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Examples in this article were generated with 4.2.1 by the packages PowerTOST1 and TeachingDemos.2

More examples are given in the respective vignettes.3 4 See also the README on GitHub for an overview and the online manual5 for details.

For background about sample size estimations in replicate designs see the respective articles (ABE, RSABE, and ABEL). See also the articles about power and sensitivity analyses.

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

1. Basics about power and sample size methodology – requiring no or only limited statistical expertise.

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

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

1. An advanced knowledge of statistics and/or R is required. Not recommended for beginners in particular.
• Click to show / hide R code.
Abbreviation Meaning
$$\small{\alpha}$$ Nominal level of the test, probability of Type I Error (patient’s risk)
(A)BE (Average) Bioequivalence
ABEL Average Bioequivalence with Expanding Limits
AUC Area Under the Curve
$$\small{\beta}$$ Probability of Type II Error (producer’s risk), where $$\small{\beta=1-\pi}$$
CDE Center for Drug Evaluation (China)
CI Confidence Interval
CL Confidence Limit
Cmax Maximum concentration
$$\small{CV_\textrm{w}}$$ (Pooled) within-subject Coefficient of Variation
$$\small{CV_\textrm{wR},\;CV_\textrm{wT}}$$ Observed within-subject Coefficient of Variation of the Reference and Test product
$$\small{\Delta}$$ Clinically relevant difference
EMA European Medicines Agency
FDA (U.S.) Food and Drug Administration
$$\small{H_0}$$ Null hypothesis (inequivalence)
$$\small{H_1}$$ Alternative hypothesis (equivalence)
HVD(P) Highly Variable Drug (Product)
$$\small{k}$$ Regulatory constant in ABEL (0.760)
$$\small{\mu_\textrm{T}/\mu_\textrm{R}}$$ True T/R-ratio
$$\small{n}$$ Sample size
$$\small{\pi}$$ (Prospective) power, where $$\small{\pi=1-\beta}$$
PE Point Estimate
R Reference product
RSABE Reference-Scaled Average Bioequivalence
SABE Scaled Average Bioequivalence
$$\small{s_\textrm{bR}^2,\;s_\textrm{bT}^2}$$ Observed between-subject variance of the Reference and Test product
$$\small{s_\textrm{wR},\;s_\textrm{wT}}$$ Observed within-subject standard deviation of the Reference and Test product
$$\small{s_\textrm{wR}^2,\;s_\textrm{wT}^2}$$ Observed within-subject variance of the Reference and Test product
$$\small{\sigma_\textrm{wR}}$$ True within-subject standard deviation of the Reference product
T Test product
$$\small{\theta_0}$$ True T/R-ratio
$$\small{\theta_1,\;\theta_2}$$ Fixed lower and upper limits of the acceptance range (generally 80.00 – 125.00%)
$$\small{\theta_\textrm{s}}$$ Regulatory constant in RSABE (0.8925742…)
$$\small{\theta_{\textrm{s}_1},\;\theta_{\textrm{s}_2}}$$ Scaled lower and upper limits of the acceptance range
TIE Type I Error (patient’s risk)
TIIE Type II Error (producer’s risk: 1 – power)
uc Upper cap of expansion in ABEL
2×2×2 2-treatment 2-sequence 2-period crossover design (TR|RT)
2×2×3 2-treatment 2-sequence 3-period full replicate designs (TRT|RTR and TTR|RRT)
2×2×4 2-treatment 2-sequence 4-period full replicate designs (TRTR|RTRT, TRRT|RTTR, and TTRR|RRTT)
2×3×3 2-treatment 3-sequence 3-period partial replicate design (TRR|RTR|RRT)
2×4×2 2-treatment 4-sequence 2-period full replicate design (TR|RT|TT|RR)
2×4×4 2-treatment 4-sequence 4-period full replicate designs (TRTR|RTRT|TRRT|RTTR and TRRT|RTTR|TTRR|RRTT)

# Introduction

What are the differences between Average Bioequivalence (ABE), Reference-Scaled Average Bioequivalence (RSABE), and Average Bioequivalence with Expanding Limits (ABEL) in terms of power and sample sizes?

For details about inferential statistics and hypotheses in equivalence see another article.

Definitions:

• A Highy Variable Drug (HVD) shows a within-subject Coefficient of Variation (CVwR) > 30% if administered as a solution in a replicate design. The high variability is an intrinsic property of the drug (absorption/permeation, clearance).
• A Highy Variable Drug Product (HVDP) shows a CVwR > 30% in a replicate design.6

The concept of Scaled Average Bioequivalence (SABE) for HVD(P)s is based on the following considerations:

• HVD(P)s are safe and efficacious despite their high variability because:
• They have a wide therapeutic index (i.e., a flat dose-response curve). Consequently, even substantial changes in concentrations have only a limited impact on the effect.
If they would have a narrow therapeutic index, adverse effects (due to high concentrations) and lacking effects (due to low concentrations) would have been observed in Phase II (or in Phase III at the latest) and therefore, the originator’s product not have been approved in the first place.
• Once approved, the product has a documented safety / efficacy record in phase IV and in clinical practice – despite its high variability.
If problems were evident, the product would have been taken off the market.
• Given that, the conventional ‘clinically relevant difference’ Δ of 20% in ABE (leading to the fixed limits of 80.00 – 125.00%) is overly conservative and therefore, requires large sample sizes.
• Thus, a more relaxed Δ > 20% was proposed. A natural approach is to scale (expand / widen) the limits based on the within-subject variability of the reference product σwR.7

The conventional confidence interval inclusion approach in ABE is based on $\begin{matrix}\tag{1} \theta_1=1-\Delta,\theta_2=\left(1-\Delta\right)^{-1}\\ H_0:\;\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\not\subset\left\{\theta_1,\,\theta_2\right\}\;vs\;H_1:\;\theta_1<\frac{\mu_\textrm{T}}{\mu_\textrm{R}}<\theta_2, \end{matrix}$ where $$\small{\Delta}$$ is the clinically relevant difference, $$\small{\theta_1}$$ and $$\small{\theta_2}$$ are the fixed lower and upper limits of the acceptance range, $$\small{H_0}$$ is the null hypothesis of inequivalence, and $$\small{H_1}$$ is the alternative hypothesis. $$\small{\mu_\textrm{T}}$$ and $$\small{\mu_\textrm{R}}$$ are the geometric least squares means of $$\small{\textrm{T}}$$ and $$\small{\textrm{R}}$$, respectively.

$$\small{(1)}$$ is modified in Scaled Average Bioequivalence (SABE) to $H_0:\;\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\Big{/}\sigma_\textrm{wR}\not\subset\left\{\theta_{\textrm{s}_1},\,\theta_{\textrm{s}_2}\right\}\;vs\;H_1:\;\theta_{\textrm{s}_1}<\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\Big{/}\sigma_\textrm{wR}<\theta_{\textrm{s}_2},\tag{2}$ where $$\small{\sigma_\textrm{wR}}$$ is the standard deviation of the reference. The scaled limits $$\small{\left\{\theta_{\textrm{s}_1},\,\theta_{\textrm{s}_2}\right\}}$$ of the acceptance range depend on conditions given by the agency.

RSABE is recommended by the FDA and China’s CDE. ABEL is another variant of SABE and recommended in all other jurisdictions.

In order to apply the methods8 following conditions have to be fulfilled:

• The study has to be performed in a replicate design, i.e., at least the reference product has to be administered twice.
Realization: Ob­servations (in a sample) of a random variable (of the population).
• The realized within-subject variability of the reference has to be high
(in RSABE swR ≥ 0.2949 and in ABEL CVwR > 30%).
• ABEL only:
• A clinical justification must be given that the expanded limits will not impact safety / efficacy.
• There is an ‘upper cap’ of scaling (uc = 50%, except for Health Canada, where uc ≈ 57.382%10), i.e., the expansion is limited to 69.84 – 143.19% or 67.7 – 150.0%, respectively.
• Except for applications in Brazil and Chile, it has to be demonstrated that the high variability of the reference is not caused by ‘outliers’.

In all methods a point estimate-constraint is imposed. Even if a study would pass the scaled limits, the PE has to lie within 80.00 – 125.00% in order to pass.

It should be noted that larger deviations between geometric mean ratios arise as a natural, direct consequence of the higher variability.
Since extreme values are common for HVD(P)s, assessment of ‘outliers’ is not required by the FDA and China’s CDE for RSABE, as well as by Brazil’s ANVISA and Chile’s ANAMED for ABEL.

The PE-constraint – together with the upper cap of expansion in jurisdictions applying ABEL – lead to truncated distributions. Hence, the test assuming the normal distribution of $$\small{\log_{e}}$$-transformed data is not correct in the strict sense.

top of section ↩︎

# Preliminaries

A basic knowledge of R is required. To run the scripts at least version 1.4.8 (2019-08-29) of PowerTOST is required and at least 1.5.3 (2021-01-18) 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.

library(PowerTOST)     # attach the packages
library(TeachingDemos) # to run the examples

# Sample size

The idea behind reference-scaling is to avoid extreme sample sizes required for ABE and preserve power independent from the CV.

Let’s explore some examples. I assumed a $$\small{CV}$$ of 0.45, a T/R-ratio ($$\small{\theta_0}$$) of 0.90, and targeted ≥ 80% power in some common replicate designs.
Note that sample sizes are integers and follow a staircase function because in software packages balanced sequences are returned.

CV      <- 0.45
theta0  <- 0.90
target  <- 0.80
designs <- c("2x2x4", "2x2x3", "2x3x3")
method  <- c("ABE", "ABEL", "RSABE")
res     <- data.frame(design = rep(designs, each = length(method)),
method = method, n = NA)
for (i in 1:nrow(res)) {
if (res$method[i] == "ABE") { res[i, 3] <- sampleN.TOST(CV = CV, theta0 = theta0, design = res$design[i],
targetpower = target,
print = FALSE)[["Sample size"]]
}
if (res$method[i] == "ABEL") { res[i, 3] <- sampleN.scABEL(CV = CV, theta0 = theta0, design = res$design[i],
targetpower = target,
print = FALSE,
details = FALSE)[["Sample size"]]
}
if (res$method[i] == "RSABE") { res[i, 3] <- sampleN.RSABE(CV = CV, theta0 = theta0, design = res$design[i],
targetpower = target,
print = FALSE,
details = FALSE)[["Sample size"]]
}
}
print(res, row.names = FALSE)
#  design method   n
#   2x2x4    ABE  84
#   2x2x4   ABEL  28
#   2x2x4  RSABE  24
#   2x2x3    ABE 124
#   2x2x3   ABEL  42
#   2x2x3  RSABE  36
#   2x3x3    ABE 126
#   2x3x3   ABEL  39
#   2x3x3  RSABE  33

