International Conference on Harmonisation; Draft Guideline 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; Draft Guideline 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 draft

guideline entitled ``Statistical Principles for Clinical Trials.'' The

draft guideline was prepared under the auspices of the International

Conference on Harmonisation of Technical Requirements for Registration

of Pharmaceuticals for Human Use (ICH). The draft guideline 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: Written comments by June 23, 1997.

ADDRESSES: Submit written comments on the draft guideline to the

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

12420 Parklawn Dr., rm. 1-23, Rockville, MD 20857. Copies of the draft

guideline 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 draft guideline 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 guideline: Robert T. 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.

On January 17, 1997, the ICH Steering Committee agreed that a draft

guideline entitled ``Statistical Principles for Clinical Trials''

should be made available for public comment. The draft guideline is the

product of the Efficacy Expert Working Group of the ICH. Comments about

this draft will be considered by FDA and the other regulatory agency

members of the Efficacy Expert Working Group.

The draft guideline addresses principles of statistical methodology

applied to clinical trials for marketing applications. The draft

guideline provides recommendations 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 draft

guideline 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 draft guideline 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.

Interested persons may, on or before June 23, 1997, submit to the

Dockets Management Branch (address above) written comments on the draft

guideline. 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

draft guideline 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 draft guideline is available on the

Internet using the World Wide Web (WWW) (http://www.fda.gov/cder/

guidance.htm) or through the CBER home page (http://www.fda.gov/cber/

cberftp.html).

The text of the draft guideline follows:

Statistical Principles for Clinical Trials

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

annex to this guideline.

Table of Contents

I. Introduction

1.1 Background and Purpose

1.2 Scope and Direction

II. Considerations for Overall Clinical Development

2.1 Study Context

2.1.1 Development Plan

2.1.2 Confirmatory Trial

2.1.3 Exploratory Trial

2.2 Study Scope

2.2.1 Population

2.2.2 Primary and Secondary Variables

2.3 Design Techniques to Avoid Bias

2.3.1 Blinding

2.3.2 Randomization

III. Study Design Considerations

3.1 Study Configuration

3.1.1 Parallel Group Design

3.1.2 Cross-Over Design

3.1.3 Factorial Designs

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3.2 Multicenter Trials

3.3 Type of Comparison

3.3.1 Trials to Show Superiority

3.3.2 Trials to Show Equivalence or Non-inferiority

3.3.3 Dose-Response Designs

3.4 Group Sequential Designs

3.5 Sample Size

3.6 Data Capture and Processing

IV. Study Conduct

4.1 Trial Monitoring

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

5.1 Prespecified Analysis Plan

5.2 Analysis Sets

5.2.1 All Randomized Subjects

5.2.2 Per Protocol Subjects

5.2.3 Roles of the All Randomized Subjects Analysis and the

Per Protocol Analysis

5.3 Missing Values and Outliers

5.4 Data Transformation/Modification

5.5 Estimation, Confidence Intervals and Hypothesis Testing

5.6 Adjustment of Type I Error and Confidence Levels

5.7 Subgroups, Interactions and Covariates

5.8 Integrity of Data and Computer Software

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 Single Study versus 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 (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

guideline 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 guideline 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. FDA document entitled ``Guideline

for the Format and Content of the Clinical and Statistical Sections

of New Drug Applications'' (July 1988). Some topics related to

statistical principles and methodology are also embedded within

other ICH guidelines, particularly those listed below. The specific

guideline that contains related text will be identified in various

sections of this document.

E1: 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 guideline 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 late Phase II and Phase III

clinical trials.

1.2 Scope and Direction

The focus of this guideline 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 guideline. Selected principles and

procedures related to data management or clinical trial monitoring

activities are covered in other ICH guidelines and are not addressed

here.

This guideline 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 the ``ICH Guideline for

Good Clinical Practice.'' The involvement of the statistician, in

collaboration with other clinical trial professionals, is to ensure

that statistical principles are applied appropriately in clinical

trials supporting drug development. Thus, the statistician should

have a combination of education/training and experience sufficient

to implement the principles articulated in this guideline.

All important details of the design, conduct, and proposed

analysis of each clinical trial contributing to a marketing

application 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 guideline 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 studies, and selected principles in this

guideline 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 guideline deal with

minimizing bias and maximizing precision. As used in this guideline,

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 deviate from its true value. It is important to identify

potential sources of bias to the extent 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

studies.

