International Conference on Harmonisation; Choice of Control Group in Clinical Trials

DEPARTMENT OF HEALTH AND HUMAN SERVICES

Food and Drug Administration

[Docket No. 99D-3082]

International Conference on Harmonisation; Choice of Control

Group in Clinical Trials

AGENCY: Food and Drug Administration, HHS.

ACTION: Notice.

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

guidance entitled ``E10 Choice of Control Group in Clinical Trials.''

The draft guidance was prepared under the auspices of the International

Conference on Harmonisation of Technical Requirements for Registration

of Pharmaceuticals for Human Use (ICH). The draft guidance sets forth

general principles that are relevant to all controlled trials and are

especially pertinent to the major clinical trials intended to

demonstrate drug (including biological drug) efficacy. The draft

guidance describes the principal types of control groups and discusses

their appropriateness in particular situations. The draft guidance is

intended to assist sponsors and investigators in the choice of control

groups for clinical trials.

DATES: Written comments by December 23, 1999.

ADDRESSES: Submit written comments on the draft guidance to the Dockets

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

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 Copies of the draft guidance are

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

Evaluation and Research, Food and Drug Administration, 5600 Fishers

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

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

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

Research (CBER), or by calling the CBER Voice Information System at 1-

800-835-4709 or 301-827-1800. Copies may be obtained from CBER's FAX

Information System at 1-888-CBER-FAX or 301-827-3844.

FOR FURTHER INFORMATION CONTACT:

Regarding the guidance: Robert Temple, Center for Drug Evaluation

and Research (HFD-4), Food and Drug Administration, 5600 Fishers Lane,

Rockville, MD 20857, 301-594-6758.

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

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

MD 20857, 301-827-0864.

SUPPLEMENTARY INFORMATION: In recent years, many important initiatives

have been undertaken by regulatory authorities and industry

associations to promote international harmonization of regulatory

requirements. FDA has participated in many meetings designed to enhance

harmonization and is committed to seeking scientifically based

harmonized technical procedures for pharmaceutical development. One of

the goals of harmonization is to identify and then reduce differences

in technical requirements for drug development among regulatory

agencies.

ICH was organized to provide an opportunity for tripartite

harmonization initiatives to be developed with input from both

regulatory and industry representatives. FDA also seeks input from

consumer representatives and others. ICH is concerned with

harmonization of technical requirements for the registration of

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

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

Commission, the European Federation of Pharmaceutical Industries

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

Pharmaceutical Manufacturers Association, the Centers for Drug

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

the Pharmaceutical Research and Manufacturers of America. The ICH

Secretariat, which coordinates the preparation of documentation, is

provided by the International Federation of Pharmaceutical

Manufacturers Associations (IFPMA).

The ICH Steering Committee includes representatives from each of

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

Health Organization, the Canadian Health Protection Branch, and the

European Free Trade Area.

In May 1998, the ICH Steering Committee agreed that a draft

guidance entitled ``E10 Choice of Control Group in Clinical Trials''

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

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

this draft will be considered by FDA and the Efficacy Expert Working

Group.

In accordance with FDA's good guidance practices (62 FR 8961,

February 27, 1997), this document is now being called a guidance,

rather than a guideline.

The draft guidance sets forth general principles that are relevant

to all controlled trials and are especially pertinent to the major

clinical trials intended to demonstrate drug (including biological

drug) efficacy. The draft guidance includes a description of the five

principal types of controls, a discussion of two important purposes of

clinical trials, and an exploration of the critical issue of assay

sensitivity, i.e., whether a trial could have detected a difference

between treatments when there was a difference, a particularly

important issue in noninferiority/equivalence trials. In addition, the

draft guidance presents a detailed description of each type of control

and considers, for each: (1) Its ability to minimize bias, (2) ethical

and practical issues associated with its use, (3) its usefulness and

the quality of inference in particular situations, (4) modifications of

study design or combinations with other controls that can resolve

ethical, practical, or inferential concerns, and (5) its overall

advantages and disadvantages.

This draft guidance represents the agency's current thinking on

the choice of control group in clinical trials. 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 December 23, 1999, submit to

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

draft guidance. 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 guidance and received comments may be seen in the

office above between 9 a.m. and 4 p.m., Monday through Friday. An

electronic version of this guidance is available on the Internet at

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

Web site at ``http://www.fda.gov/cber/publications.htm''.

The text of the draft guidance follows:

[[Page 51768]]

E10 Choice of Control Group in Clinical Trials\1\

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

on the choice of control group in clincal trials. It does not create

or confer any rights for or on any person and does not operate to

bind FDA or the public. An altenative approach may be used if such

approach satisfies the requirements of the applicable statute,

regulations, or both.

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1.0 Introduction

The choice of control group is always a critical decision in

designing a clinical trial. That choice affects the inferences that

can be drawn from the trial, the degree to which bias in conducting

and analyzing the study can be minimized, the types of subjects that

can be recruited and the pace of recruitment, the kind of endpoints

that can be studied, the public credibility of the results, the

acceptability of the results by regulating authorities, and many

other features of the study, its conduct, and its interpretation.

1.1 General Scheme and Purpose of Guidance

The general principles considered in this guidance are relevant

to all controlled trials. They are of especially critical importance

to the major clinical trials carried out during drug development to

demonstrate efficacy. This guidance does not address the regulatory

requirements in any region, but describes what studies using each

design can demonstrate. Although any of the control groups described

and discussed below may be useful and acceptable in studies serving

as the basis for registration in at least some circumstances, they

are not equally appropriate or useful in particular cases. After a

brief description of the five principal kinds of controls (see

section 1.3), a discussion of two important purposes of clinical

trials (see section 1.4), and an exploration of the critical issue

of whether a trial could have detected a difference between

treatments when there was a difference in noninferiority/equivalence

trials (see section 1.5), the guidance will describe each kind of

control group in more detail (see section 2.0-2.5.7) and consider,

for each:

Its ability to minimize bias

Ethical and practical issues associated with its use

Its usefulness and the quality of inference in

particular situations

Modifications of study design or combinations with

other controls that can resolve ethical, practical, or inferential

concerns

Its overall advantages and disadvantages

Several other ICH guidances are particularly relevant to the

choice of control group:

E3: Structure and Content of Clinical Study Reports

E4: Dose-Response Information to Support Drug

Registration

E6: Good Clinical Practice: Consolidated Guideline

E8: General Considerations for Clinical Trials

E9: Statistical Principles for Clinical Trials

In this guidance, the drug terms ``test drug,'' ``study drug,''

and ``investigational drug'' are considered synonymous and are used

interchangeably; similarly, ``active control'' and ``positive

control,'' ``clinical trial'' and ``clinical study,'' ``control''

and ``control group;'' and ``treatment'' and ``drug'' are

essentially equivalent terms.

1.2 Purpose of Control Group

Control groups have one major purpose: to allow discrimination

of patient outcomes (changes in symptoms, signs, or other morbidity)

caused by the test drug from outcomes caused by other factors, such

as the natural progression of the disease, observer or patient

expectations, or other treatment. The control group experience tells

us what would have happened to patients if they had not received the

test treatment (or what would have happened with a different

treatment known to be effective).

If the course of a disease were uniform in a given patient

population, or predictable from patient characteristics such that

outcome could be predicted reliably for any given subject or group

of subjects, results of treatment could simply be compared with the

known outcome without treatment. For example, one could assume that

pain would have persisted for a defined time, blood pressure would

not have changed, depression would have lasted for a defined time,

tumors would have progressed, the mortality after an acute

infarction would have been the same as previously seen. In unusual

cases, the course of illness is in fact predictable in a defined

population and it may be possible to use a similar group of patients

previously studied as a ``historical control'' (see section 1.3.5).

In most situations, however, a concurrent control group is needed

because it is not possible to predict outcome with adequate

accuracy.

A concurrent control group is one chosen from the same

population as the test group and treated in a defined way as part of

the same trial that studies the test drug. The test and control

groups should be similar with regard to all baseline and on-

treatment variables that could influence outcome other than the

study treatment. Failure to achieve this similarity can introduce a

bias into the study. Bias here (and as used in ICH E9) means the

systematic tendency of any aspects of 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.

Randomization and blinding are the two techniques usually used to

prevent such bias and to ensure that the test treatment and control

groups are similar at the start of the study and are treated

similarly in the course of the study (see ICH E9). Whether a trial

design includes these features is a critical determinant of its

quality and persuasiveness.

1.2.1 Randomization

Assurance that subject populations are similar in test and

control groups is best attained by randomly dividing a single sample

population into groups that receive the test or control treatments.

Randomization avoids systematic differences between groups with

respect to variables that could affect outcome. The inability to

eliminate systematic differences is the principal problem of studies

without a concurrent randomized control (see external control

trials, section 1.3.5). Randomization also provides a sound basis

for statistical inference.

1.2.2 Blinding

The groups should not only be similar at baseline, but should

be treated and observed similarly during the trial, except for

receiving the test and control drug. Clinical trials are often

``double-blind'' (or ``double-masked''), meaning that both subjects

and investigators (including analysts of data, sponsors, other

clinical trial personnel) are unaware of each subject's assigned

treatment, to minimize the potential biases resulting from

differences in management, treatment, or assessment of patients, or

interpretation of results that could arise as a result of subject or

investigator knowledge of the assigned treatment. For example:

Subjects on active drug might report more favorable

outcomes because they expect a benefit or might be more likely to

stay in a study if they knew they were on active drug.

Observers might be less likely to identify and report

treatment responses in a no-treatment group or might be more

sensitive to a favorable outcome or adverse event in patients

receiving active drug.

Knowledge of treatment assignment could affect vigor

of attempts to obtain on-study or followup data.

Knowledge of treatment assignment could affect

decisions about whether a subject should remain on treatment or

receive concomitant medications or other ancillary therapy.

