural aging. The estimated policy effect offsets approximately 72% of this age-related burden among individuals with long-term exposure (0.325/0.45 = 0.72), moving from net accumulation toward stabilization.

In contrast, neither the main effect of policy exposure duration (β = 0.009, p = 0.879) nor the interaction term for the medium-term exposure group (β=-0.016, p = 0.636) achieved statistical significance. These findings indicate that healthcare service delivery improvements under HC2030 require a longer implementation period (≥ 19 months) to manifest in population-level chronic disease outcomes.

The placebo test applied the main analytical model to the prepolicy period (2011–2015), using actual future policy exposure duration (measured 2016–2018) as the treatment variable (Table 4, Appendix I Table S4). The results revealed no significant interaction effects during the placebo period. The critical interaction term for long-term exposure was small and nonsignificant (β = 0.089, p = 0.474, WCB), in contrast with the significant negative effect observed in the main analysis (β=-0.325, p = 0.005). Similarly, the medium-term exposure interaction was not significant (β = 0.010, p = 0.671). These nonsignificant placebo interactions validate the parallel trends assumption, indicating that exposure groups followed similar trajectories before policy initiation.

Notably, there was a significant main time effect during the placebo period (β = -0.012, p = 0.033), indicating that provinces that would later have longer exposure periods experienced slightly greater chronic disease deceleration from 2011–2015. This main effect does not violate the parallel trends assumption, which requires parallel group-specific trajectories rather than zero baseline trends. Moreover, this effect reversed during the main analysis period (β = 0.009, p = 0.879), suggesting period-specific secular trends rather than persistent selection bias.

To assess whether the significant main time effect during the placebo period reflects spurious correlation with any continuous provincial variable, we conducted a robustness check via randomized pseudoexposure (Table 5). Critically, during the main analysis period, randomized pseudoexposure produced a small positive interaction for the long-term exposure group (β = 0.034, p = 0.007), which was in the opposite direction and approximately 10 times smaller in magnitude than the true policy effect (β=-0.325, p = 0.005). The sharp contrast in direction and magnitude provides strong evidence that the observed policy effects reflect true causal impacts rather than spurious correlations with preexisting provincial trends.

To verify that the observed effects reflect true policy impacts on chronic disease outcomes rather than unmeasured time-varying provincial confounders, we conducted a placebo outcome test using measured height as a negative control. The height of adults aged 60 years and above should not be affected by medical policies for chronic disease management. The results revealed no significant association between policy exposure and changes in height (Appendix I Table S5). The long-term exposure interaction term was small and nonsignificant (β = -0.0083, p = 0.203, WCB), approximately 40 times smaller than the effect on chronic disease count (β = -0.325, p = 0.005, WCB).

The convergence of evidence across three independent validation strategies—temporal specificity (significant postpolicy, nonsignificant prepolicy), treatment specificity (true exposure shows a negative effect, random exposure shows the opposite positive effect), and outcome specificity (significant for chronic diseases, null for height)—provides strong support for the causal interpretation of policy effects. This triangulation of evidence substantially enhances confidence in the causal inference that extended HC2030 exposure improves chronic disease management outcomes among elderly populations.

(1) Equivalence crossover point (4.1 months): the times at which the predicted chronic disease counts for the long-term and short-term exposure groups were equal. This point, calculated as t = -β₂L/β₃L, marks the point at which healthcare service improvements begin to produce relative advantages.

(2) Zero-accumulation point (13.1 months): the time when the long-term group trajectory shifts from a net increase to stabilization. This threshold, calculated as t = -(β₀ + β₂L)/(β₁ + β₃L), represents population-level stabilization rather than individual-level disease reversal; only 20% of individuals reported net disease reduction. This indicates when health system strengthening begins to produce measurable health benefits.

(3) Sustained improvement period (after 13.1 months): After the zero-crossing point, the gap between long-term and short-term groups continues to widen throughout the observation period, with effect sizes increasing monotonically and confidence intervals gradually shifting toward negative values, supporting the cumulative nature of policy effects.

Two complementary statistical findings support our conclusions: (1) Trajectory-level significance: the interaction term between the long-term exposure group and policy duration is statistically significant (β=-0.325, p = 0.005), indicating that chronic disease accumulation rates differ significantly over time across exposure groups. This tests whether trajectories (slopes) diverge—the core assumption of cumulative policy effects. (2) Time point estimates: Marginal predictions at specific time points represent effect sizes rather than hypothesis tests. Confidence intervals reflect estimation uncertainty inherent in quasiexperimental designs with provincial-level policy variation.

The converging evidence supports the robustness of the findings: effect sizes increase monotonically with exposure duration, confidence intervals gradually shift toward negative values, and temporal specificity is confirmed by placebo tests.

Further analysis revealed that the long-term exposure group (relative to the short-term group) presented a distinct temporal pattern across the three phases. During the initial period (0–4 months), the long-term group showed greater disease accumulation than did the baseline group, which is consistent with increased case identification following improved healthcare access—a detection effect commonly observed when service barriers are reduced. The transition period (4–13 months) marked a critical shift, with trajectories crossing as health management benefits began to outweigh detection effects. The sustained benefit period (after 13 months) demonstrated consistent protective effects, with the long-term group maintaining lower accumulation rates throughout the remaining observation period, indicating cumulative benefits of prolonged health system exposure.

The consistent negative direction at all time points after 13 months further supports the potential clinical relevance of these findings.

Heterogeneity analysis aims to generate hypotheses rather than validate predetermined hypotheses. Given that multiple comparisons may increase the risk of Type I error, all interaction term p values should be interpreted cautiously. The policy effects did not significantly differ across gender (p = 0.45), urban‒rural residence (p = 0.31), or education level (p = 0.28) groups, indicating that HC2030 implementation did not exacerbate existing health inequalities (Appendix I Table S6). This finding suggests that healthcare service improvements were distributed relatively equitably across social groups, supporting the policy's universal coverage strategy.

To examine whether policy implementation timing was influenced by regional prior health or economic conditions, we examined correlations between 2015 implementation timing and baseline characteristics. The results revealed no significant correlations between implementation timing and baseline chronic disease count (ρ = 0.215, p = 0.270), ADL limitations (ρ=-0.094, p = 0.631), age (ρ=-0.139, p = 0.477), or per capita GDP (ρ=-0.004, p = 0.982) (Appendix I Table S7). On the basis of policy document records (Appendix I Table S8), we conclude that provincial implementation schedules are driven primarily by external factors, such as administrative processes, rather than by regional initial health status or economic levels.