Guidance for Industry
Clinical Development Programs for
Drugs, Devices, and Biological
Products for the Treatment of
Rheumatoid Arthritis (RA)
U.S. Department of Health and Human Services
Food and Drug Administration
Center for Drug Evaluation and Research (CDER)
Center for Biologics Evaluation and Research (CBER)
Center for Devices and Radiologic Health (CDRH)
February 1999
Clin  7
  Guidance for Industry
Clinical Development Programs for Drugs,
Devices, and Biological Products for the
Treatment of Rheumatoid Arthritis (RA)
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or
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or
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Center for Devices and Radiological Health (CDRH) 
February 1999 TABLE OF CONTENTS
I.  INTRODUCTION . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1
II.  NEW CLAIMS FOR THE TREATMENT OF RA . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 2
A.  Reduction in the Signs and Symptoms of RA . . . . . . . . . . . . . . . . . . . . . . . . . . . 2
B.  Major Clinical Response . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 3
C.  Complete Clinical Response . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4
D.  Remission . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4
E.  Prevention of Disability . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4
F.  Prevention of Structural Damage . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5
III.  CONSIDERATIONS IN RA PRODUCT DEVELOPMENT . . . . . . . . . . . . . . . . . . . . . 6
A.  Preclinical Considerations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 7
B.  Pharmacokinetic/Pharmacodynamic Strategies . . . . . . . . . . . . . . . . . . . . . . . . . 11
C.    Considerations in Phase 1 Trials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11
D.  Considerations in Phase 2 Trials . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 14
E.    Efficacy Trial Considerations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16
F.    Safety Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 30
IV.  SPECIAL CONSIDERATIONS FOR BIOLOGICAL PRODUCTS  . . . . . . . . . . . . . . 32
A.  Species Specificity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
B.  Dose Responses . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
C.  Toxicity Response . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
D.  Product Homogeneity  . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
E.  The Role of Antibodies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
V.  SPECIAL CONSIDERATIONS FOR MEDICAL DEVICES . . . . . . . . . . . . . . . . . . . 33
A.  Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33
B.  Efficacy Considerations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33
C.  Safety Considerations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 34
VI.  SPECIAL CONSIDERATIONS FOR JUVENILE RHEUMATOID ARTHRITIS . . . . 35
A.  Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35
B.  Applicability of Pediatric Regulation and Impact on
Trial Design for JRA Studies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36
C.  Outcome Variables and Claims . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 37
D.  Trial Design Issues . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 3 9
E.  Concurrent Antirheumatic Agent Administration . . . . . . . . . . . . . . . . . . . . . . . 40
F.  Multicenter Trials and Center Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40
REFERENCES . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42
APPENDIX A:  COMPARATIVE TRIAL RESPONSE RATES . . . . . . . . . . . . . . . . . . . . . . 45 
i Guidance for Industry1
  Clinical Development Programs for
Drugs, Devices, and Biological Products Intended for the
Treatment of  Rheumatoid Arthritis (RA) 
I. INTRODUCTION
This guidance is intended to assist developers of drugs, biological products, and medical devices
intended for the treatment of rheumatoid arthritis (RA).  The document discusses the types of
label claims that can be considered for such products and provides guidance on the clinical
development programs to support those claims.
The central purpose of label claims is to inform prescribers and patients about the documented
benefits of a product.  Because RA is a chronic, symptomatic disease that can result in a variety of
outcomes with different chronologies, severities, and overall patient effects, any number of
different clinical outcomes could provide the basis for a label claim.
Relief of symptoms  the signs and symptoms claim   is a central therapeutic effect of most
RA therapeutics marketed circa 1997.  The claim structure proposed in this document, however,
incorporates a wider range of patient outcomes than previously allowable RA claims.  As a result,
guidance is provided for demonstrating patient benefit of greater magnitude than is needed for a
claim of symptomatic relief.  For example, the claims major clinical response, complete clinical
response, and remission (the same criteria as complete clinical response while off all
antirheumatic drugs) reflect enhanced effects on the signs and symptoms of disease.  The claim
prevention of structural damage is documented by various radiographic techniques.  The claim
prevention of disability is intended to reflect longer term benefits on disease course.  The claims
and clinical development programs discussed in this draft  guidance for industry represent the
current views of Agency rheumatologists about achievable and clinically relevant overall
outcomes that can be evaluated in clinical trials.
Traditionally, RA therapeutics have been categorized as disease modifying antirheumatic drugs
(DMARDs) or as nonsteroidal anti-inflammatory drugs (NSAIDs).  As a result of the ongoing
search for more effective therapeutics that have a positive impact on the natural history of the
disease, promising new therapies are currently being tested in the clinic.  Many of the novel agents
1 This guidance has been prepared by the Rheumatology Working Group of the Medical Policy Coordinating
Committee (MPCC) of the Center for Drug Evaluation and Research (CDER), the Center for Biologics Evaluation and
Research (CBER), and the Center for Devices and Radiological Health (CDRH). This guidance document represents the
Agencys current thinking on Clinical Development Programs for Drugs, Devices, and Biological Products Intended for
the Treatment of  Rheumatoid Arthritis.  It does not create or confer any rights for or on any person and does not operate
to bind FDA or the public.  An alternative approach may be used if such approach satisfies the requirements of the
applicable statute, regulations, or both.  under study for the treatment of RA defy categorization by putative mechanism of action.  As a
result, the usefulness of classifying them in the traditional manner may be limited.  For this reason,
information being provided in labeling about the onset and duration of action and the durability of
response of therapeutic interventions is intended to reflect the data that were gathered in clinical
trials.  Because of this, some of the claims described in this document incorporate response
duration times within their structure.
Over the past decade, there has been a search for better measures to describe patient outcomes in
RA clinical trials.  A number of organizations, including the European League Against
Rheumatism,  the International League Against Rheumatism, the American College of
Rheumatology (ACR), and the Outcome Measures in Rheumatoid Arthritis Clinical Trials
(OMERACT) group, have attempted to define core groups of measures, as well as composite
indices, that describe patient outcomes.  As a result of these efforts, several new measures have
been described and validated with clinical data.  With the hope that these measures will provide
more useful information about patient outcomes, this document provides guidance about the use
of these new measures in clinical trials to support label claims.  
One outcome measure that is not fully relied upon as a stand-alone claim is general health-related
quality of life (HR-QOL).  Since RA affects so many domains of a patients life, it is hoped that
such HR-QOL measures may provide an integrated assessment of the long-term impact of
intervention.  However, not enough information is available on the performance of general HR-
QOL measures in longer term arthritis trials.  The incorporation of such measures in planned trials
is encouraged.
II. NEW CLAIMS FOR THE TREATMENT OF RA
A number of new claims are now being evaluated in clinical trials during drug development. 
Descriptions of the claims and acceptable outcome measures to support each claim are discussed
in the following sections.
A. Reduction in the Signs and Symptoms of RA
This claim is intended to reflect the demonstration of symptomatic benefit or benefits that
includes improvement in signs of disease activity as well as symptoms.  Reduction in signs
and symptoms may ordinarily be the initial claim granted for marketing approval.
Ordinarily, this claim is established by trials of at least six months' duration, unless the
product belongs to an already well-characterized pharmacologic class (e.g., NSAIDs) for
which trials of three months' duration are sufficient to establish efficacy for signs and
symptoms.  Six-month trials are desirable for several reasons.  First, RA is a disease of
long duration.  Interventions that provide only short-term, time-limited benefit are unlikely
to have overall value to patients.  In addition, products with the potential to elicit antibody
formation should be assessed for durability, since antibodies may block effectiveness.  In
evaluating signs and symptoms, methods that evaluate response over time are preferable to
methods that incorporate only the baseline value and the final observation, unless there is a
2 reason to weight symptoms at the last visit more than intermediary symptoms.  Acceptable
outcome measures that would support claim A include:
l. Validated composite endpoints or indices of signs and symptoms
These composites may be used to construct categorical endpoints for patient
success or failure.  For example, the Paulus criteria (1990) or the ACR definition
of improvement (ACR 20)2 could be used to assess a patient's response.
Illustration:  Success for each patient in a six-month trial could be defined as
meeting the criteria for improvement over baseline in at least four of six monthly
observations and not dropping out because of toxicity.
2. Well-accepted sets of signs/symptoms measures
The four measures previously recommended in the 1988 CDER Guideline for the
Clinical Evaluation of Anti-Inflammatory and Antirheumatic Drugs (FDA 1988)
  joint counts:  pain, tenderness, and swelling and global assessments:  physician
and patient  or the ACR core set are examples of well-accepted sets of signs and
symptoms measures.  The criteria for success and the methods for statistical
analysis should be prospectively defined and agreed upon.  For example,
historically, in using joint counts and global assessments, a statistically significant
difference between the control and the treatment group in change from baseline in
at least three of the four measures has been used as the criterion for a successful
trial.  However, as stated above, comparison of only the baseline and last
observation may not be the best way to construct the analysis since this method
leaves out all intervening efficacy observations.
For both the above measures, using 66- or 28-joint count is appropriate (Smolen
1995).
B. Major Clinical Response
This claim is intended to reflect the demonstration of a continuous six-month period of
success by the ACR 70," which is defined entirely parallel to the ACR 20, except 70
percent improvement, rather than 20 percent, is needed for the component assessed.  This
claim is based on statistically significant improvement in response rates by the continuous
six-month ACR 70 definition compared to background therapy in a randomized control
group.  For reference, the number of patients satisfying various definitions of ACR
2 The ACR definition of improvement (ACR 20) is 20 percent improvement in tender and swollen joint counts
and 20 percent improvement in three of the five remaining core set measures:  patient and physician globals, pain,
disability, and an acute phase reactant (Felson 1993, 1995). For specific details on individual measures, e.g., disability,
acute phase reactant, refer to Felson 1995. 
3 responses from ACR 20 to ACR 70 in two historic databases are given in Appendix A of
this document.  Trial duration should be a minimum of seven months for an agent
expected to have a rapid onset of action and longer for agents with less prompt effects.  
C. Complete Clinical Response
This claim is intended to describe a therapeutic benefit of greater magnitude than the
major clinical response claim.  Complete clinical response and remission (see below) are
identically defined as a continuous six-month period of both remission by ACR criteria
and radiographic arrest (no radiographic progression [Larsen 1977] or modified Sharp
methods [1985]).  Complete clinical response connotes a benefit requiring ongoing drug
therapy; remission is defined by the same result while off all antirheumatic drugs.  The
1981 ACR remission criteria (Pinals 1981) require at least five of the following:  morning
stiffness less than 15 minutes, no fatigue, no joint pain by history, no joint tenderness or
pain on motion, no swelling of joints or tendon sheaths, and erythrocyte sedimentation
rate (ESR) less than 20 for males or less than 30 for females. The duration of trials
designed to support this claim will vary depending upon the rate of onset of effect of the
test product.  For all but the most rapid-onset agents, trials of one years duration should
be planned.  Longer trials may be needed for very slow-acting agents.   Trials evaluating
complete clinical response would use a categorical endpoint (patient complete response or
treatment failure) as the primary outcome measure. 
D.  Remission
This claim is defined as both remission by ACR criteria and radiographic arrest (no
radiographic progression by Larsen or modified Sharp method) over a continuous
six-month period while off all antirheumatic therapy.  Remission is not intended to imply
cure, and a remission claim could be granted even if patients relapse after six months or
more of remission.  The duration of trials designed to support a remission claim will vary,
depending upon the rate of onset of effect of the test product.  Ordinarily such trials
should be at least one year in duration, and longer trials may be needed for slow-acting
agents.
