[Federal Register: September 16, 1998 (Volume 63, Number 179)]
[Notices]               
[Page 49583-49598]
From the Federal Register Online via GPO Access [wais.access.gpo.gov]
[DOCID:fr16se98-69]

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DEPARTMENT OF HEALTH AND HUMAN SERVICES

Food and Drug Administration
[Docket No. 97D-0174]

 
International Conference on Harmonisation; Guidance on 
Statistical Principles for Clinical Trials; Availability

AGENCY:  Food and Drug Administration, HHS.

ACTION: Notice.

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SUMMARY: The Food and Drug Administration (FDA) is publishing a 
guidance entitled ``E9 Statistical Principles for Clinical Trials.'' 
The guidance was prepared under the auspices of the International 
Conference on Harmonisation of Technical Requirements for Registration 
of Pharmaceuticals for Human Use (ICH). The guidance is intended to 
provide recommendations to sponsors and scientific experts regarding 
statistical principles and methodology which, when applied to clinical 
trials for marketing applications, will facilitate the general 
acceptance of analyses and conclusions drawn from the trials.

DATES:  Effective September 16, 1998. Submit written comments at any 
time.

ADDRESSES:  Submit written comments on the guidance to the Dockets 
Management Branch (HFA-305), Food and Drug Administration, 5630 Fishers 
Lane, rm. 1061, Rockville, MD 20852. Copies of the guidance are 
available from the Drug Information Branch (HFD-210), Center for Drug 
Evaluation and Research, Food and Drug Administration, 5600 Fishers 
Lane, Rockville, MD 20857, 301-827-4573. Single copies of the guidance 
may be obtained by mail from the Office of Communication, Training and 
Manufacturers Assistance (HFM-40), Center for Biologics Evaluation and 
Research (CBER), 1401 Rockville Pike, Rockville, MD 20852-1448, or by 
calling the CBER Voice Information System at 1-800-835-4709 or 301-827-
1800. Copies may be obtained from CBER's FAX Information System at 1-
888-CBER-FAX or 301-827-3844.

FOR FURTHER INFORMATION CONTACT:
    Regarding the guidance: Robert O'Neill, Center for Drug Evaluation 
and Research (HFD-700), Food and Drug Administration, 5600 Fishers 
Lane, Rockville, MD 20857, 301-827-3195.
    Regarding the ICH: Janet J. Showalter, Office of Health Affairs 
(HFY-20), Food and Drug Administration, 5600 Fishers Lane, Rockville, 
MD 20857, 301-827-0864.

SUPPLEMENTARY INFORMATION:  In recent years, many important initiatives 
have been undertaken by regulatory authorities and industry 
associations to promote international harmonization of regulatory 
requirements. FDA has participated in many meetings designed to enhance 
harmonization and is committed to seeking scientifically based 
harmonized technical procedures for pharmaceutical development. One of 
the goals of harmonization is to identify and then reduce differences 
in technical requirements for drug development among regulatory 
agencies.
    ICH was organized to provide an opportunity for tripartite 
harmonization initiatives to be developed with input from both 
regulatory and industry representatives. FDA also seeks input from 
consumer representatives and others. ICH is concerned with 
harmonization of technical requirements for the registration of 
pharmaceutical products among three regions: The European Union, Japan, 
and the United States. The six ICH sponsors are: The European 
Commission, the European Federation of Pharmaceutical Industries 
Associations, the Japanese Ministry of Health and Welfare, the Japanese 
Pharmaceutical Manufacturers Association, the Centers for Drug 
Evaluation and Research and Biologics Evaluation and Research, FDA, and 
the Pharmaceutical Research and Manufacturers of America. The ICH 
Secretariat, which coordinates the preparation of documentation, is 
provided by the International Federation of Pharmaceutical 
Manufacturers Associations (IFPMA).
    The ICH Steering Committee includes representatives from each of 
the ICH sponsors and the IFPMA, as well as observers from the World 
Health Organization, the Canadian Health Protection Branch, and the 
European Free Trade Area.
    In the Federal Register of May 9, 1997 (62 FR 25712), FDA published 
a draft tripartite guideline entitled ``Statistical Principles for 
Clinical Trials'' (E9). The notice gave interested persons an 
opportunity to submit comments by June 23, 1997.
    After consideration of the comments received and revisions to the 
guidance, a final draft of the guidance was submitted to the ICH 
Steering Committee and endorsed by the three participating regulatory 
agencies on February 5, 1998.
    In accordance with FDA's Good Guidance Practices (62 FR 8961, 
February 27, 1997), this document has been designated a guidance, 
rather than a guideline.
    The guidance addresses principles of statistical methodology 
applied to clinical trials for marketing applications. The guidance 
provides recommendations to sponsors for the design, conduct, analysis, 
and evaluation of clinical trials of an investigational product in the 
context of its overall clinical development. The document also provides 
guidance to scientific experts in preparing application summaries or 
assessing evidence of efficacy and safety, principally from late Phase 
II and Phase III clinical trials. Application of the principles of 
statistical methodology is intended to facilitate the general 
acceptance of analyses and conclusions drawn from clinical trials.
    This guidance represents the agency's current thinking on 
statistical principles for clinical trials of drugs and biologics.

[[Page 49584]]

 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 
statute, regulations, or both.
    As with all of FDA's guidances, the public is encouraged to submit 
written comments with new data or other new information pertinent to 
this guidance. The comments in the docket will be periodically 
reviewed, and, where appropriate, the guidance will be amended. The 
public will be notified of any such amendments through a notice in the 
Federal Register.
    Interested persons may, at any time, submit written comments on the 
guidance to the Dockets Management Branch (address above). Two copies 
of any comments are to be submitted, except that individuals may submit 
one copy. Comments are to be identified with the docket number found in 
brackets in the heading of this document. The guidance and received 
comments may be seen in the office above between 9 a.m. and 4 p.m., 
Monday through Friday. An electronic version of this guidance is 
available on the Internet at ``http://www.fda.gov/cder/guidance/
index.htm'' or at CBER's World Wide Web site at ``http://www.fda.gov/
cber/publications.htm''.
    The text of the guidance follows:

E9 Statistical Principles for Clinical Trials \1\
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    \1\ This guidance represents the agency's current thinking on 
statistical principles for clinical trials of drugs and biologics. 
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 statute, regulations, or both.
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    Note: A glossary of terms and definitions is provided as an 
annex to this guidance.
I. Introduction
  1.1 Background and Purpose
  1.2 Scope and Direction
II. Considerations for Overall Clinical Development
  2.1 Trial Context
    2.1.1 Development Plan
    2.1.2 Confirmatory Trial
    2.1.3 Exploratory Trial
  2.2 Scope of Trials
    2.2.1 Population
    2.2.2 Primary and Secondary Variables
    2.2.3 Composite Variables
    2.2.4 Global Assessment Variables
    2.2.5 Multiple Primary Variables
    2.2.6 Surrogate Variables
    2.2.7 Categorized Variables
  2.3 Design Techniques to Avoid Bias
    2.3.1 Blinding
    2.3.2 Randomization
III. Trial Design Considerations
  3.1 Design Configuration
    3.1.1 Parallel Group Design
    3.1.2 Crossover Design
    3.1.3 Factorial Designs
  3.2 Multicenter Trials
  3.3 Type of Comparison
    3.3.1 Trials to Show Superiority
    3.3.2 Trials to Show Equivalence or Noninferiority
    3.3.3 Trials to Show Dose-Response Relationship
  3.4 Group Sequential Designs
  3.5 Sample Size
  3.6 Data Capture and Processing
IV. Trial Conduct Considerations
  4.1 Trial Monitoring and Interim Analysis
  4.2 Changes in Inclusion and Exclusion Criteria
  4.3 Accrual Rates
  4.4 Sample Size Adjustment
  4.5 Interim Analysis and Early Stopping
  4.6 Role of Independent Data Monitoring Committee (IDMC)
V. Data Analysis Considerations
  5.1 Prespecification of the Analysis
  5.2 Analysis Sets
    5.2.1 Full Analysis Set
    5.2.2 Per Protocol Set
    5.2.3 Roles of the Different Analysis Sets
  5.3 Missing Values and Outliers
  5.4 Data Transformation
  5.5 Estimation, Confidence Intervals, and Hypothesis Testing
  5.6 Adjustment of Significance and Confidence Levels
  5.7 Subgroups, Interactions, and Covariates
  5.8 Integrity of Data and Computer Software Validity
VI. Evaluation of Safety and Tolerability
  6.1 Scope of Evaluation
  6.2 Choice of Variables and Data Collection
  6.3 Set of Subjects to be Evaluated and Presentation of Data
  6.4 Statistical Evaluation
  6.5 Integrated Summary
VII. Reporting
  7.1 Evaluation and Reporting
  7.2 Summarizing the Clinical Database
    7.2.1 Efficacy Data
    7.2.2 Safety Data
    Annex 1 Glossary

I. Introduction

1.1 Background and Purpose

    The efficacy and safety of medicinal products should be 
demonstrated by clinical trials that follow the guidance in ``Good 
Clinical Practice: Consolidated Guideline'' (ICH E6) adopted by the 
ICH, May 1, 1996. The role of statistics in clinical trial design 
and analysis is acknowledged as essential in that ICH guideline. The 
proliferation of statistical research in the area of clinical trials 
coupled with the critical role of clinical research in the drug 
approval process and health care in general necessitate a succinct 
document on statistical issues related to clinical trials. This 
guidance is written primarily to attempt to harmonize the principles 
of statistical methodology applied to clinical trials for marketing 
applications submitted in Europe, Japan, and the United States.
    As a starting point, this guidance utilized the CPMP (Committee 
for Proprietary Medicinal Products) Note for Guidance entitled 
``Biostatistical Methodology in Clinical Trials in Applications for 
Marketing Authorizations for Medicinal Products'' (December, 1994). 
It was also influenced by ``Guidelines on the Statistical Analysis 
of Clinical Studies'' (March 1992) from the Japanese Ministry of 
Health and Welfare and the U.S. Food and Drug Administration 
document entitled ``Guideline for the Format and Content of the 
Clinical and Statistical Sections of a New Drug Application'' (July 
1988). Some topics related to statistical principles and methodology 
are also embedded within other ICH guidances, particularly those 
listed below. The specific guidance that contains related text will 
be identified in various sections of this document.
    E1A: The Extent of Population Exposure to Assess Clinical Safety
    E2A: Clinical Safety Data Management: Definitions and Standards 
for Expedited Reporting
    E2B: Clinical Safety Data Management: Data Elements for 
Transmission of Individual Case Safety Reports
    E2C: Clinical Safety Data Management: Periodic Safety Update 
Reports for Marketed Drugs
    E3: Structure and Content of Clinical Study Reports
    E4: Dose-Response Information to Support Drug Registration
    E5: Ethnic Factors in the Acceptability of Foreign Clinical Data
    E6: Good Clinical Practice: Consolidated Guideline
    E7: Studies in Support of Special Populations: Geriatrics
    E8: General Considerations for Clinical Trials
    E10: Choice of Control Group in Clinical Trials
    M1: Standardization of Medical Terminology for Regulatory 
Purposes
    M3: Nonclinical Safety Studies for the Conduct of Human Clinical 
Trials for Pharmaceuticals.
    This guidance is intended to give direction to sponsors in the 
design, conduct, analysis, and evaluation of clinical trials of an 
investigational product in the context of its overall clinical 
development. The document will also assist scientific experts 
charged with preparing application summaries or assessing evidence 
of efficacy and safety, principally from clinical trials in later 
phases of development.

1.2 Scope and Direction

    The focus of this guidance is on statistical principles. It does 
not address the use of specific statistical procedures or methods. 
Specific procedural steps to ensure that principles are implemented 
properly are the responsibility of the sponsor. Integration of data 
across clinical trials is discussed, but is not a primary focus of 
this guidance. Selected principles and procedures related to data 
management or clinical trial monitoring activities are covered in 
other ICH guidances and are not addressed here.
    This guidance should be of interest to individuals from a broad 
range of scientific disciplines. However, it is assumed that the 
actual responsibility for all statistical work associated with 
clinical trials will lie with an appropriately qualified and 
experienced statistician, as indicated in ICH E6. The role

[[Page 49585]]

and responsibility of the trial statistician (see Glossary), in 
collaboration with other clinical trial professionals, is to ensure 
that statistical principles are applied appropriately in clinical 
trials supporting drug development. Thus, the trial statistician 
should have a combination of education/training and experience 
sufficient to implement the principles articulated in this guidance.
    For each clinical trial contributing to a marketing application, 
all important details of its design and conduct and the principal 
features of its proposed statistical analysis should be clearly 
specified in a protocol written before the trial begins. The extent 
to which the procedures in the protocol are followed and the primary 
analysis is planned a priori will contribute to the degree of 
confidence in the final results and conclusions of the trial. The 
protocol and subsequent amendments should be approved by the 
responsible personnel, including the trial statistician. The trial 
statistician should ensure that the protocol and any amendments 
cover all relevant statistical issues clearly and accurately, using 
technical terminology as appropriate.
    The principles outlined in this guidance are primarily relevant 
to clinical trials conducted in the later phases of development, 
many of which are confirmatory trials of efficacy. In addition to 
efficacy, confirmatory trials may have as their primary variable a 
safety variable (e.g., an adverse event, a clinical laboratory 
variable, or an electrocardiographic measure) or a pharmacodynamic 
or pharmacokinetic variable (as in a confirmatory bioequivalence 
trial). Furthermore, some confirmatory findings may be derived from 
data integrated across trials, and selected principles in this 
guidance are applicable in this situation. Finally, although the 
early phases of drug development consist mainly of clinical trials 
that are exploratory in nature, statistical principles are also 
relevant to these clinical trials. Hence, the substance of this 
document should be applied as far as possible to all phases of 
clinical development.
    Many of the principles delineated in this guidance deal with 
minimizing bias (see Glossary) and maximizing precision. As used in 
this guidance, the term ``bias'' describes the systematic tendency 
of any factors associated with the design, conduct, analysis, and 
interpretation of the results of clinical trials to make the 
estimate of a treatment effect (see Glossary) deviate from its true 
value. It is important to identify potential sources of bias as 
completely as possible so that attempts to limit such bias may be 
made. The presence of bias may seriously compromise the ability to 
draw valid conclusions from clinical trials.
    Some sources of bias arise from the design of the trial, for 
example an assignment of treatments such that subjects at lower risk 
are systematically assigned to one treatment. Other sources of bias 
arise during the conduct and analysis of a clinical trial. For 
example, protocol violations and exclusion of subjects from analysis 
based upon knowledge of subject outcomes are possible sources of 
bias that may affect the accurate assessment of the treatment 
effect. Because bias can occur in subtle or unknown ways and its 
effect is not measurable directly, it is important to evaluate the 
robustness of the results and primary conclusions of the trial. 
Robustness is a concept that refers to the sensitivity of the 
overall conclusions to various limitations of the data, assumptions, 
and analytic approaches to data analysis. Robustness implies that 
the treatment effect and primary conclusions of the trial are not 
substantially affected when analyses are carried out based on 
alternative assumptions or analytic approaches. The interpretation 
of statistical measures of uncertainty of the treatment effect and 
treatment comparisons should involve consideration of the potential 
contribution of bias to the p-value, confidence interval, or 
inference.
    Because the predominant approaches to the design and analysis of 
clinical trials have been based on frequentist statistical methods, 
the guidance largely refers to the use of frequentist methods (see 
Glossary) when discussing hypothesis testing and/or confidence 
intervals. This should not be taken to imply that other approaches 
are not appropriate; the use of Bayesian (see Glossary) and other 
approaches may be considered when the reasons for their use are 
clear and when the resulting conclusions are sufficiently robust.

