# Sample Size Formulas Reference

Mathematical formulas, R/Python implementations, and effect size conventions for all 10 supported tests.

---

## Test 1: Diagnostic Accuracy (Sensitivity/Specificity Precision)

### Formula
For estimating a single proportion p with desired 95% CI half-width w:

```
n_positive = ceil( (z_{alpha/2} / w)^2 * p * (1 - p) )
n_total = ceil( n_positive / prevalence )
```

Where:
- `z_{alpha/2}` = 1.96 for alpha = 0.05
- `p` = expected sensitivity (or specificity)
- `w` = desired CI half-width
- `prevalence` = disease prevalence in the study population

### R Implementation
```r
z <- qnorm(1 - alpha / 2)
n_pos <- ceiling((z / ci_half_width)^2 * se_expected * (1 - se_expected))
n_total <- ceiling(n_pos / prevalence)
n_adj <- ceiling(n_total / (1 - attrition_rate))
```

### Python Implementation
```python
from scipy.stats import norm
import math

z = norm.ppf(1 - alpha / 2)
n_pos = math.ceil((z / ci_half_width)**2 * se_expected * (1 - se_expected))
n_total = math.ceil(n_pos / prevalence)
n_adj = math.ceil(n_total / (1 - attrition_rate))
```

### R Package
Base R (no additional packages needed).

### Key Reference
Buderer NMF. Statistical methodology: I. Incorporating the prevalence of disease into the sample size calculation for sensitivity and specificity. Acad Emerg Med. 1996;3(9):895-900.

---

## Test 2: ICC Agreement (Bonett 2002)

### Formula
Fisher z-transformation approach:

```
z_1 = 0.5 * ln((1 + rho_1) / (1 - rho_1))    # expected ICC
z_0 = 0.5 * ln((1 + rho_0) / (1 - rho_0))    # null ICC
n = ceil( ((z_{alpha} + z_{beta}) / (z_1 - z_0))^2 + 3 )
```

Where:
- `rho_1` = expected ICC
- `rho_0` = null hypothesis ICC
- `z_{alpha}` = qnorm(1 - alpha) for one-sided, qnorm(1 - alpha/2) for two-sided
- `z_{beta}` = qnorm(power)

### R Implementation
```r
# Option A: MKpower package (preferred)
library(MKpower)
result <- sampleSize.ICC(rho0 = icc_null, rho1 = icc_expected,
                          k = n_raters, alpha = alpha, power = power)
n <- result$n

# Option B: Manual Fisher z (if MKpower unavailable)
z_exp  <- 0.5 * log((1 + icc_expected) / (1 - icc_expected))
z_null <- 0.5 * log((1 + icc_null) / (1 - icc_null))
n <- ceiling(((qnorm(1 - alpha) + qnorm(power)) / (z_exp - z_null))^2 + 3)
```

### Python Implementation
```python
from scipy.stats import norm
import math
import numpy as np

z_exp  = 0.5 * np.log((1 + icc_expected) / (1 - icc_expected))
z_null = 0.5 * np.log((1 + icc_null) / (1 - icc_null))
z_alpha = norm.ppf(1 - alpha)
z_beta  = norm.ppf(power)
n = math.ceil(((z_alpha + z_beta) / (z_exp - z_null))**2 + 3)
```

### R Package
`MKpower` (preferred), or base R for manual calculation.

### Key Reference
Bonett DG. Sample size requirements for estimating intraclass correlations with desired precision. Stat Med. 2002;21(9):1331-1335.

---

## Test 3: Kappa Agreement (Donner & Eliasziw 1992)

### Formula
Z-test approximation for testing kappa_1 vs kappa_0:

```
n = ceil( ((z_{alpha/2} + z_{beta})^2 * kappa_1 * (1 - kappa_1)) / (kappa_1 - kappa_0)^2 + 1 )
```

Where:
- `kappa_1` = expected kappa
- `kappa_0` = null hypothesis kappa
- `pe` = expected chance agreement = (po - kappa) / (1 - kappa)

### R Implementation
```r
n_kappa <- ceiling(
  ((qnorm(1 - alpha / 2) + qnorm(power))^2 *
     kappa_expected * (1 - kappa_expected)) /
    (kappa_expected - kappa_null)^2 + 1
)
```

### Python Implementation
```python
from scipy.stats import norm
import math

z_a = norm.ppf(1 - alpha / 2)
z_b = norm.ppf(power)
n = math.ceil(((z_a + z_b)**2 * kappa_exp * (1 - kappa_exp)) /
              (kappa_exp - kappa_null)**2 + 1)
```

### R Package
Base R. Also available via `kappaSize` package.

### Key Reference
Donner A, Eliasziw M. A goodness-of-fit approach to inference procedures for the kappa statistic: confidence interval construction, significance-testing and sample size estimation. Stat Med. 1992;11(11):1511-1519.

---

## Test 4: Two-Proportion Comparison (Chi-Square)

### Formula
Based on Cohen's h effect size (arcsine transformation):

```
h = 2 * arcsin(sqrt(p1)) - 2 * arcsin(sqrt(p2))
n_per_group = ceil( ((z_{alpha/2} + z_{beta}) / h)^2 )
```

### R Implementation
```r
library(pwr)
h <- ES.h(p1, p2)
result <- pwr.2p.test(h = h, sig.level = alpha, power = power)
n_per_group <- ceiling(result$n)
n_total <- n_per_group * 2
```

### Python Implementation
```python
from statsmodels.stats.power import NormalIndPower
import numpy as np
import math

h = 2 * np.arcsin(np.sqrt(p1)) - 2 * np.arcsin(np.sqrt(p2))
analysis = NormalIndPower()
n_per_group = math.ceil(analysis.solve_power(effect_size=h, alpha=alpha, power=power,
                                              ratio=1, alternative='two-sided'))
n_total = n_per_group * 2
```

### R Package
`pwr`

### Key Reference
Cohen J. Statistical Power Analysis for the Behavioral Sciences. 2nd ed. Lawrence Erlbaum Associates; 1988.

---

## Test 5: McNemar Test (Paired Proportions)

### Formula
```
n = ceil(
  (z_{alpha/2} * sqrt(p01 + p10) + z_{beta} * sqrt(p01 + p10 - (p10 - p01)^2))^2
  / (p10 - p01)^2
)
```

Where:
- `p01` = P(Method A negative, Method B positive)
- `p10` = P(Method A positive, Method B negative)

### R Implementation
```r
n_mc <- ceiling(
  (qnorm(1 - alpha / 2) * sqrt(p01 + p10) +
     qnorm(power) * sqrt(p01 + p10 - (p10 - p01)^2))^2 /
    (p10 - p01)^2
)
```

### Python Implementation
```python
from scipy.stats import norm
import math

z_a = norm.ppf(1 - alpha / 2)
z_b = norm.ppf(power)
disc_sum = p01 + p10
disc_diff = p10 - p01
n = math.ceil((z_a * math.sqrt(disc_sum) +
               z_b * math.sqrt(disc_sum - disc_diff**2))**2 / disc_diff**2)
```

### R Package
Base R. Also available via `exact2x2` package.

### Key Reference
Connor RJ. Sample size for testing differences in proportions for the paired-sample design. Biometrics. 1987;43(1):207-211.