E. Prevention of Disability
This claim is intended to encourage long-term trials in RA.  Currently, the Health
Assessment Questionnaire (HAQ) (Fries 1982) and the Arthritis Impact Measure Scales
(AIMS) (Meenan 1982) are adequately validated measures for use as the primary outcome
measure in these trials.  Studies should be two to five years in duration.  Sponsors seeking
this claim should plan to have demonstrated previously, or to demonstrate concomitantly,
improvement in signs and symptoms.  Since the full effect of RA on a patient is not
captured without the use of more general HR-QOL measures, a validated measure such as
the SF-36 should also be collected and patients should not worsen on these measures over
the duration of the trial. 
4 F.  Prevention of Structural Damage
Prevention of structural damage is an important goal of RA therapy.  Trials evaluating this
outcome should be at least one year in duration.
The following are examples of outcome measures that could be used to support
prevention of structural damage claims.
1. Slowing X-ray progression, using either the Larsen, the modified Sharp, or
another validated radiographic index
Radiographic claims should be based on comparisons of films taken at one year
(and subsequent yearly points) with those taken at baseline.  All randomized
patients should have films at both time points, regardless of whether they are
continuing treatment.  Patients dropping out of the trial should have films taken at
that time.  Prespecification of the handling of dropouts is especially important in
these trials.
2. Prevention of new X-ray erosions  maintaining an erosion-free state or
preventing new erosions
Trials evaluating this claim would ordinarily use a categorical endpoint to assign a
status of progression or nonprogression to each patient, comparing the final state
to the baseline state.
3. Other measurement tools (e.g., MRI)
Other measures, such as MRI (magnetic resonance imaging) or ultrasonography,
could be employed.  However, because of the technique's potential for identifying
small, albeit statistically significant changes, the magnitude of the difference that
would reflect actual patient benefit is unclear and needs to be established.
Because slowing of radiographic progression does not in itself define a patient benefit, it is
expected that the claim of prevention of structural damage would be submitted for an
agent that has been shown (previously or concomitantly) to be effective for one of the
other claims (e.g., prevention of disability).  However, some agents are not intended to
affect acute inflammation, but are designed to prevent or slow joint destruction by other
means.  The first indication that such an agent is clinically useful might be slowing of
radiographic progression.  Nevertheless, the ultimate goals of slowing joint destruction are
to improve symptoms and to preserve functional ability.  Therefore, slowing radiographic
progression of disease is considered a surrogate marker for overall patient benefit in RA.
Under 21 CFR 314, subpart H and 21 CFR 601 subpart E, FDA can approve drugs
intended to treat serious and life-threatening diseases based on an effect on a surrogate
marker, provided that certain criteria are met and that there is a commitment to define the
5 actual clinical benefit of the agent in studies completed after marketing.  A demonstration
of significant slowing of radiographic progression in a seriously affected population of RA
patients would qualify for consideration under these regulations.  Sponsors are urged to
consult with the relevant FDA staff before embarking on a clinical program based on these
regulations.  
    
One example of a significant effect on radiographic progression might be the
demonstration, in a randomized controlled trial, of maintenance of an erosion-free state in
a large majority of treated patients when control patients develop multiple erosions. The
methods of measurement of the radiographic finding, the magnitude of change considered
to be clinically significant (whether a by-patient measure or treatment group means), and
the methods of statistical analysis should be prospectively defined in the clinical protocol,
and the sponsor should seek Agency concurrence with the plan for evaluating efficacy. 
The use of the accelerated approval pathway would necessitate timely completion of
phase 4 studies using acceptable clinical endpoints evaluating signs and symptoms or
prevention of disability.  It is anticipated that these investigations would be extensions of
the one-year studies used for the  accelerated approval.  
III. CONSIDERATIONS IN RA PRODUCT DEVELOPMENT
The following information on preclinical and early clinical product development pertains primarily
to pharmaceuticals (drugs and biologics).  Except in the first two sections, the general principles
outlined below also apply to devices.  For information specific to the development of devices,
refer to the section in this document entitled "Special Considerations for Medical Devices." 
Developers of products that combine therapeutic modalities (e.g., biologics and devices) may
request assistance from FDA in designating a lead center for review of the product.  Such
requests should be submitted to:  Office of the Chief Mediator and Ombudsman (HF-7), Food and
Drug Administration, 5600 Fishers Lane, Rockville, MD 20857.
Frequently encountered issues in RA product development include:
1. Selecting appropriate in vitro (animal or human systems) and in vivo animal models for
screening potentially active agents.
2. Designing and performing appropriate preclinical safety studies to support the use of a
new molecular entity in human volunteers or patients.
3. Balancing the potential need for therapeutic intervention early in the disease course with
the need to avoid exposing patients with mild disease to agents that have toxicities or little
record of safety.
4. Identifying the potential risks associated with combination therapies, particularly those
with shared target organ toxicity or potential for pharmacokinetic interactions.
6 5. Designing adequate and practical long-term safety monitoring.
6. Designing trials that definitively show clinical efficacy.
The following sections discuss approaches to the above issues.  
A. Preclinical Considerations
This section focuses on preclinical issues that are specific to the clinical development of
antirheumatic therapies.  In designing toxicity studies and the timing of such studies,
consultation with the Agency is recommended concerning the current recommendations
and guidances that address drugs, devices, and biological products.  Guidance on
preclinical safety testing, addressing the need for and design of toxicokinetic, reproductive
toxicity, genotoxicity, and carcinogenicity studies has been developed by the International
Conference on the Harmonization (ICH) of Technical Requirements for Pharmaceuticals. 
Because biologics can pose unique challenges in animal study design (for example,
species-specific binding or immunogenicity of human proteins in animals), a specific ICH
document is available that addresses the safety evaluation of biotechnology-derived
pharmaceuticals (ICH S6 1997).3  
1. Pharmacokinetics
Animal studies of drug absorption, distribution, metabolism, and excretion are
important during the early investigational new drug (IND) phase to aid in toxicity
study interpretation, but need not all be completed prior to phase 1.  Generally, for
initial studies in humans, determining pharmacokinetic (PK) parameters, such as
area under the curve (AUC), maximum concentration (C   ),  and  half-life  (t  ) in
max 1/2
animals, is sufficient to provide a basis for predicting safe clinical exposure.  
  
In the past, preclinical testing of combinations of drugs (or biologics) to be used in
patients with RA has not often been done prior to the initial clinical trials. 
However, given the variety of drugs, including NSAIDs, analgesics,
corticosteroids, and DMARDs currently used to treat RA patients, it would be
useful to consider this testing of common combinations both preclinically and
clinically.  In addition, to evaluate potential interactions, information on the impact
of concomitant therapies on pharmacokinetics may be needed to optimize dosing
regimens and to identify potential safety concerns.  Metabolic interactions often
may be assessed in an in vitro system using animal or human liver slices,
microsomal preparations, or purified P450 enzymes (FDA 1997).
Interactions may also result from the presence of individual- or 
disease-specific factors, such as rheumatoid factor, which may bind to various
3 ICH documents are available via the FDA Internet home page at http://www.fda.gov/cder or cber.
7 monoclonal antibody therapeutics; in such cases in vitro binding studies that
identify patients with high titers may be useful in identifying patients who may
exhibit unique pharmacokinetics or patterns of clinical response.
2. Biological activity 
The biological activity of a potential antirheumatic therapy should be established
using multiple preclinical model systems (i.e., in vitro, in vivo, ex vivo).  In vitro
screens can use cells or tissues derived from animal or human sources and are
generally used to select candidate drugs that have a desired effect on a molecular
target.  Such assays can also be used to devise appropriate bioassays for the
selected agent.  Animals, either healthy, with rheumatic disease (spontaneous or
induced), or genetically modified, are subsequently used to determine whether the
biological effect can be demonstrated in vivo.  While the in vivo system used
should mimic one or more aspects of rheumatoid arthritis or its etiology, it is
expected that each animal model will have limitations.  
a. In vitro
Data from in vitro studies can be useful in defining the potential mechanism
of action of a drug or biologic and for determining relevance of a particular
animal species for in vivo assessment of activity or safety.  These data are
especially useful if a potential surrogate marker can be identified in
preclinical studies.  For example, if the product is intended to affect the
CD4 receptor on lymphocytes, this receptor can be used as a surrogate
marker for both activity and certain toxicities.
Several in vitro tests could be used, depending on the mechanism of action
of the drug or biologic.  For example, binding assays may be useful for
developing receptor antagonists or monoclonal antibodies.  In vitro
functional assays (e.g., platelet and neutrophil aggregation) may be useful
tests for identifying inhibitors of inflammatory mediators.   Enzymatic
assays (e.g., in vitro or ex vivo inhibition of cyclooxygenase, lipoxygenase,
and phospholipase) may also be useful for determining selectivity for the
inhibition of isozymes. 
b. In vivo
Selection of animal models should be made on the basis of 
pharmacodynamic (PD) responses, similarity of animal disease etiology to
clinical disease, and/or to define mechanism-based toxicity.  Ideally,
products that are targeted for a subset of arthritic patients should be
developed in an experimental model(s) that is most relevant to that subset. 
For example, rats are not sensitive to drugs that inhibit 5-lipoxygenase. 
8 Therefore, mouse or rabbit models are more relevant  to evaluate the anti-
inflammatory activity of leukotriene inhibitors.
The development of rheumatic disease models to allow screening for potential RA
candidate drugs is encouraged.  The following examples are meant only to
illustrate some models in current use and are not intended to suggest excluding the
use of others.
Collagen-induced arthritis (CIA):
Collagen-inducted arthritis is often considered to be a suitable model for studying
potential drugs or biologics active in human rheumatoid arthritis because of the
involvement of localized major histocompatibility, complete class II-restricted T
helper cell activation, and the similarity of histopathological lesions.  Radiographs
of joints affected by CIA often show erosive changes similar to those seen in
human rheumatoid arthritis.  The progressive arthritis often results in RA-like joint
deformity and dysfunction.  Anticollagen antibodies, which occur in some patients
with RA, develop in the CIA model.
The CIA model has been useful for assessing immunosuppressants and steroid
hormones as well as inhibitors of inflammatory mediators.  Since this model can be
induced in several animal species, it may be especially useful for evaluating drugs
that are species-specific (e.g., leukotriene antagonists and 5-lipoxygenase
inhibitors).  In addition, although functional tests are not routinely used in this
model, incorporation of measures of mobility and joint function may enhance the
predictive value of the model.
Naturally occurring arthritis or autoimmune response:
MRL/lpr mice, Biozzi H mice and DBA/1 mice have been used to examine the
onset of drug-induced tolerance and immunosuppressant drug effects on
autoimmunity.  The MRL/lpr mouse model has been useful for evaluating
immunosuppressants and hormones.
Rat carrageenin-induced acute model of inflammation:
This model has been useful in assessing anti-inflammatory activity of
cyclooxygenase inhibitors.  Most of the animal models that involve inflammation in
the paw may be used for measuring antiphlogistic action of a drug.
Adjuvant-induced arthritis in rats (AA):
AA in rats has been frequently used for screening nonsteroidal anti-inflammatory
drugs and inhibitors of inflammatory cytokines as well as antimetabolite-like
immunosuppressants.
9 Streptococcal cell wall-induced arthritis:
This model has been used for developing cytokine inhibitors.
Experimental organ transplant in animals:
This model has been used to identify the activity of immunosuppressants and
antimetabolites, particularly those directed at cytolytic cellular immune processes.