Knowledge of treatment assignment could affect

decisions as to whether a given subject's results should be included

in an analysis.

Knowledge of treatment assignment could affect choice

of statistical analysis.

Double-blinding is intended to ensure that subjective assessments

and decisions are not affected by knowledge of treatment assignment.

1.3 Types of Controls

Control groups in clinical trials can be classified on the

basis of two critical attributes: (1) The type of treatment received

and (2) the method of determining who will be in the control group.

The type of treatment may be any of the following four: (1) Placebo,

(2) no treatment, (3) different dose or regimen of the study

treatment, or (4) different active treatment. The principal methods

of determining who will be in the control group are by randomization

or by selection of a control population separate from the population

treated in the trial (external or historical control). This document

categorizes control groups into five types. The first four are

concurrently controlled (the control group and test groups are

chosen from the same population and treated concurrently), usually

with random assignment to treatment, and are distinguished by which

of the types of control treatments listed above are received.

External (historical) control groups, regardless of the comparator

treatment, are considered together as the fifth type because

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of serious concerns about the ability to ensure comparability of

test and control groups in such trials and the ability to minimize

important biases, making this design usable only in exceptional

circumstances.

It is increasingly common to carry out studies that have more

than one kind of control group. Each kind of control is appropriate

in some circumstances, but none is usable or adequate in every

situation. The five kinds of control are:

1.3.1 Placebo Concurrent Control

In a placebo-controlled study, subjects are randomly assigned

to a test treatment or to an identical-appearing inactive treatment.

The treatments may be titrated to effect or tolerance, or may be

given at one or more fixed doses. Such trials are almost always

double-blind, with both subjects and investigator unaware of

treatment assignment. The name of the control suggests that its

purpose is to control for ``placebo'' effect (improvement in a

subject resulting from knowing that he or she is taking a drug), but

that is not its only or major benefit. Rather, the placebo

concurrent control design, by allowing blinding and randomization

and including a group that receives no treatment, controls for all

potential influences on the actual or apparent course of the disease

other than those arising from the pharmacologic action of the test

drug. These influences include spontaneous change (natural history

of the disease), subject or investigator expectations, use of other

therapy, and subjective elements of diagnosis or assessment.

Placebo-controlled trials seek to show a difference between

treatments when they are studying effectiveness, but may also seek

to show lack of difference (of specified size) in evaluating a

safety measurement.

1.3.2 No-Treatment Concurrent Control

In a no-treatment controlled study, subjects are randomly

assigned to test treatment or to no (i.e., absence of) test or

control therapy. The principal difference between this design and a

placebo-controlled trial is that subjects and investigators are not

blind to treatment assignment. Because of the advantages of double-

blind designs, this design is likely to be needed and suitable only

when it is difficult or impossible to double-blind (e.g., medical

versus surgical treatment, treatments with easily recognized

toxicity) and only when there is reasonable confidence that study

endpoints are objective and that the results of the study are

unlikely to be influenced by the factors listed in section 1.2.2.

Note that it is often possible to blind endpoint assessment, even if

the overall trial is not double-blind. This is a valuable approach

and should always be considered in studies that cannot be blinded,

but it does not solve the other problems associated with knowing the

treatment assignment (see section 1.2.2).

1.3.3 Dose-Response Concurrent Control

In a randomized, fixed-dose, dose-response study, subjects are

randomized to one of several fixed-dose groups. Subjects may either

be placed on their fixed dose initially or be raised to that dose

gradually, but the intended comparison is between the groups on

their final dose. Dose-response studies are usually double-blind.

They may include a placebo (zero dose) and/or active control. In a

concentration-controlled trial, treatment groups are titrated to

several fixed-concentration windows; this type of trial is

conceptually similar to a fixed-dose, dose-response trial.

1.3.4 Active (Positive) Concurrent Control

In an active-control (or positive control) study, subjects are

randomly assigned to the test treatment or to an active-control

drug. Such trials are usually double-blind, but this is not always

possible; many oncology studies, for example, are considered

impossible to blind because of different regimens, different routes

of administration (see section 1.3.2) and different toxicities.

Active-control trials can have two distinct objectives with respect

to showing efficacy: (1) To show efficacy of the test drug by

showing it is as good as (equivalent, not inferior to) a known

effective agent or (2) to show efficacy by showing superiority of

the test drug to the active control. They may also be used with the

primary objective of comparing the efficacy/safety of the two drugs

(see section 1.4). When this design is used to show equivalence/

noninferiority or to compare the drugs, it raises the critical

question of whether the trial was capable of distinguishing active

from inactive treatments (see section 1.5).

1.3.5 External Control (Including Historical Control)

An externally controlled study compares a group of subjects

receiving the test treatment with a group of patients external to

the study, rather than to an internal control group consisting of

patients from the same population assigned to a different treatment.

External controls can be a group of patients treated at an earlier

time (historical control) or during the same time period but in

another setting. The external control may be defined (a specific

group of patients) or nondefined (a comparator group based on

general medical knowledge of outcome). Use of this latter comparator

is particularly treacherous (such trials are sometimes called

uncontrolled) because general impressions are so often inaccurate.

Baseline-controlled studies, in which subjects' status on therapy is

compared with status before therapy (e.g., blood pressure, tumor

size), are a variation of this type of control. In this case, the

changes from baseline are often compared to a general impression of

what would have happened without intervention, rather than to a

specific historical experience, although a more defined experience

can also be used.

1.3.6 Multiple-Control Groups

As will be described further below (see section 1.5.1), it is

often possible and advantageous to use more than one kind of control

in a single study, e.g., use of both active drug and placebo.

Similarly, trials can use several doses of test drug and several

doses of active control, with or without placebo. This design may be

useful for active drug comparisons where the relative potency of the

two drugs is not well established, or where the purpose of the trial

is to establish relative potency.

1.4 Purposes of Clinical Trials

Two purposes of clinical trials should be distinguished: (1)

Assessment of the efficacy and/or safety of a treatment and (2)

assessment of the relative (comparative) efficacy, safety, benefit/

risk relationship or utility of two treatments.

1.4.1 Evidence of Efficacy

In some cases, the purpose of a trial is to demonstrate that a

test drug has any clinical effect (or an effect of some specified

size). A study using any of the control types may demonstrate

efficacy of the test drug by showing that it is superior to the

control (placebo, low dose, active drug). An active-control trial

may, in addition, demonstrate efficacy in some cases by showing the

new drug to be similar in efficacy to a known effective therapy. The

known efficacy of the control is then attributed to the new drug.

Clinical studies designed to demonstrate efficacy of a new drug by

showing that it is similar in efficacy to a standard agent have been

called ``equivalence'' trials. Because in this case the finding of

interest is one-sided, these are actually noninferiority trials,

attempting to show that the new drug is not less effective than the

control by more than a defined amount. As the fundamental assumption

of such studies is that showing noninferiority is evidence of

efficacy, the decision to utilize this trial design necessitates

attention to the question of whether the active control can be

relied upon to have an effect in the setting of the trial and

whether, as a result, the trial can be relied on not to find a truly

inferior drug to be noninferior (see section 1.5).

1.4.2 Comparative Efficacy and Safety

In some cases, the focus of the trial is the comparison with

another agent, not the efficacy of the test drug per se. Depending

on the therapeutic area, these trials may be seen as providing

information needed for relative benefit-risk assessment. The active

comparator(s) should be acceptable to the region for which the data

are meant. Depending on the situation, it may not be necessary to

show equivalence or noninferiority; for example, a less effective

drug could have safety advantages and thus be considered useful.

Even though the primary focus of such a trial is the comparison

of treatments rather than demonstration of efficacy, the cautions

described for conducting and interpreting noninferiority trials need

to be taken into account (see section 1.5). The ability of the

comparative trial to detect a difference between treatments when one

exists needs to be established because a trial incapable of

distinguishing between treatments that are in fact different cannot

provide useful comparative information.

In addition, for the comparative trial to be informative

concerning relative benefit and risk, the trial needs to be fair,

i.e., each drug should have an opportunity to perform well. In

practice, an active-control equivalence/noninferiority trial offered

as evidence of efficacy also almost always should provide a fair

comparison with the control, because any

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doubt as to whether the control in the study had its usual effect

would undermine assurance that the trial had assay sensitivity (see

section 1.5). Note that fairness is not an issue when the purpose of

the trial is to show efficacy by demonstrating superiority to the

control (i.e., the trial will show such efficacy even if the

comparator is poorly used; such a trial will not, however, show an

advantage over the control).

Among aspects of study design that could unfairly favor one

treatment group are choice of dose or patient population and

selection and timing of endpoints.

1.4.2.1 Dose. In comparing the test drug with an active

control for the purpose of assessing relative benefit/risk, it is

important to choose an appropriate dose and dose regimen of the

control. In examining the results of a comparison of two drugs, it

is important to consider whether an apparently less effective

control drug has been used at too low a dose or whether the

apparently less well tolerated control drug has been used at too

high a dose. In some cases, to show superior efficacy or safety

convincingly it will be necessary to study several doses of the

control and perhaps of the test agent, unless the dose of test agent

chosen is superior to any dose (or the only recommended dose) of the

control and at least as well tolerated.

1.4.2.2 Patient population. Selection of subjects for an

active-control trial can affect outcome; the population studied

should be carefully considered in evaluating what the trial has

shown. For example, if subjects are drawn from a population of

nonresponders to the standard agents, there would be a bias in favor

of the new agent. The results of such a study could not be

generalized to the entire population of previously untreated

patients. The result is, however, still good evidence of the

efficacy of the new drug. Moreover, a formal study of a new drug in

nonresponders to other therapy, in which treatment failures are

randomized to either the new or failed therapy (so long as this does

not place the patients at risk), can provide an excellent

demonstration of the value of the new agent in such nonresponders, a

clinically valuable observation (see appendix).

