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Examples in this article were generated with R 4.0.5 by the package PowerTOST.1

More examples are given in the respective vignette.2 See also the README on GitHub for an overview and the online manual3 for details and a collection of other articles.

  • The right-hand badges give the respective section’s ‘level’.
  1. Basics about 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.
  1. If you are not a neRd or statistics afficionado, skipping is recommended. Suggested for experts but might be confusing for others.
  • Click to show / hide R code.
Abbreviation Meaning
(A)BE (Average) Bioequivalence
ABEL Average Bioequivalence with Expanding Limits
CVb Between-subject Coefficient of Variation
CVw Within-subject Coefficient of Variation
CVwT, CVwR Within-subject Coefficient of Variation of the Test and Reference treatment
H0 Null hypothesis
H1 Alternative hypothesis (also Ha)
HVD(P) Highly Variable Drug (Product)
RSABE Reference-scaled Average Bioequivalence
SABE Scaled Average Bioequivalence



What is Reference-scaled Average Bioequivalence?

For background about inferential statistics see the article about average bioequivalence in a replicate design.

The concept of Scaled Average Bioequivalence (SABE) for Highy Variable Drugs / Drug Products 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 III and consequently, the originator’s product not be 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% (leading to the limits of 80.00 – 125.00% in ABE) is overly conservative and thus, leading to large sample sizes.
  • Hence, a more relaxed Δ of > 20% was proposed. A natural approach is to scale (expand / widen) the limits based on the within-subject variability of the reference product σwR. In this approach, power for a given sample size is essentially independent from the variability (see Fig. 3).

The conventional confidence interval inclusion approach of ABE \[\begin{matrix}\tag{1} \theta_1=1-\Delta,\theta_2=\left(1-\Delta\right)^{-1}\\ H_0:\;\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\ni\left\{\theta_1,\,\theta_2\right\}\;vs\;H_1:\;\theta_1<\frac{\mu_\textrm{T}}{\mu_\textrm{R}}<\theta_2, \end{matrix}\] where \(\small{H_0}\) is the null hypothesis of inequivalence and \(\small{H_1}\) the alternative hypothesis, \(\small{\theta_1}\) and \(\small{\theta_2}\) are the fixed lower and upper limits of the acceptance range, and \(\small{\mu_\textrm{T}}\) are the geometric least squares means of \(\small{\textrm{T}}\) and \(\small{\textrm{R}}\), respectively
is in Scaled Average Bioequivalence (SABE)4 modified to \[H_0:\;\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\Big{/}\sigma_\textrm{wR}\ni\left\{\theta_{\textrm{s}_1},\,\theta_{\textrm{s}_2}\right\}\;vs\;H_1:\;\theta_{\textrm{s}_1}<\frac{\mu_\textrm{T}}{\mu_\textrm{R}}\Big{/}\sigma_\textrm{wR}<\theta_{\textrm{s}_2},\tag{2}\] where \(\small{\sigma_\textrm{wR}}\) is the standard deviation of the reference and 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.

Alas, we are far away from global harmonization. Reference-scaled Average Bioequivalence (RSABE) for HVD(P)s is preferred by the U.S. FDA and China’s Center for Drug Evaluation, whereas Average Bioequivalence with Expanding Limits (ABEL) is preferred everywhere else.
To make things worse, the methods are acceptable for different pharmacokinetic metrics.

PK metric Method Jurisdiction
any one RSABE U.S. FDA.5
Cmax, AUC RSABE China CDE.6
Cmax ABEL EMA,7 the WHO,8 Australia,9 the East African Community,10 ASEAN states,11 the Eurasian Economic Union, 12 Egypt,13 New Zealand,14 Chile,15 Brazil,16 Canada,17 GCC.18
AUC ABEL Canada,
WHO (if in a 4-period full replicate design19).
Cmin, Cτ ABEL EMA (controlled release products in steady state).
partial AUC ABEL EMA (controlled release products).

In order to apply RSABE 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).
  • The observed within-subject standard deviation of the reference swR has to be ≥ 0.294 (CVwR ≥ ≈0.30047).

The approach given in the guidance20 is a decision scheme which hinges on the estimated standard deviation of the reference treatment \(\small{s_{\textrm{wR}}}\). If \(\small{s_\textrm{wR}<0.294}\) the study has to be assessed for ABE (left branch) and for RSABE (right branch) otherwise. In the RSABE-branch the point estimate (\(\small{PE}\)) has to lie within 80.00 – 125.00%.

Fig. 1 Decision scheme (FDA, CDE).


Based on the switching standard deviation \(\small{s_0=0.25}\) we get the regulatory constant \(\small{\theta_\textrm{s}=\frac{\log_{e}1.25}{s_0}=0.8925742\ldots}\) and finally the ‘implied limits’ \(\small{\left\{\theta_{\textrm{s}_1},\theta_{\textrm{s}_2}\right\}=100\left(\exp(\mp0.8925742\cdot s_{\textrm{wR}})\right)}\).

Fig. 2 ‘Implied limits’23 depending on the observed CVwR.
Dashed vertical lines at the switching condition (CVwR ≈25.396%)
and at applicable lower cap of scaling (CVwR ≈30.047%).

Note that scaling starts at switching standard deviation \(\small{s_0=0.25}\) (\(\small{CV_0\approx25.396\%}\)) but can be only applied if \(\small{s_{\textrm{wR}}\geq0.294}\) (\(\small{CV_{\textrm{wR}}\geq\approx0.30047}\)) thus explaining the dichotomy24 at this value.

Note also that – contrary to ABEL – there is no upper cap of scaling. However, for very large variability the decision is mainly lead by the \(\small{PE}\)-constraint.

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

Since the applicability of this approach depends on the realized values (\(\small{s_\textrm{wR}}\), \(\small{PE}\)) in the particular study – which are naturally unknown beforehand – analytical solutions for power (and hence, the sample size) do not exist.

Therefore, extensive simulations of potential combinations have to be employed.

Cave: If \(\small{s_{\textrm{wR}}<0.294}\) the method may lead to an inflated Type I Error (increased patient’s risk). It will be elaborated in another article.

top of section ↩︎



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 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 3.6.3 (2020-02-29) and later.

Note that in all functions of PowerTOST the arguments (say, the assumed T/R-ratio theta0, the assumed coefficient of variation CV, etc.) have to be given as ratios and not in percent.

sampleN.RABE() gives balanced sequences (i.e., an equal number of subjects is allocated to all sequences). Furthermore, the estimated sample size is the total number of subjects.

