name: bio-clinical-biostatistics-power-sample-size description: Computes sample size and power for clinical trials including continuous, binary, and time-to-event endpoints; superiority, non-inferiority, and equivalence designs; FDA 2016 non-inferiority margin selection with M1/M2 framework; Schoenfeld 1981 and Lakatos 1988 for survival; Schuirmann TOST and 80-125% bioequivalence; minimum clinically important difference (MCID) vs δ distinction. Use when justifying trial size in protocol or SAP per CONSORT 2025 item 16a. goal_approach_exempt: true origin: openai4s category: bioskills/clinical-biostatistics metadata: tool_type: mixed primary_tool: statsmodels third_party: name: GPTomics/bioSkills repository: https://github.com/GPTomics/bioSkills commit: d91ed3d563019e649dc854c56ccd62551359488a license: MIT
Reference examples tested with: statsmodels 0.14+, scipy 1.12+, numpy 1.26+, pandas 2.1+. R packages cited: pwr, gsDesign (Anderson/Merck), gsDesign2, rpact (Wassmer/Brannath), presize, npsurvSS, nph, simtrial.
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.
"Justify the trial's sample size" -> Compute the n needed to detect a pre-specified alternative δ with power 1-β at significance α, accounting for endpoint distribution, design (superiority/NI/equivalence), expected dropout, multiplicity, and stratification — and distinguish δ (the effect the trial is powered to detect) from MCID (the clinically meaningful difference).
δ (the alternative effect): what the trial is powered to detect. Usually set above the MCID because sponsors want a strong signal that exceeds noise + design uncertainty.
MCID (Minimum Clinically Important Difference): the smallest effect size considered clinically meaningful. Jaeschke-Singer-Guyatt 1989 Control Clin Trials 10:407 (anchor-based) and Norman-Sloan-Wyrwich 2003 Med Care 41:582 ("the remarkable universality of half a standard deviation") established the modern conventions.
Confusing the two has produced both:
Postdoc rule of thumb: for superiority, δ >= 1.5 × MCID; for NI, M2 <= 0.5 × MCID.
| Design | Formula / approach | Software | Strength | Fails when |
|---|---|---|---|---|
| Two-sample t-test, continuous | Cohen's d; n = 2 × (z_α/2 + z_β)² / d² | pwr::pwr.t.test (R); statsmodels.power.tt_ind_solve_power (Py) |
Standard | Heteroscedasticity; non-normal outcomes |
| Two-sample proportions (Fleiss) | Asymptotic normal approximation with/without continuity correction | power.prop.test (R) -- uncorrected; pwr::pwr.2p.test; statsmodels |
Standard | n < 100/arm: continuity correction debate (D'Agostino 1988) |
| Survival (Schoenfeld 1981) | events ≈ 4(z_α/2 + z_β)² / (log HR)² for 1:1 | gsDesign::nSurv; npsurvSS::size_two_arm |
Standard PH-conformant | PH violated (immuno-oncology) under-estimates by 20-50% |
| Survival under non-PH (Lakatos 1988) | Markov chain accommodating time-varying HR, accrual, dropout | gsDesign::nSurv; npsurvSS; simtrial |
Handles immuno-oncology delayed effects | Requires explicit specification of HR(t) and accrual |
| MaxCombo SS under NPH | Simulation-based; pre-specify weight family | nphRCT; simtrial |
Robust to NPH pattern | Computationally heavier |
| Non-inferiority fixed-margin | n = (z_α + z_β)² × variance / M² | pwr::pwr.t2n.test adapted; rpact::getSampleSizeMeans |