Similarly, it is sometimes possible to identify patient subsets

more or less likely to have a favorable response or to have an

adverse response to a particular drug. For example, blacks respond

poorly to the blood pressure effects of beta blockers and

angiotensin-converting enzyme inhibitors, so that a comparison of a

new antihypertensive with these drugs in these patients would tend

to show superiority of the new drug. It would not be appropriate to

conclude that the new drug is generally superior. Again, however, a

planned study in a subgroup, with recognition of its limitations and

of what conclusion can properly be drawn, could be informative. See

the appendix for a general discussion of ``enrichment'' study

designs, studies that choose a subset of the overall population to

increase sensitivity of the study or to answer a specific, but

narrow, question.

1.4.2.3 Selection and timing of endpoints. When two treatments

are used for the same disease or condition, they may differentially

affect various outcomes of interest in that disease, particularly if

they represent different classes or modalities of therapy.

Therefore, when comparing them in a clinical trial, the choice and

timing of endpoints may favor one therapy or the other. For example,

thrombolytics in patients with acute myocardial infarction can

reduce mortality but increase stroke risk. If a new, more active

thrombolytic were compared with an older thrombolytic, the more

active drug might look better if the endpoint were mortality, but

worse if the endpoint were a composite of mortality and disabling

stroke. Similarly, in comparing two analgesics in the management of

dental pain, assigning a particularly heavy weight to pain at early

time points would favor the agent with more rapid onset over an

agent that provides greater or longer lasting relief.

1.5 Sensitivity-to-Drug-Effects and Assay Sensitivity of Studies

Intended to Show Noninferiority/Equivalence

As noted in section 1.4.1, use of an active-control

noninferiority/equivalence design to demonstrate efficacy poses a

particular problem, one not found in trials intended to show a

difference between treatments. A demonstration of efficacy by

showing noninferiority/equivalence of the new therapy to the

established effective treatment or, more accurately, by showing that

the difference between them is no larger than a specified size

(margin), rests on a critical assumption: that if there is a true

difference between the treatments, i.e., if the new drug has a much

smaller effect or no effect, the study would not have concluded

there was no such difference. This assumption, in turn, rests on the

assumption that the active-control drug will have had an effect of a

defined size in the study. If these assumptions are incorrect, an

erroneous conclusion that a drug is effective may be reached because

a trial seeming to support noninferiority will not in fact have done

so.

The ability of a specific trial to detect differences between

treatments if they exist has been called, and is here termed,

``assay sensitivity.'' In the noninferiority trial setting, assay

sensitivity requires that there be an effect of the control drug in

the trial of at least a specified size and that, because of the

presence of that effect, the trial has an ability not to declare

noninferiority of a new drug when the new drug is in fact inferior.

As noted, because the actual effect size of the control in the trial

is not measured, the presence of assay sensitivity must be deduced.

In this document, the term assay sensitivity, a property of a

particular trial, is distinguished from sensitivity-to-drug-effects.

Sensitivity-to-drug-effects is defined as the ability of

appropriately designed and conducted trials in a specific

therapeutic area, using a specific active drug (or other drugs with

similar effects), to reliably show a drug effect of at least a

minimum size under the conditions of the trial. Sensitivity-to-drug-

effects is determined from historical experience; it will usually be

established by a determination that such trials, when adequately

powered, regularly distinguish active drugs from placebo.

Sensitivity-to-drug-effects, established in this way, will imply

that, in a similarly well-designed and conducted noninferiority

trial, there will be an ability not to find an ineffective agent to

be noninferior. Assay sensitivity, in contrast, applies to a

specific trial and requires the actual presence of a control drug

effect and thus the actual ability of the trial not to declare an

inferior drug noninferior. This ability depends on the details of

the design and conduct of a specific trial, as well as the presence

of sensitivity-to-drug-effects.

1.5.1 Need to Ensure Assay Sensitivity in Noninferiority

(Equivalence) Trials; Difference-Showing Versus Noninferiority

Studies

When designing a noninferiority study, study designers need to

consider the fundamental distinction between two kinds of clinical

trials: (1) Those that seek to demonstrate efficacy by showing

superiority of a treatment to a control (superiority trials) and (2)

those that seek to show efficacy by demonstrating that a new

treatment is as good as (not inferior by some specified amount to) a

treatment known to be effective. In the difference-showing trial,

the finding of a difference itself documents the assay sensitivity

of the trial and documents the efficacy of the superior treatment,

so long as the inferior treatment, if an active drug, is known to be

no worse than a placebo. In the noninferiority situation, in

contrast, a finding of noninferiority leaves unanswered the

question: Would the study have led to a conclusion of noninferiority

even if the study drug were inferior? In a noninferiority trial

without a placebo group, there is no internal standard (that is, a

showing of an active drug-placebo difference) to measure/ensure

assay sensitivity. The existence of assay sensitivity of the trial

therefore needs to be deduced or assumed based on past experience

(``historically'') with the control drug, generally from placebo-

controlled trials, establishing the sensitivity-to-drug-effects of

well-designed and conducted trials, together with evidence that the

trial was in fact well conducted.

The question of assay sensitivity, although particularly

critical in noninferiority studies, actually arises in any trial

that fails to detect a difference between treatments, including a

placebo-controlled trial. If a drug fails to show superiority to

placebo, for example, it means either that the drug was ineffective

or that the study was not capable of detecting the effect of the

drug. A straightforward solution to the problem of assay sensitivity

is the three-arm study, including both placebo and a known active

treatment, a study design with several advantages. Such a study

measures effect size (test drug versus placebo) and allows

comparison of test drug and active control in a setting where assay

sensitivity is established by the active control-placebo comparison.

The design is also particularly informative when the test drug and

placebo give similar results in the study. In that case, if the

active control is superior to placebo, the study did have assay

sensitivity and the study provides some evidence that the test drug

has little or no efficacy. On the other hand, if neither drug,

including the known effective active control, can be distinguished

from placebo with

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respect to efficacy, the clinical study lacks assay sensitivity and

does not provide evidence that the drug is ineffective.

1.5.2 Choosing the Noninferiority Margin

As noted earlier, most active-control ``equivalence'' trials

are really noninferiority trials intended to establish the efficacy

of a new drug. Analysis of the results of noninferiority trials is

discussed in the ICH guidances E9 and E3. Briefly, in such a trial,

new and established therapies are compared. Prior to the trial, an

equivalence or noninferiority margin, sometimes called a ``delta,''

is selected. This margin is the degree of inferiority of the test

drug compared to the control that the trial will attempt to exclude

statistically. If the confidence interval for the difference between

the test and control treatments excludes a degree of inferiority of

the test drug as large as, or larger than, the margin, the test drug

can be declared noninferior and thus effective; if the confidence

interval includes a difference as large as the margin, the test drug

cannot be declared noninferior and cannot be considered effective.

The margin chosen for a noninferiority trial cannot be greater

than the smallest effect size that the active drug would be reliably

expected to have compared with placebo in the setting of the planned

trial, but may be smaller based on clinical judgment. If a

difference between active control and new drug favors the control by

as much as or more than that amount, the new drug might have no

effect at all. The margin generally is identified based on past

experience in placebo-controlled trials of adequate design under

conditions similar to those planned for the new trial. Note that

exactly how to calculate the margin is not described in this

document, and there is little published experience on how to do

this. The determination of the margin is based on both statistical

reasoning and clinical judgment, should reflect uncertainties in the

evidence on which the choice is based, and should be suitably

conservative. If this is done properly, a finding that the

confidence interval for the difference between new drug and the

active control excludes a suitably chosen margin could provide

assurance that the drug has an effect greater than zero. In

practice, the margin chosen usually will be smaller than that

suggested by the smallest expected effect size of the active control

because of interest in ensuring that some particular clinically

acceptable effect size (or fraction of the control drug effect) was

maintained. This would also be true in a trial whose primary focus

is the therapeutic equivalence of a test drug and active control

(see section 1.4.2), where it would be usual to seek assurance that

the test and control drug were quite similar, not simply that the

new drug had any effect at all.

The fact that the choice of the margin to be excluded can only

be based on past experience gives the noninferiority trial an

element in common with a historically controlled (externally

controlled) study. This study design is appropriate and reliable

only when the historical estimate of an expected drug effect can be

well supported by reference to the results of previous studies of

the control drug. These studies should lead to the conclusion that

the active control can consistently be distinguished from placebo in

trials of design similar to the proposed trial (patient population,

study size, study endpoints, dose, concomitant therapy, etc.) and

should identify an effect size that represents the smallest effect

that the control can reliably be expected to have. If placebo-

controlled trials of a design similar to the one proposed more than

occasionally show no difference between the proposed active control

and placebo, and this cannot be explained by some characteristic of

the study, only superiority of the test drug would be interpretable.

Note that it is the estimated difference from placebo, not the total

change from baseline, that needs to be used to calculate the

expected effect of the control.

1.5.3 Sensitivity-to-Drug-Effects Is Difficult to Support in Many

Situations

Whether the historically based assurance of sensitivity-to-

drug-effects of a trial is supported in any given case is to some

degree a matter of judgment. There are many conditions, however, in

which drugs considered effective cannot regularly be shown superior

to placebo in well-controlled studies, and one therefore cannot

reliably determine a minimum effect the drug will have in the

setting of a specific trial. Such conditions tend to include those

in which there is substantial improvement and variability in placebo

groups, and/or in which the effects of therapy are small, or

variable, such as depression, anxiety, dementia, angina, symptomatic

congestive heart failure, seasonal allergies, and symptomatic

gastroesophageal reflux disease.

