Is Early Puberty Causally Harmful? Doubly Robust Estimation of Developmental-Timing Effects in Existing Cohorts

Children who enter puberty earlier than their peers report more anxiety, depression and behavioural problems. In the largest recent analysis, a curve-fitting model of normal pubertal development flagged early maturers in about 9,900 American adolescents, and the size of their "puberty age gap" predicted mental-health symptoms (“Puberty age gap”). That result is an association, not a cause. Children who mature early also tend to have higher childhood body weight, different family circumstances, and sometimes earlier psychological difficulties. Any of these could produce both early puberty and later symptoms. Whether early puberty itself does harm matters for intervention, because it decides whether clinicians should target pubertal timing or the conditions that produce it.

This note proposes to answer that question with the logic of a retrospective cohort study: take data that has already been collected, define an exposure, confounders and outcome on a fixed time axis, and estimate what would have happened under a different exposure. Two changes to standard practice are needed. First, "being early" and the main confounders, such as body weight, should be measured as deviations from non-linear age-specific reference curves rather than as raw values or simple predicted-minus-actual age gaps. Second, the outcome should be the whole trajectory of symptoms over the following years, estimated with a doubly robust functional estimator rather than a single follow-up score. The central empirical question is whether the early-maturation effect survives this treatment, and whether late maturation is also harmful. The "off-time" hypothesis predicts that it is, which would give a non-monotone, U-shaped pattern.

Core Claim

The claim has three parts.

The usual age gap is biased. The predicted-minus-chronological "age gap" that dominates this literature is mostly an age artifact when the underlying curve is steep and non-linear. The combined physical-plus-hormone model in the ABCD study (the Adolescent Brain Cognitive Development cohort) correlates with chronological age at only $r = 0.58$ in females and $r = 0.54$ in males (“Puberty age gap”). Predicted ages are therefore pulled strongly toward the cohort mean. Younger children systematically look "early" and older children look "late," and in a 9–13 age window chronological age is itself associated with symptom levels. A linear age correction removes this only if the reference curve is linear, and pubertal development is not.

A better exposure exists. Define the exposure instead as a within-age standing:

$$z_i = \Phi^{-1}\big(\hat F(s_i \mid \text{age}_i, \text{sex}_i)\big).$$

Here $s_i$ is child $i$'s pubertal score, $\hat F$ is the conditional distribution of that score given age and sex estimated by a flexible spline model, and $\Phi^{-1}$ maps the resulting centile to a standard normal score. By construction, $z_i$ is independent of age within the reference population. Confounders with their own steep developmental curves, chiefly body-mass index, get the same treatment, together with their pre-exposure velocity.

The estimand is a curve. With exposure groups early ($z_i$ above a threshold), on-time and late, the target is

$$\theta_a(t) = E[Y_a(t)] - E[Y_{\text{on}}(t)], \qquad a \in \{\text{early}, \text{late}\}.$$

$Y_a(t)$ is the potential symptom score $t$ months after a fixed landmark visit had the child been in group $a$. We estimate $\theta_a(t)$ with simultaneous confidence bands across all $t$.

Research Program

Method source. The estimator is borrowed, not invented. Doubly-Robust Functional Average Treatment Effect Estimation introduced DR-FoS. It combines a model of the outcome curve with a model of treatment probability (the propensity score) so that the estimate stays consistent if either model is right. It also uses cross-fitting, meaning the two models are trained and evaluated on different data splits, and it proves simultaneous confidence bands. DR-FoS was demonstrated only on adult chronic conditions in an ageing cohort (SHARE), with exposure defined directly by diagnosis. Our contribution is the regime it leaves open: a developmental exposure that is itself defined relative to a non-linear normative curve, in children, with confounders that are also developmental. The earlier The functional average treatment effect set up the functional estimand on NHEFS, the US national health survey's epidemiologic follow-up cohort, and found a near-null exercise effect there. That serves as a reminder that functional estimates can be honestly null.

Design. The retrospective-cohort discipline comes from clinical work that shows how time anchoring decides validity. Timing to intubation COVID-19 patients had to re-anchor delay to symptom onset rather than admission to avoid a distorted time axis. Analogously, we fix a landmark ABCD visit, measure the exposure there, take confounders only from that visit and earlier, and define outcomes strictly afterward. Doing this prevents outcomes from leaking into the exposure definition. Long-Term Survival in Men With High Grade Prostate Cancer is the canonical demonstration that unadjusted comparisons in such data reflect who gets "exposed" rather than what exposure does. Its propensity stratification on static baseline scalars is the design we improve upon.

Concrete build. The work produces three things.

  1. Normative curves. We fit sex-specific conditional-distribution models for pubertal stage and body-mass index on a held-out reference split of ABCD. Physical development is used as the primary pubertal measure, because the original study found it carried the strongest mental-health association.
  2. Exposure and confounders. We compute $z$-scores for the exposure and for the confounders, plus pre-landmark body-mass velocity. Remaining confounders are family socioeconomic indicators and baseline symptom scores.
  3. Estimation. We run DR-FoS for the early-versus-on-time and late-versus-on-time contrasts. Outcomes are the internalizing and externalizing symptom curves from the Child Behavior Checklist (CBCL) over subsequent waves. The nuisance models are flexible learners with cross-fitting.

