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Examples in this article were generated with 4.2.1 by the package `PowerTOST`

.^{1} See also the README on GitHub for an overview.

- The right-hand badges give the ‘level’ of the respective section.

- Basics about sample size methodology – requiring no or only limited statistical expertise.

- These sections are the most important ones. They are – hopefully – easily comprehensible even for novices.

- A somewhat higher knowledge of statistics and/or R is required. May be skipped or reserved for a later reading.

- An advanced knowledge of statistics and/or R is required. Not recommended for beginners in particular.

- If you are not a
**ne**R**d**or statistics afficionado, skipping is recommended. Suggested for experts but might be confusing for others.

- Click to show / hide R code.

Abbreviation | Meaning |
---|---|

\(\small{\alpha}\) | Nominal level of the test, probability of Type I Error (patient’s risk) |

\(\small{\beta}\) | Probability of Type II Error (producer’s risk) |

BE | Bioequivalence |

\(\small{CV_\textrm{w}}\) | Within-subject Coefficient of Variation |

\(\small{\Delta}\) | Clinically relevant difference |

\(\small{H_0}\) | Null hypothesis |

\(\small{H_1}\) | Alternative hypothesis (also \(\small{H_\textrm{a}}\)) |

\(\small{\mu_\textrm{T}/\mu_\textrm{R}}\) | True T/R-ratio |

\(\small{\pi}\) | Prospective power, where \(\small{\pi=1-\beta}\) |

\(\small{\theta_1,\;\theta_2}\) | Fixed lower and upper limits of the acceptance range (BE margins) |

What is a significant treatment effect and do we have to care about one?

Sometimes regulatory assessors ask for the ‘justification’ of a significant treatment in an equivalence trial.

I will try to clarify why such a justification is futile and – a bit provocative – asking for one demonstrates a lack of understanding the underlying statistical concepts.

A *basic* knowledge of R is required. To run the scripts at least version 1.4.3 (2016-11-01) of `PowerTOST`

is suggested. Any version of R would likely do, though the current release of `PowerTOST`

was only tested with version 4.1.3 (2022-03-10) and later.

All scripts were run on a Xeon E3-1245v3 @ 3.40GHz (1/4 cores) 16GB RAM with R 4.2.1 on Windows 7 build 7601, Service Pack 1, Universal C Runtime 10.0.10240.16390.

The examples deal with the 2×2×2 crossover design (\(\small{\textrm{TR}|\textrm{RT}}\))^{2} but the concept is applicable to any kind of crossover (Higher-Order, replicate designs) or parallel designs assessed for equivalence.

In order to get prospective power (and hence, a sample size), we need five values:

- The level of the test \(\small{\alpha}\) (in BE commonly 0.05),
- the BE-margins (commonly 0.80 – 1.25),
- the desired (or target) power \(\small{\pi}\),
- the variance (commonly expressed as a coefficient of variation), and
- the deviation of the test from the reference treatment.

1 – 2 are fixed by the agency,

3 is set by the sponsor (commonly to 0.80 – 0.90), and

4 – 5 are just (uncertain!) assumptions.

In other words, obtaining a sample size is *not* an *exact* calculation but always just an estimation.

Realization: Observations (in a sample) of a random variable (of the population).

It is extremely unlikely that all assumptions will be exactly realized in a particular study. If the realized values differ from the assumptions (*i.e.*, T less deviating from R, and/or lower *CV*, and/or fewer dropouts than anticipated), power and hence, the chance to observe a statistically significant treatment effect increases.

Let us first recap the statistical hypotheses in bioequivalence.

- The confidence interval inclusion approach:

\[H_0:\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\ni\left\{\theta_1,\theta_2\right\}\:vs\:H_1:\theta_1<\frac{\mu_\textrm{T}}{\mu_\textrm{R}}<\theta_2\tag{1}\]

- The ‘Two One-Sided Tests’ (TOST) Procedure:
^{3}

\[\begin{matrix}\tag{2} H_\textrm{0L}:\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\leq\theta_1\:vs\:H_\textrm{1L}:\frac{\mu_\textrm{T}}{\mu_\textrm{R}}>\theta_1\\ H_\textrm{0U}:\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\geq\theta_2\:vs\:H_\textrm{1U}:\frac{\mu_\textrm{T}}{\mu_\textrm{R}}<\theta_2 \end{matrix}\]

The lower and upper limits of the bioequivalence range \(\small{\{\theta_1,\theta_2\}}\) are calculated based on the *‘clinically not relevant difference’* \(\small{\Delta}\) \[\left\{\theta_1=100\,(1-\Delta),\,\theta_2=100\,(1-\Delta)^{-1}\right\}\tag{3}\] Commonly \(\small{\Delta}\) is set to 0.20. For narrow therapeutic index drugs (the EMA and other jurisdictions) \(\small{\Delta}\) is set to 0.10, and for \(\small{C_\textrm{max}}\) (Russian Federation, the EEU, South Africa) \(\small{\Delta}\) is set to 0.25. We obtain: \[\begin{matrix}\tag{4}
\left\{\theta_1=80.00\%,\,\theta_2=125.00\%\right\}\\
\left\{\theta_1=90.00\%,\,\theta_2=111.1\dot{1}\%\right\}\\
\left\{\theta_1=75.00\%,\,\theta_2=133.3\dot{3}\%\right\}
\end{matrix}\]

\(\small{(2)}\) is operationally identical to \(\small{(1)}\). From the TOST procedure we obtain two \(\small{p}\)-values (where \(\small{H_0}\) is not rejected if \(\small{\max}\{p_\textrm{L},p_\textrm{U}\}>\alpha\)). It is of historical interest because only \(\small{(1)}\) is mentioned in regulatory guidelines.