CV      <- 0.45
theta0  <- seq(0.95, 0.85, -0.001)
methods <- c("ABE", "ABEL", "RSABE")
clr     <- c("red", "magenta", "blue")
ylab    <- paste0("sample size (CV = ", 100*CV, "%)")
#################
design <- "2x2x4"
res1   <- data.frame(theta0 = theta0,
method = rep(methods, each =length(theta0)),
n = NA)
for (i in 1:nrow(res1)) {
if (res1$method[i] == "ABE") { res1$n[i] <- sampleN.TOST(CV = CV, theta0 = res1$theta0[i], design = design, print = FALSE)[["Sample size"]] } if (res1$method[i] == "ABEL") {
res1$n[i] <- sampleN.scABEL(CV = CV, theta0 = res1$theta0[i],
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
}
if (res1$method[i] == "RSABE") { res1$n[i] <- sampleN.RSABE(CV = CV, theta0 = res1$theta0[i], design = design, print = FALSE, details = FALSE)[["Sample size"]] } } dev.new(width = 4.5, height = 4.5, record = TRUE) op <- par(no.readonly = TRUE) par(lend = 2, ljoin = 1, mar = c(4, 3.3, 0.1, 0.2), cex.axis = 0.9) plot(theta0, res1$n[res1$method == "ABE"], type = "n", axes = FALSE, ylim = c(12, max(res1$n)), xlab = expression(theta[0]),
log = "xy", ylab = "")
abline(v = seq(0.85, 0.95, 0.025), lty = 3, col = "lightgrey")
abline(v = 0.90, lty = 2)
abline(h = axTicks(2, log = TRUE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.85, 0.95, 0.025))
axis(2, las = 1)
mtext(ylab, 2, line = 2.4)
legend("bottomleft", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "\u226580% power")
lines(theta0, res1$n[res1$method == "ABE"],
type = "S", lwd = 2, col = clr[1])
lines(theta0, res1$n[res1$method == "ABEL"],
type = "S", lwd = 2, col = clr[2])
lines(theta0, res1$n[res1$method == "RSABE"],
type = "S", lwd = 2, col = clr[3])
box()
#################
design <- "2x2x3"
res2   <- data.frame(theta0 = theta0,
method = rep(methods, each =length(theta0)),
n = NA)
for (i in 1:nrow(res2)) {
if (res2$method[i] == "ABE") { res2$n[i] <- sampleN.TOST(CV = CV, theta0 = res2$theta0[i], design = design, print = FALSE)[["Sample size"]] } if (res2$method[i] == "ABEL") {
res2$n[i] <- sampleN.scABEL(CV = CV, theta0 = res2$theta0[i],
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
}
if (res2$method[i] == "RSABE") { res2$n[i] <- sampleN.RSABE(CV = CV, theta0 = res2$theta0[i], design = design, print = FALSE, details = FALSE)[["Sample size"]] } } plot(theta0, res2$n[res2$method == "ABE"], type = "n", axes = FALSE, ylim = c(12, max(res2$n)), xlab = expression(theta[0]),
log = "xy", ylab = "")
abline(v = seq(0.85, 0.95, 0.025), lty = 3, col = "lightgrey")
abline(v = 0.90, lty = 2)
abline(h = axTicks(2, log = TRUE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.85, 0.95, 0.025))
axis(2, las = 1)
mtext(ylab, 2, line = 2.4)
legend("bottomleft", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "\u226580% power")
lines(theta0, res2$n[res2$method == "ABE"],
type = "S", lwd = 2, col = clr[1])
lines(theta0, res2$n[res2$method == "ABEL"],
type = "S", lwd = 2, col = clr[2])
lines(theta0, res2$n[res2$method == "RSABE"],
type = "S", lwd = 2, col = clr[3])
box()
#################
design <- "2x3x3"
res3   <- data.frame(theta0 = theta0,
method = rep(methods, each =length(theta0)),
n = NA)
for (i in 1:nrow(res3)) {
if (res3$method[i] == "ABE") { res3$n[i] <- sampleN.TOST(CV = CV, theta0 = res3$theta0[i], design = design, print = FALSE)[["Sample size"]] } if (res3$method[i] == "ABEL") {
res3$n[i] <- sampleN.scABEL(CV = CV, theta0 = res3$theta0[i],
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
}
if (res3$method[i] == "RSABE") { res3$n[i] <- sampleN.RSABE(CV = CV, theta0 = res3$theta0[i], design = design, print = FALSE, details = FALSE)[["Sample size"]] } } plot(theta0, res3$n[res3$method == "ABE"], type = "n", axes = FALSE, ylim = c(12, max(res3$n)), xlab = expression(theta[0]),
log = "xy", ylab = "")
abline(v = seq(0.85, 0.95, 0.025), lty = 3, col = "lightgrey")
abline(v = 0.90, lty = 2)
abline(h = axTicks(2, log = TRUE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.85, 0.95, 0.025))
axis(2, las = 1)
mtext(ylab, 2, line = 2.4)
legend("bottomleft", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "\u226580% power")
lines(theta0, res3$n[res3$method == "ABE"],
type = "S", lwd = 2, col = clr[1])
lines(theta0, res3$n[res3$method == "ABEL"],
type = "S", lwd = 2, col = clr[2])
lines(theta0, res3$n[res3$method == "RSABE"],
type = "S", lwd = 2, col = clr[3])
box()
par(op)

It’s obvious that we need substantially smaller sample sizes in the methods for reference-scaling than we would require for ABE. The sample size functions of the scaling methods are also not that steep, which means that even if our assumptions about the T/R-ratio would be wrong, power (and hence, sample sizes) would be affected to a lesser degree.

Nevertheless, one should not be overly optimistic about the T/R-ratio. For HVD(P)s a T/R-ratio of ‘better’ than 0.90 should be avoided.11
NB, that’s the reason why in sampleN.scABEL() and sampleN.RSABE() the default is theta0 = 0.90. If scaling is not acceptable (e.g., AUC for the EMA), I strongly recommend to specify theta0 = 0.90 in sampleN.TOST() because its default is 0.95.

Note that RSABE is more permissive than ABEL due to its regulatory constant ~0.8926 instead of 0.760 and unlimited scaling (no upper cap). Hence, sample sizes for RSABE are always smaller than ones for ABEL.

Since power depends on the number of treatments, roughly 50% more subjects are required than in 4-period full replicate designs.

Similar sample sizes than in the 3-period full replicate design because both have the same degrees of freedom. However, the step size is wider (three sequences instead of two).

Interlude 1

Before we estimate a sample size, we have to be clear about the planned evaluation. The EMA and most other agencies require an ANOVA (i.e., all effects fixed), whereas Health Canada, the FDA, and China’s CDE a mixed-effects model.

Let’s explore the replicate designs implemented in PowerTOST. Note that only ABE for Balaam’s design (TR|RT|TT|RR) is implemented.

print(known.designs()[7:11, c(2:4, 9)], row.names = FALSE) # relevant columns
#  design    df df2                      name
#   2x2x3 2*n-3 n-2 2x2x3 replicate crossover
#   2x2x4 3*n-4 n-2 2x2x4 replicate crossover
#   2x4x4 3*n-4 n-4 2x4x4 replicate crossover
#   2x3x3 2*n-3 n-3 partial replicate (2x3x3)
#   2x4x2   n-2 n-2          Balaam's (2x4x2)

The column df gives the degrees of freedom of an ANOVA and the column df2 the ones of a mixed-effects model.

Which model is intended for evaluation is controlled by the argument robust, which is FALSE (for an ANOVA) by default. If set to TRUE, the estimation will be performed for a mixed-effects model.

A simple example (T/R-ratio 0.90, CV 0.25 – 0.50, 2×2×4 design targeted at power 0.80:

theta0          <- 0.90
CV              <- seq(0.25, 0.5, 0.05)
design          <- "2x2x4"
target          <- 0.80
reg1            <- reg_const(regulator = "EMA")
reg1$name <- "USER" reg1$est_method <- "ISC" # keep conditions but change from "ANOVA"
reg2            <- reg_const("USER", r_const = log(1.25) / 0.25,
CVswitch = 0.3, CVcap = Inf) # ANOVA
#####################################################
# Note: These are internal (not exported) functions #
# Use them only if you know what you are doing!     #
#####################################################
d.no   <- PowerTOST:::.design.no(design)
df1    <- PowerTOST:::.design.df(ades, robust = FALSE)
df2    <- PowerTOST:::.design.df(ades, robust = TRUE)
ns     <- nu <- data.frame(CV = CV, ABE.fix = NA_integer_,
ABE.mix = NA_integer_, ABEL.fix = NA_integer_,
ABEL.mix = NA_integer_, RSABE.fix = NA_integer_,
RSABE.mix = NA_integer_)
for (i in seq_along(CV)) {
ns$ABE.fix[i] <- sampleN.TOST(CV = CV[i], theta0 = theta0, targetpower = target, design = design, print = FALSE, details = FALSE)[["Sample size"]] n <- ns$ABE.fix[i]
nu$ABE.fix[i] <- eval(df1) ns$ABE.mix[i]   <- sampleN.TOST(CV = CV[i], theta0 = theta0,
targetpower = target, design = design,
robust = TRUE,
print = FALSE,
details = FALSE)[["Sample size"]]
n               <- ns$ABE.mix[i] nu$ABE.mix[i]   <- eval(df2)
ns$ABEL.fix[i] <- sampleN.scABEL(CV = CV[i], theta0 = theta0, targetpower = target, design = design, print = FALSE, details = FALSE)[["Sample size"]] n <- ns$ABEL.fix[i]
nu$ABEL.fix[i] <- eval(df1) ns$ABEL.mix[i]  <- sampleN.scABEL(CV = CV[i], theta0 = theta0,
targetpower = target, design = design,
regulator = reg1,
print = FALSE,
details = FALSE)[["Sample size"]]
n               <- ns$ABEL.mix[i] nu$ABEL.mix[i]  <- eval(df2)
ns$RSABE.fix[i] <- sampleN.scABEL(CV = CV[i], theta0 = theta0, targetpower = target, design = design, regulator = reg2, print = FALSE, details = FALSE)[["Sample size"]] n <- ns$RSABE.fix[i]
nu$RSABE.fix[i] <- eval(df1) ns$RSABE.mix[i] <- sampleN.RSABE(CV = CV[i], theta0 = theta0,
targetpower = target, design = design,
print = FALSE,
details = FALSE)[["Sample size"]]
n               <- ns$RSABE.mix[i] nu$RSABE.mix[i] <- eval(df2)
}
cat("Sample sizes\n")
print(ns, row.names = FALSE)
# Sample sizes
#    CV ABE.fix ABE.mix ABEL.fix ABEL.mix RSABE.fix RSABE.mix
#  0.25      28      30       28       30        28        28
#  0.30      40      40       34       36        28        32
#  0.35      52      54       34       36        24        28
#  0.40      68      68       30       32        22        24
#  0.45      84      84       28       30        20        24
#  0.50     100     102       28       30        20        22

For the mixed-effects models sample sizes are in general slightly larger.

cat("Degrees of freedom\n")
print(nu, row.names = FALSE)
# Degrees of freedom
#    CV ABE.fix ABE.mix ABEL.fix ABEL.mix RSABE.fix RSABE.mix
#  0.25      80      28       80       28        80        26
#  0.30     116      38       98       34        80        30
#  0.35     152      52       98       34        68        26
#  0.40     200      66       86       30        62        22
#  0.45     248      82       80       28        56        22
#  0.50     296     100       80       28        56        20

In the mixed-effects models we have fewer degrees of freedom (more effects are estimated).
Note that for the FDA’s RSABE always a mixed-effects model has to be employed and thus, the results for an ANOVA are given only for comparison.