II. Considerations for Overall Clinical Development

2.1 Trial Context

2.1.1 Development Plan

    The broad aim of the process of clinical development of a new 
drug is to find out whether there is a dose range and schedule at 
which the drug can be shown to be simultaneously safe and effective, 
to the extent that the risk-benefit relationship is acceptable. The 
particular subjects who may benefit from the drug, and the specific 
indications for its use, also need to be defined.
    Satisfying these broad aims usually requires an ordered program 
of clinical trials, each with its own specific objectives (see ICH 
E8). This should be specified in a clinical plan, or a series of 
plans, with appropriate decision points and flexibility to allow 
modification as knowledge accumulates. A marketing application 
should clearly describe the main content of such plans, and the 
contribution made by each trial. Interpretation and assessment of 
the evidence from the total program of trials involves synthesis of 
the evidence from the individual trials (see section 7.2). This is 
facilitated by ensuring that common standards are adopted for a 
number of features of the trials, such as dictionaries of medical 
terms, definition and timing of the main measurements, handling of 
protocol deviations, and so on. A statistical summary, overview, or 
meta-analysis (see Glossary) may be informative when medical 
questions are addressed in more than one trial. Where possible, this 
should be envisaged in the plan so that the relevant trials are 
clearly identified and any necessary common features of their 
designs are specified in advance. Other major statistical issues (if 
any) that are expected to affect a number of trials in a common plan 
should be addressed in that plan.

2.1.2 Confirmatory Trial

    A confirmatory trial is an adequately controlled trial in which 
the hypotheses are stated in advance and evaluated. As a rule, 
confirmatory trials are necessary to provide firm evidence of 
efficacy or safety. In such trials the key hypothesis of interest 
follows directly from the trial's primary objective, is always 
predefined, and is the hypothesis that is subsequently tested when 
the trial is complete. In a confirmatory trial, it is equally 
important to estimate with due precision the size of the effects 
attributable to the treatment of interest and to relate these 
effects to their clinical significance.
    Confirmatory trials are intended to provide firm evidence in 
support of claims; hence adherence to protocols and standard 
operating procedures is particularly important. Unavoidable changes 
should be explained and documented, and their effect examined. A 
justification of the design of each such trial and of other 
important statistical aspects, such as the principal features of the 
planned analysis, should be set out in the protocol. Each trial 
should address only a limited number of questions.
    Firm evidence in support of claims requires that the results of 
the confirmatory trials demonstrate that the investigational product 
under test has clinical benefits. The confirmatory trials should 
therefore be sufficient to answer each key clinical question 
relevant to the efficacy or safety claim clearly and definitively. 
In addition, it is important that the basis for generalization (see 
Glossary) to the intended patient population is understood and 
explained; this may also influence the number and type (e.g., 
specialist or general practitioner) of centers and/or trials needed. 
The results of the confirmatory trial(s) should be robust. In some 
circumstances, the weight of evidence from a single confirmatory 
trial may be sufficient.

2.1.3 Exploratory Trial

    The rationale and design of confirmatory trials nearly always 
rests on earlier clinical work carried out in a series of 
exploratory studies. Like all clinical trials, these exploratory 
studies should have clear and precise objectives. However, in 
contrast to confirmatory trials, their objectives may not always 
lead to simple tests of predefined hypotheses. In addition, 
exploratory trials may sometimes require a more flexible approach to 
design so that changes can be made in response to accumulating 
results. Their analysis may entail data exploration. Tests of 
hypothesis may be carried out, but the choice of hypothesis may be 
data dependent. Such trials cannot be the basis of the formal proof 
of efficacy, although they may contribute to the total body of 
relevant evidence.
    Any individual trial may have both confirmatory and exploratory 
aspects. For example, in most confirmatory trials the data are also 
subjected to exploratory analyses which serve as a basis for 
explaining or supporting their findings and for suggesting further 
hypotheses for later research. The protocol should make a clear 
distinction between the aspects of a trial which will be used for 
confirmatory proof and the aspects

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which will provide data for exploratory analysis.

2.2 Scope of Trials

2.2.1 Population

    In the earlier phases of drug development, the choice of 
subjects for a clinical trial may be heavily influenced by the wish 
to maximize the chance of observing specific clinical effects of 
interest. Hence they may come from a very narrow subgroup of the 
total patient population for which the drug may eventually be 
indicated. However, by the time the confirmatory trials are 
undertaken, the subjects in the trials should more closely mirror 
the target population. In these trials, it is generally helpful to 
relax the inclusion and exclusion criteria as much as possible 
within the target population while maintaining sufficient 
homogeneity to permit precise estimation of treatment effects. No 
individual clinical trial can be expected to be totally 
representative of future users because of the possible influences of 
geographical location, the time when it is conducted, the medical 
practices of the particular investigator(s) and clinics, and so on. 
However, the influence of such factors should be reduced wherever 
possible and subsequently discussed during the interpretation of the 
trial results.

2.2.2 Primary and Secondary Variables

    The primary variable (``target'' variable, primary endpoint) 
should be the variable capable of providing the most clinically 
relevant and convincing evidence directly related to the primary 
objective of the trial. There should generally be only one primary 
variable. This will usually be an efficacy variable, because the 
primary objective of most confirmatory trials is to provide strong 
scientific evidence regarding efficacy. Safety/tolerability may 
sometimes be the primary variable, and will always be an important 
consideration. Measurements relating to quality of life and health 
economics are further potential primary variables. The selection of 
the primary variable should reflect the accepted norms and standards 
in the relevant field of research. The use of a reliable and 
validated variable with which experience has been gained either in 
earlier studies or in published literature is recommended. There 
should be sufficient evidence that the primary variable can provide 
a valid and reliable measure of some clinically relevant and 
important treatment benefit in the patient population described by 
the inclusion and exclusion criteria. The primary variable should 
generally be the one used when estimating the sample size (see 
section 3.5).
    In many cases, the approach to assessing subject outcome may not 
be straightforward and should be carefully defined. For example, it 
is inadequate to specify mortality as a primary variable without 
further clarification; mortality may be assessed by comparing 
proportions alive at fixed points in time or by comparing overall 
distributions of survival times over a specified interval. Another 
common example is a recurring event; the measure of treatment effect 
may again be a simple dichotomous variable (any occurrence during a 
specified interval), time to first occurrence, rate of occurrence 
(events per time units of observation), and so on. The assessment of 
functional status over time in studying treatment for chronic 
disease presents other challenges in selection of the primary 
variable. There are many possible approaches, such as comparisons of 
the assessments done at the beginning and end of the interval of 
observation, comparisons of slopes calculated from all assessments 
throughout the interval, comparisons of the proportions of subjects 
exceeding or declining beyond a specified threshold, or comparisons 
based on methods for repeated measures data. To avoid multiplicity 
concerns arising from post hoc definitions, it is critical to 
specify in the protocol the precise definition of the primary 
variable as it will be used in the statistical analysis. In 
addition, the clinical relevance of the specific primary variable 
selected and the validity of the associated measurement procedures 
will generally need to be addressed and justified in the protocol.
    The primary variable should be specified in the protocol, along 
with the rationale for its selection. Redefinition of the primary 
variable after unblinding will almost always be unacceptable, since 
the biases this introduces are difficult to assess. When the 
clinical effect defined by the primary objective is to be measured 
in more than one way, the protocol should identify one of the 
measurements as the primary variable on the basis of clinical 
relevance, importance, objectivity, and/or other relevant 
characteristics, whenever such selection is feasible.
    Secondary variables are either supportive measurements related 
to the primary objective or measurements of effects related to the 
secondary objectives. Their predefinition in the protocol is also 
important, as well as an explanation of their relative importance 
and roles in interpretation of trial results. The number of 
secondary variables should be limited and should be related to the 
limited number of questions to be answered in the trial.

 2.2.3 Composite Variables

    If a single primary variable cannot be selected from multiple 
measurements associated with the primary objective, another useful 
strategy is to integrate or combine the multiple measurements into a 
single or ``composite'' variable, using a predefined algorithm. 
Indeed, the primary variable sometimes arises as a combination of 
multiple clinical measurements (e.g., the rating scales used in 
arthritis, psychiatric disorders, and elsewhere). This approach 
addresses the multiplicity problem without requiring adjustment to 
the Type I error. The method of combining the multiple measurements 
should be specified in the protocol, and an interpretation of the 
resulting scale should be provided in terms of the size of a 
clinically relevant benefit. When a composite variable is used as a 
primary variable, the components of this variable may sometimes be 
analyzed separately, where clinically meaningful and validated. When 
a rating scale is used as a primary variable, it is especially 
important to address factors such as content validity (see 
Glossary), inter- and intrarater reliability (see Glossary), and 
responsiveness for detecting changes in the severity of disease.

2.2.4 Global Assessment Variables

    In some cases, ``global assessment'' variables (see Glossary) 
are developed to measure the overall safety, overall efficacy, and/
or overall usefulness of a treatment. This type of variable 
integrates objective variables and the investigator's overall 
impression about the state or change in the state of the subject, 
and is usually a scale of ordered categorical ratings. Global 
assessments of overall efficacy are well established in some 
therapeutic areas, such as neurology and psychiatry.
    Global assessment variables generally have a subjective 
component. When a global assessment variable is used as a primary or 
secondary variable, fuller details of the scale should be included 
in the protocol with respect to:
    (1) The relevance of the scale to the primary objective of the 
trial;
    (2) The basis for the validity and reliability of the scale;
    (3) How to utilize the data collected on an individual subject 
to assign him/her to a unique category of the scale;
    (4) How to assign subjects with missing data to a unique 
category of the scale, or otherwise evaluate them.
    If objective variables are considered by the investigator when 
making a global assessment, then those objective variables should be 
considered as additional primary or, at least, important secondary 
variables.
    Global assessment of usefulness integrates components of both 
benefit and risk and reflects the decisionmaking process of the 
treating physician, who must weigh benefit and risk in making 
product use decisions. A problem with global usefulness variables is 
that their use could in some cases lead to the result of two 
products being declared equivalent despite having very different 
profiles of beneficial and adverse effects. For example, judging the 
global usefulness of a treatment as equivalent or superior to an 
alternative may mask the fact that it has little or no efficacy but 
fewer adverse effects. Therefore, it is not advisable to use a 
global usefulness variable as a primary variable. If global 
usefulness is specified as primary, it is important to consider 
specific efficacy and safety outcomes separately as additional 
primary variables.

2.2.5 Multiple Primary Variables

    It may sometimes be desirable to use more than one primary 
variable, each of which (or a subset of which) could be sufficient 
to cover the range of effects of the therapies. The planned manner 
of interpretation of this type of evidence should be carefully 
spelled out. It should be clear whether an impact on any of the 
variables, some minimum number of them, or all of them, would be 
considered necessary to achieve the trial objectives. The primary 
hypothesis or hypotheses and parameters of interest (e.g., mean, 
percentage, distribution) should be clearly stated with respect to 
the primary variables identified, and the approach to statistical 
inference described. The effect on the Type I error should be 
explained because of the potential for multiplicity problems (see 
section 5.6);

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the method of controlling Type I error should be given in the 
protocol. The extent of intercorrelation among the proposed primary 
variables may be considered in evaluating the impact on Type I 
error. If the purpose of the trial is to demonstrate effects on all 
of the designated primary variables, then there is no need for 
adjustment of the Type I error, but the impact on Type II error and 
sample size should be carefully considered.