As long as the \(\small{100\,(1-2\,\alpha)}\) confidence interval lies entirely within pre-specified limits \(\small{\{\theta_1,\theta_2\}}\), the null hypothesis of inequivalence in \(\small{(1)}\) is rejected and the alternative hypothesis of equivalence in \(\small{(1)}\) is accepted.

Neither the point estimate \(\small{\theta_0}\) nor the width of the CI, as well as *post hoc* power play any role in this decision.

Since \(\small{(1)}\) and \(\small{(2)}\) are operationally equivalent, it follows that if one of the \(\small{p}\) values of \(\small{(2)}\) < \(\small{\alpha}\), the \(\small{100\,(1-2\,\alpha)}\) CI does not include 100%.

In such a case treatments differ *statistically significant*, although this difference is not *clinically relevant*.

Asking for the ‘justification’ of a statistical significant treatment difference contradicts the accepted standard by \(\small{(1)}\) – as laid down in guidances since the early 1990s.^{4} ^{5} ^{6} As an aside, this standard has not changed ever since.

With a sufficiently large sample size any treatment with a \(\small{\theta_0\neq100\%}\) will show a statistically significant difference.^{7}

Most agencies (like the EMA) require an ANOVA of \(\small{\log_{e}}\) transformed responses, *i.e.*, a linear model where all effects are fixed.

In `R`

```
model <- lm(logPK ~ sequence + subject %in% sequence +
period + treatment, data = data)
coef(model)[["treatmentT"]]
confint(model, "treatmentT", level = 0.9)
```

`SAS`

PROC GLM data = data; class subject period sequence treatment; model logPK = sequence subject(sequence) period treatment; estimate 'T-R' treatment -1 1 / CL alpha = 0.1; run;

In Phoenix WinNonlin

The FDA and Health Canada require a mixed-effects model where *sequence*, *period*, and *treatment* are fixed effects and *subject(sequence)* is a random effect.

In `R`

```
library(nlme)
model <- lme(logPK ~ sequence + period + treatment,
random = ~ 1 | subject, data = data)
intervals(model, which = "fixed",
level= 1 - 2 * 0.05)[[1]]["treatmentT", c(1, 3)]
```

`SAS`

PROC MIXED data = data; class subject period sequence treatment; model logPK = sequence subject(sequence) period treatment; estimate 'T-R' treatment -1 1 / CL alpha = 0.1; run;

In Phoenix WinNonlin

Throughout the examples I’m dealing with studies in a 2×2×2 Crossover Design. Of course, the same logic is applicable for any other as well.

```
library(PowerTOST) # attach it to run the examples
balance <- function(n, seq = 2) {
return(as.integer(seq * (n %/% seq + as.logical(n %% seq))))
}
nadj <- function(n, do, seq) {
return(as.integer(balance(n / (1 - do), seq)))
}
```

Say, the assumed *CV* was 15%, the T/R-ratio 0.95, and we planned the study for power ≥ 90% and an anticipated a dropout-rate of 15%. More subjects than estimated were dosed (quite often the management decides). In a small survey a whopping 37% of respondents reported that.^{8}

```
CV <- 0.15
target <- 0.90
do <- 0.15
theta0 <- pe <- TR <- 0.95
n <- sampleN.TOST(CV = CV, targetpower = target,
theta0 = theta0,
print = FALSE)[["Sample size"]]
n <- nadj(n, do, 2) # adjust for droputs, balanced
ns <- n:(n*2.5)
res1 <- data.frame(n = ns, CL.lo = NA, CL.hi = NA,
p.lo = NA, p.hi = NA,
post.hoc = NA)
# as planned
for (i in seq_along(ns)) {
res1[i, 2:3] <- 100*CI.BE(CV = CV, pe = pe,
n = ns[i])
res1[i, 4:5] <- suppressMessages(
pvalues.TOST(CV = CV, pe = pe,
n = ns[i]))
res1[i, 6] <- suppressMessages(
power.TOST(CV = CV, n = ns[i],
theta0 = theta0))
}
windows(width = 4.5, height = 4.5)
op <- par(no.readonly = TRUE)
par(mar = c(4.1, 4, 0, 0), cex.axis = 0.9)
plot(ns, rep(100, length(ns)), ylim = c(80, 125),
type = "n", axes = FALSE, log = "y",
xlab = "sample size",
ylab = "T/R-ratio (90% CI)")
axis(1, at = seq(n, tail(ns, 1), 6))
axis(2, at = c(80, 90, 100, 110, 120, 125), las = 1)
grid(nx = NA, ny = NULL)
abline(v = seq(n, tail(ns, 1), 6), col = "lightgray", lty = 3)
abline(h = c(80, 100, 125), lty = 2,
col = c("red", "black", "red"))
abline(v = head(res1$n[res1$CL.hi < 100], 1), lty = 2)
segments(x0 = ns[1], x1 = tail(ns, 1),
y0 = 100*TR, col = "blue")
lines(res1$n, res1$CL.lo, type = "s", col = "blue", lwd = 2)
lines(res1$n, res1$CL.hi, type = "s", col = "blue", lwd = 2)
box()
par(op)
```

We face a significant treatment effect with ≥ 48 subjects (upper confidence limit ≤ 99.98%).

