Statistical Approaches 
to Establishing 
Bioequivalence 
Guidance for Industry 
 
 
 
 
DRAFT GUIDANCE 
 
This guidance document is being distributed for comment purposes only. 
 
Comments and suggestions regarding this draft document should be submitted within 60 days of 
publication in the Federal Register of the notice announcing the availability of the draft 
guidance.  Submit electronic comments to https://www.regulations.gov.  Submit written 
comments to the Dockets Management Staff (HFA-305), Food and Drug Administration, 5630 
Fishers Lane, Rm. 1061, Rockville, MD 20852.  All comments should be identified with the 
docket number listed in the notice of availability that publishes in the Federal Register.  
  
For questions regarding this draft document, contact (CDER) David Coppersmith at 301-796-
9193.   
 
 
 
 
 
U.S. Department of Health and Human Services 
Food and Drug Administration 
Center for Drug Evaluation and Research (CDER) 
 
December 2022 
Biopharmaceutics 
 
Revision 1 
    
Statistical Approaches 
to Establishing 
Bioequivalence  
Guidance for Industry 
 
 
 
 
 
 
 
Additional copies are available from: 
Office of Communications, Division of Drug Information  
Center for Drug Evaluation and Research 
Food and Drug Administration 
10001 New Hampshire Ave., Hillandale Bldg., 4th Floor  
Silver Spring, MD 20993-0002  
Phone: 855-543-3784 or 301-796-3400; Fax: 301-431-6353 
Email: druginfo@fda.hhs.gov  
https://www.fda.gov/drugs/guidance-compliance-regulatory-information/guidances-drugs 
  
 
 
 
 
 
 
 
 
 
 
    U.S. Department of Health and Human Services 
Food and Drug Administration 
Center for Drug Evaluation and Research (CDER) 
 
December 2022 
Biopharmaceutics 
 
Revision 1 
 
   
 
 
TABLE OF CONTENTS 
I.  INTRODUCTION............................................................................................................. 1 
 
  A.    Overview.................................................................................................................................. 1 
  B.    Statistical Guidance Background .......................................................................................... 2 
II.  GENERAL CONSIDERATIONS ................................................................................... 3 
  A.    Study Design ........................................................................................................................... 3  
  B     Data Preparation .................................................................................................................... 8 
  C.    Statistical Models .................................................................................................................. 11 
III.  SPECIFIC SITUATIONS .............................................................................................. 14 
  A.    In Vitro Bioequivalence and Population Bioequivalence .................................................. 14 
  B.    Statistical Methods for Narrow Therapeutic Index and                                                            
Highly Variable Drug Products .......................................................................................... 19 
  C.    Comparative Clinical Endpoint Bioequivalence Studies .................................................. 21 
  D.    Studies in Multiple Groups .................................................................................................. 22 
  E.    Bioequivalence Statistics for Adhesion and Irritation Studies ......................................... 23 
  F.    Dose Scale for Bioequivalence Assessment ......................................................................... 24 
  G.   Bioequivalence Studies Using Multiple References ............................................................ 24 
V.  APPENDICES ................................................................................................................. 25 
  A.    Choice of Specific Replicated Crossover Designs .............................................................. 25 
  B.     Rationale for Logarithmic Transformation of Pharmacokinetic Data ........................... 27 
  C.    SAS Program Statements for Average Bioequivalence Analysis of                        
Replicated Crossover Studies .............................................................................................. 28 
 
 
 
  
 
 
  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
1  Statistical Approaches to Establishing Bioequivalence 
2  Guidance for Industry1 
3   
4   
5  This draft guidance, when finalized, will represent the current thinking of the Food and Drug 
6  Administration (FDA or Agency) on this topic.  It does not establish any rights for any person and is not 
7  binding on FDA or the public.  You can use an alternative approach if it satisfies the requirements of the 
8  applicable statutes and regulations.  To discuss an alternative approach, contact the FDA staff responsible 
9  for this guidance as listed on the title page.   
10   
11   
12   
13  I.  INTRODUCTION 
14   
15  Requirements for submitting bioavailability (BA) and bioequivalence (BE) data in 
16  investigational new drugs (INDs), new drug applications (NDAs), abbreviated new drug 
17  applications (ANDAs), and supplements; the definitions of BA and BE; and the types of in vitro 
18  and in vivo studies that are appropriate to measure BA and establish BE are set forth in part 320 
19  (21 CFR part 320).  This guidance provides recommendations on how to meet provisions of part 
20  320 for all drug products. 
21   
22  In general, FDAs guidance documents do not establish legally enforceable responsibilities.  
23  Instead, guidances describe the Agencys current thinking on a topic and should be viewed only 
24  as recommendations, unless specific regulatory or statutory requirements are cited.  The use of 
25  the word should in Agency guidances means that something is suggested or recommended, 
26  but not required. 
27   
28  A.  Overview 
29   
30  This guidance provides recommendations to sponsors and applicants who intend to use 
31  equivalence criteria in analyzing in vivo or in vitro BE studies for INDs, NDAs, ANDAs, and 
32  supplements to these applications.  This guidance discusses statistical approaches for BE 
33  comparisons and focuses on how to use these approaches both generally and in specific 
34  situations.  When finalized, this guidance will replace the guidance for industry Statistical 
35  Approaches to Establishing Bioequivalence, which was issued in February 2001 (2001 
36  guidance).  This guidance provides recommendations on the topics covered in the 2001 guidance 
37  as well as recommendations on additional topics, including missing data and intercurrent events, 
38  adaptive design, and specific situations, such as narrow therapeutic index drugs and highly 
39  variable drugs.  
40   
 
1 This guidance has been prepared by the Office of Generic Drugs in the Center for Drug Evaluation and Research 
(CDER) in cooperation with CDERs Office of Translational Sciences and Office of Pharmaceutical Quality at the 
Food and Drug Administration.   
  1  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
41  Defined as relative BA, the assessment of BE involves comparison between a test (T) and 
42  reference (R) drug product, where T and R can vary depending on the comparison to be 
43  performed (e.g., to-be-marketed formulation versus clinical trial formulation, generic drug versus 
44  reference listed drug (RLD), originally approved formulation versus postapproval formulation 
45  changes).  Although BA and BE are closely related, BE comparisons normally rely on (1) a 
46  criterion, (2) a confidence interval for the criterion, and (3) a predetermined BE limit.  BE 
47  comparisons could also be used in certain pharmaceutical product line extensions, such as 
48  additional strengths, new dosage forms (e.g., changes from immediate release to extended 
49  release), and new routes of administration.2  In these contexts, the approaches described in this 
50  guidance can be used to determine BE.  The general approaches discussed in this guidance may 
51  also be useful when assessing pharmaceutical equivalence (i.e., the identical dosage form and 
52  route(s) of administration that contain identical amounts of the identical active drug ingredient) 
53  or performing equivalence comparisons in clinical pharmacology studies and other areas. 
54   
55  This guidance is intended to encourage the use of science-based approaches to making statistical 
56  BE assessments.  Given the evolving nature of statistical approaches and technologies, FDA 
57  encourages generic and new drug applicants to propose and discuss novel methodologies (e.g., 
58  model-based BE and novel adaptive designs for comparative clinical endpoint BE studies) with 
59  the Agency through appropriate regulatory meetings, as described below.  
60   
61  B.  Statistical Guidance Background 
62   
63  In the July 1992 guidance on Statistical Procedures for Bioequivalence Studies Using a Standard 
64  Two-Treatment Crossover Design (the 1992 guidance), the Center for Drug Evaluation and 
65  Research (CDER) recommended that a standard in vivo BE study design be based on the 
66  administration of either single or multiple doses of the T and R products to healthy subjects on 
67  separate occasions, with random assignment to the two possible sequences of drug product 
68  administration.  The 1992 guidance further recommended that statistical analysis for 
69  pharmacokinetic (PK) measures, such as area under the curve (AUC) and peak concentration 
70  (C ), be based on the two one-sided tests procedure to determine whether the average values 
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71  for the PK measures determined after administration of the T and R products were comparable.  
72  This approach is termed average BE (ABE) and involves the calculation of a 90% confidence 
73  interval for the ratio of the averages (population geometric means) of the measures for the T and 
74  R products.  To establish BE, the calculated confidence interval should fall within a BE limit, 
75  usually 80 to 125% for the ratio of the product averages.3  In addition to this general approach, 
76  the 1992 guidance provided specific recommendations for (1) logarithmic transformation of PK 
77  data, (2) methods to evaluate sequence effects, and (3) methods to evaluate outlier data. 
 
