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Across 50 real randomized trials, simple prespecified covariate adjustment improves precision consistently — 13.3% median variance reduction for continuous, 4.6% for binary — and matches or beats machine-learning estimators.

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Across 50 real randomized trials, simple prespecified covariate adjustment improved precision as much as or more than machine-learning estimators, with no systematic bias.

T0 review reviewed 2026-08-03 challenge →

load-bearing objection A genuinely useful empirical benchmark of covariate adjustment in RCTs, with a real but fixable selective-success problem in the binary-outcome ML comparison. the 3 major comments →

arxiv 2602.00434 v3 pith:SVZMKF5H submitted 2026-01-31 stat.AP

How should covariates be handled in randomized trials? Empirical evidence from 50 trials and recommendations for practice

Yulin Shao , Liangbo Lyu , Menggang Yu , Bingkai Wang This is my paper
classification stat.AP MSC 62P10
keywords covariate adjustmentrandomized clinical trialsANCOVAmachine learningprecision gainsbaseline covariatesempirical benchmarking
verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

Using individual-level data from 50 completed randomized trials (29,094 participants, 574 treatment-outcome comparisons), the paper benchmarks six covariate-adjustment estimators under three covariate-selection rules. It tries to establish that routine adjustment with a small, prespecified set of prognostic baseline covariates consistently improves precision — median variance reductions of 13.3% for continuous outcomes and 4.6% for binary outcomes — without systematically shifting point estimates or increasing the risk of losing a significant result. The paper also argues that parsimonious regression methods such as ANCOVA are at least as precise as machine-learning estimators in these real trials, and more reliable in small samples. That matters because regulatory guidance already recommends covariate adjustment, but practicing trialists lack empirical evidence on which strategy to prespecify. If correct, trial protocols can safely prespecify simple, transparent adjustment and reap power gains.

Core claim

Across 574 treatment-outcome comparisons drawn from 50 real RCTs, covariate adjustment improves precision in most settings, with median proportional variance reductions of 13.3% (continuous) and 4.6% (binary). ANCOVA adjusting for all available covariates gives the largest precision gains and rarely loses precision; in small samples, more complex estimators — ANHECOVA with interactions, IPW, g-computation, and the machine-learning estimators TMLE and DML — are either similar or worse, and the machine-learning methods show elevated error rates for binary outcomes. Under a prespecified 'Baseline+' adjustment set (baseline outcome, stratification factors, age, sex, weight), gains remain consist

What carries the argument

The object doing the analytical work is the benchmark corpus plus the two operating-characteristic metrics: proportional variance reduction (PVR = 1 − Var(adjusted)/Var(unadjusted)) and the covariate-adjustment gain/loss (CAG/CAL), the conditional probabilities that adjustment creates or removes a 5%-significant finding relative to the unadjusted analysis. PVR translates directly into the sample-size reduction needed to maintain power, and CAG/CAL translate method performance into clinical decision impact. The estimators under study are anchored by ANCOVA, which here is the reference parsimonious strategy and is guaranteed asymptotically no less precise than the unadjusted estimator under eq

Load-bearing premise

The load-bearing premise is that the 50 publicly deposited trials, which the authors themselves say 'may not be fully representative of the broader landscape of modern clinical trials' (Discussion), represent the range of real trials where these recommendations will be applied; if public-repository trials differ systematically from commercial or preprint-only trials in sample size, outcome type, or covariate quality, the median gains and the ANCOVA-over-machine-learning ranki

What would settle it

Take any independent set of, say, 50 archived randomized trials (ideally including non-publicly-deposited industry trials) and recompute the median proportional variance reduction and the ANCOVA-versus-TMLE/DML gap; the central claim fails if the new median PVR is near zero or negative, or if machine-learning estimators show a consistent precision advantage in small samples with binary outcomes.

Watch this falsifier. Get emailed when new claim-graph text bears on it.

