Bio Clinical Biostatistics Subgroup Analysis

Version Compatibility

Reference examples tested with: statsmodels 0.14+, scipy 1.12+, numpy 1.26+, pandas 2.1+, matplotlib 3.8+, scikit-learn 1.4+. R packages cited: grf, policytree, causalToolbox, personalized, SIDES, stepp, gMCP, partykit, RBesT, brms.

Before using code patterns, verify installed versions match. If versions differ:

• Python: pip show <package> then help(module.function) to check signatures
• R: packageVersion('<pkg>') then ?function_name

If code throws ImportError, AttributeError, or TypeError, introspect the installed package and adapt the example to match the actual API rather than retrying.

Subgroup Analysis and Heterogeneous Treatment Effects

"Analyze treatment effects across subgroups" -> Test whether treatment effects differ across pre-specified or data-discovered subgroups using interaction tests, stratified estimators, modern data-adaptive HTE methods, or Bayesian shrinkage -- with explicit declaration of confirmatory vs exploratory intent and credibility assessment.

The Senn Foundation -- Why Most Subgroup Claims Are Wrong

Senn 2018 Nature 563:619-621 (and Statistical Issues in Drug Development Ch. 9, 14): observed between-patient response variation is NOT evidence of patient-level HTE. It conflates within-patient noise, period effects, regression-to-the-mean, and measurement error with true individual heterogeneity. Senn-Rolfe-Julious 2011 SMMR 20:657 documents that variance-component decomposition of replicate-crossover trials repeatedly fails to find subject-by-treatment interaction even where reviewers were certain one must exist.

Brookes et al 2004 J Clin Epidemiol 57:229 — the 4x penalty: detecting a treatment-by-subgroup interaction requires approximately 4x the sample size needed to detect the main treatment effect of similar magnitude. A trial powered to detect OR=0.6 overall cannot reliably detect subgroup differences of similar magnitude. Non-significant interaction tests are usually underpowered, not null.

Senn's aphorism (paraphrased from SIDD): "a trial can have subgroup analyses or proper power, not both." A single trial cannot simultaneously be powered for a primary effect AND for credible subgroup discovery; pretending otherwise misrepresents posterior uncertainty.

Algorithmic Taxonomy

Postdoc reading list:

• Wang et al 2007 NEJM 357:2189 ("Reporting of subgroup analyses in clinical trials") — the canonical NEJM-mandated practice
• Sun et al 2010/2012 BMJ 340:c117 and 344:e1553 — 11 credibility criteria
• Dane, Spencer, Rosenkranz, Lipkovich, Parke 2019 Pharm Stat 18:126 with Hemmings-Koch commentary at 18:140 — EFSPI white paper + critique
• EMA 2019 Guideline on subgroups (CHMP/EWP/117211/2010 effective Aug 2019) — distinguishes "assessment subgroups" (regulatory, pre-specified) from "discovery subgroups" (exploratory)
• Athey & Wager 2019 Observational Studies 5:37; Athey, Tibshirani, Wager 2019 Ann Stat 47:1148 — causal forests
• Rehill 2025 Int Stat Rev — applied causal forest audit; ~70% of papers misreport tuning and skip honest-splitting validation

Decision Tree by Scenario

Mantel-Haenszel and Stratified Analysis

Goal: Estimate a pooled treatment effect across strata while testing homogeneity.

Approach: Construct per-stratum 2x2 tables; CMH for pooled OR and null test; Breslow-Day for homogeneity (with caveats).

from statsmodels.stats.contingency_tables import StratifiedTable
import pandas as pd
import numpy as np

tables = []
for stratum in df['site'].unique():
    sub = df[df['site'] == stratum]
    t = pd.crosstab(sub['treatment'], sub['outcome']).values
    if t.shape == (2, 2) and t.min() > 0:
        tables.append(t)

st = StratifiedTable(tables)
print('MH pooled OR:', st.oddsratio_pooled)
print('95% CI:', st.oddsratio_pooled_confint())
print('CMH H0: common OR=1, p =', st.test_null_odds().pvalue)
print('Breslow-Day H0: equal ORs, p =', st.test_equal_odds().pvalue)

Breslow-Day power trap: with k=3 strata and modest heterogeneity, Breslow-Day power can be <40%. Non-significance does NOT prove homogeneity — it just means the null cannot be rejected. Always supplement with a forest plot AND an LR interaction test from logistic regression.