In all these cases, there is no doubt that the standard

treatments are effective because there are many well-controlled

studies of each of these drugs that have shown an effect. Based on

available experience, however, it would be difficult to describe

study conditions in which the drug would reliably have at least a

minimum effect (i.e., conditions in which there is sensitivity-to-

drug-effects) and that, therefore, could be used to identify an

appropriate margin. In some cases, the experience on which the

expectation of sensitivity-to-drug-effects is based may be of

questionable relevance, e.g., if standards of treatment and

diagnosis have changed substantially over time. If someone proposing

to use an active-control noninferiority design cannot provide

acceptable support for the sensitivity-to-drug-effects of the study

with the chosen inferiority margin, a finding of noninferiority

cannot be considered informative with respect to efficacy or to a

showing of clinical comparability/equivalence.

1.5.4 Assay Sensitivity and Study Quality in Noninferiority

Designs

Even where historical experience indicates that studies in a

particular therapeutic area are likely to have sensitivity-to-drug-

effects, this likelihood can be undermined by the particular

circumstances under which the study was conducted. Great attention

therefore needs to be paid to how the trial was designed and

conducted to determine whether it actually did have assay

sensitivity. There are many factors that can reduce a trial's assay

sensitivity, such as:

1. Poor compliance with therapy

2. Poor responsiveness of the study population to drug effects

3. Use of concomitant medication or other treatment that

interferes with the test drug or that reduces the extent of the

potential response

4. A population that tends to improve spontaneously, leaving no

room for further drug-induced improvement

5. Poor diagnostic criteria (patients lacking the disease to be

studied)

6. Inappropriate (insensitive) measures of drug effect

7. Excessive variability of measurements

8. Biased assessment of endpoint because of knowledge that all

patients are receiving a potentially active drug, e.g., a tendency

to read blood pressure responses as greater than they actually are,

reducing the difference between test drug and control

Clinical researchers and trial sponsors intend to perform high

quality studies, and the publication of the Good Clinical Practices

guidance will enhance study quality. Nonetheless, it should be

appreciated that in trials intended to show a difference between

treatments there is a strong imperative to utilize a good study

design and minimize study errors, because trial imperfections

increase the likelihood of failing to show a difference between

treatments when one exists. In placebo-controlled trials, for

example, there is often a withdrawal period to be sure study

subjects actually have the disease for which treatment is intended,

and great care is taken in defining entry criteria to be sure

patients have an appropriate stage of the disease. It is common to

have a single-blind placebo run-in period to discover and eliminate

subjects who recover spontaneously, whose measurements are too

variable, or who are likely to comply poorly with the protocol.

There is close attention to trial conduct, including administration

of the correct treatments to patients, encouraging compliance with

medication use, controlling (or at least recording) concomitant drug

use and other concomitant illness, and use of standard procedures

for measurement (technique, timing, training periods). All of these

efforts will help ensure that an effective drug will be

distinguished from placebo. Nonetheless, in many clinical settings,

despite the strong stimulus and extensive efforts to ensure study

excellence and assay sensitivity, clinical studies are often unable

to reliably distinguish effective drugs from placebo.

In contrast, in trials intended to show that there is not a

difference of a particular size (noninferiority) between two

treatments, there is a much weaker stimulus to engage in many of

these efforts, which help ensure that differences will be detected,

i.e., ensure sensitivity, because failure to show a difference

greater than the margin is the desired outcome of the study.

Although some kinds of study error diminish observed differences

between treatments, it is noted that some kinds of study errors can

increase variance, which would decrease the likelihood of showing

noninferiority by widening the confidence interval so that a

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test drug control difference greater than the margin cannot be

excluded. There would therefore be a strong stimulus in these trials

to reduce variance, which might be caused, for example, by poor

measurement technique. Many errors of the kind described, however,

reduce the observed difference between treatments (and thus assay)

without necessarily increasing variance. They therefore increase the

likelihood that an inferior drug will be found noninferior.

When a noninferiority study is offered as evidence of

effectiveness of a new drug, both the sponsor and regulatory

authority need to pay particularly close attention to study quality.

Whether a given study has assay sensitivity often cannot be

determined, but the known reasons for failure to have such

sensitivity should be monitored. The design and conduct of the study

need to be shown to be similar to studies of the active control that

were successful in the past. To ensure that sensitivity-to-drug-

effects seen in past studies is likely to be present in the new

study, there should be close attention to critical design

characteristics such as the entry criteria and characteristics of

the study population (severity of medical condition, method of

diagnosis), the specific endpoint measured and timing of

assessments, and the use of washout periods to exclude patients

without disease or to exclude patients with spontaneous improvement.

Similarly, aspects of study conduct that could decrease assay

sensitivity should also be examined, including such characteristics

as compliance with therapy, monitoring of concomitant therapy,

enforcement of entry criteria, and prevention of study dropouts.

One other possibility should be considered. Even where a study

seems likely to have sensitivity-to-drug-effects based on prior

studies, the population studied or other aspects of study design or

conduct in a noninferiority study may be so different that results

with the active-control treatment are visibly atypical (e.g., cure

rate in an antibiotic trial that is unusually high or low). In that

case, the results of a noninferiority trial may not be persuasive.

2.0 Detailed Consideration of Types of Control

2.1 Placebo Control

2.1.1 Description (See Section 1.3.1)

In a placebo-controlled study, subjects are assigned, almost

always by randomization, to either a test drug or to a placebo. A

placebo is a ``dummy'' medication that appears as identical as

possible to the investigational or test drug with respect to

physical characteristics such as color, weight, taste and smell, but

that does not contain the test drug. Some trials may study more than

one dose of the test drug or include both an active control and

placebo. In these cases, it may be easier for the investigator to

use more than one placebo (``double-dummy'') than to try to make all

treatments look the same. The use of placebo facilitates, and is

almost always accompanied by, double-blinding (or double-masking).

The difference in measured outcome between the active drug and

placebo groups is the measure of drug effect under the conditions of

the study. Within this general description there is a wide variety

of designs that can be used successfully: Parallel or cross-over

designs (see ICH E9), single fixed dose or titration in the active

drug group, several fixed doses. Several designs meriting special

attention will be described below. Note that not every study that

includes a placebo is a placebo-controlled study. For example, an

active-control study could use a placebo for each drug (double-

dummy) to facilitate blinding; this is still an active-control

trial, not a placebo-controlled trial. A placebo-controlled trial is

one in which treatment with a placebo is compared with treatment

with an active drug.

2.1.2 Ability to Minimize Bias

The placebo-controlled trial, using randomization and blinding,

generally reduces subject and investigator bias maximally, but such

trials are not impervious to blind-breaking through recognition of

pharmacologic effects of one treatment (perhaps a greater concern in

cross-over designs); blinded outcome assessment can enhance bias

reduction in such cases.

2.1.3 Ethical Issues

When a new agent is tested for a condition for which no

effective treatment is known, there is usually no ethical problem

with a study comparing the new agent to placebo. Use of a placebo

control may raise problems of ethics, acceptability, and

feasibility, however, when an effective treatment is available for

the condition under study in a proposed trial. In cases where an

available treatment is known to prevent serious harm, such as death

or irreversible morbidity in the study population, it is generally

inappropriate to use a placebo control. There are occasional

exceptions, however, such as cases in which standard therapy has

toxicity so severe that many patients will refuse therapy.

In other situations, when there is no major health risk

associated with withholding or delay of effective therapy, it is

considered ethical to ask patients to participate in a placebo-

controlled trial, even if they may experience discomfort as a

result, provided the setting is noncoercive and they are fully

informed about available therapies and the consequences of delaying

treatment. Such trials, however, may pose important practical

problems. For example, deferred treatment of pain or other symptoms

may be unacceptable to patients or physicians and they may not want

to participate in such a study. Whether a particular placebo-

controlled trial of a new agent will be acceptable to subjects and

investigators when there is known effective therapy is a matter of

investigator, patient, and institutional review board (IRB)/

independent ethics committee (IEC) judgment, and acceptability may

differ among ICH regions. Acceptability could depend on the specific

design of the study and the patient population chosen, as will be

discussed below (see section 2.1.5).

Whether a particular placebo-controlled trial is ethical may,

in some cases, depend on what is believed to have been clinically

demonstrated and on the particular circumstances of the trial. For

example, a short term placebo-controlled study of a new

antihypertensive agent in patients with mild essential hypertension

and no end-organ disease might be considered generally acceptable,

while a longer study, or one that included sicker patients, probably

would not be.

It should be noted that use of a placebo or no-treatment

control does not imply that the patient does not get any treatment

at all. For instance, in an oncology trial, when no active drug is

approved, patients in both the placebo/no-treatment group and the

test drug group will receive needed palliative treatment, such as

analgesics.

2.1.4 Usefulness of Placebo-Controlled Trials and Quality/Validity

of Inference in Particular Situations

When used to show effectiveness of a treatment, the placebo-

controlled trial is as free of assumptions and need for external

(extra-study) information as it is possible to be. Most trial design

problems and careless errors result in failure to demonstrate a

treatment difference (and thereby establish efficacy), so that the

trial contains built-in incentives for study excellence. Even when

the primary purpose of a trial is comparison of two active agents or

assessment of dose-response, the addition of a placebo provides an

internal standard that enhances the inferences that can be drawn

from the other comparisons.

Placebo-controlled trials also provide the maximum ability to

distinguish adverse effects due to drug from those due to underlying

disease or intercurrent illness. Note that where they are used to

show similarity, for example, to show the absence of an adverse

effect, placebo-controlled trials have the same assay sensitivity

problem as any equivalence or noninferiority trial (see section

1.5.1). To interpret the result, one must know that if the study

drug caused an adverse event, it would have been observed.

2.1.5 Modifications of Design and Combinations With Other Controls

That Can Resolve Ethical, Practical, or Inferential Issues

It is often possible to address the ethical or practical

limitations of placebo-controlled trials by using modified study

designs that still retain the inferential advantages of these

trials. In addition, placebo-controlled trials can be made more

informative by inclusion of additional treatment groups, such as

multiple doses of the test agent or a known active-control

treatment.