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 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

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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, if a variety of analyses of

the data that take into account changing assumptions were to be

performed, the treatment effect and primary conclusions of the trial

would be consistent. 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.

This guideline largely refers to the use of frequentist methods

when discussing hypothesis testing and/or confidence intervals.

However, the use of Bayesian or other approaches may be considered

when the reasons for their use are clear and when the resulting

conclusions are sufficiently robust compared to alternative

assumptions.

II. Considerations for Overall Clinical Development

2.1 Study 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. 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 overview or meta-analysis 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 a controlled trial in which a hypothesis

is 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. Therefore, adherence to their planned design and

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 all other statistical

aspects, such as 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 to

the intended patient population is understood and explained; this

may also influence the number and type 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 that will be used for

confirmatory proof and the aspects that will provide data for

exploratory analysis.

2.2 Study Scope

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 intended users. In these trials, it is generally helpful to

relax the inclusion and exclusion criteria as much as possible

within the target indication, while maintaining sufficient

homogeneity to permit a successful trial to be carried out. 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 subject 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, and especially when treatment is directed at a

chronic rather than an acute process, 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 outcome.

The measure of treatment effect may again be a simple dichotomous

variable (any occurrence during a specified interval), time to first

occurrence, or rate of occurrence (events per time units of

observation), to give a few possibilities. 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

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approaches, such as comparisons of the assessments done at the

beginning and end of the interval of observation, comparison of

slopes calculated from all assessments throughout the interval, or

comparisons of the proportions of subjects exceeding or declining

beyond a prespecified threshold. To avoid multiplicity concerns, 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 relevant,

the validity and reliability of the primary variable should be

described. 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. 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. Another

strategy that may be useful in some situations 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 for multiple comparisons. 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

composite variables are used as primary variables, the individual

components of these variables are often analyzed separately. When a

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

important to address factors such as content validity, inter- and

intrarater reliability, and sensitivity for discriminating different

medical conditions.

In some cases, ``global assessment'' variables 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

effectiveness are well established in many therapeutic areas,

especially psychotropic drugs and nonsteroidal anti-inflammatory

drugs.

Global assessment variables generally have a subjective

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

secondary variable, fuller details should be included in the

protocol with respect to:

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

of the trial;

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

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

to assign him/her to a unique category of the global assessment

scale;

(4) How to uniquely categorize subjects with missing data.If

objective variables are considered by the investigator when making a

global assessment, then those objective variables should be

considered additional primary or, at least, important secondary

variables.

Overall 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 scales 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, if usefulness is used as a primary

variable, it is important to consider specific efficacy and safety

outcomes separately as additional primary variables.

It may sometimes be desirable to use more than one primary

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

basis for marketing approval, to cover the range of effects of the

therapies. The planned manner of interpretation of this type of

evidence should be carefully spelled out. For example, 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 for approval.

The primary hypothesis or hypotheses should be clearly stated with

respect to the primary variables identified and the approach to

testing the hypotheses described. This should include specification

of the statistical parameters being tested (e.g., mean, percentage,

distribution). The effect on the Type I error should be explained

because of the potential for multiple comparison problems (see

section 5.6); 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 success of the trial depends upon demonstrating

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 needs should be carefully considered.

When direct assessment of the clinical benefit to the subject

through observing actual clinical efficacy is not practical,

indirect criteria (surrogate variables) 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 along one particular pathway, 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 status; conversely, there are

cases of treatments conferring clinical benefit without measurable

impact on proposed surrogates. Additionally, 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 the

biological plausibility of the relationship, the demonstration in

epidemiological studies of the prognostic value of the surrogate for

the clinical outcome, and 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.

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 two most important design techniques for avoiding bias in

clinical trials are blinding and randomization, and these should be

a normal feature 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. The protocol should also specify

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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 frequency

of such problems and to handle the problems that do occur in the

analysis of data.

2.3.1 Blinding

Blinding 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 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 is 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; 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 (SOP's) 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 not the subject. 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 in any way (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

because: (1) The treatments may be of a completely different nature,

for example, surgery and drug therapy; (2) 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, so that bioequivalence of the formulations may need to

be established; (3) 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'' 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.

In some clinical trials, although double blinding is planned, it

may be partially compromised by apparent treatment induced effects.