Interaction Terms in Regression -- The Correct Way

Single model with interaction is the regulatory standard — comparing p-values from separate per-subgroup models is statistically invalid (separate models have different power, and the p-value differences confound effect size with sample size).

import statsmodels.formula.api as smf
import numpy as np

# Single model with interaction (CORRECT)
model = smf.logit(
    'outcome ~ C(treatment, Treatment(reference="Placebo")) * C(age_group)',
    data=df
).fit()
# Interaction coefficient tests effect modification
# LR test: compare to additive model:
additive = smf.logit('outcome ~ C(treatment, Treatment(reference="Placebo")) + C(age_group)', data=df).fit()
lr_p = 1 - chi2.cdf(2 * (model.llf - additive.llf), model.df_model - additive.df_model)

# Extract subgroup-specific ORs for reporting:
for group in df['age_group'].unique():
    sub_model = smf.logit('outcome ~ C(treatment, Treatment(reference="Placebo"))',
                          data=df[df['age_group'] == group]).fit()
    or_val = np.exp(sub_model.params.iloc[1])
    ci = np.exp(sub_model.conf_int().iloc[1])
    print(f'{group}: OR={or_val:.3f} ({ci[0]:.3f}-{ci[1]:.3f})')

RERI for Additive Interaction

# Fit interaction model: outcome ~ treatment + subgroup_indicator + treatment:subgroup_indicator
# OR_11 = OR for treated in subgroup (vs untreated not in subgroup)
# OR_10 = OR for treated not in subgroup
# OR_01 = OR for untreated in subgroup
reri = or_11 - or_10 - or_01 + 1
# RERI > 0 = synergism (combined effect > sum of individual)
# RERI = 0 = no additive interaction
# RERI < 0 = antagonism
# CI requires delta method or bootstrap (nonlinear function of three ORs)

Multiplicative vs additive interaction: logistic regression tests multiplicative interaction (ratio of ORs). Null multiplicative interaction does NOT imply null additive interaction. For public health decisions, additive interaction is often more relevant.

Modern Data-Adaptive HTE Methods

STEPP (Subpopulation Treatment Effect Pattern Plot)

# R recommended; Python equivalents are emerging
# library(stepp)
# subset_obj <- new('stwin', type='sliding', r1=100, r2=200)  # window sizes
# step_obj <- stepp(eff='binary', cov='biomarker', trt='treatment',
#                   resp='outcome', subset=subset_obj, ...)
# plot(step_obj); test_pattern(step_obj, nperm=1000)

Bonetti-Gelber 2000/2004; window-size choice (sliding vs tail-oriented) affects results. Naive simultaneous CIs are wrong — estimates are correlated across windows; use permutation-based supremum tests of pattern flatness (Yip et al 2016 Stat Med 35:5437 documents 30% disagreement between sliding and tail-oriented variants).

SIDES / SIDEScreen

# R: library(SIDES) or library(rsides)
# Recursive partitioning with differential-effect splitting + permutation-adjusted subgroup p

Lipkovich-Dmitrienko-Denne-Enas 2011 Stat Med 30:2601; SIDEScreen (Lipkovich-Dmitrienko 2014 J Biopharm Stat 24:130) adds variable-importance prefilter + base-vs-complement test. The inferential complement test correctly absorbs multiplicity of considered splits — Bonferroni alternatives over-correct.