---

## Test 6: Independent t-Test

### Formula
```
d = mean_diff / pooled_sd    (Cohen's d)
n_per_group = ceil( 2 * ((z_{alpha/2} + z_{beta}) / d)^2 )
```

### R Implementation
```r
library(pwr)
d <- mean_diff / pooled_sd
result <- pwr.t.test(d = d, sig.level = alpha, power = power, type = "two.sample")
n_per_group <- ceiling(result$n)
n_total <- n_per_group * 2
```

### Python Implementation
```python
from statsmodels.stats.power import TTestIndPower
import math

d = mean_diff / pooled_sd
analysis = TTestIndPower()
n_per_group = math.ceil(analysis.solve_power(effect_size=d, alpha=alpha, power=power,
                                              ratio=1, alternative='two-sided'))
n_total = n_per_group * 2
```

### R Package
`pwr`

### Key Reference
Cohen J. Statistical Power Analysis for the Behavioral Sciences. 2nd ed. Lawrence Erlbaum Associates; 1988.

---

## Test 7: Survival / Log-Rank Test (Schoenfeld 1981)

### Formula
Step 1 -- Required number of events:
```
d = ceil( ((z_{alpha/2} + z_{beta}) / ln(HR))^2 )
```

Step 2 -- Total sample size:
```
lambda_ctrl = ln(2) / median_ctrl
lambda_trt  = lambda_ctrl * HR
p_event_ctrl = 1 - exp(-lambda_ctrl * follow_up)
p_event_trt  = 1 - exp(-lambda_trt * follow_up)
avg_p_event  = (p_event_ctrl + p_event_trt) / 2
n_total = ceil( d / avg_p_event )
```

### R Implementation
```r
n_events <- ceiling((qnorm(1 - alpha / 2) + qnorm(power))^2 / (log(hr))^2)
lambda_ctrl <- log(2) / median_ctrl
lambda_trt  <- lambda_ctrl * hr
p_event_ctrl <- 1 - exp(-lambda_ctrl * follow_up)
p_event_trt  <- 1 - exp(-lambda_trt * follow_up)
avg_p_event  <- (p_event_ctrl + p_event_trt) / 2
n_total <- ceiling(n_events / avg_p_event)
n_adj <- ceiling(n_total / (1 - drop_rate))
```

### Python Implementation
```python
from scipy.stats import norm
import math
import numpy as np

z_a = norm.ppf(1 - alpha / 2)
z_b = norm.ppf(power)
n_events = math.ceil((z_a + z_b)**2 / np.log(hr)**2)
lambda_ctrl = np.log(2) / median_ctrl
lambda_trt = lambda_ctrl * hr
p_event_ctrl = 1 - np.exp(-lambda_ctrl * follow_up)
p_event_trt = 1 - np.exp(-lambda_trt * follow_up)
avg_p_event = (p_event_ctrl + p_event_trt) / 2
n_total = math.ceil(n_events / avg_p_event)
n_adj = math.ceil(n_total / (1 - drop_rate))
```

### R Package
Base R. Also available via `gsDesign`, `survival` packages.

### Key Reference
Schoenfeld DA. The asymptotic properties of nonparametric tests for comparing survival distributions. Biometrika. 1981;68(1):316-319.

---

## Test 8: One-Way ANOVA

### Formula
Using Cohen's f effect size:

```
f = sigma_between / sigma_within
```

Where:
- `sigma_between` = SD of group means
- `sigma_within` = pooled within-group SD

From eta-squared: `f = sqrt(eta_sq / (1 - eta_sq))`

The sample size per group is obtained via the F-test power formula (implemented in `pwr`).

### R Implementation
```r
library(pwr)
result <- pwr.anova.test(k = k, f = f, sig.level = alpha, power = power)
n_per_group <- ceiling(result$n)
n_total <- n_per_group * k
n_adj <- ceiling(n_total / (1 - attrition_rate))
```

### Python Implementation
```python
from statsmodels.stats.power import FTestAnovaPower
import math

analysis = FTestAnovaPower()
n_per_group = math.ceil(analysis.solve_power(effect_size=f, nobs=None, alpha=alpha,
                                              power=power, k_groups=k))
n_total = n_per_group * k
n_adj = math.ceil(n_total / (1 - attrition_rate))
```

### R Package
`pwr`

### Key Reference
Cohen J. Statistical Power Analysis for the Behavioral Sciences. 2nd ed. Lawrence Erlbaum Associates; 1988. (Chapter 8: F tests for ANOVA)

---

## Test 9: Logistic Regression

### Approach A: Peduzzi Rule of Thumb (EPV >= 10)

```
N_events = 10 * p   (where p = number of predictor variables)
N_total = N_events / event_rate
```

This ensures at least 10 events per predictor variable (EPV), the widely accepted minimum for stable logistic regression estimates.

### Approach B: Hsieh (1989) Formula

For detecting a specific odds ratio (OR) for a continuous or binary predictor:

```
# For a binary predictor (proportion B exposed):
n_unadj = ((z_{alpha/2} + z_{beta})^2) / (B * (1-B) * ln(OR)^2)

# Adjusted for correlation with other predictors:
n_adj = n_unadj / (1 - R^2)
```

Where:
- `OR` = odds ratio of interest
- `B` = proportion of subjects exposed (for binary predictor) or use p*(1-p) for the outcome
- `R^2` = multiple correlation of the predictor with other covariates

For a continuous predictor, the formula uses the standard normal density.

### R Implementation
```r
# Approach A: Peduzzi
n_events_peduzzi <- 10 * n_predictors
n_total_peduzzi <- ceiling(n_events_peduzzi / event_rate)

# Approach B: Hsieh (binary predictor)
z_a <- qnorm(1 - alpha / 2)
z_b <- qnorm(power)
n_hsieh <- ceiling((z_a + z_b)^2 /
                     (event_rate * (1 - event_rate) * log(or_interest)^2))
n_hsieh_adj <- ceiling(n_hsieh / (1 - r2_other))

# Report the larger of the two
n_final <- max(n_total_peduzzi, n_hsieh_adj)
```

### Python Implementation
```python
from scipy.stats import norm
import math
import numpy as np

# Approach A: Peduzzi
n_events_peduzzi = 10 * n_predictors
n_total_peduzzi = math.ceil(n_events_peduzzi / event_rate)

# Approach B: Hsieh (binary predictor)
z_a = norm.ppf(1 - alpha / 2)
z_b = norm.ppf(power)
n_hsieh = math.ceil((z_a + z_b)**2 /
                     (event_rate * (1 - event_rate) * np.log(or_interest)**2))
n_hsieh_adj = math.ceil(n_hsieh / (1 - r2_other))

n_final = max(n_total_peduzzi, n_hsieh_adj)
```

### R Package
Base R. Also see `powerMediation` package for Hsieh's formula.

### Key References
- Peduzzi P, Concato J, Kemper E, Holford TR, Feinstein AR. A simulation study of the number of events per variable in logistic regression analysis. J Clin Epidemiol. 1996;49(12):1373-1379.
- Hsieh FY. Sample size tables for logistic regression. Stat Med. 1989;8(7):795-802.