Semi-synthetic benchmark. Because real causal effects are unknown, we also build a benchmark in the spirit of the semi-synthetic MIMIC-III design of Dynamic Survival Transformers. That design kept real covariates and simulated treatment and outcomes so that ground truth was known. Our version keeps real ABCD covariate histories and simulates two things: assignment to early maturation as a function of body-mass deviation and velocity, and symptom curves with a known $\theta(t)$ that may be zero, monotone or U-shaped.

Baselines

Naive reference. The do-nothing reference is the unadjusted difference in mean symptom curves between early and on-time maturers, with groups defined by the conventional predicted-minus-chronological gap. This is roughly what a descriptive reading of the original association implies. Beating it is not an achievement in itself. Its role is to show how much of the raw association the corrections remove.

Established associational analysis. This baseline reproduces the published approach: spline-based age modelling of puberty, the resulting age gap, and a multivariable regression of symptoms on the gap with age, sex and socioeconomic covariates (“Puberty age gap”). It is the strongest competitor on this specific question because it is what the field currently reports. The comparison uses the same participants, waves and covariates. The only paper-reported numbers for it are the age-prediction correlations above and AIC model comparisons. There is no reported causal-effect number on Lacuna for ABCD pubertal timing, so on real data we compare the estimates themselves rather than claim to beat a figure.

Static-covariate propensity analysis. This baseline is propensity matching on landmark-visit scalars (age, raw body-mass index, socioeconomic indicators, baseline symptoms), following Long-Term Survival in Men With High Grade Prostate Cancer, with symptoms compared at each wave.

Strongest existing method. The strongest existing method is DR-FoS run on raw covariates and raw pre-landmark histories with the same flexible learners, the same cross-fitting folds and the same hyperparameter search budget as our version (Doubly-Robust Functional Average Treatment Effect Estimation). It differs from the proposal only in the input representation. For its accuracy there is no reported result found on Lacuna for DR-FoS bias or band coverage on SHARE; the file reports only the qualitative widening gap. On the semi-synthetic benchmark, "beating it" means lower integrated squared error of $\hat\theta(t)$ and band coverage closer to nominal at a fixed cohort size.

Ablations. Two ablations isolate the key ingredients. One swaps the centile exposure $z_i$ for the conventional age gap while keeping everything else fixed. The other keeps $z_i$ but feeds confounders in raw form.

Why not just…?

Why not just add age and body-mass index as covariates in a regression, as the original study did? Regression adjustment is correct only if the outcome model is right. In the simulations of Doubly-Robust Functional Average Treatment Effect Estimation, outcome-regression error grew sharply under misspecification while the doubly robust estimator stayed stable. The specific worry here is that body-mass index and age act on both puberty and symptoms along curved paths. Association of body mass index with severity and mortality of COVID-19 pneumonia shows how easily linear terms hide U-shaped relationships in exactly this kind of variable. The baseline comparison and the semi-synthetic misspecification arms will measure how much this matters here.

Why not just give a flexible learner the raw histories and let it discover the reference curves? This is the serious threat. With roughly 9,900 children, a gradient-boosted propensity model on raw age, raw body-mass index and recent changes may implicitly learn the same deviations. The case for explicit centiles is a sample-size argument. Curves estimated from a large reference population transfer information that a small retrospective cohort cannot estimate on its own. We test this directly by fitting reference curves on one split and running the causal analysis on subsamples of decreasing size from the rest. If the raw-history DR-FoS matches ours at every subsample size, we drop the representation claim and report that the contribution reduces to the exposure correction and the functional estimand.

Why not just test each follow-up wave separately? Separate per-wave tests ignore the strong correlation between adjacent waves and multiply the testing burden. They also cannot say whether an effect grows, fades or reverses with time, and that pattern is the substance of the off-time hypothesis. Simultaneous bands from DR-FoS address this (Doubly-Robust Functional Average Treatment Effect Estimation). A cheaper alternative, per-wave doubly robust estimates with a Bonferroni correction, is included in the comparison so the gain in band width is measured rather than asserted.

Why not just keep the age gap and regress out age linearly? This works only if the reference curve is linear. With a prediction correlation of about 0.55, a curved residual age dependence will remain. The first decisive check below measures it directly.

Decisive Checks

Exposure artifact. Within ABCD, we plot the conventional age gap and $z_i$ against chronological age, before and after linear age correction. The proposal's premise fails if the linearly corrected gap shows no residual age structure.

Semi-synthetic recovery. On the benchmark, each estimator is scored by integrated squared error and simultaneous-band coverage of $\theta(t)$. This is done across effect shapes (null, monotone, U-shaped), confounding strengths, and cohort sizes from a few hundred up to the full sample. The null-effect arm is the most important. An estimator that reports early-maturation harm when none was simulated is reproducing the confounding story.

Real-data question. On the real data, we report $\hat\theta_{\text{early}}(t)$ and $\hat\theta_{\text{late}}(t)$ with bands for internalizing and externalizing symptoms, alongside the attenuation relative to the associational baseline. Three outcomes are each informative:

  • The early effect survives with a band excluding zero. This strengthens the case for timing itself as a target.
  • The early effect shrinks to null once body-mass deviation and velocity are handled. This points to adiposity pathways.
  • A late-maturer effect also appears. This supports the non-monotone off-time hypothesis, which no linear gap analysis can detect.

Unmeasured confounding. Because none of this removes bias from confounders that were never recorded, a sensitivity analysis reports how strong an unmeasured confounder would have to be to erase the estimated effect.