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

DEPARTMENT OF HEALTH AND HUMAN SERVICES

Food and Drug Administration

[Docket No. 97D-0174]

International Conference on Harmonisation; Guidance on

Statistical Principles for Clinical Trials; Availability

AGENCY: Food and Drug Administration, HHS.

ACTION: Notice.

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SUMMARY: The Food and Drug Administration (FDA) is publishing a

guidance entitled ``E9 Statistical Principles for Clinical Trials.''

The guidance was prepared under the auspices of the International

Conference on Harmonisation of Technical Requirements for Registration

of Pharmaceuticals for Human Use (ICH). The guidance is intended to

provide recommendations to sponsors and scientific experts regarding

statistical principles and methodology which, when applied to clinical

trials for marketing applications, will facilitate the general

acceptance of analyses and conclusions drawn from the trials.

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

time.

ADDRESSES: Submit written comments on the guidance to the Dockets

Management Branch (HFA-305), Food and Drug Administration, 5630 Fishers

Lane, rm. 1061, Rockville, MD 20852. Copies of the guidance are

available from the Drug Information Branch (HFD-210), Center for Drug

Evaluation and Research, Food and Drug Administration, 5600 Fishers

Lane, Rockville, MD 20857, 301-827-4573. Single copies of the guidance

may be obtained by mail from the Office of Communication, Training and

Manufacturers Assistance (HFM-40), Center for Biologics Evaluation and

Research (CBER), 1401 Rockville Pike, Rockville, MD 20852-1448, or by

calling the CBER Voice Information System at 1-800-835-4709 or 301-827-

1800. Copies may be obtained from CBER's FAX Information System at 1-

888-CBER-FAX or 301-827-3844.

FOR FURTHER INFORMATION CONTACT:

Regarding the guidance: Robert O'Neill, Center for Drug Evaluation

and Research (HFD-700), Food and Drug Administration, 5600 Fishers

Lane, Rockville, MD 20857, 301-827-3195.

Regarding the ICH: Janet J. Showalter, Office of Health Affairs

(HFY-20), Food and Drug Administration, 5600 Fishers Lane, Rockville,

MD 20857, 301-827-0864.

SUPPLEMENTARY INFORMATION: In recent years, many important initiatives

have been undertaken by regulatory authorities and industry

associations to promote international harmonization of regulatory

requirements. FDA has participated in many meetings designed to enhance

harmonization and is committed to seeking scientifically based

harmonized technical procedures for pharmaceutical development. One of

the goals of harmonization is to identify and then reduce differences

in technical requirements for drug development among regulatory

agencies.

ICH was organized to provide an opportunity for tripartite

harmonization initiatives to be developed with input from both

regulatory and industry representatives. FDA also seeks input from

consumer representatives and others. ICH is concerned with

harmonization of technical requirements for the registration of

pharmaceutical products among three regions: The European Union, Japan,

and the United States. The six ICH sponsors are: The European

Commission, the European Federation of Pharmaceutical Industries

Associations, the Japanese Ministry of Health and Welfare, the Japanese

Pharmaceutical Manufacturers Association, the Centers for Drug

Evaluation and Research and Biologics Evaluation and Research, FDA, and

the Pharmaceutical Research and Manufacturers of America. The ICH

Secretariat, which coordinates the preparation of documentation, is

provided by the International Federation of Pharmaceutical

Manufacturers Associations (IFPMA).

The ICH Steering Committee includes representatives from each of

the ICH sponsors and the IFPMA, as well as observers from the World

Health Organization, the Canadian Health Protection Branch, and the

European Free Trade Area.

In the Federal Register of May 9, 1997 (62 FR 25712), FDA published

a draft tripartite guideline entitled ``Statistical Principles for

Clinical Trials'' (E9). The notice gave interested persons an

opportunity to submit comments by June 23, 1997.

After consideration of the comments received and revisions to the

guidance, a final draft of the guidance was submitted to the ICH

Steering Committee and endorsed by the three participating regulatory

agencies on February 5, 1998.

In accordance with FDA's Good Guidance Practices (62 FR 8961,

February 27, 1997), this document has been designated a guidance,

rather than a guideline.

The guidance addresses principles of statistical methodology

applied to clinical trials for marketing applications. The guidance

provides recommendations to sponsors for the design, conduct, analysis,

and evaluation of clinical trials of an investigational product in the

context of its overall clinical development. The document also provides

guidance to scientific experts in preparing application summaries or

assessing evidence of efficacy and safety, principally from late Phase

II and Phase III clinical trials. Application of the principles of

statistical methodology is intended to facilitate the general

acceptance of analyses and conclusions drawn from clinical trials.

This guidance represents the agency's current thinking on

statistical principles for clinical trials of drugs and biologics.

[[Page 49584]]

It does not create or confer any rights for, or on, any person and

does not operate to bind FDA or the public. An alternative approach may

be used if such approach satisfies the requirements of the applicable

statute, regulations, or both.

As with all of FDA's guidances, the public is encouraged to submit

written comments with new data or other new information pertinent to

this guidance. The comments in the docket will be periodically

reviewed, and, where appropriate, the guidance will be amended. The

public will be notified of any such amendments through a notice in the

Federal Register.

Interested persons may, at any time, submit written comments on the

guidance to the Dockets Management Branch (address above). Two copies

of any comments are to be submitted, except that individuals may submit

one copy. Comments are to be identified with the docket number found in

brackets in the heading of this document. The guidance and received

comments may be seen in the office above between 9 a.m. and 4 p.m.,

Monday through Friday. An electronic version of this guidance is

available on the Internet at ``http://www.fda.gov/cder/guidance/

index.htm'' or at CBER's World Wide Web site at ``http://www.fda.gov/

cber/publications.htm''.

The text of the guidance follows:

E9 Statistical Principles for Clinical Trials \1\

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\1\ This guidance represents the agency's current thinking on

statistical principles for clinical trials of drugs and biologics.

It does not create or confer any rights for or on any person and

does not operate to bind FDA or the public. An alternative approach

may be used if such approach satisfies the requirements of the

applicable statute, regulations, or both.

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Note: A glossary of terms and definitions is provided as an

annex to this guidance.

I. Introduction

1.1 Background and Purpose

1.2 Scope and Direction

II. Considerations for Overall Clinical Development

2.1 Trial Context

2.1.1 Development Plan

2.1.2 Confirmatory Trial

2.1.3 Exploratory Trial

2.2 Scope of Trials

2.2.1 Population

2.2.2 Primary and Secondary Variables

2.2.3 Composite Variables

2.2.4 Global Assessment Variables

2.2.5 Multiple Primary Variables

2.2.6 Surrogate Variables

2.2.7 Categorized Variables

2.3 Design Techniques to Avoid Bias

2.3.1 Blinding

2.3.2 Randomization

III. Trial Design Considerations

3.1 Design Configuration

3.1.1 Parallel Group Design

3.1.2 Crossover Design

3.1.3 Factorial Designs

3.2 Multicenter Trials

3.3 Type of Comparison

3.3.1 Trials to Show Superiority

3.3.2 Trials to Show Equivalence or Noninferiority

3.3.3 Trials to Show Dose-Response Relationship

3.4 Group Sequential Designs

3.5 Sample Size

3.6 Data Capture and Processing

IV. Trial Conduct Considerations

4.1 Trial Monitoring and Interim Analysis

4.2 Changes in Inclusion and Exclusion Criteria

4.3 Accrual Rates

4.4 Sample Size Adjustment

4.5 Interim Analysis and Early Stopping

4.6 Role of Independent Data Monitoring Committee (IDMC)

V. Data Analysis Considerations

5.1 Prespecification of the Analysis

5.2 Analysis Sets

5.2.1 Full Analysis Set

5.2.2 Per Protocol Set

5.2.3 Roles of the Different Analysis Sets

5.3 Missing Values and Outliers

5.4 Data Transformation

5.5 Estimation, Confidence Intervals, and Hypothesis Testing

5.6 Adjustment of Significance and Confidence Levels

5.7 Subgroups, Interactions, and Covariates

5.8 Integrity of Data and Computer Software Validity

VI. Evaluation of Safety and Tolerability

6.1 Scope of Evaluation

6.2 Choice of Variables and Data Collection

6.3 Set of Subjects to be Evaluated and Presentation of Data

6.4 Statistical Evaluation

6.5 Integrated Summary

VII. Reporting

7.1 Evaluation and Reporting

7.2 Summarizing the Clinical Database

7.2.1 Efficacy Data

7.2.2 Safety Data

Annex 1 Glossary

I. Introduction

1.1 Background and Purpose

The efficacy and safety of medicinal products should be

demonstrated by clinical trials that follow the guidance in ``Good

Clinical Practice: Consolidated Guideline'' (ICH E6) adopted by the

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

and analysis is acknowledged as essential in that ICH guideline. The

proliferation of statistical research in the area of clinical trials

coupled with the critical role of clinical research in the drug

approval process and health care in general necessitate a succinct

document on statistical issues related to clinical trials. This

guidance is written primarily to attempt to harmonize the principles

of statistical methodology applied to clinical trials for marketing

applications submitted in Europe, Japan, and the United States.

As a starting point, this guidance utilized the CPMP (Committee

for Proprietary Medicinal Products) Note for Guidance entitled

``Biostatistical Methodology in Clinical Trials in Applications for

Marketing Authorizations for Medicinal Products'' (December, 1994).

It was also influenced by ``Guidelines on the Statistical Analysis

of Clinical Studies'' (March 1992) from the Japanese Ministry of

Health and Welfare and the U.S. Food and Drug Administration

document entitled ``Guideline for the Format and Content of the

Clinical and Statistical Sections of a New Drug Application'' (July

1988). Some topics related to statistical principles and methodology

are also embedded within other ICH guidances, particularly those

listed below. The specific guidance that contains related text will

be identified in various sections of this document.

E1A: The Extent of Population Exposure to Assess Clinical Safety

E2A: Clinical Safety Data Management: Definitions and Standards

for Expedited Reporting

E2B: Clinical Safety Data Management: Data Elements for

Transmission of Individual Case Safety Reports

E2C: Clinical Safety Data Management: Periodic Safety Update

Reports for Marketed Drugs

E3: Structure and Content of Clinical Study Reports

E4: Dose-Response Information to Support Drug Registration

E5: Ethnic Factors in the Acceptability of Foreign Clinical Data

E6: Good Clinical Practice: Consolidated Guideline

E7: Studies in Support of Special Populations: Geriatrics

E8: General Considerations for Clinical Trials

E10: Choice of Control Group in Clinical Trials

M1: Standardization of Medical Terminology for Regulatory

Purposes

M3: Nonclinical Safety Studies for the Conduct of Human Clinical

Trials for Pharmaceuticals.

This guidance is intended to give direction to sponsors in the

design, conduct, analysis, and evaluation of clinical trials of an

investigational product in the context of its overall clinical

development. The document will also assist scientific experts

charged with preparing application summaries or assessing evidence

of efficacy and safety, principally from clinical trials in later

phases of development.

1.2 Scope and Direction

The focus of this guidance is on statistical principles. It does

not address the use of specific statistical procedures or methods.

Specific procedural steps to ensure that principles are implemented

properly are the responsibility of the sponsor. Integration of data

across clinical trials is discussed, but is not a primary focus of

this guidance. Selected principles and procedures related to data

management or clinical trial monitoring activities are covered in

other ICH guidances and are not addressed here.

This guidance should be of interest to individuals from a broad

range of scientific disciplines. However, it is assumed that the

actual responsibility for all statistical work associated with

clinical trials will lie with an appropriately qualified and

experienced statistician, as indicated in ICH E6. The role

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and responsibility of the trial statistician (see Glossary), in

collaboration with other clinical trial professionals, is to ensure

that statistical principles are applied appropriately in clinical

trials supporting drug development. Thus, the trial statistician

should have a combination of education/training and experience

sufficient to implement the principles articulated in this guidance.

For each clinical trial contributing to a marketing application,

all important details of its design and conduct and the principal

features of its proposed statistical analysis should be clearly

specified in a protocol written before the trial begins. The extent

to which the procedures in the protocol are followed and the primary

analysis is planned a priori will contribute to the degree of

confidence in the final results and conclusions of the trial. The

protocol and subsequent amendments should be approved by the

responsible personnel, including the trial statistician. The trial

statistician should ensure that the protocol and any amendments

cover all relevant statistical issues clearly and accurately, using

technical terminology as appropriate.

The principles outlined in this guidance are primarily relevant

to clinical trials conducted in the later phases of development,

many of which are confirmatory trials of efficacy. In addition to

efficacy, confirmatory trials may have as their primary variable a

safety variable (e.g., an adverse event, a clinical laboratory

variable, or an electrocardiographic measure) or a pharmacodynamic

or pharmacokinetic variable (as in a confirmatory bioequivalence

trial). Furthermore, some confirmatory findings may be derived from

data integrated across trials, and selected principles in this

guidance are applicable in this situation. Finally, although the

early phases of drug development consist mainly of clinical trials

that are exploratory in nature, statistical principles are also

relevant to these clinical trials. Hence, the substance of this

document should be applied as far as possible to all phases of

clinical development.