---

## Test 10: Non-Inferiority / Equivalence

### Non-Inferiority (Proportions)

```
n_per_group = ceil(
  ((z_{1-alpha} + z_{beta})^2 * (p_ref*(1-p_ref) + p_new*(1-p_new))) /
  (margin - |p_new - p_ref|)^2
)
```

When assuming p_new = p_ref (no true difference):
```
n_per_group = ceil( ((z_{1-alpha} + z_{beta})^2 * 2 * p*(1-p)) / margin^2 )
```

Note: alpha is one-sided (typically 0.025) for non-inferiority.

### Non-Inferiority (Continuous)

```
n_per_group = ceil( ((z_{1-alpha} + z_{beta})^2 * 2 * sd^2) / margin^2 )
```

### Equivalence / TOST (Proportions)

```
n_per_group = ceil(
  ((z_{1-alpha/2} + z_{beta})^2 * 2 * p*(1-p)) / margin^2
)
```

Note: For TOST, each one-sided test uses alpha (e.g., alpha = 0.05 for overall 5% type I error).

### Equivalence / TOST (Continuous)

```
n_per_group = ceil( ((z_{1-alpha} + z_{beta})^2 * 2 * sd^2) / margin^2 )
```

### R Implementation
```r
# Non-inferiority for proportions (assuming no true difference)
z_a <- qnorm(1 - alpha)  # one-sided, alpha = 0.025
z_b <- qnorm(power)
p <- p_reference
n_per_group <- ceiling(((z_a + z_b)^2 * 2 * p * (1 - p)) / margin^2)
n_total <- n_per_group * 2

# Non-inferiority for continuous
n_per_group <- ceiling(((z_a + z_b)^2 * 2 * sd^2) / margin^2)
n_total <- n_per_group * 2

# Equivalence / TOST for continuous
n_per_group <- ceiling(((z_a + z_b)^2 * 2 * sd^2) / margin^2)
n_total <- n_per_group * 2

n_adj <- ceiling(n_total / (1 - attrition_rate))
```

### Python Implementation
```python
from scipy.stats import norm
import math

# Non-inferiority for proportions (assuming no true difference)
z_a = norm.ppf(1 - alpha)  # one-sided, alpha = 0.025
z_b = norm.ppf(power)
p = p_reference
n_per_group = math.ceil(((z_a + z_b)**2 * 2 * p * (1 - p)) / margin**2)
n_total = n_per_group * 2

# Non-inferiority for continuous
n_per_group = math.ceil(((z_a + z_b)**2 * 2 * sd**2) / margin**2)
n_total = n_per_group * 2

# Equivalence / TOST for continuous
# Same formula; the difference is in the hypothesis and alpha interpretation
n_per_group = math.ceil(((z_a + z_b)**2 * 2 * sd**2) / margin**2)
n_total = n_per_group * 2

n_adj = math.ceil(n_total / (1 - attrition_rate))
```

### R Package
Base R. Also see `TrialSize`, `PowerTOST` packages.

### Key References
- Julious SA. Sample sizes for clinical trials with normal data. Stat Med. 2004;23(12):1921-1986.
- Schuirmann DJ. A comparison of the two one-sided tests procedure and the power approach for assessing the equivalence of average bioavailability. J Pharmacokinet Biopharm. 1987;15(6):657-680.

---

## Test 11: Cox Regression EPV (Events Per Variable)

### Formula
```
N_events = EPV × k    (where k = number of predictor variables)
N_total = ceil( N_events / event_rate )
N_adj = ceil( N_total / (1 - attrition_rate) )
```

Where:
- `EPV` = events per variable (minimum 10, recommended 20)
- `k` = number of predictors in the Cox model
- `event_rate` = proportion of subjects experiencing the event

### R Implementation
```r
n_events <- epv * n_predictors
n_total <- ceiling(n_events / event_rate)
n_adj <- ceiling(n_total / (1 - attrition_rate))

cat(sprintf("EPV = %d, Predictors = %d\n", epv, n_predictors))
cat(sprintf("Required events = %d\n", n_events))
cat(sprintf("Total N = %d (event rate = %.0f%%)\n", n_total, event_rate * 100))
cat(sprintf("Adjusted N = %d (attrition = %.0f%%)\n", n_adj, attrition_rate * 100))
```

### Python Implementation
```python
import math

n_events = epv * n_predictors
n_total = math.ceil(n_events / event_rate)
n_adj = math.ceil(n_total / (1 - attrition_rate))
```

### R Package
Base R (no additional packages needed).

### Key References
- Peduzzi P, Concato J, Feinstein AR, Holford TR. Importance of events per independent variable in proportional hazards regression analysis. II. Accuracy and precision of regression estimates. J Clin Epidemiol. 1995;48(12):1503-1510.
- Vittinghoff E, McCulloch CE. Relaxing the rule of ten events per variable in logistic and Cox regression. Am J Epidemiol. 2007;165(6):710-718.

---

## Cohen's Effect Size Conventions

| Measure | Small | Medium | Large | Context |
|---------|-------|--------|-------|---------|
| d (t-test) | 0.20 | 0.50 | 0.80 | Difference in means / pooled SD |
| f (ANOVA) | 0.10 | 0.25 | 0.40 | SD of group means / within-group SD |
| h (proportions) | 0.20 | 0.50 | 0.80 | Arcsine-transformed proportion difference |
| w (chi-square) | 0.10 | 0.30 | 0.50 | Chi-square contingency effect |
| OR (logistic) | 1.5 | 2.0 | 3.0+ | Odds ratio (approximate equivalence) |
| HR (survival) | 0.80 | 0.65 | 0.50 | Hazard ratio (values < 1 favor treatment) |
| ICC | 0.50-0.75 | 0.75-0.90 | > 0.90 | Poor/moderate/good/excellent |
| Kappa | 0.21-0.40 | 0.41-0.60 | 0.61-0.80 | Fair/moderate/substantial |

**Important**: Cohen's conventions are rules of thumb. Always prefer effect sizes estimated from prior literature or pilot data. When conventions are used, explicitly state this limitation in the IRB justification.