Transgenic animal models:
A number of transgenic animal models are being developed for the study of
rheumatoid arthritis and may prove useful over the next decade.  Some examples
include transgenic mice that carry genes for the env-Px region of the human T cell
leukemia virus type I genome, human TNF, CD4, and HLA B-27.
3. Toxicology
Preclinical toxicology studies of a drug or biological product are designed to
characterize general and specific toxicity using dosing routes and regimens as
similar as possible to the proposed clinical trials with consideration of the
demographics and disease status of the intended patient population.  For instance,
the prevalence of RA is high in females.  Therefore, reproductive toxicity studies
should be completed early in clinical development to support the inclusion of
women of childbearing age in early phases of clinical trials.  The need for
reproductive studies for biological products is likely to be case-specific due to
complications arising from immunogenicity and species selectivity.  Therefore,
standardized study designs, such as those recommended in the ICH reproductive
toxicology guidance, may not be feasible or clinically relevant for biologics (ICH
S5 1994).  The need, and specific designs, for these studies may be discussed with
Agency review staff.
Immunomodulatory or immunosuppressive agents administered to RA patients as
monotherapy or in combination raise concerns about the adverse effects of
prolonged immunosuppression.  For example, malignancies (i.e., lymphomas) are a
known risk of long-term, nonselective immunosuppression used for treatment of
graft recipients.  Investigational drug-related opportunistic infections and mortality
related to immunosuppression have occurred in RA patients.  Sponsors are
encouraged to identify and use animal models that assist in selecting drug
candidates that selectively inhibit cells and processes responsible for RA. 
  Antirheumatic drugs are often used in combination in an attempt to improve
outcomes and minimize toxicities.  However, drug interactions may result in
increased toxicity, even at lower than previously evaluated doses of either agent. 
This concern is especially evident for agents that have long half-lives or
10 nonselective activity, or for drugs that share common target organ toxicity. 
Preclinical toxicity studies that evaluate the use of combined agents may be helpful
in predicting clinical safety hazards.  The duration of toxicity dosing of animals is
usually linked to patient dosing regimens.  Development and validation of in vitro
or whole animal models is encouraged to address concerns regarding short- or
long-term toxicity and to identify surrogate markers for patient
immunocompetence.  
B.  Pharmacokinetic/Pharmacodynamic Strategies
In vivo pharmacokinetic studies should be used to evaluate drug disposition and
metabolism, degree of linearity and accumulation, dose proportionality, and, for oral
dosage forms, food interactions (Peck 1992).  Some of these data can be gathered in a
single study designed to evaluate a number of parameters.  During formulation
development, bioequivalence studies linking formulations may be recommended.  
A particular concern with biological agents is the development of antibodies that may
accelerate drug clearance or alter its distribution, resulting in changes in therapeutic
benefit over time, or following repeated courses of treatment.  To address this
consideration, it is desirable for sponsors to build into their repeat-dose clinical protocols a
coordinated evaluation of drug levels, receptor saturation, antidrug antibodies, and clinical
responses.  Optimally, these assessments would be conducted at the initiation of therapy
and at several time points over the course of therapy.  The presence of antidrug antibodies
and their role in altering drug exposure, clinical activity endpoints, or adverse events
would be evaluated.  The goal of an integrated analysis of these parameters is to provide
data to guide drug dosage or schedule changes to optimize therapeutic benefit.  The best
time for conducting these pharmacokinetic studies is prior to phase 3, before commitments
have been made regarding dose and schedule.
  Because polypharmacy is common during the treatment of rheumatic disorders, in vitro
binding studies with blood from patients with active disease should be used as a
preliminary screening tool for potential displacement reactions.
For products that may interact with rheumatoid factors (e.g., monoclonal antibodies), the
frequency of patients with rheumatoid factor reactive to the antibody, as well as the effect
of interactions on the pharmacokinetics of the product, should be evaluated.
  C.   Considerations in Phase 1 Trials
For general information on clinical development pertaining to most drugs and biological
products, see the CDER guidance General Considerations for the Clinical Evaluation of
Drugs (FDA 1978). 
The term phase 1 has two connotations:  one refers to the earliest, first-time-into-humans
trials, while the other encompasses studies of pharmacokinetics, metabolism, drug
11 interactions, special populations, and the other clinical pharmacology trials as described
above.  It is expected that both kinds of phase 1 trials ordinarily will be conducted during
the clinical evaluation of therapies for RA.  This section is primarily intended to discuss
issues related to the first time people are exposed to the drug (including to a particular
dose level, combination, or duration of therapy).
1.   Settings and investigators
First-time-into-humans phase 1 studies should be carried out in institutions with a
full range of clinical and laboratory facilities, and the patients should be kept under
close observation.  It is desirable that the trials be under the direction of physicians
with experience in early drug development and rheumatology, or that a team of
investigators combining experience in rheumatology and clinical pharmacology be
employed.
2.   Subjects
First-time-into-humans drug trials are frequently conducted in healthy volunteers. 
Such studies are predicated upon the ability to perform and to interpret the results
of preclinical animal tests.  If the preclinical testing does not reveal potential
mutagenic or immune system effects, or potentially serious effects at or near the
expected therapeutic range, testing in volunteers may be initiated.  However, for
products that have potentially serious toxicities, it may be appropriate for initial
testing to be performed in patients with some potential to benefit.  This has created
challenges in selecting an appropriate initial patient population.
For products that have been tested in relevant preclinical toxicity evaluations and
have been found relatively safe (without the potential for mutagenic, immune
system or other serious effects at the proposed doses), trials may be initiated in
healthy volunteers.  However, if significant effects have been demonstrated or
might be possible, selection of an appropriate patient population is necessary.  It is
recommended that patients meet the ACR criteria for both diagnosis and activity of
RA and be without other serious medical conditions.   Patients with minimal
disease are sometimes not appropriate for the same reasons that the testing is not
initiated in healthy volunteers.  Patients with devastating RA may also not be the
best starting population because of the medical complications of their disease.  In
addition, they may be less likely to respond to therapy. 
There is ongoing epidemiologic work on identifying markers of increased risk in
RA.  These could be useful for identifying patients with poor prognoses, who
might be considered for very aggressive treatments of potential high toxicity (e.g.,
immunoablative therapies followed by stem cell transplants).  Application of
epidemiologic studies may allow a very aggressive treatment to be restricted to a
subset of RA patients who have a demonstrated shortened life span due to their
12 disease (e.g., subjects with greater than 30 affected joints or a HAQ score with
fewer than 75 percent of questions answered without difficulty).
When the characteristics of the agent suggest that it may potentially have long-
term gonadal effects, it is desirable that men and women not wishing to parent
children be chosen for phase 1 studies. 
3.  Trial design
Ordinarily, initial phase 1 studies are sequential dose escalation trials, in which
safety and tolerance at a specific dose is established before exposing additional
subjects to a higher dose.  A single dose is almost always tested first, followed by
repeated dose studies; however, this design is influenced by the type of agent used. 
Although escalating the dosage to a clearly determined maximum-tolerated-dose
(MTD) will aid future trial design, in some instances it is not medically prudent to
try to fully characterize the MTD.  Additionally, for some products, an MTD may
be undefinable.
The starting dose chosen is often a no-adverse-effect dose (determined by
interspecies milligrams (mg)/meter square/day dose conversion from animal to
human).  For biologics, the initial dose chosen is often one thought to have no
adverse biological effect, with caution regarding the possibility of relative species
specificity and comparing receptor avidity between test species and humans. 
Conservative dose escalations (e.g., half log or less) are usually recommended.  
4.  Concomitant therapy
Use of low-dose corticosteroids (up to 10 mg prednisone equivalent daily) and
NSAIDS may ordinarily be continued in phase 1 trials.  Concomitant therapy with
methotrexate and similar agents should be avoided in initial phase 1 trials of all
novel antirheumatic drugs, biologics, and devices because of the difficulty of
differentiating the toxicity of the novel agent from that of the co-administered
product. 
Physicians now prescribe methotrexate and similar agents earlier in the course of
rheumatoid arthritis.  Recruiting adequate numbers of patients not taking these
agents may be difficult.  Approaches that may allow the use of methotrexate and
similar agents in later phase 1 trials include (a) obtaining reassuring evidence of
lack of toxicity from relevant animal models in which co-administration occurred
and (b) starting at doses significantly lower than the no-adverse-effect level of the
single agent as determined by earlier phase 1 studies or preclinical studies, or both. 
Such proposals should be discussed in the planning stages with Agency staff. 
5. Observations
13 a.   Safety
The standard batteries of safety observations have been described
elsewhere (ICH S5A 1994).  However, additional types of safety
observations may be necessary (e.g., tests of effects on cellular and
humoral immune function or host defenses).  For products with the
potential for effects lasting long after administration, or for delayed
toxicity, appropriate follow-up should be designed.  For example, phase 1
studies of agents used to deplete or modify the function of T-cell subsets
should be designed to carefully assess both the short- and long-term effects
on number and functional status (e.g., delayed type hypersensitivity
responses) of cell populations and other pertinent pharmacodynamic assays
during therapy and during follow-up.
It is also desirable to incorporate individual patient adverse event
stopping/withdrawal rules into protocol designs.  In addition, it is often
advisable to incorporate into trial designs rules for trial stopping or trial
modification in case adverse events are observed.  For example, dose
escalation rules should be clearly defined in dose-finding studies, with
provisions for enrollment of additional patients at or below the dose-
causing toxicity if possible significant adverse events are observed. 
It is desirable to develop a standardized toxicity grading scale for use in all
trials of a product based on the known and suspected toxicities of the
product or of the drug class.  This may improve consistency of adverse
event reporting and allow more accurate comparisons among trials.
b.  Efficacy   
Developing an understanding of the agent's therapeutic potential in early
trials is highly desirable for efficient product development.  This may be
attempted in phase 1, but can ordinarily be achieved only by performing
controlled trials.  RA responses in open trials are of little value in indicating
efficacy.  Consideration should be given to the more modest goal of
determining whether the pharmacological effect predicted from the
preclinical development is present (proof of concept). 
D. Considerations in Phase 2 Trials
During phase 2, larger, often longer, term trials are employed to better define the dose-
and exposure-related activity and toxicity of the agent.  Enough information should be
generated to ensure that the phase 3 trials can be conducted safely and with a probability
of success.  In addition, phase 2 trials should solidify a total drug development strategy to
ensure that, after the phase 3 safety/efficacy trials are done, all of the information needed
for registration will have been gathered, including an appropriate safety database, clinical
14 pharmacology, dose-response data, the exploration in special populations (e.g., renal
failure, hepatic failure, pediatric patients), and information on drug interaction with agents
expected to be co-administered.  
There is nothing to preclude conducting additional phase 1 clinical pharmacology studies
and phase 2 trials while the phase 3 development is ongoing.  
The following issues are important for phase 2 trials in RA:
1.   Trial design  
Dose finding is a central challenge of phase 2 development.  Once a reasonably
safe range of doses has been established, randomized, parallel-arm dose-
comparison trials are ordinarily recommended.  The use of a placebo arm is
desirable for several reasons.  First, if no difference is found among doses, there is
usually no other way to determine whether all doses were equally effective or
equally ineffective.  Second, if a dose-response trend is found, the placebo arm
may indicate the possible magnitude of the observed effect.  If use of a placebo is
impossible, designs should include wide dose ranges or durations, or repetitions. 
Active controlled designs that specify an arm with a well-characterized, known
therapy can also be very useful.