All examples deal with studies where the response variables likely follow a lognormal distribution, i.e., we assume a multiplicative model (ratios instead of differences). We work with \(\small{\log_{e}}\)-transformed data in order to allow analysis by the t-test (requiring differences).

previous section ↩︎



It may sound picky but ‘sample size calculation’ (as used in most guidelines and alas, in some publications and textbooks) is sloppy terminology. In order to get prospective power (and hence, a sample size), we need five values:

  1. The level of the test (in BE commonly 0.05),
  2. the (potentially) expanded/widened BE-margin,
  3. the desired (or target) power,
  4. the variance (commonly expressed as a coefficient of variation), and
  5. the deviation of the test from the reference treatment,


  1. is fixed by the agency,
  2. depends on the observed25 CVwR (which is unknown beforehand),
  3. is set by the sponsor (commonly to 0.80 – 0.90),
  4. is an uncertain assumption,
  5. is an uncertain assumption.

In other words, obtaining a sample size is not an exact calculation like \(\small{2\times2=4}\) but always just an estimation.

Power Calculation – A guess masquerading as mathematics.

Of note, it is extremely unlikely that all assumptions will be exactly realized in a particular study. Hence, calculating retrospective (a.k.a. post hoc, a posteriori) power is not only futile but plain nonsense.26

Since generally the within-subject variability \(\small{CV_\textrm{w}}\) is smaller than the between-subject variability \(\small{CV_\textrm{b}}\), crossover studies are so popular.
Of note, there is no relationship between \(\small{CV_\textrm{w}}\) and \(\small{CV_\textrm{b}}\). An example are drugs which are subjected to polymorphic metabolism. For these drugs \(\small{CV_\textrm{w}\ll CV_\textrm{b}}\).
Furthermore, the drugs’ within-subject variability may be unequal (i.e., \(\small{s_{\textrm{wT}}^{2}\neq s_{\textrm{wR}}^{2}}\)). For details see the section Heteroscedasticity.

Carryover: A residual effect of a previous period.

It is a prerequisite that no carryover from one period to the next exists. Only then the comparison of treatments will be unbiased.27 Carryover is elaborated in another article.

Studies in a replicate design can be not only performed in healthy volunteers but also in patients with a stable disease (e.g., asthma).

previous section ↩︎

Power → Sample size


The sample size cannot be directly estimated, in SABE only power simulated for an already given sample size based on assumptions.

Power. That which statisticians are always calculating but never have.
Stephen Senn, Statistical Issues in Drug Development. Wiley, 2nd ed 2007.


Let’s start with PowerTOST.

library(PowerTOST) # attach it to run the examples

The sample size functions’ defaults are:

Argument Default Meaning
alpha 0.05 Nominal level of the test.
targetpower 0.80 Target (desired) power.
theta0 0.90 Assumed T/R-ratio.
theta1 0.80 Lower BE-limit in ABE and lower PE-constraint in ABEL.
theta2 1.25 Upper BE-limit in ABE and upper PE-constraint in ABEL.
design "2x3x3" Treatments × Sequences × Periods.
regulator "FDA" Guess…
nsims 1e05 Number of simulations.
print TRUE Output to the console.
details TRUE Show regulatory settings and sample size search.
setseed TRUE Set a fixed seed (recommended for reproducibility).

For a quick overview of the ‘implied limits’ use the function scABEL() – for once in percent according to the guidance.

df <- data.frame(CV = 100*c(0.25, se2CV(0.25), 0.3, se2CV(0.294),
                            0.5, 0.65),
                 swR = NA,
                 method = c("ABE", rep("SABE", 5)),
                 applicable = c(rep("ABE", 3), rep("RSABE", 3)),
                 cap = c(rep("lower", 3), rep("  -  ", 3)),
                 L = NA, U = NA)
for (i in 1:6) {
  df$swR[i]  <- signif(CV2se(df$CV[i]/100), 5)
  df[i, 6:7] <- sprintf("%.2f%%", 100*scABEL(df$CV[i]/100,
                                             regulator = "FDA"))
df$CV     <- sprintf("%.3f%%", df$CV)
print(df, row.names = FALSE)
R>       CV     swR method applicable   cap      L       U
R>  25.000% 0.24622    ABE        ABE lower 80.00% 125.00%
R>  25.396% 0.25000   SABE        ABE lower 80.00% 125.00%
R>  30.000% 0.29356   SABE        ABE lower 80.00% 125.00%
R>  30.047% 0.29400   SABE      RSABE   -   76.92% 130.01%
R>  50.000% 0.47238   SABE      RSABE   -   65.60% 152.45%
R>  65.000% 0.59365   SABE      RSABE   -   58.87% 169.87%

The sample size functions of PowerTOST use a modification of Zhang’s method28 for the first guess.

# Note that theta0 = 0.90 is the default
sampleN.RSABE(CV = 0.45, targetpower = 0.80,
              design = "2x2x4", details = TRUE)
R> ++++++++ Reference scaled ABE crit. +++++++++
R>            Sample size estimation
R> ---------------------------------------------
R> Study design: 2x2x4 (4 period full replicate)
R> log-transformed data (multiplicative model)
R> 1e+05 studies for each step simulated.
R> alpha  = 0.05, target power = 0.8
R> CVw(T) = 0.45; CVw(R) = 0.45
R> True ratio = 0.9
R> ABE limits / PE constraints = 0.8 ... 1.25 
R> FDA regulatory settings
R> - CVswitch            = 0.3 
R> - regulatory constant = 0.8925742 
R> - pe constraint applied
R> Sample size search
R>  n     power
R> 18   0.71411 
R> 20   0.75794 
R> 22   0.79514 
R> 24   0.82450

previous section ↩︎



Throughout the examples I’m referring to studies in a single center – not multiple groups within them or multicenter studies. That’s another story.

A Simple Case


We assume a CV of 0.45, a T/R-ratio of 0.90, a target a power of 0.80, and want to perform the study in a 2-sequence 4-period full replicate study (TRTR|RTRT or TRRT|RTTR or TTRR|RRTT).

Since theta0 = 0.90,29 targetpower = 0.80, and regulator = "FDA" are defaults of the function, we don’t have to give them explicitely. As usual in bioequivalence, alpha = 0.05 is employed (we will assess the study by a \(\small{100(1-2\,\alpha)=90\%}\) confidence interval). Hence, you need to specify only the CV (assuming \(\small{CV_\textrm{wT}=CV_\textrm{wR}}\)) and design = "2x2x4".
To shorten the output, use the argument details = FALSE.

sampleN.RSABE(CV = 0.45, design = "2x2x4", details = FALSE)
R> ++++++++ Reference scaled ABE crit. +++++++++
R>            Sample size estimation
R> ---------------------------------------------
R> Study design: 2x2x4 (4 period full replicate)
R> log-transformed data (multiplicative model)
R> 1e+05 studies for each step simulated.
R> alpha  = 0.05, target power = 0.8
R> CVw(T) = 0.45; CVw(R) = 0.45
R> True ratio = 0.9
R> ABE limits / PE constraints = 0.8 ... 1.25 
R> Regulatory settings: FDA 
R> Sample size
R>  n    power
R> 24   0.82450

Sometimes we are not interested in the entire output and want to use only a part of the results in subsequent calculations. We can suppress the output by stating the additional argument print = FALSE and assign the result to a data.frame (here df).

df <- sampleN.RSABE(CV = 0.45, design = "2x2x4",
                    details = FALSE, print = FALSE)

Although you could access the elements by the number of the column(s), I don’t recommend that, since in various functions these numbers are different and hence, difficult to remember.