In such cases, blinding may be improved by blinding investigators 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. Also,

under either of these circumstances, 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.

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

only when knowledge of the treatment assignment is deemed essential

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

or unintentional breaking of the blind should be reported and

explained at the end of the trial, irrespective of the reason for

its occurrence. The procedure and timing for revealing the treatment

assignments should be documented.

In this document, the blind review 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. If specific sponsor staff need to be unblinded during this

period to ensure the integrity of the database or the suitability of

statistical assumptions, appropriate SOP's should be developed to

describe how the treatment code will be protected from broader

dissemination.

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 should have different procedures for

generating randomization schedules. The randomization schedule

should be capable of being reproduced (if the need arises). Whenever

possible, this should be accomplished through the use of the same

random number table, or the same computer routine and seed for its

random number generator.

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 cross-over 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 long enough

to avoid predictability towards the end of the sequence in a block.

Investigators 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 often provide the opportunity for intelligent guesswork.)

In multicenter trials, 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, etc.) 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. Where it is

necessary, the use of a dynamic allocation procedure (see below) may

help to achieve balance across all factors simultaneously, provided

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

approach of this type.

The next subject to be randomized into a study 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. These tasks will normally be carried out by staff at the

investigator's center, who will then dispense the relevant blinded

trial supplies. Details of the

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randomization which facilitate predictability (e.g., block length)

should not be contained in the study 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, either partially or completely. 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 randomization 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. 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. Study Design Considerations

3.1 Study 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, there may be

additional features of the design which complicate the analysis and

interpretation (e.g., covariates, repeated measurements over time,

interactions between design factors, protocol violations, dropouts,

and withdrawals).

3.1.2 Cross-Over Design

In the cross-over design, each subject is randomized to a

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

for treatment comparisons. This simple maneuver is attractive

primarily because it reduces the number of subjects and, usually,

the number of assessments needed to achieve a specific power,

sometimes to a marked extent. In the simplest 2x2 cross-over 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.

Cross-over designs have a number of problems which can

invalidate their results. The chief difficulty concerns carryover,

that is, the residual influence of treatments in subsequent

treatment periods. In an additive model, the effect of unequal

carryover will be to bias direct treatment comparisons. In the 2x2

design, the relevant contrast cannot be statistically distinguished

from the interaction between treatment and period, and the test for

either of these lacks power because it is a ``between subject''

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

cannot be entirely dismissed.

Therefore, when the cross-over design is used, it is 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.

A common, and generally satisfactory, use of the 2x2 cross-over

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 rather 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.

There are additional problems that need careful attention in

cross-over 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 the

ICH E4 topic on ``Dose-Response Information to Support Drug

Registration.'' The cross-over design should generally be restricted

to situations where losses of subjects from the trial are expected

to be small.

3.1.3 Factorial Designs

In a factorial design, two or more treatments are evaluated

simultaneously in the same set of subjects through the use of

varying combinations of the treatments. The simplest example is the

2x2 factorial design in which subjects are randomly allocated to one

of the four possible combinations of two treatments, A and B. These

are: A alone; B alone; both A and B; neither A nor B. In many cases

this design is used for the specific purpose of examining the

interaction of A and B. The statistical test of interaction is model

dependent and 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 a combination product, e.g.,

one combining treatments C and D, especially when the efficacy of

each monotherapy has been established at some dose in prior studies.

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 mn 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.

In some cases, the 2x2 design may be used to make efficient use

of clinical trial subjects by evaluating the efficacy of the two

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

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

to be particularly valuable for very large mortality studies. The

efficiency 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 cross-over 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

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

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

would be likely to involve a large number of investigators and

centers.

[[Page 25718]]

It might sometimes be conducted in a number of different countries

to facilitate generalizability 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 study, and by careful monitoring during the study. 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 which avoid excessive variation in the

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

small centers have advantages if it is later found necessary to

examine 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 Guideline 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. It is

sometimes possible to characterize the centers by historical

measures of response to the control treatment or to other standard

treatments, and this information may help to support decisions

concerning the combination of centers for analysis.

The statistical model to be adopted for the comparison of

treatments 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 center by

treatment interaction. In the absence of a true center by treatment

interaction, the routine inclusion of interaction terms in the model

reduces the efficiency of the test for the main effects. In the

presence of a true center by treatment interaction, the

interpretation of the main treatment effect is controversial.