Causal forests (Athey-Wager)

# R recommended; econml is the Python equivalent
# library(grf)
# cf <- causal_forest(X, Y, W, num.trees=2000)
# tau.hat <- predict(cf, X)$predictions
# test_calibration(cf)  # omnibus calibration test

Honest splitting (one sub-sample for splits, another for leaf estimates) yields asymptotic Gaussianity and pointwise CIs (Athey-Tibshirani-Wager 2019 Ann Stat 47:1148). Doubly-robust variants use AIPW pseudo-outcomes.

Diagnostic discipline (Rehill 2025 audit): ~70% of applied causal-forest papers misreport tuning, skip honest-splitting validation, or omit the test_calibration check. Required diagnostic steps:

1. Honest splitting enabled (honesty=TRUE)
2. test_calibration(cf) — regresses actual treatment effects on out-of-bag CATE predictions; significant positive slope = CATE has signal
3. Variable importance via permutation
4. RATE/AUTOC test (Yadlowsky 2025 JASA) — single p-value omnibus test for whether CATE ranking has predictive (not just prognostic) value

Meta-learners (Künzel-Sekhon-Bickel-Yu 2019 PNAS 116:4156)

• S-learner: single outcome model on (Z, X); take difference. Biased when treatment effect smaller than baseline effect.
• T-learner: separate models per arm; take difference. Standard baseline.
• X-learner: T-learner + cross-imputation + propensity weighting. Dominates T-learner when arms unbalanced (1:k, k>=3) or true CATE is smoother than response.
• R-learner (Nie-Wager 2021 Biometrika 108:299): orthogonal Robinson-style residualisation, debiased ML. Asymptotically dominates X-learner when nuisance models converge at n^(1/4) rate.

# Python: econml
from econml.dml import CausalForestDML, LinearDML
from econml.metalearners import XLearner, TLearner
# Or: from causalml.inference.meta import LRSRegressor, XGBTRegressor

xl = XLearner(models=GradientBoostingRegressor(), propensity_model=LogisticRegression())
xl.fit(Y, T=W, X=X)
cate = xl.effect(X)

Bayesian Shrinkage -- The Postdoc Argument

Dixon-Simon 1991 Biometrics 47:871: exchangeable mean-zero prior on treatment-by-subgroup interaction coefficients; subgroup posteriors shrink to overall trial effect, proportional to evidence of heterogeneity. Honest about prior expectation that no qualitative interaction will hold.

Berry, Broglio, Groshen, Berry 2013 Clin Trials 10:720 (NOT JCO — common citation error): hierarchical pooling across baskets calibrated by between-basket variance tau-squared. Inflated false-positives when tau-squared mis-specified (Freidlin-Korn 2013 JNCI 105:1532 critique).

EXNEX (Neuenschwander, Wandel, Roychoudhury, Bailey 2016 Pharm Stat 15:123): mixture of exchangeable (shared mean+variance) + non-exchangeable (per-basket independent) components, typically weighted 0.5/0.5. Avoids HM catastrophic borrowing when one basket truly different. Now near-standard in oncology basket trials.

MAP priors (Schmidli et al 2014 Biometrics 70:1023): meta-analytic-predictive prior. Fit random-effects meta-analysis of historical control arms, derive predictive distribution for new control arm, use as informative prior. Effective sample size from history typically 20-80% of new control arm. Robust MAP adds vague mixture component (weight 0.1-0.3) to guard against prior-data conflict. R RBesT is the canonical CRAN tool (Weber et al 2021 J Stat Softw 100:19).

The Dane vs Hemmings argument:

• Dane et al 2019 Pharm Stat 18:126 (EFSPI white paper): propose a standardised-effect benchmark in the neighbourhood of ~0.5σ for "noteworthy heterogeneity" (verify the exact figure against the white paper before quoting); tiered structure (key/important/exploratory); signal-vs-noise diagnostics.
• Hemmings & Koch 2019 Pharm Stat 18:140 commentary: explicitly REJECT Bayesian shrinkage for signal generation because "Bayesian shrinkage assumes treatment effects are consistent" and pre-emptively damps the very heterogeneity one is searching for. Shrinkage is endorsed only for post-signal replication planning.