Pre-discounted M | Constancy assumption violation invisible |
| Non-inferiority synthesis | Pool historical control-vs-placebo + current test-vs-control | gsDesign::ssTwoArmTest |
More efficient than fixed-margin | Constancy assumption MUST hold exactly |
| Equivalence TOST | Two one-sided tests at α each | pwr::pwr.t.test adapted; presize |
No multiplicity adjustment needed | Wrong question when superiority/NI is intended |
| Group-sequential | Lan-DeMets spending function | rpact; gsDesign |
Interim analyses; early stopping | More complex SAP |
| Sample-size re-estimation (Mehta-Pocock) | Promising-zone conditional power | rpact::getSampleSizeMeans with reestimation |
Recovers power if interim shows promise | Unblinded SSR scares FDA |
| Cluster-randomised | Adjust for design effect = 1 + (m-1)ICC | clusterPower; pwr adapted |
Standard | ICC misspecification |
Postdoc reading list:
| Scenario | Recommended approach | Why |
|---|---|---|
| Continuous outcome, two-arm parallel, superiority | Fleiss / Cohen's d formula via power.t.test or statsmodels |
Standard; cite Fleiss 1981 |
| Binary outcome, n > 100/arm | Uncorrected normal approximation via power.prop.test; statsmodels power_proportions_2indep |
Adequate for n > 100 |
| Binary outcome, n < 100/arm | Fisher exact-based simulation OR Fleiss with continuity correction | Continuity correction debate; cite D'Agostino 1988 if uncorrected |
| Time-to-event with PH | Schoenfeld 1981 via gsDesign::nSurv |
Standard; pre-specify hazards |
| Time-to-event under expected NPH (immuno-oncology) | Lakatos 1988 OR simulation via simtrial::simtrial/nphRCT |
Schoenfeld under-estimates by 20-50%; cite Lin 2020 |
| Non-inferiority continuous | Fixed-margin with M2 = 0.5 × historical M1 (discounted) | FDA 2016 NI guidance; cite Temple-Ellenberg 2000 |
| Non-inferiority binary | Fixed-margin with Miettinen-Nurminen CI for RD | Cite EMA NI guidance; MN-CI standard |
| Bioequivalence (Cmax/AUC) | TOST with 80-125% margins on geometric mean ratio | FDA 1992 BE guidance; Schuirmann 1987 |
| Cluster-randomised | n × design effect = 1 + (m-1)ICC | Cite Murray 1998 cluster RCT methodology |
| Group-sequential | Lan-DeMets spending function | rpact or gsDesign |
| Pilot for sample size re-estimation | Blinded SSR (Friede-Kieser 2006) | No Type-I inflation; safer than unblinded |
| Promising-zone reestimation | Mehta-Pocock 2011 with pre-specified increase rule | Recovers power; cite caveat re Jennison-Turnbull 2015 critique |
from statsmodels.stats.power import tt_ind_solve_power
# Solve for n per group
n = tt_ind_solve_power(
effect_size=0.5, # Cohen's d = (mu1 - mu2) / sigma
alpha=0.05,
power=0.80,
alternative='two-sided'
)
print(f'n per arm = {np.ceil(n):.0f}')
# Solve for power given n
power = tt_ind_solve_power(effect_size=0.5, alpha=0.05, nobs1=100, alternative='two-sided')
Cohen's d benchmarks: small = 0.2, medium = 0.5, large = 0.8. Choose d to detect based on prior literature or clinically meaningful effect, NOT post-hoc to fit the affordable n.
Inflate for dropout: if dropout rate is q, multiply final n by 1/(1-q). For q=0.20, n_total = n/0.80.
Stratified randomisation efficiency: if randomisation stratifies on prognostic factors with combined R² = r against outcome, the effective n is n/(1-r²). Senn 2013 Stat Med 32:1439 makes the precision argument explicit.
