Guidance for Industry

Statistical Approaches to

Establishing Bioequivalence

U.S. Department of Health and Human Services

Food and Drug Administration

Center for Drug Evaluation and Research (CDER)

January 2001

BP
Guidance for Industry

Statistical Approaches to

Establishing Bioequivalence

Additional copies are available from:

Office of Training and Communications

Division of Communications Management

Drug Information Branch, HFD-210

5600 Fishers Lane

Rockville MD 20857

(Tel) 301-827-4573

(Internet) http://www.fda.gov/cder/guidance/index.htm

U.S. Department of Health and Human Services

Food and Drug Administration

Center for Drug Evaluation and Research (CDER)

January 2001

BP
Table of Contents

I. INTRODUCTION..................................................................................................................................................................1

II. BACKGROUND....................................................................................................................................................................1

A. GENERAL............................................................................................................................................................................. 1

B. STATISTICAL ...................................................................................................................................................................... 2

III. STATISTICAL MODEL......................................................................................................................................................3

IV. STATISTICAL APPROACHES FOR BIOEQUIVALENCE.........................................................................................3

A. AVERAGE BIOEQUIVALENCE.............................................................................................................................................. 4

B. POPULATION BIOEQUIVALENCE ......................................................................................................................................... 5

C. INDIVIDUAL BIOEQUIVALENCE ........................................................................................................................................... 6

V. STUDY DESIGN....................................................................................................................................................................7

A. EXPERIMENTAL DESIGN..................................................................................................................................................... 7

B. SAMPLE SIZE AND DROPOUTS........................................................................................................................................... 8

VI. STATISTICAL ANALYSIS ................................................................................................................................................9

A. LOGARITHMIC TRANSFORMATION .................................................................................................................................... 9

B. DATA ANALYSIS .............................................................................................................................................................. 10

VII. MISCELLANEOUS ISSUES ........................................................................................................................................13

A. STUDIES IN MULTIPLE GROUPS....................................................................................................................................... 13

B. CARRYOVER EFFECTS...................................................................................................................................................... 13

C. OUTLIER CONSIDERATIONS ............................................................................................................................................. 14

D. DISCONTINUITY................................................................................................................................................................ 15

REFERENCES ................................................................................................................................................................................16

APPENDIX A..................................................................................................................................................................................21

APPENDIX B..................................................................................................................................................................................25

APPENDIX C..................................................................................................................................................................................28

APPENDIX D..................................................................................................................................................................................32

APPENDIX E..................................................................................................................................................................................34

APPENDIX F..................................................................................................................................................................................35

APPENDIX G..................................................................................................................................................................................40

APPENDIX H..................................................................................................................................................................................45
J:\!GUIDANC\3616fnl.doc

01/31/01

GUIDANCE FOR INDUSTRY1

Statistical Approaches

to Establishing Bioequivalence

I. INTRODUCTION

This guidance provides recommendations to sponsors and applicants who intend, either before or after

approval, to use equivalence criteria in analyzing in vivo or in vitro bioequivalence (BE) studies for

investigational new drug applications (INDs), new drug applications (NDAs), abbreviated new drug

applications (ANDAs) and supplements to these applications. This guidance discusses three

approaches for BE comparisons: average, population, and individual. The guidance focuses on how to

use each approach once a specific approach has been chosen. This guidance replaces a prior FDA

guidance entitled Statistical Procedures for Bioequivalence Studies Using a Standard TwoTreatment Crossover Design, which was issued in July 1992.

II. BACKGROUND

A. General

Requirements for submitting bioavailability (BA) and BE data in NDAs, ANDAs, and

supplements, the definitions of BA and BE, and the types of in vivo studies that are appropriate

to measure BA and establish BE are set forth in 21 CFR part 320. This guidance provides

recommendations on how to meet provisions of part 320 for all drug products.

Defined as relative BA, BE involves comparison between a test (T) and reference (R) drug

product, where T and R can vary, depending on the comparison to be performed (e.g., to-bemarketed dosage form versus clinical trial material, generic drug versus reference listed drug,

 

1

This guidance has been prepared by the Population and Individual Bioequivalence Working Group of the

Biopharmaceutics Coordinating Committee in the Office of Pharmaceutical Science, Center for Drug Evaluation and

Research (CDER) at the Food and Drug Administration (FDA).

This guidance represents the Food and Drug Administration's current thinking on this topic. It

does not create or confer any rights for or on any person and does not operate to bind FDA or the

public. An alternative approach may be used if such approach satisfies the requirements of the

applicable statutes and regulations.
2

drug product changed after approval versus drug product before the change). Although BA

and BE are closely related, BE comparisons normally rely on (1) a criterion, (2) a confidence

interval for the criterion, and (3) a predetermined BE limit. BE comparisons could also be used

in certain pharmaceutical product line extensions, such as additional strengths, new dosage

forms (e.g., changes from immediate release to extended release), and new routes of

administration. In these settings, the approaches described in this guidance can be used to

determine BE. The general approaches discussed in this guidance may also be useful when

assessing pharmaceutical equivalence or performing equivalence comparisons in clinical

pharmacology studies and other areas.

B. Statistical

In the July 1992 guidance on Statistical Procedures for Bioequivalence Studies Using a

Standard Two-Treatment Crossover Design (the 1992 guidance), CDER recommended that

a standard in vivo BE study design be based on the administration of either single or multiple

doses of the T and R products to healthy subjects on separate occasions, with random

assignment to the two possible sequences of drug product administration. The 1992 guidance

further recommended that statistical analysis for pharmacokinetic measures, such as area under

the curve (AUC) and peak concentration (Cmax), be based on the two one-sided tests

procedure to determine whether the average values for the pharmacokinetic measures

determined after administration of the T and R products were comparable. This approach is

termed average bioequivalence and involves the calculation of a 90% confidence interval for

the ratio of the averages (population geometric means) of the measures for the T and R

products. To establish BE, the calculated confidence interval should fall within a BE limit,

usually 80-125% for the ratio of the product averages.2 In addition to this general approach,

the 1992 guidance provided specific recommendations for (1) logarithmic transformation of

pharmacokinetic data, (2) methods to evaluate sequence effects, and (3) methods to evaluate

outlier data.

Although average BE is recommended for a comparison of BA measures in most BE studies,

this guidance describes two new approaches, termed population and individual

bioequivalence. These new approaches may be useful, in some instances, for analyzing

in vitro and in vivo BE studies.3 The average BE approach focuses only on the comparison of

population averages of a BE measure of interest and not on the variances of the measure for the

 

2

 For a broad range of drugs, a BE limit of 80 to 125% for the ratio of the product averages has been adopted

for use of an average BE criterion. Generally, the BE limit of 80 to 125% is based on a clinical judgment that a test

product with BA measures outside this range should be denied market access. 

3

 For additional recommendations on in vivo studies, see the FDA guidance for industry on Bioavailability

and Bioequivalence Studies for Orally Administered Drug Products C General Considerations. Additional

recommendations on in vitro studies will be provided in an FDA guidance for industry on Bioavailability and

Bioequivalence Studies for Nasal Aerosols and Nasal Sprays for Local Action, when finalized.
3

T and R products. The average BE method does not assess a subject-by-formulation

interaction variance, that is, the variation in the average T and R difference among individuals. 

In contrast, population and individual BE approaches include comparisons of both averages and

variances of the measure. The population BE approach assesses total variability of the measure

in the population. The individual BE approach assesses within-subject variability for the T and

R products, as well as the subject-by-formulation interaction.

III. STATISTICAL MODEL

Statistical analyses of BE data are typically based on a statistical model for the logarithm of the BA

measures (e.g., AUC and Cmax). The model is a mixed-effects or two-stage linear model. Each

subject, j, theoretically provides a mean for the log-transformed BA measure for each formulation, μTj

and μRj for the T and R formulations, respectively. The model assumes that these subject-specific

means come from a distribution with population means μT and μR, and between-subject variances σBT

2

and σBR

2

, respectively. The model allows for a correlation, ρ, between μTj and μRj. The subject-byformulation interaction variance component (Schall and Luus 1993), σD

2

, is related to these parameters

as follows:

σD

2 = variance of (μTj - μRj)

 = (σBT - σBR)

2

 + 2 (1-ρ)σBTσBR Equation 1

For a given subject, the observed data for the log-transformed BA measure are assumed to be

independent observations from distributions with means μTj and μRj, and within-subject variances σWT

2

and σWR

2

. The total variances for each formulation are defined as the sum of the within- and betweensubject components (i.e., σTT

2

 = σWT

2

 + σBT

2

 and σTR

2

 = σWR

2

 + σBR

2

). For analysis of crossover

studies, the means are given additional structure by the inclusion of period and sequence effect terms.

IV. STATISTICAL APPROACHES FOR BIOEQUIVALENCE

The general structure of a BE criterion is that a function (Θ) of population measures should be

demonstrated to be no greater than a specified value (θ). Using the terminology of statistical hypothesis

testing, this is accomplished by testing the hypothesis H0: Θ>θ versus HA: Θ#θ at a desired level of

significance, often 5%. Rejection of the null hypothesis H0 (i.e., demonstrating that the estimate of Θ is

statistically significantly less than θ) results in a conclusion of BE. The choice of Θ and θ differs in

average, population, and individual BE approaches.

