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
Method
What it answers
Inference
Strength
Fails when
Mantel-Haenszel / CMH
Common OR across pre-defined strata
Asymptotic
Preserves stratification factor from randomisation
Stratum ORs reverse direction (Simpson)
Breslow-Day
Homogeneity of stratum ORs
Asymptotic chi-square
Test of effect modification
Underpowered with few/sparse strata; non-significance NOT proof of homogeneity
Gail-Simon 1985
Qualitative interaction (sign reversal)
Likelihood ratio
Distinguishes quantitative from qualitative
Original LR is liberal at small n; use exact critical values (Pan-Wolfe 1997)
Logistic regression interaction
Per-subgroup conditional OR
Wald, LR
Most efficient single-model approach
Conditional ORs subject to non-collapsibility; over-fits in multi-way
RERI
Additive interaction on multiplicative scale
Delta-method or bootstrap CI
Captures public-health-relevant scale
Delta-method poor near boundary; nonlinear function of three ORs
STEPP (Bonetti-Gelber 2000)
Continuous covariate subgroups via overlapping windows
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 (EMA/CHMP/539146/2013, 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; many papers misreport tuning and omit honest-splitting/calibration diagnostics
Decision Tree by Scenario
Scenario
Recommended approach
Why
Pre-specified subgroup in confirmatory trial
Interaction term in single model + graphical-procedure multiplicity (gMCP)
EMA 2019 "assessment subgroup"; interaction test + Bonferroni-graph alpha control
Stratified randomisation by site/region
CMH or logistic with strata as covariates; stratum-specific OR reported in forest plot
Kahan-Morris 2012; ignoring strata is over-conservative (SE biased upward, power loss); strata-specific ORs for transparency
Gail-Simon 1985 LR test with Pan-Wolfe 1997 exact critical values
Distinguishes quantitative from qualitative; critical for label restriction
Data-discovery of HTE subgroup
SIDES/SIDEScreen with permutation FWER + replication mandate
Lipkovich 2011; signal-discovery not signal-confirmation
Continuous CATE estimation with many covariates
Causal forest (R grf::causal_forest) + RATE test (Yadlowsky 2025)
Modern HTE; honest splitting; influence-function CIs; RATE tests whether ranking is predictive vs prognostic
Basket trial across rare-disease strata
EXNEX or robust MAP with RBesT
Borrows across strata while permitting one to detach if truly different
Subgroup signal needing replication planning
Bayesian shrinkage for adjusted estimates; Sun 2012 winner's curse
Selected subgroups have inflated effect by selection bias
Pediatric extrapolation borrowing from adult data
Power prior (gamma in 0.3-0.6) per FDA Bayesian draft Jan 2026
Partial borrowing with discount; standard regulatory approach
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.
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 Clin Trials 13(4):382; tail-oriented STEPP is more stable than the sliding-window variant).
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.
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 Clin Cancer Res 19:1326 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
Aspect
Pre-specified ("assessment")
Post-hoc ("discovery")
Timing
Before unblinding, in SAP
After seeing data
Credibility
High if biologically justified
Low; hypothesis-generating only
Regulatory weight per EMA 2019
Can support labeling claims
Cannot support claims alone
Multiplicity adjustment
Required per SAP (graphical or Holm)
Required + heavy skepticism
Number expected
Few (5-15); pre-justified
Unlimited but unblindable
EMA 2019 Guideline on Investigation of Subgroups in Confirmatory Trials (EMA/CHMP/539146/2013, 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):
Covariate measured pre-randomisation
A priori hypothesis
Direction pre-specified
One of few tests with multiplicity adjustment
Within-study comparison (not between)
Interaction test significant
Statistically independent subgroup
Large effect and all subgroups reported
Consistent across related outcomes
Consistent across studies
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 Stat Med 16(14):1645, Li-Chan 2006 J Biopharm Stat 16(6):831: tests for qualitative interaction of clinical significance; the original Gail-Simon normal-approximation LR 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 found that of 207 trials reporting subgroup analyses, 64 claimed a primary-outcome subgroup effect, yet most claims failed the credibility criteria — the textbook winner's-curse signature, where effects in selected significant subgroups are inflated by chance and regression to the mean.
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
Pattern
Likely cause
Action
Causal forest CATE shows HTE; interaction test in logistic non-significant
Causal forest detects nonlinear/multivariate HTE; interaction test only linear bivariate
Causal forest with Yadlowsky RATE 2025 omnibus test is more sensitive; cite as discovery, not confirmatory; replicate in independent sample
STEPP pattern significant at one window choice; flat at another
Window-size choice (sliding vs tail-oriented) affects results (Yip 2016; tail-oriented more stable than sliding)
Pre-specify window choice in SAP; report sensitivity over choices; use permutation supremum test
Bayesian shrinkage (Dixon-Simon) yields null subgroup effect; frequentist sees signal
tau ~ HalfNormal(0, 0.1), 0.25, 0.5 reported; results stable across plausible priors.
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 of the data. Stat Med 19(19):2595-2609.
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 randomized trials: risks of subgroup-specific analyses; power and sample size for the interaction test. 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. EMA/CHMP/539146/2013.
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 18:140-144.
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. Stat Med 16(14):1645-1652.
Rehill P. 2025. How do applied researchers use the causal forest? A methodological review. 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