In some studies, for example, some large mortality studies 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 studies, 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 appropriate to include a term for

center in the model, because in this situation randomization is

rarely stratified by center.

If positive treatment effects are found in a trial with

appreciable numbers of subjects per center, there should generally

be a subsequent exploration of treatment by center interaction, as

this may affect the generalizability of the conclusions. Marked

treatment by center interaction may be identified by graphical

display of the results of individual centers or by analytical

methods, such as a significance test of the 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 a treatment by center interaction 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 define the

appropriate further analysis and interpretation. In the absence of

an explanation, marked quantitative interactions imply that

alternative estimates of the treatment effect may be needed, giving

different weights to the centers, in order to substantiate the

robustness of the estimates of treatment effect. It is even more

important to understand the basis of any marked qualitative

interactions, and failure to find an explanation may necessitate

further clinical trials before the treatment effect can be reliably

predicted.

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 section 5.2.3). In this

guideline, 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 the active control should be

considered. The appropriateness of placebo control versus active

control should be considered on a study-by-study 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 and the other is a

``noninferiority'' trial.

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 ``relative potency assay,'' which is a study where

multiple doses of the investigational drug are compared with the

recommended dose or multiple doses of the standard drug.

Active control equivalence or noninferiority trials may also

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

for example, establishing superiority to placebo, thereby validating

the study design and evaluating the degree of similarity of efficacy

and safety to the active comparator. There are well-known

limitations associated with the use of the active control

equivalence (or noninferiority) trials that do not incorporate a

placebo. 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 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.

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 study. To this end, the new trial should

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

of the active comparator, eligibility criteria, etc.) as the

previously conducted superiority trials in which the active

comparator clearly demonstrated clinically relevant efficacy.

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

equivalence or

[[Page 25719]]

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 which can be judged

as being clinically acceptable. For the active control equivalence

trial, both the upper and the lower equivalence margins are needed,

while for the active control non-inferiority trial, only the lower

margin is needed. There should be clinical justification for the

choice of equivalence margins.

Statistical analysis is generally based on the use of confidence

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

1-2 (alpha) confidence limits should be used. Equivalence

is inferred when the entire confidence interval falls within the

equivalence margins. 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 of the equivalence margins

versus the (composite) alternative that the treatment difference is

within the limits. With this method, the Type I error is controlled

at a level of . For noninferiority trials, the one-sided 1-

interval should be used. The confidence interval approach

has a one-sided hypothesis test counterpart 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. Sample size calculations should be based on

these methods (see section 3.5). The choice of should be a

consideration separate from the choice of a one-sided or two-sided

test.

It is inappropriate to conclude 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.

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

analysis of all randomized subjects may be biased toward

demonstrating equivalence (see section 5.2.3).

3.3.3 Dose-Response Designs

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 studies 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 estimation

procedures, including the construction of confidence intervals and

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). 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 independent data monitoring committee (IDMC)

may be used 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, this should be made clear and justified. For example, a

trial sized on the basis of safety questions or requirements may

need larger numbers of subjects than one sized on the basis of

efficacy questions. (See, for example, ICH E1A ``Population

Exposure: The Extent of Population Exposure to Assess Clinical

Safety.'')

When 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 studies, assumptions

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

earlier studies. The treatment difference to be detected may be

based on a judgement concerning the minimal effect that has clinical

relevance in the management of patients or on a judgement concerning

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

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

or less or as dictated by any adjustments made necessary for

multiplicity considerations; the precise choice is 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 20 percent or less; it is in the sponsor's

interest to keep this figure as low as feasible, especially in the

case of studies that are difficult or impossible to repeat.

Sample size calculations should refer to the number of subjects

required for the primary analysis. If this is the ``all randomized

subjects'' set, estimates about the effect size may need to be

reduced compared to the per protocol set. This is due to the

diluting effect of the inclusion of treatment withdrawals. The

assumptions of 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. For equivalence trials, the power is usually assessed at

a true difference of zero but can be underestimated if the true

difference is not zero. For noninferiority trials, the power is

usually assessed at an expected (nonzero) difference, but can be

underestimated if the true difference is less than expected. The

choice of a ``clinically acceptable'' difference needs

justification, 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 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 rule and the true treatment difference. The

design of the stopping rule 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

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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 analysis plan, 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 analysis plan.