2 For example, to submit an ANDA that is not the same as its RLD because it has a different strength, dosage form, 
or route of administration than that of the RLD, an applicant first must obtain permission from FDA through the 
citizen petition process.  See section 505(j)(2)(C) of the Federal Food, Drug and Cosmetic Act (21 U.S.C. 
355(j)(2)(C)); 21 CFR 314.93(b).  Such petitions are referred to as suitability petitions.   
3
 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.   
  2  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
78   
79  In addition to reiterating the key points from the 1992 guidance and replacing that guidance, the 
80  2001 guidance introduced two additional approaches to assessing BE: population BE and 
81  individual BE.  Both of these approaches, unlike the average BE approach, include a comparison 
82  of the variabilities of the PK metrics of the two products being compared, as well as the average 
83  responses.  However, the individual BE approach is not currently used in the regulatory setting 
84  while the population BE approach is mainly used for certain in vitro BE studies.  The 2001 
85  guidance also includes discussion of replicated crossover designs  crossover designs in which 
86  at least some of the subjects receive at least one of the products more than once.  The discussion 
87  of these designs in that guidance included their implications for possible carryover effects and 
88  their use in screening for outliers. 
89   
90  This guidance provides recommendations on the topics covered by the 1992 guidance and the 
91  2001 guidance, as well as recommendations on some additional topics.  As noted in the 
92  Overview section above, when finalized, this guidance will replace the 2001 guidance. 
93   
94   
95  II.  GENERAL CONSIDERATIONS 
96   
97  A.  Study Design 
98   
99  1.  Experimental Design 
100   
101  a.  Nonreplicated designs 
102   
103  A conventional nonreplicated design, such as the standard two-formulation, two-period, two-
104  sequence crossover design, can be used to generate data when an average or population approach 
105  is chosen for BE comparisons.  Under certain circumstances, such as products with apparent, 
106  long half-lives where crossover studies are impractical, parallel designs can be used. 
107   
108  b.  Replicated crossover designs 
109   
110  Replicated crossover designs can be used irrespective of which BE approach is selected to 
111  establish BE, although they are not necessary when an average or population BE approach is 
112  used.  When a reference-scaled BE approach is used, replicated crossover designs are critical to 
113  allow estimation of within-subject variances for the R (and T if a fully replicated study is used) 
114  measures.  In particular, the following four-period, two-sequence, two-formulation design is 
115  recommended for fully replicated BE studies (see Appendix A for further discussion of 
116  replicated crossover designs). 
117   
      Period     
    1  2  3  4 
Sequence  1  T  R  T  R 
  2   R  T  R  T 
  3  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
118   
119   
120  For this design, the same lots of the T and R formulations should be used for the replicated 
121  administration.  Each period should be separated by an adequate washout period.  
122   
123  Other fully replicated crossover designs are also possible.  For example, a three-period design, as 
124  shown below, could be used. A fully replicated design can estimate the subject-by-formulation 
125  interaction variance components.   
126   
    Period     
    1  2  3 
Sequence  1  T  R  T 
  2  R  T  R 
127   
128  The following three-period, three-sequence, two-formulation, partially replicated design can also 
129  be used for assessing reference-scaled BE, though it cannot fully estimate the subject-by-
130  formulation interaction variance component (as a fully replicated design can). 
131    
    Period     
    1  2  3 
Sequence  1  T  R  R 
  2  R  T  R 
  3  R  R  T 
132  A greater number of subjects would be needed for the three-period designs compared to the 
133  recommended four-period design to achieve the same statistical power to conclude BE. 
134   
135  c.  Adaptive design 
136   
137  An adaptive design is a clinical trial design that allows for prospectively planned modifications 
138  to one or more aspects of the design based on accumulating data from subjects in the trial.  An 
139  adaptive design can be a group sequential design, or other design with one or more adaptive 
140  features.4  For example, Potvins methods (Potvin et al. 2008, Xu et al. 2016)5 are a combination 
141  of a group sequential design and an adaptive design with sample size re-estimation.  
142   
 
4 See the guidance for industry Adaptive Designs for Clinical Trials of Drugs and Biologics (November 2019).  We 
update guidances periodically. For the most recent version of a guidance, check the FDA guidance web page at 
https://www.fda.gov/regulatory-information/search-fda-guidance-documents. 
5 Potvin, D., C.E. DiLiberti, W.W. Hauck, A.F. Parr, D.J. Schuirmann, and R.A. Smith, 2008, Sequential Design 
Approaches for Bioequivalence Studies With Crossover Designs, Pharmaceutical Statistics: The Journal of Applied 
Statistics in the Pharmaceutical Industry 7, no. 4: 245-262; Xu, J., C. Audet, C.E. DiLiberti, W.W. Hauck, T.H. 
Montague, A.F. Parr, D. Potvin, and D.J. Schuirmann, 2016, Optimal Adaptive Sequential Designs for Crossover 
Bioequivalence Studies, Pharmaceutical Statistics (15) 1:15-27. 
  4  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
143  Adaptive design can provide ethical advantages6 and statistical efficiency.  When appropriately 
144  implemented, adaptive designs can reduce resources used, decrease time to study completion, 
145  and increase the chance of study success, especially when the prior information needed for the 
146  study design is limited.  However, use of adaptive designs can also have limitations.  For 
147  example, adaptive designs may call for certain statistical methods to avoid increasing the chance 
148  of erroneous conclusions and introducing bias in estimates and for complex adaptive designs, 
149  such methods may not be readily available.7  The decision to use or not use an adaptive design is 
150  at the applicants discretion.  
151   
152  In general, the design, conduct, and analysis of a proposed adaptive study design should satisfy 
153  the following recommendations: 
154   
155    The details of the adaptive design should be completely specified prior to initiation of the 
156  study and documented accordingly.  For example, prospective planning should include 
157  prespecification of the anticipated number and timing of interim analyses, the type of 
158  adaptation, the statistical inference methods to be used and the specific algorithm 
159  governing the adaptive decision.  If a study should be stopped early (e.g., for futility or 
160  for success in demonstrating BE), detailed stopping criteria should be pre-specified and 
161  scientifically justified. 
162    
163    The applicant should establish that estimation of treatment effect will be sufficiently 
164  reliable, and the chance of erroneous conclusions will be adequately controlled.  The 
165  Agency will accept appropriately designed BE studies that are scientifically justified.  
166  Support might include published literature in peer-reviewed journals in which the 
167  applicants proposed approach is validated or simulation results meeting desired criteria 
168  (e.g., the Type I error probability of the proposed approach is controlled at a nominal 
169  level of 0.05 for a BE test).  Appropriate details (e.g., literature references, proofs, 
170  simulation codes/results) for the methodology should be submitted. 
171    
172    The applicant should ensure that study integrity will be appropriately maintained.  A 
173  comprehensive written data access plan defining how study integrity will be maintained 
174  in the presence of the planned adaption should be included in the protocol or statistical 
175  analysis plan (SAP).  This applies to both adaptive comparative clinical endpoint BE 
176  studies and PK BE studies, whether blinded or unblinded by design.  
177   
178  For details, refer to the guidance for industry Adaptive Design for Clinical Trials of Drugs and 
179  Biologics (November 2019). 
 
6 See footnote 4.  For example, the ability to stop a trial early if it becomes clear that the trial is unlikely to 
demonstrate equivalence can reduce the number of patients exposed to the unnecessary risk of an ineffective 
investigational treatment and allow subjects the opportunity to explore more promising therapeutic alternatives.   
7 See footnotes 4 and 5.   
  5  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
180  Due to the increased complexity of adaptive studies and uncertainties regarding their operating 
181  characteristics, applicants are encouraged to contact the Agency early to discuss their proposed 
182  adaptive study designs and statistical methods via the controlled correspondence,8 pre-ANDA 
183  meeting,9 pre-IND meeting, or pre-NDA meeting pathway.10 
184   
185  d.  Design with sparse sampling 
186   
187  For certain generic products, a sparse BE design is used, where the sampling for each subject is 
188  done at a single or very limited number of time points rather than the number needed to get a full 
189  concentration profile.  For example, some ophthalmic products are studied using a sparse BE 
190  design, where only a single sample is collected from a single eye of each subject, at one assigned 
191  sampling time point for that subject.  More generally, a sparse BE study design can be a parallel 
192  design where each subject should receive only one treatment, T or R, but not both.  Alternatively, 
193  a crossover sparse study design can be used where each subject receives both test and reference 
194  treatments (e.g., in subjects undergoing indicated cataract surgery for both eyes). 
195   
196  For a sparse BE study design, the mean concentration for each product at each time point of 
197  measurement is calculated by using the mean concentration of the subjects measured at each time 
198  point to derive the mean profile for each product.  Based on the trapezoid rule, the   for 
199  each product is computed as a weighted linear combination of these mean concentrations at each 
200  time point through time  .  The   is the area under the concentration  time cAurUvCe 0frotm 
201  zero to the time  .  C  and T  (time to maximum observed concentration) can be determined 
max max
202  accordingly.  The ratios tof  AU Ca0ndt C  between the test and the reference product are used 
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203  to assess BE.  Esttimation of the standard deviation and confidence interval for the ratio of 
204   may be done by boAotUstCr0apt or parametric methods (e.g., Bailers methods (Bailer 1988)11 
205  for a parallel study design), and that for the ratio of C  may be done by bootstrap methods.  BE 
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206  iAsU sCup0ptorted if the 90% confidence interval for the ratio of   between the test and the 
207  reference product lies within the BE margin (80.00%, 125.00%).  Model-based approaches can 
208  be considered when they can reliably control the error rate AofU cCotncluding BE for bio inequivalent 
209  products (Type I error).12   
210   
211  For complicated issues such as other forms of sparse design or alternative statistical methods, 
212  applicants are encouraged to contact the Agency early to discuss their proposed study design and 
213  statistical methods via the controlled correspondence, pre-ANDA meeting, pre-IND meeting, or 
214  pre-NDA meeting pathway.13 
 
