Therapeutic Products Programme
Holland Cross, Tower "B"
2nd Floor, 1600 Scott Street
Address Locator # 3102D1
OTTAWA, Ontario
K1A 1B6
99-028136
To Associations
Re: E10: Choice of Control Groups in Clinical Trials (Step 2)
The aforementioned Step 2 draft guideline was released by the ICH Steering
Committee for consultation and is being sent to your association for information
and comment in accordance with Step 2 of the ICH process.
It is important to note that this document does not make any inferences
regarding regulatory requirements in any ICH region, but rather presents
general principles, as well as more detailed considerations, that should
aid sponsors in the choice of appropriate control groups when designing
clinical trials.
Please note that draft guidelines are only made available in English
until finalized by the ICH.
All comments forwarded to the TPP will be transmitted to the ICH as is,
with the disclaimer that they are provided for information and do not
necessarily represent the views of the TPP, except as specifically indicated
in separate TPP comments.
Alternatively, your organization may wish to provide comments to your
affiliate association in the U.S., Europe or Japan for their input directly
to ICH.
Comments provided to the TPP should be submitted no later than
October
29, 1999, in order to allow sufficient time for their assessment and subsequent
transmission to the ICH. Comments should be directed to:
Dr. André-Marie Leroux
Endocrinology, Metabolism & Allergy Unit
Bureau of Pharmaceutical Assessment
A/L 0202D2
Therapeutic Products Programme
Health Canada
Finance Building
Tunney's Pasture
Ottawa, Ontario
K1A 1B6
Internet: Andre-Marie_Leroux@hc-sc.gc.ca
Fax: (613) 941-1365
The Step 2 ICH document is also being posted to the TPP Website as a
PDF file under Guidelines\ICH\Draft External Guidelines Out for Comment.
Dann M. Michols
Director General
Attachment
INTERNATIONAL CONFERENCE ON HARMONISATION OF TECHNICAL REQUIREMENTS FOR
REGISTRATION OF PHARMACEUTICALS FOR HUMAN USE
DRAFT CONSENSUS GUIDELINE
CHOICE OF CONTROL GROUP IN CLINICAL TRIALS
Released for Consultation
at Step 2 of the ICH Process
on 7 May 1999
by the ICH Steering Committee
At Step 2 of the ICH Process, a consensus draft text or guideline, agreed
by the appropriate ICH Expert Working Group, is transmitted by the ICH
Steering Committee to the regulatory authorities of the three ICH regions
(the European Union, Japan and the USA) for internal and external consultation,
according to national or regional procedures.
CHOICE OF CONTROL GROUP IN CLINICAL TRIALS
Draft ICH Consensus Guideline
Released for Consultation, 7 May 1999, at Step 2 of the ICH Process
TABLE OF CONTENTS
1. Introduction
1.1 General scheme and purpose of guideline
1.2 Purpose of control group
1.2.1 Randomization
1.2.2 Blinding
1.3 Types of controls
1.3.1 Placebo concurrent control
1.3.2 No-treatment concurrent control
1.3.3 Dose-response concurrent control
1.3.4 Active (positive) concurrent control
1.3.5 External control (including historical control)
1.3.6 Multiple control groups
1.4 Purposes of clinical trials
1.4.1 Evidence of efficacy
1.4.2 Comparative efficacy and safety
1.4.2.1 Dose
1.4.2.2 Patient Population
1.4.2.3 Selection and Timing of Endpoints
1.5 Sensitivity-to-Drug-Effects and Assay
Sensitivity of studies intended to show noninferiority/ equivalence
1.5.1 Need to assure assay sensitivity
in non-inferiority (equivalence) trials; difference-showing vs non-inferiority
studies
1.5.2 Choosing the non-inferiority margin
1.5.3 Sensitivity-to-drug-effects is difficult to support
in many situations
1.5.4 Assay sensitivity and study quality in non-inferiority
designs
2. Detailed consideration of types of control
2.1 Placebo control
2.1.1 Description
2.1.2 Ability to minimize bias
2.1.3 Ethical issues
2.1.4 Usefulness of placebo-controlled trials and quality/validity
of inference in particular situations
2.1.5 Modifications of design and combinations with other
controls that can resolve ethical, practical, or inferential issues
2.1.5.1 Additional control groups
2.1.5.1.1 Three-arm study; placebo and active control
2.1.5.1.2 Additional doses
2.1.5.1.3 Factorial/Combination studies
2.1.5.2 Changes in study design
2.1.5.2.1 Add-on study, placebo-controlled; replacement
study
2.1.5.2.2 "Early escape;" rescue medication
2.1.5.2.3 Limited placebo period
2.1.5.2.4 Randomized withdrawal
2.1.5.2.5 Other design considerations
2.1.6 Advantages of placebo-controlled trials
2.1.6.1 Ability to demonstrate efficacy credibly
2.1.6.2 Measures "absolute" effectiveness
and safety
2.1.6.3 Efficiency
2.1.6.4 Minimizing the effect of subject and investigator
expectations
2.1.7 Disadvantages of placebo-controlled trials
2.1.7.1 Ethical concerns
2.1.7.2 Patient and physician practical concerns
2.1.7.3 Generalizability
2.1.7.4 No comparative information
2.2 No-treatment concurrent control
2.3 Dose-response concurrent control
2.3.1 Description
2.3.2 Ability to minimize bias
2.3.3 Ethical issues
2.3.4 Usefulness of dose-response studies and quality/validity
of inference in particular situations
2.3.5 Modifications of design and combinations with other
controls that can resolve ethical, practical, or inferential problems
2.3.6 Advantages of dose-response trials, other than
those related to any difference-showing study
2.3.6.1 Efficiency
2.3.6.2 Possible ethical advantage
2.3.7 Disadvantages of dose-response study
2.4 Active control
2.4.1 Description
2.4.2 Ability to minimize bias
2.4.3 Ethical issues
2.4.4 Usefulness of active-control trials and quality/validity
of inference in particular situations
2.4.5 Modifications of design and combinations with other
controls that can resolve ethical, practical, or inferential issues
2.4.6 Advantages of active control trials
2.4.6.1 Ethical/practical advantages
2.4.6.2 Information content
2.4.7 Disadvantages of active control trials
2.4.7.1 Information content
2.4.7.2 Large sample size
2.5 External control (historical control)
2.5.1 Description
2.5.2 Ability to minimize bias
2.5.3 Ethical issues
2.5.4 Usefulness of externally controlled trials and
quality/validity of inference in particular situations
2.5.5 Modifications of design and combinations with other
controls that can resolve ethical, practical or inferential problems
2.5.6 Advantages of externally controlled trials
2.5.7 Disadvantages of the external control trials
3. Choosing the control group
Appendix
CHOICE OF CONTROL GROUP IN CLINICAL TRIALS
1. 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 guideline