2.2.6 Surrogate Variables

    When direct assessment of the clinical benefit to the subject 
through observing actual clinical efficacy is not practical, 
indirect criteria (surrogate variables--see Glossary) may be 
considered. Commonly accepted surrogate variables are used in a 
number of indications where they are believed to be reliable 
predictors of clinical benefit. There are two principal concerns 
with the introduction of any proposed surrogate variable. First, it 
may not be a true predictor of the clinical outcome of interest. For 
example, it may measure treatment activity associated with one 
specific pharmacological mechanism, but may not provide full 
information on the range of actions and ultimate effects of the 
treatment, whether positive or negative. There have been many 
instances where treatments showing a highly positive effect on a 
proposed surrogate have ultimately been shown to be detrimental to 
the subjects' clinical outcome; conversely, there are cases of 
treatments conferring clinical benefit without measurable impact on 
proposed surrogates. Secondly, proposed surrogate variables may not 
yield a quantitative measure of clinical benefit that can be weighed 
directly against adverse effects. Statistical criteria for 
validating surrogate variables have been proposed but the experience 
with their use is relatively limited. In practice, the strength of 
the evidence for surrogacy depends upon (i) the biological 
plausibility of the relationship, (ii) the demonstration in 
epidemiological studies of the prognostic value of the surrogate for 
the clinical outcome, and (iii) evidence from clinical trials that 
treatment effects on the surrogate correspond to effects on the 
clinical outcome. Relationships between clinical and surrogate 
variables for one product do not necessarily apply to a product with 
a different mode of action for treating the same disease.

2.2.7 Categorized Variables

    Dichotomization or other categorization of continuous or ordinal 
variables may sometimes be desirable. Criteria of ``success'' and 
``response'' are common examples of dichotomies that should be 
specified precisely in terms of, for example, a minimum percentage 
improvement (relative to baseline) in a continuous variable or a 
ranking categorized as at or above some threshold level (e.g., 
``good'') on an ordinal rating scale. The reduction of diastolic 
blood pressure below 90 mmHg is a common dichotomization. 
Categorizations are most useful when they have clear clinical 
relevance. The criteria for categorization should be predefined and 
specified in the protocol, as knowledge of trial results could 
easily bias the choice of such criteria. Because categorization 
normally implies a loss of information, a consequence will be a loss 
of power in the analysis; this should be accounted for in the sample 
size calculation.

2.3 Design Techniques to Avoid Bias

    The most important design techniques for avoiding bias in 
clinical trials are blinding and randomization, and these should be 
normal features of most controlled clinical trials intended to be 
included in a marketing application. Most such trials follow a 
double-blind approach in which treatments are prepacked in 
accordance with a suitable randomization schedule, and supplied to 
the trial center(s) labeled only with the subject number and the 
treatment period, so that no one involved in the conduct of the 
trial is aware of the specific treatment allocated to any particular 
subject, not even as a code letter. This approach will be assumed in 
section 2.3.1 and most of section 2.3.2, exceptions being considered 
at the end.
    Bias can also be reduced at the design stage by specifying 
procedures in the protocol aimed at minimizing any anticipated 
irregularities in trial conduct that might impair a satisfactory 
analysis, including various types of protocol violations, 
withdrawals and missing values. The protocol should consider ways 
both to reduce the frequency of such problems and to handle the 
problems that do occur in the analysis of data.

2.3.1 Blinding

    Blinding or masking is intended to limit the occurrence of 
conscious and unconscious bias in the conduct and interpretation of 
a clinical trial arising from the influence that the knowledge of 
treatment may have on the recruitment and allocation of subjects, 
their subsequent care, the attitudes of subjects to the treatments, 
the assessment of end-points, the handling of withdrawals, the 
exclusion of data from analysis, and so on. The essential aim is to 
prevent identification of the treatments until all such 
opportunities for bias have passed.
    A double-blind trial is one in which neither the subject nor any 
of the investigator or sponsor staff involved in the treatment or 
clinical evaluation of the subjects are aware of the treatment 
received. This includes anyone determining subject eligibility, 
evaluating endpoints, or assessing compliance with the protocol. 
This level of blinding is maintained throughout the conduct of the 
trial, and only when the data are cleaned to an acceptable level of 
quality will appropriate personnel be unblinded. If any of the 
sponsor staff who are not involved in the treatment or clinical 
evaluation of the subjects are required to be unblinded to the 
treatment code (e.g., bioanalytical scientists, auditors, those 
involved in serious adverse event reporting), the sponsor should 
have adequate standard operating procedures to guard against 
inappropriate dissemination of treatment codes. In a single-blind 
trial the investigator and/or his staff are aware of the treatment 
but the subject is not, or vice versa. In an open-label trial the 
identity of treatment is known to all. The double-blind trial is the 
optimal approach. This requires that the treatments to be applied 
during the trial cannot be distinguished (by appearance, taste, 
etc.) either before or during administration, and that the blind is 
maintained appropriately during the whole trial.
    Difficulties in achieving the double-blind ideal can arise: The 
treatments may be of a completely different nature, for example, 
surgery and drug therapy; two drugs may have different formulations 
and, although they could be made indistinguishable by the use of 
capsules, changing the formulation might also change the 
pharmacokinetic and/or pharmacodynamic properties and hence 
necessitate that bioequivalence of the formulations be established; 
the daily pattern of administration of two treatments may differ. 
One way of achieving double-blind conditions under these 
circumstances is to use a ``double-dummy'' (see Glossary) technique. 
This technique may sometimes force an administration scheme that is 
sufficiently unusual to influence adversely the motivation and 
compliance of the subjects. Ethical difficulties may also interfere 
with its use when, for example, it entails dummy operative 
procedures. Nevertheless, extensive efforts should be made to 
overcome these difficulties.
    The double-blind nature of some clinical trials may be partially 
compromised by apparent treatment induced effects. In such cases, 
blinding may be improved by blinding investigators and relevant 
sponsor staff to certain test results (e.g., selected clinical 
laboratory measures). Similar approaches (see below) to minimizing 
bias in open-label trials should be considered in trials where 
unique or specific treatment effects may lead to unblinding 
individual patients.
    If a double-blind trial is not feasible, then the single-blind 
option should be considered. In some cases only an open-label trial 
is practically or ethically possible. Single-blind and open-label 
trials provide additional flexibility, but it is particularly 
important that the investigator's knowledge of the next treatment 
should not influence the decision to enter the subject; this 
decision should precede knowledge of the randomized treatment. For 
these trials, consideration should be given to the use of a 
centralized randomization method, such as telephone randomization, 
to administer the assignment of randomized treatment. In addition, 
clinical assessments should be made by medical staff who are not 
involved in treating the subjects and who remain blind to treatment. 
In single-blind or open-label trials every effort should be made to 
minimize the various known sources of bias and primary variables 
should be as objective as possible. The reasons for the degree of 
blinding adopted, as well as steps taken to minimize bias by other 
means, should be explained in the protocol. For example, the sponsor 
should have adequate standard operating procedures to ensure that 
access to the treatment code is appropriately restricted during the 
process of cleaning the database prior to its release for analysis.
    Breaking the blind (for a single subject) should be considered 
only when knowledge of the treatment assignment is deemed essential 
by the subject's physician for the subject's care. Any intentional 
or unintentional breaking of the blind should be reported and 
explained at the end of the trial,

[[Page 49588]]

irrespective of the reason for its occurrence. The procedure and 
timing for revealing the treatment assignments should be documented.
    In this document, the blind review (see Glossary) of data refers 
to the checking of data during the period of time between trial 
completion (the last observation on the last subject) and the 
breaking of the blind.

2.3.2 Randomization

    Randomization introduces a deliberate element of chance into the 
assignment of treatments to subjects in a clinical trial. During 
subsequent analysis of the trial data, it provides a sound 
statistical basis for the quantitative evaluation of the evidence 
relating to treatment effects. It also tends to produce treatment 
groups in which the distributions of prognostic factors, known and 
unknown, are similar. In combination with blinding, randomization 
helps to avoid possible bias in the selection and allocation of 
subjects arising from the predictability of treatment assignments.
    The randomization schedule of a clinical trial documents the 
random allocation of treatments to subjects. In the simplest 
situation it is a sequential list of treatments (or treatment 
sequences in a crossover trial) or corresponding codes by subject 
number. The logistics of some trials, such as those with a screening 
phase, may make matters more complicated, but the unique preplanned 
assignment of treatment, or treatment sequence, to subject should be 
clear. Different trial designs will necessitate different procedures 
for generating randomization schedules. The randomization schedule 
should be reproducible (if the need arises).
    Although unrestricted randomization is an acceptable approach, 
some advantages can generally be gained by randomizing subjects in 
blocks. This helps to increase the comparability of the treatment 
groups, particularly when subject characteristics may change over 
time, as a result, for example, of changes in recruitment policy. It 
also provides a better guarantee that the treatment groups will be 
of nearly equal size. In crossover trials, it provides the means of 
obtaining balanced designs with their greater efficiency and easier 
interpretation. Care should be taken to choose block lengths that 
are sufficiently short to limit possible imbalance, but that are 
long enough to avoid predictability towards the end of the sequence 
in a block. Investigators and other relevant staff should generally 
be blind to the block length; the use of two or more block lengths, 
randomly selected for each block, can achieve the same purpose. 
(Theoretically, in a double-blind trial predictability does not 
matter, but the pharmacological effects of drugs may provide the 
opportunity for intelligent guesswork.)
    In multicenter trials (see Glossary), the randomization 
procedures should be organized centrally. It is advisable to have a 
separate random scheme for each center, i.e., to stratify by center 
or to allocate several whole blocks to each center. More generally, 
stratification by important prognostic factors measured at baseline 
(e.g., severity of disease, age, sex) may sometimes be valuable in 
order to promote balanced allocation within strata; this has greater 
potential benefit in small trials. The use of more than two or three 
stratification factors is rarely necessary, is less successful at 
achieving balance, and is logistically troublesome. The use of a 
dynamic allocation procedure (see below) may help to achieve balance 
across a number of stratification factors simultaneously, provided 
the rest of the trial procedures can be adjusted to accommodate an 
approach of this type. Factors on which randomization has been 
stratified should be accounted for later in the analysis.
    The next subject to be randomized into a trial should always 
receive the treatment corresponding to the next free number in the 
appropriate randomization schedule (in the respective stratum, if 
randomization is stratified). The appropriate number and associated 
treatment for the next subject should only be allocated when entry 
of that subject to the randomized part of the trial has been 
confirmed. Details of the randomization that facilitate 
predictability (e.g., block length) should not be contained in the 
trial protocol. The randomization schedule itself should be filed 
securely by the sponsor or an independent party in a manner that 
ensures that blindness is properly maintained throughout the trial. 
Access to the randomization schedule during the trial should take 
into account the possibility that, in an emergency, the blind may 
have to be broken for any subject. The procedure to be followed, the 
necessary documentation, and the subsequent treatment and assessment 
of the subject should all be described in the protocol.
    Dynamic allocation is an alternative procedure in which the 
allocation of treatment to a subject is influenced by the current 
balance of allocated treatments and, in a stratified trial, by the 
stratum to which the subject belongs and the balance within that 
stratum. Deterministic dynamic allocation procedures should be 
avoided and an appropriate element of randomization should be 
incorporated for each treatment allocation. Every effort should be 
made to retain the double-blind status of the trial. For example, 
knowledge of the treatment code may be restricted to a central trial 
office from where the dynamic allocation is controlled, generally 
through telephone contact. This in turn permits additional checks of 
eligibility criteria and establishes entry into the trial, features 
that can be valuable in certain types of multicenter trials. The 
usual system of prepacking and labeling drug supplies for double-
blind trials can then be followed, but the order of their use is no 
longer sequential. It is desirable to use appropriate computer 
algorithms to keep personnel at the central trial office blind to 
the treatment code. The complexity of the logistics and potential 
impact on the analysis should be carefully evaluated when 
considering dynamic allocation.

III. Trial Design Considerations

3.1 Design Configuration

3.1.1 Parallel Group Design

    The most common clinical trial design for confirmatory trials is 
the parallel group design in which subjects are randomized to one of 
two or more arms, each arm being allocated a different treatment. 
These treatments will include the investigational product at one or 
more doses, and one or more control treatments, such as placebo and/
or an active comparator. The assumptions underlying this design are 
less complex than for most other designs. However, as with other 
designs, there may be additional features of the trial that 
complicate the analysis and interpretation (e.g., covariates, 
repeated measurements over time, interactions between design 
factors, protocol violations, dropouts (see Glossary), and 
withdrawals).

3.1.2 Crossover Design

    In the crossover design, each subject is randomized to a 
sequence of two or more treatments and hence acts as his own control 
for treatment comparisons. This simple maneuver is attractive 
primarily because it reduces the number of subjects and usually the 
number of assessments needed to achieve a specific power, sometimes 
to a marked extent. In the simplest 2 2 crossover design, each 
subject receives each of two treatments in randomized order in two 
successive treatment periods, often separated by a washout period. 
The most common extension of this entails comparing n(<ls-thn-eq>2) 
treatments in n periods, each subject receiving all n treatments. 
Numerous variations exist, such as designs in which each subject 
receives a subset of n(<ls-thn-eq>2) treatments, or designs in which 
treatments are repeated within a subject.
    Crossover designs have a number of problems that can invalidate 
their results. The chief difficulty concerns carryover, that is, the 
residual influence of treatments in subsequent treatment periods. In 
an additive model, the effect of unequal carryover will be to bias 
direct treatment comparisons. In the 2 2 design, the carryover 
effect cannot be statistically distinguished from the interaction 
between treatment and period and the test for either of these 
effects lacks power because the corresponding contrast is ``between 
subject.'' This problem is less acute in higher order designs, but 
cannot be entirely dismissed.
    When the crossover design is used, it is therefore important to 
avoid carryover. This is best done by selective and careful use of 
the design on the basis of adequate knowledge of both the disease 
area and the new medication. The disease under study should be 
chronic and stable. The relevant effects of the medication should 
develop fully within the treatment period. The washout periods 
should be sufficiently long for complete reversibility of drug 
effect. The fact that these conditions are likely to be met should 
be established in advance of the trial by means of prior information 
and data.
    There are additional problems that need careful attention in 
crossover trials. The most notable of these are the complications of 
analysis and interpretation arising from the loss of subjects. Also, 
the potential for carryover leads to difficulties in assigning 
adverse events that occur in later treatment periods to the 
appropriate treatment. These and other issues are described in ICH 
E4. The crossover design should generally be restricted to 
situations where losses of

[[Page 49589]]

subjects from the trial are expected to be small.
    A common, and generally satisfactory, use of the 2 2 crossover 
design is to demonstrate the bioequivalence of two formulations of 
the same medication. In this particular application in healthy 
volunteers, carryover effects on the relevant pharmacokinetic 
variable are most unlikely to occur if the wash-out time between the 
two periods is sufficiently long. However, it is still important to 
check this assumption during analysis on the basis of the data 
obtained, for example, by demonstrating that no drug is detectable 
at the start of each period.