Many of the principles delineated in this guidance deal with

minimizing bias (see Glossary) and maximizing precision. As used in

this guidance, the term ``bias'' describes the systematic tendency

of any factors associated with the design, conduct, analysis, and

interpretation of the results of clinical trials to make the

estimate of a treatment effect (see Glossary) deviate from its true

value. It is important to identify potential sources of bias as

completely as possible so that attempts to limit such bias may be

made. The presence of bias may seriously compromise the ability to

draw valid conclusions from clinical trials.

Some sources of bias arise from the design of the trial, for

example an assignment of treatments such that subjects at lower risk

are systematically assigned to one treatment. Other sources of bias

arise during the conduct and analysis of a clinical trial. For

example, protocol violations and exclusion of subjects from analysis

based upon knowledge of subject outcomes are possible sources of

bias that may affect the accurate assessment of the treatment

effect. Because bias can occur in subtle or unknown ways and its

effect is not measurable directly, it is important to evaluate the

robustness of the results and primary conclusions of the trial.

Robustness is a concept that refers to the sensitivity of the

overall conclusions to various limitations of the data, assumptions,

and analytic approaches to data analysis. Robustness implies that

the treatment effect and primary conclusions of the trial are not

substantially affected when analyses are carried out based on

alternative assumptions or analytic approaches. The interpretation

of statistical measures of uncertainty of the treatment effect and

treatment comparisons should involve consideration of the potential

contribution of bias to the p-value, confidence interval, or

inference.

Because the predominant approaches to the design and analysis of

clinical trials have been based on frequentist statistical methods,

the guidance largely refers to the use of frequentist methods (see

Glossary) when discussing hypothesis testing and/or confidence

intervals. This should not be taken to imply that other approaches

are not appropriate; the use of Bayesian (see Glossary) and other

approaches may be considered when the reasons for their use are

clear and when the resulting conclusions are sufficiently robust.

II. Considerations for Overall Clinical Development

2.1 Trial Context

2.1.1 Development Plan

The broad aim of the process of clinical development of a new

drug is to find out whether there is a dose range and schedule at

which the drug can be shown to be simultaneously safe and effective,

to the extent that the risk-benefit relationship is acceptable. The

particular subjects who may benefit from the drug, and the specific

indications for its use, also need to be defined.

Satisfying these broad aims usually requires an ordered program

of clinical trials, each with its own specific objectives (see ICH

E8). This should be specified in a clinical plan, or a series of

plans, with appropriate decision points and flexibility to allow

modification as knowledge accumulates. A marketing application

should clearly describe the main content of such plans, and the

contribution made by each trial. Interpretation and assessment of

the evidence from the total program of trials involves synthesis of

the evidence from the individual trials (see section 7.2). This is

facilitated by ensuring that common standards are adopted for a

number of features of the trials, such as dictionaries of medical

terms, definition and timing of the main measurements, handling of

protocol deviations, and so on. A statistical summary, overview, or

meta-analysis (see Glossary) may be informative when medical

questions are addressed in more than one trial. Where possible, this

should be envisaged in the plan so that the relevant trials are

clearly identified and any necessary common features of their

designs are specified in advance. Other major statistical issues (if

any) that are expected to affect a number of trials in a common plan

should be addressed in that plan.

2.1.2 Confirmatory Trial

A confirmatory trial is an adequately controlled trial in which

the hypotheses are stated in advance and evaluated. As a rule,

confirmatory trials are necessary to provide firm evidence of

efficacy or safety. In such trials the key hypothesis of interest

follows directly from the trial's primary objective, is always

predefined, and is the hypothesis that is subsequently tested when

the trial is complete. In a confirmatory trial, it is equally

important to estimate with due precision the size of the effects

attributable to the treatment of interest and to relate these

effects to their clinical significance.

Confirmatory trials are intended to provide firm evidence in

support of claims; hence adherence to protocols and standard

operating procedures is particularly important. Unavoidable changes

should be explained and documented, and their effect examined. A

justification of the design of each such trial and of other

important statistical aspects, such as the principal features of the

planned analysis, should be set out in the protocol. Each trial

should address only a limited number of questions.

Firm evidence in support of claims requires that the results of

the confirmatory trials demonstrate that the investigational product

under test has clinical benefits. The confirmatory trials should

therefore be sufficient to answer each key clinical question

relevant to the efficacy or safety claim clearly and definitively.

In addition, it is important that the basis for generalization (see

Glossary) to the intended patient population is understood and

explained; this may also influence the number and type (e.g.,

specialist or general practitioner) of centers and/or trials needed.

The results of the confirmatory trial(s) should be robust. In some

circumstances, the weight of evidence from a single confirmatory

trial may be sufficient.

2.1.3 Exploratory Trial

The rationale and design of confirmatory trials nearly always

rests on earlier clinical work carried out in a series of

exploratory studies. Like all clinical trials, these exploratory

studies should have clear and precise objectives. However, in

contrast to confirmatory trials, their objectives may not always

lead to simple tests of predefined hypotheses. In addition,

exploratory trials may sometimes require a more flexible approach to

design so that changes can be made in response to accumulating

results. Their analysis may entail data exploration. Tests of

hypothesis may be carried out, but the choice of hypothesis may be

data dependent. Such trials cannot be the basis of the formal proof

of efficacy, although they may contribute to the total body of

relevant evidence.

Any individual trial may have both confirmatory and exploratory

aspects. For example, in most confirmatory trials the data are also

subjected to exploratory analyses which serve as a basis for

explaining or supporting their findings and for suggesting further

hypotheses for later research. The protocol should make a clear

distinction between the aspects of a trial which will be used for

confirmatory proof and the aspects

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which will provide data for exploratory analysis.

2.2 Scope of Trials

2.2.1 Population

In the earlier phases of drug development, the choice of

subjects for a clinical trial may be heavily influenced by the wish

to maximize the chance of observing specific clinical effects of

interest. Hence they may come from a very narrow subgroup of the

total patient population for which the drug may eventually be

indicated. However, by the time the confirmatory trials are

undertaken, the subjects in the trials should more closely mirror

the target population. In these trials, it is generally helpful to

relax the inclusion and exclusion criteria as much as possible

within the target population while maintaining sufficient

homogeneity to permit precise estimation of treatment effects. No

individual clinical trial can be expected to be totally

representative of future users because of the possible influences of

geographical location, the time when it is conducted, the medical

practices of the particular investigator(s) and clinics, and so on.

However, the influence of such factors should be reduced wherever

possible and subsequently discussed during the interpretation of the

trial results.

2.2.2 Primary and Secondary Variables

The primary variable (``target'' variable, primary endpoint)

should be the variable capable of providing the most clinically

relevant and convincing evidence directly related to the primary

objective of the trial. There should generally be only one primary

variable. This will usually be an efficacy variable, because the

primary objective of most confirmatory trials is to provide strong

scientific evidence regarding efficacy. Safety/tolerability may

sometimes be the primary variable, and will always be an important

consideration. Measurements relating to quality of life and health

economics are further potential primary variables. The selection of

the primary variable should reflect the accepted norms and standards

in the relevant field of research. The use of a reliable and

validated variable with which experience has been gained either in

earlier studies or in published literature is recommended. There

should be sufficient evidence that the primary variable can provide

a valid and reliable measure of some clinically relevant and

important treatment benefit in the patient population described by

the inclusion and exclusion criteria. The primary variable should

generally be the one used when estimating the sample size (see

section 3.5).

In many cases, the approach to assessing subject outcome may not

be straightforward and should be carefully defined. For example, it

is inadequate to specify mortality as a primary variable without

further clarification; mortality may be assessed by comparing

proportions alive at fixed points in time or by comparing overall

distributions of survival times over a specified interval. Another

common example is a recurring event; the measure of treatment effect

may again be a simple dichotomous variable (any occurrence during a

specified interval), time to first occurrence, rate of occurrence

(events per time units of observation), and so on. The assessment of

functional status over time in studying treatment for chronic

disease presents other challenges in selection of the primary

variable. There are many possible approaches, such as comparisons of

the assessments done at the beginning and end of the interval of

observation, comparisons of slopes calculated from all assessments

throughout the interval, comparisons of the proportions of subjects

exceeding or declining beyond a specified threshold, or comparisons

based on methods for repeated measures data. To avoid multiplicity

concerns arising from post hoc definitions, it is critical to

specify in the protocol the precise definition of the primary

variable as it will be used in the statistical analysis. In

addition, the clinical relevance of the specific primary variable

selected and the validity of the associated measurement procedures

will generally need to be addressed and justified in the protocol.

The primary variable should be specified in the protocol, along

with the rationale for its selection. Redefinition of the primary

variable after unblinding will almost always be unacceptable, since

the biases this introduces are difficult to assess. When the

clinical effect defined by the primary objective is to be measured

in more than one way, the protocol should identify one of the

measurements as the primary variable on the basis of clinical

relevance, importance, objectivity, and/or other relevant

characteristics, whenever such selection is feasible.

Secondary variables are either supportive measurements related

to the primary objective or measurements of effects related to the

secondary objectives. Their predefinition in the protocol is also

important, as well as an explanation of their relative importance

and roles in interpretation of trial results. The number of

secondary variables should be limited and should be related to the

limited number of questions to be answered in the trial.

2.2.3 Composite Variables

If a single primary variable cannot be selected from multiple

measurements associated with the primary objective, another useful

strategy is to integrate or combine the multiple measurements into a

single or ``composite'' variable, using a predefined algorithm.

Indeed, the primary variable sometimes arises as a combination of

multiple clinical measurements (e.g., the rating scales used in

arthritis, psychiatric disorders, and elsewhere). This approach

addresses the multiplicity problem without requiring adjustment to

the Type I error. The method of combining the multiple measurements

should be specified in the protocol, and an interpretation of the

resulting scale should be provided in terms of the size of a

clinically relevant benefit. When a composite variable is used as a

primary variable, the components of this variable may sometimes be

analyzed separately, where clinically meaningful and validated. When

a rating scale is used as a primary variable, it is especially

important to address factors such as content validity (see

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

responsiveness for detecting changes in the severity of disease.

2.2.4 Global Assessment Variables

In some cases, ``global assessment'' variables (see Glossary)

are developed to measure the overall safety, overall efficacy, and/

or overall usefulness of a treatment. This type of variable

integrates objective variables and the investigator's overall

impression about the state or change in the state of the subject,

and is usually a scale of ordered categorical ratings. Global

assessments of overall efficacy are well established in some

therapeutic areas, such as neurology and psychiatry.

Global assessment variables generally have a subjective

component. When a global assessment variable is used as a primary or

secondary variable, fuller details of the scale should be included

in the protocol with respect to:

(1) The relevance of the scale to the primary objective of the

trial;

(2) The basis for the validity and reliability of the scale;

(3) How to utilize the data collected on an individual subject

to assign him/her to a unique category of the scale;

(4) How to assign subjects with missing data to a unique

category of the scale, or otherwise evaluate them.

If objective variables are considered by the investigator when

making a global assessment, then those objective variables should be

considered as additional primary or, at least, important secondary

variables.

Global assessment of usefulness integrates components of both

benefit and risk and reflects the decisionmaking process of the

treating physician, who must weigh benefit and risk in making

product use decisions. A problem with global usefulness variables is

that their use could in some cases lead to the result of two

products being declared equivalent despite having very different

profiles of beneficial and adverse effects. For example, judging the

global usefulness of a treatment as equivalent or superior to an

alternative may mask the fact that it has little or no efficacy but

fewer adverse effects. Therefore, it is not advisable to use a

global usefulness variable as a primary variable. If global

usefulness is specified as primary, it is important to consider

specific efficacy and safety outcomes separately as additional

primary variables.

2.2.5 Multiple Primary Variables

It may sometimes be desirable to use more than one primary

variable, each of which (or a subset of which) could be sufficient

to cover the range of effects of the therapies. The planned manner

of interpretation of this type of evidence should be carefully

spelled out. It should be clear whether an impact on any of the

variables, some minimum number of them, or all of them, would be

considered necessary to achieve the trial objectives. The primary

hypothesis or hypotheses and parameters of interest (e.g., mean,

percentage, distribution) should be clearly stated with respect to

the primary variables identified, and the approach to statistical

inference described. The effect on the Type I error should be

explained because of the potential for multiplicity problems (see

section 5.6);

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the method of controlling Type I error should be given in the

protocol. The extent of intercorrelation among the proposed primary

variables may be considered in evaluating the impact on Type I

error. If the purpose of the trial is to demonstrate effects on all

of the designated primary variables, then there is no need for

adjustment of the Type I error, but the impact on Type II error and

sample size should be carefully considered.