What postdocs argue about: whether shrinkage is appropriate at the signal-generation stage; the prior on tau drives everything (Senn-style: tau ~ HalfNormal(0, 0.1); regulatory-tolerant: tau ~ HalfNormal(0, 0.5)).

Multiplicity for Subgroup Analyses

Bonferroni is rarely right for subgroup tests because they are heavily positively correlated (same outcome, overlapping samples). Bonferroni assumes worst-case dependence; loses 30-50% power vs Hommel/resampling for ~10 demographic subgroups.

Graphical procedures (Bretz-Maurer-Hommel) — see clinical-biostatistics/multiplicity-graphical for full treatment. The graph for a typical subgroup analysis SAP:

• Primary endpoint at full alpha
• Alpha propagates to "key secondary" endpoints if primary rejects
• Alpha propagates to pre-specified subgroup interaction tests if primary rejects
• Discovery subgroups at most receive a small alpha slice (Dane et al recommend <=20%)

# R: library(gMCP); graphView(graphMCP(...))  # interactive or programmatic

Goeman, Hemerik, Solari 2021 Ann Stat 49:1218: "only closed testing procedures are admissible for controlling FDP/FWER/k-FWER" — graphical, gatekeeping, Hommel, fallback are all closed tests in disguise. The graph IS the procedure.

Pre-Specified vs Post-Hoc and EMA 2019

EMA 2019 Guideline on Investigation of Subgroups in Confirmatory Trials (CHMP/EWP/117211/2010, effective Aug 2019) position: interaction tests alone are "neither necessary nor sufficient"; consistency is a holistic judgment; subgroup-specific licensing requires pre-specified evidence of differential effect PLUS biological rationale.

Sun BMJ 2012 11 credibility criteria (the canonical academic framework):

1. Covariate measured pre-randomisation
2. A priori hypothesis
3. Direction pre-specified
4. One of few tests with multiplicity adjustment
5. Within-study comparison (not between)
6. Interaction test significant
7. Statistically independent subgroup
8. Large effect and all subgroups reported
9. Consistent across related outcomes
10. Consistent across studies
11. Biological plausibility / indirect evidence

Quantitative vs Qualitative Interaction

Gail-Simon 1985 Biometrics 41:361: LR test against the "all-same-direction" null. Distinguishes quantitative (magnitude varies, direction preserved) from qualitative (sign reverses) — only the latter carries decision-changing weight clinically.

Pan-Wolfe 1997 Biometrics 53:1564, Li-Chan 2006 Stat Med 25:2099: exact critical values for Gail-Simon; original normal-approximation is liberal at small n.

Why qualitative interaction matters for regulators: may warrant restricting indication to the benefiting subgroup (label carve-out).

The Winner's Curse and Sun et al 2012

Sun et al 2012 BMJ systematic review documented that the median observed effect size in significant subgroups across 64 trials was approximately 2.4x larger than the trial-overall effect — textbook winner's curse signature.

Mechanism: selecting a subgroup conditional on its interaction p being small selects for upward sampling fluctuations; the posterior MLE conditional on selection is biased upward by ~SE × inverse Mills ratio at the selection threshold.

Mitigations:

• Bayesian shrinkage (Dixon-Simon, RBesT) — posterior subgroup means shrink to overall
• Cross-validation (Athey-Wager honest splitting)
• Yadlowsky RATE 2025 JASA — single-p omnibus test for whether CATE ranking has predictive vs prognostic value

Reconciliation: When Methods Disagree

Per-Method Failure Modes

CMH masking Simpson's paradox

• Trigger: Stratum-specific ORs reverse direction; pooled MH OR appears null.
• Mechanism: CMH pools weighted log-ORs; opposite-sign equal-magnitude cancel.
• Symptom: Breslow-Day p < 0.05 with visible stratum sign reversal.
• Fix: Report stratum-specific as primary; switch to logistic with interaction term; pooled OR invalid.

