Guidance for Industry

E9 Statistical Principles for Clinical

Trials

U.S. Department of Health and Human Services

Food and Drug Administration

Center for Drug Evaluation and Research (CDER)

Center for Biologics Evaluation and Research (CBER)

September 1998

ICH
Guidance for Industry

E9 Statistical Principles for Clinical

Trials

Additional copies are available from:

Office of Training and Communications

Division of Drug Information (HFD-240)

Center for Drug Evaluation and Research (CDER),

5600 Fishers Lane, Rockville, MD 20857 (Tel) 301-827-4573

http://www.fda.gov/cder/guidance/index.htm

or

Office of Communication, Training, and Manufacturers Assistance (HFM-40)

Center for Biologics Evaluation and Research (CBER)

1401 Rockville Pike, Rockville, MD 20852-1448

http://www.fda.gov/cber/guidelines.htm; (Fax) 888-CBERFAX or 301-827-3844

(Voice Information) 800-835-4709 or 301-827-1800

U.S. Department of Health and Human Services

Food and Drug Administration

Center for Drug Evaluation and Research (CDER)

Center for Biologics Evaluation and Research (CBER)

September 1998

ICH
i

TABLE OF CONTENTS

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

A. BACKGROUND AND PURPOSE (1.1) ...........................................................................................................................1

B. SCOPE AND DIRECTION (1.2).....................................................................................................................................2

II. CONSIDERATIONS FOR OVERALL CLINICAL DEVELOPMENT.................................................................4

A. TRIAL CONTEXT (2.1)................................................................................................................................................4

B. SCOPE OF TRIALS (2.2) .............................................................................................................................................6

C. DESIGN TECHNIQUES TO AVOID BIAS (2.3).............................................................................................................10

III. TRIAL DESIGN CONSIDERATIONS...................................................................................................................14

A. DESIGN CONFIGURATION (3.1)................................................................................................................................14

B. MULTICENTER TRIALS (3.2)....................................................................................................................................16

C. TYPE OF COMPARISON (3.3)....................................................................................................................................18

D. GROUP SEQUENTIAL DESIGNS (3.4).........................................................................................................................21

E. SAMPLE SIZE (3.5)...................................................................................................................................................21

F. DATA CAPTURE AND PROCESSING (3.6)...................................................................................................................23

IV. TRIAL CONDUCT CONSIDERATIONS..............................................................................................................23

A. TRIAL MONITORING AND INTERIM ANALYSIS (4.1) .................................................................................................23

B. CHANGES IN INCLUSION AND EXCLUSION CRITERIA (4.2)........................................................................................24

C. ACCRUAL RATES (4.3) ............................................................................................................................................24

D. SAMPLE SIZE ADJUSTMENT (4.4).............................................................................................................................24

E. INTERIM ANALYSIS AND EARLY STOPPING (4.5) ......................................................................................................24

F. ROLE OF INDEPENDENT DATA MONITORING COMMITTEE (IDMC) (4.6) ...............................................................26

V. DATA ANALYSIS CONSIDERATIONS................................................................................................................27

A. PRESPECIFICATION OF THE ANALYSIS (5.1).............................................................................................................27

B. ANALYSIS SETS (5.2) ..............................................................................................................................................27

C. MISSING VALUES AND OUTLIERS (5.3)....................................................................................................................31

D. DATA TRANSFORMATION (5.4)................................................................................................................................31

E. ESTIMATION, CONFIDENCE INTERVALS, AND HYPOTHESIS TESTING (5.5) ..............................................................32

F. ADJUSTMENT OF SIGNIFICANCE AND CONFIDENCE LEVELS (5.6).............................................................................33

G. SUBGROUPS, INTERACTIONS, AND COVARIATES (5.7) .............................................................................................33

H. INTEGRITY OF DATA AND COMPUTER SOFTWARE VALIDITY (5.8).............................................................................34

VI. EVALUATION OF SAFETY AND TOLERABILITY.......................................................................................34

A. SCOPE OF EVALUATION (6.1)...................................................................................................................................34

B. CHOICE OF VARIABLES AND DATA COLLECTION (6.2).............................................................................................34

C. SET OF SUBJECTS TO BE EVALUATED AND PRESENTATION OF DATA (6.3) ...............................................................35

D. STATISTICAL EVALUATION (6.4)..............................................................................................................................36

E. INTEGRATED SUMMARY (6.5)...................................................................................................................................37

VII. REPORTING.......................................................................................................................................................37

