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.
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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.
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.
Power and Sample Size for Clinical Trials
"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).
The Foundational Distinction -- δ vs MCID
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:
Underpowered trials where sponsor sets δ = MCID and gets a CI straddling zero
Overgenerous NI margins where sponsor sets M2 = full MCID (NI margin should be a fraction of MCID)
Postdoc rule of thumb: for superiority, δ >= 1.5 × MCID; for NI, M2 <= 0.5 × MCID.
Norman GR, Sloan JA, Wyrwich KW 2003 Med Care 41:582 (0.5 SD heuristic)
Snapinn SM 2000 Curr Control Trials Cardiovasc Med 1:19 (NI biocreep)
Temple R, Ellenberg SS 2000 Ann Intern Med 133:455 + 133:464 (NI assay sensitivity; Ann Intern Med NOT NEJM — common citation error)
Hung HMJ, Wang SJ, O'Neill RT 2005 Biom J (NI within-trial Type-I not guaranteed)
Mehta CR, Pocock SJ 2011 Stat Med 30:3267 (promising zone)
Lin RS, Lin J, Roychoudhury S et al 2020 Stat Biopharm Res (NPH Working Group)
Decision Tree by Scenario
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
Continuous Outcomes -- Two-Sample t-Test
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.
Binary Outcomes -- The Continuity Correction Debate
The continuity correction debate (D'Agostino, Chase & Belanger 1988 Am Stat 42:198):
Pro (Fleiss, Yates): better matches the exact distribution under H0
Con: overly conservative, wastes ~10% sample size; modern computing makes exact (Fisher-Irwin, Boschloo) tests feasible
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.
Survival (Time-to-Event)
Schoenfeld 1981 -- the canonical formula
import math
# Events needed for two-sample log-rank under PH (Schoenfeld 1981)from scipy.stats import norm
defschoenfeld_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
Lakatos 1988 -- complex survival
Use R gsDesign::nSurv() or npsurvSS::size_two_arm() for complex scenarios with:
Time-varying hazard ratios (delayed effect)
Non-uniform accrual
Different dropout rates per arm
Cure fractions
library(gsDesign)
n_lakatos <- nSurv(
lambdaC =0.04,# control hazard per month
hr =0.70,# treatment HR
eta =0.005,# dropout hazard per monthT=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)
Under non-PH (immuno-oncology with delayed effect)
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
Non-Inferiority Designs -- The FDA 2016 Framework
FDA NI Trials Guidance (November 2016) establishes the canonical M1/M2 framework:
M1 = entire effect of active control vs placebo (lower bound of CI from historical meta-analysis)
M2 = clinically acceptable loss, typically M1/2 (50% effect retention) but as conservative as M1/4 for mortality endpoints
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 2005Biom 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.
Equivalence Designs and Bioequivalence
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 outcomeimport math
deftost_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 Designs -- Bioequivalence and Repeated-Measures
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
defcrossover_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
Bioequivalence (FDA 1992 / EMA 2010 framework)
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()):
Widens BE bounds proportional to within-subject variability of reference
PowerTOST::sampleN.scABEL() for sample size
Carryover assessment (Grizzle 1965)
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 effect
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.
Decision tree -- when crossover is appropriate
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
MCID -- Anchor-Based vs Distribution-Based
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.