2.2.6 Surrogate Variables

When direct assessment of the clinical benefit to the subject

through observing actual clinical efficacy is not practical,

indirect criteria (surrogate variables--see Glossary) may be

considered. Commonly accepted surrogate variables are used in a

number of indications where they are believed to be reliable

predictors of clinical benefit. There are two principal concerns

with the introduction of any proposed surrogate variable. First, it

may not be a true predictor of the clinical outcome of interest. For

example, it may measure treatment activity associated with one

specific pharmacological mechanism, but may not provide full

information on the range of actions and ultimate effects of the

treatment, whether positive or negative. There have been many

instances where treatments showing a highly positive effect on a

proposed surrogate have ultimately been shown to be detrimental to

the subjects' clinical outcome; conversely, there are cases of

treatments conferring clinical benefit without measurable impact on

proposed surrogates. Secondly, proposed surrogate variables may not

yield a quantitative measure of clinical benefit that can be weighed

directly against adverse effects. Statistical criteria for

validating surrogate variables have been proposed but the experience

with their use is relatively limited. In practice, the strength of

the evidence for surrogacy depends upon (i) the biological

plausibility of the relationship, (ii) the demonstration in

epidemiological studies of the prognostic value of the surrogate for

the clinical outcome, and (iii) evidence from clinical trials that

treatment effects on the surrogate correspond to effects on the

clinical outcome. Relationships between clinical and surrogate

variables for one product do not necessarily apply to a product with

a different mode of action for treating the same disease.

2.2.7 Categorized Variables

Dichotomization or other categorization of continuous or ordinal

variables may sometimes be desirable. Criteria of ``success'' and

``response'' are common examples of dichotomies that should be

specified precisely in terms of, for example, a minimum percentage

improvement (relative to baseline) in a continuous variable or a

ranking categorized as at or above some threshold level (e.g.,

``good'') on an ordinal rating scale. The reduction of diastolic

blood pressure below 90 mmHg is a common dichotomization.

Categorizations are most useful when they have clear clinical

relevance. The criteria for categorization should be predefined and

specified in the protocol, as knowledge of trial results could

easily bias the choice of such criteria. Because categorization

normally implies a loss of information, a consequence will be a loss

of power in the analysis; this should be accounted for in the sample

size calculation.

2.3 Design Techniques to Avoid Bias

The most important design techniques for avoiding bias in

clinical trials are blinding and randomization, and these should be

normal features of most controlled clinical trials intended to be

included in a marketing application. Most such trials follow a

double-blind approach in which treatments are prepacked in

accordance with a suitable randomization schedule, and supplied to

the trial center(s) labeled only with the subject number and the

treatment period, so that no one involved in the conduct of the

trial is aware of the specific treatment allocated to any particular

subject, not even as a code letter. This approach will be assumed in

section 2.3.1 and most of section 2.3.2, exceptions being considered

at the end.

Bias can also be reduced at the design stage by specifying

procedures in the protocol aimed at minimizing any anticipated

irregularities in trial conduct that might impair a satisfactory

analysis, including various types of protocol violations,

withdrawals and missing values. The protocol should consider ways

both to reduce the frequency of such problems and to handle the

problems that do occur in the analysis of data.

2.3.1 Blinding

Blinding or masking is intended to limit the occurrence of

conscious and unconscious bias in the conduct and interpretation of

a clinical trial arising from the influence that the knowledge of

treatment may have on the recruitment and allocation of subjects,

their subsequent care, the attitudes of subjects to the treatments,

the assessment of end-points, the handling of withdrawals, the

exclusion of data from analysis, and so on. The essential aim is to

prevent identification of the treatments until all such

opportunities for bias have passed.

A double-blind trial is one in which neither the subject nor any

of the investigator or sponsor staff involved in the treatment or

clinical evaluation of the subjects are aware of the treatment

received. This includes anyone determining subject eligibility,

evaluating endpoints, or assessing compliance with the protocol.

This level of blinding is maintained throughout the conduct of the

trial, and only when the data are cleaned to an acceptable level of

quality will appropriate personnel be unblinded. If any of the

sponsor staff who are not involved in the treatment or clinical

evaluation of the subjects are required to be unblinded to the

treatment code (e.g., bioanalytical scientists, auditors, those

involved in serious adverse event reporting), the sponsor should

have adequate standard operating procedures to guard against

inappropriate dissemination of treatment codes. In a single-blind

trial the investigator and/or his staff are aware of the treatment

but the subject is not, or vice versa. In an open-label trial the

identity of treatment is known to all. The double-blind trial is the

optimal approach. This requires that the treatments to be applied

during the trial cannot be distinguished (by appearance, taste,

etc.) either before or during administration, and that the blind is

maintained appropriately during the whole trial.

Difficulties in achieving the double-blind ideal can arise: The

treatments may be of a completely different nature, for example,

surgery and drug therapy; two drugs may have different formulations

and, although they could be made indistinguishable by the use of

capsules, changing the formulation might also change the

pharmacokinetic and/or pharmacodynamic properties and hence

necessitate that bioequivalence of the formulations be established;

the daily pattern of administration of two treatments may differ.

One way of achieving double-blind conditions under these

circumstances is to use a ``double-dummy'' (see Glossary) technique.

This technique may sometimes force an administration scheme that is

sufficiently unusual to influence adversely the motivation and

compliance of the subjects. Ethical difficulties may also interfere

with its use when, for example, it entails dummy operative

procedures. Nevertheless, extensive efforts should be made to

overcome these difficulties.

The double-blind nature of some clinical trials may be partially

compromised by apparent treatment induced effects. In such cases,

blinding may be improved by blinding investigators and relevant

sponsor staff to certain test results (e.g., selected clinical

laboratory measures). Similar approaches (see below) to minimizing

bias in open-label trials should be considered in trials where

unique or specific treatment effects may lead to unblinding

individual patients.

If a double-blind trial is not feasible, then the single-blind

option should be considered. In some cases only an open-label trial

is practically or ethically possible. Single-blind and open-label

trials provide additional flexibility, but it is particularly

important that the investigator's knowledge of the next treatment

should not influence the decision to enter the subject; this

decision should precede knowledge of the randomized treatment. For

these trials, consideration should be given to the use of a

centralized randomization method, such as telephone randomization,

to administer the assignment of randomized treatment. In addition,

clinical assessments should be made by medical staff who are not

involved in treating the subjects and who remain blind to treatment.

In single-blind or open-label trials every effort should be made to

minimize the various known sources of bias and primary variables

should be as objective as possible. The reasons for the degree of

blinding adopted, as well as steps taken to minimize bias by other

means, should be explained in the protocol. For example, the sponsor

should have adequate standard operating procedures to ensure that

access to the treatment code is appropriately restricted during the

process of cleaning the database prior to its release for analysis.

Breaking the blind (for a single subject) should be considered

only when knowledge of the treatment assignment is deemed essential

by the subject's physician for the subject's care. Any intentional

or unintentional breaking of the blind should be reported and

explained at the end of the trial,

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irrespective of the reason for its occurrence. The procedure and

timing for revealing the treatment assignments should be documented.

In this document, the blind review (see Glossary) of data refers

to the checking of data during the period of time between trial

completion (the last observation on the last subject) and the

breaking of the blind.

2.3.2 Randomization

Randomization introduces a deliberate element of chance into the

assignment of treatments to subjects in a clinical trial. During

subsequent analysis of the trial data, it provides a sound

statistical basis for the quantitative evaluation of the evidence

relating to treatment effects. It also tends to produce treatment

groups in which the distributions of prognostic factors, known and

unknown, are similar. In combination with blinding, randomization

helps to avoid possible bias in the selection and allocation of

subjects arising from the predictability of treatment assignments.

The randomization schedule of a clinical trial documents the

random allocation of treatments to subjects. In the simplest

situation it is a sequential list of treatments (or treatment

sequences in a crossover trial) or corresponding codes by subject

number. The logistics of some trials, such as those with a screening

phase, may make matters more complicated, but the unique preplanned

assignment of treatment, or treatment sequence, to subject should be

clear. Different trial designs will necessitate different procedures

for generating randomization schedules. The randomization schedule

should be reproducible (if the need arises).

Although unrestricted randomization is an acceptable approach,

some advantages can generally be gained by randomizing subjects in

blocks. This helps to increase the comparability of the treatment

groups, particularly when subject characteristics may change over

time, as a result, for example, of changes in recruitment policy. It

also provides a better guarantee that the treatment groups will be

of nearly equal size. In crossover trials, it provides the means of

obtaining balanced designs with their greater efficiency and easier

interpretation. Care should be taken to choose block lengths that

are sufficiently short to limit possible imbalance, but that are

long enough to avoid predictability towards the end of the sequence

in a block. Investigators and other relevant staff should generally

be blind to the block length; the use of two or more block lengths,

randomly selected for each block, can achieve the same purpose.

(Theoretically, in a double-blind trial predictability does not

matter, but the pharmacological effects of drugs may provide the

opportunity for intelligent guesswork.)

In multicenter trials (see Glossary), the randomization

procedures should be organized centrally. It is advisable to have a

separate random scheme for each center, i.e., to stratify by center

or to allocate several whole blocks to each center. More generally,

stratification by important prognostic factors measured at baseline

(e.g., severity of disease, age, sex) may sometimes be valuable in

order to promote balanced allocation within strata; this has greater

potential benefit in small trials. The use of more than two or three

stratification factors is rarely necessary, is less successful at

achieving balance, and is logistically troublesome. The use of a

dynamic allocation procedure (see below) may help to achieve balance

across a number of stratification factors simultaneously, provided

the rest of the trial procedures can be adjusted to accommodate an

approach of this type. Factors on which randomization has been

stratified should be accounted for later in the analysis.

The next subject to be randomized into a trial should always

receive the treatment corresponding to the next free number in the

appropriate randomization schedule (in the respective stratum, if

randomization is stratified). The appropriate number and associated

treatment for the next subject should only be allocated when entry

of that subject to the randomized part of the trial has been

confirmed. Details of the randomization that facilitate

predictability (e.g., block length) should not be contained in the

trial protocol. The randomization schedule itself should be filed

securely by the sponsor or an independent party in a manner that

ensures that blindness is properly maintained throughout the trial.

Access to the randomization schedule during the trial should take

into account the possibility that, in an emergency, the blind may

have to be broken for any subject. The procedure to be followed, the

necessary documentation, and the subsequent treatment and assessment

of the subject should all be described in the protocol.

Dynamic allocation is an alternative procedure in which the

allocation of treatment to a subject is influenced by the current

balance of allocated treatments and, in a stratified trial, by the

stratum to which the subject belongs and the balance within that

stratum. Deterministic dynamic allocation procedures should be

avoided and an appropriate element of randomization should be

incorporated for each treatment allocation. Every effort should be

made to retain the double-blind status of the trial. For example,

knowledge of the treatment code may be restricted to a central trial

office from where the dynamic allocation is controlled, generally

through telephone contact. This in turn permits additional checks of

eligibility criteria and establishes entry into the trial, features

that can be valuable in certain types of multicenter trials. The

usual system of prepacking and labeling drug supplies for double-

blind trials can then be followed, but the order of their use is no

longer sequential. It is desirable to use appropriate computer

algorithms to keep personnel at the central trial office blind to

the treatment code. The complexity of the logistics and potential

impact on the analysis should be carefully evaluated when

considering dynamic allocation.

III. Trial Design Considerations

3.1 Design Configuration

3.1.1 Parallel Group Design

The most common clinical trial design for confirmatory trials is

the parallel group design in which subjects are randomized to one of

two or more arms, each arm being allocated a different treatment.

These treatments will include the investigational product at one or

more doses, and one or more control treatments, such as placebo and/

or an active comparator. The assumptions underlying this design are

less complex than for most other designs. However, as with other

designs, there may be additional features of the trial that

complicate the analysis and interpretation (e.g., covariates,

repeated measurements over time, interactions between design

factors, protocol violations, dropouts (see Glossary), and

withdrawals).

3.1.2 Crossover Design

In the crossover design, each subject is randomized to a

sequence of two or more treatments and hence acts as his own control

for treatment comparisons. This simple maneuver is attractive

primarily because it reduces the number of subjects and usually the

number of assessments needed to achieve a specific power, sometimes

to a marked extent. In the simplest 2 2 crossover design, each

subject receives each of two treatments in randomized order in two

successive treatment periods, often separated by a washout period.

The most common extension of this entails comparing n(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 2 2 design, the carryover

effect cannot be statistically distinguished from the interaction

between treatment and period and the test for either of these

effects lacks power because the corresponding contrast is ``between

subject.'' This problem is less acute in higher order designs, but

cannot be entirely dismissed.

When the crossover design is used, it is therefore important to

avoid carryover. This is best done by selective and careful use of

the design on the basis of adequate knowledge of both the disease

area and the new medication. The disease under study should be

chronic and stable. The relevant effects of the medication should

develop fully within the treatment period. The washout periods

should be sufficiently long for complete reversibility of drug

effect. The fact that these conditions are likely to be met should

be established in advance of the trial by means of prior information

and data.

There are additional problems that need careful attention in

crossover trials. The most notable of these are the complications of

analysis and interpretation arising from the loss of subjects. Also,

the potential for carryover leads to difficulties in assigning

adverse events that occur in later treatment periods to the

appropriate treatment. These and other issues are described in ICH

E4. The crossover design should generally be restricted to

situations where losses of

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subjects from the trial are expected to be small.