Let’s retrieve the column names of df:

R>  [1] "Design"         "alpha"          "CVwT"          
R>  [4] "CVwR"           "theta0"         "theta1"        
R>  [7] "theta2"         "Sample size"    "Achieved power"
R> [10] "Target power"   "nlast"

Now we can access the elements of df by their names. Note that double square brackets [[…]] have to be used (single ones are used to access elements by their numbers).

df[["Sample size"]]
R> [1] 24
df[["Achieved power"]]
R> [1] 0.8245

If you insist in accessing elements by column-numbers, use single square brackets […].

R>   Sample size Achieved power
R> 1          24         0.8245

With 24 subjects (12 per sequence) we achieve the power we desire.

What happens if we have one dropout?

power.RSABE(CV = 0.45, design = "2x2x4",
            n = df[["Sample size"]] - 1)
R> Unbalanced design. n(i)=12/11 assumed.
R> [1] 0.8105

Still above 0.80 we desire. However, with two dropouts (22 eligible subjects) we would slightly fall short (0.7951).

Since dropouts are common, it makes sense to include / dose more subjects in order to end up with a number of eligible subjects which is not lower than our initial estimate.

Let us explore that in the next section.

previous section ↩︎



We define two supportive functions:

  1. Provide equally sized sequences, i.e., any total sample size n will be rounded up to achieve balance.
balance <- function(n, n.seq) {
  return(as.integer(n.seq * (n %/% n.seq + as.logical(n %% n.seq))))
  1. Provide the adjusted sample size based on the original sample size n and the anticipated droput-rate do.rate.
nadj <- function(n, do.rate, n.seq) {
  return(as.integer(balance(n / (1 - do.rate), n.seq)))

In order to come up with a suggestion we have to anticipate a (realistic!) dropout rate. Note that this not the job of the statistician; ask the Principal Investigator.

It is a capital mistake to theorise before one has data.



The dropout-rate is calculated from the eligible and dosed subjects
or simply \[\begin{equation}\tag{3} do.rate=1-n_\textrm{eligible}/n_\textrm{dosed} \end{equation}\] Of course, we know it only after the study was performed.

By substituting \(n_\textrm{eligible}\) with the estimated sample size \(n\), providing an anticipated dropout-rate and rearrangement to find the adjusted number of dosed subjects \(n_\textrm{adj}\) we should use \[\begin{equation}\tag{4} n_\textrm{adj}=\;\upharpoonleft n\,/\,(1-do.rate) \end{equation}\] where \(\upharpoonleft\) denotes rounding up to the next even number as implemented in the functions above.

An all too common mistake is to increase the estimated sample size \(n\) by the drop­out-rate according to \[\begin{equation}\tag{5} n_\textrm{adj}=\;\upharpoonleft n\times(1+do.rate) \end{equation}\] If you used \((5)\) in the past – you are not alone. In a small survey a whooping 29% of respondents reported to use it.30 Consider changing your routine.

There are no routine statistical questions, only questionable statistical routines.

top of section ↩︎ previous section ↩︎

Adjusted Sample Size


In the following I specified more arguments to make the function more flexible.
Note that I wrapped the function power.RSABE() in suppressMessages(). Otherwise, the function will throw for any odd sample size a message telling us that the design is unbalanced. Well, we know that.

CV      <- 0.45 # within-subject CV
target  <- 0.80 # target (desired) power
theta0  <- 0.90 # assumed T/R-ratio
design  <- "2x2x4"
do.rate <- 0.15 # anticipated dropout-rate 15%
                # might be realively high due
                # to the 4 periods
n.seq   <- as.integer(substr(design, 3, 3))
lims    <- scABEL(CV) # expanded limits
df      <- sampleN.RSABE(CV = CV, theta0 = theta0,
                         targetpower = target,
                         design = design,
                         details = FALSE,
                         print = FALSE)
# calculate the adjusted sample size
n.adj   <- nadj(df[["Sample size"]], do.rate, n.seq)
# (decreasing) vector of eligible subjects
n.elig  <- n.adj:df[["Sample size"]]
info    <- paste0("Assumed CV              : ",
                  "\nAssumed T/R ratio       : ",
                  "\nExpanded limits         : ",
                  lims[1], lims[2]),
                  "\nPE constraints          : ",
                  0.80, 1.25), # fixed in ABEL
                  "\nTarget (desired) power  : ",
                  "\nAnticipated dropout-rate: ",
                  "\nEstimated sample size   : ",
                  df[["Sample size"]], " (",
                  df[["Sample size"]]/n.seq, "/sequence)",
                  "\nAchieved power          : ",
                  signif(df[["Achieved power"]], 4),
                  "\nAdjusted sample size    : ",
                  n.adj, " (",  n.adj/n.seq, "/sequence)",
# explore the potential outcome for
# an increasing number of dropouts
do.act <- signif((n.adj - n.elig) / n.adj, 4)
df     <- data.frame(dosed    = n.adj,
                     eligible = n.elig,
                     dropouts = n.adj - n.elig,
                     do.act   = do.act,
                     power    = NA)
for (i in 1:nrow(df)) {
  df$power[i] <- suppressMessages(
                   power.RSABE(CV = CV,
                               theta0 = theta0,
                               design = design,
                               n = df$eligible[i]))
cat(info); print(round(df, 4), row.names = FALSE)
R> Assumed CV              : 0.45
R> Assumed T/R ratio       : 0.9
R> Expanded limits         : 0.7215…1.3859
R> PE constraints          : 0.8000…1.2500
R> Target (desired) power  : 0.8
R> Anticipated dropout-rate: 0.15
R> Estimated sample size   : 24 (12/sequence)
R> Achieved power          : 0.8245
R> Adjusted sample size    : 30 (15/sequence)
R>  dosed eligible dropouts do.act  power
R>     30       30        0 0.0000 0.8899
R>     30       29        1 0.0333 0.8810
R>     30       28        2 0.0667 0.8729
R>     30       27        3 0.1000 0.8612
R>     30       26        4 0.1333 0.8508
R>     30       25        5 0.1667 0.8377
R>     30       24        6 0.2000 0.8245

In the worst case (6 dropouts) we end up with the originally estimated sample size of 24. Power preserved, mission accomplished. If we have less dropouts, splendid – we gain power.