---

## Common Attrition Rates by Study Type

| Study Type | Typical Attrition | Recommended Adjustment |
|------------|-------------------|------------------------|
| Randomized controlled trial (RCT) | 15-20% | 20% |
| Prospective observational / cohort | 10-15% | 15% |
| Cross-sectional / survey | 5-10% | 10% |
| Retrospective chart review | 3-5% | 5% |
| Diagnostic accuracy (imaging) | 5-10% | 10% |
| Inter-rater agreement study | 5-10% | 10% |
| Survival / long follow-up (> 2 yr) | 15-25% | 20% |

**Note**: Attrition rates vary widely by disease, population, and follow-up duration. Use study-specific estimates when available.

---

## Key References

1. **Cohen J.** Statistical Power Analysis for the Behavioral Sciences. 2nd ed. Hillsdale, NJ: Lawrence Erlbaum Associates; 1988.
   - Foundation for effect size conventions (d, f, h, w) and power analysis methodology.

2. **Schoenfeld DA.** The asymptotic properties of nonparametric tests for comparing survival distributions. Biometrika. 1981;68(1):316-319.
   - Formula for required number of events in log-rank test.

3. **Bonett DG.** Sample size requirements for estimating intraclass correlations with desired precision. Stat Med. 2002;21(9):1331-1335.
   - ICC-based sample size using Fisher z-transformation.

4. **Hsieh FY.** Sample size tables for logistic regression. Stat Med. 1989;8(7):795-802.
   - Power-based sample size for detecting a specific odds ratio.

5. **Peduzzi P, Concato J, Kemper E, Holford TR, Feinstein AR.** A simulation study of the number of events per variable in logistic regression analysis. J Clin Epidemiol. 1996;49(12):1373-1379.
   - EPV >= 10 rule for logistic regression model stability.

6. **Donner A, Eliasziw M.** A goodness-of-fit approach to inference procedures for the kappa statistic: confidence interval construction, significance-testing and sample size estimation. Stat Med. 1992;11(11):1511-1519.
   - Sample size for testing kappa against a null value.

7. **Buderer NMF.** Statistical methodology: I. Incorporating the prevalence of disease into the sample size calculation for sensitivity and specificity. Acad Emerg Med. 1996;3(9):895-900.
   - Prevalence-adjusted sample size for diagnostic accuracy.

8. **Julious SA.** Sample sizes for clinical trials with normal data. Stat Med. 2004;23(12):1921-1986.
   - Comprehensive non-inferiority and equivalence sample size formulas.

9. **Schuirmann DJ.** A comparison of the two one-sided tests procedure and the power approach for assessing the equivalence of average bioavailability. J Pharmacokinet Biopharm. 1987;15(6):657-680.
   - TOST (two one-sided tests) procedure for equivalence testing.

10. **Koo TK, Li MY.** A guideline of selecting and reporting intraclass correlation coefficients for reliability research. J Chiropr Med. 2016;15(2):155-163.
    - ICC interpretation benchmarks.

11. **Landis JR, Koch GG.** The measurement of observer agreement for categorical data. Biometrics. 1977;33(1):159-174.
    - Kappa interpretation benchmarks.

12. **Connor RJ.** Sample size for testing differences in proportions for the paired-sample design. Biometrics. 1987;43(1):207-211.
    - McNemar test sample size formula.

13. **Peduzzi P, Concato J, Feinstein AR, Holford TR.** Importance of events per independent variable in proportional hazards regression analysis. II. Accuracy and precision of regression estimates. J Clin Epidemiol. 1995;48(12):1503-1510.
    - EPV >= 10 rule for Cox regression model stability.

14. **Vittinghoff E, McCulloch CE.** Relaxing the rule of ten events per variable in logistic and Cox regression. Am J Epidemiol. 2007;165(6):710-718.
    - Evidence that EPV 5-10 may be acceptable with careful validation.

# Sample-size justification — worked prose exemplars (IRB / Methods)

Reviewer-safe **justification paragraphs** for the prospective designs this skill computes,
complementing `formulas.md` (the math) and the retrospective/experience-based templates in
SKILL.md Phase 2b. Each shows the same five elements a methods reviewer or IRB looks for; fill
the `[brackets]` from the actual calculation — never invent the inputs. These are synthetic
teaching models of *standard* justification structure, not copied text.

## The five elements (every justification states all five)
1. The **primary outcome** and its effect/precision target (with the **source** of the assumed
   value — prior study, pilot, or a minimal clinically important difference, cited).
2. **α** (and one- vs two-sided) and **power** (or the target CI half-width for a precision aim).
3. The **test/method** the calculation matches (it must match the planned primary analysis).
4. The resulting **n**, including any **inflation** for attrition/clustering/multiplicity.
5. The **software/approach** used (named, so it is reproducible).

## Exemplars by design

**Two proportions (superiority).** "Assuming an event rate of `[p1]` in the control arm
(from `[cited source]`) and a clinically meaningful absolute reduction to `[p2]`, a two-sided
α = 0.05 and 80% power require `[n/arm]` per arm (two-proportion test). Allowing for `[d]%`
attrition, we will enrol `[N]`."

**Two means (superiority).** "To detect a between-group difference of `[Δ]` in `[outcome]`
(SD `[s]`, from `[source]`; standardised effect `[d]`) with two-sided α = 0.05 and 90% power
requires `[n/arm]` per arm (two-sample t-test)."

**Diagnostic accuracy (precision aim).** "To estimate sensitivity with a 95% CI half-width of
`[w]`, assuming sensitivity `[Se]` and disease prevalence `[π]`, `[N_total]` participants
(`[N_diseased]` with the target condition) are needed; the **specificity** target is checked
separately from the non-diseased count `[N_nondiseased]` and is satisfied at this n. The aim is
**precision, not power** — no comparison hypothesis is tested." (Cite Hajian-Tilaki / Buderer.)

**Survival (log-rank).** "To detect a hazard ratio of `[HR]` (median `[m1]` vs `[m2]`) with
two-sided α = 0.05 and 80% power, `[E]` events are required (Schoenfeld); with an accrual of
`[a]` over `[t]` and follow-up `[f]`, this needs `[N]` participants. The **event count**, not N,
drives power."

**Agreement / reliability (ICC).** "Assuming a true ICC of `[ρ]` with `[k]` raters per subject,
`[n]` subjects give a 95% CI half-width of `[w]` (a **precision** aim, Bonett/Walter) —
*or*, framed as **assurance**, `[n]` subjects so the 95% CI lower bound exceeds the minimally
acceptable `[ρ0]`. State which of the two aims you used; report the CI target, not power."