2.1.5.1 Additional control groups.

2.1.5.1.1 Three-arm study; placebo and active control. As

noted in section 1.5.1, three-arm studies including an active-

control as well as a placebo-control group can readily assess

whether a failure to distinguish test drug from placebo implies

ineffectiveness of the test drug or simply a study that lacked the

ability to identify an active drug. The placebo-standard drug

comparison in such a trial provides internal evidence of assay

sensitivity. It is possible to make the active groups larger than

the placebo group in order to improve the precision of the active

drug comparison, if this is considered important. This may also make

the study more

[[Page 51773]]

appealing to patients, as there is less chance of being randomized

to placebo.

2.1.5.1.2 Additional doses. Randomization among several fixed

doses of the test drug in addition to placebo allows assessment of

dose-response and may be particularly useful in a comparative trial

to ensure a fair comparison of treatments (see ICH E4: Dose-Response

Information to Support Drug Registration).

2.1.5.1.3 Factorial/combination studies. Factorial/

combination (response-surface) designs may be used to explore

several doses of the investigational drug as monotherapy and in

combination with several doses of another agent proposed for use in

combination with it. A single study of this type can define the

properties of a wide array of combinations. Such studies are common

in the evaluation of new antihypertensive therapies, but can be

considered in a variety of settings where more than one treatment is

used simultaneously. For example, the independent additive effects

of aspirin and streptokinase in preventing mortality after a heart

attack were shown in such a trial.

2.1.5.2 Changes in study design.

2.1.5.2.1 Add-on study, placebo-controlled; replacement study.

An ``add-on'' study is a placebo-controlled trial of a new agent

conducted in people also receiving standard therapy. Such studies

are useful when standard therapy is known to decrease mortality or

irreversible morbidity, so that the therapy cannot be withheld from

a patient population known to benefit from it, and when a

noninferiority trial with standard treatment as the active control

cannot be carried out or would be difficult to interpret (see

section 1.5). It is common to study anticancer, antiepileptic, and

anti-heart-failure drugs this way. This design is useful only when

standard therapy is not fully effective (which, however, is almost

always the case), and it has the advantage of providing evidence of

improved clinical outcomes (rather than ``mere'' noninferiority).

Efficacy is, of course, established by such studies only for

combination therapy, and the dose in a monotherapy situation might

be different from the dose found to be effective in combination. In

general, this approach is likely to succeed only when the new and

standard therapies utilize different pharmacologic mechanisms,

although there are exceptions. For example, AIDS combination

therapies may show a beneficial effect of pharmacologically-related

drugs because of delays in development of resistance.

A variation of this design that can sometimes give information

on monotherapy and that is particularly applicable in the setting of

chronic disease, is the replacement study, in which the new drug or

placebo is added by random assignment to conventional treatment

given at an effective dose and the conventional treatment is then

withdrawn, usually by tapering. The ability to maintain the

subjects' baseline status is then observed in the drug and placebo

groups using predefined success criteria. This approach has been

used to study steroid-sparing substitutions in steroid-dependent

patients without need for initial steroid withdrawal and

recrudescence of symptoms in a wash-out period, and has also been

used to study antiepileptic drug monotherapy.

2.1.5.2.2 ``Early escape''; rescue medication. It is possible

to design a study to plan for ``early escape'' from ineffective

therapy. Early escape refers to prompt removal of subjects whose

clinical status worsens or fails to improve to a defined level

(blood pressure not controlled by a prespecified time, seizure rate

greater than some prescribed value, blood pressure rising to a

certain level, angina frequency above a defined level, liver enzymes

failing to normalize by a preset time in patients with hepatitis),

who have a single event that treatment was intended to prevent

(first recurrence of unstable angina, grand mal seizure, paroxysmal

supraventricular arrhythmia), or who otherwise require added

therapy. In such cases, the need to change therapy becomes a study

endpoint. The criteria for deciding whether these endpoints have

occurred should be well specified, and the timing of measurements

should ensure that patients will not remain untreated with an active

drug while their disease is poorly controlled. The primary

difficulty with this trial design is that it may give information

only on short-term effectiveness. The randomized withdrawal trial

(see section 2.1.5.2.4), however, which can also incorporate early-

escape features, can give information on long-term effectiveness. It

should be noted that formal use of rescue medication in response to

clinical deterioration could be utilized similarly.

2.1.5.2.3 Limited placebo period. In a longer term active-

control trial, the addition of a placebo group treated for a short

period may establish assay sensitivity (at least for short-term

effects). The trial would then continue without the placebo group.

2.1.5.2.4 Randomized withdrawal. In a randomized withdrawal

study, subjects receiving an investigational therapy for a specified

time are randomly assigned to continued treatment with the

investigational therapy or to placebo (i.e., withdrawal of active

therapy). Subjects for such a trial could be derived from an

organized open single-arm study, from an existing clinical cohort

(but usually with a formal ``wash-in'' phase to establish the

initial on-therapy baseline), from the active arm of a controlled

trial, or from one or both arms of an active-control trial. Any

difference that emerges between groups receiving continued treatment

and placebo would demonstrate the effect of the active treatment.

The prerandomization observation period on drug can be of any

length; this approach can therefore be used to study long-term

persistence of effectiveness when long-term placebo treatment would

not be acceptable. The postwithdrawal observation period could be of

fixed duration or could use early escape or time to event (e.g.,

relapse of depression) approaches. As with the early-escape design,

procedures for monitoring patients and assessing study endpoints

need careful attention to ensure that patients failing on an

assigned treatment are identified rapidly.

The randomized withdrawal approach is suitable in several

situations. First, it may be suitable for drugs that appear to

resolve an episode of recurring illness (e.g., antidepressants), in

which case the withdrawal study is in effect a relapse-prevention

study. Second, it may be used for drugs that suppress a symptom or

sign (chronic pain, hypertension, angina), but where a long-term

placebo-controlled trial would be difficult; in this case, the study

can establish long-term efficacy. Third, the design can be used to

determine how long a therapy should be continued (e.g.,

postinfarction treatments with a beta-blocker).

The general advantage of randomized withdrawal designs, when

used with an early-escape endpoint, such as return of symptoms, is

that the period of placebo exposure with poor response that a

patient would have to undergo is short.

Dosing issues can be addressed by this type of design. After

all patients had received an initial fixed dose, they could be

randomly assigned in the ``withdrawal'' phase to several different

doses (as well as placebo), a particularly useful approach when

there is reason to think the initial and maintenance doses might be

different, either on pharmacodynamic grounds or because there is

substantial accumulation of active drug resulting from a long half

life of parent drug or active metabolite. Note that the randomized

withdrawal design could be used to assess dose-response after an

initial placebo-controlled titration study. The titration study is

an efficient design for establishing effectiveness, but does not

give good dose-response information. The randomized withdrawal

phase, with responders randomly assigned to several fixed doses and

placebo, will study dose-response rigorously while allowing the

efficiency of the titration design.

In utilizing randomized withdrawal designs, it is important to

appreciate the possibility of withdrawal phenomena, suggesting the

wisdom of relatively slow tapering. A patient may develop tolerance

to a drug such that no benefit is being accrued, but the drug's

withdrawal may lead to disease exacerbation, resulting in an

erroneous conclusion of persisting efficacy. It is also important to

realize that treatment effects observed in these studies may be

larger than those seen in the general population because randomized

withdrawal studies are ``enriched'' with responders (see appendix).

This phenomenon results when the study explicitly includes only

subjects who appear to have responded to the drug or includes only

people who have completed a previous phase of study (which is often

an indicator of a good response).

2.1.5.2.5 Other design considerations. In any placebo-

controlled study, unbalanced randomization (e.g., 2:1, study drug to

placebo) may enhance the safety data base and may also make the

study more attractive to patients and/or investigators.

2.1.6 Advantages of Placebo-Controlled Trials

2.1.6.1 Ability to demonstrate efficacy credibly. Like other

difference-showing trials, the interpretation of the placebo-

controlled study relies on no externally based

[[Page 51774]]

assumptions of sensitivity-to-drug-effects nor an assessment of

assay sensitivity. These may be the only credible study designs in

situations where it is not possible to conclude that noninferiority

studies would have assay sensitivity (see section 1.5).

2.1.6.2 Measures ``absolute'' effectiveness and safety. The

placebo-controlled trial measures the absolute effect of treatment

and allows a distinction between adverse events due to the drug and

those due to the underlying disease or ``background noise.'' The

absolute effect size information is valuable in a three-group trial

(test, placebo, active), even if the primary purpose of the trial is

the test versus active control comparison.

2.1.6.3 Efficiency. Placebo-controlled trials are efficient in

that they can detect treatment effects with a smaller sample size

than any other type of concurrently controlled study. Active-control

trials intended to show superiority of the new treatment are

generally seeking smaller differences than the active-placebo

difference sought in a placebo-controlled trial, resulting in need

for a larger sample size. Noninferiority active-control trials also

need larger sample sizes because they must use conservative

assumptions about the effect size of the control drug to ensure that

noninferiority of the test drug would in fact demonstrate efficacy.

Designers of dose-response studies need to guess at the shape and

position of the dose-response curve and may wastefully assign some

subjects to several doses that have no effect or are on a response

plateau.

2.1.6.4 Minimizing the effect of subject and investigator

expectations. Use of a blinded placebo control may decrease the

amount of improvement resulting from subject or investigator

expectations because both are aware that some subjects will receive

no active drug. This may increase the ability of the study to detect

true drug effects.