A common, and generally satisfactory, use of the 2 2 crossover

design is to demonstrate the bioequivalence of two formulations of

the same medication. In this particular application in healthy

volunteers, carryover effects on the relevant pharmacokinetic

variable are most unlikely to occur if the wash-out time between the

two periods is sufficiently long. However, it is still important to

check this assumption during analysis on the basis of the data

obtained, for example, by demonstrating that no drug is detectable

at the start of each period.

3.1.3 Factorial Designs

In a factorial design, two or more treatments are evaluated

simultaneously through the use of varying combinations of the

treatments. The simplest example is the 2 2 factorial design in

which subjects are randomly allocated to one of the four possible

combinations of two treatments, A and B. These are: A alone; B

alone; both A and B; neither A nor B. In many cases, this design is

used for the specific purpose of examining the interaction of A and

B. The statistical test of interaction may lack power to detect an

interaction if the sample size was calculated based on the test for

main effects. This consideration is important when this design is

used for examining the joint effects of A and B, in particular, if

the treatments are likely to be used together.

Another important use of the factorial design is to establish

the dose-response characteristics of the simultaneous use of

treatments C and D, especially when the efficacy of each monotherapy

has been established at some dose in prior trials. A number, m, of

doses of C is selected, usually including a zero dose (placebo), and

a similar number, n, of doses of D. The full design then consists of

m n treatment groups, each receiving a different combination of

doses of C and D. The resulting estimate of the response surface may

then be used to help identify an appropriate combination of doses of

C and D for clinical use (see ICH E4).

In some cases, the 2 2 design may be used to make efficient use

of clinical trial subjects by evaluating the efficacy of the two

treatments with the same number of subjects as would be required to

evaluate the efficacy of either one alone. This strategy has proved

to be particularly valuable for very large mortality trials. The

efficiency and validity of this approach depends upon the absence of

interaction between treatments A and B so that the effects of A and

B on the primary efficacy variables follow an additive model. Hence

the effect of A is virtually identical whether or not it is

additional to the effect of B. As for the crossover trial, evidence

that this condition is likely to be met should be established in

advance of the trial by means of prior information and data.

3.2 Multicenter Trials

Multicenter trials are carried out for two main reasons. First,

a multicenter trial is an accepted way of evaluating a new

medication more efficiently. Under some circumstances, it may

present the only practical means of accruing sufficient subjects to

satisfy the trial objective within a reasonable timeframe.

Multicenter trials of this nature may, in principle, be carried out

at any stage of clinical development. They may have several centers

with a large number of subjects per center or, in the case of a rare

disease, they may have a large number of centers with very few

subjects per center.

Second, a trial may be designed as a multicenter (and multi-

investigator) trial primarily to provide a better basis for the

subsequent generalization of its findings. This arises from the

possibility of recruiting the subjects from a wider population and

of administering the medication in a broader range of clinical

settings, thus presenting an experimental situation that is more

typical of future use. In this case, the involvement of a number of

investigators also gives the potential for a wider range of clinical

judgment concerning the value of the medication. Such a trial would

be a confirmatory trial in the later phases of drug development and

would be likely to involve a large number of investigators and

centers. It might sometimes be conducted in a number of different

countries to facilitate generalizability (see Glossary) even

further.

If a multicenter trial is to be meaningfully interpreted and

extrapolated, then the manner in which the protocol is implemented

should be clear and similar at all centers. Furthermore, the usual

sample size and power calculations depend upon the assumption that

the differences between the compared treatments in the centers are

unbiased estimates of the same quantity. It is important to design

the common protocol and to conduct the trial with this background in

mind. Procedures should be standardized as completely as possible.

Variation of evaluation criteria and schemes can be reduced by

investigator meetings, by the training of personnel in advance of

the trial, and by careful monitoring during the trial. Good design

should generally aim to achieve the same distribution of subjects to

treatments within each center and good management should maintain

this design objective. Trials that avoid excessive variation in the

numbers of subjects per center and trials that avoid a few very

small centers have advantages if it is later found necessary to take

into account the heterogeneity of the treatment effect from center

to center, because they reduce the differences between different

weighted estimates of the treatment effect. (This point does not

apply to trials in which all centers are very small and in which

center does not feature in the analysis.) Failure to take these

precautions, combined with doubts about the homogeneity of the

results, may, in severe cases, reduce the value of a multicenter

trial to such a degree that it cannot be regarded as giving

convincing evidence for the sponsor's claims.

In the simplest multicenter trial, each investigator will be

responsible for the subjects recruited at one hospital, so that

``center'' is identified uniquely by either investigator or

hospital. In many trials, however, the situation is more complex.

One investigator may recruit subjects from several hospitals; one

investigator may represent a team of clinicians (subinvestigators)

who all recruit subjects from their own clinics at one hospital or

at several associated hospitals. Whenever there is room for doubt

about the definition of center in a statistical model, the

statistical section of the protocol (see section 5.1) should clearly

define the term (e.g., by investigator, location or region) in the

context of the particular trial. In most instances, centers can be

satisfactorily defined through the investigators. (ICH E6 provides

relevant guidance in this respect.) In cases of doubt, the aim

should be to define centers to achieve homogeneity in the important

factors affecting the measurements of the primary variables and the

influence of the treatments. Any rules for combining centers in the

analysis should be justified and specified prospectively in the

protocol where possible, but in any case decisions concerning this

approach should always be taken blind to treatment, for example, at

the time of the blind review.

The statistical model to be adopted for the estimation and

testing of treatment effects should be described in the protocol.

The main treatment effect may be investigated first using a model

that allows for center differences, but does not include a term for

treatment-by-center interaction. If the treatment effect is

homogeneous across centers, the routine inclusion of interaction

terms in the model reduces the efficiency of the test for the main

effects. In the presence of true heterogeneity of treatment effects,

the interpretation of the main treatment effect is controversial.

In some trials, for example, some large mortality trials with

very few subjects per center, there may be no reason to expect the

centers to have any influence on the primary or secondary variables

because they are unlikely to represent influences of clinical

importance. In other trials, it may be recognized from the start

that the limited numbers of subjects per center will make it

impracticable to include the center effects in the statistical

model. In these cases, it is not considered appropriate to include a

term for center in the model, and it is not necessary to stratify

the randomization by center in this situation.

If positive treatment effects are found in a trial with

appreciable numbers of subjects per center, there should generally

be an exploration of the heterogeneity of treatment effects across

centers, as this may affect the generalizability of the conclusions.

Marked heterogeneity may be identified by graphical display of the

results of individual centers or by analytical methods, such as a

significance test of the treatment-by-center interaction. When using

such a statistical significance test, it is important to recognize

that this generally has low power in a trial designed to detect the

main effect of treatment.

If heterogeneity of treatment effects is found, this should be

interpreted with care, and vigorous attempts should be made to find

an explanation in terms of other features of trial management or

subject characteristics. Such an explanation will usually suggest

appropriate further analysis and interpretation. In the absence of

an explanation, heterogeneity of treatment effect, as evidenced, for

example, by marked quantitative interactions (see Glossary) implies

that alternative estimates of the

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treatment effect, giving different weights to the centers, may be

needed to substantiate the robustness of the estimates of treatment

effect. It is even more important to understand the basis of any

heterogeneity characterized by marked qualitative interactions (see

Glossary), and failure to find an explanation may necessitate

further clinical trials before the treatment effect can be reliably

predicted.

Up to this point, the discussion of multicenter trials has been

based on the use of fixed effect models. Mixed models may also be

used to explore the heterogeneity of the treatment effect. These

models consider center and treatment-by-center effects to be random

and are especially relevant when the number of sites is large.

3.3 Type of Comparison

3.3.1 Trials to Show Superiority

Scientifically, efficacy is most convincingly established by

demonstrating superiority to placebo in a placebo-controlled trial,

by showing superiority to an active control treatment, or by

demonstrating a dose-response relationship. This type of trial is

referred to as a ``superiority'' trial (see Glossary). In this

guidance superiority trials are generally assumed, unless explicitly

stated otherwise.

For serious illnesses, when a therapeutic treatment that has

been shown to be efficacious by superiority trial(s) exists, a

placebo-controlled trial may be considered unethical. In that case

the scientifically sound use of an active treatment as a control

should be considered. The appropriateness of placebo control versus

active control should be considered on a trial-by-trial basis.

3.3.2 Trials to Show Equivalence or Noninferiority

In some cases, an investigational product is compared to a

reference treatment without the objective of showing superiority.

This type of trial is divided into two major categories according to

its objective; one is an ``equivalence'' trial (see Glossary) and

the other is a ``noninferiority'' trial (see Glossary).

Bioequivalence trials fall into the former category. In some

situations, clinical equivalence trials are also undertaken for

other regulatory reasons such as demonstrating the clinical

equivalence of a generic product to the marketed product when the

compound is not absorbed and therefore not present in the blood

stream.

Many active control trials are designed to show that the

efficacy of an investigational product is no worse than that of the

active comparator and, hence, fall into the latter category. Another

possibility is a trial in which multiple doses of the

investigational drug are compared with the recommended dose or

multiple doses of the standard drug. The purpose of this design is

simultaneously to show a dose-response relationship for the

investigational product and to compare the investigational product

with the active control.

Active control equivalence or noninferiority trials may also

incorporate a placebo, thus pursuing multiple goals in one trial.

For example, they may establish superiority to placebo and hence

validate the trial design and simultaneously evaluate the degree of

similarity of efficacy and safety to the active comparator. There

are well-known difficulties associated with the use of the active

control equivalence (or noninferiority) trials that do not

incorporate a placebo or do not use multiple doses of the new drug.

These relate to the implicit lack of any measure of internal

validity (in contrast to superiority trials), thus making external

validation necessary. The equivalence (or noninferiority) trial is

not conservative in nature, so that many flaws in the design or

conduct of the trial will tend to bias the results towards a

conclusion of equivalence. For these reasons, the design features of

such trials should receive special attention and their conduct needs

special care. For example, it is especially important to minimize

the incidence of violations of the entry criteria, noncompliance,

withdrawals, losses to follow-up, missing data, and other deviations

from the protocol, and also to minimize their impact on the

subsequent analyses.

Active comparators should be chosen with care. An example of a

suitable active comparator would be a widely used therapy whose

efficacy in the relevant indication has been clearly established and

quantified in well-designed and well-documented superiority trial(s)

and that can be reliably expected to exhibit similar efficacy in the

contemplated active control trial. To this end, the new trial should

have the same important design features (primary variables, the dose

of the active comparator, eligibility criteria, and so on) as the

previously conducted superiority trials in which the active

comparator clearly demonstrated clinically relevant efficacy, taking

into account advances in medical or statistical practice relevant to

the new trial.

It is vital that the protocol of a trial designed to demonstrate

equivalence or noninferiority contain a clear statement that this is

its explicit intention. An equivalence margin should be specified in

the protocol; this margin is the largest difference that can be

judged as being clinically acceptable and should be smaller than

differences observed in superiority trials of the active comparator.

For the active control equivalence trial, both the upper and the

lower equivalence margins are needed, while only the lower margin is

needed for the active control noninferiority trial. The choice of

equivalence margins should be justified clinically.

Statistical analysis is generally based on the use of confidence

intervals (see section 5.5). For equivalence trials, two-sided

confidence intervals should be used. Equivalence is inferred when

the entire confidence interval falls within the equivalence margins.

Operationally, this is equivalent to the method of using two

simultaneous one-sided tests to test the (composite) null hypothesis

that the treatment difference is outside the equivalence margins

versus the (composite) alternative hypothesis that the treatment

difference is within the margins. Because the two null hypotheses

are disjoint, the Type I error is appropriately controlled. For

noninferiority trials, a one-sided interval should be used. The

confidence interval approach has a one-sided hypothesis test

counterpart for testing the null hypothesis that the treatment

difference (investigational product minus control) is equal to the

lower equivalence margin versus the alternative that the treatment

difference is greater than the lower equivalence margin. The choice

of Type I error should be a consideration separate from the use of a

one-sided or two-sided procedure. Sample size calculations should be

based on these methods (see section 3.5).

Concluding equivalence or noninferiority based on observing a

nonsignificant test result of the null hypothesis that there is no

difference between the investigational product and the active

comparator is considered inappropriate.

There are also special issues in the choice of analysis sets.

Subjects who withdraw or drop out of the treatment group or the

comparator group will tend to have a lack of response; hence the

results of using the full analysis set (see Glossary) may be biased

toward demonstrating equivalence (see section 5.2.3).