**Non-inferiority.** "With a non-inferiority margin of `[m]` (justified clinically and by
`[regulatory/prior]` precedent), assuming true equivalence and a control rate `[p]`, one-sided
α = 0.025 and 90% power require `[n/arm]` per arm. The margin and its rationale are pre-specified."

## Discipline
- The calculation must match the **planned primary analysis** (do not power for a t-test and
  analyse with a mixed model); state any clustering (design effect) or multiplicity adjustment.
- For a **precision** aim (DTA, agreement, single-arm), report the **CI half-width**, not power —
  do not invent a comparison hypothesis to manufacture a power statement.
- Never reverse-engineer the effect size from an achievable n (post-hoc justification); the
  assumed effect comes from a cited source or an MCID. Post-hoc/observed power is uninformative.

# MRMC reader-study sample size (multi-reader multi-case)

For a **reader study** — the design that asks "do radiologists read better *with* the AI than
without", or "is the AI non-inferior to radiologists" — the single-reader AUC-precision
calculation (Test 1) **under-sizes the study**, often badly. This reference is the design-time
sizing for that class of study. It is the sizing counterpart to the flagship "clearing move" in
`design-study/references/venue_accept_recipe.md` (a reader study measuring clinical impact is
what lifts a study to the flagship tier) — and an under-sized reader study cannot deliver it.

## Why a single-reader power calculation is the wrong tool

A reader study generalizes to **radiologists in general**, not to the specific readers you hired.
So **both the readers and the cases are random effects**, and the uncertainty of the
reader-averaged AUC (or of the AI−reader ΔAUC) carries a **reader-variance** term the single-reader
calculation omits entirely. Size on case variance alone and the study is powered to detect an
effect *in your particular readers*, not in the population of readers — which is exactly the claim
a reviewer reads the paper as making. The practical consequence: studies sized as if readers were
fixed are routinely **under-powered**, and a null result from an under-sized reader study is
**inconclusive, not negative**.

## The framework — Obuchowski–Rockette / Hillis (OR)

The multi-reader multi-case (MRMC) analysis of variance treats the figure of merit (usually AUC,
or a difference in AUC between modalities/AI-conditions) as an outcome with **reader**, **case**,
and **reader×case** (plus modality) random components. Sizing inverts the OR variance formula:

- You choose the **number of readers `J`** and the **case counts** (diseased `N⁺`, non-diseased
  `N⁻`), and the OR formula returns the power to detect the target effect.
- Power depends on the **variance components** — the error variance and the between-reader /
  within-reader covariances (`Cov1`, `Cov2`, `Cov3` in the OR parameterization, or Hillis'
  equivalent `σ²` terms). **You cannot size an MRMC study without these**, and they are the real
  bottleneck: take them from a **pilot** (a handful of readers on a subset) or from **published
  component estimates** for a similar task/modality, and state the source.

## The inputs to pre-specify (before any data)

1. **The effect**: the ΔAUC to detect (superiority) *or* the non-inferiority margin (an AI-vs-reader
   claim is usually **non-inferiority**, so state the margin, not a difference).
2. **The expected AUC level** of the reference arm (variance of an AUC estimate depends on where it
   sits).
3. **The variance components** (pilot or literature — the hard part; §above).
4. **The design**: **fully-crossed** (every reader reads every case in every condition) is the
   default and the most efficient; a **crossover with washout** (readers read with and without AI,
   separated by a washout so the first read does not cue the second) is the standard AI-assistance
   design.
5. **Power and α** (commonly 80–90% at two-sided 0.05).

## Readers vs cases — where the power comes from

Because the **reader-variance term usually dominates** the generalization uncertainty, past a
modest case count **adding readers often buys more power than adding cases** — yet readers are the
scarcer, costlier resource. Report the **`J × N` power grid**, not a single number, so the
reader/case trade-off is an explicit, defensible design choice. A study with many cases but only
3–4 readers is a common, predictable under-powering.

## Compute it — integrate, do not reimplement

- **`RJafroc`** (R; Chakraborty) — `SsPowerGivenJK` / sample-size functions for ROC & FROC MRMC.
- **`MRMCaov`** (R) — OR analysis + power.
- **`iMRMC`** (Gallas, FDA) — MRMC sizing/analysis, widely accepted by regulators.
- **OR-DBM / DBM** procedures for the variance-component estimation from a pilot.

Feed the pilot/literature variance components + the target effect into one of these; do not hand-roll
the OR variance algebra.

## Grounding exemplars (accepted reader studies)

Realistic `J × N` and design choices from accepted open-access papers:
- **8-reader MRMC crossover, 500 cases** — PCN CT model, *npj Digital Medicine* 2025
  (`10.1038/s41746-025-01970-y`): readers spanning residents→seniors, accuracy **and** reading-time
  endpoints.
- **26 physicians × 150 cases × 3 conditions with ≥2-week washout** — pelvic-radiograph AI-support,
  *npj Digital Medicine* 2025 (`10.1038/s41746-025-01923-5`): a crossover across no-AI / alert /
  heatmap, specialty-stratified.

These illustrate the crossover-with-washout design and the reader-count range a flagship reader
study lands in; they are patterns, not templates.

## Reporting (what the Methods must state)

The number of readers `J`, the case split `N⁺`/`N⁻`, the **design** (fully-crossed / crossover +
washout), the **target effect** (ΔAUC or NI margin) and power/α, the **source of the variance
components** (pilot vs literature), and the **software**. Analysis of the completed study uses the
matching OR/DBM procedure (see `analyze-stats` `reader_study` table-type + `diagnostic_accuracy`
guide); the reader-study *design internals* (rubric, blinding, washout, experience mix) are in
`design-study/references/reader_elicitation_design.md`, and an AI-vs-human-expert benchmark routes
to `/design-ai-benchmarking`.

## References (methodology — cite, do not copy)

- Obuchowski NA, Rockette HE. *Commun Stat Simul Comput* 1995 (the OR method).
- Hillis SL, Berbaum KS, Metz CE. *Acad Radiol* 2008 (OR/DBM equivalence, sizing).
- Hillis SL. *Stat Med* 2007 (degrees of freedom for MRMC).
- Chakraborty DP. *Observer Performance Methods for Diagnostic Imaging* (RJafroc).

# Between-model comparison sample size (is model A really better than B, C, …)

For a study whose claim is that **one model outperforms others** — several architectures / families
compared head-to-head on the same task — the sizing question is not single-model precision (Test 15
for Dice, Test 1 for AUC) but **how many cases separate the models**. A study powered only to
estimate each model's metric can still be too small to tell whether the ranking is real. This is the
**size** counterpart to the fair-comparison **design** in
`design-study/references/multi_model_comparison_design.md`; decide it before data collection.

## Why single-model precision under-sizes a comparison

Sizing each arm to a tight marginal CI does **not** guarantee the *difference* is distinguishable
from zero — two models can each have a narrow CI and still overlap. The comparison is powered by the
**difference**, and its precision depends on the **SD of the per-case difference**, which the
marginal SDs do not give you.