If we would have adjusted the sample size acc. to \((5)\) we would have dosed 28 subjects.
If the anticipated dropout rate of 15% is realized in the study, we would have 23 eligible subjects (power 0.8105). In this example we achieve still more than our target power but the loss might be relevant in other cases.

top of section ↩︎ previous section ↩︎

Post hoc Power


As said in the preliminaries, calculating post hoc power is futile.

There is simple intuition behind results like these: If my car made it to the top of the hill, then it is powerful enough to climb that hill; if it didn’t, then it obviously isn’t powerful enough. Retrospective power is an obvious answer to a rather uninteresting question. A more meaningful question is to ask whether the car is powerful enough to climb a particular hill never climbed before; or whether a different car can climb that new hill. Such questions are prospective, not retrospective.

However, sometimes we are interested in it for planning the next study.

If you give and odd total sample size n, power.RSABE() will try to keep sequences as balanced as possible and show in a message how that was done.

n.act <- 25
signif(power.RSABE(CV = 0.45, n = n.act,
                   design = "2x2x4"), 6)
R> Unbalanced design. n(i)=13/12 assumed.
R> [1] 0.83767

Say, our study was more unbalanced. Let us assume that we dosed 30 subjects, the total number of subjects was also 25 but all drop­outs occured in one sequence (unlikely but possible).
Instead of the total sample size n we can give the number of subjects of each sequence as a vector (the order is generally31 not relevant, i.e., it does not matter which element refers to which sequence).


By setting details = TRUE we can retrieve the components of the simulations (probability to pass each test).

design   <- "2x2x4"
CV       <- 0.45
n.adj    <- 30
n.act    <- 25
n.s1     <- n.adj / 2
n.s2     <- n.act - n.s1
theta0   <- 0.90
post.hoc <- suppressMessages(
              power.RSABE(CV  = CV,
                          n = c(n.s1, n.s2),
                          theta0 = theta0,
                          design = design,
                          details = TRUE))
ABE.xact <- power.TOST(CV = CV,
                       n = c(n.s1, n.s2),
                       theta0 = theta0,
                       design = design)
sig.dig  <- nchar(as.character(n.adj))
fmt      <- paste0("%", sig.dig, ".0f (%", 
                   sig.dig, ".0f dropouts)")
cat(paste0("Dosed subjects: ", sprintf("%2.0f", n.adj),
           "\nEligible      : ",
           sprintf(fmt, n.act, n.adj - n.act),
           "\n  Sequence 1  : ",
           sprintf(fmt, n.s1, n.adj / 2 - n.s1),
           "\n  Sequence 1  : ",
           sprintf(fmt, n.s2, n.adj / 2 - n.s2),
           "\nPower overall :  ",
           sprintf("%.5f", post.hoc[1]),
           "\n  p(ABEL)     :  ",
           sprintf("%.5f", post.hoc[2]),
           "\n  p(PE)       :  ",
           sprintf("%.5f", post.hoc[3]),
           "\n  p(ABE)      :  ",
           sprintf("%.5f", post.hoc[4]),
           "\n  p(ABE) exact:  ",
           sprintf("%.5f", ABE.xact), "\n"))
R> Dosed subjects: 30
R> Eligible      : 25 ( 5 dropouts)
R>   Sequence 1  : 15 ( 0 dropouts)
R>   Sequence 1  : 10 ( 5 dropouts)
R> Power overall :  0.82821
R>   p(ABEL)     :  0.84762
R>   p(PE)       :  0.91031
R>   p(ABE)      :  0.34574
R>   p(ABE) exact:  0.35740

The components of overall power are:

  • p(ABEL) is the probability that the confidence interval is within the expanded / widened limits.
  • p(PE) is the probability that the point estimate is within 80.00–125.00%.
  • p(ABE) is the probability of passing conventional Average Bioequivalence.
    The line below gives the exact result obtained by power.TOST() – confirming the simulation’s result.

Of course, in a particular study you will provide the numbers in the n vector directly.

top of section ↩︎ previous section ↩︎

Lost in Assumptions


The CV and the T/R-ratio are only assumptions. Whatever their origin might be (literature, previous studies) they carry some degree of uncertainty. Hence, believing32 that they are the true ones may be risky.
Some statisticians call that the ‘Carved-in-Stone’ approach.

Say, we performed a pilot study in 16 subjects and estimated the CV as 0.45.

The \(\alpha\) confidence interval of the CV is obtained via the \(\chi^2\)-distribution of its error variance \(\sigma^2\) with \(\small{n-2}\) degrees of freedom. \[\begin{matrix}\tag{6} s^2=\log_{e}(CV^2+1)\\ L=\frac{(n-1)\,s^2}{\chi_{\alpha/2,\,n-2}^{2}}\leq\sigma^2\leq\frac{(n-1)\,s^2}{\chi_{1-\alpha/2,\,n-2}^{2}}=U\\ \left\{lower\;CL,\;upper\;CL\right\}=\left\{\sqrt{\exp(L)-1},\sqrt{\exp(U)-1}\right\} \end{matrix}\]

Let’s calculate the 95% confidence interval of the CV to get an idea.

m  <- 16 # pilot study
ci <- CVCL(CV = 0.45, df = m - 2,
           side = "2-sided", alpha = 0.05)
signif(ci, 4)
R> lower CL upper CL 
R>   0.3223   0.7629

Surprised? Although 0.45 is the best estimate for planning the next study, there is no guarantee that we will get exactly the same outcome. Since the \(\chi^2\)-distribution is skewed to the right, it is more likely to get a higher CV than a lower one in the planned study.

If we plan the study based on 0.45, we would opt for 24 subjects like in the examples before (not adjusted for the dropout-rate).
If the CV will be lower, we loose power (less expansion). But what if it will be higher? Depends. Since we may expand more, we gain power. However, if we cross the upper cap of scaling (50% for the EMA), we will loose power. But how much?

Let’s explore what might happen at the confidence limits of the CV.

m    <- 16
ci   <- CVCL(CV = 0.45, df = m - 2,
             side = "2-sided", alpha = 0.05)
n    <- 28
comp <- data.frame(CV = c(ci[["lower CL"]], 0.45,
                          ci[["upper CL"]]),
                   power = NA)
for (i in 1:nrow(comp)) {
  comp$power[i] <- power.RSABE(CV = comp$CV[i],
                               design = "2x2x4",
                               n = n)
comp[, 1] <- signif(comp[, 1], 4)
comp[, 2] <- signif(comp[, 2], 6)
print(comp, row.names = FALSE)
R>      CV   power
R>  0.3223 0.79246
R>  0.4500 0.87287
R>  0.7629 0.81122

Might hurt.