A general objective in assessing BE is to compare the log-transformed BA measure after administration

of the T and R products. As detailed in Appendix A, population and individual approaches are based

on the comparison of an expected squared distance between the T and R formulations to the expected
4

squared distance between two administrations of the R formulation. An acceptable T formulation is one

where the T-R distance is not substantially greater than the R-R distance. In both population and

individual BE approaches, this comparison appears as a comparison to the reference variance, which is

referred to as scaling to the reference variability.

Population and individual BE approaches, but not the average BE approach, allow two types of scaling:

 reference-scaling and constant-scaling. Reference-scaling means that the criterion used is scaled to the

variability of the R product, which effectively widens the BE limit for more variable reference products. 

Although generally sufficient, use of reference-scaling alone could unnecessarily narrow the BE limit for

drugs and/or drug products that have low variability but a wide therapeutic range. This guidance,

therefore, recommends mixed-scaling for the population and individual BE approaches (section IV.B

and C). With mixed scaling, the reference-scaled form of the criterion should be used if the reference

product is highly variable; otherwise, the constant-scaled form should be used.

A. Average Bioequivalence

The following criterion is recommended for average BE:

(μT - μR)

2

# θA

2 Equation 2

where

μT = population average response of the log-transformed measure for the T

 formulation

μR = population average response of the log-transformed measure for the R

 formulation

as defined in section III above.
5

This criterion is equivalent to:

-θA # (μT - μR) # θA Equation 3

and, usually, θA = ln(1.25).

B. Population Bioequivalence

The following mixed-scaling approach is recommended for population BE (i.e., use the

reference-scaled method if the estimate of σTR > σT0 and the constant-scaled method if the

estimate of σTR # σT0). 

The recommended criteria are:

! Reference-Scaled:

 (μT - μR)

2

 + (σTT

2

 - σTR

2

)

-------------------------------- # θp Equation 4

 σTR

2

or

! Constant-Scaled:

 (μT - μR)

2

 + (σTT

2

 - σTR

2

)

-------------------------------- # θp Equation 5

 σT0

2

where:

μT = population average response of the log-transformed measure

 for the T formulation

μR = population average response of the log-transformed measure

 for the R formulation

σTT

2

= total variance (i.e., sum of within- and between-subject

 variances) of the T formulation

σTR

2

= total variance (i.e., sum of within- and between-subject

 variances) of the R formulation

σT0

2

= specified constant total variance

θp = BE limit
6

Equations 4 and 5 represent an aggregate approach where a single criterion on the left-hand

side of the equation encompasses two major components: (1) the difference between the T and

R population averages (μT - μR), and (2) the difference between the T and R total variances

(σTT

2

 - σTR

2

). This aggregate measure is scaled to the total variance of the R product or to a

constant value (σT0

2

, a standard that relates to a limit for the total variance), whichever is

greater.

The specification of both σT0 and θP relies on the establishment of standards. The generation of

these standards is discussed in Appendix A. When the population BE approach is used, in

addition to meeting the BE limit based on confidence bounds, the point estimate of the

geometric test/reference mean should fall within 80-125%.

C. Individual Bioequivalence

The following mixed-scaling approach is one approach for individual BE (i.e., use the referencescaled method if the estimate of σWR > σW0, and the constant-scaled method if the estimate of

σWR # σW0). Also see section VII.D, Discontinuity, for further discussion.

The recommended criteria are:

! Reference-Scaled:

 (μT - μR)

2

 + σD

2

 + (σWT

2

 - σWR

2

)

----------------------------------------- # θI Equation 6

 σWR

2

or

! Constant-Scaled:

 (μT - μR)

2

 + σD

2

 + (σWT

2

 - σWR

2

)

----------------------------------------- # θI Equation 7

 σW0

2

where:

μT = population average response of the log-transformed measure

 for the T formulation

μR = population average response of the log-transformed measure

 for the R formulation

σD

2

= subject-by-formulation interaction variance component
7

σWT

2

= within-subject variance of the T formulation

σWR

2

= within-subject variance of the R formulation

σW0

2

= specified constant within-subject variance

θI = BE limit

Equations 6 and 7 represent an aggregate approach where a single criterion on the left-hand

side of the equation encompasses three major components: (1) the difference between the T

and R population averages (μT - μR), (2) subject-by-formulation interaction (σD

2

), and (3) the

difference between the T and R within-subject variances (σWT

2

 - σWR

2

). This aggregate

measure is scaled to the within-subject variance of the R product or to a constant value (σW0

2

, a

standard that relates to a limit for the within-subject variance), whichever is greater.

The specification of both σW0 and θI relies on the establishment of standards. The generation of

these standards is discussed in Appendix A. When the individual BE approach is used, in

addition to meeting the BE limit based on confidence bounds, the point estimate of the

geometric test/reference mean ratio should fall within 80-125%.

V. STUDY DESIGN

A. Experimental Design

1. Nonreplicated Designs

A conventional nonreplicated design, such as the standard two-formulation, two-period,

two-sequence crossover design, can be used to generate data where an average or

population approach is chosen for BE comparisons. Under certain circumstances,

parallel designs can also be used.

2. Replicated Crossover Designs

Replicated crossover designs can be used irrespective of which approach is selected to

establish BE, although they are not necessary when an average or population approach

is used. Replicated crossover designs are critical when an individual BE approach is

used to allow estimation of within-subject variances for the T and R measures and the

subject-by-formulation interaction variance component. The following four-period,

two-sequence, two-formulation design is recommended for replicated BE studies (see

Appendix B for further discussion of replicated crossover designs).
8

Period

1 2 3 4

1 T R T R

Sequence

2 R T R T

For this design, the same lots of the T and R formulations should be used for the

replicated administration. Each period should be separated by an adequate washout

period.

Other replicated crossover designs are possible. For example, a three-period design,

as shown below, could be used.

 Period

1 2 3

1 T R T

Sequence

2 R T R

A greater number of subjects would be encouraged for the three-period design

compared to the recommended four-period design to achieve the same statistical power

to conclude BE (see Appendix C).

B. Sample Size and Dropouts

A minimum number of 12 evaluable subjects should be included in any BE study. When an

average BE approach is selected using either nonreplicated or replicated designs, methods

appropriate to the study design should be used to estimate sample sizes. The number of

subjects for BE studies based on either the population or individual BE approach can be

estimated by simulation if analytical approaches for estimation are not available. Further

information on sample size is provided in Appendix C. 

Sponsors should enter a sufficient number of subjects in the study to allow for dropouts. 

Because replacement of subjects during the study could complicate the statistical model and

analysis, dropouts generally should not be replaced. Sponsors who wish to replace dropouts

during the study should indicate this intention in the protocol. The protocol should also state
9

whether samples from replacement subjects, if not used, will be assayed. If the dropout rate is

high and sponsors wish to add more subjects, a modification of the statistical analysis may be

recommended. Additional subjects should not be included after data analysis unless the trial

was designed from the beginning as a sequential or group sequential design.

VI. STATISTICAL ANALYSIS

The following sections provide recommendations on statistical methodology for assessment of average,

population, and individual BE.

A. Logarithmic Transformation

1. General Procedures

This guidance recommends that BE measures (e.g., AUC and Cmax) be logtransformed using either common logarithms to the base 10 or natural logarithms (see

Appendix D). The choice of common or natural logs should be consistent and should

be stated in the study report. The limited sample size in a typical BE study precludes a

reliable determination of the distribution of the data set. Sponsors and/or applicants are

not encouraged to test for normality of error distribution after log-transformation, nor

should they use normality of error distribution as a reason for carrying out the statistical

analysis on the original scale. Justification should be provided if sponsors or applicants

believe that their BE study data should be statistically analyzed on the original rather

than on the log scale.

2. Presentation of Data

The drug concentration in biological fluid determined at each sampling time point should

be furnished on the original scale for each subject participating in the study. The

pharmacokinetic measures of systemic exposure should also be furnished on the original

scale. The mean, standard deviation, and coefficient of variation for each variable

should be computed and tabulated in the final report. 

In addition to the arithmetic mean and associated standard deviation (or coefficient of

variation) for the T and R products, geometric means (antilog of the means of the logs)

should be calculated for selected BE measures. To facilitate BE comparisons, the

measures for each individual should be displayed in parallel for the formulations tested. 

In particular, for each BE measure the ratio of the individual geometric mean of the T

product to the individual geometric mean of the R product should be tabulated side by

side for each subject. The summary tables should indicate in which sequence each
10

subject received the product. 

B. Data Analysis

1. Average Bioequivalence

a. Overview

Parametric (normal-theory) methods are recommended for the analysis of logtransformed BE measures. For average BE using the criterion stated in

equations 2 or 3 (section III.A), the general approach is to construct a 90%

confidence interval for the quantity μT-μR and to reach a conclusion of average

BE if this confidence interval is contained in the interval [-θA , θA]. Due to the

nature of normal-theory confidence intervals, this is equivalent to carrying out

two one-sided tests of hypothesis at the 5% level of significance (Schuirmann

1987).