3.3.3 Trials to Show Dose-Response Relationship

How response is related to the dose of a new investigational

product is a question to which answers may be obtained in all phases

of development and by a variety of approaches (see ICH E4). Dose-

response trials may serve a number of objectives, among which the

following are of particular importance: The confirmation of

efficacy; the investigation of the shape and location of the dose-

response curve; the estimation of an appropriate starting dose; the

identification of optimal strategies for individual dose

adjustments; the determination of a maximal dose beyond which

additional benefit would be unlikely to occur. These objectives

should be addressed using the data collected at a number of doses

under investigation, including a placebo (zero dose) wherever

appropriate. For this purpose, the application of procedures to

estimate the relationship between dose and response, including the

construction of confidence intervals and the use of graphical

methods, is as important as the use of statistical tests. The

hypothesis tests that are used may need to be tailored to the

natural ordering of doses or to particular questions regarding the

shape of the dose-response curve (e.g., monotonicity). The details

of the planned statistical procedures should be given in the

protocol.

3.4 Group Sequential Designs

Group sequential designs are used to facilitate the conduct of

interim analysis (see section 4.5 and Glossary). While group

sequential designs are not the only acceptable types of designs

permitting interim analysis, they are the most commonly applied

because it is more practicable to assess grouped subject outcomes at

periodic intervals during the trial than on a continuous basis as

data from each subject become available. The statistical methods

should be fully specified in advance of the availability of

information on treatment outcomes and subject treatment assignments

(i.e., blind breaking, see section 4.5). An

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independent data monitoring committee (IDMC) (see Glossary) may be

used to review or to conduct the interim analysis of data arising

from a group sequential design (see section 4.6). While the design

has been most widely and successfully used in large, long-term

trials of mortality or major nonfatal endpoints, its use is growing

in other circumstances. In particular, it is recognized that safety

must be monitored in all trials; therefore, the need for formal

procedures to cover early stopping for safety reasons should always

be considered.

3.5 Sample Size

The number of subjects in a clinical trial should always be

large enough to provide a reliable answer to the questions

addressed. This number is usually determined by the primary

objective of the trial. If the sample size is determined on some

other basis, then this should be made clear and justified. For

example, a trial sized on the basis of safety questions or

requirements or important secondary objectives may need larger

numbers of subjects than a trial sized on the basis of the primary

efficacy question (see, for example, ICH E1A).

Using the usual method for determining the appropriate sample

size, the following items should be specified: A primary variable;

the test statistic; the null hypothesis; the alternative

(``working'') hypothesis at the chosen dose(s) (embodying

consideration of the treatment difference to be detected or rejected

at the dose and in the subject population selected); the probability

of erroneously rejecting the null hypothesis (the Type I error) and

the probability of erroneously failing to reject the null hypothesis

(the Type II error); as well as the approach to dealing with

treatment withdrawals and protocol violations. In some instances,

the event rate is of primary interest for evaluating power, and

assumptions should be made to extrapolate from the required number

of events to the eventual sample size for the trial.

The method by which the sample size is calculated should be

given in the protocol, together with the estimates of any quantities

used in the calculations (such as variances, mean values, response

rates, event rates, difference to be detected). The basis of these

estimates should also be given. It is important to investigate the

sensitivity of the sample size estimate to a variety of deviations

from these assumptions and this may be facilitated by providing a

range of sample sizes appropriate for a reasonable range of

deviations from assumptions. In confirmatory trials, assumptions

should normally be based on published data or on the results of

earlier trials. The treatment difference to be detected may be based

on a judgment concerning the minimal effect which has clinical

relevance in the management of patients or on a judgment concerning

the anticipated effect of the new treatment, where this is larger.

Conventionally, the probability of Type I error is set at 5 percent

or less or as dictated by any adjustments made necessary for

multiplicity considerations; the precise choice may be influenced by

the prior plausibility of the hypothesis under test and the desired

impact of the results. The probability of Type II error is

conventionally set at 10 percent to 20 percent. It is in the

sponsor's interest to keep this figure as low as feasible,

especially in the case of trials that are difficult or impossible to

repeat. Alternative values to the conventional levels of Type I and

Type II error may be acceptable or even preferable in some cases.

Sample size calculations should refer to the number of subjects

required for the primary analysis. If this is the ``full analysis

set,'' estimates of the effect size may need to be reduced compared

to the per protocol set (see Glossary). This is to allow for the

dilution of the treatment effect arising from the inclusion of data

from patients who have withdrawn from treatment or whose compliance

is poor. The assumptions about variability may also need to be

revised.

The sample size of an equivalence trial or a noninferiority

trial (see section 3.3.2) should normally be based on the objective

of obtaining a confidence interval for the treatment difference that

shows that the treatments differ at most by a clinically acceptable

difference. When the power of an equivalence trial is assessed at a

true difference of zero, then the sample size necessary to achieve

this power is underestimated if the true difference is not zero.

When the power of a noninferiority trial is assessed at a zero

difference, then the sample size needed to achieve that power will

be underestimated if the effect of the investigational product is

less than that of the active control. The choice of a ``clinically

acceptable'' difference needs justification with respect to its

meaning for future patients, and may be smaller than the

``clinically relevant'' difference referred to above in the context

of superiority trials designed to establish that a difference

exists.

The exact sample size in a group sequential trial cannot be

fixed in advance because it depends upon the play of chance in

combination with the chosen stopping guideline and the true

treatment difference. The design of the stopping guideline should

take into account the consequent distribution of the sample size,

usually embodied in the expected and maximum sample sizes.

When event rates are lower than anticipated or variability is

larger than expected, methods for sample size reestimation are

available without unblinding data or making treatment comparisons

(see section 4.4).

3.6 Data Capture and Processing

The collection of data and transfer of data from the

investigator to the sponsor can take place through a variety of

media, including paper case record forms, remote site monitoring

systems, medical computer systems, and electronic transfer. Whatever

data capture instrument is used, the form and content of the

information collected should be in full accordance with the protocol

and should be established in advance of the conduct of the clinical

trial. It should focus on the data necessary to implement the

planned analysis, including the context information (such as timing

assessments relative to dosing) necessary to confirm protocol

compliance or identify important protocol deviations. ``Missing

values'' should be distinguishable from the ``value zero'' or

``characteristic absent.''

The process of data capture, through to database finalization,

should be carried out in accordance with good clinical practice

(GCP) (see ICH E6, section 5). Specifically, timely and reliable

processes for recording data and rectifying errors and omissions are

necessary to ensure delivery of a quality database and the

achievement of the trial objectives through the implementation of

the planned analysis.

IV. Trial Conduct Considerations

4.1 Trial Monitoring and Interim Analysis

Careful conduct of a clinical trial according to the protocol

has a major impact on the credibility of the results (see ICH E6).

Careful monitoring can ensure that difficulties are noticed early

and their occurrence or recurrence minimized.

There are two distinct types of monitoring that generally

characterize confirmatory clinical trials sponsored by the

pharmaceutical industry. One type of monitoring concerns the

oversight of the quality of the trial, while the other type involves

breaking the blind to make treatment comparisons (i.e., interim

analysis). Both types of trial monitoring, in addition to entailing

different staff responsibilities, involve access to different types

of trial data and information, and thus different principles apply

for the control of potential statistical and operational bias.

For the purpose of overseeing the quality of the trial, the

checks involved in trial monitoring may include whether the protocol

is being followed, the acceptability of data being accrued, the

success of planned accrual targets, the appropriateness of the

design assumptions, success in keeping patients in the trials, and

so on (see sections 4.2 to 4.4). This type of monitoring does not

require access to information on comparative treatment effects nor

unblinding of data and, therefore, has no impact on Type I error.

The monitoring of a trial for this purpose is the responsibility of

the sponsor (see ICH E6) and can be carried out by the sponsor or an

independent group selected by the sponsor. The period for this type

of monitoring usually starts with the selection of the trial sites

and ends with the collection and cleaning of the last subject's

data.

The other type of trial monitoring (interim analysis) involves

the accruing of comparative treatment results. Interim analysis

requires unblinded (i.e., key breaking) access to treatment group

assignment (actual treatment assignment or identification of group

assignment) and comparative treatment group summary information.

Therefore, the protocol (or appropriate amendments prior to a first

analysis) should contain statistical plans for the interim analysis

to prevent certain types of bias. This is discussed in sections 4.5

and 4.6.

4.2 Changes in Inclusion and Exclusion Criteria

Inclusion and exclusion criteria should remain constant, as

specified in the protocol, throughout the period of subject

recruitment.

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Changes may occasionally be appropriate, for example, in long-term

trials, where growing medical knowledge either from outside the

trial or from interim analyses may suggest a change of entry

criteria. Changes may also result from the discovery by monitoring

staff that regular violations of the entry criteria are occurring or

that seriously low recruitment rates are due to over-restrictive

criteria. Changes should be made without breaking the blind and

should always be described by a protocol amendment. This amendment

should cover any statistical consequences, such as sample size

adjustments arising from different event rates, or modifications to

the planned analysis, such as stratifying the analysis according to

modified inclusion/exclusion criteria.

4.3 Accrual Rates

In trials with a long time-scale for the accrual of subjects,

the rate of accrual should be monitored. If it falls appreciably

below the projected level, the reasons should be identified and

remedial actions taken to protect the power of the trial and

alleviate concerns about selective entry and other aspects of

quality. In a multicenter trial, these considerations apply to the

individual centers.

4.4 Sample Size Adjustment

In long-term trials there will usually be an opportunity to

check the assumptions which underlie the original design and sample

size calculations. This may be particularly important if the trial

specifications have been made on preliminary and/or uncertain

information. An interim check conducted on the blinded data may

reveal that overall response variances, event rates or survival

experience are not as anticipated. A revised sample size may then be

calculated using suitably modified assumptions, and should be

justified and documented in a protocol amendment and in the clinical

study report. The steps taken to preserve blindness and the

consequences, if any, for the Type I error and the width of

confidence intervals should be explained. The potential need for re-

estimation of the sample size should be envisaged in the protocol

whenever possible (see section 3.5).

4.5 Interim Analysis and Early Stopping

An interim analysis is any analysis intended to compare

treatment arms with respect to efficacy or safety at any time prior

to formal completion of a trial. Because the number, methods, and

consequences of these comparisons affect the interpretation of the

trial, all interim analyses should be carefully planned in advance

and described in the protocol. Special circumstances may dictate the

need for an interim analysis that was not defined at the start of a

trial. In these cases, a protocol amendment describing the interim

analysis should be completed prior to unblinded access to treatment

comparison data. When an interim analysis is planned with the

intention of deciding whether or not to terminate a trial, this is

usually accomplished by the use of a group sequential design that

employs statistical monitoring schemes as guidelines (see section

3.4). The goal of such an interim analysis is to stop the trial

early if the superiority of the treatment under study is clearly

established, if the demonstration of a relevant treatment difference

has become unlikely, or if unacceptable adverse effects are

apparent. Generally, boundaries for monitoring efficacy require more

evidence to terminate a trial early (i.e., they are more

conservative) than boundaries for monitoring safety. When the trial

design and monitoring objective involve multiple endpoints, then

this aspect of multiplicity may also need to be taken into account.

The protocol should describe the schedule of interim analyses

or, at least, the considerations that will govern its generation,

for example, if flexible alpha spending function approaches are to

be employed. Further details may be given in a protocol amendment

before the time of the first interim analysis. The stopping

guidelines and their properties should be clearly described in the

protocol or amendments. The potential effects of early stopping on

the analysis of other important variables should also be considered.

This material should be written or approved by the data monitoring

committee (see section 4.6), when the trial has one. Deviations from

the planned procedure always bear the potential of invalidating the

trial results. If it becomes necessary to make changes to the trial,

any consequent changes to the statistical procedures should be

specified in an amendment to the protocol at the earliest

opportunity, especially discussing the impact on any analysis and

inferences that such changes may cause. The procedures selected

should always ensure that the overall probability of Type I error is

controlled.

The execution of an interim analysis should be a completely

confidential process because unblinded data and results are

potentially involved. All staff involved in the conduct of the trial

should remain blind to the results of such analyses, because of the

possibility that their attitudes to the trial will be modified and

cause changes in the characteristics of patients to be recruited or

biases in treatment comparisons. This principle may be applied to

all investigator staff and to staff employed by the sponsor except

for those who are directly involved in the execution of the interim

analysis. Investigators should be informed only about the decision

to continue or to discontinue the trial, or to implement

modifications to trial procedures.

Most clinical trials intended to support the efficacy and safety

of an investigational product should proceed to full completion of

planned sample size accrual; trials should be stopped early only for

ethical reasons or if the power is no longer acceptable. However, it

is recognized that drug development plans involve the need for

sponsor access to comparative treatment data for a variety of

reasons, such as planning other trials. It is also recognized that

only a subset of trials will involve the study of serious life-

threatening outcomes or mortality which may need sequential

monitoring of accruing comparative treatment effects for ethical

reasons. In either of these situations, plans for interim

statistical analysis should be in place in the protocol or in

protocol amendments prior to the unblinded access to comparative

treatment data in order to deal with the potential statistical and

operational bias that may be introduced.

For many clinical trials of investigational products, especially

those that have major public health significance, the responsibility

for monitoring comparisons of efficacy and/or safety outcomes should

be assigned to an external independent group, often called an

independent data monitoring committee (IDMC), a data and safety

monitoring board, or a data monitoring committee, whose

responsibilities should be clearly described.

