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

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	Permutation supremum test	Avoids dichotomisation of biomarkers	Window-size choice affects results; correlated estimates require permutation inference
SIDES / SIDEScreen (Lipkovich 2011)	Data-discovered subgroups via recursive partitioning	Resampling-adjusted base-vs-complement p	Multiplicity correctly absorbed	Tuning skeleton parameters affects FWER calibration
QUINT (Dusseldorp 2014)	Qualitative-interaction trees	Bootstrap stability	Directly tests crossover (A-better, B-better, equal)	Only two-arm continuous/binary; survival extensions ad hoc
Virtual Twins (Foster 2011)	Per-subject CATE via twin RF predictions	Bootstrap	Decouples nuisance from interpretable subgroup	Biased when RF underestimates effect heterogeneity in either arm
Causal forests (Athey-Wager 2019)	Pointwise CATE with honest splits	Influence-function CI	Asymptotic Gaussianity; doubly robust via AIPW	Finite-sample CI validity at trial-scale n debated (Rehill 2025)
Meta-learners X/R-learner (Künzel 2019)	Marginal/conditional CATE	Cross-fit influence function	X-learner dominates T-learner when arms unbalanced	Needs propensity for X-learner; R-learner requires nuisance n^(1/4) rate
MOB (Zeileis 2008)	Parameter-instability trees	M-fluctuation test	Theoretically clean; invariant to monotone transforms	Worse out-of-sample CATE than causal forest at large p
Bayesian shrinkage (Dixon-Simon 1991)	Posterior subgroup effects shrunken to overall	Posterior intervals from MCMC	Honest about prior expectation of no qualitative interaction	Prior choice on tau drives results; Dane et al 2019 white paper warns against for signal generation
EXNEX (Neuenschwander 2016)	Mixture of exchangeable + per-basket non-exchangeable	Posterior	Avoids HM "catastrophic borrowing" when one basket truly different	Weight choice (often 0.5/0.5 default) affects borrowing strength

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 (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
5-15 pre-specified subgroups, regulatory submission	Forest plot + interaction tests + Holm/graphical FWER correction	Default regulatory presentation; multiplicity adjustment expected
Continuous biomarker subgroup (e.g., HbA1c, biomarker score)	STEPP (sliding-window plot + permutation supremum test)	Avoids arbitrary dichotomisation; cite Bonetti-Gelber 2004
Suspected qualitative interaction (treatment helps some, harms others)	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.

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 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.

Diagnostic discipline (Rehill 2025 audit): applied causal-forest papers frequently 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 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):

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 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	Shrinkage pulls subgroup posteriors toward overall trial effect	Bayesian shrinkage appropriate for replication PLANNING (Hemmings-Koch 2019), not signal generation; report frequentist as primary in discovery
MH stratified analysis gives different pooled OR than logistic with strata as covariates	MH conditions on stratum; logistic does not (assumes additivity of strata effects)	Both are valid under different assumptions; logistic preferred when stratum-treatment interaction tested formally
EXNEX basket trial gives different per-basket estimate under default 0.5/0.5 vs 0.3/0.7 mixture	Mixture weight controls borrowing strength (Neuenschwander 2016)	Sensitivity over weights 0.1-0.9; primary at 0.5/0.5; cite range
Gail-Simon qualitative interaction test rejects; LR interaction test does not	Qualitative test detects sign reversal; LR test detects magnitude	Both tests are answering different questions; qualitative interaction is regulatorily significant (label restriction)
Subgroup signal from data-adaptive HTE method (SIDES, causal forest) without replication	Winner's curse (Sun 2012); effects in selected subgroups are inflated	Apply Bayesian shrinkage OR honest cross-validation; report as discovery only; require Phase 3 replication
Causal forest test_calibration passes; RATE/AUTOC fails	test_calibration measures any signal (prognostic OR predictive); RATE measures predictive value	RATE 2025 is the modern omnibus; should replace test_calibration as primary HTE check

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: Over-conservative subgroup interaction tests (SE biased upward, Type-I below nominal, power loss).
• Fix: Include stratification factors as model covariates (Kahan-Morris 2012).