8 See the guidance for industry Controlled Correspondence Related to Generic Drug Development (December 
2020).  
9 See the guidance for industry Formal Meetings Between FDA and ANDA Applicants of Complex Products Under 
GDUFA (October 2022).   
10 See the draft guidance for industry Formal Meetings Between the FDA and Sponsors or Applicants of PDUFA 
Products (December 2017).  When final, this guidance will represent FDAs current thinking on this topic. 
11 Bailer, A.J., 1988, Testing for the Equality of Area Under the Curves When Using Destructive Measurement 
Techniques, Journal of Pharmacokinetics and Biopharmaceutics, 16(3): 303-309. 
12 Zhao, L., M.-J. Kim, L. Zhang, and R. Lionberger, 2019, Generating Model Integrated Evidence for Generic Drug 
Development and Assessment, Clinical Pharmacology and Therapeutics, 105(2): 338-349.  
13 See footnotes 8, 9, and 10.   
  6  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
215   
216  2.  Sample Size Determination   
217   
218  It is an applicants responsibility to design an adequately powered BE study for the proposed 
219  study.  We recommend that applicants enroll enough subjects to power the study at a level of 0.8 
220  or higher, for a BE test to be carried out with a type 1 error rate of 0.05 (see section III.C.1.a for 
221  more details).  When determining the sample size, rates of attrition and noncompliance (e.g., 
222  protocol violation) should be taken into consideration.  Enough subjects should be recruited, 
223  randomized, and dosed at the beginning of the study to ensure that the desired number of 
224  evaluable subjects will be available for analysis.  All eligible subjects who were dosed should be 
225  included in the analysis.  For BE studies, add-on subjects after the pre-specified number of 
226  subjects have been reached are generally not encouraged except in an adaptive study design with 
227  a pre-specified adaptation to add subjects and statistical methods to control the Type I error rate 
228  under the nominal level. 
229   
230  The number of subjects to be included in a study should be based on an appropriate sample size 
231  calculation for the proposed study design.14,15,16  For example, the standard 22 cross-over study 
232  will use a particular calculation while studies with a different design or set of endpoints will use 
233  different calculations.  For sample size re-estimation in an adaptive study design, refer to Section 
234  II.A.1.c. Adaptive Design. 
235   
236  Sample size and power calculation should be supported by established scientific practice.  For 
237  complex study designs with no analytical solutions for sample size calculation, simulation can be 
238  used to estimate the needed sample size in order to reach a desired power.  The method by which 
239  the sample size is determined should be given in the protocol, together with the estimates of any 
240  quantities used in the calculations (such as variances, mean values, response rates, the assumed 
241  effect size).  The basis for these estimates should also be given.  For example, variance estimates 
242  can be obtained from the biomedical literature and/or pilot studies.  It is important to investigate 
243  the sensitivity of the sample size calculated to a variety of deviations from the assumed 
244  estimates.  This may be facilitated by providing a range of sample sizes appropriate for a 
245  reasonable range of deviations from the assumptions or alternative approaches supported by 
246  published peer-reviewed literature.  
247   
248  Applicants should enter a sufficient number of subjects in the study to allow for dropouts.  
249  Dropouts generally should not be replaced because replacement of subjects during the study 
250  could complicate the statistical model and analysis.  Applicants who wish to replace dropouts 
251  during the study should indicate this intention in the protocol.  The protocol should also state 
252  whether samples from replacement subjects, if not used, will be assayed.  If the dropout rate is 
253  high and applicants wish to add more subjects, a modification of the statistical analysis may be 
 
14 Chow, S.-C. and J.-P. Liu, 2008, Design and Analysis of Bioavailability and Bioequivalence Studies, 3rd Edition, 
New York: Chapman and Hall/CRC. 
15 Draft guidance for industry Bioequivalence Studies with Pharmacokinetic Endpoints for Drugs Submitted Under 
an ANDA (August 2021). When final, this guidance will represent FDAs current thinking on this topic.   
16 Patterson, S.D. and B. Jones, 2017, Bioequivalence and Statistics in Clinical Pharmacology, 2nd Edition, New 
York: Chapman and Hall/CRC. 
  7  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
254  recommended.  Additional subjects should not be included after data analysis unless the study 
255  was designed from the beginning as an adaptive design. 
256   
257  In general, for PK BE or in vitro BE studies, sample size calculation should be based on BE 
258  metrics (e.g., AUC, C ) after log-transformation; for comparative clinical endpoint BE studies, 
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259  sample size calculation should be based on the un-transformed comparative clinical endpoints 
260  unless otherwise noted in the relevant FDA product-specific guidance (PSG).17  The number of 
261  evaluable subjects in a PK BE study should not be less than 12.  For highly variable drug 
262  products, a minimum of 24 subjects are recommended for BE assessment.18  
263   
264  B.  Data Preparation  
265   
266  The drug concentration in biological fluid determined at each sampling time point should be 
267  furnished on the original scale for each subject participating in the study.  The PK measures of 
268  systemic exposure should also be furnished on the original scale.  The variables for a 
269  comparative clinical endpoint BE study should also be furnished on the original scale.  The 
270  mean, standard deviation, and coefficient of variation for each variable should be computed and 
271  tabulated in the final report.   
272   
273  1.  Log-Transformation   
274   
275  A general approach to assessing BE is to compare the log-transformed BA measures after 
276  administration of the T and R products. 
277   
278  a.  Logarithmic transformation for PK measures  
279   
280  This guidance recommends that PK BE measures (e.g., AUC and C ) be log-transformed (see 
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281  Appendix B).  The choice of common or natural logs should be consistent and should be stated in 
282  the study report.  The limited sample size in a typical BE study precludes a reliable 
283  determination of the distribution of the data set.  Sponsors and/or applicants are not encouraged 
284  to test for normality of error distribution after log-transformation, nor should they use normality 
285  of error distribution as a reason for carrying out the statistical analysis on the original scale.  
286  Justification should be provided if sponsors or applicants believe that their BE study data should 
287  be statistically analyzed on the original rather than on the log scale.  
288   
289   
290   
291   
 
17 For the most recent version of a product-specific guidance, check the product-specific web page at 
https://www.accessdata.fda.gov/scripts/cder/psg/index.cfm.  
18 Davit, B. and D. Conner, 2010, Reference-Scaled Average Bioequivalence Approach. In: I. Kanfer and L. 
Shargel, editors. Generic Drug Product Development  International Regulatory Requirements for Bioequivalence, 
New York, NY: Informa Healthcare, 271-272; Food and Drug Administration, Advisory Committee for 
Pharmaceutical Science, October 5-6, 2006.  
  8  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
292  b.  Data transformation for comparative pharmacodynamic and clinical 
293  endpoint BE study 
294          
295  The decision on whether and how to transform a variable for a comparative pharmacodynamic 
296  (PD) or comparative clinical endpoint BE study should be specified in the protocol, especially 
297  for the primary variable(s).  The basis for the variables should also be given in the protocol.  For 
298  example, these variables can be obtained from the biomedical literature and/or pilot studies.  
299  Similar considerations apply to other derived variables, such as the use of change from baseline, 
300  percentage change from baseline, the area under the curve of repeated measures, or the ratio of 
301  two different variables.  Subsequent clinical interpretation should be carefully considered.  
302  Regarding comparative clinical endpoint studies, in general the log-transformation is not 
303  used.  For example, in the case of the Fiellers confidence interval for the ratio of two means, the 
304  raw (untransformed) data are used for the confidence interval derivation.19 
305   
306  c.  Negative values for baseline corrected PK or PD endpoints  
307   
308  Because data transformation and scales might affect BE conclusions, they should be chosen 
309  carefully and appropriately justified in the protocol.20  If a baseline correction results in a 
310  negative plasma concentration value, the value should be set equal to 0 before calculating the 
311  baseline-corrected AUC.    
312   
313  2.  Missing Data and Intercurrent Events 
314   
315  Subjects may have missing data in the study for various reasons (e.g., subjects refusal to 
316  continue in the study, worsening of conditions or emergence of adverse events, subjects failure 
317  to meet scheduled appointments for evaluation).  Subjects may also have intercurrent (post-
318  randomization) events that affect either the interpretation or the existence of the measurements 
319  associated with the question of interest (e.g., noncompliance with the protocol for various 
320  reasons, use of rescue medication due to lack of efficacy, death).  Missing data and intercurrent 
321  events can introduce problems such as bias, misleading inference, loss of precision and loss of 
322  power, which make it hard to interpret the trial outcome. 
323   
324  The ICH (Internal Council for Harmonization) E9(R1) Addendum introduces the concept of an 
325  estimand, which is a precise description of the treatment effect reflecting the clinical question 
326  posed by a particular study objective.21  The trial protocol of a BE study should include the 
327  following components of an estimand: (1) the treatment of interest and alternative treatment(s) to 
328  which comparison will be made: e.g., test drug compared with reference drug; (2) the analysis 
329  population for BE assessment; (3) the variable (or endpoint) to be measured for each subject 
330  (e.g., AUC or C ); (4) the specification of how to account for intercurrent events in assessing 
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331  the scientific question of interest (for example, in a comparative clinical endpoint BE study with 
 