Similar to the previous example but the management was more relaxed (24 subjects dosed).

This time the T/R-ratio turned out to be worse (0.92 instead of the assumed 0.95).

```
theta0 <- 0.95
target <- 0.90
do <- 0.15
TR <- 0.92
n <- sampleN.TOST(CV = CV, targetpower = target,
theta0 = theta0,
print = FALSE)[["Sample size"]]
n.adj <- nadj(n, do, 2) # adjust for droputs, balanced
n.hi <- balance(n.adj * 1.2, 2)
ns <- n:n.hi
res2 <- data.frame(n = ns, CL.lo = NA, CL.hi = NA,
p.lo = NA, p.hi = NA,
post.hoc = NA)
for (i in seq_along(ns)) {
res2[i, 2:3] <- 100*CI.BE(CV = CV, pe = TR,
n = ns[i])
res1[i, 4:5] <- suppressMessages(
pvalues.TOST(CV = CV, pe = TR,
n = ns[i]))
res1[i, 6] <- suppressMessages(
power.TOST(CV = CV, n = ns[i],
theta0 = TR))
}
windows(width = 4.5, height = 4.5)
op <- par(no.readonly = TRUE)
par(mar = c(4.1, 4, 0, 0), cex.axis = 0.9)
plot(ns, rep(100, length(ns)), ylim = c(80, 125),
type = "n", axes = FALSE, log = "y",
xlab = "sample size",
ylab = "T/R-ratio (90% CI)")
axis(1, at = seq(n, tail(ns, 1), 2))
axis(2, at = c(80, 90, 100, 110, 120, 125), las = 1)
grid(nx = NA, ny = NULL)
abline(v = seq(n, tail(ns, 1), 2), col = "lightgray", lty = 3)
abline(h = c(80, 100, 125), lty = 2,
col = c("red", "black", "red"))
abline(v = head(res2$n[res2$CL.hi < 100], 1), lty = 2)
segments(x0 = ns[1], x1 = tail(ns, 1),
y0 = 100*TR, col = "blue")
lines(res2$n, res2$CL.lo, type = "s", col = "blue", lwd = 2)
lines(res2$n, res2$CL.hi, type = "s", col = "blue", lwd = 2)
box()
par(op)
```

We face a significant treatment effect with ≥ 20 subjects (upper confidence limit ≤ 99.84%).

We had to deal with a drug with low variability. The assumed *CV* was 10%, the T/R-ratio 0.95, and we planned the study for power ≥ 80%. Theoretically we would need only eight [*sic*] subjects but the minimum sample size according to the guidelines is twelve. We adjusted the sample size for an anticipated a dropout-rate of 15%.

The T/R-ratio turned out to be slightly worse (0.935 instead of the assumed 0.95).

```
CV <- 0.10
target <- 0.80
theta0 <- 0.95
TR <- 0.935
do <- 0.15
n <- sampleN.TOST(CV = CV, targetpower = target,
theta0 = theta0,
print = FALSE)[["Sample size"]]
if (n < 12) n <- 12 # acc. to GL
n.adj <- nadj(n, do, 2) # adjust for droputs
ns <- n:n.adj
res3 <- data.frame(n = ns, CL.lo = NA, CL.hi = NA,
p.lo = NA, p.hi = NA,
post.hoc = NA)
for (i in seq_along(ns)) {
res3[i, 2:3] <- 100*CI.BE(CV = CV, pe = TR,
n = ns[i])
res1[i, 4:5] <- suppressMessages(
pvalues.TOST(CV = CV, pe = TR,
n = ns[i]))
res3[i, 6] <- suppressMessages(
power.TOST(CV = CV, n = ns[i],
theta0 = TR))
}
windows(width = 4.5, height = 4.5)
op <- par(no.readonly = TRUE)
par(mar = c(4.1, 4, 0, 0), cex.axis = 0.9)
plot(ns, rep(100, length(ns)), ylim = c(80, 125),
type = "n", axes = FALSE, log = "y",
xlab = "sample size",
ylab = "T/R-ratio (90% CI)")
axis(1, at = ns)
axis(2, at = c(80, 90, 100, 110, 120, 125), las = 1)
grid(nx = NA, ny = NULL)
abline(v = ns, col = "lightgray", lty = 3)
abline(h = c(80, 100, 125), lty = 2,
col = c("red", "black", "red"))
abline(v = head(res3$n[res3$CL.hi < 100], 1), lty = 2)
segments(x0 = ns[1], x1 = tail(ns, 1),
y0 = 100*TR, col = "blue")
lines(res3$n, res3$CL.lo, type = "s", col = "blue", lwd = 2)
lines(res3$n, res3$CL.hi, type = "s", col = "blue", lwd = 2)
box()
par(op)
```

Already with 14 subjects we face a significant treatment effect (upper confidence limit 99.998%). This ‘nasty’ value will disappear due to rounding but will remain in the output of the ANOVA.