IV. Study Conduct

4.1 Trial Monitoring

Careful conduct of a clinical trial according to the protocol

has a major impact on the credibility of the results. 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. Both types of trial monitoring, in addition

to entailing different staff responsibilities, involve access to

different types of study data and information, thus different

principles apply for the control of potential statistical and

operational bias.

One type of monitoring concerns the oversight of the quality of

the trial, including whether the protocol is being followed,

acceptability of data being accrued, success of planned accrual

targets, checking the design assumptions, etc. (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 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 study sites and ends with the collection and

cleaning of the last subject's data.

The other type of trial monitoring involves breaking the blind

to make treatment comparisons. It therefore involves the accruing of

comparative treatment results, which requires that a protocol (or

appropriate amendments prior to a first analysis) contain

statistical plans to prevent certain types of bias. This type of

trial monitoring involves unblinded (i.e., key breaking) access to

treatment group assignment (actual treatment assignment or

identification of group assignment) and comparative treatment group

summary information. This type of monitoring 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. Occasionally, however, changes may be appropriate; in

long-term studies, for example, 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 that

should cover any statistical consequences, such as sample size

adjustments arising from different event rates, or modifications to

the analysis plan, such as stratifying the analysis according to

modified inclusion/exclusion criteria.

4.3 Accrual Rates

In studies 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 allay

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 final

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 reestimation of the

sample size should be envisaged in the protocol whenever possible

(see section 3.5).

4.5 Interim Analysis and Early Stopping

Any analysis intended to compare treatment arms with respect to

efficacy or safety at any time prior to formal completion of a trial

is an interim analysis. 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, or otherwise specified in amendments

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., more conservative) than do boundaries to terminate a trial

for safety reasons. When the trial design and monitoring objective

involve multiple endpoints, then this aspect of multiplicity may

also need to be taken into account.

The schedule of interim analyses, or at least the considerations

which will govern its generation, should be stated in the protocol

or a protocol amendment before the time of the first interim

analysis; as flexible statistical methods are available to conduct

interim analyses according to a variety of needs (early or late in a

trial), the stopping guidelines and their properties should be

clearly stated in the protocol or amendments. This material should

be written or approved by the data monitoring committee, when the

study has one (see section 4.6). Deviations from the planned

procedure always bear the potential of invalidating the study

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 recruitment patterns or biases in treatment

comparisons. This principle applies to the investigators and their

staff and to staff employed by the sponsor that come into contact

with clinic staff or subjects. 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 studies or when 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

[[Page 25721]]

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 the sharing of information. The sponsor

should ensure and document that the internal monitoring committee

has complied with written SOP's and that minutes of decisionmaking

meetings are maintained.

Any interim analysis that is not planned in the protocol or

specified in an amendment to the protocol prior to unblinding the

data (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 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 Guideline 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 its meetings. 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

ethics board, 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.

V. Data Analysis

5.1 Prespecified Analysis Plan

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

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.

Subsequently, a statistical analysis plan may be written as a

separate document. In this document, a more technical and detailed

elaboration of the principal features stated in the protocol may be

included. The statistical analysis plan is usually an internal

document and may include detailed procedures for executing the

statistical analysis. The statistical analysis plan should be

reviewed and possibly updated as a result of the blind review of the

data (see section 7.1 for definition).

If the blind review suggests changes to the principal features

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

amendment. Otherwise, it will 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.

The statistical methodology, including when in the clinical

trial process methodology decisions were made, should be clearly

described in the statistical section of the clinical study report

(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 study

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 any 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 occur in the analysis of data. The blind

review of data to identify possible amendments to the analysis plan

due to the protocol violations should be carried out before

unblinding. 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 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 All Randomized Subjects

The intention-to-treat principle implies that the primary

analysis should include all randomized subjects. In practice, this

ideal may be difficult to achieve, for reasons to be described.

Hence, analysis sets referred to as ``all randomized subjects'' may

not, in fact, include every subject. For example, it is common

practice to exclude from the all randomized set any subject who

failed to take at least one dose of trial medication or any subject

without data post randomization. No analysis is complete unless the

potential biases arising from these exclusions are addressed and can

be reasonably dismissed.