19 Fieller, E., Some Problems in Interval Estimation, 1954, Journal of the Royal Statistical Society, 16(2): 175-185.   
20 For example, see Sun, W., S. Grosser, and Y. Tsong, 2017, Ratio of Means vs. Difference of Means as Measures 
of Superiority, Noninferiority, and Average Bioequivalence, Journal Biopharmaceutical Statistics, 27(2): 338-355.         
21 Guidance for industry E9(R1) Statistical Principles for Clinical Trials: Addendum: Estimands and Sensitivity 
Analysis in Clinical Trials, Revision 1 (May 2021).  
  9  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
332  a binary endpoint, subjects who discontinue study treatment early  due to lack of treatment effect 
333  should be included as treatment failures); and (5) the population-level summary for the variable 
334  to compare between treatment conditions, e.g., the geometric mean ratio of the test to reference 
335  drug in a PK BE study. 
336   
337  The protocol should include plans to minimize missing data.  The trial protocol should 
338  prospectively define anticipated causes of missing data, the corresponding statistical assumptions 
339  about reasons for the missing data, and how missing data will be treated in the statistical 
340  analysis.  The treatment of missing data in the statistical analysis should be justified such that 
341  valid statistical inferences can be made under the assumptions about the missing data 
342  mechanism.  
343   
344  Statistical methods for handling missing data include complete case analysis, available case 
345  analysis, weighting methods, imputation, and model-based approaches.  For example, in a two-
346  way crossover study, a complete case analysis could be a general linear model as implemented in 
347  SAS PROC GLM, which removes all subjects with any missing observations for any variables 
348  included in the GLM model (i.e., removes subjects missing one or both periods).  An available 
349  case analysis could be done using SAS PROC MIXED, which uses all observed data (e.g., in a 
350  two-way crossover study, uses all subjects with one or two complete periods of data).  
351   
352  Approaches for handling missing data and the statistical methods for the primary BE analysis 
353  (e.g., GLM vs. MIXED) should be pre-specified in the study protocol or SAP.  Depending on the 
354  nature of the assumed or likely missing data mechanism, statistical methods from any of these 
355  categories may be appropriate.  The validity of a statistical approach to handle missing data 
356  depends on a variety of factors, including, but not limited to, the mechanism for missingness, the 
357  fraction of incomplete cases, the values that are missing, specifics of the analysis, and definition 
358  of the estimand.  Sensitivity analyses using alternative approaches may also be used in the 
359  statistical analysis to address missing data.  Sensitivity analyses should be pre-specified in the 
360  trial protocol to evaluate the robustness of conclusions to deviations from the assumptions about 
361  the missing data mechanism.  The applicant should provide detailed information about reasons 
362  for missing data and any observed intercurrent events. 
363   
364  For a particular drug product, if the PSG recommends certain approaches to handling missing 
365  data, the applicants should refer to that PSG.  Applicants may choose to contact the Agency via 
366  the controlled correspondence, pre-ANDA meeting, pre-IND meeting, or pre-NDA meeting 
367  pathway to discuss their proposed approach to handling missing data if such an approach is 
368  different from what is recommended in the PSG or if the applicants have further questions. 
369    
370  3.  Outlier Detection 
371   
372  Outlier data in BE studies are defined as subject data for one or more BA measures that are 
373  discordant with corresponding data for that subject and/or for the rest of the subjects in a study.  
374  Because BE studies are usually carried out as crossover studies, the most important type of 
375  subject outlier is the within-subject outlier, when one subject or a few subjects differ notably 
376  from the rest of the subjects with respect to a within-subject T-R comparison.  The existence of a 
  10  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
377  subject outlier with no protocol violations and for which there are not bioanalytical errors could 
378  indicate one of the following situations: 
379   
380  a.   Product failure 
381   
382  Product failure could occur, for example, when a subject exhibits an unusually high or low 
383  response to one or the other of the products because of a problem with the specific dosage unit 
384  administered.  This could occur, for example, with a sustained and/or delayed-release dosage 
385  form exhibiting dose dumping or a dosage unit with a coating that inhibits dissolution. 
386   
387  b.  Subject-by-formulation interaction  
388   
389  A subject-by-formulation interaction could occur when an individual is representative of subjects 
390  present in the general population in low numbers, for whom the relative BA of the two products 
391  is markedly different from that for most of the population, and for whom the two products are 
392  not bioequivalent, even though they might be bioequivalent in most of the population.  In the 
393  case of product failure, the unusual response could be present for either the T or R product.  
394  However, in the case of a subpopulation, even if the unusual response is observed on the R 
395  product, there could still be concern about lack of bioequivalence of the two products.  For these 
396  reasons, applicants should not remove data from the statistical analysis of BE studies solely 
397  because those data are identified as statistical outliers.   
398   
399  In general, outlier data (whether due to product failure, subject-by-formulation interaction, or 
400  another cause) may only be removed from the BE statistical analysis if there is real-time 
401  documentation demonstrating a protocol violation during the clinical and/or 
402  analytical/experimental phase of the BE study.  Applicants should include a prospective plan in 
403  the BE study protocol for handling subjects (experimental outliers) in the BE statistical analysis.  
404  Data from redosing studies are not considered valid evidence to support removal of outlier data 
405  from the statistical analysis.  All subject data should be submitted, with potential outliers flagged 
406  with appropriate documentation as part of the submission.  However, for a replicated PK BE 
407  study, if reference-scaled average BE is used, the applicant should ensure that the calculated 
408  intra-subject variability is not inflated due to extreme values or situations.   
409   
410  To characterize aberrant observations for exploratory or quality control purposes, the choice of 
411  the appropriate technique depends on whether there are outlying subjects or outlying 
412  observations, as well as on the study design. 
413   
414  C.  Statistical Models 
415    
416  1.  General Statistical Criteria for Bioequivalence  
417   
418  The general structure of a BE criterion is that a function () of population measures should be 
419  demonstrated to be no greater than a specified value ().  Using the terminology of statistical 
420  hypothesis testing, this is accomplished by testing the hypothesis H :  versus H : < at a 
0 a
  11  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
421  desired level of significance, often 5%.  Rejection of the null hypothesis H  (i.e., demonstrating 
0
422  that the estimate of  is statistically significantly less than ) results in a conclusion of BE. 
423   
424  a.  Use of confidence intervals to do two one-sided tests  
425   
426  In BE assessment we are frequently interested in testing whether a parameter (for example, the 
427  difference of means for a T and R product for a specific endpoint) is contained within a defined 
428  interval, call it [ ,  ].  The recommended method for doing such a test is the Two One-Sided 
1 2
429  Tests Procedure.22  A one-sided statistical test is carried out to determine whether the parameter 
430  is   , and a second one-sided test is carried out to determine whether the parameter is   ; 
1 2
431  both tests are carried out at a level of significance , which is usually 0.05.  If both tests are 
432  successful (that is, we reject the null hypothesis in both cases), we conclude that the parameter is 
433  contained in [ ,  ]. 
1 2
434   
435  These two one-sided tests are sometimes carried out by calculating a 100 (1-2) % confidence 
436  interval for the parameter and determining whether this confidence interval is completely 
437  contained in the interval [ ,  ].  For this confidence interval method of carrying out the tests to 
1 2
438  be valid, the confidence interval should be an equal tails confidence interval.  If the lower and 
439  upper confidence limits of the 100 (1-2) % confidence interval are L  and L , respectively, then 
1 2
440  the confidence interval is equal tails if L , by itself, is at least a 100 (1-) % lower confidence 
1
441  bound for the parameter and L , by itself, is at least a 100 (1-) % upper confidence bound for 
2
442  the parameter. 
443   
444  In some cases, there may not be general agreement as to the best choice of a particular statistical 
445  testing methodology for carrying out the two one-sided tests (for example, if the parameter of 
446  interest is the difference between the success probabilities for a T and R product for a binary 
447  endpoint).  In such cases, careful consideration should be given to the choice of statistical 
448  methods for doing the two one-sided tests, which may or may not correspond to a confidence 
449  interval method. 
450   
451  2.  Statistical Information and Implementation of Criteria for PK Measures (AUC , 
0-t
452  AUC , and C )  
0- max
453   
454  We recommend that applicants provide the following statistical information for AUC ,  
0-t
455  AUC , and C : 
0- max
456   
457    Geometric means for the formulations tested 
458    Arithmetic means for the formulations tested 
459    Geometric mean ratios of Test vs. Reference and their corresponding 90% confidence 
460  intervals or 95% upper confidence bounds (e.g., for highly variable drugs or narrow 
461  therapeutic index drugs)  
 
22 Schuirmann, D. J., 1987, A Comparison of the Two One-Sided Tests Procedure and the Power Approach for 
Assessing the Equivalence of Average Bioavailability, Journal of Pharmacokinetics and Biopharmaceutics, 15(6): 
657-680. 
  12  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
462   
463  Recommended statistical information for other types of outcome measures is discussed in section 
464  III: Specific Situations.   
465   
466  To facilitate BE comparisons, for crossover studies, the measures for each individual should be 
467  displayed in parallel for the formulations tested.  For each BE measure, the ratio of the individual 
468  geometric mean of the T product to the individual geometric mean of the R product should be 
469  tabulated side by side.  The summary tables should indicate in which sequence each subject 
470  received the product.   
471   
472  Statistical analyses of BE data are typically based on a statistical model for the logarithm of the 
473  BA measures (e.g., AUC and C ).  The model is a mixed-effects or two-stage linear model.  
max
474  Each subject, j, theoretically provides a mean for the log-transformed BA measure for each 
475  formulation,  and   for the T and R formulations, respectively.  The model assumes that 
Tj  Rj
476  these subject-specific means come from a distribution with population means   and  , and 
T R
477  between-subject variances  2 and  2, respectively.  The model allows for a correlation, , 
BT BR
478  between  and  .  The subject-by-formulation interaction variance component,  2, is related 
Tj  Rj D
479  to these parameters as follows: 
480   
481   2 = variance of ( -  ) 
D Tj  Rj
482   
483  = (  -  )2 + 2 (1-)  [23]   
BT BR BT BR 
484   
485  For a given subject, the observed data for the log-transformed BA measure are assumed to be 
486  independent observations from distributions with means   and  , and within-subject variances 
Tj Rj
487   2 and  2.  The total variances for each formulation are defined as the sum of the within- 
WT WR
488  and between-subject components (i.e.,  2 =  2 +  2 and  2 =  2 +  2).  For analysis 
TT WT BT TR WR BR
489  of crossover studies, the means are given additional structure by the inclusion of period and 
490  sequence effect terms.  
491   
492  The applicant may also consider prespecifying inclusion of important demographic and baseline 
493  prognostic covariates in the statistical model for parallel studies.  This sort of adjustment can 
494  increase the precision and power of the statistical analysis and compensate for any lack of 
495  balance between treatment groups with no inflation of Type 1 error.  
496   
497   
498   
499   
 