## Pair the design — it shrinks the required n

Run **all models on the same cases** (a paired / within-case design) and size on the **SD of the
per-case difference**. With equal marginal SDs σ and between-model correlation ρ,
`SD_Δ = σ·√(2(1−ρ))` — **smaller than either marginal SD only once ρ > 0.5**, a bar that models
scored on the *same* cases usually clear by a wide margin (easy cases are easy for every model, hard
cases are hard for every model). Whatever ρ turns out to be, the paired design also **collects fewer
cases** than two independent arms at equal power, because one case serves every model — and it is the
only design that supports the paired statistics below.

## Metric-specific paired sizing

- **Classification / detection — paired ΔAUC:** use the **DeLong** (1988) variance of the *difference*
  of two correlated AUCs (or Obuchowski for the MRMC / clustered case); size so the **ΔAUC CI excludes
  zero** (superiority) or so its **lower bound clears −δ**, the non-inferiority margin — requiring the
  *whole* interval inside ±δ is the stricter **equivalence** claim, so do not size one and call it the
  other. Sizing on each AUC's marginal CI
  is the wrong tool — the covariance between the two ROC curves is exactly what a paired calc uses.
- **Segmentation — paired ΔDice / ΔHD95 / ΔNSD:** size on the SD of the **per-case metric difference**
  and report the delta CI by **bootstrapping the paired per-case differences (BCa)** — a t-interval on
  the mean per-case difference is closed-form, but it leans on a normality that a bounded metric
  bunched near ceiling does not deliver, and BCa resamples whole *patients* rather than lesions or
  structures. This extends the A-vs-B section of `segmentation_metric_sample_size.md` beyond
  a single contrast; **size on the worst structure** you must report.
- Take the **per-case-difference SD from a pilot** (or a prior head-to-head), never from a marginal-SD
  formula that assumes independence.

## More than two models — multiplicity across contrasts

Comparing **k models** creates up to k(k−1)/2 pairwise contrasts. Decide the estimand **before** the
data:

- **Primary-contrast design (preferred):** pre-specify **one** primary comparison — the proposed model
  vs the **strong, fairly-tuned reference baseline** (e.g., nnU-Net) — sized at full α; everything else
  is secondary / exploratory and labelled so. This avoids sizing for a multiplicity you do not need.
- **All-pairs confirmatory:** if every pairwise claim is confirmatory, a **family-wise correction**
  (Bonferroni / Tukey-analog) lowers the per-contrast α, which **inflates the required n per contrast** —
  budget for it. Running k(k−1)/2 unplanned tests and headlining the one that clears p < 0.05 is the
  rejected pattern (`analyze-stats` `analysis_guides/multiplicity.md`).

## Ranking stability — the trap a difference calc still misses

A **single-run** leaderboard ranks models by *true skill + run-to-run noise* (random seed, data order,
augmentation draw). Near-tied models can swap rank between seeds, so "our model ranked first" from one
run is not evidence. Two additions:

- **Report run-to-run variance:** train each model over **multiple seeds** and report the metric's
  seed SD; for the paired difference of repeated cross-validation runs use the **Nadeau–Bengio
  corrected-resampled variance** (a naïve paired t over overlapping CV folds is anticonservative).
- **Comparing many models across independent datasets:** the **Demšar (2006)** framework — Friedman
  test + Nemenyi **critical-difference** — tells you which rank gaps are real. Its sampling unit is the
  **independent dataset**, so its N is the *number of datasets*: extra seeds and overlapping CV folds do
  not raise it (those buy you the run-to-run spread above), and per-structure scores from one cohort are
  correlated blocks, not substitutes for datasets. Models inside the critical difference are **not
  separated by the test** — leave them unranked, and do not upgrade that to a demonstrated tie
  (failure to reject is not evidence of equality; an equivalence claim needs its own margin).

## Required parameters

The **per-case-difference SD** of the primary metric (pilot / prior head-to-head; per structure for
segmentation), the **metric** and its paired-CI method (DeLong for AUC, bootstrap for Dice), the target
**δ or NI margin on the delta**, the **number of models + which single contrast is primary**, and (for
a ranking claim) the **seed-to-seed SD**. Report N, the difference-SD source, the primary contrast, and
the multiplicity handling.

## Cross-links

The fair-comparison design the size serves → `design-study/references/multi_model_comparison_design.md`;
the single-metric precision + one A-vs-B Dice contrast → `segmentation_metric_sample_size.md`;
reader-in-the-loop (AI-vs-reader) sizing → `mrmc_reader_study_sample_size.md` (Test 14); presenting the
result → `make-figures` `exemplar_plots/model_comparison_leaderboard.md` + `analyze-stats`
`table-standards/table-types/model_comparison.md`; the multiplicity discipline →
`analyze-stats` `analysis_guides/multiplicity.md`.

# Observational Cohort Sample Size: Precision Branch

Use this reference when a cohort study is extraction-constrained or when the goal is precision rather than formal power.

## When To Use

- Retrospective hospital-based cohort with all eligible records included.
- National database cohort where the sample is fixed by release permissions.
- Sparse-event outcome where the real question is whether confidence intervals are narrow enough to support a claim.

## Core Checks

1. Primary estimand: risk difference, odds ratio, hazard ratio, incidence rate, or mean difference.
2. Event count: total events and events per modeled parameter.
3. Precision target: acceptable confidence interval half-width or maximum acceptable upper bound.
4. Model complexity: covariate count relative to events.
5. Fragility: subgroup and sensitivity analyses with smaller denominators.

## Rule-of-Thumb Gates

| Situation | Minimum check |
|---|---|
| Logistic or Cox model | Events per parameter and shrinkage/penalization consideration |
| Sparse binary outcome | Exact or profile-likelihood confidence intervals |
| Incidence rate | Poisson exact CI around event rate |
| Null association claim | Upper CI bound must exclude clinically meaningful effect |
| Subgroup analysis | Interaction test plus event count per subgroup |

## Manuscript Phrase

"The study size was determined by all eligible participants in the released cohort. We therefore evaluated statistical informativeness by the number of outcome events, events per modeled parameter, and the width of the 95% confidence intervals around the primary estimate rather than by a conventional a priori recruitment target."

## Minimal R Sketch

```r
events <- 130
parameters <- 8
epv <- events / parameters

rate <- 130 / 250000
poisson.test(130, T = 250000)$conf.int
```

## Reviewer-Safe Interpretation

- If events are sparse, do not write "no association" without discussing the upper confidence bound.
- If EPV is below 10, state that estimates are exploratory or use penalized/sparse models.
- If a subgroup has few events, report it descriptively even when the p-value looks attractive.