from statsmodels.stats.power import NormalIndPower
import math
# Without continuity correction
p1, p2 = 0.30, 0.20
pbar = (p1 + p2) / 2
z_alpha = 1.96 # two-sided alpha=0.05
z_beta = 0.84 # power=0.80
n = ((z_alpha * math.sqrt(2 * pbar * (1 - pbar)) +
z_beta * math.sqrt(p1 * (1 - p1) + p2 * (1 - p2))) / (p1 - p2)) ** 2
print(f'n per arm (uncorrected) = {math.ceil(n)}')
# Continuity-corrected (Fleiss formula)
correction = (1 + math.sqrt(1 + 4 / (n * abs(p1 - p2)))) ** 2 / 4
n_corrected = math.ceil(n * correction)
print(f'n per arm (continuity corrected) = {n_corrected}')
The continuity correction debate (D'Agostino, Chase & Belanger 1988 Am Stat 42:198):
R's power.prop.test uses uncorrected normal approximation — can over-state power 5-10% in small samples (n<100). For confirmatory work with n<100, use simulation-based SS via simr or presize.
import math
# Events needed for two-sample log-rank under PH (Schoenfeld 1981)
from scipy.stats import norm
def schoenfeld_events(hr, alpha=0.05, power=0.80, allocation_ratio=1.0, two_sided=True):
"""
events = (z_crit + z_beta)^2 / (p*(1-p) * log(HR)^2)
where z_crit = z_{1-alpha/2} for two-sided test OR z_{1-alpha} for one-sided.
"""
z_crit = norm.ppf(1 - alpha/2) if two_sided else norm.ppf(1 - alpha)
z_beta = norm.ppf(power)
p = 1 / (1 + allocation_ratio)
return math.ceil((z_crit + z_beta) ** 2 / (p * (1 - p) * math.log(hr) ** 2))
# For HR=0.70, alpha=0.05 two-sided, 80% power, 1:1 -> approx 247 events
events_needed = schoenfeld_events(hr=0.70)
print(f'Events needed for HR=0.70: {events_needed}')
Events drive power, not subjects. Convert to n via expected event rate and follow-up:
# n needed = events / overall event probability over follow-up
expected_overall_event_prob = 0.40 # from pilot or historical
n_per_arm = math.ceil(events_needed / (2 * expected_overall_event_prob))
# Inflate for dropout
n_per_arm_with_dropout = math.ceil(n_per_arm / (1 - 0.15)) # 15% dropout
Use R gsDesign::nSurv() or npsurvSS::size_two_arm() for complex scenarios with:
library(gsDesign)
n_lakatos <- nSurv(
lambdaC = 0.04, # control hazard per month
hr = 0.70, # treatment HR
eta = 0.005, # dropout hazard per month
T = 24, # total study duration in months
minfup = 12, # minimum follow-up
accrualTime = 12, # accrual duration
alpha = 0.025, # one-sided
beta = 0.10 # power = 90%
)
print(n_lakatos)
Schoenfeld 1981 ASSUMES PH. Under immuno-oncology with delayed separation, the formula under-estimates required events by 20-50%. The fix:
# Simulate under expected hazard pattern (Lin 2020 NPH Working Group recommendation)
library(simtrial)
sim_result <- simtrial(
n_per_arm = 250,
enroll_rate = piecewise_enroll(),
fail_rate = piecewise_fail( # delayed-effect specification
duration = c(6, 18),
fail_rate = c(0.04, 0.04), # control
hr = c(1.0, 0.5), # treatment HR is 1 for first 6 months, then 0.5
dropout_rate = c(0.005, 0.005)
),
total_duration = 36
)
# Compute empirical power via MaxCombo or weighted log-rank
FDA NI Trials Guidance (November 2016) establishes the canonical M1/M2 framework:
The "double discount" trap: M2 = 0.5 × (lower CI bound of M1) effectively requires 50% retention of a discounted historical estimate, yielding a much tighter margin than naive point-estimate retention. This has effectively halted new antibiotic NDA development under stringent NI margins.
# Fixed-margin NI sample size (binary endpoint)
import math
p_control = 0.85 # historical/observed control success rate
p_test = 0.85 # null assumption: test = control (NI null is test - control < -M2)
margin_M2 = 0.05 # pre-specified clinically acceptable loss
z_alpha = 1.645 # one-sided alpha=0.025
z_beta = 0.84 # power=0.80
# Approximate: n per arm
variance_term = p_control * (1 - p_control) + p_test * (1 - p_test)
n = math.ceil((z_alpha + z_beta) ** 2 * variance_term / margin_M2 ** 2)
print(f'NI sample size per arm: {n}')
Use Miettinen-Nurminen score CI for RD (the regulatory standard) when computing the NI margin from observed proportions. Cite ratesci::scoreci (R) for production.