23 Schall, R., and H. G. Luus, 1993, On Population and Individual Bioequivalence, Statistics in Medicine, 12(12): 
1109-1124. 
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500  III.  SPECIFIC SITUATIONS24   
501   
502  A.  In Vitro Bioequivalence and Population Bioequivalence  
503   
504  This section discusses statistical methods for assessment of in vitro BE, including population BE 
505  (PBE), a similarity index (f ), statistical approaches respectively for in vitro release tests (IVRT), 
2
506  in vitro permeation tests (IVPT) and in vitro abuse-deterrent formulations (ADF) comparative 
507  studies, and a profile comparison approach based on Earth Movers Distance (EMD). 
508   
509  1.  Population Bioequivalence   
510   
511  One of the recommended statistical approaches for evaluating in vitro BE is population BE 
512  (PBE).  To test for PBE, the null and alternative hypotheses are given as follows: 
513     vs.     
514  where    if the estimated   or    if the estimated 
2 2 2 HH0:  PP HHaa: < PP 2 2 2
(TR) +TR (TR) +TR
515    . = R2 RR > 0  = 02
516  Here,   and   are the population means,   and   are the population variances of the log-
517  trRRansfor0med measure for T and R products, re2spectiv2ely;   is a regulatory constant for variance; 
518  and   iTTs the PBRRE limit. The concept of PBETT is to coRRmpare2 the difference of the T and R 
519  products with that of the reference versus reference itself.  0This comparison can be denoted in 
520  termsPP of the population difference ratio as follows: 
521   
2 2 2 2
E(YTYR) (TR) +R +T 
522  The regulatory constant variance,  2,= is set based on t2he followin=g cons+ide1r.ations.  Due to the 
E(YR YR) 2R 2
523  low variability of in vitro measurem2ents, this guidance recommends that the ratio of geometric 
524  means should fall within 0.90 and 10.11.  As a result, an upper BE limit of 1.11 is recommended 
525  for the average BE limit for in vitro data.  Assuming   ,   and the 
526  maximum allowable limit for population difference rat2io is 12.25, th2is leads to the recommended 
527  choice of  .  R = T = 0 T R = ln1.11
528     2
529  The determ0in=ati0on.0 o1f PBE limit,  , is based on the consideration of average BE criterion and 
530  the addition of variance terms to PBE criterion as the following form: 
PP
531   
2 2 2
(TR) +T R Average BE limit+Variance term
532    2 2 = .
533  The FDA recommendemd aaxll{ow0a,ncRe} for the varianceS ctearlmed i vs a0r.i0a1n. c Te hteisr mvalue may be adjusted 
534  depending on the average BE limit for in vitro data based on further communication with the 
535  Agency.  Accordingly, the PBE limit,  , is recommended as follows: 
PP
 
24 Some specific situations are addressed in the following subsections with specified choices of BE criteria.  Further 
discussion regarding these specified choices can be found in the guidances cited in those subsections.           
 
  14  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
536   
2
537    (ln1.11) +0.01
PP =   = 2.089
538  A linearized form is recommended to use to 0te.0st1  .  That is, testing   is 
539  equivalent to testing   where   if the estimated 
HH0:   PP H0:  PP
540    or    if 2the est2imate2d  2.  Here, 
H0:  0  = (TT RR) +(T R)PPRR
541  ,     and  2 2   2  if the2 estimated   or     if the 
542  esRRti>mat0ed 2  = (.  TT 2RR) +(T2R)2 PP0 RR  0 2 1 =2
543  (SuTTpposeRR )  is a2 = TT upper c3on=fideRRn+ce bPPouRnd for  .  Then, PBRRE >is su0pport3ed= if RRan+d onPPly0 if 
544  .  Based onRR the w0ork of Howe (1974)25 and Ting et al. (1990)26, an approximate 95% upper 
545  confidenceUU boun9d 5f%or   is given as follows:   UU 
0
546   

547    2 2 2
548  where  ,  , and UU  =are 1po+int2 estim3a+tors (of1  , 1), an+d( 2, resp2e)cti+ve(ly3;  a3n)d   are 95% 
549  upper confidence bounds for   and   and   is a 95% lower confidence bound for  .  For 
550  further d1etai2l, see, e3.g., the draft PSGs for Bud1eso2nide sus3pension (Septem1ber 20122) and 
551  Fluticasone Propionate metered1 spray 2(June 23020).27  3
552   
553  2.  Similarity Index (f )   
2
554   
555  For a comparison of dissolution profiles, similarity is assessed using the similarity index, f  
2
556  (Shah et al., 1998),28 as described in detail in the guidance for industry Immediate Release Solid 
557  Oral Dosage Forms Scale-Up and Postapproval Changes: Chemistry, Manufacturing, and 
558  Controls, In Vitro Dissolution Testing, and In Vivo Bioequivalence Documentation (November 
559  1995).  In particular, given that all profiles are conducted on a minimum of 12 individual dosage 
560  units, 2 profiles are similar if the value of their similarity factor f  is between 50 and 100.   
2
561   
562  3.  In-Vitro Release Test 
563   
564  When an in-vitro release test (IVRT) is used to support a demonstration of BE for topical 
565  dermatological drug products as part of an in vitro characterization-based BE approach, a two-
566  stage, nonparametric statistical approach is recommended, and described in the draft guidance 
567  for industry In Vitro Release Test Studies for Topical Drug Products Submitted in ANDAs 
568  (October 2022).29  The statistical approach is the same as that used to assess the equivalence of 
569  drug release rates for non-sterile semisolid dosage forms evaluated by a comparative IVRT study 
570  in the context of certain postapproval changes; this is shown in detail in the guidance for industry 
 
25 Howe, W.G., 1974, Approximate Confidence Limits of the Mean of X+Y Where X and Y are Two Tabled 
Independent Random Variables, Journal of the American Statistical Association, 69:789-794. 
26 Ting, N., R.K. Burdick, F. Graybill, S. Jeyaratnam, and T.F.C. Lu, 1990, Confidence Intervals on Linear 
Combinations of Variance Components That Are Unrestricted in Sign, Journal of Statistical Computation and 
Simulation, 35:135-143. 
27 When final, these guidances will represent FDAs current thinking on these topics.   
28 Shah, V.P., Y. Tsong, P. Sathe, and J.P. Liu, 1998, In Vitro Dissolution Profile ComparisonStatistics and 
Analysis of the Similarity Factor, f2, Pharmaceutical Research, 15(6):889-896. 
29 When final, this guidance will represent FDAs current thinking on this topic.   
  15  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
571  Nonsterile Semisolid Dosage Forms  Scale-Up and Postapproval Changes: Chemistry, 
572  Manufacturing, and Controls; In Vitro Release Testing and In Vivo Bioequivalence 
573  Documentation (May 1997).   
574   
575  The assessment of equivalence by an IVRT involves a comparison of the median in vitro drug 
576  release rates of two formulations using a non-parametric statistical test which is resistant to 
577  outliers that are expected to occur under the particular testing conditions. 
578   
579  4.  In-Vitro Permeation Test  
580   
581  When an in-vitro permeation test (IVPT) is used to support a demonstration of BE for topical 
582  dermatological drug products as part of an in vitro characterization-based BE approach, a mixed 
583  scaled criterion is recommended, and described in detail in the draft guidance for industry In 
584  Vitro Permeation Test Studies for Topical Drug Products Submitted in ANDAs (October 2022).30  
585  According to that methodology, a confidence interval is calculated for each of the endpoints, log-
586  transformed maximum flux ( ) and log-transformed total (cumulative) amount (AMT) 
587  permeated.  The permeation test is performed with excised skin sections from patients 
588  undergoing a surgical procedJJummreaa mmor from cadaver donors and the statistical test uses the within-
589  reference standard deviation,  , as the threshold that prompts use of either the unscaled or 
590  scaled confidence interval. 
591    SSWWRR
592  The mixed-scaled criterion uses the within-reference standard deviation as a threshold, 
593  independently, for each endpoint.  Specifically, for   or log-transformed total (cumulative) 
594  amount permeated, the reference-scaled average BE approach is used for the endpoint only if it 
595  has a  . The regular ABE approach (refJJemmr aatomm Schuirmann, 1987)31 is used for the 
596  endpoint with  . 
597    SSWWRR > 0.294
598  In the referencSSeWW-sRRcaled0 .a2v9e4rage BE approach, the hypotheses to be tested are: 
599   
600   
2
(TT RR)
HH0: 2   
601  WWRR  
2
(TT RR)
602  Here we determine the 100(1-)% upper conHHfidaa:ence b2ound f<or    
WWRR
603  where:  2 2
604  -   = mean difference of T and R products  (TT RR) WWRR
605  -   = within-subject variance of R product 
TT RR
2
606  -  ,  , and   (regulatory constant) 
WWRR 2
(ln (mm))
607  For the T =pro(duWWc0t) 2to bmme b=io1e.q2u5ivalent WWto0 th=e 0R. 2p5roduct, both of the following conditions must be  
608  satisfied for each endpoint tested: 
 
30 When final, this guidance will represent FDAs current thinking on this topic.  
31 See footnote 22.  
  16  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
609   
610  a.  The 95% upper confidence bound for   must be less than 
611  or equal to zero (numbers should be kept to a min2imum 2of four significant 
612  figures for comparison).  (TT RR) WWRR
613   
614  b.  The point estimate of the T/R geometric mean ratio must fall within the pre-
615  specified limits  , where m = 1.25. 
1
616   
mm, mm
617  In the case of the non-scaled approach, we calculate the 100(1-2)% confidence interval for 
618   as 
619   
TT RR
620   
2
SSII
621     II.tt(1),(nn1)
nn
622  where: 
623  -    is the point estimate for the mean difference of T and R products 
624  -  stimate of inter-donor variability 
II.
2
625  -  SSII    is the 100   percentile of the students t-distribution with   
626  degrees of freedom 
 tt(1),(nn1) (1) (nn1)
627  -   n is the number of donors 
628        -   the value of  is usually set at 0.05 
629   
630  For the T product to be bioequivalent to the R product, the 100(1-2)% confidence interval for 
631   must be contained within the limits   in the original scale for each endpoint 
1
632  tested, where m = 1.25. 
TT RR mm, mm
633   
634  5.  Abuse-Deterrent Formulation Comparative Studies  
635   
636  An ADF is a formulation that has abuse-deterrent properties, which are defined as drug product 
637  properties that are expected to meaningfully deter certain types of abuse, even if they do not fully 
638  prevent abuse.32  The general BE statistical considerations for in vitro ADF comparative studies 
639  presented in this guidance align with the guidance for industry  Abuse-Deterrent Opioids  
640  Evaluation and Labeling33 and the guidance for industry  General Principles for Evaluating the 
641  Abuse Deterrence of Generic Solid Oral Opioid Drug Products (November 2017).  The potential 
642  route of abuse (i.e., ingestion (oral route), injection (parenteral route), insufflation (nasal route), or 
643  smoking (inhalation route)) and its relevance to ADF design feature(s) will determine how an 
644  applicant should evaluate the abuse deterrence of the product utilizing a tier-based approach.  To 
645  support  in  vitro  ADF  comparative  studies,  the  Agency  recommends  applicants  provide 
 