# Power

Let’s change the point of view. As above, I assumed $$\small{CV=0.45}$$, $$\small{\theta_0=0.90}$$, and targeted ≥ 80% power. This time I explored how $$\small{CV}$$ different from my assumption affects power with the estimated sample size.

Additionally I assessed ‘pure’ SABE, i.e., without an upper cap of scaling and without the PE-constraint for the EMA’s conditions (switching $$\small{CV_\textrm{wR}=30\%}$$, regulatory constant $$\small{k=0.760}$$).

CV      <- 0.45
theta0  <- 0.90
target  <- 0.80
designs <- c("2x2x4", "2x2x3", "2x3x3")
method  <- c("ABE", "ABEL", "RSABE", "SABE")
# Pure SABE (only for comparison)
# No upper cap of scaling, no PE constraint
pure    <- reg_const("USER",
r_const  = 0.760,
CVswitch = 0.30,
CVcap    = Inf)
pure$pe_constr <- FALSE res <- data.frame(design = rep(designs, each = length(method)), method = method, n = NA, power = NA, CV0.40 = NA, CV0.50 = NA) for (i in 1:nrow(res)) { if (res$method[i] == "ABE") {
res[i, 3:4] <- sampleN.TOST(CV = CV, theta0 = theta0,
design = res$design[i], targetpower = target, print = FALSE)[7:8] res[i, 5] <- power.TOST(CV = 0.4, theta0 = theta0, n = res[i, 3], design = res$design[i])
res[i, 6]   <- power.TOST(CV = 0.5, theta0 = theta0,
n = res[i, 3],
design = res$design[i]) } if (res$method[i] == "ABEL") {
res[i, 3:4] <- sampleN.scABEL(CV = CV, theta0 = theta0,
design = res$design[i], targetpower = target, print = FALSE, details = FALSE)[8:9] res[i, 5] <- power.scABEL(CV = 0.4, theta0 = theta0, n = res[i, 3], design = res$design[i])
res[i, 6]   <- power.scABEL(CV = 0.5, theta0 = theta0,
n = res[i, 3],
design = res$design[i]) } if (res$method[i] == "RSABE") {
res[i, 3:4] <- sampleN.RSABE(CV = CV, theta0 = theta0,
design = res$design[i], targetpower = target, print = FALSE, details = FALSE)[8:9] res[i, 5] <- power.RSABE(CV = 0.4, theta0 = theta0, n = res[i, 3], design = res$design[i])
res[i, 6]   <- power.RSABE(CV = 0.5, theta0 = theta0,
n = res[i, 3],
design = res$design[i]) } if (res$method[i] == "SABE") {
res[i, 3:4] <- sampleN.scABEL(CV = CV, theta0 = theta0,
design = res$design[i], targetpower = target, regulator = pure, print = FALSE, details = FALSE)[8:9] res[i, 5] <- power.scABEL(CV = 0.4, theta0 = theta0, n = res[i, 3], design = res$design[i],
regulator = pure)
res[i, 6]   <- power.scABEL(CV = 0.5, theta0 = theta0,
n = res[i, 3],
design = res$design[i], regulator = pure) } } res[, 4:6] <- signif(res[, 4:6], 5) print(res, row.names = FALSE) # design method n power CV0.40 CV0.50 # 2x2x4 ABE 84 0.80569 0.87483 0.73700 # 2x2x4 ABEL 28 0.81116 0.78286 0.81428 # 2x2x4 RSABE 24 0.82450 0.80516 0.83001 # 2x2x4 SABE 28 0.81884 0.78415 0.84388 # 2x2x3 ABE 124 0.80012 0.87017 0.73102 # 2x2x3 ABEL 42 0.80017 0.77676 0.80347 # 2x2x3 RSABE 36 0.81147 0.79195 0.81888 # 2x2x3 SABE 42 0.80961 0.77868 0.83463 # 2x3x3 ABE 126 0.80570 0.87484 0.73701 # 2x3x3 ABEL 39 0.80588 0.77587 0.80763 # 2x3x3 RSABE 33 0.82802 0.80845 0.83171 # 2x3x3 SABE 39 0.81386 0.77650 0.84100 # Cave: very long runtime CV.fix <- 0.45 CV <- seq(0.35, 0.55, length.out = 201) theta0 <- 0.90 methods <- c("ABE", "ABEL", "RSABE", "SABE") clr <- c("red", "magenta", "blue", "#00800080") # Pure SABE (only for comparison) # No upper cup of scaling, no PE constraint pure <- reg_const("USER", r_const = 0.760, CVswitch = 0.30, CVcap = Inf) pure$pe_constr <- FALSE
#################
design  <- "2x2x4"
res1    <- data.frame(CV = CV,
method = rep(methods, each =length(CV)),
power = NA)
n.ABE   <- sampleN.TOST(CV = CV.fix, theta0 = theta0,
design = design,
print = FALSE)[["Sample size"]]
n.RSABE <- sampleN.RSABE(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.ABEL  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.SABE  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
regulator = pure,
details = FALSE)[["Sample size"]]
for (i in 1:nrow(res1)) {
if (res1$method[i] == "ABE") { res1$power[i] <- power.TOST(CV = res1$CV[i], theta0 = theta0, n = n.ABE, design = design) } if (res1$method[i] == "ABEL") {
res1$power[i] <- power.scABEL(CV = res1$CV[i], theta0 = theta0,
n = n.ABEL, design = design, nsims = 1e6)
}
if (res1$method[i] == "RSABE") { res1$power[i] <- power.RSABE(CV = res1$CV[i], theta0 = theta0, n = n.RSABE, design = design, nsims = 1e6) } if (res1$method[i] == "SABE") {
res1$power[i] <- power.scABEL(CV = res1$CV[i], theta0 = theta0,
n = n.ABEL, design = design,
regulator = pure, nsims = 1e6)
}
}
dev.new(width = 4.5, height = 4.5, record = TRUE)
par(mar = c(4, 3.3, 0.1, 0.1), cex.axis = 0.9)
plot(CV, res1$power[res1$method == "ABE"], type = "n", axes = FALSE,
ylim = c(0.65, 1), xlab = "CV", ylab = "")
abline(v = seq(0.35, 0.55, 0.05), lty = 3, col = "lightgrey")
abline(v = 0.45, lty = 2)
abline(h = axTicks(2, log = FALSE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.35, 0.55, 0.05))
axis(2, las = 1)
mtext("power", 2, line = 2.6)
legend("topright", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "n for CV = 45%")
lines(CV, res1$power[res1$method == "ABE"], lwd = 2, col = clr[1])
lines(CV, res1$power[res1$method == "ABEL"], lwd = 2, col = clr[2])
lines(CV, res1$power[res1$method == "RSABE"], lwd = 2, col = clr[3])
lines(CV, res1$power[res1$method == "SABE"], lwd = 2, col = clr[4])
box()
#################
design  <- "2x2x3"
res2    <- data.frame(CV = CV,
method = rep(methods, each =length(CV)),
power = NA)
n.ABE   <- sampleN.TOST(CV = CV.fix, theta0 = theta0,
design = design,
print = FALSE)[["Sample size"]]
n.RSABE <- sampleN.RSABE(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.ABEL  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.SABE  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
regulator = pure,
details = FALSE)[["Sample size"]]
for (i in 1:nrow(res2)) {
if (res2$method[i] == "ABE") { res2$power[i] <- power.TOST(CV = res2$CV[i], theta0 = theta0, n = n.ABE, design = design) } if (res2$method[i] == "ABEL") {
res2$power[i] <- power.scABEL(CV = res2$CV[i], theta0 = theta0,
n = n.ABEL, design = design, nsims = 1e6)
}
if (res2$method[i] == "RSABE") { res2$power[i] <- power.RSABE(CV = res2$CV[i], theta0 = theta0, n = n.RSABE, design = design, nsims = 1e6) } if (res2$method[i] == "SABE") {
res2$power[i] <- power.scABEL(CV = res2$CV[i], theta0 = theta0,
n = n.ABEL, design = design,
regulator = pure, nsims = 1e6)
}
}
plot(CV, res2$power[res2$method == "ABE"], type = "n", axes = FALSE,
ylim = c(0.65, 1), xlab = "CV", ylab = "")
abline(v = seq(0.35, 0.55, 0.05), lty = 3, col = "lightgrey")
abline(v = 0.45, lty = 2)
abline(h = axTicks(2, log = FALSE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.35, 0.55, 0.05))
axis(2, las = 1)
mtext("power", 2, line = 2.6)
legend("topright", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "n for CV = 45%")
lines(CV, res2$power[res2$method == "ABE"], lwd = 2, col = clr[1])
lines(CV, res2$power[res2$method == "ABEL"], lwd = 2, col = clr[2])
lines(CV, res2$power[res2$method == "RSABE"], lwd = 2, col = clr[3])
lines(CV, res2$power[res2$method == "SABE"], lwd = 2, col = clr[4])
box()
#################
design  <- "2x3x3"
res3    <- data.frame(CV = CV,
method = rep(methods, each =length(CV)),
power = NA)
n.ABE   <- sampleN.TOST(CV = CV.fix, theta0 = theta0,
design = design,
print = FALSE)[["Sample size"]]
n.RSABE <- sampleN.RSABE(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.ABEL  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
details = FALSE)[["Sample size"]]
n.SABE  <- sampleN.scABEL(CV = CV.fix, theta0 = theta0,
design = design, print = FALSE,
regulator = pure,
details = FALSE)[["Sample size"]]
for (i in 1:nrow(res3)) {
if (res3$method[i] == "ABE") { res3$power[i] <- power.TOST(CV = res3$CV[i], theta0 = theta0, n = n.ABE, design = design) } if (res3$method[i] == "ABEL") {
res3$power[i] <- power.scABEL(CV = res3$CV[i], theta0 = theta0,
n = n.ABEL, design = design, nsims = 1e6)
}
if (res3$method[i] == "RSABE") { res3$power[i] <- power.RSABE(CV = res3$CV[i], theta0 = theta0, n = n.RSABE, design = design, nsims = 1e6) } if (res3$method[i] == "SABE") {
res3$power[i] <- power.scABEL(CV = res3$CV[i], theta0 = theta0,
n = n.ABEL, design = design,
regulator = pure, nsims = 1e6)
}
}
plot(CV, res3$power[res3$method == "ABE"], type = "n", axes = FALSE,
ylim = c(0.65, 1), xlab = "CV", ylab = "")
abline(v = seq(0.35, 0.55, 0.05), lty = 3, col = "lightgrey")
abline(v = 0.45, lty = 2)
abline(h = axTicks(2, log = FALSE), lty = 3, col = "lightgrey")
axis(1, at = seq(0.35, 0.55, 0.05))
axis(2, las = 1)
mtext("power", 2, line = 2.6)
legend("topright", legend = methods, inset = 0.02, lwd = 2, cex = 0.9,
col = clr, box.lty = 0, bg = "white", title = "n for CV = 45%")
lines(CV, res3$power[res3$method == "ABE"], lwd = 2, col = clr[1])
lines(CV, res3$power[res3$method == "ABEL"], lwd = 2, col = clr[2])
lines(CV, res3$power[res3$method == "RSABE"], lwd = 2, col = clr[3])
lines(CV, res3$power[res3$method == "SABE"], lwd = 2, col = clr[4])
box()
par(op)

As expected, power of ABE is extremely dependent on the CV. Not surprising, because the acceptance limits are fixed at 80.00 – 125.00%.