# Prediction-model sample size (Riley) — development & external validation

For a **clinical prediction model** (or a medical-AI model evaluated as one), the
events-per-variable rule of thumb (EPV ≥ 10) is **outdated and reviewer-vulnerable**. EPV
does not target the things that determine whether a developed model is trustworthy
(overfitting, precise risk estimates) or whether a validation is conclusive (precise
discrimination and calibration). Use the **Riley criteria** instead — they are the current
TRIPOD+AI-aligned standard, and they are implemented in the R packages `pmsampsize`
(development) and `pmvalsampsize` (external validation).

Apply this whenever the goal is **risk prediction / classification for use**, not a single
predictor's hypothesis test. (For a single-predictor association test, the Hsieh/logistic
power calculation in Test 9 is appropriate.)

## Development sample size — `pmsampsize` (Riley et al.)

The minimum development sample size is the largest N satisfying four criteria
simultaneously:

1. **Small overfitting** — global shrinkage factor ≥ 0.9.
2. **Small optimism in apparent fit** — absolute difference between apparent and adjusted
   Nagelkerke R² ≤ 0.05.
3. **Precise estimate of overall risk** — margin of error of the mean predicted outcome
   (the intercept) ≤ 0.05.
4. **(time-to-event)** precise estimate of the baseline survival at a key time point.

Inputs you must specify (and justify from prior literature, not guess):
- number of **candidate predictor parameters** (count dummy variables and non-linear terms,
  not just variables);
- the anticipated model performance — a conservative **Cox-Snell R²** (derivable from an
  expected **C-statistic** + outcome prevalence) or expected R²;
- the **outcome prevalence** (binary) or **event rate + mean follow-up** (time-to-event),
  or outcome mean/SD (continuous).

```r
library(pmsampsize)
# Binary outcome: prevalence 0.20, 30 candidate parameters, expected C ≈ 0.78
# (convert C to a conservative Cox-Snell R²; pmsampsize accepts csrsquared or cstatistic)
pmsampsize(type = "b", cstatistic = 0.78, parameters = 30, prevalence = 0.20)

# Time-to-event: rate per person-year, mean follow-up, timepoint of interest
pmsampsize(type = "s", csrsquared = 0.05, parameters = 30,
           rate = 0.08, timepoint = 5, meanfup = 4.2)
```

Report the **minimum N and the required number of events**, the assumed C-statistic / R²
and its source, and the binding criterion. A development set below this is a standard
high-impact-journal rejection.

## External-validation sample size — `pmvalsampsize` (Riley et al.)

Size the validation set to estimate the key performance metrics **precisely enough to be
conclusive** — target the confidence-interval width of each:

- **discrimination** — C-statistic (target CI width, e.g. ±0.05);
- **calibration slope** (target SE / CI width);
- **calibration-in-the-large / O:E ratio**;
- **(if reporting clinical utility)** the standardized **net benefit** at the decision
  threshold.

```r
library(pmvalsampsize)
# Validate a model with expected prevalence 0.20, anticipated C ≈ 0.78,
# targeting a C-statistic CI half-width of 0.05 and a precise calibration slope
pmvalsampsize(type = "b", prevalence = 0.20, cstatistic = 0.78,
              cslope = 1, oe = 1, lpnormal = c(-0.5, 0.5),
              cstatci = 0.10)   # target CI *width* for the C-statistic
```

A common **floor** is ≥ 100 events and ≥ 100 non-events (Vergouwe; Collins), but
`pmvalsampsize` gives the precise target for your metrics and usually requires more.

## Sample size for net benefit / decision-curve

If the model's value claim rests on **net benefit** (decision-curve analysis), size the
study to estimate net benefit at the relevant threshold with adequate precision —
`pmvalsampsize` supports a net-benefit target, and the development criteria should be met
so the model is not overfit before its utility is judged. Do not claim clinical utility
from a decision curve estimated on an underpowered validation set.

## Reporting

- State that sizing followed the **Riley criteria** (cite the originals) — not EPV-10.
- Report the assumed C-statistic / R² / prevalence and **where they came from**.
- For development, report N + events + the binding criterion; for validation, report the
  targeted CI widths and the resulting N (events and non-events).

## References (cite the originals)

- Riley RD, Snell KIE, Ensor J, et al. Minimum sample size for developing a multivariable
  prediction model: PART II — binary and time-to-event outcomes. *Stat Med* 2019.
- Riley RD, Ensor J, Snell KIE, et al. Calculating the sample size required for developing
  a clinical prediction model. *BMJ* 2020.
- Riley RD, Debray TPA, Collins GS, et al. Minimum sample size for external validation of a
  clinical prediction model with a binary outcome. *Stat Med* 2021.
- Collins GS, Ogundimu EO, Altman DG. Sample size considerations for the external
  validation of a multivariable prognostic model. *Stat Med* 2016.

# Sizing a segmentation *usability* claim (acceptability rate, failure bound, edit time)

For a study whose claim is that a segmentation model is **clinically usable** — a share of cases a
clinician accepts, a bounded catastrophic-failure rate, a time saving — the endpoint is **not the
mean of a per-case metric**. Test 15 sizes a mean Dice to a target precision; that calculation says
nothing about how many cases you need to state an acceptability *rate*, and a study sized for
metric precision is routinely far too small to bound a failure rate. This is the **size**
counterpart to the fair-usability **design** in
`design-study/references/segmentation_failure_characterization_design.md`; decide it before data
collection.

## The endpoint is a proportion, not a mean

An acceptability endpoint (*use-as-is*, *acceptable after minor edits*, *clinically acceptable*) is a
**binomial proportion**. Size it to a target CI half-width δ:

```
n ≈ (z/δ)² · p(1−p)          z = 1.96 for 95%
```

At p = 0.90 and δ = 0.05 that is ≈ **138 cases**; at p = 0.50 (the worst case, and the value to use
when the pilot is thin) it is ≈ **384**. Two consequences follow immediately. A proportion near the
ceiling is cheap and one near 50% is expensive — and **you do not know which you have until you
measure**, so size on the pessimistic p unless a pilot in the same anatomy justifies otherwise. And
the rate is **per structure class**: acceptability is not one number (accepted use-as-is rates for a
single pipeline have ranged from ~40% for target volumes to ~89% for normal tissue), so size on the
**structure whose acceptability you must claim**, not on the pooled average.

If the claim is against a threshold ("≥80% of cases acceptable"), size the **one-sided** comparison
of the observed proportion to that threshold, and state the threshold and its justification before
the data — a threshold chosen after seeing the rate is not a threshold.