32 See the guidance for industry Abuse-Deterrent Opioids - Evaluation and Labeling (April 2015).  
33 Ibid.  
  17  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
646  justification for the sample size, statistical test, and number of batches to assess the abuse-deterrent 
647  properties and demonstrate consistency of abuse-deterrent performance throughout the drug 
648  product  shelf-life  and  lifecycle  (i.e.,  postapproval  changes).    Applicants  should  consider  a 
649  standardized accept/reject criterion based on delta or confidence interval relevant to the abuse-
650  deterrent outcome.  The Agency recommends the use of relevant statistics (e.g., sampling plans) 
651  to support evaluation of abuse-deterrent properties.   
652   
653  For ANDA submissions, a non-inferiority approach should be taken when comparing T product 
654  with R product to conclude that T product is no less abuse deterrent than R product.34  The Agency 
655  recommends inferential analyses to evaluate the abuse deterrence of T product versus R product.  
656  In the analyses, a hierarchical set of null hypotheses serves as a gatekeeper for subsequent null 
657  hypotheses, evaluating the abuse deterrence of T and R products under progressively more 
658  challenging conditions.  A hierarchical inferential approach is used to maintain a fixed family-wise 
659  experiment Type I error rate.  Typically, the acceptable Type I error probability () will be set at 
660  5%. 
661   
662  6.  Earth Movers Distance Based Profile Comparison Approach  
663   
664  EMD is a statistical metric that measures the discrepancy (distance) between distributions 
665  without a prior assumption of the distribution.35  The EMD has been recommended in a profile 
666  comparison approach to assess equivalence of particle size distribution profile,36 where the 
667  profile exhibits complex distribution (i.e., multiple peaks) that cannot be accurately described by 
668  some conventional descriptors (e.g., the D50 and SPAN).  The EMD-based profile comparison 
669  approach is briefly described as follows. To assess equivalence between the T and R product 
670  formulations in the particle size distribution shape, an average profile of all R product samples 
671  (i.e., R center) is calculated and serves as the reference profile to compute the distance between 
672  an R or a T product sample to the R center using the EMD algorithm.  After obtaining the profile 
673  distances between each R product sample and the R product average (R  R center distance), and 
674  the profile distances between each T product sample and the R product average (T  R center 
675  distance), a statistical equivalence method, e.g., the PBE, is then applied to the two groups of 
676  distances to indicate whether the T and R products are statistically equivalent in the particle size 
677  distribution shape.  For details, refer to Rubner et al. (2000).37 
678   
679  Importantly, considering the increasingly emerging technologies and methods for in vitro BE 
680  studies, applicants are encouraged to contact the Agency early to discuss their proposed study 
681  designs and statistical methods via the controlled correspondence, pre-ANDA meeting, pre-IND 
682  meeting, or pre-NDA meeting pathway.38 
683   
 
34 Guidance for Industry Evaluating the Abuse Deterrence of Generic Solid Oral Opioid Drug Products (November 
2017). 
35 Rubner, Y., C. Tomasi, and L.J. Guibas, 2000, The Earth Movers Distance as a Metric for Image Retrieval, 
International Journal of Computer Vision, 40(2):99-121. 
36 Draft PSG for industry on Cyclosporine emulsion (October 2016). When final, this guidance will represent the 
FDAs current thinking on this topic.   
37 See footnote 35.   
38 See footnotes 8, 9, and 10.  
  18  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
684  B.  Statistical Methods for Narrow Therapeutic Index and Highly Variable Drug 
685  Products 
686   
687  1.  Statistical Method for Narrow Therapeutic Index Drugs  
688   
689  If a drug is a narrow therapeutic index drug, a fully replicated cross-over design should be used.  
690  The statistical analysis should be carried out using both the ABE and the reference-scaled 
691  average BE tests for both AUC and C .  
max
692    
693  The reference-scaled average BE is evaluated by testing the null hypothesis: 
694       
2
( TTRR )
695  versus the alterHHna0t i v: e   hypoWW2tRRhesis:  
696        
2
( TTRR )
697    HHaa  :    WW2RR <  
698  where: 
699     is the population average response of the log-transformed measure for the Test 
700  formulation. 
TT
701       is the population average response of the log-transformed measure for the 
702  Reference formulation. 
RR
703    is the population within subject variance of the Reference formulation. 
2
WWRR
704     is the BE limit. 
2
[ln()]
2
 = WW0
705       and   are predetermined constants.  Refer to the draft guidance for industry 
706  Bioequiv2alence Studies With Pharmacokinetic Endpoints for Drugs Submitted 
 WW0
707  Under an ANDA (August 2021) for the values of   and  .39 
2
708  Testing is usually done at =0.05 and that rejection of the null hypothesiWWs 0supports the 
709  conclusion of bioequivalence. 
710   
711  Narrow therapeutic index BE studies should pass both the reference-scaled approach and the 
712  unscaled average BE limits of 80.00 to 125.00%.  
713   
714  In addition, the test/reference ratio of the within-subject standard deviation should be evaluated.  
715  The within-subject variability comparison of the T and R drug products is carried out by a one-
716  sided F test.  The null hypothesis for this test is the following. 
717   
718     
WWTT
HH0  :WWRR    
 
39 When final, this guidance will represent FDAs current thinking on this topic.   
  19  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
719   
720  And the alternative hypothesis is: 
721   
722     
WWTT
723   
HHaa  :WWRR  <  
724  where  is the within-subject standard deviation for the test product,  is the within-subject 
WT  WR 
725  standard deviation for the reference product and  is the limit to declare the within-subject 
726  variability of the test product is not greater than that of the reference product (refer to the draft 
727  guidance for industry Bioequivalence Studies With Pharmacokinetic Endpoints for Drugs 
728  Submitted Under an ANDA (August 2021) where   was set to 2.5).40  
729   
730    The 100(1-)% CI for  /  is given by 
WT WR
731     
sswwww/sswwRR sswwww/sswwRR
FF2(vv1,vv2),FF12(vv1,vv2)
732  Here, =0.1,   and   are the values of the F-distribution with   
733  (numerator) and   (denominator) degrees of freedom that has probability of /2 and 1-
FF2(vv1,vv2) FF12(vv1,vv2) vv1
734  /2 to its right, respectively. 
735    vv2
736  2.  Statistical Method for Highly Variable Drugs  
737   
738  If a drug is a high variable drug, a partial or fully replicated cross-over design should be used.  
739  The statistical analysis should be carried out using the mixed scaling approach below for both 
740  AUC and C .  
max   
741   
742  The mixed scaling approach:  
743   
744  If the estimated within-subject standard deviation of the RLD is < 0.294, the two one-sided test 
745  procedure should be used to determine BE for the individual PK parameter.  Otherwise, the 
746  reference-scaled procedure should be used to determine BE for the individual PK parameter 
747  together with a point estimate constraint for the estimated test/reference geometric mean ratio. 
748    
749  For the reference-scaled approach the upper BE limit for Test/Reference ratio of geometric 
750  means is    the regulatory constant is  and the point estimate constraint is 
1
751  80.00 to 125.00%. 
  = 0.8  , ww0 = 0.25 
752   
753  Refer to the draft guidance for industry Bioequivalence Studies With Pharmacokinetic Endpoints 
754  for Drugs Submitted Under an ANDA (August 2021) for further details.41  
755   
 
40 When final, this guidance will represent FDAs current thinking on this topic.  
41 When final, this guidance will represent FDAs current thinking on this topic.   
  20  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
756  C.  Comparative Clinical Endpoint Bioequivalence Studies  
757   
758  For some products, the PSG may recommend an appropriately designed comparative clinical 
759  endpoint BE study.  In particular, a comparative clinical endpoint BE study is an option to be 
760  considered for measuring BA or demonstrating BE of dosage forms intended to deliver the active 
761  moiety locally, e.g., topical preparations for the skin, eye, and mucous membranes; oral dosage 
762  forms not intended to be systemically absorbed, e.g., an antacid; bronchodilators administered by 
763  oral inhalation.  
764   
765  In general, these studies will have a randomized, parallel group design, with three arms: test, 
766  reference, and placebo/vehicle. 
767   
768    A placebo/vehicle arm is recommended to demonstrate that the T product and R product 
769  are active and to establish that the study is sufficiently sensitive to detect differences 
770  between products at the lower end of the dose/response curve. 
771   
772  To establish BE, it is recommended that the following compound hypotheses (continuous 
773  endpoint or dichotomous endpoint) be tested.  Rejection of the null hypothesis supports the 
774  conclusion of equivalence of the two products. 
775   
776  For a continuous endpoint: 
777  The null hypothesis for this test is: 
778   
779  H :   /     or   /      
0 T R 1 T R 2
780   
781  versus the alternative hypothesis: 
782  H :   <   /  <   
a 1 T R 2
783     
784  where:   
785     = mean of the primary endpoint for the test group, and 
T 
786      = mean of the primary endpoint for the reference group. 
R
787   
788  The null hypothesis, H , is rejected with a Type I error () of 0.05 (two one-sided tests) if the 
0
789  90% confidence interval for the ratio of the means between T and R products (  / ) is 
T R
790  contained within the interval [ ,  ].  
1 2
791   
792  For a dichotomous endpoint: 
793  The null hypothesis for this test is: 
794   
795  H :      or          
0 T R 1 T R 2
796   
797  versus the alternative hypothesis: 
798  H :   <  -   <   
a 1 T  R 2
799   
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Draft  Not for Implementation 
 