In many clinical trials, the ``all randomized subjects''

approach is conservative and also gives estimates of treatment

effects that are more likely to mirror those observed in subsequent

practice. Randomization prevents biased allocation of subjects to

treatments and provides the foundation of statistical tests. The

problems associated with the analysis of all randomized subjects lie

in the handling of protocol violations and the subtleties that this

can involve.

There are two types of major protocol violations. One is

violation of entry criteria. The second is violation of the protocol

after randomization. Subjects who fail to satisfy an objective entry

criterion measured prior to randomization, but who enter the trial,

may be excluded from analysis without introducing bias into the

treatment comparison, assuming all subjects receive equal scrutiny

for eligibility violations. (This may be difficult to ensure if the

data are unblinded.) Not all entry criteria are sufficiently

objective for this to be done satisfactorily. Reasons for excluding

subjects from the analysis of all randomized subjects should be

justified.

Other problems occur after randomization (error in treatment

assignment, use of excluded medications, poor compliance, loss to

followup, missing data, and other protocol violations). These

problems are especially difficult when their occurrence is related

to treatment assignment. It is good practice to assess the pattern

of such problems with respect to frequency and time to occurrence

among treatment groups. Subjects withdrawn from treatment may

introduce serious bias and, if they have provided no data after

withdrawal, there is no obvious solution. Severe protocol violation,

such as use of excluded medication, may also introduce serious bias

into measurements after such a violation. The necessary inclusion of

such subjects in the analysis may require some redefinition of the

primary variable or some assumptions about the subjects' outcomes.

Measurements of primary variables made at the time of the loss

to followup of a subject for any reason or at the time of a severe

[[Page 25722]]

protocol violation, or subsequently collected in accordance with the

protocol, are valuable in the context of all randomized subjects

analysis. Their use in analysis should be described and justified in

the statistical section of the protocol and their collection

described elsewhere in the protocol. However, the use of imputation

techniques can lead to biased estimates of treatment effects,

particularly when the likelihood of the loss of a subject is related

to treatment or response. Any other methods to be employed to ensure

the availability of measurements of primary variables for every

subject in the all randomized subjects analysis should be described.

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 study and, if so, this should be stated in

the protocol.

5.2.2 Per Protocol Subjects

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 data used in the all

randomized subjects analysis and is characterized by the following

criteria:

(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 where the nature of and reasons for

these protocol violations should be defined and documented before

breaking the blind.

This 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, it may or may

not be conservative, depending on the study, and may be subject to

bias (possibly severe) because the subjects adhering most diligently

to the study protocol may not be representative of the entire study

population.

5.2.3 Roles of the All Randomized Subjects Analysis and the Per

Protocol Analysis

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 all randomized subjects and per

protocol analyses, 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

all randomized subjects and the per protocol analyses come to

essentially the same conclusions, confidence in the study 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 study.

All randomized subjects and per protocol analyses 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 studies, the all randomized

subjects analysis usually tends to avoid the optimistic estimate of

efficacy which may result from a per protocol analysis, since the

noncompliers included in an all randomized subjects analysis will

generally diminish the overall treatment effect. However, in an

equivalence or noninferiority trial, the all randomized subjects

analysis is no longer 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. However, in reality there will almost always be

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

provided the methods of dealing with missing values are sensible,

particularly if those methods are predefined in the analysis plan of

the protocol. Predefinition of methods may be facilitated by

updating this aspect of the 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

should not favor any treatment group a priori. Once again, this

aspect of the analysis plan can be usefully updated during blind

review. If no procedure for dealing with outliers was foreseen in

the study 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/Modification

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 data modifications

sometimes used to create a variable for analysis, 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 modification 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 to satisfy the 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. The plan should also describe any intentions

to use baseline data to improve precision and to adjust estimates

for potential baseline differences, for example, by means of

analysis of covariance. The reporting of precise p-values (e.g.,

``P=0.034'') should be envisaged in the plan, rather than exclusive

reference to critical values (e.g., ``P<0.05''). 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 formal hypothesis tests are not considered

appropriate, then the alternative process for arriving at

statistical conclusions should be given.

The particular statistical model chosen should reflect the

current state of medical and statistical knowledge about the

variables to be analyzed. 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, 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), as this

may influence the choice when there is any doubt about the

appropriateness of the method.

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 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

studies, for example, for safety data.