The general principles considered in this guideline 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 guideline 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 non-inferiority/equivalence trials (see
section 1.5), the guideline 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 guidelines are particularly relevant to the choice
of control group:
- E-3: Structure and Content of Clinical Study Reports
- E-4: Dose-Response Information to Support Drug Registration
- E-6: Good Clinical Practice: Consolidated Guideline
- E-8: General Considerations for Clinical Trials
- E-9: Statistical Principles for Clinical Trials
In this guideline, 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.
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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 happen 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, etc.
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 E-9) 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 assure
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
E-9). 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.
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1.2.2 Blinding
The groups should not only be similar at baseline but need to 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 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 follow-up 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 assure that subjective assessments and
decisions are not affected by knowledge of treatment assignment.
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1.3 Types of controls
Control groups in clinical trials can be classified on the basis of two
critical attributes: the type of treatment received and the method of
determining who will be in the control group. The type of treatment may
be any of the following four: placebo, no treatment, different dose or
regimen of the study treatment, or a 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
of serious concerns about the ability to assure 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.
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1.3.2 No-treatment concurrent control
In a no-treatment controlled study, subjects are randomly assigned to
test treatment or to no (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 doubleblind
(e.g., medical vs 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.
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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/non-inferiority 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 non-defined, 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.
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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 non-inferiority
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 non-inferiority 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 non-inferior (see section
1.5).
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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 non-inferiority 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/non-inferiority
trial offered as evidence of efficacy also almost always needs to provide
a fair comparison with the control, because any 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; it 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.
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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 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 needs to be carefully considered in evaluating
what the trial has shown. For example, if subjects are drawn from a population
of non-responders 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 non-responders 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 non-responders,
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.
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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 non-inferiority/equivalence.
As noted above (section 1.4.1), use of an active control non-inferiority/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 non-inferiority/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 non-inferiority 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 non-inferiority 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 non-inferiority 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-drugeffects
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
non-inferiority trial, there will be an ability not to find an ineffective
agent to be non-inferior. 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.
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1.5.1 Need to assure assay sensitivity in non-inferiority (equivalence)
trials; difference-showing vs non-inferiority studies
When designing a non-inferiority study, study designers need to consider
the fundamental distinction between two kinds of clinical trials: those
that seek to demonstrate efficacy by showing superiority of a treatment
to a control (superiority trials) and 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 non-inferiority situation, in contrast, a finding
of non-inferiority leaves unanswered the question: would the study have
led to a conclusion of noninferiority even if the study drug were inferior.
In a non-inferiority trial without a placebo group, there is no internal
standard (that is, a showing of an active drug-placebo difference) to
measure/assure 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
non-inferiority 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 vs 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 respect to efficacy, the clinical study lacks assay
sensitivity and does not provide evidence that the drug is ineffective.
1.5.2 Choosing the non-inferiority margin
As noted earlier, most active control "equivalence" trials
are really non-inferiority trials intended to establish the efficacy of
a new drug. Analysis of the results of non-inferiority trials is discussed
in the ICH documents E-9 and E-3. Briefly, in such a trial new and established
therapies are compared. Prior to the trial, an equivalence or non-inferiority
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 non-inferior and thus effective;
if the confidence interval includes a difference as large as the margin,
the test drug cannot be declared non-inferior and cannot be considered
effective.
The margin chosen for a non-inferiority 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 assuring 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 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 non-inferiority 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.