800  where:  
801     = the success rate of the primary endpoint for the treatment group, and  = the 
T R
802  success rate of the primary endpoint for the reference group. 
803   
804  The null hypothesis, H , is rejected with a Type I error () of 0.05 (two one-sided tests) if the 
0
805  estimated 90% confidence interval for the difference of the success rates between T and R 
806  products (  ) is contained within the interval [ ,  ].  
T R 1 2
807   
808    For continuous and binary endpoints, in order to demonstrate adequate study sensitivity, 
809  the test product and reference product should both be statistically superior to placebo 
810  (p<0.05) with regard to the primary endpoint. 
811   
812    Refer to PSGs for comparative clinical endpoint BE study designs, definitions of study 
813  populations, regulatory constant (e.g., equivalence interval limit), and analyses specific to 
814  a given product. 
815   
816  D.  Studies in Multiple Groups  
817   
818  There can be multiple sources of group42 effects in BE studies.  Sometimes, groups reflect 
819  factors arising from study design and conduct. For example, a PK BE study can be carried out in 
820  two or more clinical centers and the study may be considered a multi-group BE study.  The 
821  combination of multiple factors may complicate the designation of group.  Therefore, sponsors 
822  should minimize the group effect in a PK BE study as recommended below: 
823   
824  (1) Dose all groups at the same clinic unless multiple clinics are needed to enroll a 
825  sufficient number of subjects.  
826   
827  (2) Recruit subjects from the same enrollment pool to achieve similar demographics 
828  among groups. 
829   
830  (3) Recruit all subjects, and randomly assign them to group and treatment arm, at study 
831  outset. 
832   
833  (4) Follow the same protocol criteria and procedures for all groups. 
834   
835  (5) When feasible (e.g., when healthy volunteers are enrolled), assign an equal sample 
836  size to each group. 
837    
838  Bioequivalence should be determined based on the overall treatment effect in the whole study 
839  population.  In general, the assessment of BE in the whole study population should be done 
840  without including the treatment and group interaction(s) term in the model, but applicants may 
841  also use other pre-specified models, as appropriate (Fleiss 1986, Permutt 2003, Tsiatis et al. 
 
42 In literature, the term group is sometimes referred to as subgroup. 
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Draft  Not for Implementation 
 
842  2008).43  The assessment of interaction between the treatment and group(s) is important, 
843  especially if any of the first four study design criteria recommended above are not met and the 
844  PK BE data are considered pivotal information for drug approval.  If the interaction term of 
845  group and treatment is significant (Alosh et al. 2015, Grizzle 1965),44 heterogeneity of treatment 
846  effect across groups should be carefully examined and interpreted with care.  If the observed 
847  treatment effect of the products varies greatly among the groups, vigorous attempts should be 
848  made to find an explanation for the heterogeneity in terms of other features of trial management 
849  or subject characteristics, which may suggest appropriate further analysis and interpretation.  
850   
851  It is important that statistical methods and models for the primary BE analysis are fully pre-
852  specified in the protocol or SAP (e.g., in an ANDA study, the applicant should pre-specify 
853  detailed statistical criteria and models to be used if the interaction term of group and treatment is 
854  applicable).  In addition, the statistical model should reflect the multigroup nature of the study.  
855  For example, if subjects are dosed in two groups in a crossover BE study, the model should 
856  reflect the fact that the periods for the first group are different from the periods for the second 
857  group, i.e., the period effect should be nested within the group effect.  
858   
859  When there are multiple centers with very few subjects in some centers and sponsors want to 
860  combine centers in the analysis, any rules for combination should be pre-specified in the protocol 
861  or SAP and a sensitivity analysis is recommended.  More complicated scenarios may be 
862  discussed with the appropriate CDER review division before submission. 
863   
864  E.  Bioequivalence Statistics for Adhesion and Irritation Studies  
865   
866  In terms of the statistical method used in irritation, sensitization or/and adhesion studies for 
867  Transdermal and Topical Delivery Systems, refer to the Statistical Consideration section in the 
868  draft guidance for industry Assessing the Irritation and Sensitization Potential of Transdermal 
869  and Topical Delivery Systems for ANDAs (October 2018) and the Considerations for Statistical 
870  Analysis section in the draft guidance for industry Assessing Adhesion With Transdermal and 
871  Topical Delivery Systems for ANDAs (October 2018).45   
872   
873   
874   
 
43 Fleiss, J.L., 1986, Analysis of Data from Multiclinic Trials, Controlled Clinical Trials, 7(4):267-275; 
Permutt, T., 2003, Probability Models and Computational Models for ANOVA in Multicenter Clinical Trials, 
Journal of Biopharmaceutical Statistics, 13(3):495-505; Tsiatis, A.A., M. Davidian, M. Zhang, and X. Lu, 2008, 
Covariate Adjustment for Two-Sample Treatment Comparisons in Randomized Clinical Trials: A Principled Yet 
Flexible Approach, Statistics in Medicine, 27(23):4658-4677. 
44Alosh, M., K. Fritsch, M. Huque, K. Mahjoob, G. Pennello, M. Rothmann, E. Russek-Cohen, F. Smith, S. Wilson, 
and L. Yue, 2015, Statistical Considerations on Subgroup Analysis in Clinical Trials, Statistics in Biopharmaceutical 
Research, 7(4):286-303; Grizzle, J.E., 1965, The Two-Period Change-Over Design and Its Use in Clinical Trials, 
Biometrics, 21(2):467-480. 
45See also the draft guidance for industry Assessment of Adhesion for Topical and Transdermal Systems Submitted in 
New Drug Applications (July 2021).  When final, these guidances will represent FDAs current thinking on these 
topics.  
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Draft  Not for Implementation 
 
875  F.  Dose Scale for Bioequivalence Assessment  
876   
877  In this method, the BE assessment is based on relative bioavailability of the test and reference 
878  formulations at the site(s) of action.  The relative bioavailability, F, is the ratio of the doses of 
879  test and reference formulations that produce an equivalent PD response.  
880   
881  Generally, the F is estimated by fitting an Emax model that describes the within-study dose-
882  response relationship.  Among available statistical methods for Emax model fitting, nonlinear 
883  mixed effect (NLME) modeling is recommended, because the NLME modeling is capable of 
884  characterizing between-subject variability and residual unexplained variability, and less sensitive 
885  to aberrant observation and missing values. 
886    
887  For model fitting details, refer to the PSG on Orlistat oral capsule.46 
888   
889  To determine BE, the 90% confidence interval for F can be estimated by a bootstrap procedure.  
890  Each bootstrap estimation includes the calculation of F by fitting the selected model to a sample 
891  dose-response data set, which is generated by resampling with replacement.  To maintain the 
892  correlation of observations within subject, resampling by subject (remaining observations from 
893  all T and R treatment arms) is recommended rather than resampling by observations.  The 
894  Agency has also recommended using Efron's bias corrected and accelerated method to compute a 
895  90% confidence interval for F.47  Alternatively, the 90% confidence interval for F can be 
896  estimated without a bootstrap procedure, directly from the point estimate of logF and its standard 
897  error calculated using NLME modeling.  
898   
899  Given the complexity of dose scale analysis for comparative PD BE studies, applicants are 
900  encouraged to contact the Agency early to discuss their proposed study designs and statistical 
901  methods (e.g., alternative modeling approaches, impact of the missing data and the handling 
902  strategy) via the controlled correspondence, pre-ANDA meeting, pre-IND meeting, or pre-NDA 
903  meeting pathway.48 
904   
905  G.  Bioequivalence Studies Using Multiple References  
906   
907  In BE studies with more than two reference treatment arms (e.g., a three-period study including 
908  two references, one from the European Union (EU) and another from the United States, or a 
909  four-period study including test and reference in fed and fasted states), the BE determination 
910  should be based on the comparison between the relevant test and reference products, using only 
911  the data from those products.  The BE analysis for this comparison should be conducted 
912  excluding the data from the non-relevant treatment(s)  for example, in a BE study with a T 
913  product, an EU reference product, and a U.S. reference product, the comparison of the T product 
914  to the U.S. reference product should be based on an analysis excluding the data from the EU 
915  reference.  However, full data from the BE studies, including data comparing the T product that 
 
46 Draft PSG for industry on Orlistat oral capsule (August 2021).  When final, this guidance will represent FDAs 
current thinking on this topic.   
47 Ibid.  
48 See footnotes 8, 9, and 10.   
  24  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
916  is the subject of the application with non-U.S. reference products, should be submitted in the 
917  application for completeness.  The applicant may discuss the study design and statistical 
918  approach with the appropriate CDER review division before study conduct. 
919   
920   
  25  Contains Nonbinding Recommendations 
Draft  Not for Implementation 
 