Signs and symptoms measures may be used for dose-finding studies, but it is
possible that separate dose-finding studies may be needed for longer term
endpoints.
For agents that are thought to have prompt onset and rapid offset of effect,
alternative designs, including crossover and titration designs, may be useful,
although historically this has not been the case.  Trials of two or more doses that
permit liberal titrating per the patients' responses are unlikely to clearly
demonstrate a dose response because these titration designs result in a blurring of
any existing dose distinction. 
The desirability of identifying a range of doses with acceptable toxicity and
reasonable activity for study in phase 3 cannot be stressed enough.
2.   Safety  
Every RA investigational therapy raises safety concerns.  Whenever there is a
potential for significant toxicities, long-lasting or delayed-onset, it is desirable to
design the phase 2 studies to provide a group of patients with longer term follow-
up preceding the larger phase 3 studies.  Provisions for long-term follow-up can be
helpful in addressing issues raised during premarket review (e.g., potential for
immunosuppression, opportunistic infections, neoplasia, and induction of
15 autoimmune disease).  Standard toxicity grading scales and stopping rules are also
desirable in phase 2.
3.   Additional development aspects
a.   Concomitant therapy
Before starting phase 3 trials, an evaluation of the test product's interaction
with other agents likely to be used by the target population should be
performed.  Initial information can be established based on metabolic
pathways, studies of in vitro systems, animal or human pharmacology
studies, or drug interaction studies.  This type of information helps in
directing areas in need of clinical evaluation.  When products are intended
to be tested as combination therapy with the investigational agent,
substantial information on interactions and safety of co-administration
should be developed in phase 2.
b.   Gender effects
Most RA trials have predominantly female enrollment.  Sponsors should
evaluate whether the observed safety and efficacy findings are restricted to
women or can be also extrapolated to male subjects.  This may be
accomplished by subset analyses from trials, PK data, or other information
(FDA 1993).  
E.   Efficacy Trial Considerations
The overall goal of phase 3 work is to demonstrate the efficacy of the product in
convincing controlled trials and to accrue a sufficient safety database.  Efficacy trial
protocols should contain an analytical plan that precisely identifies the primary
comparison(s) to be made, the criteria for success of the trial, and the statistical tests that
will be used. Protocols should be designed to generate data that support desired labeling
claims.  Any additional planned, ongoing, or completed trials that are also intended to
generate data supporting the claim should be identified. 
1.   Global considerations
          a. Patient selection 
Activity of disease:  Unless some other specific subgroup is targeted,
patients enrolled in efficacy trials should at a minimum meet the disease
definition and disease activity as defined by ACR criteria.  Consultation
with the Agency on the generalizability of claims derived from trials with
significant limitations on entry criteria is recommended. 
16 To enhance the power of the trial, strategies to improve the chances of a
response to therapy are often employed.  Some designs incorporate an
attempt to select active patients by withdrawing background treatment and
allowing patients to flare.  Only individuals with sufficiently high scores are
enrolled.  The relevance of this type of observed flare is questionable, and
its ability to predict the normal course of active disease has not been
established.  Many patients randomized to placebo in such studies exhibit
the characteristic response of rapidly returning almost to baseline without
further treatment.  In addition, when patients undergo blinded withdrawal
from therapy within these trials, similar dramatic flares are not observed. 
This raises the question of whether there is an expectation bias on the part
of patients, who have been told about the flare procedure, and
ascertainment bias on the part of investigators, who wish to have patients
meet the entry criteria and enroll in the study.  These uncertainties and
instabilities around the outcome measures used in such trials should be kept
in mind when employing these designs.
A proportionately smaller, but nevertheless noticeable and prompt,
regression to the mean is noted in the joint scores of patients required to
have a certain minimum value for trial entry in trials not employing a flare
strategy.  This means that patients, on the whole, will not actually have
disease as active as anticipated when the entry criteria are set. 
Subgrouping patients by disease markers:  RA is likely composed of a
number of more or less distinct diseases delineated by a common genetic
background, corresponding clinical manifestations, similar serologies, and
responses to therapy and prognoses.  The study of RA possibly may be
made more efficient with the use of markers with clear prognostic
significance as entry criteria to increase patient homogeneity.  Novel
epidemiologic and molecular genetic approaches may lead to identification
of even more subgroups.  However, prospective studies are first needed to
confirm the clinical usefulness of new purported prognostic factors.  Where
existing data do support markers as prognostic indicators (risk factors),
such as the presence of rheumatoid factor, erosive or vasculitic disease, and
DR4 homozygosity, they can be taken into consideration in the design of
trials, as can factors known to affect treatment responses.  Although in
some cases such studies could limit generalizability and impact labeling of
the final product, it is also possible that such targeting could improve the
risk/benefit profile. 
     b. Concomitant antirheumatic therapy
 
Studies in RA patients, except in those with very mild disease, are carried
out in the presence of concurrent active therapies, including steroids,
NSAIDS, hydroxychloroquine, etc.  This concurrent therapy creates
17 numerous challenges in patient selection, toxicity monitoring, and clinical
trial design.  For example, since methotrexate therapy is used to treat many
RA patients, it is inevitable that new agents will be used in combination
with methotrexate in clinical practice unless a contraindication exists. 
Therefore, unless a prohibition on concurrent methotrexate is supportable,
data regarding use of the investigational agent in combination with
methotrexate are needed to evaluate the potential for immunosuppression
from combination therapy.  Other agents should be similarly evaluated.  
In addition, patients can be categorized according to their prior responses
to standard therapy.  Varying trial designs may help assess the response of
different response categories to an investigational therapy.  For example,
with respect to methotrexate use, the RA population can be divided into
five groups:  (1) methotrexate noncandidates  disease too mild or too
early for methotrexate; (2) methotrexate candidates  disease sufficiently
(or will become sufficiently) active to justify methotrexate; (3)
methotrexate successes  disease reduced to negligible amounts; (4)
methotrexate failures  clear drug failures, for inefficacy or tolerability,
and (5) methotrexate partial responders  with considerable residual
disease despite methotrexate.  Each of these groups might be considered
separately for candidacy for an investigational agent and with respect to an
appropriate trial design.  If only a subpopulation of RA patients (e.g.
methotrexate nonresponders) is studied in a particular trial, the results
strictly reflect efficacy in that group only, but they may, of course, imply
something about efficacy in other groups.  Single trials in various responder
subpopulations could be supported by positive results in other
subpopulations.  Any planned subpopulations should be clinically
distinguishable.  Sponsors should consult Agency personnel when planning
a clinical development program contemplating an RA claim that is limited
to a subpopulation with the disease.
   
c.   Other concomitant therapies
Most patients with RA are taking concomitant medications.  Use of
medicines unlikely to influence treatment outcomes (e.g.,
antihypertensives) should simply be recorded, although investigators should
be alert for possible drug interactions.  Obtaining information during
clinical development on co-administration of the test medication and
expected concomitant medications is desirable.  The following approaches
may be considered in dealing with arthritis medications or analgesics.   
Prohibit use:  This strategy may result in noncompliance or an increased
number of dropouts.
18 Incorporate protocol-specified use, with monitoring:  With this strategy,
additional analgesic use (and possibly other arthritis medications) may be
used according to protocol-specified criteria.  In addition, for long duration
studies, protocols should address (1) whether intra-articular steroids are
permitted and, if so, for how long assessments of the involved joint are
excluded from analysis; (2) the manner in which stress doses of
corticosteroids for surgery, etc., are to be handled; and (3) how soon after
such doses protocol assessments would be allowed.
Design analgesic use, or its quantitative consumption, as (part of) an
efficacy endpoint.
Define use of more arthritis treatments as (part of) an efficacy endpoint.
     d.   Stratification
Randomization is intended to balance populations for confounding
variables; however, there is always a chance that randomization may fail to
achieve balance, particularly in smaller trials.  It may be advisable to stratify
known (or highly suspected) major risk factors to ensure their balance
across arms.  Any factor whose influence on the outcome is suspected to
be as strong as the treatments influence should be considered for
stratification (e.g., erosive disease, presence of rheumatoid factor).  An
often overlooked risk factor is the patient's past therapeutic history.  (See
statistical section for further discussion.)
e. Blinding
Because most RA outcome measures have a high degree of subjectivity,
the highest confidentiality in patient and assessor blinding should be sought
to achieve a credible inference.  Blinding may be compromised if there is
not an approximate parallelism in time to onset, nature of response, and
toxicity profile between active and controlled interactions.  Trials should
have parallel (e.g., double dummy) dosing in all arms when possible so
that a drug requiring frequent dose manipulations does not threaten the
blind.  If arm specific treatment adjustments are necessary (e.g., per
monitored drug levels), these can be done by an unblinded (and
sequestered) third party to maintain patient and assessor blinding.  In this
case, parallel changes should be made as dummy adjustments in the control
arm to preserve blinding.  Similarly, if the blind is likely to be compromised
by infusion-related events or other features of the treatment protocol,
critical treatment endpoints, such as joint counts, should be assessed by an
independent party with no knowledge of the subjects history.
f. Effects of dropouts and noncompliance.  
19 It is important that trials be designed to minimize dropouts and the
attendant information loss.  Traditionally, recommended RA trial designs
have focused on eliminating sources of variability, for example, extra pain
medications, and intra-articular injections.  Often, these interventions were
defined as major protocol violations, requiring that the patient be dropped
from the study.  There is a trade-off between patient retention and
tolerance of variability in RA trial design.  Protocols demanding rigid
adherence may yield uninterpretable results because of dropouts and
noncompliance emanating from patient and investigator intolerance of the
requirements.  On the other hand, protocols permitting any kind of
additional intervention may likewise be so confounded as to defy
interpretation.  
The following strategies may help minimize loss of information:
i. Use screening or run-in periods so that patients are randomized to
treatment groups only after their eligibility and commitment are
confirmed.
ii. Thoroughly train investigators and study personnel to minimize
inappropriate enrollments, protocol violations, and other deviations
that would decrease the ability to assess trial outcomes. 
iii. Include dropouts in the definition of the endpoint, as in a time to
defined treatment failure, or a defined by-patient success or failure. 
A sufficiently late time point should be chosen as the endpoint to
avoid the situation where the time course for response differs
between two active therapies in a trial, which can introduce bias.
One example of this approach would be to use a protocol-defined
response rate as the primary endpoint, wherein dropouts due to lack
of efficacy are classified as nonresponders.  With this type of
endpoint, the criteria for classification as a nonresponder should  be
clearly and prospectively defined.  The use of this type of endpoint
could be justified in situations where there are robust phase 2 data
suggesting drug responsiveness at a defined point after initiation of
therapy and durability of that response.  In this case, one could
define the primary analysis as a comparison of the proportion of
patients with an ACR 20 response at six months.  The protocol
could specify that if no improvement compared to baseline were
seen on two consecutive study visits after two months on protocol,
the subject would be declared a nonresponder.  Experience will
determine whether this approach effectively limits information loss
due to dropouts.
 
20 iv. Make provisions for following patients who have stopped
experimental treatment.  Options include allowing a
protocol-specified crossover to a standard therapy for patients
meeting predefined criteria for treatment failure.
v. Allow more flexibility in treatment options during the study.  Some
designs that have been used include allowing dose adjustment of the
comparator arm (assessor and patient blinded), allowing add-on
therapy for patients meeting predefined criteria for inadequate
response, and allowing a limited number of joint injections, with
elimination of that joint from assessment.