3.1.3 Factorial Designs

    In a factorial design, two or more treatments are evaluated 
simultaneously through the use of varying combinations of the 
treatments. The simplest example is the 2 2 factorial design in 
which subjects are randomly allocated to one of the four possible 
combinations of two treatments, A and B. These are: A alone; B 
alone; both A and B; neither A nor B. In many cases, this design is 
used for the specific purpose of examining the interaction of A and 
B. The statistical test of interaction may lack power to detect an 
interaction if the sample size was calculated based on the test for 
main effects. This consideration is important when this design is 
used for examining the joint effects of A and B, in particular, if 
the treatments are likely to be used together.
    Another important use of the factorial design is to establish 
the dose-response characteristics of the simultaneous use of 
treatments C and D, especially when the efficacy of each monotherapy 
has been established at some dose in prior trials. A number, m, of 
doses of C is selected, usually including a zero dose (placebo), and 
a similar number, n, of doses of D. The full design then consists of 
m n treatment groups, each receiving a different combination of 
doses of C and D. The resulting estimate of the response surface may 
then be used to help identify an appropriate combination of doses of 
C and D for clinical use (see ICH E4).
    In some cases, the 2 2 design may be used to make efficient use 
of clinical trial subjects by evaluating the efficacy of the two 
treatments with the same number of subjects as would be required to 
evaluate the efficacy of either one alone. This strategy has proved 
to be particularly valuable for very large mortality trials. The 
efficiency and validity of this approach depends upon the absence of 
interaction between treatments A and B so that the effects of A and 
B on the primary efficacy variables follow an additive model. Hence 
the effect of A is virtually identical whether or not it is 
additional to the effect of B. As for the crossover trial, evidence 
that this condition is likely to be met should be established in 
advance of the trial by means of prior information and data.

3.2 Multicenter Trials

    Multicenter trials are carried out for two main reasons. First, 
a multicenter trial is an accepted way of evaluating a new 
medication more efficiently. Under some circumstances, it may 
present the only practical means of accruing sufficient subjects to 
satisfy the trial objective within a reasonable timeframe. 
Multicenter trials of this nature may, in principle, be carried out 
at any stage of clinical development. They may have several centers 
with a large number of subjects per center or, in the case of a rare 
disease, they may have a large number of centers with very few 
subjects per center.
    Second, a trial may be designed as a multicenter (and multi-
investigator) trial primarily to provide a better basis for the 
subsequent generalization of its findings. This arises from the 
possibility of recruiting the subjects from a wider population and 
of administering the medication in a broader range of clinical 
settings, thus presenting an experimental situation that is more 
typical of future use. In this case, the involvement of a number of 
investigators also gives the potential for a wider range of clinical 
judgment concerning the value of the medication. Such a trial would 
be a confirmatory trial in the later phases of drug development and 
would be likely to involve a large number of investigators and 
centers. It might sometimes be conducted in a number of different 
countries to facilitate generalizability (see Glossary) even 
further.
    If a multicenter trial is to be meaningfully interpreted and 
extrapolated, then the manner in which the protocol is implemented 
should be clear and similar at all centers. Furthermore, the usual 
sample size and power calculations depend upon the assumption that 
the differences between the compared treatments in the centers are 
unbiased estimates of the same quantity. It is important to design 
the common protocol and to conduct the trial with this background in 
mind. Procedures should be standardized as completely as possible. 
Variation of evaluation criteria and schemes can be reduced by 
investigator meetings, by the training of personnel in advance of 
the trial, and by careful monitoring during the trial. Good design 
should generally aim to achieve the same distribution of subjects to 
treatments within each center and good management should maintain 
this design objective. Trials that avoid excessive variation in the 
numbers of subjects per center and trials that avoid a few very 
small centers have advantages if it is later found necessary to take 
into account the heterogeneity of the treatment effect from center 
to center, because they reduce the differences between different 
weighted estimates of the treatment effect. (This point does not 
apply to trials in which all centers are very small and in which 
center does not feature in the analysis.) Failure to take these 
precautions, combined with doubts about the homogeneity of the 
results, may, in severe cases, reduce the value of a multicenter 
trial to such a degree that it cannot be regarded as giving 
convincing evidence for the sponsor's claims.
    In the simplest multicenter trial, each investigator will be 
responsible for the subjects recruited at one hospital, so that 
``center'' is identified uniquely by either investigator or 
hospital. In many trials, however, the situation is more complex. 
One investigator may recruit subjects from several hospitals; one 
investigator may represent a team of clinicians (subinvestigators) 
who all recruit subjects from their own clinics at one hospital or 
at several associated hospitals. Whenever there is room for doubt 
about the definition of center in a statistical model, the 
statistical section of the protocol (see section 5.1) should clearly 
define the term (e.g., by investigator, location or region) in the 
context of the particular trial. In most instances, centers can be 
satisfactorily defined through the investigators. (ICH E6 provides 
relevant guidance in this respect.) In cases of doubt, the aim 
should be to define centers to achieve homogeneity in the important 
factors affecting the measurements of the primary variables and the 
influence of the treatments. Any rules for combining centers in the 
analysis should be justified and specified prospectively in the 
protocol where possible, but in any case decisions concerning this 
approach should always be taken blind to treatment, for example, at 
the time of the blind review.
    The statistical model to be adopted for the estimation and 
testing of treatment effects should be described in the protocol. 
The main treatment effect may be investigated first using a model 
that allows for center differences, but does not include a term for 
treatment-by-center interaction. If the treatment effect is 
homogeneous across centers, the routine inclusion of interaction 
terms in the model reduces the efficiency of the test for the main 
effects. In the presence of true heterogeneity of treatment effects, 
the interpretation of the main treatment effect is controversial.
    In some trials, for example, some large mortality trials with 
very few subjects per center, there may be no reason to expect the 
centers to have any influence on the primary or secondary variables 
because they are unlikely to represent influences of clinical 
importance. In other trials, it may be recognized from the start 
that the limited numbers of subjects per center will make it 
impracticable to include the center effects in the statistical 
model. In these cases, it is not considered appropriate to include a 
term for center in the model, and it is not necessary to stratify 
the randomization by center in this situation.
    If positive treatment effects are found in a trial with 
appreciable numbers of subjects per center, there should generally 
be an exploration of the heterogeneity of treatment effects across 
centers, as this may affect the generalizability of the conclusions. 
Marked heterogeneity may be identified by graphical display of the 
results of individual centers or by analytical methods, such as a 
significance test of the treatment-by-center interaction. When using 
such a statistical significance test, it is important to recognize 
that this generally has low power in a trial designed to detect the 
main effect of treatment.
    If heterogeneity of treatment effects is found, this should be 
interpreted with care, and vigorous attempts should be made to find 
an explanation in terms of other features of trial management or 
subject characteristics. Such an explanation will usually suggest 
appropriate further analysis and interpretation. In the absence of 
an explanation, heterogeneity of treatment effect, as evidenced, for 
example, by marked quantitative interactions (see Glossary) implies 
that alternative estimates of the

[[Page 49590]]

treatment effect, giving different weights to the centers, may be 
needed to substantiate the robustness of the estimates of treatment 
effect. It is even more important to understand the basis of any 
heterogeneity characterized by marked qualitative interactions (see 
Glossary), and failure to find an explanation may necessitate 
further clinical trials before the treatment effect can be reliably 
predicted.
    Up to this point, the discussion of multicenter trials has been 
based on the use of fixed effect models. Mixed models may also be 
used to explore the heterogeneity of the treatment effect. These 
models consider center and treatment-by-center effects to be random 
and are especially relevant when the number of sites is large.

3.3 Type of Comparison

3.3.1 Trials to Show Superiority

    Scientifically, efficacy is most convincingly established by 
demonstrating superiority to placebo in a placebo-controlled trial, 
by showing superiority to an active control treatment, or by 
demonstrating a dose-response relationship. This type of trial is 
referred to as a ``superiority'' trial (see Glossary). In this 
guidance superiority trials are generally assumed, unless explicitly 
stated otherwise.
    For serious illnesses, when a therapeutic treatment that has 
been shown to be efficacious by superiority trial(s) exists, a 
placebo-controlled trial may be considered unethical. In that case 
the scientifically sound use of an active treatment as a control 
should be considered. The appropriateness of placebo control versus 
active control should be considered on a trial-by-trial basis.

3.3.2 Trials to Show Equivalence or Noninferiority

    In some cases, an investigational product is compared to a 
reference treatment without the objective of showing superiority. 
This type of trial is divided into two major categories according to 
its objective; one is an ``equivalence'' trial (see Glossary) and 
the other is a ``noninferiority'' trial (see Glossary).
    Bioequivalence trials fall into the former category. In some 
situations, clinical equivalence trials are also undertaken for 
other regulatory reasons such as demonstrating the clinical 
equivalence of a generic product to the marketed product when the 
compound is not absorbed and therefore not present in the blood 
stream.
    Many active control trials are designed to show that the 
efficacy of an investigational product is no worse than that of the 
active comparator and, hence, fall into the latter category. Another 
possibility is a trial in which multiple doses of the 
investigational drug are compared with the recommended dose or 
multiple doses of the standard drug. The purpose of this design is 
simultaneously to show a dose-response relationship for the 
investigational product and to compare the investigational product 
with the active control.
    Active control equivalence or noninferiority trials may also 
incorporate a placebo, thus pursuing multiple goals in one trial. 
For example, they may establish superiority to placebo and hence 
validate the trial design and simultaneously evaluate the degree of 
similarity of efficacy and safety to the active comparator. There 
are well-known difficulties associated with the use of the active 
control equivalence (or noninferiority) trials that do not 
incorporate a placebo or do not use multiple doses of the new drug. 
These relate to the implicit lack of any measure of internal 
validity (in contrast to superiority trials), thus making external 
validation necessary. The equivalence (or noninferiority) trial is 
not conservative in nature, so that many flaws in the design or 
conduct of the trial will tend to bias the results towards a 
conclusion of equivalence. For these reasons, the design features of 
such trials should receive special attention and their conduct needs 
special care. For example, it is especially important to minimize 
the incidence of violations of the entry criteria, noncompliance, 
withdrawals, losses to follow-up, missing data, and other deviations 
from the protocol, and also to minimize their impact on the 
subsequent analyses.
    Active comparators should be chosen with care. An example of a 
suitable active comparator would be a widely used therapy whose 
efficacy in the relevant indication has been clearly established and 
quantified in well-designed and well-documented superiority trial(s) 
and that can be reliably expected to exhibit similar efficacy in the 
contemplated active control trial. To this end, the new trial should 
have the same important design features (primary variables, the dose 
of the active comparator, eligibility criteria, and so on) as the 
previously conducted superiority trials in which the active 
comparator clearly demonstrated clinically relevant efficacy, taking 
into account advances in medical or statistical practice relevant to 
the new trial.
    It is vital that the protocol of a trial designed to demonstrate 
equivalence or noninferiority contain a clear statement that this is 
its explicit intention. An equivalence margin should be specified in 
the protocol; this margin is the largest difference that can be 
judged as being clinically acceptable and should be smaller than 
differences observed in superiority trials of the active comparator. 
For the active control equivalence trial, both the upper and the 
lower equivalence margins are needed, while only the lower margin is 
needed for the active control noninferiority trial. The choice of 
equivalence margins should be justified clinically.
    Statistical analysis is generally based on the use of confidence 
intervals (see section 5.5). For equivalence trials, two-sided 
confidence intervals should be used. Equivalence is inferred when 
the entire confidence interval falls within the equivalence margins. 
Operationally, this is equivalent to the method of using two 
simultaneous one-sided tests to test the (composite) null hypothesis 
that the treatment difference is outside the equivalence margins 
versus the (composite) alternative hypothesis that the treatment 
difference is within the margins. Because the two null hypotheses 
are disjoint, the Type I error is appropriately controlled. For 
noninferiority trials, a one-sided interval should be used. The 
confidence interval approach has a one-sided hypothesis test 
counterpart for testing the null hypothesis that the treatment 
difference (investigational product minus control) is equal to the 
lower equivalence margin versus the alternative that the treatment 
difference is greater than the lower equivalence margin. The choice 
of Type I error should be a consideration separate from the use of a 
one-sided or two-sided procedure. Sample size calculations should be 
based on these methods (see section 3.5).
    Concluding equivalence or noninferiority based on observing a 
nonsignificant test result of the null hypothesis that there is no 
difference between the investigational product and the active 
comparator is considered inappropriate.
    There are also special issues in the choice of analysis sets. 
Subjects who withdraw or drop out of the treatment group or the 
comparator group will tend to have a lack of response; hence the 
results of using the full analysis set (see Glossary) may be biased 
toward demonstrating equivalence (see section 5.2.3).