As stated above, ideally reference-scaling should preserve power independent from the CV. If that would be the case, power would be a line parallel to the x-axis. However, the methods implemented by authorities are decision schemes (outlined in the articles about RSABE and ABEL), where certain conditions have to be observed. Therefore, beyond a maximum around 50%, power starts to decrease because the PE-constraint becomes increasingly important and – for ABEL – the upper cap of scaling sets in.

On the other hand, ‘pure’ SABE shows the unconstrained behavior of ABEL.

Let’s go deeper into the matter. As above but a wider range of CV values (0.3 – 1).

Here we see a clear difference between RSABE and ABEL. Although in both the PE-constraint has to be observed, in the former no upper cap of scaling is imposed and hence, power affected to a minor degree.
On the contrary, due to the upper upper cap of scaling in the latter, it behaves similarly to ABE with fixed limits of 69.84 – 143.19%.

Consequently, if the CV will be substantially larger than assumed, in ABEL power may be compromised.

Note also the huge gap between ABEL and ‘pure’ SABE. Whilst the PE-constraint is statistically not justified, it was introduced in all jurisdictions ‘for political reasons’.

1. There is no scientific basis or rationale for the point estimate recommendations
2. There is no belief that addition of the point estimate criteria will improve the safety of approved generic drugs
3. The point estimate recommendations are only “political” to give greater assurance to clinicians and patients who are not familiar (don’t understand) the statistics of highly variable drugs

# Statistical issues

If in Reference-Scaled Average Bioequivalence the realized $$\small{s_\textrm{wR}<0.294}$$, the study has to be assessed for Average Bioequivalence.

Over-speci­fi­ca­tion: More parameters than could be uniquely estimated.

Alas, the recommended mixed-effects model13 14 is over-specified for partial (aka semi-replicate) designs – since T is not repeated – and therefore, the software’s optimizer may fail to converge.15
Note that there are no problems in Average Bioequivalence with Expanding Limits because a simple ANOVA (all effects fixed and assuming $$\small{s_\textrm{wT}^2\equiv s_\textrm{wR}^2}$$) has to be used.16

Say, the $$\small{\log_{e}}$$-transformed AUC data are given by pk. Then the SAS code recommended by the FDA13 14 17 is:

PROC MIXED
data = pk;
CLASSES SEQ SUBJ PER TRT;
MODEL LAUC = SEQ PER TRT/ DDFM = SATTERTH;
RANDOM TRT/TYPE = FA0(2) SUB = SUBJ G;
REPEATED/GRP = TRT SUB = SUBJ;
ESTIMATE 'T vs. R' TRT 1 -1/CL ALPHA = 0.1;
ods output Estimates = unsc1;
title1 'unscaled BE 90% CI - guidance version';
title2 'AUC';
run;

data unsc1;
set unsc1;
unscabe_lower = exp(lower);
unscabe_upper = exp(upper);
run;


FA0(2) denotes a ‘No Diagonal Factor Analytic’ covariance structure with $$\small{q=2}$$ [sic] factors, i.e., $$\small{\frac{q}{2}(2t-q+1)+t=(2t-2+1)+t}$$ parameters, where the $$\small{i,j}$$ element is $$\small{\sum_{k=1}^{\textrm{min}(i,j,q=2)}\lambda_{ik}\lambda_{jk}}$$.18 The model has five variance components ($$\small{s_\textrm{wR}^2}$$, $$\small{s_\textrm{wT}^2}$$, $$\small{s_\textrm{bR}^2}$$, $$\small{s_\textrm{bT}^2}$$, and $$\small{cov(\textrm{bR},\textrm{bT})}$$), where the last three are combined to give the ‘subject-by-formulation interaction’ variance component as $$\small{s_\textrm{bR}^2+s_\textrm{bT}^2-cov(\textrm{bR},\textrm{bT})}$$.

That’s perfectly fine for all full replicate designs, i.e.,
TR|RT|TT|RR,19
TRT|RTR,
TRR|RTT,
TRTR|RTRT,
TRRT|RTTR,
TTRR|RRTT,
TRTR|RTRT|TRRT|RTTR, and
TTRRT|RTTR|TTRR|RRTT

where all components can be uniquely estimated.

However, in partial replicate designs, i.e.,
TRR|RTR|RRT13 14  and
TRR|RTR20 21

only R is repeated and consequently, just $$\small{s_\textrm{wR}^2}$$, $$\small{s_\textrm{bR}^2}$$, and the total variance of T ($$\small{s_\textrm{T}^2=s_\textrm{wT}^2+s_\textrm{bT}^2}$$) can be estimated.

In the partial replicate designs the optimizer tries hard to come up with the solution we requested.
In the ‘best’ case one gets the correct $$\small{s_\textrm{wR}^2}$$ and – rightly –
 NOTE: Convergence criteria met but final hessian is not positive definite.
Of course, $$\small{s_\textrm{wT}^2}$$ is nonsense (and differs between software packages…).
In the worst case the optimizer shows us the finger.
 WARNING: Did not converge.
 WARNING: Output 'Estimates' was not created.

Terrible consequence: Study performed, no result, the innocent statistician – falsely – blamed.
With an R script the PE can be obtaind but not the required 90% confidence interval.15

There are workarounds. In most cases FA0(1) converges and generally CSH (heterogeneous compound-sym­metry) or simply CS (compound-symmetry). Since these structures are not stated in the guidance(s), one risks a ‘Refuse-to-Receive’22 in the application. It must be mentioned that – in extremely rare cases – nothing helps!
Try to invoice the .

I simulated 10,000 partial replicate studies23 with $$\small{\theta_0=1}$$, $$\small{s_\textrm{wT}^2=s_\textrm{wR}^2=0.086}$$ $$\small{(CV_\textrm{w}\approx 29.97\%)}$$, $$\small{s_\textrm{bT}^2=s_\textrm{bR}^2=0.172}$$ $$\small{(CV_\textrm{b}\approx 43.32\%)}$$, $$\small{\rho=1}$$, i.e., homoscedasticity and no subject-by-formulation interaction. With $$\small{n=24}$$ subjects 82.38% power to demonstrate ABE.
Evaluation in Phoenix / WinNonlin,24 singularity tolerance and convergence criterion 10–12 (instead of 10–10), ite­ration limit 250 (instead of 50) and got: $\small{\begin{array}{lrrc}\hline \text{Convergence} & \texttt{FA0(2)} & \texttt{FA0(1)} & \texttt{CS}\\ \hline \text{Achieved} & 30.14\% & 99.97\% & 100\% \\ \text{Modif. Hessian} & 69.83\% & - & - \\ >\text{Iteration limit} & 0.03\% & 0.03\% & - \\\hline \end{array} \hphantom{a} \begin{array}{lrrc}\hline \text{Warnings} & \texttt{FA0(2)} & \texttt{FA0(1)} & \texttt{CS}\\ \hline \text{Neg. variance component} & 9.01\% & 3.82\% & 11.15\% \\ \text{Modified Hessian} & 68.75\% & - & - \\ \text{Both} & 2.22\% & 0.06\% & - \\\hline \end{array}}$

As long as we achieve convergence, it doesn’t matter. Perhaps as long as the data set is balanced and/or does not contain ‘outliers’, all is good. I compared the results obtained with FA0(1) and CS to the guidances’ FA0(2). 80.95% of simulated studies passed ABE. $\small{\begin{array}{lcrcrrrr} \hline & s_\textrm{wR}^2 & \textrm{RE (%)} & s_\textrm{bR}^2 & \textrm{RE (%)} & \text{PE}\;\;\; & \textrm{90% CL}_\textrm{lower} & \textrm{90% CL}_\textrm{upper}\\ \hline \text{Min.} & 0.020100 & -76.6\% & 0.00005 & -100.0\% & 75.59 & 65.96 & 84.88\\ \text{Q I} & 0.067613 & -21.4\% & 0.12461 & -27.6\% & 95.14 & 83.84 & 107.59\\ \text{Med.} & 0.083282 & -3.2\% & 0.16537 & -3.9\% & 99.95 & 88.29 & 113.15\\ \text{Q III} & 0.102000 & -18.6\% & 0.21408 & +24.5\% & 105.00 & 92.92 & 119.15\\ \text{Max.} & 0.199367 & +131.8\% & 0.51370 & +198.7\% & 135.92 & 123.82 & 149.75\\\hline \end{array}}$ Up to the 4th decimal (rounded to percent, i.e., 6–7 significant digits) the CIs were identical in all cases. Only when I looked at the 5th decimal for both covariance structures, ~1/500 differed (the CI was wider than with FA0(2) and hence, more conservative). Since all guidelines require rounding to the 2nd decimal, that’s not relevant anyhow.

One example where the optimizer was in deep trouble with FA0(2), FA0(1), and CSH (all with singularity tolerance and convergence criterion 10–15). $\small{\begin{array}{rccccc} \hline \text{Iter}_\textrm{max} & s_\textrm{wR}^2 & \textrm{-2REML LL} & \textrm{AIC} & df & \textrm{90% CI}\\ \hline 50 & 0.084393 & 39.368 & 61.368 & 22.10798 & \text{82.212 -- 111.084}\\ 250 & 0.085094 & 39.345 & 61.345 & 22.18344 & \text{82.223 -- 111.070}\\ \text{1,250} & 0.085271 & 39.339 & 61.339 & 22.20523 & \text{82.225 -- 111.066}\\ \text{6,250} & 0.085309 & 39.338 & 61.338 & 22.20991 & \text{82.226 -- 111.066}\\ \text{31,250} & 0.085317 & 39.338 & 61.338 & 22.21032 & \text{82.226 -- 111.066}\\\hline \end{array}}$

A warning was thrown in all cases:
 Failed to converge in allocated number of iterations. Output is suspect.
 Negative final variance component. Consider omitting this VC structure.

Note that $$\small{s_\textrm{wR}^2}$$ increases with the number of iterations, which is over-compensated by increasing degrees of freedom and hence, the CI narrows.
Note also that SAS forces negative variance components to zero – which is questionable as well.

However, with CS (compound-symmetry) convergence was achieved after just four (‼) iterations without any warnings: $$\small{s_\textrm{wR}^2=0.089804}$$, $$\small{df=22.32592}$$, $$\small{\textrm{90% CI}=\text{82.258 -- 111.023}}$$.