A. EVALUATION AND REPORTING (7.1) ........................................................................................................................37

B. SUMMARIZING THE CLINICAL DATABASE (7.2).........................................................................................................39

GLOSSARY (ANNEX 1) ...................................................................................................................................................41
1

GUIDANCE FOR INDUSTRY1

E9 Statistical Principles for Clinical Trials

I. INTRODUCTION

A. Background and Purpose (1.1) 2

The efficacy and safety of medicinal products should be demonstrated by clinical trials that

follow the guidance in E6 Good Clinical Practice: Consolidated Guidance adopted by the

ICH, May 1, 1996. The role of statistics in clinical trial design and analysis is

acknowledged as essential in that ICH guidance. 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

 

1

 This guidance was developed within the Expert Working Group (Efficacy) of the International Conference on

Harmonisation of Technical Requirements for Registration of Pharmaceuticals for Human Use (ICH) and has been subject to

consultation by the regulatory parties, in accordance with the ICH process. This document has been endorsed by the ICH

Steering Committee at Step 4 of the ICH process, February 1998. At Step 4 of the process, the final draft is recommended for

adoption to the regulatory bodies of the European Union, Japan, and the United States. This guidance was published in the

Federal Register on September 16, 1998 (63 FR 49583), and is applicable to drug and biological products. 

2 Arabic numbers reflect the organizational breakdown in the document endorsed by the ICH Steering Committee at

Step 4 of the ICH process, February 1998.

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

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

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

statutes and regulations.
2

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 (March 1995)

E2A Clinical Safety Data Management: Definitions and Standards for Expedited

Reporting (March 1995)

E2B Clinical Safety Data Management: Data Elements for Transmission of Individual

Case Safety Reports (January 1998)

E2C Clinical Safety Data Management: Periodic Safety Update Reports for Marketed

Drugs (November 1996)

E3 Structure and Content of Clinical Study Reports (July 1996)

E4 Dose-Response Information to Support Drug Registration (November 1994)

E5 Ethnic Factors in the Acceptability of Foreign Clinical Data (June 1998)

E6 Good Clinical Practice: Consolidated Guideline (April 1996)

E7 Studies in Support of Special Populations: Geriatrics (August 1994)

E8 General Considerations for Clinical Trials (December 1997

E10 Choice of Control Group in Clinical Trials (September 1999)

M1 Standardization of Medical Terminology for Regulatory Purposes (November

1999)

M3 Nonclinical Safety Studies for the Conduct of Human Clinical Trials for

Pharmaceuticals (July 1997)

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.

B. Scope and Direction (1.2)

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 froma 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 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
3

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
4

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

A. Trial Context (2.1)

1. Development Plan (2.1.1)

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 VII.B). 

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. Confirmatory Trial (2.1.2)

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,
5

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.

3. Exploratory Trial (2.1.3)

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 which will provide data for exploratory analysis.
6

B. Scope of Trials (2.2)

1. Population (2.2.1)

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. Primary and Secondary Variables (2.2.2)

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 III.E).

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
7

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.

3. Composite Variables (2.2.3)

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
8

validity (see Glossary), inter- and intrarater reliability (see Glossary), and

responsiveness for detecting changes in the severity of disease.

4. Global Assessment Variables (2.2.4)

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:

• The relevance of the scale to the primary objective of the trial;

• The basis for the validity and reliability of the scale;

• How to utilize the data collected on an individual subject to assign him/her

to a unique category of the scale;

• 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.
9

5. Multiple Primary Variables (2.2.5)

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 V.F); 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.

6. Surrogate Variables (2.2.6)

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. Second, 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.
10

7. Categorized Variables (2.2.7)

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. 

C. Design Techniques to Avoid Bias (2.3)

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 II.C.1 and most of section II.C.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.

1. Blinding (2.3.1)

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.
11

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
12

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 openlabel 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, 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. Randomization (2.3.2)

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
13

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
14

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

A. Design Configuration (3.1)

1. Parallel Group Design (3.1.1)

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).

2. Crossover Design (3.1.2)

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 2x2 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(>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(>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 2x2 design, the carryover effect

cannot be statistically distinguished from the interaction between treatment and
15

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 subjects from the trial

are expected to be small.

A common, and generally satisfactory, use of the 2x2 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. Factorial Designs (3.1.3)

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 2x2

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
16

similar number, n, of doses of D. The full design then consists of mxn 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 2x2 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.