If this is right

  • Prespecifying a small prognostic set (baseline outcome, stratification factors, age, sex, weight) and fitting ANCOVA for continuous endpoints or g-computation from logistic regression for binary endpoints is a sufficient, transparent primary-analysis strategy in most trials.
  • Trials can be sized using the expected PVR: a 13.3% median variance reduction for continuous outcomes corresponds to roughly a 13% sample-size saving at equal power, and the paper's guidance gives a way to anticipate this at the planning stage.
  • Default-hyperparameter machine-learning estimators should not be the primary analysis in small-to-moderate samples: they did not beat linear regression and had error rates up to 12% for binary outcomes when all covariates were used.
  • Covariate adjustment in real trial data is more likely to convert a non-significant unadjusted result into a significant one (CAG) than the reverse (CAL), so routine adjustment will rarely 'lose' an effect that was genuinely there.
  • When sample size is roughly above 100, estimator choice matters less; below that, simple regression is the safer default.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

  • A natural next test is whether hyperparameter-tuned or stratified-cross-validation versions of TMLE/DML close the gap; the paper's own error-rate analysis suggests the two-layer sample splitting is the likely culprit, not the estimators' statistical framework.
  • Because the corpus is 50 trials with many treatment-arm comparisons sharing covariates, the median PVR should be treated as a distribution, not a guarantee; replicating on a per-therapeutic-area basis (or on trials with large samples and highly nonlinear outcomes) would show where flexible models start paying off.
  • If these results generalize, the practice of reporting only unadjusted analyses in trial registries and primary papers carries a quantifiable efficiency cost; one could compute the expected power loss directly from the observed PVR distribution and use it to argue for prespecified adjustment in protocols.
  • The CAG/CAL asymmetry suggests a screening metric: trials whose unadjusted analysis is just at the significance boundary are the ones where covariate adjustment most plausibly flips the conclusion, so sensitivity analyses should be reported there.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, simulated authors' rebuttal, and a circularity audit.

Referee Report

3 major / 5 minor

Summary. The paper assembles individual-level data from 50 publicly available randomized trials (29,094 participants; 574 treatment–outcome pairs) and benchmarks 18 covariate-adjustment strategies: six estimators (ANCOVA, ANHECOVA, IPW, g-logistic, DML, TMLE) crossed with three covariate-selection rules (All, Top-3, Baseline+). Performance is measured by proportional variance reduction (PVR), standardized point-estimate shifts, covariate adjustment gain/loss, and error rates. The headline findings are that covariate adjustment improves precision in most settings (median PVR 13.3% continuous, 4.6% binary), that parsimonious prespecified regression approaches such as ANCOVA perform as well as or better than machine-learning estimators, and that ML estimators add little precision while failing more often for binary outcomes. The authors release all curated data and code and provide practical, decision-oriented recommendations favoring prespecified adjustment with a small set of prognostic covariates.

Significance. If the empirical comparisons are trustworthy, this is a valuable and timely contribution. It is, to my knowledge, one of the first large-scale benchmarks of covariate-adjustment strategies on real RCT data rather than simulations, and the open release of 50 harmonized datasets is a reusable resource for future methodological work. The paper is also unusually transparent about limitations, including the representativeness of public-repository trials and the correlation induced by multiple treatment–outcome pairs from the same trial. However, the central claim that machine-learning estimators 'did not provide additional precision' is currently vulnerable to a differential-success bias in the binary-outcome analysis, and the Top-3 strategy is evaluated in-sample despite being data-driven. Those issues are fixable but load-bearing for the paper's practical recommendations.