## Ratings are nested in cases — a rate judged by k readers is not a simple binomial

When m readers rate each of n cases, the total **is not** n·m independent observations. Ratings of
the same case are correlated (an easy case is easy for every reader) and ratings by the same reader
are correlated (a lenient reader is lenient throughout). Pooling them as independent overstates
precision by the **design effect**:

```
DE ≈ 1 + (m − 1)·ρ           n_effective ≈ n·m / DE
```

With 3 readers per case and ρ = 0.5, DE = 2 — half the apparent sample. Either analyse at the
**case level** (a pre-specified consensus or majority rule across readers, then a plain binomial on n
cases) or model the clustering (mixed-effects / GEE with case and reader as random effects) and size
with the inflation. Pick one at design time; the choice changes n by a factor of two or more.

## Bounding a catastrophic-failure rate — the rule of three

A usability claim usually carries an implicit safety claim: *catastrophic failures are rare*.
Rarity has to be sized for, and it is expensive. If **zero** events are observed in n cases, the
one-sided 95% upper bound on the rate is approximately

```
upper bound ≈ 3 / n
```

So bounding a catastrophic-failure rate at **≤ 1% requires ~300 clean cases**; at ≤ 0.5%, ~600. This
is the number that most often breaks a usability claim retrospectively: a study sized to estimate
mean Dice on 40–60 cases can observe zero catastrophic failures and still only bound the rate at
~5–8%, which is not a safety statement. If the design cannot reach n, say what the observed data can
actually bound rather than reporting "no failures occurred" as though it settled the question.

## Edit time / correction effort — paired, per structure

If the claim is that the model saves work, the endpoint is a **paired per-case time difference**
(edit the auto-contour vs contour from scratch, same cases): size on the **SD of the per-case
difference**, exactly as in Test 16, not on the SDs of the two marginal times. Two design points the
published record insists on:

- **Size per structure, not on the pooled saving.** A multi-centre evaluation reporting an overall
  46% saving simultaneously found **no significant saving** for five lymph-node levels, and some
  centres were **slower editing than contouring manually**. A study powered only on the pooled
  contrast cannot support or refute any per-structure claim.
- **Site is a second grouping factor.** If the claim is multi-centre, the per-centre effects differ
  in sign, so size for the centres you intend to claim over (or restrict the claim).

## Required parameters

The **acceptability definition and scale** and which level counts as "accepted" (*use-as-is* and
*acceptable-after-minor-edits* are different endpoints with different n); the **expected rate p** per
structure class (pilot, else 0.5) and the target **δ or threshold**; the **number of readers per
case** and the analysis unit (consensus vs mixed-effects) with the assumed ρ; the **catastrophic-rate
bound** you must be able to state; and, for a work-saving claim, the **SD of the per-case time
difference** per structure. Report n, the assumed p and ρ, the analysis unit, and what
failure rate the design can bound.

## Cross-links

The usability design this size serves → `design-study`
`references/segmentation_failure_characterization_design.md`; the single-metric precision (mean Dice
per structure) → `segmentation_metric_sample_size.md` (Test 15); the paired between-model delta →
`multi_model_comparison_sample_size.md` (Test 16); reader-in-the-loop diagnostic sizing →
`mrmc_reader_study_sample_size.md` (Test 14); presenting the result →
`make-figures` `exemplar_plots/segmentation_failure_panel.md`; abstention and risk–coverage instead
of a fixed acceptability rate → `/uncertainty-imaging`.

# Segmentation-metric sample size (Dice / HD95 / NSD precision)

For a **segmentation** validation, the sizing question is not "how many events" but **how many
cases to estimate the segmentation metric precisely enough to be conclusive** — and, for a
comparison, precisely enough to separate the models. The diagnostic-accuracy calc (Test 1) and the
Riley prediction-model calc (Tests 12–13) do not apply: the outcome is a per-case **overlap /
boundary** score (Dice, HD95, NSD), bounded and often skewed, not a proportion or a risk. This is
the **design-time** case count for a segmentation study — including the external cohort a genuine
generalization claim needs (see `design-study/references/combine_models_ablation_design.md` and
`venue_accept_recipe.md`).

## Why a proportion/events calculation is the wrong tool

Per-case **Dice is bounded [0,1] and heteroscedastic**: near-ceiling and low-variance for large,
easy organs, but low and high-variance for **small or hard structures**. Precision therefore depends
on the **SD of per-case Dice**, which you must take from a **pilot or literature** — not from a
formula that assumes a proportion. **HD95 / NSD** are even more skewed (a few outlier cases dominate),
so their precision is worse at the same n.

## Precision sizing (estimate a mean metric within ±δ)

To estimate the mean metric with a two-sided 95% CI half-width **δ**:

    n ≈ ( 1.96 · SD / δ )²

where **SD** is the pilot/literature SD of the **per-case** metric. Because Dice is bounded and
non-normal, **report the CI by bootstrapping the per-case values (BCa)**, not a naïve normal CI —
the formula sizes the study, the bootstrap reports it. For near-ceiling Dice consider a variance-
stabilizing view or report the full distribution, since a symmetric ±δ misleads at the ceiling.

## Comparison sizing (model A vs B, or internal vs external, or an ablation contrast)

A model comparison on the **same cases** is **paired**: size on the **SD of the per-case
*difference*** (usually much smaller than the marginal SD, because easy cases are easy for both) or,
for an "as good as" claim, a **non-inferiority margin** on Dice. This is the calculation behind the
ablation contrasts in `combine_models_ablation_design.md` (un-adapted base, best single component,
direct-train-vs-transfer) — each needs enough cases to make its ΔDice CI exclude zero (or the
margin).

## Size on the worst structure, and size the external cohort

- **Per-structure, not the average.** Small/hard structures dominate the variance; size on the
  **worst structure you must report**, or the study is under-powered exactly where it matters (the
  batch's honest failures: orbital-lymphoma T1c, medulloblastoma cystic subregions).
- **The external cohort needs its own n.** The #1 acceptance lever is a *precise* external estimate
  with an honest drop; a 30-case external set gives a wide Dice CI. Size it to the precision the
  generalization claim requires (the G72 batch's external cohorts — AMOS, a 33-patient 3-centre set,
  a 72-CT set — motivate the range).

## Required parameters + compute

- Pilot/literature **SD of the per-case metric** (per structure), the target **precision δ** or the
  **NI margin**, the metric itself. A t-interval on mean per-case Dice is closed-form, but the metric
  is **bounded and skewed near the ceiling**, so its nominal coverage is not the real one → **bootstrap
  per-case values** (BCa, resampling whole patients rather than structures); use the pilot for SD.
  Report N, the per-structure SD source, and δ / margin.

## Cross-links

Metric **selection** (Dice + a boundary/agreement metric, per-structure) → `/model-evaluation`;
validation design + the split-leakage gate → `/model-validation`; the comparator/ablation the size
serves → `design-study/references/combine_models_ablation_design.md`; presenting the across-cohort
result → `make-figures` `exemplar_plots/external_validation_comparison.md`.