Quantitative Thresholds

Threshold	Source	Rationale
~4x sample size for interaction detection vs main effect	Brookes et al 2004 J Clin Epidemiol 57:229	Subgroup analyses are powered by interaction effect, not main effect
0.5σ standardised effect = "noteworthy heterogeneity"	Dane et al 2019 EFSPI white paper Pharm Stat 18:126	Discipline for declaring subgroup signals worth pursuing
Pre-specified subgroups for label claim	EMA 2019 subgroup guideline	Discovery subgroups cannot support indication restriction
Bonferroni: ~10 subgroups -> 30-50% power loss vs Hommel	Sarkar 1998	Subgroup tests positively correlated; Bonferroni over-conservative
Honest splitting required for causal forest	Athey-Tibshirani-Wager 2019; Rehill 2025	Without it, CIs are invalid; Rehill 2025 finds many applied papers omit it
11 credibility criteria	Sun BMJ 2012 344:e1553	Canonical academic checklist; EMA 2019 implicitly references
RATE/AUTOC test (Yadlowsky 2025)	JASA 120(549):38-51	Single-p omnibus for HTE-ranking predictive value

Common Errors

Error / symptom	Cause	Solution
Per-subgroup p-values compared as evidence of HTE	Statistically invalid	Single model with interaction term; report interaction p, not per-subgroup p
"Non-significant interaction = no HTE"	Underpowered interaction test	Cite Brookes 2004 4x rule; "absence of evidence" framing
Breslow-Day non-sig taken as homogeneity	Low power with few strata	Forest plot + LR interaction; cite EMA 2019
STEPP with naive pointwise CIs reported	Correlated estimates	Permutation supremum test (R stepp::test_pattern)
Causal forest CIs without honest splitting	Default settings	honesty=TRUE; tune; calibration test; cite Rehill 2025
Bayesian shrinkage for "fishing" subgroup discovery	Misapplication	Use for replication planning per Hemmings-Koch; cite Dane white paper
Selected subgroup effect reported without shrinkage	Winner's curse	Apply Bayesian shrinkage (RBesT) or report selection-corrected estimate
Subgroup p < 0.05 claimed as evidence with no multiplicity	Common SAP omission	Graphical procedure with pre-specified alpha allocation (gMCP)
MH pooled OR with sign-reversing stratum ORs	Simpson's paradox	Report stratum-specific; switch to interaction model
Causal forest tau.hat reported without RATE test	Missing modern omnibus test	Yadlowsky 2025 RATE/AUTOC; cite

Anticipated Reviewer Pushback

Pushback	Response
"Is this pre-specified?"	Per EMA 2019, distinguish assessment (pre-specified, regulatory weight) vs discovery (post-hoc, hypothesis-generating); be explicit.
"Where is multiplicity correction?"	Graphical procedure with alpha allocation per SAP; cite Bretz-Maurer 2009 + gMCP.
"Interaction power check?"	Brookes 2004: ~4x main effect SS needed; report interaction power calculation in SAP.
"Is this finding clinically plausible?"	Cite biological mechanism (e.g., known pharmacogenomic pathway); cite Sun 2012 criterion 11.
"Winner's curse control?"	Bayesian shrinkage per Dixon-Simon (RBesT) for adjusted estimate; or honest cross-validation.
"Why STEPP not categorical subgroups?"	Avoids arbitrary dichotomisation of continuous biomarker; cite Bonetti-Gelber 2004.
"Causal forest calibration?"	test_calibration p-value reported; honest splitting enabled; cite Rehill 2025 audit standards.
"Sensitivity to prior in shrinkage analysis?"	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.
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• 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.
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• 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.
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• 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.
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• 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.
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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