2. Trial designs in RA
Clinical trials in RA can be designed in a variety of ways.  More than one claim can
be pursued in the same trial, and claims can be submitted singly or together.  Trials
can be designed to test a difference  demonstrating that the investigational
product is superior to control (placebo, lower test dose, another active agent), or
they can be designed to test no difference  demonstrating that the product is
adequately similar in efficacy to active control.  Placebo-, dose-, concentration- or
active-controlled designs can be used.
Because the persuasiveness of trials showing a difference is, in general, much
greater than that of equivalence trials, it is highly desirable for a claim to be
convincingly demonstrated in at least one trial showing superiority of the test agent
over placebo or active control.  If a claim of superiority over a specific comparator
is sought,  rather than just straightforward efficacy, the claim should be
substantiated by two adequate and well-controlled trials showing superiority.  Such
trials can also be the basis for demonstrating the product's efficacy.
a.    Superiority trials  
The standard two-arm, investigational agent versus placebo design has
been the most common RA design and is the most straightforward.  The
details of trial design will depend on the population tested.  Patients with
mildly active RA taking only NSAIDS, who have never been treated with
an additional class of therapy, may be enrolled in a placebo-controlled trial
with continuation of NSAID background therapy; however, patients doing
poorly on NSAIDs alone are usually not appropriate candidates for
placebo-controlled trials.  The same considerations apply to patients who
are partial responders to, or who have failed, various other treatments.  
Alternatives to the two-arm difference design are a standard dose-response
study and a superior-to-active-control hypothesis.  These designs may
21 accommodate the need to provide active treatment to patient groups where
randomization to placebo is infeasible.
b.   Equivalence trials
Equivalence trials are designed to demonstrate that the test drug is
adequately similar to an active control.  This is done using a prospectively
defined equivalence test, specifying to a 95 percent confidence level that
the real difference between test and control is smaller than some
predetermined amount.  Achieving similar point estimates of efficacy of
two agents is not a demonstration of equivalence. 
Equivalence trials can serve two purposes.  First, they can be used to
supply evidence for a simple efficacy claim.  Second, they can be used to
pursue a specific equivalence to drug X claim.  Both purposes could also
be pursued in the same trial.  The important point to note is that the
strength of the evidence may need to be stronger for a claim of
equivalence to drug X than for a simple efficacy claim.  Thus, the
equivalence test may differ, depending on which claim is intended. 
Currently, the equivalence standard that is appropriate for a given trial in
RA will be determined on a case-by-case basis.  As noted above, this test
may be more stringent if a claim of equivalence to drug X is being pursued. 
Additionally, the test of equivalence may be constructed differently if a
placebo arm is present, since the presence of the placebo allows estimates
of absolute and relative drug effect size.
In either case, the statistical test for equivalency needs to be quantitatively
described in the protocol.  Under either the pursuit of a simple efficacy
claim or the pursuit of a specific equivalence to drug X claim, the basis of
the decision on an appropriate test remains, fundamentally, a clinical one. 
It represents a consensus, in that particular circumstance and for that
particular claim, on what small potential difference can be considered
clinically insignificant, to allow the treatments to be considered clinically
equivalent.
 
There is considerable experience in the interpretation of active-controlled
trials in clinical situations where the response to the intervention is high. 
As an example, antibiotics are evaluated by the Division of Anti-Infective
Drug Products (CDER, FDA).  For these products, the magnitude of the
potential difference permitted in an equivalence determination depends on
the response rate of the standard treatment.  For example, a new agent
being compared to standards with response rates of 90 percent or more will
be allowed a 10 percent window to provide confidence that the difference
between the standard response rate and the test response rate is no more
than 10 percent.  Technically, this means the 95 percent confidence interval
22 of the difference must lie fully to the right of 10 percent.  If the standard
treatment is known to have an 80 to 90 percent response rate, a 15 percent
window is used.  These equivalence tests were designed for trials without a
placebo arm and for clinical situations where the placebo response is
known to be very low.
 
Treatment response rates in RA are often in the vicinity of only 50 percent
(depending, of course, on the endpoint used) with placebo rates of about
20 percent, so the clinical decision for an allowable small difference may
differ from that with antibiotic therapy.  At this time, the decision will have
to be individualized for each trial.  
A major problem in equivalency trials lacking a placebo arm is ensuring
that both treatments are equally effective, rather than equally ineffective.  A
number of the agents that are approved for RA have fairly small effects and
may fail to show efficacy when tested against a placebo.  Comparative
trials intended to show equivalence to such treatments, when not anchored
by a placebo control group, may lack credibility.  Thus, it is desirable in
equivalence designs to select highly effective comparative agents.  If
possible, use of a third (placebo or lower dose) arm, so that a treatment
difference can be shown, is a desirable strategy in equivalence trials.  This
arm would not necessarily have as many patients or as long a duration as
the active comparators.  If a placebo arm is present, both the test and
active arms need to statistically exceed placebo for a finding of equivalence
to have meaning.
Strict attention to numerous aspects of trial design and conduct are
important to ensure accurate inferences from equivalency trials.  Design
decisions regarding patient population, dosing, and efficacy and safety
assessments should be done in a manner that is unbiased against the control
to ensure a fair comparison.  Furthermore, attention to certain problems in
trial conduct, such as minimizing dropouts, noncompliance, and missing
data is essential to the reliability of the inference.  These aspects of trial
conduct may obscure differences and lead to a false conclusion of
equivalence.  This is the opposite of their effect in a difference design to
show superiority, where they work against trial success. 
In any particular development, the choice of trial design depends on many
factors.  Since controlled evidence showing a difference is more persuasive
than that showing equivalence, greater efficiency (fewer patients or shorter
exposures) is available with development strategies using trials employing
maximal differences between trial arms.  Optimally, this means placebo
controls, with the requisite background therapy, given to all patients. 
c.    Trial designs novel to the study of RA
23 Although not used traditionally in the study of new RA treatments, the
withdrawal design can be considered in certain circumstances.  The
withdrawal design is sometimes used to assess efficacy.  In this design,
patients in both arms of a study are treated with the investigational agent,
which is then blindly withdrawn from one arm, after which patient
outcomes are compared.  Showing that patients taken off the
investigational drug get worse demonstrates effectiveness.  Natural
endpoints for withdrawal designs are time to (predefined) worsening using
standard time-to-occurrence statistical tests or a simple comparison of
proportion of outcomes in the two arms.  Withdrawal studies may be
performed with both arms on background therapy.
There are a number of caveats about withdrawal designs.  If the product is
very toxic, so that only a small (tolerant) subset of the original population
remains at the end of the trial and is available for the double-blind
withdrawal phase, the generalization of any inference from the withdrawal
design is limited to that tolerant subset.  Additionally, it should be noted
that, if a drug induces habituation or tolerance, withdrawal or rebound
phenomena may make withdrawn patients worse even though drug therapy
did not have a beneficial effect. 
  
3. Analytical Issues
a.   Handling dropouts  
Historically, RA trials have suffered from information loss due to dropouts. 
Dropouts probably never occur randomly, and rarely occur fully
independent of the treatment being tested, so there is always the possibility
that dropouts introduce a bias.  This problem is common in many
randomized trials.  Methods for analyzing the effects of dropouts have been
proposed, but none is fully adequate. 
The problem of dropouts is not resolved by using an intent-to-treat (i.e., all
randomized patients included) analysis with an imputation by last-
observation-carried-forward (ITT/LOCF) or by showing that both the
ITT/LOCF and PP/OC (per protocol completers/observed cases only)
analyses concur, although these approaches may increase confidence in the
results.  It should also be noted that there are other methods of modeling
missing data, for example, see Little and Rubin (1987).   Such modeling
methods require assumptions that are nonverifiable by existing data.
The effects of dropouts should be addressed in all trial analyses to
demonstrate that the conclusion is robust. One trial design approach is
following all patients, including dropouts, to the planned trial endpoint,
even if postdropout information is confounded by new therapy, and
24 performing an analysis including these patients.  Another approach involves
the worst case rule:  assigning the best possible score to all postdropout
placebo patients and the worst score to all postdropout treatment patients,
then performing an analysis including these scores. 
b.   Comparison to baseline outcome measures
A phenomenon frequently observed in RA, as well as in other conditions, is
that patients who stay in trials do better than those who drop out: 
responders do better than nonresponders.  This is true both for placebo
groups and active treatment groups.  If observations of the disease were
made exclusively from clinical trials, one might conclude that the natural
history of the disease is inexorable improvement.  This phenomenon is
attributable to preferential dropout of worsening patients (a phenomenon
not adequately compensated for in LOCF analysis) as well as regression to
the mean.  The problem is exacerbated in flare designs, where all patients
have major improvement regardless of treatment status.  This fact makes
comparison-to-baseline outcome measures difficult to assess, since, very
often, much of the improvement noted has no relationship to a treatment
effect.  For these reasons, active-controlled trials not incorporating a
placebo arm and using comparisons to baseline may be extremely difficult
to interpret, especially if a flare design is employed.  In any case, success in
any trial implies improvement over control.
4. Statistical Considerations in Efficacy Trial Design
It is advisable to discuss the design and analysis with the FDA review team prior to
embarking on a study.  In addition, FDAs Guideline for Format and Content of
the Clinical and Statistical Sections of New Drug Applications (1988) contains
useful information.
a. Randomization/stratification
Randomization is intended to allocate patients to treatment groups to avoid
bias and to ensure that statistical procedures can be appropriately applied.
In some clinical trials, there are known factors that are at least as influential
in controlling the observed severity of disease as the drugs being studied. 
Stratification may be  used to avoid relying on randomization properties to
balance patient assignment for these factors.  Stratification is implemented
by constraining simple randomization to balance the assignment of patients
to treatment groups for the chosen stratification factors.  
Every phase 2 and phase 3 study protocol should contain a randomization
section.  All constraints imposed on the randomization should be explicitly
25 identified.  It can then be inferred, when a stratification factor or sample
size allocation constraint is not mentioned in a protocol, that there exists no
corresponding randomization constraint.  This applies to whether patients
are blocked to balance treatment assignment for time of patient entry into
study and to the more obvious stratifications on center and baseline.  
Because stratification implies constraints on randomization, studies that
have been stratified for certain factor(s) should account for these factors in
the statistical analysis section.  The protocol-defined analysis should be
implemented for each study.
There are also statistical procedures to address bias in treatment group
comparisons by adjusting for factors (covariates) that, like the stratification
factors, are to be prespecified in the protocol or by using a mechanism to
determine a fixed number of covariates prespecified.  It is important to
prospectively identify covariates (or criteria for choosing covariates) in the
protocol.  In addition, statistical adjustment procedures should be used
with care and include appropriate verifications of assumptions.
In deciding whether to stratify randomization in all clinical trials, practical
judgment is required.  There are reasons to choose stratification and
reasons to choose statistical adjustments.  
The first advantage of stratification is that it avoids possibly major
statistical adjustments of differential treatment effects.  Stratification would
essentially eliminate the effect of such adjustments before analysis began. 
Second, although stratification and statistical adjustment procedures are
both designed to remove bias in estimated treatment effects, stratification is
usually more powerful.  This is because stratification leads to smaller
variances of estimated treatment effects than does statistical adjustment
without stratification.  Finally, the inclusion of stratification factors into a
statistical analysis model should result in increased power to detect
effectiveness.
Stratification becomes increasingly clumsy as the number of strata increases
and, consequently, the available number of randomizable patients per cell
decreases.  In this case, it is logistically simpler to not stratify, but to rely
on statistical methods to adjust for these factors.  
The best approach may be to combine stratification, applied to a limited
number of the most influential prognostic factors, with statistical modeling. 