2.1.7 Disadvantages of Placebo-Controlled Trials

2.1.7.1 Ethical concerns (see sections 2.1.3 and 2.1.4). When

effective therapy that is known to prevent harm exists for a

particular population, that population cannot usually be ethically

studied in placebo-controlled trials; the particular conditions and

populations for which this is true may be controversial. Ethical

concerns may also direct studies toward less ill subjects or cause

studies to examine short-term endpoints when long-term outcomes are

of greater interest. Where a placebo-controlled trial is unethical

and an active-control trial would not be credible, it may be very

difficult to study new drugs at all. For example, it would not be

considered ethical to carry out a placebo-controlled trial of a beta

blocker in postinfarction patients; yet it would be difficult to

conclude that a noninferiority trial would have sensitivity-to-drug-

effects. The designs described in section 2.1.5 may be useful in

some of these cases.

2.1.7.2 Patient and physician practical concerns. Physicians

and/or patients may be reluctant to accept the possibility that the

patient will be assigned to the placebo treatment, even if there is

general agreement that withholding or delaying treatment will not

result in harm. Subjects who sense they are not improving may drop

out of trials because they attribute lack of effect to having been

treated with placebo, complicating the analysis of the study. With

care, however, drop-out for lack of effectiveness can sometimes be

used as a study endpoint. Although this may provide some information

on drug effectiveness, such information is less precise than actual

information on clinical status in subjects receiving their assigned

treatment.

2.1.7.3 Generalizability. It is sometimes argued that any

controlled trial, but especially a placebo-controlled trial,

represents an artificial environment that gives results different

from true ``real world'' effectiveness. If study populations are

unrepresentative in placebo-controlled trials because of ethical or

practical concerns, questions about the generalizability of study

results can arise. For example, patients with more serious disease

may be excluded by protocol, investigator, or patient choice from

placebo-controlled trials. In some cases, only a limited member of

patients or centers may be willing to participate in studies.

Whether these concerns actually (as opposed to theoretically) limit

generalizability has not been established.

2.1.7.4 No comparative information. Placebo-controlled trials

lacking an active control give little useful information about

comparative effectiveness, information that is of interest and

importance in many circumstances. Such information cannot reliably

be obtained from cross-study comparisons, as the conditions of the

studies may have been quite different.

2.2 No-Treatment Concurrent Control (See Section 1.3.2)

The randomized no-treatment control is similar in its general

properties and its advantages and disadvantages to the placebo-

controlled trial. Unlike the placebo-controlled trial, however, it

cannot be fully blinded, and this can affect all aspects of the

trial, including subject retention, patient management, and all

aspects of observation (see section 1.2.2). This design is

appropriate in circumstances where a placebo-controlled trial would

be performed, except that blinding is not feasible because the

treatments themselves are so different, e.g. radiation therapy

versus surgery, or because the treatment side effects are so

different. When this design is used, it is desirable to have

critical decisions, such as eligibility and endpoint determination

or changes in management, made by an observer blinded to treatment

assignment. Decisions related to data analysis, such as inclusion of

patients in analysis sets, should also be made by individuals

without access to treatment assignment (See ICH E9 for further

discussion).

2.3 Dose-Response Concurrent Control (See Section 1.3.3)

2.3.1 Description

A dose-response study is one in which subjects are randomly

assigned to one of several dosing groups, with or without a placebo

group. Dose-response studies are carried out to establish the

relation between dose and efficacy/adverse effects and/or to

demonstrate efficacy. The first use is considered in ICH E4; the

latter is the subject of this guidance. Evidence of efficacy could

be based on significant differences in pair-wise comparisons between

dosing groups or between dosing groups and placebo, or on evidence

of a significant positive trend with increasing dose, even if no two

groups are significantly different. In the latter case, however,

further study may be needed to assess the effectiveness of the low

doses. As noted in ICH E9, the particular approach for the primary

efficacy analysis should be prespecified.

There are several advantages to inclusion of a placebo (zero-

dose) group in a dose-response study. First, it avoids studies that

are uninterpretable because all doses produce similar effects so

that one cannot assess whether all doses are equally effective or

equally ineffective. Second, the placebo group permits an estimate

of absolute size of effect, although the estimate may not be very

precise if the dosing groups are relatively small. Third, as the

drug-placebo difference is generally larger than inter-dose

differences, use of placebo may permit smaller sample sizes. The

size of various dose groups need not be identical; e.g., larger

samples could be used to give more precise information about the

effect of smaller doses or be used to increase the power of the

study to show a clear effect of what is expected to be the optimal

dose. Dose-response studies can include one or more doses of an

active-control agent. Randomized withdrawal designs can also assign

subjects to multiple dosage levels.

2.3.2 Ability to Minimize Bias

If the dose-response study is blinded, it shares with other

blinded designs an ability to minimize subject and investigator

bias. When a drug has pharmacologic effects that could break the

blind for some patients or investigators, it may be easier to

preserve blinding in a dose-response study than in a placebo-

controlled trial. Masking treatments may necessitate multiple

dummies or preparation of several different doses that look alike.

2.3.3 Ethical Issues

The ethical and practical concerns related to a dose-response

study are similar to those affecting placebo-controlled trials.

Where there is therapy known to be effective in preventing death or

irreversible morbidity, it is no more ethically acceptable to

randomize deliberately to subeffective therapy than it is to

randomize to placebo. Where therapy is directed at less serious

conditions or where the toxicity of the therapy is substantial

relative to its benefits, dose-response studies that use low,

potentially subeffective doses or placebo may be acceptable to

patients and investigators.

2.3.4 Usefulness of Dose-Response Studies and Quality/Validity of

Inference in Particular Situations

In general, a blinded dose-response study is useful for the

determination of efficacy and safety in situations where a placebo-

controlled trial would be useful and has similar credibility (see

section 2.1.4).

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2.3.5 Modifications of Design and Combinations With Other Controls

That Can Resolve Ethical, Practical, or Inferential Problems

In general, the sorts of modification made to placebo-

controlled studies to mitigate ethical, practical, or inferential

problems are also applicable to dose-response studies (see section

2.1.5).

2.3.6 Advantages of Dose-response Trials, Other Than Those Related

to Any Difference-Showing Study

2.3.6.1 Efficiency. Although a comparison of a large, fully

effective dose to placebo is maximally efficient for showing

efficacy, this design may produce unacceptable toxicity and gives no

dose-response information. When the dose-response is monotonic, the

dose-response trial is reasonably efficient in showing efficacy and

also yields dose-response information. If the optimally effective

dose is not known, it may be more prudent to study a range of doses

than to choose a single dose that may prove to be suboptimal or

toxic.

2.3.6.2 Possible ethical advantage. In some cases, notably

those in which there is likely to be dose-related efficacy and dose-

related important toxicity, the dose-response study may represent a

difference-showing trial that can be ethically or practically

conducted even where a placebo-controlled trial could not be,

because there is reason for patients and investigators to accept

lesser effectiveness in return for greater safety.

2.3.7 Disadvantages of Dose-Response Study

A potential problem that needs to be recognized is that a

positive dose-response trend (i.e., a significant correlation

between the dose and the efficacy outcome), without significant

pair-wise differences, can establish efficacy, but may leave

uncertainty as to which doses (other than the largest) are actually

effective. But, of course, a single-dose study poses a similar

problem with respect to doses below the one studied, giving no

information at all about such doses.

It should also be appreciated that it is not uncommon to show

no difference between doses in a dose-response study; if there is no

placebo group to provide a clear demonstration of an effect, this is

a very costly ``no test'' outcome.

If the therapeutic range is not known at all, the design may be

inefficient, as many patients may be assigned to sub-therapeutic or

supratherapeutic doses.

Dose-response designs may be less efficient than placebo-

controlled titration designs for showing the presence of a drug

effect; they do, however, in most cases provide better dose-response

information (see ICH E4).

2.4 Active Control

2.4.1 Description (See Section 1.3.4)

An active-control (positive-control) trial is one in which an

investigational drug is compared with a known active drug. Such

trials are usually randomized and usually double-blind. The most

crucial design question is whether the trial is intended to show a

difference between the two drugs or to show noninferiority/

equivalence. A sponsor intending to demonstrate effectiveness by

means of a trial showing noninferiority of the test drug to a

standard agent needs to address the issue of the sensitivity-to-

drug-effects and assay sensitivity of the trial, as discussed in

section 1.5. In a noninferiority/equivalence trial, the active-

control agent needs to be of established efficacy at the dose used

and under the conditions of the study (see ICH E9: Statistical

Principles for Clinical Trials). In general, this means it should be

an agent acceptable in the region to which the studies will be

submitted for the same indication at the dose being studied. A

superiority study favoring the test drug, on the other hand, is

readily interpretable as evidence of efficacy, even if the dose of

active control is too low or the active control is of uncertain

benefit (but not if it could be harmful). Such a result, however--

superiority in the trial of the test agent to the control--is

interpretable as actual superiority of the test drug to the control

treatment only when the active control is used in appropriate

patients at an optimal dose and schedule (see section 1.4.2). Lack

of appropriate use of the control drug would also make the study

unusable as a noninferiority study if superiority of the test drug

is not shown, because assay sensitivity of the study would not be

ensured (see section 1.5.4).

2.4.2 Ability to Minimize Bias

A randomized and blinded active-control trial generally

minimizes subject and investigator bias, but a note of caution is

warranted. In a noninferiority trial, investigators and subjects

know that all subjects are getting active drug, although they do not

know which one. This could lead to a biased interpretation of

results in the form of a tendency toward categorizing borderline

cases as successes in partially subjective evaluations, e.g., in an

antidepressant study. Such biases may decrease variance and/or

treatment differences and thus can increase the likelihood of an

incorrect finding of equivalence.