Drugs with a low *CV* regularly show a significant treatment effect, since following the guidelines leads to ‘overpowered’ studies. With the minimum twelve subjects according to the guidelines we will have a *post hoc* power of 97.2% (though we planned only for 80%).

Commonly equivalence of more than one endpoint has to be demonstrated.

In bioequivalence the pharmacokinetic metrics \(\small{C_\textrm{max}}\) and \(\small{AUC_{0-\textrm{t}}}\) are mandatory (in some jurisdictions like the FDA additionally \(\small{AUC_{0-\infty}}\)).

We don’t have to worry about multiplicity issues (inflated Type I Error) since if *all* tests must pass at level \(\alpha\), we are protected by the intersection-union principle.^{9} ^{10}

We design the study always for the worst case combination, *i.e.*, based on the PK metric requiring the largest sample size.

The assumed *CV* of \(\small{C_\textrm{max}}\) is 25% and the one of \(\small{AUC}\) is lower (say the variance ratio is 0.70). We assume a T/R-ratio of 0.95 for both, aiming at power ≥ 80%. The anticipated dropout-rate is 10%.

The supportive function `opt()`

provides extreme point estimates of \(\small{AUC}\) which will still give our target power (only the lower one is given in the 4^{th} column). If this value is realized in the study, its upper confidence limit will not include 100% if we have not at least two droputs.

```
opt <- function(x) {
suppressMessages(
power.TOST(theta0 = x, CV = res4$CV[2],
n = n.est)) - target
}
metrics <- c("Cmax", "AUC")
ratio <- 0.70 # variance ratio (AUC / Cmax)
CV.Cmax <- 0.25 # CV of Cmax
CV.AUC <- mse2CV(CV2mse(CV.Cmax)*ratio)
CV <- signif(c(CV.Cmax, CV.AUC))
theta0 <- 0.95 # both metrics
target <- 0.80 # target (desired) power
do.rate <- 0.10 # anticipated dropout-rate 10%
res4 <- data.frame(metric = metrics, theta0 = theta0,
CV = CV, n = NA, power1 = NA,
nadj = NA, power2 = NA)
# sample sizes for both metrics
# study sample size based one the one with
# higher CV and adjusted for the dropout-rate
for (i in 1:nrow(res4)) {
res4[i, 4:5] <- sampleN.TOST(CV = CV[i],
theta0 = theta0,
targetpower = target,
print = FALSE)[7:8]
}
res4$nadj <- nadj(max(res4$n), do.rate, 2)
res4$power1 <- res4$power1
for (i in 1:nrow(res4)) {
res4[i, 7] <- power.TOST(CV = CV[i], theta0 = theta0,
n = res4$nadj[i])
}
res4[, c(5, 7)] <- signif(res4[, c(5, 7)], 4)
names(res4)[c(5, 7)] <- c("pwr (n)", "pwr (nadj)")
res5 <- data.frame(n = max(res4$nadj):max(res4$n),
PE = theta0, CL.hi1 = NA,
PE.lo = NA, CL.hi2 = NA, power = NA)
for (i in 1:nrow(res5)) {
n.est <- res5$n[i]
if (theta0 < 1) {
res5$PE.lo[i] <- uniroot(opt, tol = 1e-8,
interval =
c(0.80 + 1e-4,
theta0))$root
}else {
res5$PE.lo[i] <- uniroot(opt, tol = 1e-8,
interval =
c(theta0,
1.25 - 1e-4))$root
}
res5[i, 3] <- CI.BE(CV = CV[2], pe = theta0,
n = res5$n[i])[["upper"]]
res5[i, 5] <- CI.BE(CV = CV[2],
pe = res5$PE.lo[i],
n = res5$n[i])[["upper"]]
res5[i, 6] <- round(suppressMessages(
power.TOST(CV = CV[2], n = n.est)), 4)
}
res5[, 2:5] <- round(100*res5[, 2:5], 2)
names(res5)[c(3, 5)] <- rep("upper CL", 2)
print(res4, row.names = FALSE)
cat("AUC:\n");
print(res5, row.names = FALSE)
```

```
# metric theta0 CV n pwr (n) nadj pwr (nadj)
# Cmax 0.95 0.250000 28 0.8074 32 0.8573
# AUC 0.95 0.208208 20 0.8057 32 0.9467
# AUC:
# n PE upper CL PE.lo upper CL power
# 32 95 103.68 91.20 99.53 0.9467
# 31 95 103.83 91.41 99.91 0.9403
# 30 95 104.00 91.62 100.29 0.9337
# 29 95 104.17 91.85 100.71 0.9258
# 28 95 104.35 92.08 101.14 0.9176
```

Due to its lower *CV* we would need only 20 subjects for \(\small{AUC}\). However, for \(\small{C_\textrm{max}}\) we need 28. We perform the study in 32 subjects (adjusted for the dropout-rate). Consequently, the study is ‘overpowered’ for \(\small{AUC}\) (~95% instead of ~81% with 20 subjects).