When a sponsor assumes the role of monitoring efficacy or safety

comparisons and therefore has access to unblinded comparative

information, particular care should be taken to protect the

integrity of the trial and to manage and limit appropriately the

sharing of information. The sponsor should ensure and document that

the internal monitoring committee has complied with written standard

operating procedures and that minutes of decisionmaking meetings,

including records of interim results, are maintained.

Any interim analysis that is not planned appropriately (with or

without the consequences of stopping the trial early) may flaw the

results of a trial and possibly weaken confidence in the conclusions

drawn. Therefore, such analyses should be avoided. If unplanned

interim analysis is conducted, the clinical study report should

explain why it was necessary and the degree to which blindness had

to be broken, and provide an assessment of the potential magnitude

of bias introduced and the impact on the interpretation of the

results.

4.6 Role of Independent Data Monitoring Committee (IDMC)(see

sections 1.25 and 5.5.2 of ICH E6)

An IDMC may be established by the sponsor to assess at intervals

the progress of a clinical trial, safety data, and critical efficacy

variables and recommend to the sponsor whether to continue, modify

or terminate a trial. The IDMC should have written operating

procedures and maintain records of all its meetings, including

interim results; these should be available for review when the trial

is complete. The independence of the IDMC is intended to control the

sharing of important comparative information and to protect the

integrity of the clinical trial from adverse impact resulting from

access to trial information. The IDMC is a separate entity from an

institutional review board (IRB) or an independent ethics committee

(IEC), and its composition should include clinical trial scientists

knowledgeable in the appropriate disciplines, including statistics.

When there are sponsor representatives on the IDMC, their role

should be clearly defined in the operating procedures of the

committee (for example, covering whether or not they can vote on key

issues). Since these sponsor staff would have access to unblinded

information, the procedures should also address the control of

dissemination of interim trial results within the sponsor

organization.

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V. Data Analysis Considerations

5.1 Prespecification of the Analysis

When designing a clinical trial, the principal features of the

eventual statistical analysis of the data should be described in the

statistical section of the protocol. This section should include all

the principal features of the proposed confirmatory analysis of the

primary variable(s) and the way in which anticipated analysis

problems will be handled. In the case of exploratory trials, this

section could describe more general principles and directions.

The statistical analysis plan (see Glossary) may be written as a

separate document to be completed after finalizing the protocol. In

this document, a more technical and detailed elaboration of the

principal features stated in the protocol may be included (see

section 7.1). The plan may include detailed procedures for executing

the statistical analysis of the primary and secondary variables and

other data. The plan should be reviewed and possibly updated as a

result of the blind review of the data (see section 7.1 for

definition) and should be finalized before breaking the blind.

Formal records should be kept of when the statistical analysis plan

was finalized as well as when the blind was subsequently broken.

If the blind review suggests changes to the principal features

stated in the protocol, these should be documented in a protocol

amendment. Otherwise, it should suffice to update the statistical

analysis plan with the considerations suggested from the blind

review. Only results from analyses envisaged in the protocol

(including amendments) can be regarded as confirmatory.

In the statistical section of the clinical study report, the

statistical methodology should be clearly described including when

in the clinical trial process methodology decisions were made (see

ICH E3).

5.2 Analysis Sets

The set of subjects whose data are to be included in the main

analyses should be defined in the statistical section of the

protocol. In addition, documentation for all subjects for whom trial

procedures (e.g., run-in period) were initiated may be useful. The

content of this subject documentation depends on detailed features

of the particular trial, but at least demographic and baseline data

on disease status should be collected whenever possible.

If all subjects randomized into a clinical trial satisfied all

entry criteria, followed all trial procedures perfectly with no

losses to followup, and provided complete data records, then the set

of subjects to be included in the analysis would be self-evident.

The design and conduct of a trial should aim to approach this ideal

as closely as possible, but, in practice, it is doubtful if it can

ever be fully achieved. Hence, the statistical section of the

protocol should address anticipated problems prospectively in terms

of how these affect the subjects and data to be analyzed. The

protocol should also specify procedures aimed at minimizing any

anticipated irregularities in study conduct that might impair a

satisfactory analysis, including various types of protocol

violations, withdrawals and missing values. The protocol should

consider ways both to reduce the frequency of such problems and to

handle the problems that do occur in the analysis of data. Possible

amendments to the way in which the analysis will deal with protocol

violations should be identified during the blind review. It is

desirable to identify any important protocol violation with respect

to the time when it occurred, its cause, and its influence on the

trial result. The frequency and type of protocol violations, missing

values, and other problems should be documented in the clinical

study report and their potential influence on the trial results

should be described (see ICH E3).

Decisions concerning the analysis set should be guided by the

following principles: (1) To minimize bias and (2) to avoid

inflation of Type I error.

5.2.1 Full Analysis Set

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

primary analysis should include all randomized subjects. Compliance

with this principle would necessitate complete followup of all

randomized subjects for study outcomes. In practice, this ideal may

be difficult to achieve, for reasons to be described. In this

document, the term ``full analysis set'' is used to describe the

analysis set which is as complete as possible and as close as

possible to the intention-to-treat ideal of including all randomized

subjects. Preservation of the initial randomization in analysis is

important in preventing bias and in providing a secure foundation

for statistical tests. In many clinical trials, the use of the full

analysis set provides a conservative strategy. Under many

circumstances, it may also provide estimates of treatment effects

that are more likely to mirror those observed in subsequent

practice.

There are a limited number of circumstances that might lead to

excluding randomized subjects from the full analysis set, including

the failure to satisfy major entry criteria (eligibility

violations), the failure to take at least one dose of trial

medication, and the lack of any data post randomization. Such

exclusions should always be justified. Subjects who fail to satisfy

an entry criterion may be excluded from the analysis without the

possibility of introducing bias only under the following

circumstances:

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

(ii) The detection of the relevant eligibility violations can be

made completely objectively.

(iii) All subjects receive equal scrutiny for eligibility

violations. (This may be difficult to ensure in an open-label study,

or even in a double-blind study if the data are unblinded prior to

this scrutiny, emphasizing the importance of the blind review.)

(iv) All detected violations of the particular entry criterion

are excluded.

In some situations, it may be reasonable to eliminate from the

set of all randomized subjects any subject who took no trial

medication. The intention-to-treat principle would be preserved

despite the exclusion of these patients provided, for example, that

the decision of whether or not to begin treatment could not be

influenced by knowledge of the assigned treatment. In other

situations it may be necessary to eliminate from the set of all

randomized subjects any subject without data post randomization. No

analysis should be considered complete unless the potential biases

arising from these specific exclusions, or any others, are

addressed.

When the full analysis set of subjects is used, violations of

the protocol that occur after randomization may have an impact on

the data and conclusions, particularly if their occurrence is

related to treatment assignment. In most respects, it is appropriate

to include the data from such subjects in the analysis, consistent

with the intention-to-treat principle. Special problems arise in

connection with subjects withdrawn from treatment after receiving

one or more doses who provide no data after this point, and subjects

otherwise lost to followup, because failure to include these

subjects in the full analysis set may seriously undermine the

approach. Measurements of primary variables made at the time of the

loss to follow-up of a subject for any reason, or subsequently

collected in accordance with the intended schedule of assessments in

the protocol, are valuable in this context; subsequent collection is

especially important in studies where the primary variable is

mortality or serious morbidity. The intention to collect data in

this way should be described in the protocol. Imputation techniques,

ranging from the carrying forward of the last observation to the use

of complex mathematical models, may also be used in an attempt to

compensate for missing data. Other methods employed to ensure the

availability of measurements of primary variables for every subject

in the full analysis set may require some assumptions about the

subjects' outcomes or a simpler choice of outcome (e.g., success/

failure). The use of any of these strategies should be described and

justified in the statistical section of the protocol, and the

assumptions underlying any mathematical models employed should be

clearly explained. It is also important to demonstrate the

robustness of the corresponding results of analysis, especially when

the strategy in question could itself lead to biased estimates of

treatment effects.

Because of the unpredictability of some problems, it may

sometimes be preferable to defer detailed consideration of the

manner of dealing with irregularities until the blind review of the

data at the end of the trial, and, if so, this should be stated in

the protocol.

5.2.2 Per Protocol Set

The ``per protocol'' set of subjects, sometimes described as the

``valid cases,'' the ``efficacy'' sample, or the ``evaluable

subjects'' sample, defines a subset of the subjects in the full

analysis set who are more compliant with the protocol and is

characterized by criteria such as the following:

(i) The completion of a certain prespecified minimal exposure to

the treatment regimen;

(ii) The availability of measurements of the primary

variable(s);

(iii) The absence of any major protocol violations, including

the violation of entry criteria.

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The precise reasons for excluding subjects from the per protocol

set should be fully defined and documented before breaking the blind

in a manner appropriate to the circumstances of the specific trial.

The use of the per protocol set may maximize the opportunity for

a new treatment to show additional efficacy in the analysis, and

most closely reflects the scientific model underlying the protocol.

However, the corresponding test of the hypothesis and estimate of

the treatment effect may or may not be conservative, depending on

the trial. The bias, which may be severe, arises from the fact that

adherence to the study protocol may be related to treatment and

outcome.

The problems that lead to the exclusion of subjects to create

the per protocol set, and other protocol violations, should be fully

identified and summarized. Relevant protocol violations may include

errors in treatment assignment, the use of excluded medication, poor

compliance, loss to followup, and missing data. It is good practice

to assess the pattern of such problems among the treatment groups

with respect to frequency and time to occurrence.

5.2.3 Roles of the Different Analysis Sets

In general, it is advantageous to demonstrate a lack of

sensitivity of the principal trial results to alternative choices of

the set of subjects analyzed. In confirmatory trials, it is usually

appropriate to plan to conduct both an analysis of the full analysis

set and a per protocol analysis, so that any differences between

them can be the subject of explicit discussion and interpretation.

In some cases, it may be desirable to plan further exploration of

the sensitivity of conclusions to the choice of the set of subjects

analyzed. When the full analysis set and the per protocol set lead

to essentially the same conclusions, confidence in the trial results

is increased, bearing in mind, however, that the need to exclude a

substantial proportion of subjects from the per protocol analysis

throws some doubt on the overall validity of the trial.

The full analysis set and the per protocol set play different

roles in superiority trials (which seek to show the investigational

product to be superior) and in equivalence or noninferiority trials

(which seek to show the investigational product to be comparable,

see section 3.3.2). In superiority trials, the full analysis set is

used in the primary analysis (apart from exceptional circumstances)

because it tends to avoid over-optimistic estimates of efficacy

resulting from a per protocol analysis. This is because the

noncompliers included in the full analysis set will generally

diminish the estimated treatment effect. However, in an equivalence

or noninferiority trial, use of the full analysis set is generally

not conservative and its role should be considered very carefully.

5.3 Missing Values and Outliers

Missing values represent a potential source of bias in a

clinical trial. Hence, every effort should be undertaken to fulfill

all the requirements of the protocol concerning the collection and

management of data. In reality, however, there will almost always be

some missing data. A trial may be regarded as valid, nonetheless,

provided the methods of dealing with missing values are sensible,

particularly if those methods are predefined in the protocol.

Definition of methods may be refined by updating this aspect in the

statistical analysis plan during the blind review. Unfortunately, no

universally applicable methods of handling missing values can be

recommended. An investigation should be made concerning the

sensitivity of the results of analysis to the method of handling

missing values, especially if the number of missing values is

substantial.

A similar approach should be adopted to exploring the influence

of outliers, the statistical definition of which is, to some extent,

arbitrary. Clear identification of a particular value as an outlier

is most convincing when justified medically as well as

statistically, and the medical context will then often define the

appropriate action. Any outlier procedure set out in the protocol or

the statistical analysis plan should be such as not to favor any

treatment group a priori. Once again, this aspect of the analysis

can be usefully updated during blind review. If no procedure for

dealing with outliers was foreseen in the trial protocol, one

analysis with the actual values and at least one other analysis

eliminating or reducing the outlier effect should be performed and

differences between their results discussed.

5.4 Data Transformation

The decision to transform key variables prior to analysis is

best made during the design of the trial on the basis of similar

data from earlier clinical trials. Transformations (e.g., square

root, logarithm) should be specified in the protocol and a rationale

provided, especially for the primary variable(s). The general

principles guiding the use of transformations to ensure that the

assumptions underlying the statistical methods are met are to be

found in standard texts; conventions for particular variables have

been developed in a number of specific clinical areas. The decision

on whether and how to transform a variable should be influenced by

the preference for a scale that facilitates clinical interpretation.

Similar considerations apply to other derived variables, such as

the use of change from baseline, percentage change from baseline,

the ``area under the curve'' of repeated measures, or the ratio of

two different variables. Subsequent clinical interpretation should

be carefully considered, and the derivation should be justified in

the protocol. Closely related points are made in section 2.2.2.