The 90% confidence interval for the difference in the means of the logtransformed data should be calculated using methods appropriate to the

experimental design. The antilogs of the confidence limits obtained constitute

the 90% confidence interval for the ratio of the geometric means between the T

and R products.

b. Nonreplicated Crossover Designs

For nonreplicated crossover designs, this guidance recommends parametric

(normal-theory) procedures to analyze log-transformed BA measures. General

linear model procedures available in PROC GLM in SAS or equivalent

software are preferred, although linear mixed-effects model procedures can also

be indicated for analysis of nonreplicated crossover studies. 

For example, for a conventional two-treatment, two-period, two-sequence (2 x

2) randomized crossover design, the statistical model typically includes factors

accounting for the following sources of variation: sequence, subjects nested in

sequences, period, and treatment. The Estimate statement in SAS PROC

GLM, or equivalent statement in other software, should be used to obtain

estimates for the adjusted differences between treatment means and the

standard error associated with these differences.

c. Replicated Crossover Designs
11

Linear mixed-effects model procedures, available in PROC MIXED in SAS or

equivalent software, should be used for the analysis of replicated crossover

studies for average BE. Appendix E includes an example of SAS program

statements.

d. Parallel Designs

For parallel designs, the confidence interval for the difference of means in the

log scale can be computed using the total between-subject variance. As in the

analysis for replicated designs (section VI. B.1.b), equal variances should not

be assumed.

2. Population Bioequivalence

a. Overview

Analysis of BE data using the population approach (section IV.B) should focus

first on estimation of the mean difference between the T and R for the logtransformed BA measure and estimation of the total variance for each of the

two formulations. This can be done using relatively simple unbiased estimators

such as the method of moments (MM) (Chinchilli 1996, and Chinchilli and

Esinhart 1996). After the estimation of the mean difference and the variances

has been completed, a 95% upper confidence bound for the population BE

criterion can be obtained, or equivalently a 95% upper confidence bound for a

linearized form of the population BE criterion can be obtained. Population BE

should be considered to be established for a particular log-transformed BA

measure if the 95% upper confidence bound for the criterion is less than or

equal to the BE limit, θP, or equivalently if the 95% upper confidence bound for

the linearized criterion is less than or equal to 0. 

To obtain the 95% upper confidence bound of the criterion, intervals based on

validated approaches can be used. Validation approaches should be reviewed

with appropriate staff in CDER. Appendix F includes an example of upper

confidence bound determination using a population BE approach.

b. Nonreplicated Crossover Designs

For nonreplicated crossover studies, any available method (e.g., SAS PROC

GLM or equivalent software) can be used to obtain an unbiased estimate of the

mean difference in log-transformed BA measures between the T and R

products. The total variance for each formulation should be estimated by the
12

usual sample variance, computed separately in each sequence and then pooled

across sequences.

c. Replicated Crossover Designs

For replicated crossover studies, the approach should be the same as for

nonreplicated crossover designs, but care should be taken to obtain proper

estimates of the total variances. One approach is to estimate the within- and

between-subject components separately, as for individual BE (see section

VI.B.3), and then sum them to obtain the total variance. The method for the

upper confidence bound should be consistent with the method used for

estimating the variances. 

d. Parallel Designs

The estimate of the means and variances from parallel designs should be the

same as for nonreplicated crossover designs. The method for the upper

confidence bound should be modified to reflect independent rather than paired

samples and to allow for unequal variances.

3. Individual Bioequivalence

Analysis of BE data using an individual BE approach (section IV.C) should focus on

estimation of the mean difference between T and R for the log-transformed BA

measure, the subject-by-formulation interaction variance, and the within-subject

variance for each of the two formulations. For this purpose, we recommend the MM

approach.

To obtain the 95% upper confidence bound of a linearized form of the individual BE

criterion, intervals based on validated approaches can be used. An example is

described in Appendix G. After the estimation of the mean difference and the variances

has been completed, a 95% upper confidence bound for the individual BE criterion can

be obtained, or equivalently a 95% upper confidence bound for a linearized form of the

individual BE criterion can be obtained. Individual BE should be considered to be

established for a particular log-transformed BA measure if the 95% upper confidence

bound for the criterion is less than or equal to the BE limit, θI, or equivalently if the 95%

upper confidence bound for the linearized criterion is less than or equal to 0. 

The restricted maximum likelihood (REML) method may be useful to estimate mean

differences and variances when subjects with some missing data are included in the

statistical analysis. A key distinction between the REML and MM methods relates to
13

differences in estimating variance terms and is further discussed in Appendix H. 

Sponsors considering alternative methods to REML or MM are encouraged to discuss

their approaches with appropriate CDER review staff prior to submitting their

applications.

VII. MISCELLANEOUS ISSUES

A. Studies in Multiple Groups

If a crossover study is carried out in two or more groups of subjects (e.g., if for logistical

reasons only a limited number of subjects can be studied at one time), the statistical model

should be modified to reflect the multigroup nature of the study. In particular, the model should

reflect the fact that the periods for the first group are different from the periods for the second

group. This applies to all of the approaches (average, population, and individual BE) described

in this guidance.

If the study is carried out in two or more groups and those groups are studied at different clinical

sites, or at the same site but greatly separated in time (months apart, for example), questions

may arise as to whether the results from the several groups should be combined in a single

analysis. Such cases should be discussed with the appropriate CDER review division.

A sequential design, in which the decision to study a second group of subjects is based on the

results from the first group, calls for different statistical methods and is outside the scope of this

guidance. Those wishing to use a sequential design should consult the appropriate CDER

review division.

B. Carryover Effects

Use of crossover designs for BE studies allows each subject to serve as his or her own control

to improve the precision of the comparison. One of the assumptions underlying this principle is

that carryover effects (also called residual effects) are either absent (the response to a

formulation administered in a particular period of the design is unaffected by formulations

administered in earlier periods) or equal for each formulation and preceding formulation. If

carryover effects are present in a crossover study and are not equal, the usual crossover

estimate of μT-μR could be biased. One limitation of a conventional two-formulation, twoperiod, two-sequence crossover design is that the only statistical test available for the presence

of unequal carryover effects is the sequence test in the analysis of variance (ANOVA) for the

crossover design. This is a between-subject test, which would be expected to have poor

discriminating power in a typical BE study. Furthermore, if the possibility of unequal carryover

effects cannot be ruled out, no unbiased estimate of μT-μR based on within-subject
14

comparisons can be obtained with this design.

For replicated crossover studies, a within-subject test for unequal carryover effects can be

obtained under certain assumptions. Typically only first-order carryover effects are considered

of concern (i.e., the carryover effects, if they occur, only affect the response to the formulation

administered in the next period of the design). Under this assumption, consideration of

carryover effects could be more complicated for replicated crossover studies than for

nonreplicated studies. The carryover effect could depend not only on the formulation that

preceded the current period, but also on the formulation that is administered in the current

period. This is called a direct-by-carryover interaction. The need to consider more than just

simple first-order carryover effects has been emphasized (Fleiss 1989). With a replicated

crossover design, a within-subject estimate of μT-μR unbiased by general first-order carryover

effects can be obtained, but such an estimate could be imprecise, reducing the power of the

study to conclude BE.

In most cases, for both replicated and nonreplicated crossover designs, the possibility of

unequal carryover effects is considered unlikely in a BE study under the following circumstances:

! It is a single-dose study. 

! The drug is not an endogenous entity.

! More than an adequate washout period has been allowed between periods of the study

and in the subsequent periods the predose biological matrix samples do not exhibit a

detectable drug level in any of the subjects.

! The study meets all scientific criteria (e.g., it is based on an acceptable study protocol

and it contains sufficient validated assay methodology).

The possibility of unequal carryover effects can also be discounted for multiple-dose studies

and/or studies in patients, provided that the drug is not an endogenous entity and the studies

meet all scientific criteria as described above. Under all other circumstances, the sponsor or

applicant could be asked to consider the possibility of unequal carryover effects, including a

direct-by-carryover interaction. If there is evidence of carryover effects, sponsors should

describe their proposed approach in the study protocol, including statistical tests for the

presence of such effects and procedures to be followed. Sponsors who suspect that carryover

effects might be an issue may wish to conduct a BE study with parallel designs.

C. Outlier Considerations

Outlier data in BE studies are defined as subject data for one or more BA measures that are
15

discordant with corresponding data for that subject and/or for the rest of the subjects in a study.

 Because BE studies are usually carried out as crossover studies, the most important type of

subject outlier is the within-subject outlier, where one subject or a few subjects differ notably

from the rest of the subjects with respect to a within-subject T-R comparison. The existence of

a subject outlier with no protocol violations could indicate one of the following situations:

1. Product Failure

Product failure could occur, for example, when a subject exhibits an unusually high or

low response to one or the other of the products because of a problem with the specific

dosage unit administered. This could occur, for example, with a sustained and/or

delayed-release dosage form exhibiting dose dumping or a dosage unit with a coating

that inhibits dissolution.

2. Subject-by-Formulation Interaction

A subject-by-formulation interaction could occur when an individual is representative of

subjects present in the general population in low numbers, for whom the relative BA of

the two products is markedly different than for the majority of the population, and for

whom the two products are not bioequivalent, even though they might be bioequivalent

in the majority of the population.