Multiple Endpoints -- See multiplicity-graphical
For co-primary endpoints, power-adjust per FDA Multiple Endpoints Guidance (October 2022):
Co-primary (all-must-win): each endpoint at full alpha but joint power = product -> inflate n
Multiple primary (any-wins): alpha split (e.g., Bonferroni or graphical)
Hierarchical: test in order; if any fail, downstream cannot be claimed
Reconciliation: When Methods Disagree
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
Per-Method Failure Modes
Schoenfeld under non-PH
Trigger: Immunotherapy or other delayed-effect mechanism
Trigger: NI trial with new standard of care differing from historical
Mechanism: M1 derived from historical data no longer reflects current control efficacy
Symptom: Active control performs worse than expected; "successful" NI may mask true inferiority
Fix: Synthesis approach with formal sensitivity to constancy; consider three-arm trial with small placebo
MCID confused with δ
Trigger: Sponsor sets δ = MCID in power calculation
Mechanism: Trial powered to detect smallest meaningful effect, with no margin for noise/dropout
Symptom: Effect estimate near MCID with wide CI straddling zero
Fix: δ >= 1.5 × MCID; document rationale in SAP
Promising-zone "stealth alpha inflation"
Trigger: Mehta-Pocock SSR applied without sufficient simulation
Mechanism: a naive unblinded increase analysed with the conventional (unweighted) statistic inflates Type-I error (Cui-Hung-Wang 1999); the pre-specified weighted CHW statistic preserves alpha
Symptom: Type-I inflation when the CHW weighting is dropped; separately, Jennison-Turnbull 2015 show the promising zone is inefficient -- the largest power gains per added patient lie outside it
Mechanism: Sponsor inference from sample-size increase decision reveals direction of interim effect
Symptom: Regulator audit reveals unblinding
Fix: Strict firewall; only "increase / no increase" communicated to sponsor; document SOP
Quantitative Thresholds
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
Common Errors
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
Anticipated Reviewer Pushback
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
References
Cui L, Hung HMJ, Wang SJ. 1999. Modification of sample size in group sequential clinical trials. Biometrics 55:853-857.
D'Agostino RB, Chase W, Belanger A. 1988. The appropriateness of some common procedures for testing the equality of two independent binomial populations. Am Stat 42:198-202.
FDA. 2016. Non-Inferiority Clinical Trials to Establish Effectiveness. Final Guidance.
FDA. 2022. Multiple Endpoints in Clinical Trials. Final Guidance.
Fleiss JL. 1981. Statistical Methods for Rates and Proportions (2nd ed). Wiley.
Friede T, Kieser M. 2006. Sample size recalculation in internal pilot study designs. Biom J 48:537-555.
Hung HMJ, Wang SJ, O'Neill RT. 2005. A regulatory perspective on choice of margin and statistical inference issue in non-inferiority trials. Biom J 47:28-36.
Jaeschke R, Singer J, Guyatt GH. 1989. Measurement of health status: ascertaining the minimal clinically important difference. Control Clin Trials 10:407-415.
Lakatos E. 1988. Sample sizes based on the log-rank statistic in complex clinical trials. Biometrics 44:229-241.
Lin RS, Lin J, Roychoudhury S, Anderson KM, Hu T, Huang B, Leon LF, Liao JJZ, Liu R, Luo X, Mukhopadhyay P, Qin R, Tatsuoka K, Wang X, Wang Y, Zhu J, Chen TT, Iacona R. 2020. Alternative analysis methods for time to event endpoints under nonproportional hazards: a comparative analysis. Stat Biopharm Res.
Mehta CR, Pocock SJ. 2011. Adaptive increase in sample size when interim results are promising. Stat Med 30:3267-3284.
Norman GR, Sloan JA, Wyrwich KW. 2003. Interpretation of changes in health-related quality of life: the remarkable universality of half a standard deviation. Med Care 41:582-592.
Schoenfeld DA. 1981. The asymptotic properties of nonparametric tests for comparing survival distributions. Biometrika 68:316-319.
Schuirmann DJ. 1987. A comparison of the two one-sided tests procedure and the power approach for assessing the equivalence of average bioavailability. J Pharmacokinet Biopharm 15:657-680.
Senn S. 2013. Seven myths of randomisation in clinical trials. Stat Med 32:1439-1450.
Snapinn SM. 2000. Noninferiority trials. Curr Control Trials Cardiovasc Med 1:19-21.
Temple R, Ellenberg SS. 2000. Placebo-controlled trials and active-control trials in the evaluation of new treatments, part 1: ethical and scientific issues. Ann Intern Med 133:455-463.
Ellenberg SS, Temple R. 2000. Placebo-controlled trials and active-control trials in the evaluation of new treatments, part 2: practical issues and specific cases. Ann Intern Med 133:464-470.
Wyrwich KW, Tierney WM, Wolinsky FD. 1999. Further evidence supporting an SEM-based criterion for the identification of meaningful intra-individual changes in health-related quality of life. J Clin Epidemiol 52:861-873.