This protocol-defined statistical modeling would both account for
stratification and be used to adjust for the effects of a parsimonious number
of the most important remaining factors.
26 b. Identification of primary efficacy variables  
Each phase 2 or phase 3 study protocol should identify the primary and
secondary efficacy variables.  Primary efficacy variables are critical to the
identification of the effectiveness of the product.  Secondary efficacy
variables are those that support the validity of the primary variables but are
less critical in deciding if this product is effective.  It is helpful, but not
necessary, that statistical evidence of efficacy be shown for secondary
efficacy variables.  
c. Prespecification of statistical analysis
Statistical analysis of clinical endpoints is part of the process for obtaining
consistent and convincing evidence of product efficacy.  These statistical
analyses should not be data driven.  This is implemented by identifying, in
each study protocol, before data are available for analysis, a sufficient
description of the statistical analyses of primary efficacy variables so that an
independent statistician could perform the protocol analyses.  A brief
description of the statistical analyses should include but not necessarily be
limited to specifying:  (1) the level of significance to be used; (2) whether
statistical tests of hypothesis or confidence intervals will be 1- or 2-sided;
(3) whether interim analyses are planned and, if so, how the tests of
hypotheses and confidence intervals will be adjusted to account for interim
looks at the data; (4) the mathematical expression of the statistical model(s)
used; (5) the minimal statistical results needed to demonstrate a successful
outcome; (6) the treatment of missing values and dropouts; (7) the method
used for controlling type I error rates for multiple primary efficacy
variables; and (8) the method used for making multiple treatment
comparisons.
d. Multiple endpoints
There has often been a clinical argument for using multiple endpoints to
assess primary evidence of effectiveness in RA.  The theoretical bases for
such combination endpoints are the focus of an area of ongoing statistical
research.  For example, for the four measures recommended in FDAs
previous guidance (FDA 1988), trial results were considered to support a
conclusion of effectiveness when statistical evidence of efficacy was shown
for at least three of the four measures:  physician global assessment, patient
global assessment, swollen joint count, and painful joint count.
Multivariate statistical methods are also available for analyzing the set of
primary efficacy variables.  Procedures are being developed for inferences
derived from multiple endpoint results.
27 Efficacy variables can be combined within patients (composite endpoint). 
Such a fixed combination of efficacy measures should be well defined in the
study protocol.  Composite efficacy variables have the advantage of
avoiding several statistical and inferential difficulties associated with
multiple endpoints.
e. Dropouts
Dropouts are patients who, after a certain period of time in a trial, fail to
provide clinical efficacy data scheduled to be collected by the protocol. 
Frequently, dropouts occur for reasons related to taking the assigned test
drug (adverse effects or lack of efficacy).  Since dropouts do not usually
occur randomly, the remaining patients constitute a biased subsample of the
patients originally randomized.  Unless trial dropouts can be assumed to be
random (which is rare), no model used to impute their effects can be
verified.
Methods used to handle dropouts, such as LOCF and completers analyses,
are not fully satisfactory even though they have often served as the basis
for determining that adequate statistical evidence of efficacy has been
provided.  The LOCF method usually does not preserve the size of the test,
either for the comparison of final observations or for the comparison of
rates of change.  Alternative methods include growth curve analysis and
random effects regression.  These are also susceptible to informative
censoring  that is, dropping out depends on the value of the response.  It
is often useful to show that the results hold for a variety of analyses (i.e.,
they are robust).
f. Trials with several treatment groups/multiple comparisons
In clinical trials involving more than two treatment groups, a statistical
multiple comparison procedure controlling the experiment-wise error rate
to 5 percent or less should be applied.  In essence, there should be overall
statistical evidence of a treatment main effect before attempting to make
specific drug comparisons relevant to proposed drug labeling.  
g.  Trials simultaneously used to pursue more than one claim
A single trial can be used to pursue simultaneously more than one claim; an
adjustment of significance level for multiple analyses is not always
necessary.  If the order of testing the hypotheses is prespecified, then no
penalty need be taken.  For example, when a trial is simultaneously
pursuing a six-month signs and symptoms claim and a twelve-month x-ray
claim, if the trial wins by the first hypothesis tested  signs and symptoms
28  then the x-ray hypothesis can be calculated without an  adjustment
penalty.  
h. Interim analyses
Interim analyses are those that, for any purpose, are repeatedly performed
on accumulating clinical trial efficacy data.  Methods have been developed
to compensate for the fact that multiple tests (including interim analyses)
alter the true significance level.  The study protocol should state whether
such interim analyses are planned or not.  Should interim analyses be
planned, the plan and its implementation should be described in the
protocol. The description should include who will have access to the
interim data, the scheduling of these interim analyses, the method to be
applied for adjusting significance levels, and the corresponding time
sequence of significance levels at which statistically significant results will
be claimed.  
Although an interim analysis may not be thought to affect the subsequent
collection of efficacy data, interim analyses carry the additional risk that the
blinding or conduct of a study may have been compromised. Statistical
methods cannot compensate for any unblinding and bias that may result
from gathering the information needed to perform an interim analysis. 
Finally, if any major protocol change becomes necessary (e.g., a new
therapy becomes available), it is important that such a change not be
influenced by those unblinded to data.
i. Sample size
Failure to recruit an adequate number of patients is a major reason why an
effective product may fail to meet established statistical criteria for efficacy,
independent of whether the purpose was to show superiority or
comparability of treatment effect.  The method for determining the sample
size should be stipulated in sufficient detail to permit independent
verification of the computation.  This should include identifying the efficacy
variable that the sample size determination is based on, the magnitude of
the hypothesized clinical difference, the standard deviation, the power, the
significance level, and the sidedness of the statistical procedure(s)
described in the analysis plan.  Furthermore, the size of the clinical
difference chosen should be justified, and the rationale for the choice of the
efficacy variable used to determine sample size should be discussed.  For
comparability from one trial to the next, it is optimal to use the same
efficacy variables as were used to power earlier studies. 
j. Trials to show clinical equivalence
29 The words clinical equivalence are used in a much narrower sense than
these words might imply to the casual reader.  First, there is often no intent
to show equivalence of two or more drugs across the broad spectrum of
pharmacologic effect.  Rather, focus is on showing no clinically relevant
differences for one or possibly more variables that are to be clearly
identified in advance.  The concept of equivalence is two-sided in that if,
for any outcome measure, one drug is sufficiently different from another
drug, then these drugs are no longer deemed equivalent in that variable.
  
To show equivalence, the variables serving to measure these effects of
interest should be defined in the protocol.  For each efficacy variable for
which clinical equivalence of effect is sought, the magnitude of a difference
deemed to be inconsequential should be identified.  The clinical data should
then show, with 95 percent confidence, that this predefined difference is
not exceeded.  
Inference based on trials to show equivalence is inherently less convincing
than inference based on trials to show the existence of a difference.  Often,
clinical trials do not detect treatment differences that are known to exist. 
In such cases, statistical methods may then seemingly provide evidence of
equivalent effect (e.g., to placebo).  
        
k.  Appropriateness of the statistical methodology
The appropriateness of the statistical model should be assessed, including
checking for outliers and determining if distributional assumptions (usually
normality) are met and if common variance assumptions hold.  
l.  Site effects
If the patients have been stratified and randomized by site, the analysis
should include a site effect.  There may be a site-by-treatment interaction
reflecting the degree to which the treatment varies across sites.  This is
often notable when there is a great variation in enrolled patients across
sites.  Site-by-treatment interaction should be explored. 
F.   Safety Analysis
The approach to evaluating adverse event data and laboratory values has traditionally
differed from that used to evaluate efficacy.  The purpose of safety evaluations is usually
not to test a specific hypothesis, but to examine the pattern of effects and to detect
unusual or delayed events.  Analyses using cumulative occurrences, scatter-plots of
laboratory values (baseline versus on-therapy), or other techniques may be helpful.  The
safety profile should address to what extent adverse events (drug reactions or lab values)
depend on duration of drug exposure, dose level, coexisting medical conditions, or
30 possible drug interactions.  Incidence rates should be calculated using denominators that
reflect the period of drug exposure for the population at risk.  Cumulative incidences
(hazard rates, instant probabilities) do a better job representing the temporal pattern of
drug effects than do prevalence rates; comparative cumulative incidence tables  drug
versus active control(s), versus placebo  also are very helpful to practitioners.  Critical
incidence rates should be described with 95 percent confidence intervals.
Ensuring safety during the development of a drug, biologic, or device can be optimized by
adequate preclinical evaluations and the development of a standardized clinical safety
assessment system.  Elements of a successful safety assessment system include the use of
predefined standard terminology (such as the Medical Dictionary for Regulatory
Activities Terminology) and criteria to define and assess adverse events (AEs), approaches
to optimize AE detection, and appropriate safety stopping rules in trials.  It is also useful
to capture AE severity (grades 1 [mild], 2 [moderate], 3 [severe], or 4 [life-threatening]),
outcomes (such as the need for therapy and whether resolution or death occurred),
treating physician assessment of association with study agent (remotely, possibly, or
probably related), and impact on the trial (none, dose of agent delayed or changed, or
patient withdrawn from further therapy).  Stopping rules, determined by the risk/benefit
ratio for the agent in the study population, are desirable both for individual patients (a
single grade 3-4 AE is often used) as well as for the clinical trial, especially in dose-
escalation studies.
 
1. Intrinsic trial design considerations
An attempt should be made to characterize the patient population susceptible to
adverse drug effects.  Some extraneous factors, such as variations in soliciting and
reporting adverse events among the investigators and differences in the definition
of normal ranges for lab values among different laboratories can complicate the
safety data.  Since adjustment for their effects may be difficult, precautions should
be taken in the design stage of the trial to minimize the influence of these factors
by preparing clear and specific instructions for data collection and monitoring
adherence of the investigators and the laboratories to the protocol.  Procedures for
normalizing laboratory data, for example, may be employed.  As previously
mentioned, developing standardized toxicity grading scales that can be employed in
all studies may also be useful.
2. Adequate numbers
The ability to detect adverse experiences is dependent on the number of patients
evaluated in the clinical trials and in clinical usage.  In studies of 300 or more
patients having adequate exposure to the investigational drug, it is expected (with
95 percent confidence) that at least one patient will manifest an adverse event
having an incidence rate of 1 percent or greater.  Smaller studies fail to meet even
this minimal incidence detection standard.  In most cases, however, it is possible to
combine studies of equal duration to establish adverse experience rates.
31 For any chronically administered product, the safety database should include at
least 300 patients treated with the maximally recommended dose for at least six
months and at least 100 patients treated for at least twelve months (ICH E1A
1995).  Larger and/or longer safety databases may be advisable for agents with
known or potential safety problems.
IV.  SPECIAL CONSIDERATIONS FOR BIOLOGICAL PRODUCTS 
Although there are similarities between RA trial designs for drugs and biologics, biologics have
special characteristics and problems that should be considered in their development.  
A.  Species Specificity 
The schemes used traditionally in determining the initial human dose may not pertain to
biologics.  Biological agents may behave differently in animal models than in humans,
depending on the physiologic relevance and avidity for the receptor of the ligand in the
animal compared to the human.  Immunogenicity may also be species specific.  
B.  Dose Responses
The dose-response curve may be steep and/or even hyperbolic, and an agent can be quite
toxic at levels just above those thought to show efficacy.
C.  Toxicity Response
The toxicity response may be highly unpredictable and potentially very dangerous and may
include the risk of disease worsening.  Agents may have narrow therapeutic windows. 