In the case of product failure, the unusual response could be present for either the T or R

product. However, in the case of a subpopulation, even if the unusual response is observed on

the R product, there could still be concern for lack of interchangeability of the two products. 

For these reasons, deletion of outlier values is generally discouraged, particularly for

nonreplicated designs. With replicated crossover designs, the retest character of these designs

should indicate whether to delete an outlier value or not. Sponsors or applicants with these

types of data sets may wish to review how to handle outliers with appropriate review staff.

D. Discontinuity

The mixed-scaling approach has a discontinuity at the changeover point, σW0 (individual BE

criterion) or σT0 (population BE criterion), from constant- to reference-scaling. For example, if

the estimate of the within-subject standard deviation of the reference is just above the

changeover point, the confidence interval will be wider than just below. In this context, the

confidence interval could pass the predetermined BE limit if the estimate is just below the

boundary and could fail if just above. This guidance recommends that sponsors applying the

individual BE approach may use either reference-scaling or constant-scaling at either side of the

changeover point. With this approach, the multiple testing inflates the type I error rate slightly,

to approximately 6.5%, but only over a small interval of σWR (about 0.18-0.20).
16

REFERENCES

Anderson, S., and W.W. Hauck, 1990, "Consideration of Individual Bioequivalence," J.

Pharmacokin. Biopharm., 18:259-73.

Anderson, S., 1993, "Individual Bioequivalence: A Problem of Switchability (with discussion),"

Biopharmaceutical Reports, 2(2):1-11.

Anderson, S., 1995, "Current Issues of Individual Bioequivalence," Drug Inf. J., 29:961-4.

Chen, M.-L., 1997, "Individual Bioequivalence — A Regulatory Update (with discussion)," J.

Biopharm. Stat., 7:5-111.

Chen, M.-L., R. Patnaik, W.W. Hauck, D.J. Schuirmann, T. Hyslop, R.L. Williams, and the FDA

Population and Individual Bioequivalence Working Group, 2000, AAn Individual Bioequivalence

Criterion: Regulatory Considerations,@ Stat. Med., 19:2821-42.

Chen, M.-L., S.-C. Lee, M.-J. Ng, D.J. Schuirmann, L. J. Lesko, and R.L. Williams, 2000,

"Pharmacokinetic analysis of bioequivalence trials: Implications for sex-related issues in clinical

pharmacology and biopharmaceutics," Clin. Pharmacol. Ther., 68(5):510-21.

Chinchilli, V.M., 1996, "The Assessment of Individual and Population Bioequivalence," J. Biopharm.

Stat., 6:1-14.

Chinchilli, V.M., and J.D. Esinhart, 1996, ADesign and Analysis of Intra-Subject Variability in CrossOver Experiments,@ Stat. Med., 15:1619-34.

Chow, S.-C., 1999, AIndividual Bioequivalence — A Review of the FDA Draft Guidance,@ Drug Inf.

J., 33:435-44.

Diletti E., D. Hauschke, and V.W. Steinijans, 1991, ASample Size Determination for Bioequivalence

Assessment By Means of Confidence Intervals,@ Int. J. Clin. Pharmacol. Therap., 29:1-8.

Efron, B., 1987, "Better Bootstrap Confidence Intervals (with discussion)," J. Amer. Stat. Assoc.,

82:171-201.

Efron, B., and R.J. Tibshirani, 1993, An Introduction to the Bootstrap, Chapman and Hall, Ch. 14.
17

Ekbohm, G., and H. Melander, 1989, "The Subject-by-Formulation Interaction as a Criterion for

Interchangeability of Drugs," Biometrics, 45:1249-54.

Ekbohm, G., and H. Melander, 1990, "On Variation, Bioequivalence and Interchangeability," Report

14, Department of Statistics, Swedish University of Agricultural Sciences.

Endrenyi, L., and M. Schulz, 1993, "Individual Variation and the Acceptance of Average

Bioequivalence," Drug Inf. J., 27:195-201.

Endrenyi, L., 1993, "A Procedure for the Assessment of Individual Bioequivalence," in BioInternational: Bioavailability, Bioequivalence and Pharmacokinetics (H.H.Blume, K.K. Midha,

eds.), Medpharm Publications, 141-6.

Endrenyi, L., 1994, "A Method for the Evaluation of Individual Bioequivalence," Int. J. Clin.

Pharmacol. Therap., 32:497-508.

Endrenyi, L., 1995, "A Simple Approach for the Evaluation of Individual Bioequivalence," Drug Inf. J.,

29:847-55.

Endrenyi, L., and K.K. Midha, 1998, AIndividual Bioequivalence — Has Its Time Come?,@ Eur. J.

Pharm. Sci., 6:271-8.

Endrenyi, L., G.L. Amidon, K.K. Midha, and J.P. Skelly, 1998, AIndividual Bioequivalence: Attractive

in Principle, Difficult in Practice,@ Pharm. Res., 15:1321-5.

Endrenyi, L., and Y. Hao, 1998, AAsymmetry of the Mean-Variability Tradeoff Raises Questions

About the Model in Investigations of Individual Bioequivalence,@ Int. J. Pharmacol. Therap., 36:450-

7.

Endrenyi, L., and L. Tothfalusi, 1999, ASubject-by-Formulation Interaction in Determination of

Individual Bioequivalence: Bias and Prevalence,@ Pharm. Res., 16:186-8.

Esinhart, J.D., and V.M. Chinchilli, 1994, "Sample Size Considerations for Assessing Individual

Bioequivalence Based on the Method of Tolerance Interval," Int. J. Clin. Pharmacol. Therap.,

32(1):26-32.

Esinhart, J.D., and V.M. Chinchilli, 1994, "Extension to the Use of Tolerance Intervals for the

Assessment of Individual Bioequivalence," J. Biopharm. Stat., 4(1):39-52.

Fleiss, J.L., 1989, AA Critique of Recent Research on the Two-Treatment Crossover Design,@

Controlled Clinical Trials, 10:237-43.
18

Graybill, F., and C.M. Wang, 1980, AConfidence Intervals on Nonnegative Linear Combinations of

Variances,@ J. Amer. Stat. Assoc., 75:869-73.

Hauck, W.W., and S. Anderson, 1984, "A New Statistical Procedure for Testing Equivalence in TwoGroup Comparative Bioavailability Trials," J. Pharmacokin. Biopharm., 12:83-91.

Hauck, W.W., and S. Anderson, 1992, "Types of Bioequivalence and Related Statistical

Considerations," Int. J. Clin. Pharmacol. Therap., 30:181-7.

Hauck, W.W., and S. Anderson, 1994, "Measuring Switchability and Prescribability: When is Average

Bioequivalence Sufficient?," J. Pharmacokin. Biopharm., 22:551-64.

Hauck, W.W., M.-L. Chen, T. Hyslop, R. Patnaik, D. Schuirmann, and R.L. Williams for the FDA

Population and Individual Bioequivalence Working Group, 1996, AMean Difference vs. Variability

Reduction: Tradeoffs in Aggregate Measures for Individual Bioequivalence," Int. J. Clin. Pharmacol.

Therap., 34:535-41.

Holder, D.J., and F. Hsuan, 1993, "Moment-Based Criteria for Determining Bioequivalence,"

Biometrika, 80:835-46.

Holder, D.J., and F. Hsuan, 1995, "A Moment-Based Method for Determining Individual

Bioequivalence," Drug Inf. J., 29:965-79.

Howe, W.G., 1974. AApproximate Confidence Limits on the Mean of X+Y Where X and Y are Two

Tabled Independent Random Variables,@ J. Amer. Stat. Assoc., 69:789-94.

Hsu, J.C., J.T.G. Hwang, H.-K. Liu, and S.J. Ruberg, 1994, AConfidence Intervals Associated with

Tests for Bioequivalence,@ Biometrika, 81:103-14.

Hwang, S., P.B. Huber, M. Hesney, and K.C. Kwan, 1978, "Bioequivalence and Interchangeability,"

J. Pharm. Sci., 67:IV "Open Forum."

Hyslop, T., F. Hsuan, and D.J. Holder, 2000, AA Small-Sample Confidence Interval Approach to

Assess Individual Bioequivalence,@ Stat. Med., 19:2885-97.

Kimanani, E.K., and D. Potvin, 1998, AParametric Confidence Interval for a Moment-Based Scaled

Criterion for Individual Bioequivalence,@ J. Pharm. Biopharm., 25:595-614.

Liu, J.-P, 1995, AUse of the Repeated Crossover Designs in Assessing Bioequivalence,@ Stat. Med.,

14:1067-78.
19

Patnaik, R. N., L.J. Lesko, M.-L. Chen, R.L. Williams, and the FDA Population and Individual

Bioequivalence Working Group, 1997, "Individual Bioequivalence: New Concepts in the Statistical

Assessment of Bioequivalence Metrics," Clin. Pharmacokin., 33:1-6.

Schall, R., 1995, "Unified View of Individual, Population and Average Bioequivalence," in BioInternational 2: Bioavailability, Bioequivalence and Pharmacokinetic Studies (H.H.Blume,

K.K.Midha, eds.), Medpharm Scientific Publishers, 91-105.