2.4.3 Ethical Issues

Active-control trials are generally considered to pose fewer

ethical and practical problems than placebo-controlled trials

because all subjects receive active treatment. It should be

appreciated, however, that subjects getting a new agent are not

getting standard therapy (just as a placebo group is not) and may be

receiving an ineffective or harmful drug. This is an important

matter if the active-control therapy is known to improve survival or

decrease the occurrence of irreversible morbidity. There should

therefore be a sound rationale for the investigational agent. If

there is not strong reason to expect the new drug to be at least as

good as the standard, an add-on study (see section 2.1.5.2.1) may be

more appropriate, if the conditions allow such a design.

Using a very low dose, either of the active control or of the

test drug, may provide a de facto placebo that can be shown inferior

to the full dose of the test drug. This, however, is only considered

ethical where a placebo would also be ethical, unless there is a

legitimate reason to study such low doses.

2.4.4 Usefulness of Active-Control Trials and Quality/Validity of

Inference in Particular Situations

When a new drug shows an advantage over an active control, the

study has inferential properties regarding the presence of efficacy

equivalent to any other difference-showing trial, assuming that the

active control is not actually harmful. When an active-control trial

is used to show noninferiority/equivalence, there is the special

consideration of sensitivity-to-drug-effects and assay sensitivity,

which are considered above in section 1.5. If assay sensitivity is

established, either historically (by reference to past experience

with the control drug) or by including a placebo control as well as

active control, the active-control trial can assess comparative

efficacy.

2.4.5 Modifications of Design and Combinations With Other Controls

That Can Resolve Ethical, Practical, or Inferential Issues

As discussed earlier (section 2.1.5), active-control studies

can include a placebo group, multiple-dose groups of the test drug,

and/or other dose groups of the active control. Comparative dose-

response studies, in which there are several doses of both test and

active control, are typical in analgesic trials. The doses in

active-control trials can be fixed or titrated, and both cross-over

and parallel designs can be used. The assay sensitivity of a

noninferiority trial can sometimes be supported by a randomized

placebo-controlled withdrawal phase at the end (see section

2.1.5.2.4). Active-control superiority studies in selected

populations (nonresponders to other therapy) can be very useful and

are generally easy to interpret (see appendix), although the results

may not be generalizable.

2.4.6 Advantages of Active-Control Trials

2.4.6.1 Ethical/practical advantages. The active-control

design, whether intended to show noninferiority/equivalence or

superiority, reduces ethical concerns that arise from failure to use

drugs with documented important health benefits. It also addresses

patient and physician concerns about failure to use documented

effective therapy. Recruitment and IRB/IEC approval may be

facilitated, and it may be possible to study larger samples. There

may be fewer dropouts due to lack of effectiveness.

2.4.6.2 Information content. Where superiority to an active

treatment is shown, active-control studies are readily interpretable

regarding evidence of efficacy. The larger sample sizes needed are

sometimes more achievable and acceptable in active-control trials

and can provide more safety information. Active-control trials also

can, if properly designed, provide information about relative

efficacy.

2.4.7 Disadvantages of Active-Control Trials

2.4.7.1 Information content. See section 1.5 for discussion of

the problem of assay sensitivity and the ability of the trial to

support an efficacy conclusion in noninferiority/equivalence trials.

Even when assay sensitivity is supported and the study is suitable

for detecting efficacy, there is no

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direct assessment of absolute effect size and greater difficulty in

quantitating safety outcomes as well.

2.4.7.2 Large sample size. Generally, in noninferiority

trials, the margin of difference that needs to be excluded is chosen

conservatively, first, because the smallest effect of the active

control expected in trials will ordinarily be used as the estimate

of its effect and, second, because there will usually be an intent

to rule out loss of more than some reasonable fraction (see section

1.5.2) of the control drug effect, leading to a still smaller

margin. Because of the need for conservative assumptions about

control drug effect size, sample sizes may be very large. In a

difference-showing active-control trial, the difference between two

drugs is always smaller, often much smaller, than the expected

difference between drug and placebo, again leading to large sample

sizes.

2.5 External Control (Historical Control)

2.5.1 Description

An externally controlled trial is one in which the control

group consists of patients who are not part of the same randomized

study as the group receiving the investigational agent, i.e., there

is no concurrently randomized comparative group. The control group

is thus not derived from exactly the same population as the treated

population. Usually, the control group is a well-documented

population of patients observed at an earlier time (historical

control) at another institution, or even at the same institution but

outside the study. An external-control study could be a superiority

study or an equivalence study. Sometimes certain patients from a

larger experience are selected as a control group on the basis of

particular characteristics that make them similar to the treatment

group; there may even be an attempt to ``match'' particular control

and treated patients.

So-called ``baseline-controlled studies'' are a variety of

externally controlled trials; these are sometimes thought to use

``the patient as his own control,'' but that is logically incorrect.

In fact, the comparator group is an estimate of what would have

happened in the absence of therapy to the patients. Both baseline-

controlled trials and studies that use a more complicated on-off-on

(cross-over) design, but that do not include a concurrently

randomized control group, are of this type. As noted, in these

studies the observed changes from baseline or between study periods

are always compared, at least implicitly, to some estimate of what

would have happened without the intervention. Such estimates are

generally made on the basis of ``general knowledge,'' without

reference to a specific control population. Although in some cases

this is plainly reasonable, e.g., when the effect is dramatic,

occurs rapidly following treatment, and is unlikely to have occurred

spontaneously (e.g., general anesthesia, cardioversion, measurable

tumor shrinkage), in most cases it is not so obvious and a specific

historical experience should be sought. Designers and analysts of

such trials need to be aware of the risks of this type of control

and should be prepared to support its use.

2.5.2 Ability to Minimize Bias

Inability to control bias is the major and well-recognized

limitation of externally controlled trials and is sufficient in many

cases to make the design unsuitable. It is always difficult, in many

cases impossible, to establish comparability of the treatment and

control groups and thus to fulfill the major purpose of a control

group (see section 1.2). The groups can be dissimilar with respect

to a wide range of factors, other than the study drug, that could

affect outcome, including demographic characteristics, diagnostic

criteria, stage or duration of disease, concomitant treatments, and

observational conditions (such as methods of assessing outcome,

investigator expectations). Blinding and randomization are not

available to minimize bias when external controls are used. It is

well documented that untreated historical-control groups tend to

have worse outcomes than an apparently similar control group in a

randomized study, primarily because of selection bias. Control

groups in a randomized study should meet certain criteria to be

entered into the study, criteria that are generally more stringent

and identify a less sick population than is typical of external-

control groups. The group is often identified retrospectively,

leading to potential bias in its selection. A consequence of the

recognized inability to control bias is that the persuasiveness of

findings from externally controlled trials depends on obtaining much

more extreme levels of statistical significance and much larger

estimated differences between treatments than would be considered

persuasive in concurrently controlled trials.

The inability to control bias restricts use of the external-

control design to situations in which the effect of treatment is

dramatic and the usual course of the disease highly predictable. In

addition, use of external controls should be limited to cases in

which the endpoints are objective and the impact of baseline and

treatment variables on the endpoint is well characterized.

As noted, the lack of randomization and blinding, and the

resultant problems with lack of assurance of comparability of test

group and control group, make the likelihood of substantial bias

inherent in this design and impossible to quantitate. Nonetheless,

some approaches to design and conduct of externally controlled

trials could lead them to be more persuasive and potentially less

biased. A control group should be chosen for which there is detailed

information, including, where needed, individual patient data

regarding demographics, baseline status, concomitant therapy, and

course on study. The control patients should be as similar as

possible to the population expected to receive the test drug in the

study and should have been treated in a similar setting and in a

similar manner, except with respect to the study therapy. Study

observations should utilize timing and methodology similar to those

used in the control patients. To reduce selection bias, selection of

the control group should be made before performing comparative

analyses; this may not always be feasible, as outcomes from these

control groups may have been published. Any matching on selection

criteria or adjustments made to account for population differences

should be specified prior to selection of the control and

performance of the study. Where no obvious single ``optimal''

external control exists, it may be advisable to study multiple

external controls, providing that the analytic plan specifies

conservatively how each will be utilized in drawing inferences

(e.g., study group should be substantially superior to the most

favorable control to conclude efficacy). In some cases, it may be

useful to have an independent set of reviewers reassess endpoints in

the control group and in the test group in a blinded manner

according to common criteria.

2.5.3 Ethical Issues

When a drug is intended to treat a serious illness for which

there is no satisfactory treatment, especially if the new drug is

seen as promising on the basis of theoretical considerations, animal

data, or early human experience, there may be understandable

reluctance to perform a comparative study with a concurrent control

group of patients who would not receive the new treatment. At the

same time, it is not responsible or ethical to carry out studies

that have no realistic chance of credibly showing the efficacy of

the treatment. It should be appreciated that many promising

therapies have had less dramatic effects than expected or have shown

no efficacy at all when tested in controlled trials. Investigators

may, in these situations, be faced with very difficult judgments. It

may be tempting in exceptional cases to initiate an externally

controlled trial, hoping for a convincingly dramatic effect, with a

prompt switch to randomized trials if this does not materialize.

Alternatively, and generally preferably, in dealing with

serious illnesses for which there is no satisfactory treatment, but

where the course of the disease cannot be reliably predicted, even

the earliest studies should be randomized. This is usually possible

when studies are carried out before there is an impression that the

therapy is effective. Studies can be monitored by independent data

monitoring committees so that dramatic benefit can be detected

early. Despite the use of a single-treatment group in an externally

controlled trial, a placebo-controlled trial is usually a more

efficient design (needing fewer subjects) in such cases, as the

estimate of control group outcome generally needs to be made

conservatively, causing need for a larger sample size. Great caution

(e.g., applying a more stringent significance level) is called for

because there are likely to be both identified and unidentified or

unmeasurable differences between the treatment and control groups,

often favoring treatment. The concurrently controlled trial can

detect extreme effects very rapidly and, in addition, can detect

modest, but still valuable, effects that would not be credibly

demonstrated by an externally controlled trial.