3.3.3 Trials to Show Dose-Response Relationship

    How response is related to the dose of a new investigational 
product is a question to which answers may be obtained in all phases 
of development and by a variety of approaches (see ICH E4). Dose-
response trials may serve a number of objectives, among which the 
following are of particular importance: The confirmation of 
efficacy; the investigation of the shape and location of the dose-
response curve; the estimation of an appropriate starting dose; the 
identification of optimal strategies for individual dose 
adjustments; the determination of a maximal dose beyond which 
additional benefit would be unlikely to occur. These objectives 
should be addressed using the data collected at a number of doses 
under investigation, including a placebo (zero dose) wherever 
appropriate. For this purpose, the application of procedures to 
estimate the relationship between dose and response, including the 
construction of confidence intervals and the use of graphical 
methods, is as important as the use of statistical tests. The 
hypothesis tests that are used may need to be tailored to the 
natural ordering of doses or to particular questions regarding the 
shape of the dose-response curve (e.g., monotonicity). The details 
of the planned statistical procedures should be given in the 
protocol.

3.4 Group Sequential Designs

    Group sequential designs are used to facilitate the conduct of 
interim analysis (see section 4.5 and Glossary). While group 
sequential designs are not the only acceptable types of designs 
permitting interim analysis, they are the most commonly applied 
because it is more practicable to assess grouped subject outcomes at 
periodic intervals during the trial than on a continuous basis as 
data from each subject become available. The statistical methods 
should be fully specified in advance of the availability of 
information on treatment outcomes and subject treatment assignments 
(i.e., blind breaking, see section 4.5). An

[[Page 49591]]

independent data monitoring committee (IDMC) (see Glossary) may be 
used to review or to conduct the interim analysis of data arising 
from a group sequential design (see section 4.6). While the design 
has been most widely and successfully used in large, long-term 
trials of mortality or major nonfatal endpoints, its use is growing 
in other circumstances. In particular, it is recognized that safety 
must be monitored in all trials; therefore, the need for formal 
procedures to cover early stopping for safety reasons should always 
be considered.

3.5 Sample Size

    The number of subjects in a clinical trial should always be 
large enough to provide a reliable answer to the questions 
addressed. This number is usually determined by the primary 
objective of the trial. If the sample size is determined on some 
other basis, then this should be made clear and justified. For 
example, a trial sized on the basis of safety questions or 
requirements or important secondary objectives may need larger 
numbers of subjects than a trial sized on the basis of the primary 
efficacy question (see, for example, ICH E1A).
    Using the usual method for determining the appropriate sample 
size, the following items should be specified: A primary variable; 
the test statistic; the null hypothesis; the alternative 
(``working'') hypothesis at the chosen dose(s) (embodying 
consideration of the treatment difference to be detected or rejected 
at the dose and in the subject population selected); the probability 
of erroneously rejecting the null hypothesis (the Type I error) and 
the probability of erroneously failing to reject the null hypothesis 
(the Type II error); as well as the approach to dealing with 
treatment withdrawals and protocol violations. In some instances, 
the event rate is of primary interest for evaluating power, and 
assumptions should be made to extrapolate from the required number 
of events to the eventual sample size for the trial.
    The method by which the sample size is calculated should be 
given in the protocol, together with the estimates of any quantities 
used in the calculations (such as variances, mean values, response 
rates, event rates, difference to be detected). The basis of these 
estimates should also be given. It is important to investigate the 
sensitivity of the sample size estimate to a variety of deviations 
from these assumptions and this may be facilitated by providing a 
range of sample sizes appropriate for a reasonable range of 
deviations from assumptions. In confirmatory trials, assumptions 
should normally be based on published data or on the results of 
earlier trials. The treatment difference to be detected may be based 
on a judgment concerning the minimal effect which has clinical 
relevance in the management of patients or on a judgment concerning 
the anticipated effect of the new treatment, where this is larger. 
Conventionally, the probability of Type I error is set at 5 percent 
or less or as dictated by any adjustments made necessary for 
multiplicity considerations; the precise choice may be influenced by 
the prior plausibility of the hypothesis under test and the desired 
impact of the results. The probability of Type II error is 
conventionally set at 10 percent to 20 percent. It is in the 
sponsor's interest to keep this figure as low as feasible, 
especially in the case of trials that are difficult or impossible to 
repeat. Alternative values to the conventional levels of Type I and 
Type II error may be acceptable or even preferable in some cases.
    Sample size calculations should refer to the number of subjects 
required for the primary analysis. If this is the ``full analysis 
set,'' estimates of the effect size may need to be reduced compared 
to the per protocol set (see Glossary). This is to allow for the 
dilution of the treatment effect arising from the inclusion of data 
from patients who have withdrawn from treatment or whose compliance 
is poor. The assumptions about variability may also need to be 
revised.
    The sample size of an equivalence trial or a noninferiority 
trial (see section 3.3.2) should normally be based on the objective 
of obtaining a confidence interval for the treatment difference that 
shows that the treatments differ at most by a clinically acceptable 
difference. When the power of an equivalence trial is assessed at a 
true difference of zero, then the sample size necessary to achieve 
this power is underestimated if the true difference is not zero. 
When the power of a noninferiority trial is assessed at a zero 
difference, then the sample size needed to achieve that power will 
be underestimated if the effect of the investigational product is 
less than that of the active control. The choice of a ``clinically 
acceptable'' difference needs justification with respect to its 
meaning for future patients, and may be smaller than the 
``clinically relevant'' difference referred to above in the context 
of superiority trials designed to establish that a difference 
exists.
    The exact sample size in a group sequential trial cannot be 
fixed in advance because it depends upon the play of chance in 
combination with the chosen stopping guideline and the true 
treatment difference. The design of the stopping guideline should 
take into account the consequent distribution of the sample size, 
usually embodied in the expected and maximum sample sizes.
    When event rates are lower than anticipated or variability is 
larger than expected, methods for sample size reestimation are 
available without unblinding data or making treatment comparisons 
(see section 4.4).

3.6 Data Capture and Processing

    The collection of data and transfer of data from the 
investigator to the sponsor can take place through a variety of 
media, including paper case record forms, remote site monitoring 
systems, medical computer systems, and electronic transfer. Whatever 
data capture instrument is used, the form and content of the 
information collected should be in full accordance with the protocol 
and should be established in advance of the conduct of the clinical 
trial. It should focus on the data necessary to implement the 
planned analysis, including the context information (such as timing 
assessments relative to dosing) necessary to confirm protocol 
compliance or identify important protocol deviations. ``Missing 
values'' should be distinguishable from the ``value zero'' or 
``characteristic absent.''
    The process of data capture, through to database finalization, 
should be carried out in accordance with good clinical practice 
(GCP) (see ICH E6, section 5). Specifically, timely and reliable 
processes for recording data and rectifying errors and omissions are 
necessary to ensure delivery of a quality database and the 
achievement of the trial objectives through the implementation of 
the planned analysis.

IV. Trial Conduct Considerations

4.1 Trial Monitoring and Interim Analysis

    Careful conduct of a clinical trial according to the protocol 
has a major impact on the credibility of the results (see ICH E6). 
Careful monitoring can ensure that difficulties are noticed early 
and their occurrence or recurrence minimized.
    There are two distinct types of monitoring that generally 
characterize confirmatory clinical trials sponsored by the 
pharmaceutical industry. One type of monitoring concerns the 
oversight of the quality of the trial, while the other type involves 
breaking the blind to make treatment comparisons (i.e., interim 
analysis). Both types of trial monitoring, in addition to entailing 
different staff responsibilities, involve access to different types 
of trial data and information, and thus different principles apply 
for the control of potential statistical and operational bias.
    For the purpose of overseeing the quality of the trial, the 
checks involved in trial monitoring may include whether the protocol 
is being followed, the acceptability of data being accrued, the 
success of planned accrual targets, the appropriateness of the 
design assumptions, success in keeping patients in the trials, and 
so on (see sections 4.2 to 4.4). This type of monitoring does not 
require access to information on comparative treatment effects nor 
unblinding of data and, therefore, has no impact on Type I error. 
The monitoring of a trial for this purpose is the responsibility of 
the sponsor (see ICH E6) and can be carried out by the sponsor or an 
independent group selected by the sponsor. The period for this type 
of monitoring usually starts with the selection of the trial sites 
and ends with the collection and cleaning of the last subject's 
data.
    The other type of trial monitoring (interim analysis) involves 
the accruing of comparative treatment results. Interim analysis 
requires unblinded (i.e., key breaking) access to treatment group 
assignment (actual treatment assignment or identification of group 
assignment) and comparative treatment group summary information. 
Therefore, the protocol (or appropriate amendments prior to a first 
analysis) should contain statistical plans for the interim analysis 
to prevent certain types of bias. This is discussed in sections 4.5 
and 4.6.

4.2 Changes in Inclusion and Exclusion Criteria

    Inclusion and exclusion criteria should remain constant, as 
specified in the protocol, throughout the period of subject 
recruitment.

[[Page 49592]]

 Changes may occasionally be appropriate, for example, in long-term 
trials, where growing medical knowledge either from outside the 
trial or from interim analyses may suggest a change of entry 
criteria. Changes may also result from the discovery by monitoring 
staff that regular violations of the entry criteria are occurring or 
that seriously low recruitment rates are due to over-restrictive 
criteria. Changes should be made without breaking the blind and 
should always be described by a protocol amendment. This amendment 
should cover any statistical consequences, such as sample size 
adjustments arising from different event rates, or modifications to 
the planned analysis, such as stratifying the analysis according to 
modified inclusion/exclusion criteria.

4.3 Accrual Rates

    In trials with a long time-scale for the accrual of subjects, 
the rate of accrual should be monitored. If it falls appreciably 
below the projected level, the reasons should be identified and 
remedial actions taken to protect the power of the trial and 
alleviate concerns about selective entry and other aspects of 
quality. In a multicenter trial, these considerations apply to the 
individual centers.

4.4 Sample Size Adjustment

    In long-term trials there will usually be an opportunity to 
check the assumptions which underlie the original design and sample 
size calculations. This may be particularly important if the trial 
specifications have been made on preliminary and/or uncertain 
information. An interim check conducted on the blinded data may 
reveal that overall response variances, event rates or survival 
experience are not as anticipated. A revised sample size may then be 
calculated using suitably modified assumptions, and should be 
justified and documented in a protocol amendment and in the clinical 
study report. The steps taken to preserve blindness and the 
consequences, if any, for the Type I error and the width of 
confidence intervals should be explained. The potential need for re-
estimation of the sample size should be envisaged in the protocol 
whenever possible (see section 3.5).

4.5 Interim Analysis and Early Stopping

    An interim analysis is any analysis intended to compare 
treatment arms with respect to efficacy or safety at any time prior 
to formal completion of a trial. Because the number, methods, and 
consequences of these comparisons affect the interpretation of the 
trial, all interim analyses should be carefully planned in advance 
and described in the protocol. Special circumstances may dictate the 
need for an interim analysis that was not defined at the start of a 
trial. In these cases, a protocol amendment describing the interim 
analysis should be completed prior to unblinded access to treatment 
comparison data. When an interim analysis is planned with the 
intention of deciding whether or not to terminate a trial, this is 
usually accomplished by the use of a group sequential design that 
employs statistical monitoring schemes as guidelines (see section 
3.4). The goal of such an interim analysis is to stop the trial 
early if the superiority of the treatment under study is clearly 
established, if the demonstration of a relevant treatment difference 
has become unlikely, or if unacceptable adverse effects are 
apparent. Generally, boundaries for monitoring efficacy require more 
evidence to terminate a trial early (i.e., they are more 
conservative) than boundaries for monitoring safety. When the trial 
design and monitoring objective involve multiple endpoints, then 
this aspect of multiplicity may also need to be taken into account.
    The protocol should describe the schedule of interim analyses 
or, at least, the considerations that will govern its generation, 
for example, if flexible alpha spending function approaches are to 
be employed. Further details may be given in a protocol amendment 
before the time of the first interim analysis. The stopping 
guidelines and their properties should be clearly described in the 
protocol or amendments. The potential effects of early stopping on 
the analysis of other important variables should also be considered. 
This material should be written or approved by the data monitoring 
committee (see section 4.6), when the trial has one. Deviations from 
the planned procedure always bear the potential of invalidating the 
trial results. If it becomes necessary to make changes to the trial, 
any consequent changes to the statistical procedures should be 
specified in an amendment to the protocol at the earliest 
opportunity, especially discussing the impact on any analysis and 
inferences that such changes may cause. The procedures selected 
should always ensure that the overall probability of Type I error is 
controlled.
    The execution of an interim analysis should be a completely 
confidential process because unblinded data and results are 
potentially involved. All staff involved in the conduct of the trial 
should remain blind to the results of such analyses, because of the 
possibility that their attitudes to the trial will be modified and 
cause changes in the characteristics of patients to be recruited or 
biases in treatment comparisons. This principle may be applied to 
all investigator staff and to staff employed by the sponsor except 
for those who are directly involved in the execution of the interim 
analysis. Investigators should be informed only about the decision 
to continue or to discontinue the trial, or to implement 
modifications to trial procedures.
    Most clinical trials intended to support the efficacy and safety 
of an investigational product should proceed to full completion of 
planned sample size accrual; trials should be stopped early only for 
ethical reasons or if the power is no longer acceptable. However, it 
is recognized that drug development plans involve the need for 
sponsor access to comparative treatment data for a variety of 
reasons, such as planning other trials. It is also recognized that 
only a subset of trials will involve the study of serious life-
threatening outcomes or mortality which may need sequential 
monitoring of accruing comparative treatment effects for ethical 
reasons. In either of these situations, plans for interim 
statistical analysis should be in place in the protocol or in 
protocol amendments prior to the unblinded access to comparative 
treatment data in order to deal with the potential statistical and 
operational bias that may be introduced.
    For many clinical trials of investigational products, especially 
those that have major public health significance, the responsibility 
for monitoring comparisons of efficacy and/or safety outcomes should 
be assigned to an external independent group, often called an 
independent data monitoring committee (IDMC), a data and safety 
monitoring board, or a data monitoring committee, whose 
responsibilities should be clearly described.
    When a sponsor assumes the role of monitoring efficacy or safety 
comparisons and therefore has access to unblinded comparative 
information, particular care should be taken to protect the 
integrity of the trial and to manage and limit appropriately the 
sharing of information. The sponsor should ensure and document that 
the internal monitoring committee has complied with written standard 
operating procedures and that minutes of decisionmaking meetings, 
including records of interim results, are maintained.
    Any interim analysis that is not planned appropriately (with or 
without the consequences of stopping the trial early) may flaw the 
results of a trial and possibly weaken confidence in the conclusions 
drawn. Therefore, such analyses should be avoided. If unplanned 
interim analysis is conducted, the clinical study report should 
explain why it was necessary and the degree to which blindness had 
to be broken, and provide an assessment of the potential magnitude 
of bias introduced and the impact on the interpretation of the 
results.