Schall, R., and H.G. Luus, 1993, AOn Population and Individual Bioequivalence,@ Stat. Med., 12:1109-

24.

Schall R., 1995, "Assessment of Individual and Population Bioequivalence Using the Probability That

Bioavailabilities Are Similar," Biometrics, 51:615-26.

Schall, R., and R.L. Williams for the FDA Individual Bioequivalence Working Group, 1996, "Towards

a Practical Strategy for Assessing Individual Bioequivalence," J. Pharmacokin. Biopharm, 24:133-49.

Schuirmann, D.J., 1987, "A Comparison of the Two One-Sided Tests Procedure and the Power

Approach for Assessing the Equivalence of Average Bioavailability,@ J. Pharmacokin. Biopharm.,

15:657-80.

Schuirmann, D.J., 1989, "Treatment of Bioequivalence Data: Log Transformation," in Proceedings of

Bio-International '89 — Issues in the Evaluation of Bioavailability Data, Toronto, Canada,

October 1-4, 159-61.

Senn, S., and D. Lambrou, 1998, ARobust and Realistic Approaches to Carry-Over,@ Stat. Med.,

17:2849-64.

Sheiner, L. B., 1992, "Bioequivalence Revisited," Stat. Med., 11:1777-88.

Ting, N., R.K. Burdick, F.A. Graybill, S. Jeyaratnam, and T.F.C. Lu, 1990, AConfidence Intervals on

Linear Combinations of Variance Components That Are Unrestricted in Sign,@ J. Stat. Comp. Sim.,

35:135-43.

Westlake, W.J., 1973, "The Design and Analysis of Comparative Blood-Level Trials," in Current

Concepts in the Pharmaceutical Sciences, Dosage Form Design and Bioavailability (J. Swarbrick,

ed.), Lea and Febiger, 149-79.

Westlake, W.J., 1979, "Statistical Aspects of Comparative Bioavailability Trials," Biometrics, 35:273-

80.
20

Westlake, W.J., 1981, "Response to Kirkwood, TBL.: Bioequivalence Testing — A Need to

Rethink," Biometrics, 37:589-94.

Westlake, W.J., 1988, "Bioavailability and Bioequivalence of Pharmaceutical Formulations,@ in

Biopharmaceutical Statistics for Drug Development (K.E. Peace, ed.), Marcel Dekker, Inc., 329-

52.
21

APPENDIX A

Standards

The equations in section IV call for standards to be established (i.e., σT0 and θP for assessment of

population BE, σW0 and θI for individual BE). The recommended approach to establishing these

standards is described below.

A. s T0 and s W0

As indicated in section IV, a general objective in assessing BE should be to compare the

difference in the BA log-measure of interest after the administration of the T and R formulations,

T-R, with the difference in the same log-metric after two administrations of the R formulation,

R-RN.

1. Population Bioequivalence

For population BE, the comparisons of interest should be expressed in terms of the ratio

of the expected squared difference between T and R (administered to different

individuals) and the expected squared difference between R and RN (administered to

different individuals), as shown below. 

E(T - R)2 = (μT - μR)

2

 + σTT

2

 + σTR

2 Equation 8

E(R - RN)

2 = 2σTR2 Equation 9

E(T - R)2 (μT - μR)

2

 + σTT

2

 + σTR

2

------------- = -------------------------------

Equation 10

E(R - RN)

2

 2σTR

2

The population BE criterion in equation 4 (section IV.B.) is derived from equation 10,

such that the criterion equals zero for two identical formulations. The square root of

equation 10 yields the “population difference ratio” (PDR):
22

 (μT - μR)

2

 + σTT

2

 + σTR

2

PDR = [ -------------------------------]2 Equation 11

 2σTR

2

The PDR is the square root of the ratio of the expected squared T-R difference

compared to the expected squared R-R' difference in the population. It should be

noted that the PDR is monotonically related to the population BE criterion (PBC)

described in equation 4 as follows:

PDR = (PBC/2 + 1)2 Equation 12

Sponsors or applicants wishing to use the population BE approach should contact the

Agency for further information on σT0.

2. Individual Bioequivalence

For individual BE, the comparisons of interest should be expressed in terms of the ratio

of the expected squared difference between T and R (administered to the same

individual) and the expected squared difference between R and RN (two administrations

of R to the same individual), as shown below.

E(T - R)2 = (μT - μR)

2

 + σD

2

 + σWT

2

 + σWR

2 Equation 13

E(R - RN)

2 = 2σWR2 Equation 14

E(T - R)2 (μT - μR)

2

 + σD

2

 + σWT

2

 + σWR

2

------------- = ----------------------------------------

Equation 15

E(R - RN)

2

 2σWR

2

The individual BE criterion in equation 6 (section IV.C.) is derived from equation 15,

such that the criterion equals zero for two identical formulations. The square root of

equation 15 is the individual difference ratio (IDR):
23

 (μT - μR)

2

 + σD

2

 + σWT

2

 + σWR

2

IDR = [ ----------------------------------------]2 Equation 16

 2σWR

2

The IDR is the square root of the ratio of the expected squared T-R difference

compared to the expected squared R-R' difference within an individual. The IDR is

monotonically related to the individual BE criterion (IBC) described in equation 6 as

follows:

IDR = (IBC/2 + 1)2 Equation 17

This guidance recommends that σW0 = 0.2, based on the consideration of the maximum

allowable IDR of 1.25.4

B. qP and qI

The determination of θP and θI should be based on the consideration of average BE criterion

and the addition of variance terms to the population and individual BE criterion, as expressed by

the formula below.

average BE limit + variance factor

θ = -----------------------------------------------

variance

1. Population Bioequivalence

(ln1.25)2 + εP

θP = -------------------------- Equation 18

 σT0

2

The value of εP for population BE is guided by the consideration of the variance term

(σTT

2

 - σTR

2

) added to the average BE criterion. Sponsors or applicants wishing to use

the population BE approach should contact the Agency for further information on εP

and θP.

 

4

 The IDR upper bound of 1.25 is drawn from the currently used upper BE limit of 1.25 for the average BE

criterion.
24

2. Individual Bioequivalence

(ln1.25)2 + εI

θI = ----------------------- Equation 19

 σW0

2

The value of εI for individual BE is guided by the consideration of the estimate of

subject-by-formulation interaction (σD) as well as the difference in within-subject

variability (σWT

2

 - σWR

2

) added to the average BE criterion. The recommended

allowance for the variance term (σWT

2

 - σWR

2

) is 0.02. In addition, this guidance

recommends a σD

2

 allowance of 0.03. The magnitude of σD is associated with the

percentage of individuals whose average T to R ratios lie outside 0.8-1.25. It is

estimated that if σD = 0.1356, ~10% of the individuals would have their average ratios

outside 0.8-1.25, even if μT - μR= 0. When σD = 0.1741, the probability is ~20%.

Accordingly, on the basis of consideration for both σD and variability (σWT

2

 - σWR

2

) in

the criterion, this guidance recommends that εI = 0.05.
25

APPENDIX B

Choice of Specific Replicated Crossover Designs

Appendix B describes why FDA prefers replicated crossover designs with only two sequences, and

why we recommend the specific designs described in section V.A of this guidance.

1. Reasons Unrelated to Carryover Effects

Each unique combination of sequence and period in a replicated crossover design can be called a cell of

the design. For example, the two-sequence, four-period design recommended in

section V.A.1 has 8 cells. The four-sequence, four-period design below has 16 cells.

 Period

1 2 3 4

1 T R R T

2 R T T R

Sequence

3 T T R R

4 R R T T

The total number of degrees-of-freedom attributable to comparisons among the cells is just the number

of cells minus one (unless there are cells with no observations).

The fixed effects that are usually included in the statistical analysis are sequence, period, and treatment

(i.e., formulation). The number of degrees-of-freedom attributable to each fixed effect is generally equal

to the number of levels of the effect, minus one. Thus, in the case of the two-sequence, four-period

design recommended in section V.A.1, there would be 2-1=1 degree-of-freedom due to sequence, 4-

1=3 degrees-of-freedom due to period, and 2-1=1 degree-of-freedom due to treatment, for a total of

1+3+1=5 degrees-of-freedom due to the three fixed effects. Because these 5 degrees-of-freedom do

not account for all 7 degrees-of-freedom attributable to the eight cells of the design, the fixed effects

model is not saturated. There could be some controversy as to whether a fixed effects model that

accounts for more or all of the degrees-of-freedom due to cells (i.e., a more saturated fixed effects

model) should be used. For example, an effect for sequence-by-treatment interaction might be included

in addition to the three main effects — sequence, period, and treatment. Alternatively, a sequence-by-
26

period interaction effect might be included, which would fully saturate the fixed effects model.

If the replicated crossover design has only two sequences, use of only the three main effects (sequence,

period, and treatment) in the fixed effects model or use of a more saturated model makes little difference

to the results of the analysis, provided there are no missing observations and the study is carried out in

one group of subjects. The least squares estimate of μT-μR will be the same for the main effects model

and for the saturated model. Also, the method of moments (MM) estimators of the variance terms in

the model used in some approaches to assessment of population and individual BE (see Appendix H),

which represent within-sequence comparisons, are generally fully efficient regardless of whether the

main effects model or the saturated model is used.