2.5.4 Usefulness of Externally Controlled Trials and Quality/

Validity of Inference in Particular Situations

An externally controlled trial should generally be considered

only when prior belief in the superiority of the test therapy to

[[Page 51777]]

all available alternatives is so strong that alternative designs

appear unacceptable and the disease or condition to be treated has a

well-documented, highly predictable course. It is often possible,

even in these cases, to utilize alternative, randomized,

concurrently controlled designs (see section 2.1.5 and appendix).

Externally controlled trials are most likely to be persuasive

when the study endpoint is objective, when the outcome on treatment

is markedly different from that of the external control and a high

level of statistical significance for the treatment-control

comparison is attained, when the covariates influencing outcome of

the disease are well characterized, and when the control closely

resembles the study group in all known relevant baseline, treatment

(other than study drug), and observational variables. Even in such

cases, however, there are documented examples of erroneous

conclusions arising from such trials.

When an external-control trial is considered, appropriate

attention to design and conduct may help reduce bias (see section

2.5.2).

2.5.5 Modifications of Design and Combinations With Other Controls

That Can Resolve Ethical, Practical or Inferential Problems

The external-control design can incorporate elements of

randomization and blinding through use of a randomized placebo-

controlled withdrawal phase, often with early-escape provisions, as

described earlier (see section 2.1.5.2.4). The results of the

initial period of treatment, in which subjects who appear to respond

are identified and maintained on therapy, are thus ``validated'' by

a rigorous, largely assumption- and bias-free study.

2.5.6 Advantages of Externally Controlled Trials

The main advantage of an externally controlled trial is that

all patients can receive a promising drug, making the study more

attractive to patients and physicians.

The design has some potential efficiencies (smaller sample

size) because all patients are exposed to test drug, of particular

importance in rare diseases.

2.5.7 Disadvantages of Externally Controlled Trials

The externally controlled study cannot be blinded and is

subject to patient, observer, and analyst bias, major disadvantages.

It is possible to mitigate these problems to a degree, but even the

steps suggested in section 2.5.2 cannot resolve such problems fully,

as treatment assignment is not randomized and comparability of

control and treatment groups at the start of treatment, and

comparability of treatment of patients during the trial, cannot be

ensured or well assessed. It is well documented that externally

controlled trials tend to overestimate efficacy of test therapies.

3.0 Choosing the Control Group

Figure 1 and Table 1 provide a decision tree for choosing among

different types of control groups. Although the table and figure

focus on the choice of control to demonstrate efficacy, some designs

also allow comparisons of test and control agents. The choice of

control can be affected by the availability of therapies and by

medical practices in specific regions.The potential usefulness of

the principal types of control (placebo, active, and dose-response)

in specific situations and for specific purposes is shown in Table

1. The table should be used with the text describing the details of

specific circumstances in which potential usefulness can be

realized. In all cases, it is presumed that studies are

appropriately designed. External controls are so distinct a case

that they are not included in the table. In the table, a P notation

refers to the need to make a convincing case that the study has

assay sensitivity.

In general, evidence of efficacy is most convincingly

demonstrated by showing superiority to a concurrent control

treatment. If a superiority trial is not feasible or is

inappropriate for ethical or practical reasons, and if a defined

treatment effect of the active control is regularly seen (e.g., as

it is for antibiotics in most situations), a noninferiority/

equivalence study can be utilized and can be persuasive. Use of this

design calls for close attention to the issue of sensitivity to drug

effects in active-control noninferiority trials of the condition

being studied and to the assay sensitivity of the particular study

carried out (see section 1.5).

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APPENDIX

Studies of Efficacy in Subsets of the Whole Population; Enrichment

1.0 Introduction

Ideally, the effect of a drug should be known in general and in

relevant demographic and other subsets of the population, such as

those defined by disease severity or other disease characteristics.

To the extent study patients are not a random sample of the patients

who will be treated with the drug once it is marketed, the

generalizability of the results can be questioned. Even if the

overall result is obtained in a representative sample, however, that

does not suggest the result is the same in all people. If subject

selection criteria can identify people more likely to respond to

therapy (e.g., high renin hypertensives to beta blockers), we

consider therapy more rational and the drug more useful.

Subjects entering clinical studies are in fact almost never a

random sample of the potential treatment population, and they are

not treated exactly as a nonstudy patient would be treated. They

must give informed consent, be able to follow instructions, and be

able to get to the clinic. They are sometimes assessed for

likelihood of complying with treatment. They are usually not very

debilitated and generally are without complicated or life-

threatening illness, unless those conditions are being studied. They

are usually selected using particularly stringent diagnostic

criteria that make it very certain they actually have the disease to

be treated (more likely than in clinical practice). Lead-in periods

are often used to exclude subjects who improve spontaneously or

whose relevant functional measures (blood pressure, exercise

tolerance) are too variable. Of course, the entire setting of trials

is artificial in varying degrees, generally directed toward reducing

unwanted variability and increasing study efficiency.

All of these departures from a truly unselected population of

people likely to receive the drug are directed at identifying and

including subjects likely to make a ``good assay population.'' They

can be considered methods of ``enrichment'' of the population,

modifications of a truly random sample of potential users to produce

a population of subjects more likely to discriminate between an

active and an inactive therapy. The kinds of enrichment described

above are widely accepted and ``benign,'' i.e., it seems likely that

results in such a population will be of general applicability, at

least to patients with good compliance. There is a view, however,

that in-use ``effectiveness'' may often be different from the

artificial ``efficacy'' established in these enriched ``efficacy''

trials.

There are other kinds of enrichment that could also be useful

but that would more clearly alter the inference that could be drawn

from the results. This should not discourage their use but should

encourage attention to what such studies do, and do not, show. Some

enrichments of potential value include:

1.1 Studies of Patients Nonresponsive to, or Intolerant of, Other

Therapy

In this kind of study, patients failing therapy on a drug, or

failing to tolerate it acceptably, are randomized to the failed or

poorly tolerated therapy or to the investigational treatment.

Greater efficacy (or better tolerance) of the new therapy shows that

the drug is useful in failures on the other therapy. This is a

valuable showing if, e.g., the drug is relatively toxic and intended

for a ``second-line'' use, but it does not show that the new therapy

is superior in general, and such studies need to be carefully

interpreted. By selecting study patients who will only infrequently

respond to the control agent or who are very likely to have a

particular adverse effect of the control drug, the design

facilitates showing the second drug's advantage in that

circumstance. A direct comparison of the two drugs in an unselected

population that could contain responders to both drugs would need to

be much larger to show a difference between the treatments, even if

there was an overall advantage of the new drug. Moreover, it could

be that each drug has a similar rate of nonresponders (but the other

drug works in some of these), so that no difference could be seen in

a direct comparison in unselected subjects.

In this design, it is usually critical to randomize the

nonresponders or intolerants to both the new agent and the failed

agent, rather than simply place the failures on the new drug.

Patients who failed previously may ``respond'' to the failed drug

when it is readministered in a clinical trial, or may tolerate the

previously poorly tolerated drug in the new circumstance. This can

present a problem. In the ``intolerance'' case, although subjects

can be randomized to a drug that has caused certain kinds of

intolerance, they cannot be randomized to a drug that would endanger

them if administered (e.g., if the intolerance was anaphylaxis,

liver necrosis). Similarly, in the nonresponder case, patients

cannot be restudied on the failed drug if failure would lead to

harm. In some cases, the prior experience may be an adequate control

(e.g., failure of a tumor to respond), a baseline-controlled study

design.

1.2 Studies in Likely or Known Responders

If patients cannot respond to the main pharmacologic effect of

the drug, they cannot be expected to show a clinical response. Thus,

subjects with no blood pressure response to sublingual nitroglycerin

have been excluded from trials of organic nitrates, as they show no

ability to respond to the mechanism of action of these drugs and

including them would only dilute the drug effect. A similar approach

was used in Cardiac Arrhythmia Suppression Trial (CAST). Only

subjects responding to encainide or flecainide with a 70 percent

reduction in ventricular premature beats (VPB's) were randomized to

the mortality phase of the study because there was no reason to

include people who could not possibly benefit (i.e., people with no

VPB reduction). It is important in such cases to record the number

of subjects screened in order to construct the study population so

that users of the drug will have a reasonable expectation of what

they will encounter. It will often be appropriate to incorporate

similar selection criteria in labeling the drug for use.

The nitroglycerin and CAST enrichment approaches were generally

accepted. A potentially more controversial enrichment procedure

would be to identify responders in an initial open phase, withdraw

treatment, then carry out a randomized study in the responders. This

could be a useful approach when efficacy has proved difficult to

demonstrate. For example, it has been difficult to obtain evidence

that gut motility-modifying agents are effective in gastroesophageal

reflux disease, perhaps because there are unrecognized

pathophysiologic subsets of patients, some of which can respond and

some of which cannot. It seems possible that identifying apparent

responders clinically, then randomizing the apparent responders to

drug and placebo treatments, would best utilize both clinical

observation and rigorous design.

In seeking dose-response information, little is to be learned

from studying the drug in a population of nonresponders (although

one would want to know the proportion of the population that is

nonreponsive). Such studies might better be carried out in known

responders to the drug. Similarly, in evaluating a drug of a

particular class, studies including only known responders to the

class might be more likely to detect an effect of the drug or to

show differences between members of the class.

Finally, it should be appreciated that randomized withdrawal

studies (see section 2.1.5.2.4), and studies of maintenance

treatment in general, are often studies in known responders and can

therefore be expected to show greater effect than studies in an

unselected population.

Dated: September 16, 1999.

Margaret M. Dotzel,

Acting Associate Commissioner for Policy

[FR Doc. 99-24855 Filed 9-23-99; 8:45 am]

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