B. Multicenter Trials (3.2)

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 judgement 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. 
17

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 V.A) 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-bycenter 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
18

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 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. 

C. Type of Comparison (3.3)

1. Trials to Show Superiority (3.3.1)

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.

2. Trials to Show Equivalence or Noninferiority (3.3.2)

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).
19

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 welldocumented 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
20

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 V.E). 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

III.E).

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 V.B.3).

3. Trials to Show Dose-Response Relationship (3.3.3)

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,
21

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.

D. Group Sequential Designs (3.4)

Group sequential designs are used to facilitate the conduct of interim analysis (see section

IV.E 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 IV.E). An

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

IV.F). 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.

E. Sample Size (3.5)

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 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
22

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 judgement concerning the minimal effect which has clinical relevance in the

management of patients or on a judgement 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 III.C.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 IV.D).
23

F. Data Capture and Processing (3.6)

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

A. Trial Monitoring and Interim Analysis (4.1)

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 IV.B to

IV.D). 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.
24

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

IV.E and IV.F.

B. Changes in Inclusion and Exclusion Criteria (4.2)

Inclusion and exclusion criteria should remain constant, as specified in the protocol,

throughout the period of subject recruitment. 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.

C. Accrual Rates (4.3)

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.

D. Sample Size Adjustment (4.4)

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 III.E).

E. Interim Analysis and Early Stopping (4.5)
25

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 III.D). 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 IV.F), 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
26

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.

F. Role of Independent Data Monitoring Committee (IDMC) (4.6)

(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 (e.g., covering whether or not they can vote on

key issues). Since these sponsor staff would have access to unblinded information, the
27

procedures should also address the control of dissemination of interim trial results within

the sponsor organization.

V. DATA ANALYSIS CONSIDERATIONS

A. Prespecification of the Analysis (5.1)

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

VII.A). 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 VII.A 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).

B. Analysis Sets (5.2)

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 follow-up, and provided complete data records,

then the set of subjects to be included in the analysis would be self-evident. The design
28

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.

1. Full Analysis Set (5.2.1)

The intention-to-treat (see Glossary) principle implies that the primary analysis

should include all randomized subjects. Compliance with this principle would

necessitate complete follow-up 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:

a. The entry criterion was measured prior to randomization. (i)

b. The detection of the relevant eligibility violations can be made

completely objectively. (ii)
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c. 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.) (iii)

d. All detected violations of the particular entry criterion are excluded.

(iv)

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 follow-up, 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.
30

2. Per Protocol Set (5.2.2)

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:

a. The completion of a certain prespecified minimal exposure to the

treatment regimen (i)

b. The availability of measurements of the primary variable(s) (ii)

c. The absence of any major protocol violations, including the

violation of entry criteria (iii)

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.

3. Roles of the Different Analysis Sets (5.2.3)

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.
31

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 III.C.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.

C. Missing Values and Outliers (5.3)

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.

D. Data Transformation (5.4)

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.
32

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 II.B.2.

E. Estimation, Confidence Intervals, and Hypothesis Testing (5.5)

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 V.G.) 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
33

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.

F. Adjustment of Significance and Confidence Levels (5.6)

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

data may necessitate an adjustment to the Type I error. Multiplicity may arise, for

example, from multiple primary variables (see section II.B.2), multiple comparisons of

treatments, repeated evaluation over time, and/or interim analyses (see section IV.E). 

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.

G. Subgroups, Interactions, and Covariates (5.7)

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
34

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.

H. Integrity of Data and Computer Software Validity (5.8)

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

A. Scope of Evaluation (6.1)

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.

B. Choice of Variables and Data Collection (6.2)

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
35

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).

C. Set of Subjects to Be Evaluated and Presentation of Data (6.3)

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
36

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.

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.

D. Statistical Evaluation (6.4)

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.
37

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.

E. Integrated Summary (6.5)

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 VII.B.2).

For more details on the reporting of safety and tolerability, see section 12 of ICH E3.

VII. REPORTING

A. Evaluation and Reporting (7.1)

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 V. 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 V. 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.
38

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.
39

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 V.G) 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.

B. Summarizing the Clinical Database (7.2)

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 modelling of the various sources of

variation. The sensitivity of conclusions to the assumptions and selections made should be

explored.
40

1. Efficacy Data (7.2.1)

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.

2. Safety Data (7.2.2)

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.
41

GLOSSARY (Annex 1)

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 factors associated 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 bias.

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.
42

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 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).
43

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.