If the replicated crossover design has more than two sequences, these advantages are no longer

present. Main effects models will generally produce different estimates of μT-μR than saturated models

(unless the number of subjects in each sequence is equal), and there is no well-accepted basis for

choosing between these different estimates. Also, MM estimators of variance terms will be fully efficient

only for saturated models, while for main effects models fully efficient estimators would have to include

some between-sequence components, complicating the analysis. Thus, use of designs with only two

sequences minimizes or avoids certain ambiguities due to the method of estimating variances or due to

specific choices of fixed effects to be included in the statistical model.

2. Reasons Related to Carryover Effects

One of the reasons to use the four-sequence, four-period design described above is that it is thought to

be optimal if carryover effects are included in the model. Similarly, the two-sequence, three-period

design

 Period

1 2 3

1 T R R

Sequence

2 R T T

is thought to be optimal among three-period replicated crossover designs. Both of these designs are

strongly balanced for carryover effects, meaning that each treatment is preceded by each other

treatment and itself an equal number of times.

With these designs, no efficiency is lost by including simple first-order carryover effects in the statistical

model. However, if the possibility of carryover effects is to be considered in the statistical analysis of

BE studies, the possibility of direct-by-carryover interaction should also be considered. If direct-by-
27

carryover interaction is present in the statistical model, these favored designs are no longer optimal. 

Indeed, the TRR/RTT design does not permit an unbiased within-subject estimate of μT-μR in the

presence of general direct-by-carryover interaction.

The issue of whether a purely main effects model or a more saturated model should be specified, as

described in the previous section, also is affected by possible carryover effects. If carryover effects,

including direct-by-carryover interaction, are included in the statistical model, these effects will be

partially confounded with sequence-by-treatment interaction in four-sequence or six-sequence

replicated crossover designs, but not in two-sequence designs.

In the case of the four-period and three-period designs recommended in section V.A.1, the estimate of

μT-μR, adjusted for first-order carryover effects including direct-by-carryover interaction, is as efficient

or more efficient than for any other two-treatment replicated crossover designs.

3. Two-Period Replicated Crossover Designs

For the majority of drug products, two-period replicated crossover designs such as the Balaam design

(which uses the sequences TR, RT, TT, and RR) should be avoided for individual BE because subjects

in the TT or RR sequence do not provide any information on subject-by-formulation interaction. 

However, the Balaam design may be useful for particular drug products (e.g., a long half-life drug for

which a two-period study would be feasible but a three- or more period study would not).
28

APPENDIX C

Sample Size Determination

Sample sizes for average BE should be obtained using published formulas. Sample sizes for population

and individual BE should be based on simulated data. The simulations should be conducted using a

default situation allowing the two formulations to vary as much as 5% in average BA with equal

variances and certain magnitude of subject-by-formulation interaction. The study should have 80 or

90% power to conclude BE between these two formulations. Sample size also depends on the

magnitude of variability and the design of the study. Variance estimates to determine the number of

subjects for a specific drug can be obtained from the biomedical literature and/or pilot studies.

Tables 1-4 below give sample sizes for 80% and 90% power using the specified study design, given a

selection of within-subject standard deviations (natural log scale), between-subject standard deviations

(natural log scale), and subject-by-formulation interaction, as appropriate.

Table 1

Average Bioequivalence

Estimated Numbers of Subjects

D=0.05

80% Power 90% Power

σW T = σD 2P 4P 2P 4P

0.15 0.01 12 6 16 8

0.10 14 10 18 12

0.15 16 12 22 16

0.23 0.01 24 12 32 16

0.10 26 16 36 20

0.15 30 18 38 24

0.30 0.01 40 20 54 28

0.10 42 24 56 30

0.15 44 26 60 34

0.50 0.01 108 54 144 72

0.10 110 58 148 76

0.15 112 60 150 80

Note: 1. Results for two-period designs use method of Diletti et al. (Diletti 1991).

2. Results for four-period designs use relative efficiency data of Liu (Liu 1995).
29

Table 2

Population Bioequivalence

Four-Period Design (RTRT/TRTR)

Estimated Numbers of Subjects

εP =0.02, D=0.05

σWR = σWT σBR=σBT 80% Power 90% Power

0.15 0.15 18 22

0.30 24 32

0.23 0.23 22 28

0.46 24 32

0.30 0.30 22 28

0.60 26 34

0.50 0.50 22 28

1.00 26 34

Note: Results for population BE are approximate from simulation studies

(1,540 simulations for each parameter combination), assuming two-sequence,

four-period trials with a balanced design across sequences.
30

Table 3

Individual Bioequivalence

Estimated Numbers of Subjects

εI =0.05, D=0.05

80% Power 90% Power

σW T = σD 3P 4P 3P 4P

0.15 0.01 14 10 18 12

0.10 18 14 24 16

0.15 28 22 36 26

0.23 0.01 42 22 54 30

0.10 56 30 74 40

0.15 76 42 100 56

0.30 0.01 52 28 70 36

0.10 60 32 82 42

0.15 76 42 100 56

0.50 0.01 52 28 70 36

0.10 60 32 82 42

0.15 76 42 100 56

Note: Results for individual BE are approximate using simulations (5,000 simulations

for each parameter combination). The designs used in simulations are RTR/TRT (3P)

and RTRT/TRTR (4P) assuming two-sequence trials with a balanced design across

sequences.

While the above sample sizes assume equal within-subject standard deviations, simulation studies for 3-

period and 4-period designs reveal that if Δ = 0 and 2 2s s WT − = WR 0.05 , the sample sizes given will

provide either 80% or 90% power for these studies.

To maintain consistency with section V.C, which suggests a minimum of 12 subjects in all BE studies,

the one case where n = 10 provides 80% power should be increased to n = 12.

.
31

Table 4

Individual Bioequivalence

Estimated Numbers of Subjects

εI =0.05, D=0.10

With Constraint on D (0.8 £ exp(D) £ 1.25)

80% Power 90% Power

σW T = σD 4P 4P

0.30 0.01 30 40

0.10 36 48

0.15 42 56

0.50 0.01 34 46

0.10 36 48

0.15 42 56

Note: Results for individual BE are approximate using simulations (5,000 simulations

for each parameter combination). The designs used in simulations are RTRT/TRTR (4P),

assuming two-sequence trials with a balanced design across sequences. When Δ=0.05,

sample sizes remain the same as given in Table 3. This is because the studies are already

powered for variance estimation and inference, and therefore, a constraint on the point

estimate of Δ has little influence on the sample size for small values of Δ.
32

APPENDIX D

Rationale for Logarithmic Transformation of Pharmacokinetic Data

A. Clinical Rationale

The FDA Generic Drugs Advisory Committee recommended in 1991 that the primary comparison of

interest in a BE study is the ratio, rather than the difference, between average parameter data from the T

and R formulations. Using logarithmic transformation, the general linear statistical model employed in

the analysis of BE data allows inferences about the difference between the two means on the log scale,

which can then be retransformed into inferences about the ratio of the two averages (means or medians)

on the original scale. Logarithmic transformation thus achieves a general comparison based on the ratio

rather than the differences.

B. Pharmacokinetic Rationale

Westlake observed that a multiplicative model is postulated for pharmacokinetic measures in BA/BE

studies (i.e., AUC and Cmax, but not Tmax) (Westlake 1973 and 1988). Assuming that elimination of

the drug is first-order and only occurs from the central compartment, the following equation holds after

an extravascular route of administration:

AUC0-4 = FD/CL Equation 20

 

 = FD/(VKe) Equation 21

where F is the fraction absorbed, D is the administered dose, and FD is the amount of drug absorbed. 

CL is the clearance of a given subject that is the product of the apparent volume of distribution (V) and

the elimination rate constant (Ke).5 The use of AUC as a measure of the amount of drug absorbed

 

 

5

 Note that a more general equation can be written for any multicompartmental model as

 AUC0- = FD/Vdß λn Equation 22

 

where Vdß is the volume of distribution relating drug concentration in plasma or blood to the amount of drug in the

body during the terminal exponential phase, and λn is the terminal slope of the concentration-time curve. 
33

involves a multiplicative term (CL) that might be regarded as a function of the subject. For this reason,

Westlake contends that the subject effect is not additive if the data are analyzed on the original scale of

measurement. 

Logarithmic transformation of the AUC data will bring the CL (VKe) term into the following equation in

an additive fashion:

lnAUC0-4 = ln F + ln D - ln V - ln Ke Equation 23

Similar arguments were given for Cmax. The following equation applies for a drug exhibiting one

compartmental characteristics:

Cmax = (FD/V) x e-ke*Tmax Equation 24

where again F, D and V are introduced into the model in a multiplicative manner. However, after

logarithmic transformation, the equation becomes

 lnCmax = ln F + ln D - ln V - KeTmax Equation 25

Thus, log transformation of the Cmax data also results in the additive treatment of the V term.
34

APPENDIX E

SAS Program Statements for Average BE Analysis of

Replicated Crossover Studies

The following illustrates an example of program statements to run the average BE analysis using

PROC MIXED in SAS version 6.12, with SEQ, SUBJ, PER, and TRT identifying sequence,

subject, period, and treatment variables, respectively, and Y denoting the response measure (e.g.,

log(AUC), log(Cmax)) being analyzed:

PROC MIXED;

CLASSES SEQ SUBJ PER TRT;

MODEL Y = 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;

The Estimate statement assumes that the code for the T formulation precedes the code for the R

formulation in sort order (this would be the case, for example, if T were coded as 1 and R were

coded as 2). If the R code precedes the T code in sort order, the coefficients in the Estimate

statement would be changed to -1 1.