Welcome to the hell of mixed-effects modeling. Now I understand why Health Canada requires that the optimizer’s constraints are stated in the SAP.25

If you wonder whether a 3-period full replicate design is acceptable for agencies:

• According to the EMA it is indeed.26

• Already in 2001 the FDA recommended the 2-sequence 4-period full replicate design TRTR|RTRT but stated also:17

»Other replicated crossover designs are possible.
For example, a three-period design
TRT|RTR could be used.
[…] the two-sequence, three-period design TRR|RTT is thought
to be optimal among three-period replicated crossover designs.
«

The guidance is in force for 21 years and the lousy partial replicate is not mentioned at all…

• It is unclear whether the problematic 3-sequence partial replicate design mentioned more recently13 14  is mandatory or just given as an example. Does the overarching guidance about statistics in bioequivalence17 (which is final) overrule later ones, which are only drafts? If in doubt, initiate a ‘Controlled Corres­pon­dence’27 beforehand. Good luck!28

# Study costs

Power (and hence, the sample size) depends on the number of treatments – the smaller sample size in replicate designs is compensated by more administrations. For ABE costs of a replicate design are similar to the common 2×2×2 crossover design. If the sample size of a 2×2×2 design is $$\small{n}$$, then the sample size for a 4-period replicate design is $$\small{^1/_2\,n}$$ and for a 3-period replicate design $$\small{^3/_4\,n}$$.
Nevertheless, smaller sample sizes come with a price. We have the same number of samples to analyze and study costs are driven to a good part by bioanalytics.29 We will save costs due to less pre-/post-study exams but have to pay a higher subject remuneration (more hospitalizations and blood samples). If applicable (depending on the drug): Increased costs for in-study safety and/or PD measurements.
Furthermore, one must be aware that more periods / washout phases increase the chance of dropouts.

Let’s compare study costs (approximated by the number of treatments) of 3-period replicate designs to 4-period replicate designs planned for ABEL and RSABE. I assumed a T/R-ratio of 0.90, a CV-range of 30 – 65%, and targeted ≥ 80% power.

CV      <- seq(0.30, 0.65, 0.05)
theta0  <- 0.90
target  <- 0.80
designs <- c("2x2x4", "2x2x3", "2x3x3")
res1    <- data.frame(design = designs,
CV = rep(CV, each = length(designs)),
n = NA_integer_, n.trt = NA_integer_,
costs = "100% * ")
for (i in 1:nrow(res1)) {
res1$n[i] <- sampleN.scABEL(CV = res1$CV[i], theta0 = theta0,
targetpower = target,
design = res1$design[i], print = FALSE, details = FALSE)[["Sample size"]] n.per <- as.integer(substr(res1$design[i], 5, 5))
res1$n.trt[i] <- n.per * res1$n[i]
}
ref1 <- res1[res1$design == "2x2x4", c(1:2, 4)] for (i in 1:nrow(res1)) { if (!res1$design[i] %in% ref1$design) { res1$costs[i] <- sprintf("%.0f%%   ", 100 * res1$n.trt[i] / ref1$n.trt[ref1$CV == res1$CV[i]])
}
}
names(res1)[4:5] <- c("treatments", "rel. costs")
cat("ABEL (EMA and others)\n")
print(res1, row.names = FALSE)
# ABEL (EMA and others)
#  design   CV  n treatments rel. costs
#   2x2x4 0.30 34        136    100% *
#   2x2x3 0.30 50        150    110%
#   2x3x3 0.30 54        162    119%
#   2x2x4 0.35 34        136    100% *
#   2x2x3 0.35 50        150    110%
#   2x3x3 0.35 48        144    106%
#   2x2x4 0.40 30        120    100% *
#   2x2x3 0.40 46        138    115%
#   2x3x3 0.40 42        126    105%
#   2x2x4 0.45 28        112    100% *
#   2x2x3 0.45 42        126    112%
#   2x3x3 0.45 39        117    104%
#   2x2x4 0.50 28        112    100% *
#   2x2x3 0.50 42        126    112%
#   2x3x3 0.50 39        117    104%
#   2x2x4 0.55 30        120    100% *
#   2x2x3 0.55 44        132    110%
#   2x3x3 0.55 42        126    105%
#   2x2x4 0.60 32        128    100% *
#   2x2x3 0.60 48        144    112%
#   2x3x3 0.60 48        144    112%
#   2x2x4 0.65 36        144    100% *
#   2x2x3 0.65 54        162    112%
#   2x3x3 0.65 54        162    112%

In any case 3-period designs are more costly than 4-period full replicate designs. However, in the latter dropouts are more likely and the sample size has to be adjusted accordingly. Given that, the difference diminishes. Since there are no convergence issues in ABEL, the partial replicate can be used.

Agencies are only interested in $$\small{CV_\textrm{wR}}$$.

However, I prefer one of the 3-period full replicate designs due to the additional information about $$\small{CV_\textrm{wT}}$$.

CV      <- seq(0.30, 0.65, 0.05)
theta0  <- 0.90
target  <- 0.80
designs <- c("2x2x4", "2x2x3", "2x3x3")
res2    <- data.frame(design = designs,
CV = rep(CV, each = length(designs)),
n = NA_integer_, n.trt = NA_integer_,
costs = "100% * ")
for (i in 1:nrow(res1)) {
res2$n[i] <- sampleN.RSABE(CV = res2$CV[i], theta0 = theta0,
targetpower = target,
design = res2$design[i], print = FALSE, details = FALSE)[["Sample size"]] n.per <- as.integer(substr(res1$design[i], 5, 5))
res2$n.trt[i] <- n.per * res2$n[i]
}
ref2 <- res2[res2$design == "2x2x4", c(1:2, 4)] for (i in 1:nrow(res1)) { if (!res2$design[i] %in% ref2$design) { res2$costs[i] <- sprintf("%.0f%%   ", 100 * res2$n.trt[i] / ref2$n.trt[ref2$CV == res2$CV[i]])
}
}
names(res2)[4:5] <- c("treatments", "rel. costs")
cat("RSABE (U.S. FDA and China CDE)\n")
print(res2, row.names = FALSE)
# RSABE (U.S. FDA and China CDE)
#  design   CV  n treatments rel. costs
#   2x2x4 0.30 32        128    100% *
#   2x2x3 0.30 46        138    108%
#   2x3x3 0.30 45        135    105%
#   2x2x4 0.35 28        112    100% *
#   2x2x3 0.35 42        126    112%
#   2x3x3 0.35 39        117    104%
#   2x2x4 0.40 24         96    100% *
#   2x2x3 0.40 38        114    119%
#   2x3x3 0.40 33         99    103%
#   2x2x4 0.45 24         96    100% *
#   2x2x3 0.45 36        108    112%
#   2x3x3 0.45 33         99    103%
#   2x2x4 0.50 22         88    100% *
#   2x2x3 0.50 34        102    116%
#   2x3x3 0.50 30         90    102%
#   2x2x4 0.55 22         88    100% *
#   2x2x3 0.55 34        102    116%
#   2x3x3 0.55 30         90    102%
#   2x2x4 0.60 24         96    100% *
#   2x2x3 0.60 36        108    112%
#   2x3x3 0.60 33         99    103%
#   2x2x4 0.65 24         96    100% *
#   2x2x3 0.65 36        108    112%
#   2x3x3 0.65 33         99    103%

In almost all cases 3-period designs are more costly than 4-period full replicate designs. However, in the latter dropouts are more likely and the sample size has to be adjusted accordingly. Given that, the difference diminishes. Due to the convergence issues in ABE (mandatory, if the realized $$\small{s_\textrm{wR}<0.294}$$), I strongly recommend to avoid the partial replicate design and opt for one of the 3-period full replicate designs instead.

# Pros and Cons

From a statistical perspective, replicate designs are preferrable over the 2×2×2 crossover design. If we observe discordant30 outliers in the latter, we cannot distinguish between lack of compliance (the subject didn’t take the drug), a product failure, and a subject-by-formulation interaction (the subject belongs to a subpopulation).

A member of the EMA’s PKWP once told me that he would like to see all studies performed in a replicate design – regardless whether the drug / drug product is highly variable or not. One of the rare cases where we were of the same opinion.31

We design studies always for the worst case combination, i.e., based on the PK metric requiring the largest sample size. In jurisdictions accepting reference-scaling only for Cmax (e.g. by ABEL) the sample size is driven by AUC.

metrics <- c("Cmax", "AUCt", "AUCinf")
alpha   <- 0.05
CV      <- c(0.45, 0.34, 0.36)
theta0  <- rep(0.90, 3)
theta1  <- 0.80
theta2  <- 1 / theta1
target  <- 0.80
design  <- "2x2x4"
plan    <- data.frame(metric = metrics,
method = c("ABEL", "ABE", "ABE"),
CV = CV, theta0 = theta0,
L = 100*theta1, U = 100*theta2,
n = NA, power = NA)
for (i in 1:nrow(plan)) {
if (plan$method[i] == "ABEL") { plan[i, 5:6] <- round(100*scABEL(CV = CV[i]), 2) plan[i, 7:8] <- signif( sampleN.scABEL(alpha = alpha, CV = CV[i], theta0 = theta0[i], theta1 = theta1, theta2 = theta2, targetpower = target, design = design, details = FALSE, print = FALSE)[8:9], 4) }else { plan[i, 7:8] <- signif( sampleN.TOST(alpha = alpha, CV = CV[i], theta0 = theta0[i], theta1 = theta1, theta2 = theta2, targetpower = target, design = design, print = FALSE)[7:8], 4) } } txt <- paste0("Sample size based on ", plan$metric[plan$n == max(plan$n)], ".\n")
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
#    AUCt    ABE 0.34    0.9 80.00 125.00 50 0.8055
#  AUCinf    ABE 0.36    0.9 80.00 125.00 56 0.8077
# Sample size based on AUCinf.
If the study is performed with 56 subjects and all assumed values are realized, post hoc power will be 0.9666 for Cmax. I have seen deficiency letters by regulatory assessors asking for a
»justification of too high power for Cmax«.