What can we do? The larger the previous study was, the larger the degrees of freedom and hence, the narrower the confidence interval of the CV. In simple terms: The estimate is more certain. On the other hand, it also means that very small pilot studies are practically useless. What happens when we plan the study based on the confidence interval of the CV?

m               <- seq(12, 30, 6)
df              <- data.frame(n.pilot = m, CV = 0.45,
                              l = NA, u = NA,
                              n.low = NA, n.CV = NA, n.hi = NA)
for (i in 1:nrow(df)) {
  df[i, 3:4] <- CVCL(CV = 0.45, df = m[i] - 2,
                     side = "2-sided",
                     alpha = 0.05)
  df[i, 5] <- sampleN.RSABE(CV = df$l[i], design = "2x2x4",
                            details = FALSE,
                            print = FALSE)[["Sample size"]]
  df[i, 6] <- sampleN.RSABE(CV = 0.45, design = "2x2x4",
                            details = FALSE,
                            print = FALSE)[["Sample size"]]
  df[i, 7] <- sampleN.RSABE(CV = df$u[i], design = "2x2x4",
                            details = FALSE,
                            print = FALSE)[["Sample size"]]

df[, 3:4]      <- signif(df[, 3:4], 4)
names(df)[3:4] <- c("lower CL", "upper CL")
print(df, row.names = FALSE)
R>  n.pilot   CV lower CL upper CL n.low n.CV n.hi
R>       12 0.45   0.3069   0.8744    30   24   32
R>       18 0.45   0.3282   0.7300    30   24   26
R>       24 0.45   0.3415   0.6685    28   24   24
R>       30 0.45   0.3509   0.6334    28   24   24

Small pilot studies are practically useless. One leading generic company has an internal rule to perform pilot studies of HVD(P)s in a full replicate design and at least 24 subjects. Makes sense.

Furthermore, we don’t know where the true T/R-ratio lies but we can calculate the lower 95% confidence limit of the pilot study’s point estimate to get an idea about a worst case. Say, it was 0.90.

m      <- 16
CV     <- 0.45
pe     <- 0.90
ci     <- round(CI.BE(CV = CV, pe = 0.90, n = m,
                      design = "2x2x4"), 4)
if (pe <= 1) {
  cl <- ci[["lower"]]
} else {
  cl <- ci[["upper"]]
R> [1] 0.7515

Exlore the impact of a relatively 5% lower CV (less expansion) and a relatively 5% lower T/R-ratio on power for the given sample size.

n      <- 28
CV     <- 0.45
theta0 <- 0.90
comp1  <- data.frame(CV = c(CV, CV*0.95),
                     power = NA)
comp2  <- data.frame(theta0 = c(theta0, theta0*0.95),
                     power = NA)
for (i in 1:2) {
  comp1$power[i] <- power.RSABE(CV = comp1$CV[i],
                                theta0 = theta0,
                                design = "2x2x4",
                                n = n)
comp1$power <- signif(comp1$power, 5)
for (i in 1:2) {
  comp2$power[i] <- power.RSABE(CV = CV,
                                theta0 = comp2$theta0[i],
                                design = "2x2x4",
                                n = n)
comp2$power <- signif(comp2$power, 5)
print(comp1, row.names = F); print(comp2, row.names = F)
R>      CV   power
R>  0.4500 0.87287
R>  0.4275 0.86914
R>  theta0   power
R>   0.900 0.87287
R>   0.855 0.71029


Fig. 3 Power curves for n = 28 (2×2×4 design).

Note the log-scale of the x-axis. It demonstrates that power curves are symmetrical around 1 (\(\small{\log_{e}(1)=0}\), where \(\small{\log_{e}(\theta_2)=\left|\log_{e}(\theta_1)\right|}\)) and we will achieve the same power for \(\small{\theta_0}\) and \(\small{1/\theta_0}\) (e.g., for 0.90 and 1.1111). Contrary to ABE, power is maintained.

  • A common flaw in protocols is the phrase
          »The sample size was calculated [sic] based on a T/R-ratio of 0.90 – 1.10«
    If you assume a deviation of 10% of the test from the reference and are not sure about its direction (lower or higer than 1), always use the lower T/R-ratio. If you would use the upper T/R-ratio, power would be only preserved down to 1/1.10 = 0.9091.
    Given, sometimes you will need a higher sample size with the lower T/R-ratio. There’s no free lunch.
CV      <- 0.45
delta   <- 0.10 # direction unknown
design  <- "2x2x4"
theta0s <- c(1 - delta, 1 / (1 + delta),
             1 + delta, 1 / (1 - delta))
n       <- sampleN.RSABE(CV = CV, theta0 = 1 - delta,
                         design = design,
                         details = FALSE,
                         print = FALSE)[["Sample size"]]
comp1   <- data.frame(CV = CV, theta0 = theta0s,
                      base = c(TRUE, rep(FALSE, 3)),
                      n = n, power = NA)
for (i in 1:nrow(comp1)) {
  comp1$power[i] <- power.RSABE(CV = CV,
                                theta0 = comp1$theta0[i],
                                design = design, n = n)
n       <- sampleN.RSABE(CV = CV, theta0 = 1 + delta,
                         design = design,
                         details = FALSE,
                         print = FALSE)[["Sample size"]]
comp2   <- data.frame(CV = CV, theta0 = theta0s,
                      base = c(FALSE, FALSE, TRUE, FALSE),
                      n = n, power = NA)
for (i in 1:nrow(comp2)) {
  comp2$power[i] <- power.RSABE(CV = CV,
                                theta0 = comp2$theta0[i],
                                design = design, n = n)
comp1[, c(2, 5)] <- signif(comp1[, c(2, 5)] , 4)
comp2[, c(2, 5)] <- signif(comp2[, c(2, 5)] , 4)
print(comp1, row.names = F); print(comp2, row.names = F)
R>    CV theta0  base  n  power
R>  0.45 0.9000  TRUE 24 0.8245
R>  0.45 0.9091 FALSE 24 0.8492
R>  0.45 1.1000 FALSE 24 0.8499
R>  0.45 1.1110 FALSE 24 0.8242
R>    CV theta0  base  n  power
R>  0.45 0.9000 FALSE 22 0.7951
R>  0.45 0.9091 FALSE 22 0.8199
R>  0.45 1.1000  TRUE 22 0.8212
R>  0.45 1.1110 FALSE 22 0.7954


Essentially this leads to the murky waters of prospective sensitivity analyses, which will be covered in another article.
An appetizer to show the maximum deviations (CV, T/R-ratio and decreased sample size due to dropouts) which give still a minimum acceptable power of ≥ 0.70:

CV       <- 0.45
theta0   <- 0.90
target   <- 0.80
minpower <- 0.70
pa       <- pa.scABE(CV = CV, theta0 = theta0,
                     targetpower = target,
                     minpower = minpower,
                     regulator = "FDA",
                     design = "2x2x4")
change.CV     <- 100*(tail(pa$paCV[["CV"]], 1) -
                      pa$plan[["CVwR"]]) /
change.theta0 <- 100*(head(pa$paGMR$theta0, 1) -
                      pa$plan$theta0) /
change.n      <- 100*(tail(pa$paN[["N"]], 1) -
                      pa$plan[["Sample size"]]) /
                      pa$plan[["Sample size"]]
comp     <- data.frame(parameter = c("CV", "theta0", "n"),
                       change = c(change.CV,
comp$change <- sprintf("%+.2f%%", comp$change)
names(comp)[2] <- "relative change"
print(pa, plotit = FALSE); print(comp, row.names = FALSE)
R> Sample size plan scABE (FDA/RSABE)
R>  Design alpha CVwT CVwR theta0 theta1 theta2 Sample size
R>   2x2x4  0.05 0.45 0.45    0.9    0.8   1.25          24
R>  Achieved power Target power
R>          0.8245          0.8
R> Power analysis
R> CV, theta0 and number of subjects leading to min. acceptable power of =0.7:
R>  CV= 1.1132, theta0= 0.8647
R>  n = 18 (power= 0.7141)
R>  parameter relative change
R>         CV        +147.37%
R>     theta0          -3.92%
R>          n         -25.00%

Confirms what we have seen above. As expect the method is extremely robust to changes of the CV. The sample size is also not very sensitive; many overrate the impact of dropouts on power.


I recommend to perform pilot studies in one of the fully replicated designs. When you are concerned about dropouts or the bioanalytical method requires large sample volumes, opt for one the 2-sequence 3-period designs (TRT|RTR or TRR|RTT).
Contrary to the partial replicate design (TRR|RTR|RRT) you get estimates of both \(\small{CV_\textrm{wT}}\) and \(\small{CV_\textrm{wR}}\). Since pharmaceutical technology improves, it is not uncommon that \(\small{CV_\textrm{wT}<CV_\textrm{wR}}\). If this is the case, you get an incentive in the sample size of the pivotal study (expanding the limits is based on \(\small{CV_\textrm{wR}}\) but the 90% CI on the – pooled – \(\small{s_\textrm{w}^{2}}\)).

\[\begin{matrix}\tag{7} s_\textrm{wT}^{2}=\log_{e}(CV_\textrm{wT}^{2}+1)\\ s_\textrm{wR}^{2}=\log_{e}(CV_\textrm{wR}^{2}+1)\\ s_\textrm{w}^{2}=\left(s_\textrm{wT}^{2}+s_\textrm{wR}^{2}\right)/2\\ CV_\textrm{w}=\sqrt{\exp(s_\textrm{w}^{2})-1}\end{matrix}\]

Say, we performed two pilot studies.
In the partial replicate we estimated the \(\small{CV_\textrm{w}}\) with 0.45 (and have to assume homoscedasticity, i.e., \(\small{CV_\textrm{wT}=CV_\textrm{wR}}\), which might be wrong).
In the full replicate we estimated \(\small{CV_\textrm{wT}}\) with 0.414 and \(\small{CV_\textrm{wR}}\) with 0.484. Note that the \(\small{CV_\textrm{w}}\) is 0.45 as well. How will that impact the sample size of the pivotal 4-period full replicate design?

comp <- data.frame(pilot = c("TRR|RTR|RRT", "TRT|RTR"),
                   CVwT = c(0.45, 0.414),
                   CVwR = c(0.45, 0.484),
                   CVw = NA,
                   n = NA, power = NA)
for (i in 1:nrow(comp)) {
  comp[i, 4]   <- signif(
                    mse2CV((CV2mse(comp$CVwT[i]) +
                            CV2mse(comp$CVwR[i])) / 2), 3)
  comp[i, 5:6] <- sampleN.RSABE(CV = c(comp$CVwT[i], comp$CVwR[i]),
                                 design = "2x2x4", details = FALSE,
                                 print = FALSE)[8:9]
print(comp, row.names = FALSE)
R>        pilot  CVwT  CVwR  CVw  n   power
R>  TRR|RTR|RRT 0.450 0.450 0.45 24 0.82450
R>      TRT|RTR 0.414 0.484 0.45 20 0.80146

Since bioanalytics drives study costs to a great extent, we may safe ~17%.

Note that when you give CV as two-element vector, the first element has to be \(\small{CV_\textrm{wT}}\) and the second \(\small{CV_\textrm{wR}}\).

Although acc. to the guidelines it is not required to estimate \(\small{CV_\textrm{wT}}\), its value is ‘nice to know’. Sometimes studies fail only due to the large \(\small{CV_\textrm{wR}}\) thus inflating the confidence interval. In such a case you have at least ammunation to start an argument.

Even if you plan the pivotal study in a partial replicate design (why on earth?) knowing both \(\small{CV_\textrm{wT}}\) and \(\small{CV_\textrm{wR}}\) is useful.

comp <- data.frame(pilot = c("TRR|RTR|RRT", "TRT|RTR"),
                   CVwT = c(0.45, 0.414),
                   CVwR = c(0.45, 0.484),
                   CVw = NA,
                   n = NA, power = NA)
for (i in 1:nrow(comp)) {
  comp[i, 4]   <- signif(
                    mse2CV((CV2mse(comp$CVwT[i]) +
                            CV2mse(comp$CVwR[i])) / 2), 3)
  comp[i, 5:6] <- sampleN.RSABE(CV = c(comp$CVwT[i], comp$CVwR[i]),
                                design = "2x3x3", details = FALSE,
                                print = FALSE)[8:9]
print(comp, row.names = FALSE)
R>        pilot  CVwT  CVwR  CVw  n   power
R>  TRR|RTR|RRT 0.450 0.450 0.45 33 0.82802
R>      TRT|RTR 0.414 0.484 0.45 27 0.81239

Again, a smaller sample size is possible.

previous section ↩︎

Multiple Endpoints


In demonstrating bioequivalence for the FDA the pharmacokinetic metrics Cmax, AUC0–t, and AUC0–∞ are mandatory.