[[Page 25723]]

5.6 Adjustment of Type I Error and Confidence Levels

When multiplicity is present, the usual frequentist approach to

the analysis of clinical trial data may necessitate an adjustment to

the Type I error. Multiplicity may arise, for example, from multiple

primary variables (see section 2.2.2), multiple comparisons of

treatments, repeated evaluation over time, and/or interim analyses

(see section 4.6). 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), 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 analysis plan and hence

should be set out in the protocol. Prestudy 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. 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, hence a subgroup analysis

or a statistical model including interactions is part of the

confirmatory analysis plan. 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 are unlikely to be accepted.

5.8 Integrity of Data and Computer Software

The credibility of the numerical results of the analysis

depends on the quality and validity of the methods and software 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 SOP's. 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

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 studies 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 studies, 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 studies, 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 study. 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. 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

E2B).

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 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.

Methods to account for situations where there is a substantial

background noise of signs and symptoms (e.g., in psychiatric trials)

should be considered in the estimation of risk for different adverse

events. One such method is to make use of the ``treatment emergent''

concept in which adverse events are recorded only if they emerge or

worsen relative to pretreatment baseline.

Other methods to reduce the background noise may also be

appropriate, such as ignoring adverse events of mild severity or

requiring that an event should have been

[[Page 25724]]

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 confirmatory

information from Phase III 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 quantitate 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 studies, 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 Single Study versus Integrated Summary

The safety and tolerability properties of a drug are commonly

summarized across studies continuously during an investigational

product's development and, in particular, for the submission of a

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

dependent on adequate and well-controlled individual studies 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 7.1.2.)

For more details of safety and tolerability reports, see section

12 of the ICH Guideline E3 on ``Clinical Study Reports: Structure

and Content.''

VII. Reporting

7.1 Evaluation and Reporting

As stated in the introduction, the structure and content of

clinical reports is the subject of ICH Guideline E3. That ICH

guideline 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 preanalysis review, blinded to treatment, should:

(1) Cover decisions concerning the exclusion of subjects or data

from the analysis sets; (2) check possible transformations and

define outliers; (3) add to the model important covariates

identified in other recent research; (4) reconsider 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.

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 set of all randomized subjects 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; a descriptive analysis of the

subjects should be provided, including the reasons for their loss

and the relationship of the loss 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.

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 that 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 analysis plan but having some prognostic

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

subsidiary analysis that 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 subsidiary

analyses. Subsidiary 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 need to 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 study report and should

approve the final report.

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. 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

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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 studies 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 alway

aworthwhile 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 studies 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.

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 without a natural comparator

group, and data from comparative studies are especially valuable in

overcoming this difficulty. The results from studies that 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

All randomized subjects--The analysis set that includes all

subjects who were randomized to treatment, with these subjects

assigned to the treatment group to which they were randomized.

Practical considerations, such as missing data, may lead to some

subjects in this set not being included in the corresponding

analysis.

Analysis plan--The strategy for analysis predefined in the

statistical section of the protocol and/or protocol amendments. The

plan may be elaborated in a separate document (internal to the

sponsor) to cover technical details and procedures for implementing

the statistical analyses. The plan should be reviewed and possibly

updated as a result of the blind review of the data.

Bayesian approaches--Approaches to data analysis that provide a

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

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

probability distribution for the parameter. The posterior

distribution is then used as the basis for statistical inference.

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

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

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

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

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

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

``statistical.''

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

course of the study, but before the breaking of the blind, for the

purpose of finalizing the analysis plan.

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.

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.

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 to 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.

Inter- and intrarater reliability--The level of consistency of a

rater (intra) or a group of raters (inter) in making an assessment

of treatment outcome.

Interim analysis--Any analysis intended to compare treatment

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

formal completion of a trial.

Meta-analysis--The formal evaluation of the quantitative

evidence from two or more trials bearing on the same question. This

most commonly involves the statistical combination of summary

statistics from the various trials, but the term is sometimes used

to refer to the combination of the raw data.

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Multicenter trial--A trial involving two or more study centers,

a common study protocol, and a single analysis plan pooling the data

across all centers.

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, 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.

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.

Dated: April 30, 1997.

William K. Hubbard,

Associate Commissioner for Policy Coordination.

[FR Doc. 97-12139 Filed 5-8-97; 8:45 am]

BILLING CODE 4160-01-F