In the Random statement, TYPE=FA0(2) could possibly be replaced by TYPE=CSH. This

guidance recommends that TYPE=UN not be used, as it could result in an invalid (i.e., not nonnegative definite) estimated covariance matrix.

Additions and modifications to these statements can be made if the study is carried out in more than

one group of subjects.
35

APPENDIX F

Method for Statistical Test of Population Bioequivalence Criterion

Four-Period Crossover Designs

Appendix F describes a method for using the population BE criterion (see section IV.B, equations 4

and 5). The procedure involves the computation of a test statistic that is either positive (does not

conclude population BE) or negative (concludes population BE).

Consider the following statistical model which assumes a four-period design with equal replication of

T and R in each of s sequences with an assumption of no (or equal) carryover effects (equal

carryovers go into the period effects)

Yijkl k m ikl ijk ijkl =+++ gde

where i s = 1,K indicates sequence, 1, ij n = K indicates subject within sequence i, k = R, T

indicates treatment, l =1, 2 indicates replicate on treatment k for subjects within sequence i. Yijkl is

the response of replicate l on treatment k for subject j in sequence i , ikl g represents the fixed

effect of replicate l on treatment k in sequence i , dijk is the random subject effect for subject j in

sequence i on treatment k , and ijkl e is the random error for subject j within sequence i on

replicate l of treatment k . The ijkl e ’s are assumed to be mutually independent and identically

distributed as

εijkl ~ N(0, σWk

2

 )

for i s = 1,K , 1, ij n = K , k = R, T, and l = 1, 2. Also, the random subject effects

ij ( mdmd R ijR

,

T ijT )

′

d = + + are assumed to be mutually independent and distributed as

2

2 2

~ ,

R BR BT BR

ij

T BT BR BT

N

m s rs s

m rs s s

     

     

       

d .

The following constraint is applied to the nuisance parameters to avoid overparameterization of the

model for k=R, T:
36

2

1 1

0

s

ikl

i l

g

= =

∑ ∑ =

This statistical model proposed by Chinchilli and Esinhart assumes s*p location parameters (where p

is the number of periods) that can be partitioned into t treatment parameters and sp-t nuisance

parameters (Chinchilli and Esinhart 1996). This produces a saturated model. The various nuisance

parameters are estimated in this model, but the focus is on the parameters needed for population BE.

 In some designs, the sequence and period effects can be estimated through a reparametrization of

the nuisance effects.

This model definition can be extended to other crossover designs.

Linearized Criteria (from section IV. B, equations 4 and 5):

! Reference-Scaled:

2 2 2 2

1 h m = (T − mR

) + − (s s TT TR) 0 −q s P TR ⋅ <

• Constant-Scaled:

2 2 2 2

2 0 h = (mT −+− mR

) (s s TT TR) 0 −q s P T ⋅ < 

Estimating the Linearized Criteria:

The estimation of the linearized criteria depends on study designs. The remaining estimation and

confidence interval procedures assume a four-period design with equal replication of T and R in each

of s sequences. The reparametrizations are defined as:

1 2

1 *( ) UTij = + 2

Y Y ijT ijT

1 2

1 *( ) URij = + 2

Y Y ijR ijR

1 2

1 *( )

2

VTij = − Y Y ijT ijT

1 2

1 *( )

2

VRij = − Y Y ijR ijR

ij ijT ijR I = − Y Y • •

,
37

for i s = 1, , K and 1, , ij n = K , where

( 1 2 )

1

2

YijT g = + Y Y ijT ijT and ( 1 2 )

1

2

YijR g = + Y Y ijR ijR .

Compute the formulation means pooling across sequences:

1

1 , ,

s

k i k

i

Y kRT

s

m

∧

⋅ ⋅

=

= = ∑ and ˆ

ˆ ˆ Δ = − m m T R

where

2

1 1

1

2

1

ni

i k ijkl

j l i

Y Y

n

⋅ ⋅

= =

= ∑ ∑ .

Compute the variances of , , , UUVV Tij Rij Tij Rij , pooling across sequences, and denote these variance

estimates by , , , MUT MURTR MV MV , respectively. Specifically,

( )

2

1 1

1

i

T

s n

T Tij Ti

U i j

MU U U

n = =

= − ∑∑

( )

2

1 1

1

i

T

s n

T Tij Ti

V i j

MV V V

n = =

= − ∑∑

( )

2

1 1

1

i

R

s n

R Rij Ri

U i j

MU U U

n = =

= − ∑∑

( )

2

1 1

1

i

R

s n

R Rij Ri

V i j

MV V V

n = =

= − ∑∑

1

TRTR

s

I UUV V i

i

n nnn n n s

=

 

==== = −     ∑

Then, the linearized criteria are estimated by:

! Reference-Scaled:

2

1 0.5 (1 ) [ 0.5 ] h q MUT MVT P MUR R MV

∧ ∧

= Δ + + ⋅ − + ⋅ + ⋅
38

• Constant-Scaled:

2

2 0.5 0

(1) [ 0.5 ] h MUT MVT MU R MVR q s P T

∧ ∧

= Δ + + ⋅ − ⋅ + ⋅ − ⋅

95% Upper Confidence Bounds for Criteria:

The table below illustrates the construction of a (1−a) level upper confidence bound based on the

two-sequence, four-period design, for the reference-scaled criterion, h1

∧

. Use α=0.05 for a 95%

upper confidence bound.

Hq= Confidence Bound Eq= Point Estimate Uq=(Hq- Eq)

2

2

1

2

1

2

1

1 ,

1

s

D i I

i

n s

H t n M

s

a

∧

−

=

− −

   

= +        

Δ ∑

2

ED

∧

= Δ

UD

( )

,

2

1

1

n s

nsE

H

c − a

− ⋅

=

MU E T = 1 U1

,

2

( ) 2

2

n s

nsE

H

c − a

− ⋅

=

0.5 2 MV E T⋅ = U 2

,1

2

( ) 3

3

n s

n s E rs

H rs

c − −a

− ⋅

=

− (1 3 + = qp R ) MU E rs U3rs

,1

2

( ) 4

4

n s

n s E rs

H rs

c − −a

− ⋅

=

−(1+ ⋅ qp R ) 0.5 4 ⋅ = MV E rs

U 4rs

( ) 1

1

2 HEU h = + ∑ ∑ q q

( ) 1

1

2 HEU h = + ∑ ∑ q q

is the upper 95% confidence bound for h1

∧

. Note 

1

s

i

i

n n

=

= ∑ , where s is

the number of sequences, ni is the number of subjects per sequence, and 2 c a,n s − is from the

cumulative distribution function of the chi-square distribution with n s − degrees of freedom, i.e.
39

2 2 Pr( ) c c n− − s ≤ = a,n s a. The confidence bound for h2

∧

 is computed similarly, adjusting the

constants associated with the variance components where appropriate (in particular, the constant

associated with MUR and MVR).

Hq= Confidence Bound Eq= Point Estimate Uq=(Hq- Eq)

2

2

1

2

1

2

1

1 ,

1

s

D i I

i

n s

H t n M

s

a

∧

−

=

− −

   

= +        

Δ ∑

2

ED

∧

= Δ

UD

( )

,

2

1

1

n s

nsE

H

c − a

− ⋅

=

MU E T = 1 U1

,

2

( ) 2 2

n s

nsE H

c − a

− ⋅

=

0.5 2 MV E T⋅ = U 2

( )

,1

2

3

3

n s

n s E cs

H cs

c − −a

−

= −1 3 ⋅ = MUR E cs U 3cs

( )

,1

2

4

4

n s

n s E cs

H cs

c − −a

−

=

−0.5 4 ⋅ = MVR E cs U 4cs

( ) 2

1

2 2 Hh = E U q −q s P T q 0 ∑ ∑ ⋅ +

Using the mixed-scaling approach, to test for population BE, compute the 95% upper confidence

bound of either the reference-scaled or constant-scaled linearized criterion. The selection of either

reference-scaled or constant-scaled approach depends on the study estimate of total standard

deviation of the reference product (estimated by 1[ 0.5 ] 2 MUR R + ⋅MV in the four-period design). If

the study estimate of standard deviation is ≤ sT 0, the constant-scaled criterion and its associated

confidence interval should be computed. Otherwise, the reference-scaled criterion and its

confidence interval should be computed. The procedure for computing each of the confidence

bounds is described above. If the upper confidence bound for the appropriate criterion is negative

or zero, conclude population BE. If the upper bound is positive, do not conclude population BE.
40

APPENDIX G

Method for Statistical Test of Individual Bioequivalence Criterion

Appendix G describes a method for using the individual BE criterion (see section IV.C, equations 6

and 7). The procedure (Hyslop, Hsuan, and Holder 2000) involves the computation of a test

statistic that is either positive (does not conclude individual BE) or negative (concludes individual

BE).