5.5 Estimation, Confidence Intervals, and Hypothesis Testing

The statistical section of the protocol should specify the

hypotheses that are to be tested and/or the treatment effects that

are to be estimated in order to satisfy the primary objectives of

the trial. The statistical methods to be used to accomplish these

tasks should be described for the primary (and preferably the

secondary) variables, and the underlying statistical model should be

made clear. Estimates of treatment effects should be accompanied by

confidence intervals, whenever possible, and the way in which these

will be calculated should be identified. A description should be

given of any intentions to use baseline data to improve precision or

to adjust estimates for potential baseline differences, for example,

by means of analysis of covariance.

It is important to clarify whether one- or two-sided tests of

statistical significance will be used and, in particular, to justify

prospectively the use of one-sided tests. If hypothesis tests are

not considered appropriate, then the alternative process for

arriving at statistical conclusions should be given. The issue of

one-sided or two-sided approaches to inference is controversial, and

a diversity of views can be found in the statistical literature. The

approach of setting Type I errors for one-sided tests at half the

conventional Type I error used in two-sided tests is preferable in

regulatory settings. This promotes consistency with the two-sided

confidence intervals that are generally appropriate for estimating

the possible size of the difference between two treatments.

The particular statistical model chosen should reflect the

current state of medical and statistical knowledge about the

variables to be analyzed as well as the statistical design of the

trial. All effects to be fitted in the analysis (for example, in

analysis of variance models) should be fully specified, and the

manner, if any, in which this set of effects might be modified in

response to preliminary results should be explained. The same

considerations apply to the set of covariates fitted in an analysis

of covariance. (See also section 5.7.) In the choice of statistical

methods, due attention should be paid to the statistical

distribution of both primary and secondary variables. When making

this choice (for example between parametric and nonparametric

methods), it is important to bear in mind the need to provide

statistical estimates of the size of treatment effects together with

confidence intervals (in addition to significance tests).

The primary analysis of the primary variable should be clearly

distinguished from supporting analyses of the primary or secondary

variables. Within the statistical section of the protocol or the

statistical analysis plan there should also be an outline of the way

in which data other than the primary and secondary variables will be

summarized and reported. This should include a reference to any

approaches adopted for the purpose of achieving consistency of

analysis across a range of trials, for example, for safety data.

Modeling approaches that incorporate information on known

pharmacological parameters, the extent of protocol compliance for

individual subjects, or other biologically based data may provide

valuable insights into actual or potential efficacy, especially with

regard to estimation of treatment effects. The assumptions

underlying such models should always be clearly identified, and the

limitations of any conclusions should be carefully described.

5.6 Adjustment of Significance and Confidence Levels

When multiplicity is present, the usual frequentist approach to

the analysis of

[[Page 49595]]

clinical trial data may necessitate an adjustment to the Type I

error. Multiplicity may arise, for example, from multiple primary

variables (see section 2.2.2), multiple comparisons of treatments,

repeated evaluation over time, and/or interim analyses (see section

4.5). Methods to avoid or reduce multiplicity are sometimes

preferable when available, such as the identification of the key

primary variable (multiple variables), the choice of a critical

treatment contrast (multiple comparisons), and the use of a summary

measure such as ``area under the curve'' (repeated measures). In

confirmatory analyses, any aspects of multiplicity that remain after

steps of this kind have been taken should be identified in the

protocol; adjustment should always be considered and the details of

any adjustment procedure or an explanation of why adjustment is not

thought to be necessary should be set out in the analysis plan.

5.7 Subgroups, Interactions, and Covariates

The primary variable(s) is often systematically related to other

influences apart from treatment. For example, there may be

relationships to covariates such as age and sex, or there may be

differences between specific subgroups of subjects, such as those

treated at the different centers of a multicenter trial. In some

instances, an adjustment for the influence of covariates or for

subgroup effects is an integral part of the planned analysis and

hence should be set out in the protocol. Pretrial deliberations

should identify those covariates and factors expected to have an

important influence on the primary variable(s), and should consider

how to account for these in the analysis to improve precision and to

compensate for any lack of balance between treatment groups. If one

or more factors are used to stratify the design, it is appropriate

to account for those factors in the analysis. When the potential

value of an adjustment is in doubt, it is often advisable to

nominate the unadjusted analysis as the one for primary attention,

the adjusted analysis being supportive. Special attention should be

paid to center effects and to the role of baseline measurements of

the primary variable. It is not advisable to adjust the main

analyses for covariates measured after randomization because they

may be affected by the treatments.

The treatment effect itself may also vary with subgroup or

covariate--for example, the effect may decrease with age or may be

larger in a particular diagnostic category of subjects. In some

cases such interactions are anticipated or are of particular prior

interest (e.g., geriatrics); hence a subgroup analysis or a

statistical model including interactions is part of the planned

confirmatory analysis. In most cases, however, subgroup or

interaction analyses are exploratory and should be clearly

identified as such; they should explore the uniformity of any

treatment effects found overall. In general, such analyses should

proceed first through the addition of interaction terms to the

statistical model in question, complemented by additional

exploratory analysis within relevant subgroups of subjects, or

within strata defined by the covariates. When exploratory, these

analyses should be interpreted cautiously. Any conclusion of

treatment efficacy (or lack thereof) or safety based solely on

exploratory subgroup analyses is unlikely to be accepted.

5.8 Integrity of Data and Computer Software Validity

The credibility of the numerical results of the analysis depends

on the quality and validity of the methods and software (both

internally and externally written) used both for data management

(data entry, storage, verification, correction, and retrieval) and

for processing the data statistically. Data management activities

should therefore be based on thorough and effective standard

operating procedures. The computer software used for data management

and statistical analysis should be reliable, and documentation of

appropriate software testing procedures should be available.

VI. Evaluation of Safety and Tolerability

6.1 Scope of Evaluation

In all clinical trials, evaluation of safety and tolerability

(see Glossary) constitutes an important element. In early phases

this evaluation is mostly of an exploratory nature and is only

sensitive to frank expressions of toxicity, whereas in later phases

the establishment of the safety and tolerability profile of a drug

can be characterized more fully in larger samples of subjects. Later

phase controlled trials represent an important means of exploring,

in an unbiased manner, any new potential adverse effects, even if

such trials generally lack power in this respect.

Certain trials may be designed with the purpose of making

specific claims about superiority or equivalence with regard to

safety and tolerability compared to another drug or to another dose

of the investigational drug. Such specific claims should be

supported by relevant evidence from confirmatory trials, similar to

that necessary for corresponding efficacy claims.

6.2 Choice of Variables and Data Collection

In any clinical trial, the methods and measurements chosen to

evaluate the safety and tolerability of a drug will depend on a

number of factors, including knowledge of the adverse effects of

closely related drugs, information from nonclinical and earlier

clinical trials and possible consequences of the pharmacodynamic/

pharmacokinetic properties of the particular drug, the mode of

administration, the type of subjects to be studied, and the duration

of the trial. Laboratory tests concerning clinical chemistry and

hematology, vital signs, and clinical adverse events (diseases,

signs, and symptoms) usually form the main body of the safety and

tolerability data. The occurrence of serious adverse events and

treatment discontinuations due to adverse events are particularly

important to register (see ICH E2A and ICH E3).

Furthermore, it is recommended that a consistent methodology be

used for the data collection and evaluation throughout a clinical

trial program to facilitate the combining of data from different

trials. The use of a common adverse event dictionary is particularly

important. This dictionary has a structure that makes it possible to

summarize the adverse event data on three different levels: System-

organ class, preferred term, or included term (see Glossary). The

preferred term is the level on which adverse events usually are

summarized, and preferred terms belonging to the same system-organ

class could then be brought together in the descriptive presentation

of data (see ICH M1).

6.3 Set of Subjects to be Evaluated and Presentation of Data

For the overall safety and tolerability assessment, the set of

subjects to be summarized is usually defined as those subjects who

received at least one dose of the investigational drug. Safety and

tolerability variables should be collected as comprehensively as

possible from these subjects, including type of adverse event,

severity, onset, and duration (see ICH E2B). Additional safety and

tolerability evaluations may be needed in specific subpopulations,

such as females, the elderly (see ICH E7), the severely ill, or

those who have a common concomitant treatment. These evaluations may

need to address more specific issues (see ICH E3).

All safety and tolerability variables will need attention during

evaluation, and the broad approach should be indicated in the

protocol. All adverse events should be reported, whether or not they

are considered to be related to treatment. All available data in the

study population should be accounted for in the evaluation.

Definitions of measurement units and reference ranges of laboratory

variables should be made with care; if different units or different

reference ranges appear in the same trial (e.g., if more than one

laboratory is involved), then measurements should be appropriately

standardized to allow a unified evaluation. Use of a toxicity

grading scale should be prespecified and justified.

The incidence of a certain adverse event is usually expressed in

the form of a proportion relating number of subjects experiencing

events to number of subjects at risk. However, it is not always

self-evident how to assess incidence. For example, depending on the

situation, the number of exposed subjects or the extent of exposure

(in person-years) could be considered for the denominator. Whether

the purpose of the calculation is to estimate a risk or to make a

comparison between treatment groups, it is important that the

definition is given in the protocol. This is especially important if

long-term treatment is planned and a substantial proportion of

treatment withdrawals or deaths are expected. For such situations,

survival analysis methods should be considered and cumulative

adverse event rates calculated in order to avoid the risk of

underestimation.

In situations when there is a substantial background noise of

signs and symptoms (e.g., in psychiatric trials), one should

consider ways for accounting for this in the estimation of risk for

different adverse events. One such method is to make use of the

``treatment emergent'' (see Glossary) concept in which adverse

events are recorded only if they emerge or worsen relative to

pretreatment baseline.

[[Page 49596]]

Other methods to reduce the effect of the background noise may

also be appropriate, such as ignoring adverse events of mild

severity or requiring that an event should have been observed at

repeated visits to qualify for inclusion in the numerator. Such

methods should be explained and justified in the protocol.

6.4 Statistical Evaluation

The investigation of safety and tolerability is a

multidimensional problem. Although some specific adverse effects can

usually be anticipated and specifically monitored for any drug, the

range of possible adverse effects is very large, and new and

unforeseeable effects are always possible. Further, an adverse event

experienced after a protocol violation, such as use of an excluded

medication, may introduce a bias. This background underlies the

statistical difficulties associated with the analytical evaluation

of safety and tolerability of drugs, and means that conclusive

information from confirmatory clinical trials is the exception

rather than the rule.

In most trials, the safety and tolerability implications are

best addressed by applying descriptive statistical methods to the

data, supplemented by calculation of confidence intervals wherever

this aids interpretation. It is also valuable to make use of

graphical presentations in which patterns of adverse events are

displayed both within treatment groups and within subjects.

The calculation of p-values is sometimes useful, either as an

aid to evaluating a specific difference of interest or as a

``flagging'' device applied to a large number of safety and

tolerability variables to highlight differences worthy of further

attention. This is particularly useful for laboratory data, which

otherwise can be difficult to summarize appropriately. It is

recommended that laboratory data be subjected to both a quantitative

analysis, e.g., evaluation of treatment means, and a qualitative

analysis where counting of numbers above or below certain thresholds

are calculated.

If hypothesis tests are used, statistical adjustments for

multiplicity to quantify the Type I error are appropriate, but the

Type II error is usually of more concern. Care should be taken when

interpreting putative statistically significant findings when there

is no multiplicity adjustment.

In the majority of trials, investigators are seeking to

establish that there are no clinically unacceptable differences in

safety and tolerability compared with either a comparator drug or a

placebo. As is the case for noninferiority or equivalence evaluation

of efficacy, the use of confidence intervals is preferred to

hypothesis testing in this situation. In this way, the considerable

imprecision often arising from low frequencies of occurrence is

clearly demonstrated.

6.5 Integrated Summary

The safety and tolerability properties of a drug are commonly

summarized across trials continuously during an investigational

product's development and, in particular, at the time of a marketing

application. The usefulness of this summary, however, is dependent

on adequate and well-controlled individual trials with high data

quality.

The overall usefulness of a drug is always a question of balance

between risk and benefit. In a single trial, such a perspective

could also be considered even if the assessment of risk/benefit

usually is performed in the summary of the entire clinical trial

program. (See section 7.2.2)

For more details on the reporting of safety and tolerability,

see section 12 of ICH E3.

VII. Reporting

7.1 Evaluation and Reporting

As stated in the introduction, the structure and content of

clinical study reports is the subject of ICH E3. That ICH guidance

fully covers the reporting of statistical work, appropriately

integrated with clinical and other material. The current section is

therefore relatively brief.

During the planning phase of a trial, the principal features of

the analysis should have been specified in the protocol as described

in section 5. When the conduct of the trial is over and the data are

assembled and available for preliminary inspection, it is valuable

to carry out the blind review of the planned analysis also described

in section 5. This pre-analysis review, blinded to treatment, should

cover, for example, decisions concerning the exclusion of subjects

or data from the analysis sets, the checking of possible

transformations and definitions of outliers, the addition to the

model of important covariates identified in other recent research,

and the reconsideration of the use of parametric or nonparametric

methods. Decisions made at this time should be described in the

report and should be distinguished from those made after the

statistician has had access to the treatment codes, as blind

decisions will generally introduce less potential for bias.

