---
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 7.
tool_type: mixed
primary_tool: statsmodels
goal_approach_exempt: true
---

## Version Compatibility

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.

# 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.

## Algorithmic Taxonomy

| 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:**

- Fleiss JL 1981 *Statistical Methods for Rates and Proportions* (with/without continuity correction tables)
- Schoenfeld DA 1981 *Biometrika* 68:316 (canonical TTE formula)
- Lakatos E 1988 *Biometrics* 44:229 (Markov chain SS for complex survival)
- Schuirmann DJ 1987 *J Pharmacokinet Biopharm* 15:657 (TOST)
- Jaeschke R, Singer J, Guyatt GH 1989 *Control Clin Trials* 10:407 (MCID anchor-based)
- 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

```python
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

```python
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, Casagrande, Pike 1988 *Stat Med* 7:347):

- 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

```python
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:

```python
# 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

```r
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)
```

### 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:

```r
# 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.

```python
# 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.

## 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.

```python
# 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 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.

```python
# 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
```

### 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).

```r
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)** per FDA 2010:
- 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

### Carryover assessment (Grizzle 1965)

**Grizzle test** for carryover: compares baseline-adjusted period 1 vs period 2 effects. **Now controversial:** Senn 2002 *Statistics in Medicine* showed Grizzle test has poor power; significant carryover should drive design choice (washout extension), not analysis switch.

**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:

```r
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
- **Mechanism:** Schoenfeld assumes constant log-HR
- **Symptom:** Trial under-powered; observed events insufficient
- **Fix:** Lakatos 1988 or simulation under expected HR(t); cite Lin 2020 NPH Working Group

### Continuity correction debate

- **Trigger:** Small-sample binary design
- **Mechanism:** Uncorrected normal approx over-states power; corrected wastes ~10%
- **Symptom:** Trial reach significance at lower n than expected
- **Fix:** Use simulation-based SS for n<100; pre-specify correction approach in SAP

### NI margin too liberal

- **Trigger:** M2 set to MCID rather than 50% of historical M1
- **Mechanism:** Allows clinically unacceptable inferiority within "non-inferior" CI
- **Symptom:** Regulators flag margin as inappropriate at scientific advice
- **Fix:** M2 <= 0.5 × MCID; M2 <= 0.5 × historical M1 lower bound (FDA double discount)

### Constancy assumption violated

- **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:** Jennison-Turnbull 2015 critique: increase rule + statistical test combination may inflate alpha beyond ~0.001
- **Symptom:** Independent reanalysis finds Type-I 5.3% vs nominal 5%
- **Fix:** Pre-specify increase rule transparently; report simulation operating characteristics

### Unblinded SSR -- DMC firewall failure

- **Trigger:** Interim effect estimate leaked beyond IDMC
- **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 1988 *Stat Med* 7:347 | 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.
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## Related Skills

- clinical-biostatistics/survival-analysis - TTE-specific sample size (Schoenfeld, Lakatos, simulation)
- clinical-biostatistics/effect-measures - δ on OR/RR/RD scales
- clinical-biostatistics/categorical-tests - Binary endpoint test selection
- clinical-biostatistics/multiplicity-graphical - Power adjustment for co-primary endpoints
- clinical-biostatistics/adaptive-designs - SSR, promising zone, group-sequential
- clinical-biostatistics/bayesian-trials - Bayesian SS via predictive probability of success
- clinical-biostatistics/trial-reporting - CONSORT 2025 item 7 (sample size justification)
- experimental-design/sample-size - General sample-size methods
- experimental-design/power-analysis - General power methods