Biologics have the potential for disruption of immunologic and physiologic processes. 
Monoclonal antibodies to cellular epitopes of the immune system, for example, or to TNF
receptors may cause serious morbidity at doses only slightly higher than those that are
efficacious with markedly less toxicity.
D.  Product Homogeneity 
This often plays a critical role in activity and toxicity of a compound.  Product alterations
can greatly affect physiologic activity.  Thus, biologics should demonstrate lot-to-lot
consistency to the extent possible while under development and be reasonably well
characterized to be properly evaluated. 
E. The Role of Antibodies 
If phase 2 data suggest that agent-induced neutralizing antibodies could interfere with the
efficacy of a biological agent over time, it may become necessary to formally investigate
32 the possibility in a randomized-controlled setting.  The occurrence of neutralizing
antibodies may call for the reconsideration of doses and dose regimens.  Non-neutralizing
antibodies may have a profound effect on PK and may therefore be just as important as
neutralizing antibodies.
  
V.  SPECIAL CONSIDERATIONS FOR MEDICAL DEVICES
A. Background
Medical devices used in the treatment of RA vary considerably in their therapeutic impact,
ranging from primary therapy for a specific affected joint to products used as adjuncts to
primary therapies such as the use of ultrasound or heat for symptomatic relief in
conjunction with pharmaceutical therapy.  Variability in therapeutic effects due to disease
and response heterogeneity may be exaggerated with some devices because treatments are
often targeted to a single or a few joints per patient.  
Preclinical requirements for devices include assessment of data from a diverse range of
tests, including, for example, tests that evaluate chemical composition, mechanical
reliability or the electrical properties of a given device.    Each product type has an
identified battery of tests that are evaluated to ensure that the design of the specific
product is well understood and can be expected to have the intended effect on patients as
described in its labeling.
The design of clinical trials in RA for a device may raise some unique issues uncommon in
pharmaceutical trials.  The interaction between treated and untreated joints as it affects
functional and quality of life assessments is just one example of these issues.  Selection of
an appropriate control often poses difficult questions when the active therapy under study
is an implant and the available controls are more systemic in activity.  Understanding how
to design these trials, analyze the data, and assess the contribution from each therapy can
be challenging.  
B. Efficacy Considerations
1. The selection of a control group may be quite challenging with devices because
masking for the patient and investigator is frequently impossible and a placebo may
be infeasible.  Because historical controls are often unsatisfactory and evaluating
the equivalence of local therapy to a systemic active control poses problems,
innovative trial designs are often needed.  Some innovative options include
randomization to early versus late device interventions, or rescue interventions
following failure of pharmaceutical interventions.  Although the use of a sham
(placebo) device is the most desirable control for many products evaluated for RA,
it may be inappropriate if the subject device is implanted.  Additionally, the success
of patient and/or physician masking with such shams may not always be complete. 
Patient masking is infeasible if the product requires a surgical or other invasive
33 procedure.  However, in some cases it is possible to achieve evaluator masking for
the effectiveness evaluation.  
2. For devices intended for use as adjunctive therapy, approaches and analysis
methods should be designed to account for differences in disease status and
severity to minimize potential biases in outcome measures.  One approach is to
have a consistent primary therapy with a named pharmaceutical to avoid
confounding the analyses.  The use of additional, potentially confounding co-
therapies (hot/cold treatments, splinting, physical therapy, and orthotics) also
needs to be appropriately addressed during the study design phase.
3. The use of quality of life (QOL) assessments is very important where devices are
intended for rehabilitative purposes.  QOL benefits for the intervention should be
judged with tools chosen for their validity, ease, and convenience of administration
and the ability to address both improvement in QOL and product satisfaction. 
These assessments should be kept masked from the independent effectiveness
evaluator to avoid assessment bias.
4. In the case of invasive devices necessitating in-hospital or in-office use, it is
recommended that clinical assessments include convenience in use and pain or
discomfort in administration.   Early assessment of this aspect of therapy can
provide critical information on the ultimate acceptability of the treatment and affect
decisions as to whether to pursue a treatment modality.
C. Safety Considerations
1. Obtaining well-characterized, short-term adverse events rates, as an early
assessment of safety as is common for large pharmaceutical trials is not always
meaningful in medical device trials.   Device trials are frequently much smaller in
size and the reliability of early data may not be sufficient to establish a prospective
pattern.  When the device in question is an implant, the evaluation period must be
fairly long to assesses the potential for late occurring adverse events including
device failure and adverse reactions to device materials.  In some cases, the full
assessment of safety cannot be completed in the premarket phase and extends into
mandatory postmarket surveillance.
2. When devices are used in conjunction with another medical or surgical procedure,
the distinction between an adverse event that is clearly device related and one that
is common to the procedure may be difficult to assess.  The nature, timing, and
degree of severity are some of the factors that may be useful in reaching a
determination of cause.  Since these determinations are based on clinical judgment,
a real potential for bias exists in reaching conclusions about the treatment.  Care
must be exercised in designing the protocol to provide adequate detail in
instruction to investigators to allow for consistent and unbiased decision making
on their part. 
34 3. Devices (e.g., those emitting radiation) that have the potential for intermittent or
chronic use require assessment as to whether there is a lifetime exposure limit or a
maximum frequency of exposure.    Such issues are frequently addressed with
animal data as well as with long-term clinical evaluations.
VI. SPECIAL CONSIDERATIONS FOR JUVENILE RHEUMATOID ARTHRITIS
A. Background
Juvenile rheumatoid arthritis (JRA) is a heterogeneous group of diseases that share the
common feature of chronic, idiopathic synovitis, with onset prior to 16 years of age. These
disorders have been divided into clinically distinct subsets based on the extent of joint
involvement and extra-articular manifestations: pauci-articular, poly-articular, and
systemic-onset JRA, as well as oligoarthritis associated with HLA-B27,4 and they have
been further subdivided based on clinical courses (Cassidy 1986).  Immunogenetic subsets
appear to correlate with these clinical course subsets and are also distinct from adult RA
(Nepom 1991).  Of these various entities, polyarticular JRA is similar in many aspects to
adult RA, particularly in clinical signs and symptoms, synovitis, and similar efficacy
responses to some existing pharmacotherapy (NSAIDs, methotrexate, and prednisone). 
As only 3 to 5 percent of all patients with rheumatoid arthritis develop illness onset during
childhood, many investigational therapeutic agents in this small population will receive
orphan drug status, according to 21 CFR part 316  Orphan Drugs.  The application of
principles in the conduct of clinical trials for adult RA largely applies as well to JRA, and
this section outlines only those areas of difference from adult RA.  Sponsors are generally
encouraged to develop as much information as possible on JRA patients for agents that
will be approved for adult RA.  As a minimum, dosing and safety data are strongly
encouraged.
Conducting drug studies in children is generally necessary and consistent with the
expectations of treatment regimens for this disease.  Because pediatric subjects constitute
a vulnerable population, conducting research involving minimal risk is important.  The
Committee on Drugs of the American Academy of Pediatrics has published guidelines for
the ethical conduct of studies to evaluate drugs in pediatric populations (AAP 1995a), and
general considerations for the clinical evaluation of drugs in infants and children (AAP
1982), both of which should be consulted.  Guidelines regarding informed consent and
assent of pediatric patients from the Committee on Bioethics of the American Academy of
Pediatrics should also be followed (AAP 1995b).  Conducting clinical trials for patients
with JRA and, particularly, assessing global disease activity and response to therapy
should involve pediatric rheumatologists or adult rheumatologists who have extensive
training in pediatric rheumatology and have demonstrated competence in caring for
children with rheumatic diseases. 
4 The HLA-B27 subset is not addressed in this document.
35 As a general principle, children should not be subjected to an agent that has not been first
tested for safety in adults.  Testing may begin in children, however, when the anticipated
benefits based on existing knowledge justify the anticipated risks.  An agent developed
specifically for use in JRA (e.g., a biological agent targeted against a specific pathogenic
process that is unique to JRA and not present in adult RA) may need to be tested first in
children, as exposure in adult RA patients or even normal adult volunteers may be
unrevealing.  If, however, the agent has potential for use in both adult RA and JRA, then,
at minimum, PK-PD and initial phase 1 data (including MTD) for adults should be
available prior to the start of testing in children.  JRA trials of drugs that are expected to
be similar in efficacy to existing drugs and that do not represent major therapeutic
advances or alternative approaches to the basic mechanism of intervention can be delayed
until there is extensive efficacy and safety data either from adults or in other pediatric
populations.  
The need for reliable inferences does not necessitate a placebo control, but randomization
and controls should be employed.  The choice of control is a function of what is known
about the agent at the time and what other treatments are available to potential trial
enrollees.  If only an active control is used for an equivalence trial, convincing evidence of
the efficacy of the active control should be provided, and the test proposed to establish
equivalence should be specified.  If there have been no prior adult studies, or if the agent
under development has a novel mechanism of action or represents an entirely new class of
drug, a randomized, double-blinded trial, using either a placebo or an active control group
of (anticipated) similar efficacy is indicated.  Open label extensions to obtain additional
data about risk and persistence of benefit are very valuable.  The use of active control
(standard-of-care therapy) in the control arm, dose-response design (where control
receives a lower dose(s) of the test agent), crossover, randomized withdrawal (enrichment
design) or, if the agent has a short onset of effect, randomized placebo-phase trial designs
are encouraged as possible alternatives to inactive placebo control in JRA studies (Temple
1994, Feldman 1995).  As a general principle, protocol escape clauses are encouraged to
permit children who are not responding well to experimental therapy to receive early
conventional or alternative treatment.  The sponsor should indicate how dropouts will be
handled in the analysis, whether from the escape clause, or otherwise.
B. Applicability of Pediatric Regulation and Impact on Trial Design for JRA
Studies
The pediatric use section in the labeling regulations (21 CFR 201.57(f)(9)) permits drug
and biological products to be labeled for pediatric use if they have been demonstrated to
be safe and effective for adult populations and the mechanism of action of the drug is
sufficiently similar in children.  The pediatric rule may be applied only to obtain labeling
for the signs and symptoms of JRA;  other claims, including prevention of structural
damage, remission, and prevention of disability, should be evaluated in separate JRA
efficacy studies.  Although the regulation allows extrapolation of adult efficacy data,
additional pediatric dosing and safety evaluations are usually needed.  
36 In general, sponsors seeking approval for adult RA products appropriate for use in
patients with JRA are strongly encouraged to obtain dosing and safety data in
polyarticular course JRA for inclusion in the dosing and pediatric use sections of the label. 
Specimen collection for PK studies can be reduced significantly if available data indicate
that the coefficients are similar in adults and children.  Microsampling techniques should
be employed for such studies (Hashimoto 1991).  The extent of safety testing needed
depends on the agent, its prior use, and any established safety in other pediatric
populations.  Toxicity grading scales should be adjusted for pediatric populations.  Phase 4
studies for safety evaluation will be strongly encouraged when limited preapproval data
are obtained.  It is desirable that as much efficacy evidence as possible be gathered during
the evaluation of pediatric dosing and safety.   
For currently approved traditional (cyclooxygenase inhibitor) NSAIDs and
corticosteroids, adequate efficacy information exists to support a labeled indication for all
JRA and all JRA subsets.  For methotrexate and sulfasalazine, adequate efficacy
information exists for a labeled indication for JRA patients with a polyarticular course. For
such agents, a labeling claim could be supported using only PK, PD, and safety data in
JRA patients, although submission of additional JRA efficacy data is encouraged.