4.6 Role of Independent Data Monitoring Committee (IDMC)(see 
sections 1.25 and 5.5.2 of ICH E6)

    An IDMC may be established by the sponsor to assess at intervals 
the progress of a clinical trial, safety data, and critical efficacy 
variables and recommend to the sponsor whether to continue, modify 
or terminate a trial. The IDMC should have written operating 
procedures and maintain records of all its meetings, including 
interim results; these should be available for review when the trial 
is complete. The independence of the IDMC is intended to control the 
sharing of important comparative information and to protect the 
integrity of the clinical trial from adverse impact resulting from 
access to trial information. The IDMC is a separate entity from an 
institutional review board (IRB) or an independent ethics committee 
(IEC), and its composition should include clinical trial scientists 
knowledgeable in the appropriate disciplines, including statistics.
    When there are sponsor representatives on the IDMC, their role 
should be clearly defined in the operating procedures of the 
committee (for example, covering whether or not they can vote on key 
issues). Since these sponsor staff would have access to unblinded 
information, the procedures should also address the control of 
dissemination of interim trial results within the sponsor 
organization.

[[Page 49593]]

V. Data Analysis Considerations

5.1 Prespecification of the Analysis

    When designing a clinical trial, the principal features of the 
eventual statistical analysis of the data should be described in the 
statistical section of the protocol. This section should include all 
the principal features of the proposed confirmatory analysis of the 
primary variable(s) and the way in which anticipated analysis 
problems will be handled. In the case of exploratory trials, this 
section could describe more general principles and directions.
    The statistical analysis plan (see Glossary) may be written as a 
separate document to be completed after finalizing the protocol. In 
this document, a more technical and detailed elaboration of the 
principal features stated in the protocol may be included (see 
section 7.1). The plan may include detailed procedures for executing 
the statistical analysis of the primary and secondary variables and 
other data. The plan should be reviewed and possibly updated as a 
result of the blind review of the data (see section 7.1 for 
definition) and should be finalized before breaking the blind. 
Formal records should be kept of when the statistical analysis plan 
was finalized as well as when the blind was subsequently broken.
    If the blind review suggests changes to the principal features 
stated in the protocol, these should be documented in a protocol 
amendment. Otherwise, it should suffice to update the statistical 
analysis plan with the considerations suggested from the blind 
review. Only results from analyses envisaged in the protocol 
(including amendments) can be regarded as confirmatory.
    In the statistical section of the clinical study report, the 
statistical methodology should be clearly described including when 
in the clinical trial process methodology decisions were made (see 
ICH E3).

5.2 Analysis Sets

    The set of subjects whose data are to be included in the main 
analyses should be defined in the statistical section of the 
protocol. In addition, documentation for all subjects for whom trial 
procedures (e.g., run-in period) were initiated may be useful. The 
content of this subject documentation depends on detailed features 
of the particular trial, but at least demographic and baseline data 
on disease status should be collected whenever possible.
    If all subjects randomized into a clinical trial satisfied all 
entry criteria, followed all trial procedures perfectly with no 
losses to followup, and provided complete data records, then the set 
of subjects to be included in the analysis would be self-evident. 
The design and conduct of a trial should aim to approach this ideal 
as closely as possible, but, in practice, it is doubtful if it can 
ever be fully achieved. Hence, the statistical section of the 
protocol should address anticipated problems prospectively in terms 
of how these affect the subjects and data to be analyzed. The 
protocol should also specify procedures aimed at minimizing any 
anticipated irregularities in study conduct that might impair a 
satisfactory analysis, including various types of protocol 
violations, withdrawals and missing values. The protocol should 
consider ways both to reduce the frequency of such problems and to 
handle the problems that do occur in the analysis of data. Possible 
amendments to the way in which the analysis will deal with protocol 
violations should be identified during the blind review. It is 
desirable to identify any important protocol violation with respect 
to the time when it occurred, its cause, and its influence on the 
trial result. The frequency and type of protocol violations, missing 
values, and other problems should be documented in the clinical 
study report and their potential influence on the trial results 
should be described (see ICH E3).
    Decisions concerning the analysis set should be guided by the 
following principles: (1) To minimize bias and (2) to avoid 
inflation of Type I error.

5.2.1 Full Analysis Set

    The intention-to-treat (see Glossary) principle implies that the 
primary analysis should include all randomized subjects. Compliance 
with this principle would necessitate complete followup of all 
randomized subjects for study outcomes. In practice, this ideal may 
be difficult to achieve, for reasons to be described. In this 
document, the term ``full analysis set'' is used to describe the 
analysis set which is as complete as possible and as close as 
possible to the intention-to-treat ideal of including all randomized 
subjects. Preservation of the initial randomization in analysis is 
important in preventing bias and in providing a secure foundation 
for statistical tests. In many clinical trials, the use of the full 
analysis set provides a conservative strategy. Under many 
circumstances, it may also provide estimates of treatment effects 
that are more likely to mirror those observed in subsequent 
practice.
    There are a limited number of circumstances that might lead to 
excluding randomized subjects from the full analysis set, including 
the failure to satisfy major entry criteria (eligibility 
violations), the failure to take at least one dose of trial 
medication, and the lack of any data post randomization. Such 
exclusions should always be justified. Subjects who fail to satisfy 
an entry criterion may be excluded from the analysis without the 
possibility of introducing bias only under the following 
circumstances:
    (i) The entry criterion was measured prior to randomization.
    (ii) The detection of the relevant eligibility violations can be 
made completely objectively.
    (iii) All subjects receive equal scrutiny for eligibility 
violations. (This may be difficult to ensure in an open-label study, 
or even in a double-blind study if the data are unblinded prior to 
this scrutiny, emphasizing the importance of the blind review.)
    (iv) All detected violations of the particular entry criterion 
are excluded.
    In some situations, it may be reasonable to eliminate from the 
set of all randomized subjects any subject who took no trial 
medication. The intention-to-treat principle would be preserved 
despite the exclusion of these patients provided, for example, that 
the decision of whether or not to begin treatment could not be 
influenced by knowledge of the assigned treatment. In other 
situations it may be necessary to eliminate from the set of all 
randomized subjects any subject without data post randomization. No 
analysis should be considered complete unless the potential biases 
arising from these specific exclusions, or any others, are 
addressed.
    When the full analysis set of subjects is used, violations of 
the protocol that occur after randomization may have an impact on 
the data and conclusions, particularly if their occurrence is 
related to treatment assignment. In most respects, it is appropriate 
to include the data from such subjects in the analysis, consistent 
with the intention-to-treat principle. Special problems arise in 
connection with subjects withdrawn from treatment after receiving 
one or more doses who provide no data after this point, and subjects 
otherwise lost to followup, because failure to include these 
subjects in the full analysis set may seriously undermine the 
approach. Measurements of primary variables made at the time of the 
loss to follow-up of a subject for any reason, or subsequently 
collected in accordance with the intended schedule of assessments in 
the protocol, are valuable in this context; subsequent collection is 
especially important in studies where the primary variable is 
mortality or serious morbidity. The intention to collect data in 
this way should be described in the protocol. Imputation techniques, 
ranging from the carrying forward of the last observation to the use 
of complex mathematical models, may also be used in an attempt to 
compensate for missing data. Other methods employed to ensure the 
availability of measurements of primary variables for every subject 
in the full analysis set may require some assumptions about the 
subjects' outcomes or a simpler choice of outcome (e.g., success/
failure). The use of any of these strategies should be described and 
justified in the statistical section of the protocol, and the 
assumptions underlying any mathematical models employed should be 
clearly explained. It is also important to demonstrate the 
robustness of the corresponding results of analysis, especially when 
the strategy in question could itself lead to biased estimates of 
treatment effects.
    Because of the unpredictability of some problems, it may 
sometimes be preferable to defer detailed consideration of the 
manner of dealing with irregularities until the blind review of the 
data at the end of the trial, and, if so, this should be stated in 
the protocol.

5.2.2 Per Protocol Set

    The ``per protocol'' set of subjects, sometimes described as the 
``valid cases,'' the ``efficacy'' sample, or the ``evaluable 
subjects'' sample, defines a subset of the subjects in the full 
analysis set who are more compliant with the protocol and is 
characterized by criteria such as the following:
    (i) The completion of a certain prespecified minimal exposure to 
the treatment regimen;
    (ii) The availability of measurements of the primary 
variable(s);
    (iii) The absence of any major protocol violations, including 
the violation of entry criteria.

[[Page 49594]]

    The precise reasons for excluding subjects from the per protocol 
set should be fully defined and documented before breaking the blind 
in a manner appropriate to the circumstances of the specific trial.
    The use of the per protocol set may maximize the opportunity for 
a new treatment to show additional efficacy in the analysis, and 
most closely reflects the scientific model underlying the protocol. 
However, the corresponding test of the hypothesis and estimate of 
the treatment effect may or may not be conservative, depending on 
the trial. The bias, which may be severe, arises from the fact that 
adherence to the study protocol may be related to treatment and 
outcome.
    The problems that lead to the exclusion of subjects to create 
the per protocol set, and other protocol violations, should be fully 
identified and summarized. Relevant protocol violations may include 
errors in treatment assignment, the use of excluded medication, poor 
compliance, loss to followup, and missing data. It is good practice 
to assess the pattern of such problems among the treatment groups 
with respect to frequency and time to occurrence.

5.2.3 Roles of the Different Analysis Sets

    In general, it is advantageous to demonstrate a lack of 
sensitivity of the principal trial results to alternative choices of 
the set of subjects analyzed. In confirmatory trials, it is usually 
appropriate to plan to conduct both an analysis of the full analysis 
set and a per protocol analysis, so that any differences between 
them can be the subject of explicit discussion and interpretation. 
In some cases, it may be desirable to plan further exploration of 
the sensitivity of conclusions to the choice of the set of subjects 
analyzed. When the full analysis set and the per protocol set lead 
to essentially the same conclusions, confidence in the trial results 
is increased, bearing in mind, however, that the need to exclude a 
substantial proportion of subjects from the per protocol analysis 
throws some doubt on the overall validity of the trial.
    The full analysis set and the per protocol set play different 
roles in superiority trials (which seek to show the investigational 
product to be superior) and in equivalence or noninferiority trials 
(which seek to show the investigational product to be comparable, 
see section 3.3.2). In superiority trials, the full analysis set is 
used in the primary analysis (apart from exceptional circumstances) 
because it tends to avoid over-optimistic estimates of efficacy 
resulting from a per protocol analysis. This is because the 
noncompliers included in the full analysis set will generally 
diminish the estimated treatment effect. However, in an equivalence 
or noninferiority trial, use of the full analysis set is generally 
not conservative and its role should be considered very carefully.

5.3 Missing Values and Outliers

    Missing values represent a potential source of bias in a 
clinical trial. Hence, every effort should be undertaken to fulfill 
all the requirements of the protocol concerning the collection and 
management of data. In reality, however, there will almost always be 
some missing data. A trial may be regarded as valid, nonetheless, 
provided the methods of dealing with missing values are sensible, 
particularly if those methods are predefined in the protocol. 
Definition of methods may be refined by updating this aspect in the 
statistical analysis plan during the blind review. Unfortunately, no 
universally applicable methods of handling missing values can be 
recommended. An investigation should be made concerning the 
sensitivity of the results of analysis to the method of handling 
missing values, especially if the number of missing values is 
substantial.
    A similar approach should be adopted to exploring the influence 
of outliers, the statistical definition of which is, to some extent, 
arbitrary. Clear identification of a particular value as an outlier 
is most convincing when justified medically as well as 
statistically, and the medical context will then often define the 
appropriate action. Any outlier procedure set out in the protocol or 
the statistical analysis plan should be such as not to favor any 
treatment group a priori. Once again, this aspect of the analysis 
can be usefully updated during blind review. If no procedure for 
dealing with outliers was foreseen in the trial protocol, one 
analysis with the actual values and at least one other analysis 
eliminating or reducing the outlier effect should be performed and 
differences between their results discussed.

5.4 Data Transformation

    The decision to transform key variables prior to analysis is 
best made during the design of the trial on the basis of similar 
data from earlier clinical trials. Transformations (e.g., square 
root, logarithm) should be specified in the protocol and a rationale 
provided, especially for the primary variable(s). The general 
principles guiding the use of transformations to ensure that the 
assumptions underlying the statistical methods are met are to be 
found in standard texts; conventions for particular variables have 
been developed in a number of specific clinical areas. The decision 
on whether and how to transform a variable should be influenced by 
the preference for a scale that facilitates clinical interpretation.
    Similar considerations apply to other derived variables, such as 
the use of change from baseline, percentage change from baseline, 
the ``area under the curve'' of repeated measures, or the ratio of 
two different variables. Subsequent clinical interpretation should 
be carefully considered, and the derivation should be justified in 
the protocol. Closely related points are made in section 2.2.2.