As shown in the article about ABEL, we get an incentive in the sample size if $$\small{CV_\textrm{wT}<CV_\textrm{wR}}$$. However, this does not help if reference-scaling is not acceptable (say, for the AUC in most jurisdictions) because the conventional model for ABE assumes homoscedasticity ($$\small{CV_\textrm{wT}\equiv CV_\textrm{wR}}$$).

theta0        <- 0.90
design        <- "2x2x4"
CVw           <- 0.36 # AUC - no reference-scaling
# variance-ratio 0.80: T lower than R
CV            <- signif(CVp2CV(CV = CVw, ratio = 0.80), 5)
# 'switch off' all scaling conditions of ABEL
reg           <- reg_const("USER", r_const = 0.76,
CVswitch = Inf, CVcap = Inf)
reg$pe_constr <- FALSE res <- data.frame(variance = c("homoscedastic", "heteroscedastic"), CVwT = c(CVw, CV[1]), CVwR = c(CVw, CV[2]), CVw = rep(CVw, 2), n = NA) res$n[1]      <- sampleN.TOST(CV = CVw, theta0 = theta0,
design = design,
print = FALSE)[["Sample size"]]
res$n[2] <- sampleN.scABEL(CV = CV, theta0 = theta0, design = design, regulator = reg, details = FALSE, print = FALSE)[["Sample size"]] print(res, row.names = FALSE) # variance CVwT CVwR CVw n # homoscedastic 0.36000 0.36000 0.36 56 # heteroscedastic 0.33824 0.38079 0.36 56 Although we know that the test has a lower within-subject $$\small{CV}$$ than the reference, this information is ignored and the (pooled) within-subject $$\small{CV_\textrm{w}}$$ used. ## Pros • Statistically sound. Estimation of CVwR (and in full replicate designs additionally of CVwT) is possible. The additional information is welcomed side effect. • Mandatory for ABEL and RSABE. Smaller sample sizes than for ABE. • ‘Outliers’ can be better assessed than in the 2×2×2 crossover design. • In the 2×2×2 crossover this will be rather difficult (exclusion of subjects based on statistical and/or PK grounds alone is not acceptable). • For ABEL assessment of ‘outliers’ (of the reference treatment only) is part of the recommended procedure.32 ## Cons • A larger sample size adjustment according to the anticipated dropout-rate required than in a 2×2×2 crossover design due to three or four periods instead of two.33 • Contrary to ABE – where the limits are based on Δ according to (1) – in practice the scaled limits of SABE (2) are calculated based on the realized swR. • Without access to the study report, Δ cannot be re-calculated. This is an unsatisfactory situation for physicians, pharmacists, and patients alike. • The elephant in the room: Potential inflation of the Type I Error (patient’s risk) in RSABE (if CVwR < 30%) and in ABEL (if ~25% < CVwR < ~42%). This issue is covered in another article. # Uncertain CVwR An intriguing statement of the EMA’s Pharmacokinetics Working Party. Suitability of a 3-period replicate design scheme for the demonstration of within-subject variability for Cmax The question raised asks if it is possible to use a design where subjects are randomised to receive treatments in the order of TRT or RTR. This design is not considered optimal […]. However, it would provide an estimate of the within subject variability for both test and reference products. As this estimate is only based on half of the subjects in the study the uncertainty associated with it is higher than if a RRT/RTR/TRR design is used and therefore there is a greater chance of incorrectly concluding a reference product is highly variable if such a design is used. The CHMP bioequivalence guideline requires that at least 12 patients are needed to provide data for a bioequivalence study to be considered valid, and to estimate all the key parameters. Therefore, if a 3-period replicate design, where treatments are given in the order TRT or RTR, is to be used to justify widening of a confidence interval for Cmax then it is considered that at least 12 patients would need to provide data from the RTR arm. This implies a study with at least 24 patients in total would be required if equal number of subjects are allocated to the 2 treatment sequences. EMA (2015)34 I fail to find a statement in the guideline35 that $$\small{CV_\textrm{wR}}$$ is a ‘key parameter’ – only that »The number of evaluable subjects in a bioequivalence study should not be less than 12.« However, in sufficiently powered studies such a situation is extremely unlikely (dropout-rate ≥ 42%).36 Let’s explore the uncertainty of $$\small{CV_\textrm{wR}=30\%}$$ based on its 95% confidence interval in two scenarios: 1. No dropouts. In the partial replicate design all subjects provide data for the estimation of CVwR. In full replicate designs only half of the subjects provide this information. 2. Extreme dropout-rates. Only twelve subjects remain in R-replicated sequence(s). # CI of the CV for sample sizes of replicate designs # (theta0 0.90, target power 0.80) CV <- 0.30 des <- c("2x3x3", # 3-sequence 3-period (partial) replicate design "2x2x3", # 2-sequence 3-period full replicate designs "2x2x4") # 2-sequence 4-period full replicate designs type <-c("partial", rep("full", 2)) seqs <- c("TRR|RTR|RTR", "TRT|RTR ", "TRTR|RTRT ") res <- data.frame(scenario = c(rep(1, 3), rep(2, 3)), design = rep(des, 2), type = rep(type, 2), sequences = rep(seqs, 2), n = c(rep(NA, 3), rep(0, 3)), RR = c(rep(NA, 3), rep(0, 3)), df = NA, lower = NA, upper = NA, width = NA) for (i in 1:nrow(res)) { if (is.na(res$n[i])) {
res$n[i] <- sampleN.scABEL(CV = CV, design = res$design[i],
details = FALSE, print = FALSE)[["Sample size"]]
if (res$design[i] == "2x2x3") { res$RR[i] <- res$n[i] / 2 }else { res$RR[i] <- res$n[i] } } if (i > 3) { if (res$design[i] == "2x3x3") {
res$n[i] <- res$n[i-3] - 12
res$RR[i] <- 12 # only 12 eligible subjects in sequence RTR }else { res$n[i]  <- 12       # min. sample size
res$RR[i] <- res$n[i] # CVwR can be estimated
}
}
res$df[i] <- res$RR[i] - 2
res[i, 8:9] <- CVCL(CV = CV, df = res$df[i], side = "2-sided", alpha = 0.05) res[i, 10] <- res[i, 9] - res[i, 8] } res[, 8] <- sprintf("%.1f%%", 100 * res[, 8]) res[, 9] <- sprintf("%.1f%%", 100 * res[, 9]) res[, 10] <- sprintf("%.1f%%", 100 * res[, 10]) names(res)[1] <- "sc." # Rows 1-2: Sample sizes for target power # Rows 3-4: Only 12 eligible subjects to estimate CVwR print(res, row.names = FALSE) # sc. design type sequences n RR df lower upper width # 1 2x3x3 partial TRR|RTR|RTR 54 54 52 25.0% 37.6% 12.5% # 1 2x2x3 full TRT|RTR 50 25 23 23.1% 43.0% 19.9% # 1 2x2x4 full TRTR|RTRT 34 34 32 23.9% 40.3% 16.4% # 2 2x3x3 partial TRR|RTR|RTR 42 12 10 20.7% 55.1% 34.4% # 2 2x2x3 full TRT|RTR 12 12 10 20.7% 55.1% 34.4% # 2 2x2x4 full TRTR|RTRT 12 12 10 20.7% 55.1% 34.4% Given, the CI of the $$\small{CV_\textrm{wR}}$$ in the partial replicate design is narrower than in a three period full replicate design. Is that really relevant, esp. since only twelve eligible subjects in the RTR-sequence are acceptable to provide a ‘valid’ estimate? Obviously the EMA’s PKWP is aware of the uncertainty of the realized $$\small{CV_\textrm{wR}}$$, which may lead to a misclassification (the study is assessed by ABEL although the drug / drug product is not highly variable) and hence, a potentially inflated Type I Error (TIE, patient’s risk). The partial replicate has – given studies with the same power – the largest degrees of freedom and hence, leads to the lowest TIE.37 However, it does not magically disappear. Such a misclassification may also affect the Type II Error (producer’s risk). If the realized $$\small{CV_\textrm{wR}}$$ is lower than assumed in sample size estimation, less expansion can be applied and the study will be underpowered. Of course, that’s not a regulatory concern. design <- "2x2x4" theta0 <- 0.90 # asumed T/R-atio CV.ass <- 0.35 # assumed CV CV.real <- c(CV.ass, 0.30, 0.40) # realized CV # sample size based on assumed T/R-ratio and CV, targeted at ≥ 80% power res <- data.frame(CV.ass = CV.ass, n = sampleN.scABEL(CV = CV.ass, design = design, theta0 = theta0, details = FALSE, print = FALSE)[["Sample size"]], CV.real = CV.real, L = NA_real_, U = NA_real_, TIE = NA_real_, TIIE = NA_real_) for (i in 1:nrow(res)) { res$L[i]    <- scABEL(CV = res$CV.real[i])[["lower"]] res$U[i]    <- scABEL(CV = res$CV.real[i])[["upper"]] res$TIE[i]  <- power.scABEL(CV = res$CV.real[i], design = design, theta0 = res$U[i], n = res$n[i]) res$TIIE[i] <- 1 - power.scABEL(CV = res$CV.real[i], design = design, theta0 = theta0, n = res$n[i])
}
res$CV.ass <- sprintf("%.0f%%", 100 * res$CV.ass)
res$CV.real <- sprintf("%.0f%%", 100 * res$CV.real)
res$L <- sprintf("%.2f%%", 100 * res$L)
res$U <- sprintf("%.2f%%", 100 * res$U)
res$TIE <- sprintf("%.5f", res$TIE)
res$TIIE <- sprintf("%.4f", res$TIIE)
names(res)[c(1, 3)] <- c("assumed", "realized")
print(res, row.names = FALSE)
#  assumed  n realized      L       U     TIE   TIIE
#      35% 34      35% 77.23% 129.48% 0.06557 0.1882
#      35% 34      30% 80.00% 125.00% 0.08163 0.1972
#      35% 34      40% 74.62% 134.02% 0.05846 0.1535

I recommend the article about power analysis (sections ABEL and RSABE).

Of note, if there are no / few dropouts, the estimated $$\small{CV_\textrm{wR}}$$ in 4-period full replicate designs carries a larger uncertainty due to its lower sample size and therefore, less degrees of freedom. If the PKWP is concerned about an ‘uncertain’ estimate, why is this design given as an example?16 38 Many studies are performed in this design and are accepted by agencies.

Since for RSABE generally smaller sample sizes are required than for ABEL, the estimated $$\small{CV_\textrm{wR}}$$ is more uncertain in the former.