For new agents (not yet approved for adult RA) that are not from a new pharmacologic
class, adult efficacy data can be used to support a signs and symptoms claim for
polyarticular JRA if there is biological plausibility that the agent would have a similar
effect in JRA.  The applicability of the pediatric rule to support a labeled indication for
polyarticular course JRA will be based on adult RA efficacy data considered on an
individual basis for each agent.  When evidence for biological plausibility does not exist,
evidence should be submitted to support the application of the pediatric rule.  (The
Agency should be consulted in determining whether adequate biological plausibility exists
to apply the pediatric rule.)  Pediatric safety and dosing studies should be submitted.  
For agents in a new class, efficacy studies should be performed in JRA to obtain an
indication for use in JRA.  The indication will reflect the JRA subsets included in the
efficacy study. Sponsors who seek approval for all JRA should include all JRA subsets in
an efficacy study.  The data could support a claim for JRA (subsets not specified)
provided that the data do not suggest that the agent is ineffective in any one subset.  The
label should reflect that efficacy was demonstrated and that the agent is approved for JRA
(subsets specified depending on which were included in the efficacy study). 
C. Outcome Variables and Claims
It is possible for sponsors to seek approval for all JRA subsets or to seek approval for
individual subsets.  In the former case, the label should note the number of patients from
each subset enrolled in trials and the character of each subset response.  Except as noted
above in the application of the pediatric rule, all claims should be supported by an efficacy
demonstration in the intended subset(s).
37 1. Reduction in the Signs and Symptoms of JRA
All JRA trials should evaluate improvement based on a validated endpoint for
improvement.  Currently, the one validated approach is the definition of
improvement established by the JRA core set:  three of six (MD global,
parent/patient global, number of active joints, number of joints with limited range
of motion, functional ability, and ESR) improved by at least 30 percent and no
more than one of six worsening by more than 30 percent (Giannini 1997). 
Because the JRA definition of improvement was validated using a trial of
methotrexate, which primarily included polyarticular JRA patients, protocol
individualization may necessitate a refinement in the responder test for other
patient subsets.  For example, for pauci-articular JRA, with one knee involved and
a normal ESR, use of joint and functional assessments specific to the involved
joints and evaluation of uveitis as coprimary endpoints may also be valuable
(Lindsley 1996).  For patients with systemic onset JRA, additional assessment of
fever, extra-articular manifestations, and thrombocytosis/leucocytosis may be
useful coprimary endpoints (Silverman 1994).  Outcome variables need to be
appropriate and consistent with the type of agent under investigation. 
Investigators should specify, before the trial is initiated, how much change is
considered clinically important for each outcome variable.
Trials should generally last at least six months, except when six-month efficacy
data exist in adult RA and there are no reasons to expect loss of efficacy over time.
Under these circumstances, trial durations may be three months'
blinded/randomized, but six-months' open safety data should be obtained.  As with
adult RA, a three-month trial duration is suggested for NSAIDs.
2. Major Clinical Response
Similar to adult RA, major clinical response is a claim intended to connote that the
agent provides substantial clinical benefit, including in patients who are unable to
completely respond to the treatment or remit from the disease.  At present, this
claim is only theoretical, as clinical JRA trial databases adequate for defining major
clinical response do not exist.
3.  Complete Clinical Response
The claim of complete clinical response reflects achievement on drug of six
consecutive months of morning stiffness of less than 15 minutes duration, no active
synovitis (pain, redness, tenderness to palpation, swelling, stable or decreasing
limitation of motion), no extra articular features (including fever, serositis,
adenopathy, hepatosplenomegaly, rash, uveitis), and normal laboratory parameters
(including ESR, platelets, WBC) and, where applicable, no ongoing structural
damage while continuing on therapy.  Trials should be at least one year in duration. 
Residual damage from prior disease, including extra articular manifestations, is
38 acceptable in meeting criteria for complete clinical response.  Because spontaneous
complete clinical response rates may be relatively high in JRA, these studies should
be controlled. 
4. Remission
Remission is characterized exactly as above, but while off all antirheumatic drugs. 
Remission is not intended to imply cure.
5.  Prevention of  Disability
This claim is proposed to reflect durable improvement in physical function and
disability in studies of one to two years' duration with demonstrated improvement
in signs and symptoms over the same period.  Instruments currently validated for
use in JRA include the Childhood Health Assessment Questionnaire (CHAQ), the
Juvenile Arthritis Self-Report Index (JASI), and the Juvenile Arthritis Functional
Assessment Report (JAFAR).  HR-QOL should also be measured and
demonstrated not to worsen over the trial duration.  Endpoints should be tailored
to subtypes enrolled in trials (e.g., to assess knee function in pauci-articular JRA
patients in whom knee arthritis may be the primary arthritic manifestation). 
Instruments should be developmentally validated for the age ranges studied in a
trial (Murray 1995).
6.  Prevention of Structural Damage
Similar to adult RA, this claim would reflect trials of one year or more with
concomitant success in signs and symptoms.  Currently, only sparse data exist
regarding the usefulness of only one radiographic measure in JRA:  the
carpal-metacarpal distance in those patients with wrist arthritis.  Other clinically
promising settings include the evaluation of erosive disease in systemics with
polyarthritis, hip assessment in systemics, and knee assessments in pauci-articular
JRA.
D. Trial Design Issues
Recommendations for efficacy studies are based on the nature of the agent under
development.  The principles outlined for adult RA are generally applicable.  Patients
enrolled in these trials may be of any onset or disease course subset.  Separate trials for
each JRA subset are recommended if the agent is predicted to have a target mechanism of
action that will not be applicable and equally efficacious in all JRA subsets.  Alternatively,
a single, sufficiently large trial with enrollment appropriately stratified provides for useful
conclusions to be reached about efficacy and safety for each subset.  Relevant covariates
include disease course type, disease duration, and nonresponse to prior methotrexate
treatment.  Given that JRA is an orphan disease, there is often some flexibility in trial
design, but this should be discussed on a case-by-case basis.
39 At this time, JRA patients are usually ineligible for entry into efficacy trials unless they
have failed to respond adequately to at least one standard second line agent (such as
methotrexate at a dose of at least 10 mg/m2 body surface area per week).  There may be
exceptions to this if, for example, there is evidence that greater efficacy could be obtained
by using the agent very early in the disease course, evidence that delayed use in sicker
patients potentially carries greater risk of toxicity, or evidence that the agent has a
favorable safety and efficacy profile in a comparable population studied to date and that
the agent's actions are potentially readily reversible.  Pauci-articular JRA patients are
particularly encouraged for inclusion in trials with agents targeting the treatment of uveitis
or agents that will replace existing therapy with an improved safety profile, less frequent
blood monitoring, and/or superior efficacy.
Some JRA patients exposed to new agents should be evaluated periodically for an
extended period.  Effects on skeletal growth, development, behavior, sexual maturation,
reproductive capacity, and secondary malignancy should be included in such monitoring. 
Registries or cohort follow-up studies may be useful in providing long-term safety
information.
E. Concurrent Antirheumatic Agent Administration
The principles of  use of concurrent antirheumatic therapy in JRA trials are similar to those
outlined for adult RA:  limiting their discretionary use as much as reasonably possible so
that interpretation of efficacy and safety data is not compromised.  However, limitations
on concurrent medication cannot prohibit ethically justified treatments, nor should the
protocol be made so unattractive to parents, physicians, and patients that enrollment is
threatened.  If background treatment is necessary, early tolerance studies, to ensure safety
of co-administration, should precede any large trials.
If patients receive concurrent slow-acting or prednisone therapy, the dose should be stable
prior to study entry and should preferably remain so throughout the trial.  Concurrent
medications are usually important prognostically and so may need stratification.  If
possible, intra-articular steroid injections should be disallowed for a minimum of one
month prior to beginning experimental therapy; otherwise, that joint should be discounted
in assessing therapeutic effects. 
F. Multicenter Trials and Center Effects
Although JRA is the most common rheumatic disease of childhood, its prevalence is low
compared to adult RA.  Thus, trials of JRA that require large numbers of patients will
likely be multicenter trials.  Multicenter trials should employ a standardized protocol and
data collection forms among all centers.  Pretrial meetings of all investigators and other
involved personnel are strongly encouraged to ensure uniformity in protocol
interpretation, patient evaluation, and data recording.  Studies have shown that, within a
cooperative group, a center's performance is a function of the number of patients enrolled
at the center (Sylvester 1981).  Thus, studies that use fewer centers with greater numbers
40 of patients at each center are preferable to those that use large numbers of centers with
fewer patients.  Effort should be made to enroll at least 10 to 12 patients at each center to
provide for greater quality assurance.  In all multicenter trials, center effects should be
examined.  A therapy should show effect in more than one center.  When stringent
entrance criteria restrict the number of patients eligible for study, many centers may be
unable to enroll even 10 patients.  In such situations, randomization blocked within
individual centers, rather than across all centers, may help to reduce the potential impact
of center effects.
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44 APPENDIX A:  COMPARATIVE TRIAL RESPONSE RATES 5
Three cooperative systematic studies of rheumatic diseases (CSSRD) trials:
(1) Methotrexate vs. Placebo
(2) Gold, Auranofin vs. Placebo
(3) D-Penicillamine high, low vs. Placebo
Response Rates at End of Trial Based on Different Definitions of Improvement
PLACEBO (Auranofin) High-dose 
(Low-dose D-Penicillamine)       D-Penicillamine
    Gold, Methotrexate
Definition of
Improvement n=199 n=18 n=155
ACR> 20% 10 (8.4%) 30 (25.4%) 64 (40.3%)
ACR> 30% .5 (4.2%) 14 (12.0%) 46 (29.7%)
ACR> 40%  2 (1.7%)  7  (3.4%) 18 (11.6%)
ACR> 50%  0 (0%)  4  (3.4%) 14  (9.0%)
ACR> 60%  0 (0%)  3 (2.5%)   4  (2.6%)
ACR> 70%  0 (0%)  0  (0%)  1  (0.6%)
5 CSSRD database and Tugwell et al., "Combination Therapy with Cyclosporine and Methotrexate in Severe
Rheumatoid Arthritis," N Engl J Med 333;137-141, 1995. 
45 APPENDIX A (cont.)
COMPARATIVE MULTICENTER TRIAL OF
AURANOFIN/METHOTREXATE
(END OF TRIAL)
Response Rates at End of Trial Based on Different Definitions of Improvement
Definition of
Improvement Auranofin Methotrexate
(N=118) (n=119)
ACR>20% 34 (28.8%) 77 (64.7%)
ACR>30% 30 (25.4%) 65 (54.6%)
ACR>40% 22 (18.6%) 51 (42.9%)
ACR>50% 21 (17.8%) 42 (35.3%)
ACR>60%  9  (7.6%) 22 (18.5%)
ACR>70%  7  (5.9%) 11  (9.2%)
46 APPENDIX A (cont.)
COMPARATIVE TRIAL OF CYCLOSPORINE-A
METHOTREXATE VS. METHOTREXATE ALONE
Response Rates at End of Trial Based on Different Definitions of Improvement
Percent Increase by ACR Criteria Patients Satisfying Criteria
Methotrexate +
Cyclosporine-A Methotrexate + Placebo
(n=71) (n=74)
 0% 81.7 50.0
10% 49.3 16.2
20% 45.0 12.2
30% 33.8   8.1
40% 22.5  2.7
50% 22.5  2.7
60%    5.6  2.7
70%  1.4  0.0
80%  0.0  0.0
90%  0.0  0.0
47