5.5 Estimation, Confidence Intervals, and Hypothesis Testing

    The statistical section of the protocol should specify the 
hypotheses that are to be tested and/or the treatment effects that 
are to be estimated in order to satisfy the primary objectives of 
the trial. The statistical methods to be used to accomplish these 
tasks should be described for the primary (and preferably the 
secondary) variables, and the underlying statistical model should be 
made clear. Estimates of treatment effects should be accompanied by 
confidence intervals, whenever possible, and the way in which these 
will be calculated should be identified. A description should be 
given of any intentions to use baseline data to improve precision or 
to adjust estimates for potential baseline differences, for example, 
by means of analysis of covariance.
    It is important to clarify whether one- or two-sided tests of 
statistical significance will be used and, in particular, to justify 
prospectively the use of one-sided tests. If hypothesis tests are 
not considered appropriate, then the alternative process for 
arriving at statistical conclusions should be given. The issue of 
one-sided or two-sided approaches to inference is controversial, and 
a diversity of views can be found in the statistical literature. The 
approach of setting Type I errors for one-sided tests at half the 
conventional Type I error used in two-sided tests is preferable in 
regulatory settings. This promotes consistency with the two-sided 
confidence intervals that are generally appropriate for estimating 
the possible size of the difference between two treatments.
    The particular statistical model chosen should reflect the 
current state of medical and statistical knowledge about the 
variables to be analyzed as well as the statistical design of the 
trial. All effects to be fitted in the analysis (for example, in 
analysis of variance models) should be fully specified, and the 
manner, if any, in which this set of effects might be modified in 
response to preliminary results should be explained. The same 
considerations apply to the set of covariates fitted in an analysis 
of covariance. (See also section 5.7.) In the choice of statistical 
methods, due attention should be paid to the statistical 
distribution of both primary and secondary variables. When making 
this choice (for example between parametric and nonparametric 
methods), it is important to bear in mind the need to provide 
statistical estimates of the size of treatment effects together with 
confidence intervals (in addition to significance tests).
    The primary analysis of the primary variable should be clearly 
distinguished from supporting analyses of the primary or secondary 
variables. Within the statistical section of the protocol or the 
statistical analysis plan there should also be an outline of the way 
in which data other than the primary and secondary variables will be 
summarized and reported. This should include a reference to any 
approaches adopted for the purpose of achieving consistency of 
analysis across a range of trials, for example, for safety data.
    Modeling approaches that incorporate information on known 
pharmacological parameters, the extent of protocol compliance for 
individual subjects, or other biologically based data may provide 
valuable insights into actual or potential efficacy, especially with 
regard to estimation of treatment effects. The assumptions 
underlying such models should always be clearly identified, and the 
limitations of any conclusions should be carefully described.

5.6 Adjustment of Significance and Confidence Levels

    When multiplicity is present, the usual frequentist approach to 
the analysis of

[[Page 49595]]

clinical trial data may necessitate an adjustment to the Type I 
error. Multiplicity may arise, for example, from multiple primary 
variables (see section 2.2.2), multiple comparisons of treatments, 
repeated evaluation over time, and/or interim analyses (see section 
4.5). Methods to avoid or reduce multiplicity are sometimes 
preferable when available, such as the identification of the key 
primary variable (multiple variables), the choice of a critical 
treatment contrast (multiple comparisons), and the use of a summary 
measure such as ``area under the curve'' (repeated measures). In 
confirmatory analyses, any aspects of multiplicity that remain after 
steps of this kind have been taken should be identified in the 
protocol; adjustment should always be considered and the details of 
any adjustment procedure or an explanation of why adjustment is not 
thought to be necessary should be set out in the analysis plan.

5.7 Subgroups, Interactions, and Covariates

    The primary variable(s) is often systematically related to other 
influences apart from treatment. For example, there may be 
relationships to covariates such as age and sex, or there may be 
differences between specific subgroups of subjects, such as those 
treated at the different centers of a multicenter trial. In some 
instances, an adjustment for the influence of covariates or for 
subgroup effects is an integral part of the planned analysis and 
hence should be set out in the protocol. Pretrial deliberations 
should identify those covariates and factors expected to have an 
important influence on the primary variable(s), and should consider 
how to account for these in the analysis to improve precision and to 
compensate for any lack of balance between treatment groups. If one 
or more factors are used to stratify the design, it is appropriate 
to account for those factors in the analysis. When the potential 
value of an adjustment is in doubt, it is often advisable to 
nominate the unadjusted analysis as the one for primary attention, 
the adjusted analysis being supportive. Special attention should be 
paid to center effects and to the role of baseline measurements of 
the primary variable. It is not advisable to adjust the main 
analyses for covariates measured after randomization because they 
may be affected by the treatments.
    The treatment effect itself may also vary with subgroup or 
covariate--for example, the effect may decrease with age or may be 
larger in a particular diagnostic category of subjects. In some 
cases such interactions are anticipated or are of particular prior 
interest (e.g., geriatrics); hence a subgroup analysis or a 
statistical model including interactions is part of the planned 
confirmatory analysis. In most cases, however, subgroup or 
interaction analyses are exploratory and should be clearly 
identified as such; they should explore the uniformity of any 
treatment effects found overall. In general, such analyses should 
proceed first through the addition of interaction terms to the 
statistical model in question, complemented by additional 
exploratory analysis within relevant subgroups of subjects, or 
within strata defined by the covariates. When exploratory, these 
analyses should be interpreted cautiously. Any conclusion of 
treatment efficacy (or lack thereof) or safety based solely on 
exploratory subgroup analyses is unlikely to be accepted.

5.8 Integrity of Data and Computer Software Validity

    The credibility of the numerical results of the analysis depends 
on the quality and validity of the methods and software (both 
internally and externally written) used both for data management 
(data entry, storage, verification, correction, and retrieval) and 
for processing the data statistically. Data management activities 
should therefore be based on thorough and effective standard 
operating procedures. The computer software used for data management 
and statistical analysis should be reliable, and documentation of 
appropriate software testing procedures should be available.

VI. Evaluation of Safety and Tolerability

6.1 Scope of Evaluation

    In all clinical trials, evaluation of safety and tolerability 
(see Glossary) constitutes an important element. In early phases 
this evaluation is mostly of an exploratory nature and is only 
sensitive to frank expressions of toxicity, whereas in later phases 
the establishment of the safety and tolerability profile of a drug 
can be characterized more fully in larger samples of subjects. Later 
phase controlled trials represent an important means of exploring, 
in an unbiased manner, any new potential adverse effects, even if 
such trials generally lack power in this respect.
    Certain trials may be designed with the purpose of making 
specific claims about superiority or equivalence with regard to 
safety and tolerability compared to another drug or to another dose 
of the investigational drug. Such specific claims should be 
supported by relevant evidence from confirmatory trials, similar to 
that necessary for corresponding efficacy claims.

6.2 Choice of Variables and Data Collection

    In any clinical trial, the methods and measurements chosen to 
evaluate the safety and tolerability of a drug will depend on a 
number of factors, including knowledge of the adverse effects of 
closely related drugs, information from nonclinical and earlier 
clinical trials and possible consequences of the pharmacodynamic/
pharmacokinetic properties of the particular drug, the mode of 
administration, the type of subjects to be studied, and the duration 
of the trial. Laboratory tests concerning clinical chemistry and 
hematology, vital signs, and clinical adverse events (diseases, 
signs, and symptoms) usually form the main body of the safety and 
tolerability data. The occurrence of serious adverse events and 
treatment discontinuations due to adverse events are particularly 
important to register (see ICH E2A and ICH E3).
    Furthermore, it is recommended that a consistent methodology be 
used for the data collection and evaluation throughout a clinical 
trial program to facilitate the combining of data from different 
trials. The use of a common adverse event dictionary is particularly 
important. This dictionary has a structure that makes it possible to 
summarize the adverse event data on three different levels: System-
organ class, preferred term, or included term (see Glossary). The 
preferred term is the level on which adverse events usually are 
summarized, and preferred terms belonging to the same system-organ 
class could then be brought together in the descriptive presentation 
of data (see ICH M1).

6.3 Set of Subjects to be Evaluated and Presentation of Data

    For the overall safety and tolerability assessment, the set of 
subjects to be summarized is usually defined as those subjects who 
received at least one dose of the investigational drug. Safety and 
tolerability variables should be collected as comprehensively as 
possible from these subjects, including type of adverse event, 
severity, onset, and duration (see ICH E2B). Additional safety and 
tolerability evaluations may be needed in specific subpopulations, 
such as females, the elderly (see ICH E7), the severely ill, or 
those who have a common concomitant treatment. These evaluations may 
need to address more specific issues (see ICH E3).
    All safety and tolerability variables will need attention during 
evaluation, and the broad approach should be indicated in the 
protocol. All adverse events should be reported, whether or not they 
are considered to be related to treatment. All available data in the 
study population should be accounted for in the evaluation. 
Definitions of measurement units and reference ranges of laboratory 
variables should be made with care; if different units or different 
reference ranges appear in the same trial (e.g., if more than one 
laboratory is involved), then measurements should be appropriately 
standardized to allow a unified evaluation. Use of a toxicity 
grading scale should be prespecified and justified.
    The incidence of a certain adverse event is usually expressed in 
the form of a proportion relating number of subjects experiencing 
events to number of subjects at risk. However, it is not always 
self-evident how to assess incidence. For example, depending on the 
situation, the number of exposed subjects or the extent of exposure 
(in person-years) could be considered for the denominator. Whether 
the purpose of the calculation is to estimate a risk or to make a 
comparison between treatment groups, it is important that the 
definition is given in the protocol. This is especially important if 
long-term treatment is planned and a substantial proportion of 
treatment withdrawals or deaths are expected. For such situations, 
survival analysis methods should be considered and cumulative 
adverse event rates calculated in order to avoid the risk of 
underestimation.
    In situations when there is a substantial background noise of 
signs and symptoms (e.g., in psychiatric trials), one should 
consider ways for accounting for this in the estimation of risk for 
different adverse events. One such method is to make use of the 
``treatment emergent'' (see Glossary) concept in which adverse 
events are recorded only if they emerge or worsen relative to 
pretreatment baseline.

[[Page 49596]]

    Other methods to reduce the effect of the background noise may 
also be appropriate, such as ignoring adverse events of mild 
severity or requiring that an event should have been observed at 
repeated visits to qualify for inclusion in the numerator. Such 
methods should be explained and justified in the protocol.

6.4 Statistical Evaluation

    The investigation of safety and tolerability is a 
multidimensional problem. Although some specific adverse effects can 
usually be anticipated and specifically monitored for any drug, the 
range of possible adverse effects is very large, and new and 
unforeseeable effects are always possible. Further, an adverse event 
experienced after a protocol violation, such as use of an excluded 
medication, may introduce a bias. This background underlies the 
statistical difficulties associated with the analytical evaluation 
of safety and tolerability of drugs, and means that conclusive 
information from confirmatory clinical trials is the exception 
rather than the rule.
    In most trials, the safety and tolerability implications are 
best addressed by applying descriptive statistical methods to the 
data, supplemented by calculation of confidence intervals wherever 
this aids interpretation. It is also valuable to make use of 
graphical presentations in which patterns of adverse events are 
displayed both within treatment groups and within subjects.
    The calculation of p-values is sometimes useful, either as an 
aid to evaluating a specific difference of interest or as a 
``flagging'' device applied to a large number of safety and 
tolerability variables to highlight differences worthy of further 
attention. This is particularly useful for laboratory data, which 
otherwise can be difficult to summarize appropriately. It is 
recommended that laboratory data be subjected to both a quantitative 
analysis, e.g., evaluation of treatment means, and a qualitative 
analysis where counting of numbers above or below certain thresholds 
are calculated.
    If hypothesis tests are used, statistical adjustments for 
multiplicity to quantify the Type I error are appropriate, but the 
Type II error is usually of more concern. Care should be taken when 
interpreting putative statistically significant findings when there 
is no multiplicity adjustment.
    In the majority of trials, investigators are seeking to 
establish that there are no clinically unacceptable differences in 
safety and tolerability compared with either a comparator drug or a 
placebo. As is the case for noninferiority or equivalence evaluation 
of efficacy, the use of confidence intervals is preferred to 
hypothesis testing in this situation. In this way, the considerable 
imprecision often arising from low frequencies of occurrence is 
clearly demonstrated.

6.5 Integrated Summary

    The safety and tolerability properties of a drug are commonly 
summarized across trials continuously during an investigational 
product's development and, in particular, at the time of a marketing 
application. The usefulness of this summary, however, is dependent 
on adequate and well-controlled individual trials with high data 
quality.
    The overall usefulness of a drug is always a question of balance 
between risk and benefit. In a single trial, such a perspective 
could also be considered even if the assessment of risk/benefit 
usually is performed in the summary of the entire clinical trial 
program. (See section 7.2.2)
    For more details on the reporting of safety and tolerability, 
see section 12 of ICH E3.