Constancy assumption: the historical placebo-vs-active effect must persist in the NI trial. If standard of care drifted, M1 over-estimates and margin is too liberal. Hung-Wang-O'Neill 2005 Biom J critique: NI trials have NO within-trial Type-I error guarantee — alpha is conditional on constancy.
Assay sensitivity (Temple-Ellenberg 2000 Ann Intern Med 133:455 + 133:464): NI trials have only external assay sensitivity (inferred from historical data + constancy); placebo-controlled trials have internal assay sensitivity. This is why NI trials are second-best when placebo is ethical.
TOST (Two One-Sided Tests; Schuirmann 1987): reject H0 of inequivalence iff both one-sided tests reject at α each — equivalent to the 1-2α CI lying within (-δ, +δ). Closed under intersection-union -> no multiplicity adjustment needed despite two tests.
# TOST sample size for continuous outcome
import math
def tost_sample_size(mu_diff, sigma, margin, alpha=0.05, power=0.80):
"""Sample size per arm for TOST equivalence test."""
z_alpha = 1.645 # one-sided
z_beta = 0.84
effect = abs(margin - abs(mu_diff))
if effect <= 0:
raise ValueError('|mu_diff| must be < margin')
n = math.ceil(2 * sigma ** 2 * (z_alpha + z_beta) ** 2 / effect ** 2)
return n
n_eq = tost_sample_size(mu_diff=0.0, sigma=10, margin=5)
print(f'Equivalence sample size per arm: {n_eq}')
FDA 1992 bioequivalence (80-125% rule): geometric mean ratio of Cmax and AUC must have 90% CI within (0.80, 1.25). Implemented in PowerTOST R package for crossover BE designs.
Crossover trials randomise each subject to receive both treatments in different periods. Power calculation is fundamentally different from parallel: the within-subject SD (sigma_w) drives power, not between-subject SD (sigma_b). With reasonable carryover-free designs, crossover requires ~25-50% the n of parallel for the same precision.
# Two-period crossover sample size (continuous endpoint)
import math
def crossover_n_continuous(mean_diff, sd_within, alpha=0.05, power=0.80):
"""n per sequence (so total n = 2*n) for two-period crossover."""
z_alpha = 1.96 # two-sided
z_beta = 0.84 # power=0.80
n_per_seq = math.ceil(2 * (z_alpha + z_beta)**2 * sd_within**2 / mean_diff**2)
return n_per_seq, 2 * n_per_seq # n_per_seq, n_total
Average bioequivalence: geometric mean ratio (GMR) of test/reference Cmax and AUC must have 90% CI within (0.80, 1.25). Log-transform pharmacokinetic parameters; analyse with mixed-effects ANOVA (period, sequence, treatment, subject random).
library(PowerTOST)
# Sample size for 2x2 crossover bioequivalence with CV (within-subject)
n_be <- sampleN.TOST(
alpha = 0.05,
targetpower = 0.80,
theta0 = 0.95, # expected GMR
theta1 = 0.80, # lower BE bound
theta2 = 1.25, # upper BE bound
CV = 0.25, # within-subject CV
design = '2x2x2' # standard 2-period 2-sequence
)
print(n_be)
Highly variable drugs (CV > 30%): standard 80-125% fails with feasible n. Use scaled average bioequivalence (SABE); the expanding-limits (ABEL) approach below is the EMA method (the FDA's reference-scaled RSABE uses a different criterion and PowerTOST::sampleN.RSABE()):
- Reference-scaled limits: theta = exp(0.760 * sigma_WR) when sigma_WR > 0.294
- Widens BE bounds proportional to within-subject variability of reference
- PowerTOST::sampleN.scABEL() for sample size
Grizzle test for carryover: compares baseline-adjusted period 1 vs period 2 effects. Now controversial: the two-stage Grizzle carryover pretest is misleading -- it inflates the Type-I error of the treatment comparison (Freeman 1989 Stat Med 8:1421); significant "carryover" should drive design choice (washout extension), not an analysis switch (Senn 2002, Cross-over Trials in Clinical Research, 2nd ed.).