Such a situation is quite common and the further the *CV*s of pharmacokinetic metrics are apart, the more often we will face it.

In a particular study the point estimate may be even lower and/or the *CV* whilst the study still passes. Then we will get a significant treatment effect with more dropouts.

Although that is straightforward and based on elementary statistics, below an R-script to perform simulations.

Say we assume a *CV* of \(\small{C_\textrm{max}}\) (25%), base the sample size on it (taking the dropout-rate into account) and the *CV* of \(\small{AUC}\) is lower but *unknown*. How often can we expect a significant treatment effect for a range of *CV*s (here 25% down to 15%)?

```
# Cave: Long runtime!
set.seed(123456)
nsims <- 1e4L # number of simulations
target <- 0.80 # target power
PE <- 0.95 # assumed PE (both metrics)
CV.Cmax <- 0.25 # assumed CV of Cmax
CV.AUC <- c(0.25, 0.20, 0.15)
do.rate <- 0.1 # anticipated dropout-rate (10%)
CV.do <- 0.15 # assumed CV of the dropout-rate (15%)
tmp <- sampleN.TOST(CV = CV.Cmax, theta0 = PE,
targetpower = target,
details = FALSE, print = FALSE)
n.des <- tmp[["Sample size"]]
if (n.des >= 12) {
power.Cmax <- tmp[["Achieved power"]]
} else {# GL!
n.des <- 12
power.Cmax <- power.TOST(CV = CV.Cmax, theta0 = PE, n = n.des)
}
power.AUC <- numeric()
for (j in seq_along(CV.AUC)) {
power.AUC[j] <- power.TOST(CV = CV.AUC[j], theta0 = PE, n = n.des)
}
n.adj <- nadj(n = n.des, do = do.rate, seq = 2)
res.Cmax <- data.frame(CV = rep(NA, nsims), n = NA, PE = NA,
lower = NA, upper = NA, BE = FALSE,
signif = FALSE)
post.Cmax <- data.frame(sim = 1:nsims)
res.AUC <- data.frame(CV.ass = rep(CV.AUC, each = nsims),
CV = rep(NA, nsims), n = NA, PE = NA,
lower = NA, upper = NA, BE = FALSE,
signif = FALSE)
post.AUC <- data.frame(CV.ass = rep(CV.AUC, each = nsims),
sim =1:nsims*length(CV.AUC))
for (j in 1:nsims) {
do <- rlnorm(1, meanlog = log(do.rate) - 0.5*CV2mse(CV.do),
sdlog = sqrt(CV2mse(CV.do)))
res.Cmax$n[j] <- as.integer(round(n.des * (1 - do)))
res.Cmax$CV[j] <- mse2CV(CV2mse(CV.Cmax) *
rchisq(1, df = res.Cmax$n[j] - 2)/(res.Cmax$n[j] - 2))
res.Cmax$PE[j] <- exp(rnorm(1, mean = log(PE),
sd = sqrt(0.5 / res.Cmax$n[j]) *
sqrt(CV2mse(CV.Cmax))))
res.Cmax[j, 4:5] <- round(CI.BE(CV = res.Cmax$CV[j],
pe = res.Cmax$PE[j],
n = res.Cmax$n[j]), 4)
if (res.Cmax$lower[j] >= 0.80 & res.Cmax$upper[j] <= 1.25) {
res.Cmax$BE[j] <- TRUE
if (res.Cmax$lower[j] > 1 | res.Cmax$upper[j] < 1)
res.Cmax$signif[j] <- TRUE
}
}
i <- 0
for (k in seq_along(CV.AUC)) {
for (j in 1:nsims) {
i <- i + 1
res.AUC$n[i] <- res.Cmax$n[j]
res.AUC$CV[i] <- mse2CV(CV2mse(CV.AUC[k]) *
rchisq(1, df = res.AUC$n[i] - 2)/(res.AUC$n[i] - 2))
res.AUC$PE[i] <- exp(rnorm(1, mean = log(PE),
sd = sqrt(0.5 / res.AUC$n[i]) *
sqrt(CV2mse(CV.AUC[k]))))
res.AUC[i, 5:6] <- round(CI.BE(CV = res.AUC$CV[i],
pe = res.AUC$PE[i],
n = res.AUC$n[i]), 4)
if (res.AUC$lower[i] >= 0.80 & res.AUC$upper[i] <= 1.25) {