VII. Reporting

7.1 Evaluation and Reporting

    As stated in the introduction, the structure and content of 
clinical study reports is the subject of ICH E3. That ICH guidance 
fully covers the reporting of statistical work, appropriately 
integrated with clinical and other material. The current section is 
therefore relatively brief.
    During the planning phase of a trial, the principal features of 
the analysis should have been specified in the protocol as described 
in section 5. When the conduct of the trial is over and the data are 
assembled and available for preliminary inspection, it is valuable 
to carry out the blind review of the planned analysis also described 
in section 5. This pre-analysis review, blinded to treatment, should 
cover, for example, decisions concerning the exclusion of subjects 
or data from the analysis sets, the checking of possible 
transformations and definitions of outliers, the addition to the 
model of important covariates identified in other recent research, 
and the reconsideration of the use of parametric or nonparametric 
methods. Decisions made at this time should be described in the 
report and should be distinguished from those made after the 
statistician has had access to the treatment codes, as blind 
decisions will generally introduce less potential for bias. 
Statisticians or other staff involved in unblinded interim analysis 
should not participate in the blind review or in making 
modifications to the statistical analysis plan. When the blinding is 
compromised by the possibility that treatment-induced effects may be 
apparent in the data, special care will be needed for the blind 
review.
    Many of the more detailed aspects of presentation and tabulation 
should be finalized at or about the time of the blind review so 
that, by the time of the actual analysis, full plans exist for all 
its aspects including subject selection, data selection and 
modification, data summary and tabulation, estimation, and 
hypothesis testing. Once data validation is complete, the analysis 
should proceed according to the predefined plans; the more these 
plans are adhered to, the greater the credibility of the results. 
Particular attention should be paid to any differences between the 
planned analysis and the actual analysis as described in the 
protocol, the protocol amendments, or the updated statistical 
analysis plan based on a blind review of data. A careful explanation 
should be provided for deviations from the planned analysis.
    All subjects who entered the trial should be accounted for in 
the report, whether or not they are included in the analysis. All 
reasons for exclusion from analysis should be documented; for any 
subject included in the full analysis set but not in the per 
protocol set, the reasons for exclusion from the latter should also 
be documented. Similarly, for all subjects included in an analysis 
set, the measurements of all important variables should be accounted 
for at all relevant time-points.
    The effect of all losses of subjects or data, withdrawals from 
treatment, and major protocol violations on the main analyses of the 
primary variable(s) should be considered carefully. Subjects lost to 
followup, withdrawn from treatment, or with a severe protocol 
violation should be identified and a descriptive analysis of them 
provided, including the reasons for their loss and its relationship 
to treatment and outcome.
    Descriptive statistics form an indispensable part of reports. 
Suitable tables and/or graphical presentations should illustrate 
clearly the important features of the primary and secondary 
variables and of key prognostic and demographic variables. The 
results of the main analyses relating to the objectives of the trial 
should be the subject of particularly careful descriptive 
presentation. When reporting the results of significance tests, 
precise p-values (e.g., ``p=0.034'') should be reported rather than 
making exclusive reference to critical values.
    Although the primary goal of the analysis of a clinical trial 
should be to answer the questions posed by its main objectives, new 
questions based on the observed data may well emerge during the 
unblinded analysis. Additional and perhaps complex statistical 
analysis may be the consequence. This additional work should be 
strictly distinguished in the report from work which was planned in 
the protocol.
    The play of chance may lead to unforeseen imbalances between the 
treatment groups in terms of baseline measurements not predefined as 
covariates in the planned analysis but having some prognostic 
importance nevertheless. This is best dealt with by showing that an 
additional analysis which accounts for these imbalances reaches 
essentially the same conclusions as the planned analysis. If this is 
not the case, the effect of the imbalances on the conclusions should 
be discussed.
     In general, sparing use should be made of unplanned analyses. 
Such analyses are often carried out when it is thought that the 
treatment effect may vary according to some other factor or factors. 
An attempt may then be made to identify subgroups of subjects for 
whom the effect is particularly beneficial. The potential dangers of 
over-interpretation of unplanned subgroup analyses are well known 
(see also section 5.7) and should be carefully avoided. Although 
similar problems of interpretation arise if a treatment appears to 
have no benefit or an adverse effect in a subgroup of subjects, such 
possibilities should be properly assessed and should therefore be 
reported.
    Finally, statistical judgement should be brought to bear on the 
analysis, interpretation and presentation of the results of a 
clinical trial. To this end, the trial statistician should be a 
member of the team responsible for the clinical study report and 
should approve the clinical report.

[[Page 49597]]

7.2 Summarizing the Clinical Database

    An overall summary and synthesis of the evidence on safety and 
efficacy from all the reported clinical trials is required for a 
marketing application (expert report in EU, integrated summary 
reports in the United States, gaiyou in Japan). This may be 
accompanied, when appropriate, by a statistical combination of 
results.
    Within the summary a number of areas of specific statistical 
interest arise: Describing the demography and clinical features of 
the population treated during the course of the clinical trial 
program; addressing the key questions of efficacy by considering the 
results of the relevant (usually controlled) trials and highlighting 
the degree to which they reinforce or contradict each other; 
summarizing the safety information available from the combined 
database of all the trials whose results contribute to the marketing 
application; and identifying potential safety issues. During the 
design of a clinical program, careful attention should be paid to 
the uniform definition and collection of measurements which will 
facilitate subsequent interpretation of the series of trials, 
particularly if they are likely to be combined across trials. A 
common dictionary for recording the details of medication, medical 
history and adverse events should be selected and used. A common 
definition of the primary and secondary variables is nearly always 
worthwhile and is essential for meta-analysis. The manner of 
measuring key efficacy variables, the timing of assessments relative 
to randomization/entry, the handling of protocol violators and 
deviators, and perhaps the definition of prognostic factors should 
all be kept compatible unless there are valid reasons not to do so.
    Any statistical procedures used to combine data across trials 
should be described in detail. Attention should be paid to the 
possibility of bias associated with the selection of trials, to the 
homogeneity of their results, and to the proper modeling of the 
various sources of variation. The sensitivity of conclusions to the 
assumptions and selections made should be explored.

7.2.1 Efficacy Data

    Individual clinical trials should always be large enough to 
satisfy their objectives. Additional valuable information may also 
be gained by summarizing a series of clinical trials that address 
essentially identical key efficacy questions. The main results of 
such a set of trials should be presented in an identical form to 
permit comparison, usually in tables or graphs that focus on 
estimates plus confidence limits. The use of meta-analytic 
techniques to combine these estimates is often a useful addition 
because it allows a more precise overall estimate of the size of the 
treatment effects to be generated and provides a complete and 
concise summary of the results of the trials. Under exceptional 
circumstances, a meta-analytic approach may also be the most 
appropriate way, or the only way, of providing sufficient overall 
evidence of efficacy via an overall hypothesis test. When used for 
this purpose, the meta-analysis should have its own prospectively 
written protocol.

7.2.2 Safety Data

    In summarizing safety data, it is important to examine the 
safety database thoroughly for any indications of potential toxicity 
and to follow up any indications by looking for an associated 
supportive pattern of observations. The combination of the safety 
data from all human exposure to the drug provides an important 
source of information because its larger sample size provides the 
best chance of detecting the rarer adverse events and, perhaps, of 
estimating their approximate incidence. However, incidence data from 
this database are difficult to evaluate because of the lack of a 
comparator group, and data from comparative trials are especially 
valuable in overcoming this difficulty. The results from trials 
which use a common comparator (placebo or specific active 
comparator) should be combined and presented separately for each 
comparator providing sufficient data.
    All indications of potential toxicity arising from exploration 
of the data should be reported. The evaluation of the reality of 
these potential adverse effects should take into account the issue 
of multiplicity arising from the numerous comparisons made. The 
evaluation should also make appropriate use of survival analysis 
methods to exploit the potential relationship of the incidence of 
adverse events to duration of exposure and/or followup. The risks 
associated with identified adverse effects should be appropriately 
quantified to allow a proper assessment of the risk/benefit 
relationship.
Annex 1 Glossary
    Bayesian approaches--Approaches to data analysis that provide a 
posterior probability distribution for some parameter (e.g., 
treatment effect), derived from the observed data and a prior 
probability distribution for the parameter. The posterior 
distribution is then used as the basis for statistical inference.
    Bias (statistical and operational)--The systematic tendency of 
any factorsassociated with the design, conduct, analysis and 
evaluation of the results of a clinical trial to make the estimate 
of a treatment effect deviate from its true value. Bias introduced 
through deviations in conduct is referred to as ``operational'' 
bias. The other sources of bias listed above are referred to as 
``statistical.''
    Blind review--The checking and assessment of data during the 
period of time between trial completion (the last observation on the 
last subject) and the breaking of the blind, for the purpose of 
finalizing the planned analysis.
    Content validity--The extent to which a variable (e.g., a rating 
scale) measures what it is supposed to measure.
    Double dummy--A technique for retaining the blind when 
administering supplies in a clinical trial, when the two treatments 
cannot be made identical. Supplies are prepared for Treatment A 
(active and indistinguishable placebo) and for Treatment B (active 
and indistinguishable placebo). Subjects then take two sets of 
treatment; either A (active) and B (placebo), or A (placebo) and B 
(active).
    Dropout--A subject in a clinical trial who for any reason fails 
to continue in the trial until the last visit required of him/her by 
the study protocol.
    Equivalence trial--A trial with the primary objective of showing 
that the response to two or more treatments differs by an amount 
which is clinically unimportant. This is usually demonstrated by 
showing that the true treatment difference is likely to lie between 
a lower and an upper equivalence margin of clinically acceptable 
differences.
    Frequentist methods--Statistical methods, such as significance 
tests and confidence intervals, which can be interpreted in terms of 
the frequency of certain outcomes occurring in hypothetical repeated 
realizations of the same experimental situation.
    Full analysis set--The set of subjects that is as close as 
possible to the ideal implied by the intention-to-treat principle. 
It is derived from the set of all randomized subjects by minimal and 
justified elimination of subjects.
    Generalizability, generalization--The extent to which the 
findings of a clinical trial can be reliably extrapolated from the 
subjects who participated in the trial to a broader patient 
population and a broader range of clinical settings.
    Global assessment variable--A single variable, usually a scale 
of ordered categorical ratings, that integrates objective variables 
and the investigator's overall impression about the state or change 
in state of a subject.
    Independent data monitoring committee (IDMC) (data and safety 
monitoring board, monitoring committee, data monitoring committee)--
An independent data monitoring committee that may be established by 
the sponsor to assess at intervals the progress of a clinical trial, 
the safety data, and the critical efficacy endpoints, and to 
recommend to the sponsor whether to continue, modify, or stop a 
trial.
    Intention-to-treat principle--The principle that asserts that 
the effect of a treatment policy can be best assessed by evaluating 
on the basis of the intention to treat a subject (i.e., the planned 
treatment regimen) rather than the actual treatment given. It has 
the consequence that subjects allocated to a treatment group should 
be followed up, assessed, and analyzed as members of that group 
irrespective of their compliance with the planned course of 
treatment.
    Interaction (qualitative and quantitative)--The situation in 
which a treatment contrast (e.g., difference between investigational 
product and control) is dependent on another factor (e.g., center). 
A quantitative interaction refers to the case where the magnitude of 
the contrast differs at the different levels of the factor, whereas 
for a qualitative interaction the direction of the contrast differs 
for at least one level of the factor.
    Interrater reliability--The property of yielding equivalent 
results when used by different raters on different occasions.
    Intrarater reliability--The property of yielding equivalent 
results when used by the same rater on different occasions.
    Interim analysis--Any analysis intended to compare treatment 
arms with respect to efficacy or safety at any time prior to the 
formal completion of a trial.
    Meta-analysis--The formal evaluation of the quantitative 
evidence from two or more

[[Page 49598]]

trials bearing on the same question. This most commonly involves the 
statistical combination of summary statistics from the various 
trials, but the term is sometimes also used to refer to the 
combination of the raw data.
    Multicenter trial--A clinical trial conducted according to a 
single protocol but at more than one site and, therefore, carried 
out by more than one investigator.
    Noninferiority trial--A trial with the primary objective of 
showing that the response to the investigational product is not 
clinically inferior to a comparative agent (active or placebo 
control).
    Preferred and included terms--In a hierarchical medical 
dictionary, for example, the World Health Organization's Adverse 
Reaction Terminology (WHO-Art), the included term is the lowest 
level of dictionary term to which the investigator description is 
coded. The preferred term is the level of grouping of included terms 
typically used in reporting frequency of occurrence. For example, 
the investigator text ``Pain in the left arm'' might be coded to the 
included term ``Joint pain,'' which is reported at the preferred 
term level as ``Arthralgia.''
    Per protocol set (valid cases, efficacy sample, evaluable 
subjects sample)--The set of data generated by the subset of 
subjects who complied with the protocol sufficiently to ensure that 
these data would be likely to exhibit the effects of treatment 
according to the underlying scientific model. Compliance covers such 
considerations as exposure to treatment, availability of 
measurements, and absence of major protocol violations.
    Safety and tolerability--The safety of a medical product 
concerns the medical risk to the subject, usually assessed in a 
clinical trial by laboratory tests (including clinical chemistry and 
hematology), vital signs, clinical adverse events (diseases, signs 
and symptoms), and other special safety tests (e.g., 
electrocardiograms, ophthalmology). The tolerability of the medical 
product represents the degree to which overt adverse effects can be 
tolerated by the subject.
    Statistical analysis plan--A statistical analysis plan is a 
document that contains a more technical and detailed elaboration of 
the principal features of the analysis described in the protocol, 
and includes detailed procedures for executing the statistical 
analysis of the primary and secondary variables and other data.
    Superiority trial--A trial with the primary objective of showing 
that the response to the investigational product is superior to a 
comparative agent (active or placebo control).
    Surrogate variable--A variable that provides an indirect 
measurement of effect in situations where direct measurement of 
clinical effect is not feasible or practical.
    Treatment effect--An effect attributed to a treatment in a 
clinical trial. In most clinical trials, the treatment effect of 
interest is a comparison (or contrast) of two or more treatments.
    Treatment emergent--An event that emerges during treatment, 
having been absent pretreatment, or worsens relative to the 
pretreatment state.
    Trial statistician--A statistician who has a combination of 
education/training and experience sufficient to implement the 
principles in this guidance and who is responsible for the 
statistical aspects of the trial.

    Dated: September 8, 1998.
William K. Hubbard,
Associate Commissioner for Policy Coordination.
[FR Doc. 98-24754 Filed 9-15-98; 8:45 am]
BILLING CODE 4160-01-F