# Cave: very long runtime
theta0 <- 0.90
target <- 0.80
CV     <- seq(0.3, 0.5, 0.00025)
x      <- seq(0.3, 0.5, 0.05)
des    <- c("2x3x3", # 3-sequence 3-period (partial) replicate design
"2x2x3", # 2-sequence 3-period full replicate designs
"2x2x4") # 2-sequence 4-period full replicate designs
RSABE  <- ABEL <- data.frame(design = rep(des, each = length(CV)),
n = NA, RR = NA, df = NA, CV = CV,
lower = NA, upper = NA)
for (i in 1:nrow(ABEL)) {
RSABE$n[i] <- sampleN.RSABE(CV = RSABE$CV[i], theta0 = theta0,
targetpower = target,
design = RSABE$design[i], details = FALSE, print = FALSE)[["Sample size"]] if (RSABE$design[i] == "2x2x3") {
RSABE$RR[i] <- RSABE$n[i] / 2
}else {
RSABE$RR[i] <- RSABE$n[i]
}
RSABE$df[i] <- RSABE$RR[i] - 2
RSABE[i, 6:7] <- CVCL(CV = RSABE$CV[i], df = RSABE$df[i],
side = "2-sided", alpha = 0.05)
ABEL$n[i] <- sampleN.scABEL(CV = ABEL$CV[i], theta0 = theta0,
targetpower = target,
design = ABEL$design[i], details = FALSE, print = FALSE)[["Sample size"]] if (ABEL$design[i] == "2x2x3") {
ABEL$RR[i] <- ABEL$n[i] / 2
}else {
ABEL$RR[i] <- ABEL$n[i]
}
ABEL$df[i] <- ABEL$RR[i] - 2
ABEL[i, 6:7] <- CVCL(CV = ABEL$CV[i], df = ABEL$df[i],
side = "2-sided", alpha = 0.05)
}
ylim <- range(c(RSABE[6:7], ABEL[6:7]))
col  <- c("blue", "red", "magenta")
leg  <- c("2×3×3 (partial)", "2×2×3 (full)", "2×2×4 (full)")
dev.new(width = 4.5, height = 4.5, record = TRUE)
par(mar = c(4, 4.1, 0.2, 0.1), cex.axis = 0.9)
plot(CV, rep(0.3, length(CV)), type = "n", ylim = ylim, log = "xy",
xlab = expression(italic(CV)[wR]),
ylab = expression(italic(CV)[wR]*"  (95% confidence interval)"),
axes = FALSE)
grid()
abline(h = 0.3, col = "lightgrey", lty = 3)
axis(1, at = x)
axis(2, las = 1)
axis(2, at = c(0.3, 0.5), las = 1)
lines(CV, CV, col = "darkgrey")
legend("topleft", bg = "white", box.lty = 0, title = "replicate designs",
legend = leg, col = col, lwd = 2, seg.len = 2.5, cex = 0.9,
y.intersp = 1.25)
box()
for (i in seq_along(des)) {
lines(CV, RSABE$lower[RSABE$design == des[i]], col = col[i], lwd = 2)
lines(CV, RSABE$upper[RSABE$design == des[i]], col = col[i], lwd = 2)
y <- RSABE$upper[signif(RSABE$CV, 4) %in% x & RSABE$design == des[i]] n <- RSABE$n[signif(RSABE$CV, 4) %in% x & RSABE$design == des[i]]
# sample sizes at CV = x
shadowtext(x, y, labels = n, bg = "white", col = "black", cex = 0.75)
}
plot(CV, rep(0.3, length(CV)), type = "n", ylim = ylim, log = "xy",
xlab = expression(italic(CV)[wR]),
ylab = expression(italic(CV)[wR]*"  (95% confidence interval)"),
axes = FALSE)
grid()
abline(h = 0.3, col = "lightgrey", lty = 3)
axis(1, at = x)
axis(2, las = 1)
axis(2, at = c(0.3, 0.5), las = 1); box()
lines(CV, CV, col = "darkgrey")
legend("topleft", bg = "white", box.lty = 0, title = "replicate designs",
legend = leg, col = col, lwd = 2, seg.len = 2.5, cex = 0.9,
y.intersp = 1.25)
box()
for (i in seq_along(des)) {
lines(CV, ABEL$lower[ABEL$design == des[i]], col = col[i], lwd = 2)
lines(CV, ABEL$upper[ABEL$design == des[i]], col = col[i], lwd = 2)
y <- ABEL$upper[signif(ABEL$CV, 4) %in% x & ABEL$design == des[i]] n <- ABEL$n[signif(ABEL$CV, 4) %in% x & ABEL$design == des[i]]
# sample sizes at CV = x
shadowtext(x, y, labels = n, bg = "white", col = "black", cex = 0.75)
}
par(op)
cat("RSABE\n"); print(RSABE[signif(RSABE$CV, 4) %in% x, ], row.names = FALSE) cat("ABEL\n"); print(ABEL[signif(ABEL$CV, 4) %in% x, ], row.names = FALSE)

That’s interesting. Say, we assumed $$\small{CV_\textrm{wR}=37\%}$$, a T/R-ratio 0.90 targeted at ≥ 80% power in a 4-period full replicate design intended for ABEL. We performed the study with 32 subjects. The 95% CI of the $$\small{CV_\textrm{wR}}$$ is 29.2% (no expansion, assessment for ABE) to 50.8% (already above the upper cap of 50%).
Disturbing, isn’t it?

Interlude 2

If you wonder why the confidence intervals are asymmetric ($$\small{CL_\textrm{upper}-CV_\textrm{wR}>CV_\textrm{wR}-CL_\textrm{lower}}$$): The $$\small{100\,(1-\alpha)}$$ confidence interval of the $$\small{CV_\textrm{wR}}$$ is obtained via the $$\small{\chi^2}$$-distribution of its error variance $$\small{s_\textrm{wR}^2}$$ with $$\small{n-2}$$ degrees of freedom. $\begin{matrix}\tag{3} s_\textrm{wR}^2=\log_{e}(CV_\textrm{wR}+1)\\ L=\frac{(n-1)\,s_\textrm{wR}^2}{\chi_{\alpha/2,\,n-2}^{2}}\leq s_\textrm{wR}^2\leq\frac{(n-1)\,s_\textrm{wR}^2}{\chi_{1-\alpha/2,\,n-2}^{2}}=U\\ \left\{CL_\textrm{lower},\;CL_\textrm{upper}\right\}=\left\{\sqrt{\exp(L)-1},\sqrt{\exp(U)-1}\right\} \end{matrix}$

The $$\small{\chi^2}$$-distribution is skewed to the right. Since the width of the confidence interval for a given $$\small{CV_\textrm{wR}}$$ depends on the degrees of freedom, it implies a more precise estimate in larger studies, which will be required for relatively low variabilities (least scaling).
In the example above the width of the CI in the partial replicate design is for RSABE 0.139 (n 45) at $$\small{CV_\textrm{wR}=0.30}$$ and 0.322 (n 30) at $$\small{CV_\textrm{wR}=0.50}$$. For ABEL the widths are 0.125 (n 54) and 0.273 (n 39).

# Postscript

Regularly I’m asked whether it is possible to use an adaptive Two-Stage Design (TSD) for ABEL or RSABE.

Whereas for ABE it is possible in principle (no method for replicate designs is published so far – only for 2×2×2 crossovers39), for SABE the answer is no. Contrary to ABE, where power and the Type I Error can be calculated by analytical methods, in SABE we have to rely on simulations. We would have to find a suitable adjusted $$\small{\alpha}$$ and demonstrate beforehand that the patient’s risk will be controlled.

For the implemented regulatory frameworks the sample size estimation requires 105 simulations to obtain a stable result (see here and there). Since the convergence of the empiric Type I Error is poor, we need 106 simulations. Combining that with a reasonably narrow grid of possible $$\small{n_1}$$ / $$\small{CV_\textrm{wR}}$$-combinations,40 we end up with with 1013 – 1014 simulations. I don’t see how that can be done in the near future, unless one has access to a massi­ve­ly parallel supercomputer. I made a quick estimation for my fast workstation: ~60 years running 24/7…

As outlined above, SABE is rather insensitive to the CV. Hence, the main advantage of TSDs over fixed sample designs in ABE (re-estimating the sample size based on the CV observed in the first stage) is simply not relevant. Fully adaptive methods for the 2×2×2 crossover allow also to adjust for the PE observed in the first stage. Here it is not possible. If you are concerned about the T/R-ratio, perform a (reasonably large!)41 pilot study and – even if the T/R-ratio looks promising – plan for a ‘worse’ one since it is not stable between studies.

# Post postscript

Let’s recap the basic mass balance equation of PK: $\small{F\cdot D=V\cdot k\,\cdot\int_{0}^{\infty}C(t)\,dt=CL\cdot AUC_{0-\infty}}\tag{4}$ We assess Bioequivalence by comparative Bioavailability, i.e., $\small{\frac{F_{\textrm{T}}}{F_{\textrm{R}}}\approx \frac{AUC_{\textrm{T}}}{AUC_{\textrm{R}}}}\tag{5}$ That’s only part of the story because – based on $$\small{(4)}$$ – actually $\small{AUC_{\textrm{T}}=\frac{F_\textrm{T}\cdot D_\textrm{T}}{CL}\;\land\;AUC_{\textrm{R}}=\frac{F_\textrm{R}\cdot D_\textrm{R}}{CL}}\tag{6}$ Since an adjustment for measured potency is generally not acceptable, we have to assume that the true contents equal the declared ones and further $\small{D_\textrm{T}\equiv D_\textrm{R}}\tag{7}$ This allows us to eliminate the doses from $$\small{(6)}$$; however, we still have to assume no inter-occasion variability of clearances ($$\small{CL=\textrm{const}}$$) in order to arrive at $$\small{(5)}$$.

Great, but is that true‽ If we have to deal with a HVD, the high variability is an intrinsic property of the drug itself (not the formulation). In BE were are interested in detecting potential differences of formulations, right? Since we ignored the – possibly unequal – clearances, all unexplained variability goes straight to the residual error, results in a large within-subject variance and hence, a wide confidence interval. In other words, the formulation is punished for a crime that clearance committed.

Can we do anything against it – apart from reference-scaling? We know that $\small{k=CL\big{/}V}\tag{8}$ In cross-over designs the volume of distribution of healthy subjects likely shows limited inter-occasion variability. Therefore, we can drop the volume of distribution and approximate the effect of $$\small{CL}$$ by $$\small{k}$$. This leads to $\small{\frac{F_{\textrm{T}}}{F_{\textrm{R}}}\sim \frac{AUC_{\textrm{T}}\cdot k_{\textrm{T}}}{AUC_{\textrm{R}}\cdot k_{\textrm{R}}}}\tag{9}$ A variant of $$\small{(9)}$$ – using $$\small{t_{1/2}}$$ instead of $$\small{k}$$ – was explored already in the dark ages.42 43

Although there was wide variation in milligram dosage, body weight, and estimated halflife in these studies, the average area/dose × halflife ratios are amazingly similar.
John G. Wagner (1967)44
[…] the assumption of constant clearance in the individual between the occasions of receiving the standard and the test dose is suspect for theophylline. […] If there is evidence that the clearance but not the volume of distribution varies in the individual, the AUC × k can be used to gain a more precise index of bioavailability than obtainable from AUC alone.
Upton et al. (1980)45

Confirmed (esp. for $$\small{AUC_{0-\infty}}$$) in the data set Theoph46 which is part of the Base R installation: $\small{\begin{array}{lc} \textrm{PK metric} & CV_\textrm{geom}\,\%\\\hline AUC_{0-\textrm{tlast}} & {\color{Red} {22.53\%}}\\ AUC_{0-\textrm{tlast}} \times k & {\color{Blue} {21.81\%}}\\ AUC_{0-\infty} & {\color{Red} {28.39\%}}\\ AUC_{0-\infty} \times k & {\color{Blue} {20.36\%}}\\\hline \end{array}}$

Later work47 (by an author of the FDA…) was ignored as well. Hey, for 20+ years! A recent paper demonstrated its usefulness in extensive simulations.
Abstract
Aim To quantify the utility of a terminal-phase adjusted area under the concentration curve method in increasing the probability of a correct and conclusive outcome of a bioequivalence (BE) trial for highly variable drugs when clearance (CL) varies more than the volume of distribution (V).
Methods: Data from a large population of subjects were generated with variability in CL and V, and used to simulate a two-period, two-sequence crossover BE trial. The 90% confidence interval for formulation comparison was determined following BE assessment using the area under the concentration curve (AUC) ratio test, and the proposed terminal-phase adjusted AUC ratio test. An outcome of bioequivalent, non-bio­equi­va­lent or inconclusive was then assigned according to predefined BE limits.
Results: When CL is more variable than V, the proposed approach would enhance the probability of correctly assigning bioequivalent or non-bioequivalent and reduce the risk of an inconclusive trial. For a hypothetical drug with between-subject variability of 35% for CL and 10% for V, when the true test-reference ratio of bioavailability is 1.15, a cross-over study of n=14 subjects analyzed by the proposed method would have 80% or 20% probability of claiming bioequivalent or non-bioequivalent, compared to 22%, 46% or 32% probability of claiming bioequivalent, non-bioequivalent or inconclusive using the standard AUC ratio test.
Conclusions: The terminal-phase adjusted AUC ratio test represents a simple and readily applicable approach to enhance the BE assessment of drug products when CL varies more than V.
Lucas et al. (2022)48

I ❤️ the idea. When Abdallah’s paper47 was published, I tried the approach retrospectively in a couple of my studies. Worked mostly, and if not, it was a HVDP, where the variability is caused by the formulation (e.g., gastric-re­sis­tant diclofenac).