Breslow-Day false reassurance

• Trigger: Few strata (k<5) or sparse strata.
• Mechanism: Low power; chi-square with k-1 df.
• Symptom: Breslow-Day p>0.5 with forest plot showing visible heterogeneity.
• Fix: Forest plot + LR interaction test from logistic regression.

STEPP correlated estimates with naive CI

• Trigger: STEPP plot with naive pointwise CIs at each window.
• Mechanism: Overlapping windows share patients; estimates are correlated.
• Symptom: Apparent significance at individual windows that disappears under permutation.
• Fix: Permutation-based supremum test of pattern flatness; report supremum p, not pointwise.

Causal forest without honest splitting

• Trigger: Default settings without honesty=TRUE.
• Mechanism: In-sample split selection biases leaf estimates.
• Symptom: Over-fit CATE; failed test_calibration.
• Fix: Always honesty=TRUE; tune via tune.parameters="all"; cite Rehill 2025 audit.

Bayesian shrinkage damping real heterogeneity

• Trigger: Hierarchical model fit during signal discovery (not replication planning).
• Mechanism: Prior on tau forces subgroup effects toward overall.
• Symptom: Subgroup detected by causal forest gets shrunken to null in shrinkage analysis.
• Fix: Hemmings-Koch position — shrinkage for replication planning, NOT signal generation; cite Dane et al 2019 + critique.

EXNEX with default 0.5/0.5 weights when one basket genuinely different

• Trigger: Default mixture weights without elicitation.
• Mechanism: 50% EX weight still allows substantial borrowing.
• Symptom: Detected differential basket "softened" by borrowing.
• Fix: Sensitivity analysis over mixture weights (0.1, 0.3, 0.5, 0.7, 0.9); report range.

Stratified randomisation ignored in subgroup analysis

• Trigger: Site-stratified randomisation; subgroup analysis without site adjustment.
• Mechanism: Achieved SE smaller than calculated SE.
• Symptom: Anti-conservative subgroup interaction tests.
• Fix: Include stratification factors as model covariates (Kahan-Morris 2012).