921  V.  APPENDICES  
922   
923  A.  Choice of Specific Replicated Crossover Designs    
924   
925  Appendix A describes why FDA prefers replicated crossover designs with only two sequences, 
926  and why the Agency recommends the specific designs described in section II.A.1.b of this 
927  guidance. 
928   
929  1.  Reasons Unrelated to Carryover Effects 
930   
931  Each unique combination of sequence and period in a replicated crossover design can be called a 
932  cell of the design.  For example, the two-sequence, four-period design recommended in section 
933  II.A.1.b has eight cells.  The four-sequence, four-period design below has 16 cells. 
934   
935  Period 
936   
937  1          2          3          4 
938   
939  1          T         R         R         T 
940   
941  2          R         T         T         R 
942  Sequence 
943  3          T         T         R         R 
944   
945  4          R         R         T         T 
946   
947  The total number of degrees-of-freedom attributable to comparisons among the cells is just the 
948  number of cells minus one (unless there are cells with no observations). 
949   
950  The fixed effects that are usually included in the statistical analysis are sequence, period, and 
951  treatment (i.e., formulation).  The number of degrees-of-freedom attributable to each fixed effect 
952  is generally equal to the number of levels of the effect, minus one.  Thus, in the case of the two-
953  sequence, four-period design recommended in section V.A.1, there would be 2-1=1 degree-of-
954  freedom due to sequence, 4-1=3 degrees-of-freedom due to period, and 2-1=1 degree-of-freedom 
955  due to treatment, for a total of 1+3+1=5 degrees-of-freedom due to the three fixed 
956  effects.  Because these 5 degrees-of-freedom do not account for all 7 degrees-of-freedom 
957  attributable to the eight cells of the design, the fixed-effects model is not saturated.  There could 
958  be some controversy as to whether a fixed-effects model that accounts for more or all of the 
959  degrees-of-freedom due to cells (i.e., a more saturated fixed-effects model) should be used. For 
960  example, a sequence-by-period-by-treatment interaction effect might be included, which would 
961  fully saturate the fixed-effects model. 
962   
963  If the replicated crossover design has only two sequences, use of only the three main effects 
964  (sequence, period, and treatment) in the fixed-effects model or use of a more saturated model 
965  makes little difference to the results of the analysis, provided there are no missing observations, 
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Draft  Not for Implementation 
 
966  and the study is carried out in one group of subjects.  The least squares point estimate of   
967  will be the same for the main-effects model and for the saturated model.   
968    TT RR
969  If the replicated crossover design has more than two sequences, these advantages are no longer 
970  present.  Main-effects models will generally produce different point estimates of   than 
971  saturated models (unless the number of subjects in each sequence is equal), and there is no well-
972  accepted basis for choosing between these different estimates (though  fromTT  the RR
973  saturated model was determined to be appropriate for use in the reference-scaled average BE 
974  assessment).  Thus, use of designs with only two sequences minimizes oTTr avoiRRd s certain 
975  ambiguities due to specific choices of fixed effects to be included in the statistical model. 
976   
977  2.  Reasons Related to Carryover Effects 
978   
979  One of the reasons to use the four-sequence, four-period design described above is that it is 
980  thought to be optimal if carryover effects are included in the model.   
981   
982  Similarly, the two-sequence, three-period design is thought to be optimal among three-period 
983  replicated crossover designs.  Both of these designs are strongly balanced for carryover effects, 
984  meaning that each treatment is preceded by each other treatment and itself an equal number of 
985  times. 
986   
987       Period 
988   
989  1          2          3 
990   
991  1          T         R         R 
992  Sequence 
993  2          R         T         T 
994   
995  With these designs, no efficiency is lost by including simple first-order carryover effects in the 
996  statistical model.  However, if the possibility of carryover effects is to be considered in the 
997  statistical analysis of BE studies, the possibility of direct-by-carryover interaction should also be 
998  considered.  If direct-by-carryover interaction is present in the statistical model, these favored 
999  designs are no longer optimal.  Indeed, the TRR/RTT design does not permit an unbiased within-
1000  subject estimate of   in the presence of general direct-by-carryover interaction. 
1001   
1002  The issue of whetherTT a purRRely main-effects model or a more saturated model should be specified, 
1003  as described in the previous section, also is affected by possible carryover effects.  If carryover 
1004  effects, including direct-by-carryover interaction, are included in the statistical model, these 
1005  effects will be partially confounded with sequence-by-treatment interaction in four-sequence or 
1006  six-sequence replicated crossover designs, but not in two-sequence designs. 
1007   
1008  In the case of the four-period and three-period designs recommended in section II.A.1.b, the 
1009  estimate of   adjusted for first-order carryover effects, including direct-by-carryover 
TT RR,
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Draft  Not for Implementation 
 
1010  interaction, is as efficient or more efficient than for any other two-treatment replicated crossover 
1011  designs. 
1012   
1013  3.  Two-Period Replicated Crossover Designs 
1014   
1015  For most drug products, two-period replicated crossover designs such as the Balaam design 
1016  (which uses the sequences TR, RT, TT, and RR) should be avoided.  However, the modified 
1017  Balaam design (TR, RT, RR) may be useful for particular drug products (e.g., a long half-life 
1018  drug for which a two-period study would be feasible, but a three-or-more-period study would 
1019  not) when reference-scaled average BE is needed.  
1020   
1021  B.   Rationale for Logarithmic Transformation of Pharmacokinetic Data 
1022   
1023  1.  Clinical Rationale 
1024   
1025  The FDA Generic Drugs Advisory Committee recommended in 1991 that the primary comparison of 
1026  interest in a BE study is the ratio, rather than the difference, between average PK parameter data from 
1027  the T and R formulations.  Using logarithmic transformation, the general linear statistical model 
1028  employed in the analysis of BE data allows inferences about the difference between the two means on 
1029  the log scale, which can then be retransformed into inferences about the ratio of the two averages 
1030  (geometric means) on the original scale.  Logarithmic transformation thus achieves a general 
1031  comparison based on the ratio rather than the differences. 
1032   
1033  2.  Pharmacokinetic Rationale 
1034   
1035  Westlake observed that a multiplicative model is postulated for PK measures in BA/BE studies (i.e., 
1036  AUC and C  but not T ) (Westlake 1973 and 1988).49,50  Assuming that elimination of the drug is 
max, max
1037  first order and only occurs from the central compartment, the following equation holds after an 
1038  extravascular route of administration:  
1039   
1040  AUC = F*D/CL                  
0-
1041                                                                                                             
1042   = F*D/(V*Ke) 
1043                                                                                                              
1044  where F is the fraction absorbed, D is the administered dose, and F*D is the amount of drug absorbed.  
1045  CL is the clearance of a given subject that is the product of the apparent volume of distribution (V) and 
1046  the elimination rate constant (Ke).  The use of AUC as a measure of the amount of drug absorbed 
1047  involves a multiplicative term (CL) that might be regarded as a function of the subject.  For this reason, 
 
49 Westlake, W. J., 1973, The Design and Analysis of Comparative Blood-Level Trials, J. Swarbick, editor, Current 
Concepts in the Pharmaceutical Sciences, Dosage Form Design and Bioavailability, Philadelphia: Lea and Febiger, 
149-179. 
50 Westlake, W. J., 1988, Bioavailability and Bioequivalence of Pharmaceutical Formulations, Biopharmaceutical 
Statistics for Drug Development, 329-352. 
  27  Contains Nonbinding Recommendations 
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1048  Westlake contends that the subject effect is not additive if the data are analyzed on the original scale of 
1049  measurement.   
1050   
1051  Logarithmic transformation of the AUC data will bring the CL (i.e., V*Ke) term into the following 
1052  equation in an additive fashion:  
1053   
1054  lnAUC  = ln F + ln D - ln V - ln Ke                                                     
0-
1055   
1056  Similar arguments were given for C .  The following equation applies for a drug exhibiting one 
max
1057  compartmental characteristic:  
1058   
1059  C  = (F*D/V) * exp(-Ke*T ) 
max max
1060                                                   
1061  where again F, D and V are introduced into the model in a multiplicative manner.  However, after 
1062  logarithmic transformation, the equation becomes:  
1063   
1064  lnC  = ln F + ln D - lnV  Ke*T       
max max
1065   
1066  Thus, log transformation of the C  data also results in the additive treatment of the V term. 
max
1067   
1068  C.       SAS Program Statements for Average Bioequivalence Analysis of Replicated 
1069  Crossover Studies 
1070   
1071  The following illustrates an example of program statements to run the unscaled average BE 
1072  analysis using PROC MIXED in SAS version 9, with SEQ, SUBJ, PER, and TRT identifying 
1073  sequence, subject, period, and treatment variables, respectively, and Y denoting the response 
1074  measure (e.g., log (AUC), log (C )) being analyzed: 
max
1075   
1076  PROC MIXED; 
1077  CLASSES SEQ SUBJ PER TRT; 
1078  MODEL Y = SEQ PER TRT/ DDFM=SATTERTH; 
1079  RANDOM TRT/TYPE=FA0(2) SUB=SUBJ G; 
1080  REPEATED/GRP=TRT SUB=SUBJ; 
1081  ESTIMATE 'T vs. R' TRT 1 -1/CL ALPHA=0.1; 
1082   
1083  The Estimate statement assumes that the code for the test formulation precedes the code for the 
1084  reference formulation in sort order (this would be the case, for example, if T were coded as 1 and 
1085  R were coded as 2).  If the R code precedes the T code in sort order, the coefficients in the 
1086  Estimate statement would be changed to -1 1. 
1087   
1088  In the Random statement, TYPE=FA0(2) could possibly be replaced by TYPE=CSH or UNR.   
1089   
1090  In the Model statement, DDFM=SATTERTH could possibly be replaced by DDFM=KR2.  
1091  However, the detailed model specification should be pre-specified in the protocol or SAP and 
1092  data driven post hoc selection of the model is not allowed.  
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Draft  Not for Implementation 
 
1093   
1094  Additions and modifications to these statements can be made if the study is carried out in more 
1095  than one group of subjects or other complicated scenarios.  Alternative software could also be 
1096  used if same results are generated as in PROC MIXED in SAS.
 
  29