That’s basic PK and $$\small{CL=\textrm{const}}$$ is a rather strong assumption, which might be outright false. Then the entire current concept of BE testing is built on sand: Studies are substantially larger than necessary, exposing innocent subjects to nasty drugs.

It is recommended that area correction be attempted in bioequivalence studies of drugs where high intrasubject variability in clearance is known or suspected. […] The value of this approach in regulatory decision making remains to be determined.
Abdallah (1998)47
Performance of the AUC·k ratio test […] indicate that the regulators should consider the method for its potential utility in assessing HVDs and lessening unnecessary drug exposure in BE trials.
Lucas et al. (2022)48

For HVDs (not HVDPs) probably we could counteract the high variability, avoid the potentially inflated Type I Error in SABE (which is covered in another article), use conventional ABE with fixed limits, and all will be good. Maybe agencies should revise their guidelines. Hope dies last.

Helmut Schütz 2022
R and PowerTOST GPL 3.0, TeachingDemos Artistic 2.0, pandoc GPL 2.0.
1st version April 22, 2021. Rendered July 12, 2022 12:20 CEST by rmarkdown via pandoc in 0.67 seconds.

Footnotes and References

1. Labes D, Schütz H, Lang B. PowerTOST: Power and Sample Size for (Bio)Equivalence Studies. Package version 1.5.4. 2022-02-21. CRAN.↩︎

2. Snow G. TeachingDemos: Demonstrations for Teaching and Learning. Package version 2.12. 2020-04-01. CRAN.↩︎

3. Schütz H. Average Bioequivalence. 2021-01-18. CRAN.↩︎

4. Schütz H. Reference-Scaled Average Bioequivalence. 2022-02-19. CRAN.↩︎

5. Labes D, Schütz H, Lang B. Package PowerTOST’. February 21, 2022. CRAN.↩︎

6. Some gastric resistant formulations of diclofenac are HVDPs, practically all topical formulations are HVDPs, whereas diclofenac itself is not a HVD ($$\small{CV_\textrm{w}}$$ of a solution ~8%).↩︎

7. Note that the model of SABE is based on the true $$\small{\sigma_\textrm{wR}}$$, whereas in practice the observed $$\small{s_\textrm{wR}}$$ is used.↩︎

8. Note that the intention to apply one of the SABE-methods must be stated in the protocol. It is neither acceptable to switch post hoc from ABE to SABE nor between methods (say, from ABEL to the more permissive RSABE).↩︎

9. $$\small{CV_\textrm{wR}=100\sqrt{\exp(0.294^2)-1}=30.04689\ldots\%}$$↩︎

10. Health Canada, TPD. Notice: Policy on Bioequivalence Standards for Highly Vari­able Drug Products. File number 16-104293-140. Ottawa. April 18, 2016. Online.↩︎

11. Tóthfalusi L, Endrényi L. Sample Sizes for Designing Bioequivalence Studies for Highly Variable Drugs. J Pharm Pharmaceut Sci. 2012; 15(1): 73–84. doi:10.18433/J3Z88F.  Open Access.↩︎

12. Benet L. Why Highly Variable Drugs are Safer. Presentation at the FDA Advisory Committee for Phar­ma­ceu­tical Science. Rockville. 06 October, 2006.  Internet Archive.↩︎

13. FDA, OGD. Draft Guidance on Progesterone. Rockville. Recommended April 2010, Revised February 2011. Download.↩︎

14. FDA, CDER. Draft Guidance. Bioequivalence Studies With Pharmacokinetic End­points for Drugs Submitted Under an ANDA. Rockville. August 2021. Download.↩︎

15. Fuglsang A. Mitigation of the convergence issues associated with semi-replicated bioequivalence data. Pharm Stat. 2021; 20(6): 1232–4. doi:10.1002/pst.2142.↩︎

16. EMA. EMA/582648/2016. Annex I. Online.↩︎

17. FDA, CDER. Guidance for Industry. Statistical Approaches to Estab­lish­ing Bioequivalence. Rockville. January 2001. Download.↩︎

18. SAS Institute Inc. SAS® 9.4 and SAS® Viya® 3.3 Programming Documentation. The MIXED Procedure. February 13, 2019. Online.↩︎

19. Balaam LN. A Two-Period Design with t2 Experimental Units. Biometrics. 1968; 24(1): 61–73. doi:10.2307/2528460.↩︎

20. Chow, SC, Shao J, Wang H. Individual bioequivalence testing under 2×3 designs. Stat Med. 2002; 21(5): 629–48. doi:10.1002/sim.1056.↩︎

21. Aka the ‘extra-reference’ design. It should be avoided because it is biased in the presence of period effects (T is not administered in the 3rd period).↩︎

24. Certara USA, Inc., Princeton, NJ. Phoenix® WinNonlin® version 8.1. 2018.↩︎

25. Health Canada, TPD. Guidance Document: Conduct and Analysis of Comparative Bioavailability Studies. Section 2.7.4.2 Model Fitting. Cat:H13‐9/6‐2018E. Ottawa. 2018/06/08. Online.↩︎

26. EMA, CHMP. Questions & Answers: positions on specific questions addressed to the Pharmacokinetics Working Party (PKWP). EMA/618604/2008 Rev. 13. London. 19 November 2015. Online.↩︎

27. FDA, CDER. Guidance for Industry. Controlled Correspondence Related to Generic Drug Development. Silver Spring. December 2020. Download.↩︎

28. A member of the BEBA-Forum faced two partial replicate studies where the software failed to converge (SAS and Phoenix WinNonlin). Luckily, these were just pilot studies. He sent letters to the FDA asking for a clarification. He never received an answer.↩︎

29. In case of a ‘poor’ bioanalytical method requiring a large sample volume: Since the total blood sampling volume is generally limited with the one of a blood donation, one may opt for a 3-period full replicate or has to measure HCT prior to administration in higher periods and – for safety reasons – exclude subjects if their HCT is too high.↩︎

30. The T/R-ratio in a particular subject differs from other subjects showing a ‘normal’ response. A concordant outlier will show deviant responses for both T and R. That’s not relevant in crossover designs.↩︎

31. If the study was planned for ABE, fails due to lacking power ($$\small{CV}$$ higher than assumed and $$\small{CV_\textrm{wR}>30\%}$$, and reference-scaling would be acceptable (no safety/efficacy issues with the expanded limits), one has already estimates of $$\small{CV_\textrm{wR}}$$ and $$\small{CV_\textrm{wT}}$$ and is able to design the next study properly.↩︎

32. The $$\small{CV_\textrm{wR}}$$ has to be recalculated after exlusion of the outlier(s), leading to less expansion of the limits. Never­theless, the outlying subject(s) has/have to be kept in the data set for calculating the 90% confidence interval. However, that contradicts the principle »The data from all treated subjects should be treated equally« stated in the guideline.↩︎

33. Also two or three washout phases instead of one. Once we faced a case when during a washout a volunteer was bitten by a dog. Since he had to visit a hospital to get his wound sutured, according to the protocol it was rated as a – not drug-related – SAE and we had to exlude him from the study. Shit happens.↩︎

34. EMA. Questions & Answers: positions on specific questions addressed to the Phar­ma­co­kinetics Working Party (PKWP). EMA/618604/2008. London. June 2015 (Rev. 12 and later). Online.↩︎

35. EMA, CHMP. Guideline on the Inves­ti­ga­tion of Bioequivalence. CPMP/EWP/QWP/1401/98 Rev. 1/ Corr **. London. 20 January 2010. Online.↩︎

36. Schütz H. The almighty oracle has spoken! BEBA Forum. RSABE /ABEL. 2015-07-23↩︎

37. Labes D, Schütz H. Inflation of Type I Error in the Evaluation of Scaled Average Bioequivalence, and a Method for its Control. Pharm Res. 2016; 33(11): 2805–14. doi:10.1007/s11095-016-2006-1.↩︎

38. EMA. EMA/582648/2016. Annex II. London. 21 September 2016. Online.↩︎

39. Maurer W, Jones B, Chen Y. Controlling the type 1 error rate in two-stage sequential designs when testing for average bioequivalence. Stat Med. 2018; 37(10): 1587–1607. doi:10.1002/sim.7614.↩︎

40. Step sizes of $$\small{n_1}$$ 2 in full replicate designs and 3 in the partial replicate design; step size of $$\small{CV_\textrm{wR}}$$ 2%.↩︎

41. I know one large generic player’s rule for pilot studies of HVD(P)s: The minimum sample size is 24 in a four-period full replicate design. I have seen pilot studies with 80 subjects.↩︎

42. Before the portmanteau word ‘bioavailability’ (of ‘biological’ and ‘availability’) was coined by Lindenbaum et al. in 1971. Try to search for earlier papers with the keyword ‘bioavailability’. You will be surprised.↩︎

43. Lindenbaum J, Mellow MH, Blackstone MO, Butler VP. Variation in Biologic Availability of Digoxin from Four Preparations. N Engl J Med. 1971; 285: 1344–7. doi:10.1056/nejm19711209285240.↩︎

44. Wagner JG. Method of Estimating Relative Absorption of a Drug in a Series of Clinical Studies in Which Blood Levels Are Measured After Single and/or Multiple Doses. J Pharm Sci. 1967; 56(5): 652–3. doi:10.1002/jps.2600560527.↩︎

45. Upton RA, Sansom L, Guentert TW, Powell JR, Thiercellin J-F, Shah VP, Coates PE, Riegelman S. Evaluation of the Absorption from 15 Commercial Theophylline Products Indicating Deficiencies in Currently Applied Bio­avail­ability Criteria. J Pharmacokin Biopharm. 1980; 8(3): 229–42. doi:10.1007/BF01059644.↩︎

46. Study D, Treatment II of Upton et al.: Slophyllin aqueous syrup (Dooner Laboratories), 80 mg theophylline per 15-mL dose, 60 mL ≈ 320 mg administered, twelve subjects, sampling: 0, 0.25, 0.5, 1, 2, 3.5, 5, 7, 9, 12, 24 hours. Linear-up / log-down trapezoidal rule, extrapolation based on $$\small{\widehat{C}_\textrm{last}}$$ [sic].↩︎

47. Abdallah HY. An area correction method to reduce intrasubject variability in bioequivalence studies. J Pharm Phar­ma­ceut Sci. 1998; 1(2): 60–5.  Open Access.↩︎

48. Lucas AJ, Ogungbenro K, Yang S, Aarons L. Chen C. Evaluation of area under the concentration curve adjusted by the terminal-phase as a metric to reduce the impact of variability in bioequivalence testing. Br J Clin Phar­ma­col. 2022; 88(2): 619–27. doi:10.1111/bcp.14986.↩︎