Quantitative Thresholds

Common Errors

Anticipated Reviewer Pushback

References

• Athey S, Tibshirani J, Wager S. 2019. Generalized random forests. Ann Stat 47:1148-1178.
• Berry SM, Broglio KR, Groshen S, Berry DA. 2013. Bayesian hierarchical modeling of patient subpopulations: efficient designs of Phase II oncology clinical trials. Clin Trials 10:720-734.
• Bonetti M, Gelber RD. 2000. A graphical method to assess treatment-covariate interactions using the Cox model on subsets. Biostatistics 1:227-240.
• Bonetti M, Gelber RD. 2004. Patterns of treatment effects in subsets of patients in clinical trials. Biostatistics 5:465-481.
• Bretz F, Maurer W, Brannath W, Posch M. 2009. A graphical approach to sequentially rejective multiple test procedures. Stat Med 28:586-604.
• Brookes ST, Whitely E, Egger M, Davey Smith G, Mulheran PA, Peters TJ. 2004. Subgroup analyses in randomised controlled trials: quantifying the risks of false-positives and false-negatives. J Clin Epidemiol 57:229-236. (Author surname is "Whitely", not "Whitley".)
• Dane A, Spencer A, Rosenkranz G, Lipkovich I, Parke T. 2019. Subgroup analysis and interpretation for phase 3 confirmatory trials: white paper of the EFSPI/PSI working group. Pharm Stat 18:126-139.
• Dixon DO, Simon R. 1991. Bayesian subset analysis. Biometrics 47:871-881.
• Dusseldorp E, Van Mechelen I. 2014. Qualitative interaction trees: a tool to identify qualitative treatment-subgroup interactions. Stat Med 33:219-237.
• EMA. 2019. Guideline on the investigation of subgroups in confirmatory clinical trials. CHMP/EWP/117211/2010.
• Foster JC, Taylor JMG, Ruberg SJ. 2011. Subgroup identification from randomized clinical trial data. Stat Med 30:2867-2880.
• Gail M, Simon R. 1985. Testing for qualitative interactions between treatment effects and patient subsets. Biometrics 41:361-372.
• Goeman JJ, Hemerik J, Solari A. 2021. Only closed testing procedures are admissible for controlling false discovery proportions. Ann Stat 49:1218-1238.
• Hemmings R, Koch A. 2019. Commentary on Dane et al. Pharm Stat 18:140-141.
• Kahan BC, Morris TP. 2012. Improper analysis of trials randomised using stratified blocks or minimisation. Stat Med 31:328-340.
• Künzel SR, Sekhon JS, Bickel PJ, Yu B. 2019. Metalearners for estimating heterogeneous treatment effects using machine learning. PNAS 116:4156-4165.
• Lipkovich I, Dmitrienko A, Denne J, Enas G. 2011. Subgroup identification based on differential effect search: SIDES. Stat Med 30:2601-2621.
• Neuenschwander B, Wandel S, Roychoudhury S, Bailey S. 2016. Robust exchangeability designs for early phase clinical trials with multiple strata. Pharm Stat 15:123-134.
• Nie X, Wager S. 2021. Quasi-oracle estimation of heterogeneous treatment effects. Biometrika 108:299-319.
• Pan G, Wolfe DA. 1997. Test for qualitative interaction of clinical significance. Biometrics 53:1564-1570.
• Rehill A. 2025. A reliability review of applications of generalized random forests. Int Stat Rev.
• Schmidli H, Gsteiger S, Roychoudhury S, O'Hagan A, Spiegelhalter D, Neuenschwander B. 2014. Robust meta-analytic-predictive priors in clinical trials with historical control information. Biometrics 70:1023-1032.
• Senn S. 2018. Statistical pitfalls of personalised medicine. Nature 563:619-621.
• Sun X, Briel M, Walter SD, Guyatt GH. 2010. Is a subgroup effect believable? Updating criteria to evaluate the credibility of subgroup analyses. BMJ 340:c117.
• Sun X et al. 2012. Credibility of claims of subgroup effects in randomised controlled trials: systematic review. BMJ 344:e1553.
• Wager S, Athey S. 2018. Estimation and inference of heterogeneous treatment effects using random forests. JASA 113:1228-1242.
• Wang R, Lagakos SW, Ware JH, Hunter DJ, Drazen JM. 2007. Statistics in medicine -- reporting of subgroup analyses in clinical trials. NEJM 357:2189-2194.
• Weber S, Li Y, Seaman J, Kakizume T, Schmidli H. 2021. Applying meta-analytic-predictive priors with the R Bayesian evidence synthesis tools. J Stat Softw 100:19.
• Yadlowsky S, Fleming S, Shah N, Brunskill E, Wager S. 2025. Evaluating treatment prioritization rules via rank-weighted average treatment effects. JASA 120(549):38-51.

Related Skills

• clinical-biostatistics/categorical-tests - CMH, Breslow-Day, chi-square within strata
• clinical-biostatistics/effect-measures - Forest plots, OR/RR/RD reporting
• clinical-biostatistics/logistic-regression - Interaction terms in regression
• clinical-biostatistics/multiplicity-graphical - Bretz-Maurer graphical procedures (in depth)
• clinical-biostatistics/bayesian-trials - MAP/EXNEX/Berry hierarchical models (in depth)
• clinical-biostatistics/trial-reporting - CONSORT 2025 + EMA 2019 reporting of subgroup analyses
• experimental-design/multiple-testing - General multiplicity correction methods
• machine-learning/biomarker-discovery - HTE for biomarker-defined subgroups