major comments (3)
  1. [§Error rate; Figure 2] The comparison of median PVR across estimators for binary outcomes is computed only on runs that returned results, while error rates differ sharply by method: DML fails in 12% of All-covariate analyses, 12% of Top-3, and 8% of Baseline+; TMLE fails in 4%, 3%, and 3%; ANCOVA fails in 0% (Figure 2, error-rate row). The paper states that most failures arose from rare events in outcomes. If rare-event or small-sample settings have systematically different covariate-adjustment gains, the DML/TMLE medians are estimated on a selected subset, making the comparison with ANCOVA not apples-to-apples. This directly affects the claim that ML offers no precision gain. Please provide sensitivity analyses: for example, (i) restrict all methods to the subset of trials where every estimator returns results; (ii) assign failed runs conservative PVR values (e.g., 0 or worst-case) and re-plot; and (iii) repo
  2. [§Results, Benchmarking pipeline; Figure 2] The Top-3 strategy selects the three covariates most strongly correlated with the outcome using the same dataset in which PVR is then evaluated. As the manuscript acknowledges, this carries 'invalidity from data-driven selection.' Because no sample splitting or cross-validation is used, the Top-3 PVR values are in-sample estimates that can be optimistically biased, especially in small trials. Since Top-3 is one of the parsimonious strategies used to support the recommendation that small covariate sets perform well, the analysis needs either a cross-validated version of Top-3 or an explicit statement that these figures are exploratory and not direct estimates of real-world performance. At minimum, a sensitivity analysis using a prespecified or split-sample selection rule would clarify whether the Top-3 results are an artifact of selection on the outcome.
  3. [§Figure 2; §Discussion, first limitation paragraph] The main performance summaries are median PVR values and boxplots over 574 treatment–outcome pairs, without confidence intervals or formal comparisons between methods. The 574 pairs are not independent: they are clustered within 50 trials, and the authors acknowledge that many pairs share overlapping covariate information. The robustness check restricted to primary outcomes has only 76 continuous and 18 binary pairs, so it is not a substitute for accounting for clustering in the full analysis. To support the wording 'consistently improves precision' and 'performed as well as or better,' please add uncertainty quantification that respects the trial-level clustering—for example, per-trial median PVR with a cluster bootstrap, or paired within-trial comparisons of estimators—and report the variability of the all-pairs medians.
minor comments (5)
  1. [§Methods, Performance metrics] The CAG/CAL definitions contain a typo: 'the adjusted and adjusted analysis' should read 'the adjusted and unadjusted analysis.'
  2. [Figure 3 caption; Supplementary Figure 3 caption] The caption says 'regression adn machine-learning-based estimators'—'adn' should be 'and.'
  3. [Figure 2] The figure panel includes stray text such as 'BOX ： 00 00' and the layout of the numeric summaries is hard to read. Please clean up the annotation and ensure the boxplot/error-rate panels are legible at print resolution.
  4. [References] The EMA guidance URL in reference [6] appears malformed ('euincremental/docpredefinedindicative-guideline'); please correct it.
  5. [§Methods, Datasets and preprocessing] The description of missing outcome handling says variables with >40% missingness were excluded and remaining missing outcomes were 'noted as N/A and dropped.' This is complete-case analysis; please state explicitly in the limitations that complete-case exclusion may affect estimates of precision, especially for binary outcomes.

Circularity Check

0 steps flagged

No circularity: the paper is an empirical benchmark, not a derivation; no prediction is forced by construction.

full rationale

This is an empirical benchmarking study, not a derivation chain. The central conclusions—covariate adjustment reduces variance (median PVR 13.3% continuous, 4.6% binary), parsimonious regression performs at least as well as machine-learning estimators, and Baseline+ is recommended—are summaries of computations on 50 external trial datasets, not consequences of fitted parameters. The PVR metric compares each adjusted estimator's variance with the unadjusted estimator's variance on the same data; it is a descriptive operating-characteristic comparison, and the paper does not present it as an out-of-sample prediction. The Top-3 strategy does select covariates using outcome correlations in the same datasets where PVR is then measured, which gives an in-sample, likely optimistic estimate; however, the paper itself flags 'invalidity from data-driven selection,' and the main recommendation (Baseline+) is prespecified and evaluated independently. This is a methodological limitation, not equation-level circularity. The differential error rates for binary outcomes (DML 12%, TMLE 4% vs. lower rates for ANCOVA) are a differential-completion concern affecting internal comparison, but not circularity. The self-citations to Wang et al. [18,27] for the ANCOVA interpretation and the Baseline+ variable set are routine and not load-bearing: they point to published external methodology, and the benchmark's claims stand on the reported empirical comparisons across 574 treatment-outcome pairs. The manuscript also explicitly acknowledges its main generalizability limitation: 'it may not be fully representative of the broader landscape of modern clinical trials'—a caveat, not a circular step. No specific reduction (e.g., Eq. X = Eq. Y by construction, or a fitted parameter renamed as a prediction) can be exhibited. Therefore, no significant circularity is present.

Axiom & Free-Parameter Ledger

4 free parameters · 5 axioms · 0 invented entities

The central empirical claims rest on domain assumptions about representativeness and on design choices (Top-3 selection, Baseline+ set, default hyperparameters). No fitted constants drive the conclusions, but the hand-chosen analysis configurations are free parameters in the benchmarking protocol. No new entities are postulated.