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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
non-inferiority design cannot provide acceptable support for the sensitivity-to-drug-effects
of the study with the chosen inferiority margin, a finding of non-inferiority
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 non-inferiority 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 is 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:
- Poor compliance with therapy
- Poor responsiveness of the study population to drug effects Choice
of Control Group in Clinical Trials
- Use of concomitant medication or other treatment that interference
with the test drug or that reduces the extent of the potential response
- A population that tends to improve spontaneously, leaving no room
for further drug-induced improvement
- Poor diagnostic criteria (patients lacking the disease to be studied)
- Inappropriate (insensitive) measures of drug effect
- Excessive variability of measurements
- 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 Guideline 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 assure that
an effective drug will be distinguished from placebo. Nonetheless, in
many clinical settings, despite the strong stimulus and extensive efforts
to assure 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 (non- inferiority) between two treatments, there
is a much weaker stimulus to engage in many of these efforts, which help
assure that differences will be detected, i.e., assure 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 non-inferiority
by widening the confidence interval so that a 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 non-inferior.
When a non-inferiority 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 similar to studies of the active control that were successful
in the past. To assure 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, method of diagnosis), the specific
endpoint measured and timing of assessments, 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 non-inferiority
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 non-inferiority trial may
not be persuasive.
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2. 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 crossover designs (see ICH E-9),
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.
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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 non-coercive
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 IRB/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 generally
considered 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.
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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, the placebo-controlled trial
has the same assay sensitivity problem as any equivalence or non-inferiority
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.
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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 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 assure a fair comparison of treatments
(see ICH E-4: 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.
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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 non-inferiority 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 anti-cancer, 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" non-inferiority). 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 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 pre-defined 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 anti-epileptic
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 pre-specified 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
assure 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.
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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 pre-randomization 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 post-withdrawal 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.)
post-infarction 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).
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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 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
non-inferiority 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 vs active
control comparison.
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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. Non-inferiority active control trials also need
larger sample sizes because they must use conservative assumptions about
the effect size of the control drug to assure that non-inferiority 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 post-infarction patients; yet it would be difficult to
conclude that a non-inferiority trial would have sensitivity-to-drug-effects.
The designs described in section 2.1.5 may be useful in some of these
cases.
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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.
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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 vs
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
E-9 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
E-4; 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
E-9, the particular approach for the primary efficacy analysis should
be pre-specified. 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.
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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 sub-effective
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
sub-effective, 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).
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 doseresponse 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.
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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 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 supra-therapeutic
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 E-4).
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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 non-inferiority/ equivalence. A sponsor intending to demonstrate
effectiveness by means of a trial showing non-inferiority of the test
drug to a standard agent needs to address the issue of the sensitivity-to-drugeffects
and assay sensitivity of the trial, as discussed in section 1.5. In a
non-inferiority/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 Guideline E-9: 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 non-inferiority study if superiority
of the test drug is not shown because assay sensitivity of the study would
not be assured (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 non-inferiority
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.
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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
non-inferiority/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 crossover and parallel designs can be used. The assay sensitivity
of a non-inferiority 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 (non-responders
to other therapy) can be very useful and are generally easy to interpret
(see Appendix), although the results may not be generalizable.
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2.4.6 Advantages of active control trials
2.4.6.1 Ethical/practical advantages
The active control design, whether intended to show non-inferiority/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 non-inferiority/equivalence
trials. Even when assay sensitivity is supported, and the study is suitable
for detecting efficacy, there is no direct assessment of absolute effect
size and greater difficulty in quantitating safety outcomes as well.
2.4.7.2 Large sample size
Generally, in non-inferiority trials, the margin of difference that must
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.
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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 (crossover) 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 and 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 must 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 must 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.
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2.5.3 Ethical issues
When a drug is intended to treat a serious illness for which there is
no satisfactory treatment, and 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 must be made conservatively, causing need for
a larger sample size. Great caution (e.g., applying a more stringent significance
level) is needed 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 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).
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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 the external control 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
assured or well assessed. It is well-documented that externally controlled
trials tend to overestimate efficacy of test therapies.
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3. 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 doseresponse) 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 inappropriate for ethical or practical reasons,
and if a defined treatment effect of the active control is regularly seen
(as it is, e.g., for antibiotics in most situations), a noninferiority/
equivalence study can be utilized and can be persuasive. Use of this design
requires 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).
Table 1. Usefulness of Specific Control Types in Various Situations
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Y=Yes, N=No, P=Possible, depending on a showing that this type of trial
will have sensitivity to drug effect.
* Through the direct demonstration within the trial of the ability to
demonstrate differences between treatments.
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Figure 1 Choosing the concurrent control for demonstrating efficacy
This figure shows the basic logic for choosing the control group; the
decision may depend on the available drugs or medical practices in the
specific region.
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APPENDIX
Studies of Efficacy in Subsets of the Whole Population; Enrichment
1. 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 non-study 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 populations 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 non-responsive 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 non-responders
(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 non-responders
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 re-administered
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,
etc.). Similarly, in the non-responder 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.
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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. It has been, for example,
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 non-responders (although one would want to
know the proportion of the population that is non-reponsive). 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.
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