Modern operational rule: pre-specify adequate washout (>=5 half-lives); do NOT routinely test for carryover in primary analysis. If carryover is biologically plausible, use parallel design or extend washout.
Period effects (calendar/learning) are estimable in 2x2 crossover. Standard analysis includes period as fixed effect:
library(nlme)
fit <- lme(response ~ treatment + period, random = ~1 | subject, data = df)
If period significant, treatment effect is still unbiased (orthogonal in balanced 2x2); report period effect for transparency.
| Scenario | Use crossover? | Why |
|---|---|---|
| Bioequivalence of pharmacokinetic parameters | YES | Standard regulatory; within-subject precision much higher |
| Chronic stable disease (HTN, GERD, asthma) | YES | Reversible response; ~50% sample size savings |
| Acute disease (sepsis, MI) | NO | Cannot retreat same patient |
| Curative intent (oncology, surgery) | NO | Treatment alters disease state irreversibly |
| Long-half-life drug (>1 week) | NO | Washout impractical |
| Patient-reported outcomes with strong period bias | CAUTION | Period bias may dominate |
| Method | Source | Description |
|---|---|---|
| Anchor-based | Jaeschke 1989 | Patient-reported anchor question; MCID = mean change in subjects who report "small important" change |
| 1 SEM (Wyrwich 1999) | J Clin Epidemiol | MCID ≈ standard error of measurement |
| 0.5 SD (Norman 2003) | Med Care 41:582 | "Remarkable universality of half a standard deviation" across PROMs |
| 0.5 SD baseline | Common rule of thumb | Quick approximation for unknown PROMs |
Postdoc rule: δ in power calculation should EXCEED MCID (often 1.5-2× MCID) so that trials are powered to detect effects clearly larger than the noise threshold.
For co-primary endpoints, power-adjust per FDA Multiple Endpoints Guidance (October 2022):
| Pattern | Likely cause | Action |
|---|---|---|
| Schoenfeld n much smaller than Lakatos simulation n | PH violated under expected HR(t) pattern (immuno-oncology delayed effect) | Use Lakatos OR simulation under expected HR(t); cite Lin 2020 NPH Working Group |
| Continuity-corrected vs uncorrected proportion SS differ by ~10% | Asymptotic approximation debate (D'Agostino 1988) | For confirmatory n < 100/arm, use simulation-based SS; document correction approach in SAP |
| NI margin per FDA double discount (50% of M1 lower CI) vs sponsor proposed margin (50% of M1 point estimate) | Sponsor uses point estimate; FDA expects lower-CI discount | FDA 2016 NI guidance: M2 from lower CI bound is the regulatory expectation |
| Bayesian predictive probability of success vs frequentist power give different n | Bayesian integrates prior uncertainty; frequentist conditions on hypothesised δ | Bayesian PPoS more honest about pre-trial uncertainty; frequentist preferred for confirmatory regulatory; report both for adaptive contexts |
| TOST and CI-inclusion approach give different equivalence conclusions | TOST is two-one-sided at α; CI is 1-2α — mathematically equivalent so should NOT disagree | If disagree, check α conventions (Schuirmann 1987: TOST at α, CI at 1-2α) |
| Sponsor's MCID vs published anchor-based MCID differ | Different anchor questions or population | Cite primary MCID source; cross-check with Norman 2003 0.5 SD heuristic; declare in SAP |
| Stratified-randomisation SS calculation vs unstratified differ substantially | Stratification efficiency gain via Senn 2013 formula | Use stratified formula; cite efficiency = 1/(1-r²) where r² is R² of strata against outcome |