res.AUC$BE[i] <- TRUE
if (res.AUC$lower[i] > 1 | res.AUC$upper[i] < 1)
res.AUC$signif[i] <- TRUE
}
}
}
passed.Cmax <- sum(res.Cmax$BE)
passed.AUC <- numeric(length(CV.AUC))
for (j in seq_along(CV.AUC)) {
passed.AUC[j] <- sum(res.AUC$BE[res.AUC$CV.ass == CV.AUC[j]])
}
txt <- paste("Assumed CV (Cmax) :", sprintf("%.4f", CV.Cmax),
"\nAssumed CVs (AUC) :", paste(sprintf("%.4f", CV.AUC),
collapse = ", "),
"\nAssumed PE :", sprintf("%.4f", PE),
"\nTarget power :", sprintf("%.4f", target),
"\nSample size :", n.des, "(based on Cmax)",
"\nAchieved power (Cmax):", sprintf("%.4f", power.Cmax),
"\nAchieved powers (AUC):", paste(sprintf("%.4f", power.AUC),
collapse = ", "),
"\nDosed :", n.adj,
sprintf("(anticip. dropout-rate %g)", do.rate),
"\n ", formatC(nsims, format = "d", big.mark = ","),
"simulated 2\u00D72\u00D72 studies",
"\n n:", min(res.Cmax$n), "\u2013", max(res.Cmax$n),
sprintf("(median %g)", median(res.Cmax$n)),
"\n Cmax", sprintf("(%.4f)", CV.Cmax),
"\n CV :",
sprintf("%6.4f \u2013 %6.4f", min(res.Cmax$CV), max(res.Cmax$CV)),
sprintf("(median %7.4f)", exp(median(log(res.Cmax$CV)))),
"\n PE :",
sprintf("%6.4f \u2013 %6.4f", min(res.Cmax$PE), max(res.Cmax$PE)),
sprintf("(g. mean%7.4f)", exp(mean(log(res.Cmax$PE)))),
"\n 100% not within CI (stat. significant):",
sprintf("%5.2f%%", 100*sum(res.Cmax$signif)/passed.Cmax), "\n")
for (j in seq_along(CV.AUC)) {
txt <- paste(txt, " AUC", sprintf("(%.4f)", CV.AUC[j]),
"\n CV :",
sprintf("%6.4f \u2013 %6.4f",
min(res.AUC$CV[res.AUC$CV.ass == CV.AUC[j]]),
max(res.AUC$CV[res.AUC$CV.ass == CV.AUC[j]])),
sprintf("(median %7.4f)",
exp(median(log(res.AUC$CV[res.AUC$CV.ass == CV.AUC[j]])))),
"\n PE :",
sprintf("%6.4f \u2013 %6.4f",
min(res.AUC$PE[res.AUC$CV.ass == CV.AUC[j]]),
max(res.AUC$PE[res.AUC$CV.ass == CV.AUC[j]])),
sprintf("(g. mean%7.4f)",
exp(mean(log(res.AUC$PE[res.AUC$CV.ass == CV.AUC[j]])))),
"\n 100% not within CI (stat. significant):",
sprintf("%5.2f%%",
100*sum(res.AUC$signif[res.AUC$CV.ass == CV.AUC[j]])/passed.AUC[j]),
"\n")
}
cat(txt)
```

```
# Assumed CV (Cmax) : 0.2500
# Assumed CVs (AUC) : 0.2500, 0.2000, 0.1500
# Assumed PE : 0.9500
# Target power : 0.8000
# Sample size : 28 (based on Cmax)
# Achieved power (Cmax): 0.8074
# Achieved powers (AUC): 0.8074, 0.9349, 0.9946
# Dosed : 32 (anticip. dropout-rate 0.1)
# 10,000 simulated 2×2×2 studies
# n: 23 – 26 (median 25)
# Cmax (0.2500)
# CV : 0.1199 – 0.4127 (median 0.2468)
# PE : 0.8314 – 1.0736 (g. mean 0.9502)
# 100% not within CI (stat. significant): 2.30%
# AUC (0.2500)
# CV : 0.1248 – 0.4099 (median 0.2462)
# PE : 0.8373 – 1.0814 (g. mean 0.9491)
# 100% not within CI (stat. significant): 2.70%
# AUC (0.2000)
# CV : 0.1008 – 0.3302 (median 0.1969)
# PE : 0.8506 – 1.0458 (g. mean 0.9501)
# 100% not within CI (stat. significant): 7.96%
# AUC (0.1500)
# CV : 0.0831 – 0.2663 (median 0.1481)
# PE : 0.8722 – 1.0216 (g. mean 0.9497)
# 100% not within CI (stat. significant): 19.96%
```