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.33 34

We design the study always for the worst case combination, i.e., based on the PK metric requiring the largest sample size. Let’s explore that with different CVs and T/R-ratios.

metrics <- c("Cmax", "AUC")
CV      <- c(0.45, 0.30)
theta0  <- c(0.90, 0.925)
design  <- "2x2x4"
df      <- data.frame(metric = metrics, CV = CV,
                      theta0 = theta0, n = NA, power = NA)
df[1, 4:5] <- sampleN.RSABE(CV = CV[1], theta0 = theta0[1],
                            design = design, details = FALSE,
                            print = FALSE)[8:9]
df[2, 4:5] <- sampleN.RSABE(CV = CV[1], theta0 = theta0[2],
                            design = design, details = FALSE,
                            print = FALSE)[8:9]
df$power <- signif(df$power, 5)
txt      <- paste0("Sample size based on ",
                   df$metric[df$n == max(df$n)], ".\n")
print(df, row.names = FALSE); cat(txt)
R>  metric   CV theta0  n   power
R>    Cmax 0.45  0.900 24 0.82450
R>     AUC 0.30  0.925 20 0.82262
R> Sample size based on Cmax.

As usual the ‘worse’ PK metric drives the sample size. Although for Cmax (CV 0.45) we could scale (not AUC with CV 0.30), this advantage is counteracted by its ‘worse’ T/R-ratio (0.900 instead of 0.925). Power is extremely sensitive to the T/R-ratio (see Fig. 3.).
Consequently, the study is ‘overpowered’ for AUC.


Let us assume the same T/R-ratios for both metrics. Which are the extreme T/R-ratios (largest deviations of T from R) for Cmax giving still the target power?

opt <- function(x) {
  power.RSABE(theta0 = x, CV = df$CV[1],
              design = design,
              n = df$n[2]) - target
metrics <- c("Cmax", "AUC")
CV      <- c(0.45, 0.30)
theta0  <- 0.90
target  <- 0.80
design  <- "2x2x4"
df      <- data.frame(metric = metrics, CV = CV,
                      theta0 = theta0, n = NA, power = NA)
df[1, 4:5] <- sampleN.RSABE(CV = CV[1], theta0 = theta0,
                            design = design, details = FALSE,
                            print = FALSE)[8:9]
df[2, 4:5] <- sampleN.RSABE(CV = CV[2], theta0 = theta0,
                            design = design, details = FALSE,
                            print = FALSE)[8:9]
df$power <- signif(df$power, 5)
if (theta0[1] < 1) {
  res <- uniroot(opt, tol = 1e-8,
                 interval = c(0.80 + 1e-4, theta0))
} else {
  res <- uniroot(opt, tol = 1e-8,
                 interval = c(theta0, 1.25 - 1e-4))
res     <- unlist(res)
theta0s <- c(res[["root"]], 1/res[["root"]])
txt     <- paste0("Target power for ", metrics[1],
                  " and sample size ",
                  df$n[2], "\nachieved for theta0 ",
                  sprintf("%.4f", theta0s[1]), " or ",
                  sprintf("%.4f", theta0s[2]), ".\n")
print(df, row.names = FALSE); cat(txt)
R>  metric   CV theta0  n   power
R>    Cmax 0.45    0.9 24 0.82450
R>     AUC 0.30    0.9 32 0.81666
R> Target power for Cmax and sample size 32
R> achieved for theta0 0.8661 or 1.1546.

That means, although we assumed for Cmax the same T/R-ratio as for  AUC– with the sample size of 32 required AUC, for Cmax it can be as low as ~0.866 or as high as ~1.155, which is an interesting side-effect.

previous section ↩︎

Q & A

  • Q: Can we use R in a regulated environment and is PowerTOST validated?
    A: About the acceptability of Base R see ‘A Guidance Document for the Use of R in Regulated Clinical Trial Environments’.

    The authors of PowerTOST tried to do their best to provide reliable and valid results. The ‘NEWS’-file on CRAN documents the development of the package, bug-fixes, and introduction of new methods.
    Validation of any software (yes, of SAS as well…) lies in the hands of the user. Execute the script test_RSABE.R which can be found in the /tests sub-directory of the package to reproduce tables given in the literature.35 You will notice some discrepancies: The authors employed only 10,000 simulations – which is not sufficient for a stable result (see below). Furthermore, they reported the minimum sample size which gives at least the target power, wheras sampleN.RSABE() always rounds up to give balanced sequences.

  • Q: Shall we throw away our sample size tables?
    A: Not at all. File them in your archives to collect dust. Maybe in the future you will be asked by an agency how you arrived at a sample size. But: Don’t use them any more. What you should not do (and hopefully haven’t done before): Interpolate. Power and therefore, the sample size depends in a highly nonlinear fashion on the five conditions listed above, which makes interpolation of values given in table a nontrivial job.

  • Q: I fail to understand your example about dropouts. We finish the study with 24 eligible subjects as desired. Why is the dropout-rate ~20% and not the anticipated 15%?
    A: That’s due to rounding up the calculated adjusted sample size (28.24…) to the next even number (30).
    If you manage it to dose fractional subjects (I can’t) your dropout rate would indeed equal the anticipated one: 100(1 – 24/28.24…) = 15%.

  • Q: Do we have to worry about unbalanced sequences?
    A: sampleN.RSABE() will always give the total number of subjects for balanced sequences.
    If you are interested in post hoc power, give the sample size as a vector, i.e., power.RSABE(..., n = c(foo, bar, baz), where foo, bar, and baz are the number of subjects per sequence.

  • Q: The default number of simulations in the sample size estimation is 100,000. Why?
    A: We found that with this number the simulations are stable. For the background see another article. Of course you can give a larger number in the argument nsims. However, you shouldn’t decrease the number.

Fig. 4 Empiric power for n = 24 (2×2×4 design).
Dashed lines give the result (0.8245) obtained
by the default (100,00 simulations).

  • Q: How reliable are the results?
    A: As stated above an exact method doesn’t exist. We can only compare the empiric power of the ABE-component to the exact one obtained by power.TOST(). For an example see ‘Post hoc Power’ in the section about Dropouts.

  • Q: I still have questions. How to proceed?
    A: The preferred method is to register at the BEBA Forum and post your question there (please read its Policy first).
    You can contact me at [email protected]. Be warned – I will charge you for anything beyond most basic questions.

previous section ↩︎


CC BY 4.0 Helmut Schütz 2021
1st version March 27, 2021.
Rendered 2021-04-11 10:52:33 CEST by rmarkdown in 1.56 seconds.