Statisticians or other staff involved in unblinded interim analysis

should not participate in the blind review or in making

modifications to the statistical analysis plan. When the blinding is

compromised by the possibility that treatment-induced effects may be

apparent in the data, special care will be needed for the blind

review.

Many of the more detailed aspects of presentation and tabulation

should be finalized at or about the time of the blind review so

that, by the time of the actual analysis, full plans exist for all

its aspects including subject selection, data selection and

modification, data summary and tabulation, estimation, and

hypothesis testing. Once data validation is complete, the analysis

should proceed according to the predefined plans; the more these

plans are adhered to, the greater the credibility of the results.

Particular attention should be paid to any differences between the

planned analysis and the actual analysis as described in the

protocol, the protocol amendments, or the updated statistical

analysis plan based on a blind review of data. A careful explanation

should be provided for deviations from the planned analysis.

All subjects who entered the trial should be accounted for in

the report, whether or not they are included in the analysis. All

reasons for exclusion from analysis should be documented; for any

subject included in the full analysis set but not in the per

protocol set, the reasons for exclusion from the latter should also

be documented. Similarly, for all subjects included in an analysis

set, the measurements of all important variables should be accounted

for at all relevant time-points.

The effect of all losses of subjects or data, withdrawals from

treatment, and major protocol violations on the main analyses of the

primary variable(s) should be considered carefully. Subjects lost to

followup, withdrawn from treatment, or with a severe protocol

violation should be identified and a descriptive analysis of them

provided, including the reasons for their loss and its relationship

to treatment and outcome.

Descriptive statistics form an indispensable part of reports.

Suitable tables and/or graphical presentations should illustrate

clearly the important features of the primary and secondary

variables and of key prognostic and demographic variables. The

results of the main analyses relating to the objectives of the trial

should be the subject of particularly careful descriptive

presentation. When reporting the results of significance tests,

precise p-values (e.g., ``p=0.034'') should be reported rather than

making exclusive reference to critical values.

Although the primary goal of the analysis of a clinical trial

should be to answer the questions posed by its main objectives, new

questions based on the observed data may well emerge during the

unblinded analysis. Additional and perhaps complex statistical

analysis may be the consequence. This additional work should be

strictly distinguished in the report from work which was planned in

the protocol.

The play of chance may lead to unforeseen imbalances between the

treatment groups in terms of baseline measurements not predefined as

covariates in the planned analysis but having some prognostic

importance nevertheless. This is best dealt with by showing that an

additional analysis which accounts for these imbalances reaches

essentially the same conclusions as the planned analysis. If this is

not the case, the effect of the imbalances on the conclusions should

be discussed.

In general, sparing use should be made of unplanned analyses.

Such analyses are often carried out when it is thought that the

treatment effect may vary according to some other factor or factors.

An attempt may then be made to identify subgroups of subjects for

whom the effect is particularly beneficial. The potential dangers of

over-interpretation of unplanned subgroup analyses are well known

(see also section 5.7) and should be carefully avoided. Although

similar problems of interpretation arise if a treatment appears to

have no benefit or an adverse effect in a subgroup of subjects, such

possibilities should be properly assessed and should therefore be

reported.

Finally, statistical judgement should be brought to bear on the

analysis, interpretation and presentation of the results of a

clinical trial. To this end, the trial statistician should be a

member of the team responsible for the clinical study report and

should approve the clinical report.

[[Page 49597]]

7.2 Summarizing the Clinical Database

An overall summary and synthesis of the evidence on safety and

efficacy from all the reported clinical trials is required for a

marketing application (expert report in EU, integrated summary

reports in the United States, gaiyou in Japan). This may be

accompanied, when appropriate, by a statistical combination of

results.

Within the summary a number of areas of specific statistical

interest arise: Describing the demography and clinical features of

the population treated during the course of the clinical trial

program; addressing the key questions of efficacy by considering the

results of the relevant (usually controlled) trials and highlighting

the degree to which they reinforce or contradict each other;

summarizing the safety information available from the combined

database of all the trials whose results contribute to the marketing

application; and identifying potential safety issues. During the

design of a clinical program, careful attention should be paid to

the uniform definition and collection of measurements which will

facilitate subsequent interpretation of the series of trials,

particularly if they are likely to be combined across trials. A

common dictionary for recording the details of medication, medical

history and adverse events should be selected and used. A common

definition of the primary and secondary variables is nearly always

worthwhile and is essential for meta-analysis. The manner of

measuring key efficacy variables, the timing of assessments relative

to randomization/entry, the handling of protocol violators and

deviators, and perhaps the definition of prognostic factors should

all be kept compatible unless there are valid reasons not to do so.

Any statistical procedures used to combine data across trials

should be described in detail. Attention should be paid to the

possibility of bias associated with the selection of trials, to the

homogeneity of their results, and to the proper modeling of the

various sources of variation. The sensitivity of conclusions to the

assumptions and selections made should be explored.

7.2.1 Efficacy Data

Individual clinical trials should always be large enough to

satisfy their objectives. Additional valuable information may also

be gained by summarizing a series of clinical trials that address

essentially identical key efficacy questions. The main results of

such a set of trials should be presented in an identical form to

permit comparison, usually in tables or graphs that focus on

estimates plus confidence limits. The use of meta-analytic

techniques to combine these estimates is often a useful addition

because it allows a more precise overall estimate of the size of the

treatment effects to be generated and provides a complete and

concise summary of the results of the trials. Under exceptional

circumstances, a meta-analytic approach may also be the most

appropriate way, or the only way, of providing sufficient overall

evidence of efficacy via an overall hypothesis test. When used for

this purpose, the meta-analysis should have its own prospectively

written protocol.

7.2.2 Safety Data

In summarizing safety data, it is important to examine the

safety database thoroughly for any indications of potential toxicity

and to follow up any indications by looking for an associated

supportive pattern of observations. The combination of the safety

data from all human exposure to the drug provides an important

source of information because its larger sample size provides the

best chance of detecting the rarer adverse events and, perhaps, of

estimating their approximate incidence. However, incidence data from

this database are difficult to evaluate because of the lack of a

comparator group, and data from comparative trials are especially

valuable in overcoming this difficulty. The results from trials

which use a common comparator (placebo or specific active

comparator) should be combined and presented separately for each

comparator providing sufficient data.

All indications of potential toxicity arising from exploration

of the data should be reported. The evaluation of the reality of

these potential adverse effects should take into account the issue

of multiplicity arising from the numerous comparisons made. The

evaluation should also make appropriate use of survival analysis

methods to exploit the potential relationship of the incidence of

adverse events to duration of exposure and/or followup. The risks

associated with identified adverse effects should be appropriately

quantified to allow a proper assessment of the risk/benefit

relationship.

Annex 1 Glossary

Bayesian approaches--Approaches to data analysis that provide a

posterior probability distribution for some parameter (e.g.,

treatment effect), derived from the observed data and a prior

probability distribution for the parameter. The posterior

distribution is then used as the basis for statistical inference.

Bias (statistical and operational)--The systematic tendency of

any factorsassociated with the design, conduct, analysis and

evaluation of the results of a clinical trial to make the estimate

of a treatment effect deviate from its true value. Bias introduced

through deviations in conduct is referred to as ``operational''

bias. The other sources of bias listed above are referred to as

``statistical.''

Blind review--The checking and assessment of data during the

period of time between trial completion (the last observation on the

last subject) and the breaking of the blind, for the purpose of

finalizing the planned analysis.

Content validity--The extent to which a variable (e.g., a rating

scale) measures what it is supposed to measure.

Double dummy--A technique for retaining the blind when

administering supplies in a clinical trial, when the two treatments

cannot be made identical. Supplies are prepared for Treatment A

(active and indistinguishable placebo) and for Treatment B (active

and indistinguishable placebo). Subjects then take two sets of

treatment; either A (active) and B (placebo), or A (placebo) and B

(active).

Dropout--A subject in a clinical trial who for any reason fails

to continue in the trial until the last visit required of him/her by

the study protocol.

Equivalence trial--A trial with the primary objective of showing

that the response to two or more treatments differs by an amount

which is clinically unimportant. This is usually demonstrated by

showing that the true treatment difference is likely to lie between

a lower and an upper equivalence margin of clinically acceptable

differences.

Frequentist methods--Statistical methods, such as significance

tests and confidence intervals, which can be interpreted in terms of

the frequency of certain outcomes occurring in hypothetical repeated

realizations of the same experimental situation.

Full analysis set--The set of subjects that is as close as

possible to the ideal implied by the intention-to-treat principle.

It is derived from the set of all randomized subjects by minimal and

justified elimination of subjects.

Generalizability, generalization--The extent to which the

findings of a clinical trial can be reliably extrapolated from the

subjects who participated in the trial to a broader patient

population and a broader range of clinical settings.

Global assessment variable--A single variable, usually a scale

of ordered categorical ratings, that integrates objective variables

and the investigator's overall impression about the state or change

in state of a subject.

Independent data monitoring committee (IDMC) (data and safety

monitoring board, monitoring committee, data monitoring committee)--

An independent data monitoring committee that may be established by

the sponsor to assess at intervals the progress of a clinical trial,

the safety data, and the critical efficacy endpoints, and to

recommend to the sponsor whether to continue, modify, or stop a

trial.

Intention-to-treat principle--The principle that asserts that

the effect of a treatment policy can be best assessed by evaluating

on the basis of the intention to treat a subject (i.e., the planned

treatment regimen) rather than the actual treatment given. It has

the consequence that subjects allocated to a treatment group should

be followed up, assessed, and analyzed as members of that group

irrespective of their compliance with the planned course of

treatment.

Interaction (qualitative and quantitative)--The situation in

which a treatment contrast (e.g., difference between investigational

product and control) is dependent on another factor (e.g., center).

A quantitative interaction refers to the case where the magnitude of

the contrast differs at the different levels of the factor, whereas

for a qualitative interaction the direction of the contrast differs

for at least one level of the factor.

Interrater reliability--The property of yielding equivalent

results when used by different raters on different occasions.

Intrarater reliability--The property of yielding equivalent

results when used by the same rater on different occasions.

Interim analysis--Any analysis intended to compare treatment

arms with respect to efficacy or safety at any time prior to the

formal completion of a trial.

Meta-analysis--The formal evaluation of the quantitative

evidence from two or more

[[Page 49598]]

trials bearing on the same question. This most commonly involves the

statistical combination of summary statistics from the various

trials, but the term is sometimes also used to refer to the

combination of the raw data.

Multicenter trial--A clinical trial conducted according to a

single protocol but at more than one site and, therefore, carried

out by more than one investigator.

Noninferiority trial--A trial with the primary objective of

showing that the response to the investigational product is not

clinically inferior to a comparative agent (active or placebo

control).

Preferred and included terms--In a hierarchical medical

dictionary, for example, the World Health Organization's Adverse

Reaction Terminology (WHO-Art), the included term is the lowest

level of dictionary term to which the investigator description is

coded. The preferred term is the level of grouping of included terms

typically used in reporting frequency of occurrence. For example,

the investigator text ``Pain in the left arm'' might be coded to the

included term ``Joint pain,'' which is reported at the preferred

term level as ``Arthralgia.''

Per protocol set (valid cases, efficacy sample, evaluable

subjects sample)--The set of data generated by the subset of

subjects who complied with the protocol sufficiently to ensure that

these data would be likely to exhibit the effects of treatment

according to the underlying scientific model. Compliance covers such

considerations as exposure to treatment, availability of

measurements, and absence of major protocol violations.

Safety and tolerability--The safety of a medical product

concerns the medical risk to the subject, usually assessed in a

clinical trial by laboratory tests (including clinical chemistry and

hematology), vital signs, clinical adverse events (diseases, signs

and symptoms), and other special safety tests (e.g.,

electrocardiograms, ophthalmology). The tolerability of the medical

product represents the degree to which overt adverse effects can be

tolerated by the subject.

Statistical analysis plan--A statistical analysis plan is a

document that contains a more technical and detailed elaboration of

the principal features of the analysis described in the protocol,

and includes detailed procedures for executing the statistical

analysis of the primary and secondary variables and other data.

Superiority trial--A trial with the primary objective of showing

that the response to the investigational product is superior to a

comparative agent (active or placebo control).

Surrogate variable--A variable that provides an indirect

measurement of effect in situations where direct measurement of

clinical effect is not feasible or practical.

Treatment effect--An effect attributed to a treatment in a

clinical trial. In most clinical trials, the treatment effect of

interest is a comparison (or contrast) of two or more treatments.

Treatment emergent--An event that emerges during treatment,

having been absent pretreatment, or worsens relative to the

pretreatment state.

Trial statistician--A statistician who has a combination of

education/training and experience sufficient to implement the

principles in this guidance and who is responsible for the

statistical aspects of the trial.

Dated: September 8, 1998.

William K. Hubbard,

Associate Commissioner for Policy Coordination.

[FR Doc. 98-24754 Filed 9-15-98; 8:45 am]

BILLING CODE 4160-01-F