| Cluster-RCT SS underpowered after enrollment | ICC misspecified at design (most common SS failure in cluster RCTs) | Use historical ICC + sensitivity analysis at ±50% of estimate; cite Murray 1998 |
| Threshold | Source | Rationale |
|---|---|---|
| δ >= 1.5 × MCID for superiority | Postdoc rule; Norman 2003 implication | δ = MCID gives no margin for sampling variation |
| M2 <= 0.5 × historical M1 (FDA double discount) | FDA NI 2016 guidance | Conservative retention against biocreep |
| M2 <= 0.5 × MCID for NI | Standard regulatory expectation | Acceptable loss < clinically meaningful difference |
| Schoenfeld under non-PH under-estimates by 20-50% | Lin 2020 NPH WG | Switch to Lakatos or simulation |
| Continuity correction wastes ~10% sample size | D'Agostino, Chase & Belanger 1988 Am Stat 42:198 | Modern computing makes exact tests cheap |
| 90% CI within (0.80, 1.25) for BE | FDA 1992 BE guidance | Geometric mean ratio of Cmax/AUC |
| Unblinded SSR Type-I requires CHW weights | Cui-Hung-Wang 1999 | Naive increase inflates Type-I |
| Promising-zone CP range ~30-80% | Mehta-Pocock 2011 Stat Med 30:3267 | Mathematical calibration for Type-I preservation |
| Error / symptom | Cause | Solution |
|---|---|---|
| Trial under-powered for immunotherapy | Schoenfeld formula used under non-PH | Lakatos or simulation; cite Lin 2020 |
| δ = MCID, CI straddles zero | δ-MCID confusion | Pre-specify δ >= 1.5 × MCID |
| NI "success" but active much worse than historical | Constancy violation | Cite Hung 2005; consider synthesis or 3-arm |
| Unblinded SSR with naive sample increase | Type-I inflation | CHW-weighted test; cite Cui-Hung-Wang 1999 |
power.prop.test over-states power n < 100 |
Uncorrected normal approximation | Simulation-based SS or Fleiss continuity correction |
| BE failure after large n with point estimate near 1.0 | Variability higher than assumed | Re-estimate from pilot; consider replicate design for highly variable drugs |
| Promising-zone tipping to favourable not pre-specified | Operational confusion | Document increase rule in SAP; pre-specify cap |
| Cluster RCT n based on individual-level | Design effect ignored | n × (1 + (m-1)ICC); cite Murray 1998 |
| TOST sample size with non-zero true difference | Treating null as abs(mu_diff)=0 | Include realistic mu_diff in calculation |
| Pushback | Response |
|---|---|
| "Is δ realistic?" | Justified from prior phase 2; δ exceeds MCID by factor X; pre-specified |
| "Why this NI margin?" | M2 = 50% of historical lower-CI M1 per FDA 2016 double discount; M2 < MCID |
| "Constancy assumption?" | Reviewed historical placebo-vs-active effect over time; stable; sensitivity to lower-end constancy provided |
| "Schoenfeld vs Lakatos?" | PH plausible from phase 2 KM; pre-specified Schoenfeld; Lakatos simulation under expected delayed-effect as sensitivity |
| "Continuity correction?" | n > 200/arm; uncorrected normal approximation valid (Fleiss 1981) |
| "Bioequivalence variability assumption?" | Conservative (upper bound of historical CV); pilot will trigger re-estimation if CV >X% |
| "Cluster ICC source?" | Historical ICC from prior cluster trial in similar setting; sensitivity at ICC ±50% provided |
| "MCID source?" | Anchor-based MCID from validation study (Jaeschke 1989); supported by 0.5 SD heuristic (Norman 2003) |
| "Promising zone or just blinded SSR?" | Promising zone with pre-specified CP boundaries; CHW weights for Type-I control |