Consider the following statistical model that assumes a four-period design with equal replication of T

and R in each of s sequences with an assumption of no (or equal) carryover effects (equal

carryovers go into the period effects)

Yijk l m k i k l ijk ijkl =+++ gde

where i s = 1,K indicates sequence, 1, ij n = K indicates subject within sequence i, k = R, T

indicates treatment, l=1, 2 indicates replicate on treatment k for subjects within sequence i. Yijkl is the

response of replicate l on treatment k for subject j in sequence i , ikl g represents the fixed effect

of replicate l on treatment k in sequence i , dijk is the random subject effect for subject j in

sequence i on treatment k , and ijkl e is the random error for subject j within sequence i on

replicate l of treatment k . The ijkl e ’s are assumed to be mutually independent and identically

distributed as

εijkl ~ N(0, σWk

2

 )

for i s = 1,K , 1, ij n = K , k = R, T, and l = 1, 2. Also, the random subject effects

ij ( mdmd R ijR

,

T ijT )

′

d = + + are assumed to be mutually independent and distributed as

2

2 2

~ ,

R BR BT BR

ij

T BT BR BT

N

m s rs s

m rs s s

     

     

       

d .

The following constraint is applied to the nuisance parameters to avoid overparameterization of the

model for k = R, T:
41

2

1 1

0

s

ikl

i l

g

= =

∑ ∑ =

This statistical model proposed by Chinchilli and Esinhart assumes s*p location parameters (where p

is the number of periods) that can be partitioned into t treatment parameters and sp-t nuisance

parameters (Chinchilli and Esinhart, 1996). This produces a saturated model. The various nuisance

parameters are estimated in this model, but the focus is on the parameters needed for individual BE. 

In some designs, the sequence and period effects can be estimated through a reparametrization of the

nuisance effects.

This model definition can be extended to other crossover designs.

Linearized Criteria (from section IV. C, equations 6 and 7) :

• Reference-Scaled:

2 2 2 2 2

1 h m = ( ) T − mR +sD + − ()0 s s WT WR −q sI WR ⋅ <

• Constant-Scaled:

2 2 2 2 2

2 0 h = (mT − mR

) + sD + − ()0 sWT sWR − q sI W ⋅ <

Estimating the Linearized Criteria:

The estimation of the linearized criteria depends on study designs. The remaining estimation and

confidence interval procedures assume a four-period design with equal replication of T and R in each

of s sequences. The reparametrizations are defined as:

ij ijT ijR I = − Y Y • •

Tij = − Y Y ijT1 2 ijT

Rij = − Y Y ijR1 2 ijR

for i s = 1, , K and 1, , ij n = K , where
42

( 1 2 )

1

2

YijT g = + Y Y ijT ijT and ( 1 2 )

1

2

YijR g = + Y Y ijR ijR

Compute the formulation means, and the variances of ij I , Tij , and Rij , pooling across sequences,

and denote these variance estimates by MI, MT, and MR, respectively, where

1

1 , ,

s

k i k

i

Y kRT

s

m

∧

⋅ ⋅

=

= = ∑ and ˆ

ˆ ˆ Δ = − m m T R

2

1 1

1

2

1

ni

i k ijkl

j l i

Y Y

n

⋅ ⋅

= =

= ∑ ∑

( )

2 2

1 1

1

s ni

I

I ij i

i j I

M I I

n

s

∧

= =

= = − ∑∑

1

s

I T R i

i

n n n n s

=

 

= = = −     ∑

( )

2 2

1 1

1

ˆ

2

s ni

T WT ij i

T i j

M T T

n

s

= =

= = − ∑∑

( )

2 2

1 1

1

ˆ

2

s ni

R WR ij i

R i j

M R R

n

s

= =

= = − ∑∑ .

Then, the linearized criteria are estimated by: 

• Reference-Scaled: 

 

2

1 0.5 (1.5 ) h q MI T M M I R

∧ ∧

= Δ ++⋅−+⋅

• Constant-Scaled:

 

2

2 h2 MMM I T 0.5 1.5 RIW q s 0

∧ ∧

= Δ ++⋅−⋅ − ⋅

and the subject-by-formulation interaction variance component can be estimated by:
43

( ) 2 2 1 2 2 ˆ ˆ ˆ ˆ 2

sD =sI − + s s WT WR

95% Upper Confidence Bounds for Criteria:

The table below illustrates the construction of a (1−a) level upper confidence bound based on the

two-sequence, four-period design, for the reference-scaled criterion, h1

∧

. Use α=0.05 for a 95%

upper confidence bound. 

Hq= Confidence Bound Eq= Point Estimate Uq=(Hq- Eq)

2

2 1

2

1

2

1

1 ,

1 s

D i I

i

n s H t n M

s a

∧ −

=

− −

    = +        

Δ ∑

2

ED

∧

= Δ

UD

2 ,

( ) I

n s I

nsM H

c a −

− ⋅ = E M I I = UI

2

,

0.5 ( ) T

n s

T

nsM H

ca −

⋅−⋅ = E M T T = ⋅ 0.5 UT

( )

2

1 ,

1.5 ( ) I R

n s

R

nsM

H a

q

c − −

− + ⋅−⋅ = E M R = −+⋅ (1.5 qI R ) UR

( ) 1

1

2 HEU h = + ∑ ∑ q q

where 

1

s

i

i

n n

=

= ∑ , s is the number of sequences, and 2 c a,n s − is from the cumulative distribution

function of the chi-square distribution with n s − degrees of freedom, i.e. 2 2 Pr( ) c c n− − s ≤ = a,n s a.

 Then, ( ) 1

1

2 HEU h = + ∑ ∑ q q is the upper 95% confidence bound for h1

∧

. The confidence bound

for h2

∧

 is computed similarly, adjusting the constants associated with the variance components where

appropriate (in particular, the constant associated with MR).
44

Hq= Confidence Bound Eq= Point Estimate Uq=(Hq- Eq)

2

2 1

2

1

2

1

1 ,

1 s

D i I

i

H n s t n M

s a

∧ −

=

− −

    = +        

Δ ∑

2

ED

∧

= Δ

UD

2 ,

( ) I

n s I

nsM H

c a −

− ⋅ = E M I I = UI

2

,

0.5 ( ) T

n s

T

nsM H

ca −

⋅−⋅ = E M T T = ⋅ 0.5 UT

( )

2

1 ,

1.5 ( ) R

n s

R

nsM

H

c − − a

− ⋅−⋅ = E M R R = − ⋅ (1.5) UR

( ) 2

1 2 2 Hh = E U q −q sI W q 0 ∑ ∑ ⋅ +

Using the mixed-scaling approach, to test for individual BE, compute the 95% upper confidence

bound of either the reference-scaled or constant-scaled linearized criterion. The selection of either

reference-scaled or constant-scaled criterion depends on the study estimate of within-subject

standard deviation of the reference product. If the study estimate of standard deviation is ≤sW 0 , the

constant-scaled criterion and its associated confidence interval should be computed. Otherwise, the

reference-scaled criterion and its confidence interval should be computed. The procedure for

computing each of the confidence bounds is described above. If the upper confidence bound for the

appropriate criterion is negative or zero, conclude individual BE. If the upper bound is positive, do

not conclude individual BE.

This guidance recommends that sponsors use either reference-scaling or constant-scaling at the

changeover point (see section VII.D, Discontinuity). To test for individual BE, compute the 95%

upper confidence bounds of both reference-scaled and constant-scaled linearized criteria. The

procedure for computing these confidence bounds is described above. If the upper bound of either

criterion is negative or zero (either 1 2 H H or h h ), conclude individual BE. If the upper bounds of

both criteria are positive, do not conclude individual BE.
45

APPENDIX H

Variance Estimation

Relatively simple unbiased estimators, the method of moments (MM) or the restricted maximum

likelihood (REML) method, can be used to estimate the mean and variance parameters in the

individual BE approach. A key distinction between the REML and MM methods relates to

differences in estimating variance terms. The REML method estimates each of the three variances,

σD

2

, σW R

2

, σW T

2

, separately and then combines them in the individual BE criterion. The REML

estimate of σD

2

 is found from estimates of σBR

2

, σBT

2

, and the correlation, ρ. The MM approach

is to estimate the sum of the variance terms in the numerator of the criterion, σD

2

 + σW T

2

- σW R

2

,

and does not necessarily estimate each component separately. One consequence of this difference

is that the MM estimator of σD

2

 is unbiased but could be negative. The REML approach can also

lead to negative estimates, but if the covariance matrix of the random effects is forced to be a

proper covariance matrix, the estimate of σD

2

 can be made to be non-negative. This forced nonnegativity has the effect of making the estimate positively biased and introduces a small amount of

conservatism to the confidence bound. The REML method can be used in special cases (e.g., when

substantial missing data are present). In addition, the MM approaches have not yet been adapted

to models that allow assessment of carryover effects.