Footnotes and References

  1. Labes D, Schütz H, Lang B. PowerTOST: Power and Sample Size for (Bio)Equivalence Studies. 2021-01-18. CRAN.↩︎

  2. Schütz H. Reference-Scaled Average Bioequivalence. 2020-12-23. CRAN.↩︎

  3. Labes D, Schütz H, Lang B. Package ‘PowerTOST’. January 18, 2021. CRAN.↩︎

  4. Tóthfalusi L, Endrényi L, García-Arieta A. Evaluation of bioequivalence for highly variable drugs with scaled average bioequivalence. Clin Pharma­co­kinet. 2009; 48(11): 725–43. doi:10.2165/11318040-000000000-00000.↩︎

  5. FDA. Center for Drug Evaluation and Research. Draft Guidance for Industry. Bioequivalence Studies with Pharmacokinetic Endpoints for Drugs Submitted Under an ANDA. Rockville; December 2013. download.↩︎

  6. CDE. Annex 2. Technical guidelines for research on bioequivalence of highly variable drugs. download. Chinese.↩︎

  7. European Medicines Agency, Committee for Medicinal Products for Human Use. Guideline on the Investigation of Bioequivalence. London, 20 January 2010. online.↩︎

  8. World Health Organization, Essential Medicines and Health Products: Multisource (generic) pharmaceutical products: guidelines on registration requirements to establish interchangeability. WHO Technical Report Series, No. 1003, Annex 6. Geneva, 28 April 2017. online↩︎

  9. Australian Government, Department of Health, Therapeutic Goods Administration. European Union and ICH Guidelines adopted in Australia. Guideline on the Investigation of Bioequi­valence with TGA Annotations. online.↩︎

  10. East African Community, Medicines and Food Safety Unit. Com­pen­dium of Medicines Evaluation and Registration for Medicine Regulation Harmonization in the East African Community, Part III: EAC Guidelines on Therapeutic Equivalence Requirements. online.↩︎

  11. ASEAN States Pharmaceutical Product Working Group. ASEAN Guideline for the Conduct of Bioequivalence Studies. Vientiane, March 2015. online.↩︎

  12. Eurasian Economic Commission. Regulations Conducting Bioequivalence Studies within the Framework of the Eurasian Economic Union. 3 November 2016. online. Russian.↩︎

  13. Ministry of Health and Population, The Specialized Scientific Committee for Evaluation of Bioavailability & Bioequivalence Studies. Egyptian Guideline For Conducting Bioequivalence Studies for Marketing Authorization of Generic Products. Cairo, February 2017. online.↩︎

  14. New Zealand Medicines and Medical Devices Safety Authority. Guideline on the Regulation of Therapeutic Products in New Zealand. Part 6: Bioequivalence of medicines. Wellington, February 2018. online.↩︎

  15. Departamento Agencia Nacional de Medicamentos. Instituto de Salud Pública de Chile. Guia para La realización de estudios de biodisponibilidad comparativa en formas farmacéuticas sólidas de administración oral y acción sistémica. Santiago, December 2018. Spanish.↩︎

  16. ANVISA. Critérios para a condução de estudos de biodisponibilidade relativa/bioequivalência. Consulta Pública Nº 760/2019. Brasilia, December 27, 2019. Portuguese.↩︎

  17. Health Canada. Guidance Document. Comparative Bioavailability Standards: Formulations Used for Systemic Effects. Ottawa, 08 June 2018. online.↩︎

  18. Executive Board of the Health Ministers’ Council for GCC States. The GCC Guidelines for Bioequivalence. March 2016. online.↩︎

  19. World Health Organization, Prequalification Team: medicines. Guidance Document: Application of reference-scaled criteria for AUC in bioequivalence studies conducted for submission to PQTm. Geneva, 22 November 2018. online.↩︎

  20. FDA. Office of Generic Drugs. Draft Guidance on Progesterone. Recommended Apr 2010; Revised Feb 2011. download.↩︎

  21. For unfathomable reasons the FDA recommends a mixed-effects model for fully replicated designs (SAS PROC MIXED) and a fixed-effects model (SAS PROC GLM) for the partial replicate design.↩︎

  22. Howe WG. Approximate Confidence Limits on the Mean of X+Y Where X and Y are Two Tabled Independent Random Variables. J Am Stat Assoc. 1974; 69(347): 789–794. doi:10.2307/2286019.↩︎

  23. Davit BM, Chen ML, Conner DP, Haidar SH, Kim S, Lee CH, Lionberger RA, Makhlouf FT, Nwakama PE, Patel DT, Schuirmann DJ, Yu LX. Imple­mentation of a Reference-Scaled Average Bioequivalence Approach for Highly Variable Generic Drug Products by the US Food and Drug Adminis­tration. AAPS J. 2012; 14(4): 915–24. doi:10.1208/s12248-012-9406-x.↩︎

  24. At a \(\small{CV_{\textrm{wR}}}\) which is infinitesimally lower than \(\small{CV_{\textrm{wR}}\;0.30047}\) the ‘implied limits’ are still 80.00 – 125.00% but jump to 76.92 – 130.01% at \(\small{CV_{\textrm{wR}}\approx0.30047}\).↩︎

  25. That’s contrary to methods for ABE, where the CV is an assumption as well.↩︎

  26. Hoenig JM, Heisey DM. The Abuse of Power: The Pervasive Fallacy of Power Calculations for Data Analysis. Am Stat. 2001; 55(1): 19–24. doi:10.1198/000313001300339897.↩︎

  27. There is no statistical method to ‘correct’ for unequal carryover. It can only be avoided by design, i.e., a sufficiently long washout between periods. According to the guidelines subjects with pre-dose concentrations > 5% of their Cmax can by excluded from the comparison if stated in the protocol.↩︎

  28. Zhang P. A Simple Formula for Sample Size Calculation in Equivalence Studies. J Biopharm Stat. 2003; 13(3): 529–538. doi:10.1081/BIP-120022772.↩︎

  29. Don’t be tempted to give a ‘better’ T/R-ratio – even if based on a pilot or a previous study. It is a natural property of HVD(P)s that the T/R-ratio varies between studies. Don’t be overly optimistic!↩︎

  30. Schütz H. Sample Size Estimation in Bioequivalence. Evaluation. 2020-10-23. BEBA Forum.↩︎

  31. The only exception is design = "2x2x3" (the 3-period full replicate with 3 periods and sequences TRT|RTR). Then the first element is for sequence TRT and the second for RTR.↩︎

  32. Quoting my late father: »If you believe, go to church.«↩︎

  33. Berger RL, Hsu JC. Bioequivalence Trials, Intersection-Union Tests and Equivalence Confidence Sets. Stat Sci. 1996; 11(4): 283–302. JSTOR:2246021.↩︎

  34. Zeng A. The TOST confidence intervals and the coverage probabilities with R simulation. March 14, 2014.↩︎

  35. Tóthfalusi L, Endrényi L. Sample Sizes for Designing Bioequivalence Studies for Highly Variable Drugs. J Pharm Pharmacol Sci. 2012; 15(1): 73–84. doi:10.18433/j3z88f. Open access.↩︎