free parameters (4)
  • Top-3 k = 3
    The number of covariates selected by strength of outcome correlation is fixed at 3 by the authors; results for the Top-3 strategy depend on this arbitrary choice.
  • Missingness exclusion threshold = 40%
    Outcome variables with more than 40% missingness were excluded; the threshold is hand-chosen and affects dataset composition.
  • Baseline+ covariate set = baseline outcome, stratification factors, age, sex, weight when available
    The recommended prespecified adjustment set is hand-selected by the authors; precision gains and recommendations depend on this choice.
  • ML hyperparameter defaults = R package defaults (SuperLearner, tmle, custom DML)
    Machine-learning estimators are run without tuning; the conclusion that they do not outperform simple models is contingent on these defaults.
axioms (5)
  • standard math Unadjusted difference in means is unbiased and consistent for the marginal ATE under randomization
    Used as the reference point for S-Diff; standard result for simple randomization.
  • domain assumption The 50-trial public repository corpus represents real-world RCTs well enough to support general recommendations
    Necessary for external validity; explicitly acknowledged as uncertain in the Discussion.
  • domain assumption Sandwich variance estimates remain valid after data-driven covariate selection (Top-3) on the same data
    PVR for Top-3 is computed from variance estimates after selecting covariates using outcome correlations; this ignores model-selection uncertainty.
  • domain assumption Package-default hyperparameters fairly represent machine-learning estimators' performance
    Conclusion that ML offers no advantage depends on default settings; the paper notes tuning could improve performance.
  • domain assumption Ignoring missing outcomes and covariate-adaptive randomization does not materially change relative method performance
    The Methods section excludes missing outcomes and does not explicitly model covariate-adaptive randomization; if these interact with adjustment strategies, rankings could change.

reviewed 2026-08-03 · how reviews work

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Cite this review

Pith. "Pith review of How should covariates be handled in randomized trials? Empirical evidence from 50 trials and recommendations for practice." pith.science (2026). https://pith.science/paper/SVZMKF5H

@misc{pith2026260200434,
  author       = {Pith},
  title        = {Pith review of: How should covariates be handled in randomized trials? Empirical evidence from 50 trials and recommendations for practice},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/SVZMKF5H}},
  note         = {Machine review of arXiv:2602.00434}
}
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read the original abstract

Background and Objective: Covariate adjustment can improve precision and power in randomized clinical trials and is recommended by major regulatory agencies. However, there is limited empirical evidence on how different adjustment strategies perform across diverse real-world trials, leaving uncertainty about which methods and covariates should be prespecified in statistical analysis plans. We aim to address this gap and provide practical recommendations. Methods: We conducted a large-scale empirical study using individual-level data from 50 publicly available randomized trials (29,094 participants; 574 treatment-outcome comparisons). We compared commonly used covariate-adjusted estimators, including analysis of covariance, inverse-probability weighting, g-computation, and machine-learning-based approaches, combined with three covariate-selection strategies. Performance was evaluated using precision gains, changes in point estimates, computational reliability, and the probability that covariate adjustment altered statistical significance relative to an unadjusted analysis. Results: Covariate adjustment improved precision in most settings, with a median variance reduction of 13.3\% for continuous outcomes and 4.6\% for binary outcomes. Parsimonious regression approaches using a small prespecified set of prognostic covariates performed as well as or better than more complex methods, particularly in small to medium samples. Machine-learning-based estimators did not provide additional precision and were more prone to computational failure for binary outcomes. Conclusions: Across trials, parsimonious covariate adjustment provided consistent efficiency gains without introducing systematic bias. These findings support routine covariate adjustment in primary trial analyses. All curated datasets and analysis code are openly released to support future clinical research.

Figures

Figures reproduced from arXiv: 2602.00434 by Bingkai Wang, Liangbo Lyu, Menggang Yu, Yulin Shao.

Figure 1
Figure 1. Figure 1: Workflow of the benchmarking study. Panel A displays [PITH_FULL_IMAGE:figures/full_fig_p006_1.png] view at source ↗
Figure 2
Figure 2. Figure 2: The summary results of the method comparison for con [PITH_FULL_IMAGE:figures/full_fig_p008_2.png] view at source ↗
Figure 3
Figure 3. Figure 3: Proportional variance reduction varied by sample s [PITH_FULL_IMAGE:figures/full_fig_p009_3.png] view at source ↗
Figure 4
Figure 4. Figure 4: Performance of machine-learning algorithms with TM [PITH_FULL_IMAGE:figures/full_fig_p013_4.png] view at source ↗
Figure 5
Figure 5. Figure 5: Practical recommendations for covariate adjustme [PITH_FULL_IMAGE:figures/full_fig_p015_5.png] view at source ↗

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This paper was first reviewed by deepseek-v4-flash on August 3, 2026.