What does that mean? You name it.

In most jurisdictions (*e.g.* the EMA) reference-scaling is acceptable for \(\small{C_\textrm{max}}\), whereas for \(\small{AUC}\) conventional ABE has to be assessed. If \(\small{AUC}\) is highly variable as well, the study will be ‘overpowered’ for \(\small{C_\textrm{max}}\) and a significant treatment effect possible.

```
metrics <- c("Cmax", "AUC")
CV <- c(0.45, 0.35)
theta0 <- rep(0.90, 2)
theta1 <- 0.80
theta2 <- 1 / theta1
target <- 0.80
design <- "2x2x4"
plan <- data.frame(metric = metrics,
method = c("ABEL", "ABE"),
CV = CV, theta0 = theta0,
L = 100 * theta1, U = 100 * theta2,
n = NA_integer_, power = NA_real_)
for (i in 1:nrow(plan)) {
if (plan$method[i] == "ABEL") {
# L and U are the expanded limits
plan[i, 5:6] <- round(100*scABEL(CV = CV[i]), 2)
plan[i, 7:8] <- signif(
sampleN.scABEL(CV = CV[i],
theta0 = theta0[i],
theta1 = theta1,
theta2 = theta2,
targetpower = target,
design = design,
details = FALSE,
print = FALSE)[8:9], 4)
}else {
plan[i, 7:8] <- signif(
sampleN.TOST(CV = CV[i],
theta0 = theta0[i],
theta1 = theta1,
theta2 = theta2,
targetpower = target,
design = design,
print = FALSE)[7:8], 4)
}
}
txt <- paste0("L and U are the – if applicable, expanded – BE limits.",
"\nSample size based on ",
plan$metric[plan$n == max(plan$n)], ".")
pwr <- power.scABEL(CV = plan$CV[plan$metric ==
plan$metric[plan$n == min(plan$n)]],
theta0 = plan$theta0[plan$metric ==
plan$metric[plan$n == min(plan$n)]],
n = plan$n[plan$n == max(plan$n)], design = design)
CI <- CI.BE(CV = plan$CV[plan$metric ==
plan$metric[plan$n == min(plan$n)]],
pe = plan$theta0[plan$metric ==
plan$metric[plan$n == min(plan$n)]],
n = max(plan$n), design = design)
txt <- paste0(txt, "\nPower for ", plan$metric[plan$n == min(plan$n)],
" with ", max(plan$n), " subjects: ",
sprintf("%.4g", pwr), ".")
if (CI[["lower"]] > 1 | CI[["upper"]] < 1) {
txt <- paste0(txt, "\nSignificant treatment effect for ",
plan$metric[plan$n == min(plan$n)], " expected.\n")
} else {
txt <- paste0(txt, "\nNo significant treatment effect for ",
plan$metric[plan$n == min(plan$n)], " expected.\n")
}
plan[, 5] <- sprintf("%.2f%%", plan[, 5])
plan[, 6] <- sprintf("%.2f%%", plan[, 6])
print(plan, row.names = FALSE)
cat(txt)
```

```
# metric method CV theta0 L U n power
# Cmax ABEL 0.45 0.9 72.15% 138.59% 28 0.8112
# AUC ABE 0.35 0.9 80.00% 125.00% 52 0.8003
# L and U are the – if applicable, expanded – BE limits.
# Sample size based on AUC.
# Power for Cmax with 52 subjects: 0.9579.
# Significant treatment effect for Cmax expected.
```

Let’s explore what might happen if all assumed values will be realized in the study.

```
res <- data.frame(metric = metrics,
method = c("ABEL", "ABE"),
CV = CV, theta0 = theta0,
lower.CL = NA_real_,
upper.CL = NA_real_,
n = max(plan$n), power = NA_real_)
res[1, 5:6] <- CI.BE(CV = CV[1], pe = theta0[1], n = max(plan$n),
design = design)
res[1, 8] <- power.scABEL(CV = CV[1], theta0 = theta0[1],
n = max(plan$n), design = design)
res[2, 5:6] <- CI.BE(CV = CV[2], pe = theta0[2], n = max(plan$n),
design = design)
res[2, 8] <- power.TOST(CV = CV[2], theta0 = theta0[2],
n = max(plan$n), design = design)
res[, 5] <- sprintf("%.2f%%", 100 * res[, 5])
res[, 6] <- sprintf("%.2f%%", 100 * res[, 6])
res[, 8] <- sprintf("%.4g", res[, 8])
print(res, row.names = FALSE)
```

```
# metric method CV theta0 lower.CL upper.CL n power
# Cmax ABEL 0.45 0.9 81.55% 99.32% 52 0.9579
# AUC ABE 0.35 0.9 83.25% 97.30% 52 0.8003
```

Although we expected a significant treatment effect only for \(\small{C_\textrm{max}}\), for both metrics the upper confidence limits are with 99.32% and 97.30% below 100%. Like in the other examples, the study is ‘overpowered” for \(\small{C_\textrm{max}}\).

Sometimes drugs are classified as an NTID but narrowing the acceptance range is only required for one of the PK metrics. An example is tacrolimus, where the EMA recommends 90.00 – 111.11% for \(\small{AUC_{0-72}}\) and 80.00 – 125.00% for \(\small{C_\textrm{max}}\).^{11}

Let’s explore a study from the literature.^{12} Assuming a *CV* of ≈11% and a T/R-ratio of 95% the authors claimed that the study was powered to 80% for the narrow limits of \(\small{AUC_{0-72}}\) with 52 subjects.^{13} 56 subjects were dosed and 52 completed both periods of the study.

```
design <- "2x2x2"
n <- 52
AUC <- setNames(c(1.037831, 0.974019, 1.105824, 0.1949),
c("PE", "lower", "upper", "CV"))
Cmax <- setNames(c(1.150745, 1.098079, 1.205938, 0.1433),
c("PE", "lower", "upper", "CV"))
res <- data.frame(metric = c("AUC", "Cmax"),
CV = c(AUC[["CV"]], Cmax[["CV"]]),
PE = c(AUC[["PE"]], Cmax[["PE"]]),
lower.CL = c(AUC[["lower"]], Cmax[["lower"]]),
upper.CL = c(AUC[["upper"]], Cmax[["upper"]]),
theta1 = c(0.90, 0.80), theta2 = 1 / c(0.90, 0.80),
p = NA, power = NA)
for (i in 1:nrow(res)) {
res$p[i] <- pvalue.TOST(pe = res$PE[i], CV = res$CV[i], n = n,
theta1 = res$theta1[i])
res$power[i] <- power.TOST(CV = res$CV[i], n = n,
theta1 = res$theta1[i],
theta0 = res$PE[i], design = design)
}
res <- res[, -c(6:7)] # remove thetas
res[, 6:7] <- round(res[, 6:7], 4)
res[, 3] <- sprintf("%.2f%%", 100 * res[, 3])
res[, 4] <- sprintf("%.2f%%", 100 * res[, 4])
res[, 5] <- sprintf("%.2f%%", 100 * res[, 5])
print(res, row.names = FALSE)
```

```
# metric CV PE lower.CL upper.CL p power
# AUC 0.1949 103.78% 97.40% 110.58% 0.0388 0.5333
# Cmax 0.1433 115.07% 109.81% 120.59% 0.0024 0.8986
```

The study passed BE for both metrics (90% CI of \(\small{AUC_{0-72}}\) within 90.00 – 111.11% and of \(\small{C_\textrm{max}}\) within 80.00 – 125.00%). We see a significant treatment effect for \(\small{C_\textrm{max}}\) because its confidence interval of 109.81 – 120.59% does not include 100%.

The *CV*s were substantially higher than the assumed 11%. The T/R-ratio of \(\small{C_\textrm{max}}\) was much worse than assumed and only the large sample size required for \(\small{AUC_{0-72}}\) ‘saved’ the study from failing. Since with 110.58% the upper confidence limit of \(\small{AUC_{0-7 2}}\) was close to the boundary of 111.11%, *post hoc* power was only 53.33%. Whilst not clinically relevant (see another article), IMHO, it was curageous to assume such a low variability taking results of other studies into account.

Coming back to the questions asked in the Introduction. To repeat:

What is a significant treatment effect … ?

- It is a natural property of any test at level
powered with*α*.*π*

If a study passes, it does not refute the conclusion (statistical significance ≠ clinical relevance).

… and do we have to care about one?

- Not at all.

However, if you are asked by a regulator for a ‘justification’, answer in a diplomatic way. Keep calm and stay polite.

Licenses

Helmut Schütz 2022

`R`

and `PowerTOST`

GPL 3.0, `pandoc`

GPL 2.0.

1^{st} version March 18, 2021. Rendered June 27, 2022 13:53 CEST by rmarkdown via pandoc in 0.70 seconds.

Footnotes and References

Labes D, Schütz H, Lang B.

*PowerTOST: Power and Sample Size for (Bio)Equivalence Studies.*Package version 1.5.4. 2022-02-21. CRAN.↩︎Statisticians may be more familiar with the terminology \(\small{\textrm{AB}|\textrm{BA}}\).

Forgive me – in bioequivalence \(\small{\textrm{TR}|\textrm{RT}}\) is commonly used, where \(\small{\textrm{T}}\) denotes the Test and \(\small{\textrm{R}}\) the Reference treatment (formulation).↩︎Schuirmann DJ.

*A Comparison of the Two One-Sided Tests Procedure and the Power Approach for Assessing the Equivalence of Average Bioavailability.*J Pharmacokin Biopharm. 1987; 15(6): 657–80. doi:10.1007/BF01068419.↩︎EEC.

*Note for Guidance. Investigation of Bioavailability and Bioequivalence.*3CC15a. Brussels. December 1991. Online.↩︎FDA, CDER.

*Guidance for Industry. Statistical Procedures for Bioequivalence Studies Using a Standard Two-Treatment Crossover Design.*Rockville. Jul 1992. Internet Archive.↩︎Health Canada, HPFB,

*Guidance for Industry. Conduct and Analysis of Bioavailability and Bioequivalence Studies - Part A: Oral Dosage Formulations Used for Systemic Effects.*H42-2/56-1992E. Ottawa. 1992. Online.↩︎Stupid example:

*CV*= 10% (NTID),*n*= 120, 4-period full replicate design, \(\small{\theta_0=98.5\%}\)

→ 90% CI: 97.03 – 99.99%, \(\small{p}\) 5·10^{–72}…↩︎Schütz H.

*Sample Size Estimation in Bioequivalence. Evaluation.*BEBA Forum. 2020-10-23. Online.↩︎Berger RL, Hsu JC.

*Bioequivalence Trials, Intersection-Union Tests and Equivalence Confidence Sets.*Stat Sci. 1996; 11(4): 283–302. JSTOR:2246021. Open Access.↩︎Zeng A.

*The TOST confidence intervals and the coverage probabilities with R simulation.*March 14, 2014. Online.↩︎EMA, CHMP.

*Tacrolimus granules for oral suspension 0.2 and 1 mg product-specific bioequivalence guidance.*EMA/CHMP/159744/2016. London. 31 April 2016. Online.↩︎ Mohanty L, Bhushan S, Rüttger B.

*Bioequivalence of two tacrolimus 1-mg formulations under fasting conditions in healthy subjects: A randomized, two-period crossover trial.*Int J Clin Pharmacol Ther. 2020; 58(3): 183–93. doi:10.5414/CP203534. Free Full Text.↩︎Given, I estimated 54.↩︎