Transcript CLINICAL TRIAL DESIGN

Chapter 4
Basic Study DESIGN
1
Types of Clinical Trials
1. Drug Development
(Phase 0, Phase I, & Phase II)
 Dose and activity
2. Experimental (Clinical Trial) Phase III
 “Effect”
2
Phases of Clinical Trials [1]
Phase 0 - Preclinical
• Preclinical animal studies
• Looking for dose-response
Phase I
• Seeking maximum tolerated dose (MTD)
• Volunteer patients
Phase II
• Estimate of drug activity
• Decide if drug warrants further testing (Phase III)
• Estimate of serious toxicities
3
Phases of Clinical Trials [2]
Phase III
• Provide effectiveness of drug or therapy
• Various designs
– No control
– Historical control
– Concurrent
– Randomized
• Testing for treatment effect
Phase IV
• Long term post Phase III follow-up
• Concern for safety
4
5
Phase III Introduction
• The foundation for the design of controlled
experiments established for agricultural experiments
• The need for control groups in clinical studies
recognized, but not widely accepted until 1950s
• No comparison groups needed when results dramatic:
– Penicillin for pneumococcal pneumonia (肺炎)
– Rabies vaccine (狂犬病疫苗)
• Use of proper control group necessary due to:
– Natural history of most diseases
– Variability of a patient's response to intervention
6
Phase III Design
• Comparative Studies
• Experimental Group vs. Control Group
• Establishing a Control
1. Historical
2. Concurrent
3. Randomized
• Randomized Control Trial (RCT) is the
gold standard
– Eliminates several sources of bias
7
Purpose of Control Group
• To allow discrimination of patient
outcomes caused by test treatment
from those caused by other factors
– Natural progression of disease
– Observer/patient expectations
– Other treatment
• Fair comparisons
– Necessary to be informative
8
Choice of Control Group
• Goals of Controlled Clinical Trials
• Types of Control Groups
• Significance of Control Group
• Assay Sensitivity
9
Goals of Controlled
Clinical Trials (1)
• Superiority Trials
– A controlled trial may demonstrate efficacy
of the test treatment by showing that it is
superior to the control
• No treatment
• Best standard of care
10
Goals of Controlled
Clinical Trials (2)
• Non-Inferiority Trials
– Controlled trial may demonstrate efficacy by
showing the test treatment to be similar in efficacy to
a known effective treatment
• The active control had to be effective under the
conditions of the trials
• New treatment cannot be worse by a pre-specified
amount
• New treatment may not be better than the standard
but may have other advantages
– Cost
– Toxicity
– Invasiveness
11
Superiority vs Noninferiority

Benefit
Harm
1.0
Placebo
.8
1.25
(
X
(
(
) Harm
X
) Non-significant
) Benefit
X

Active Control

Better
Worse
1.0
Standard
(
X
(
Better(
X
RR
RR
Plbo
X
) Worse
) Non-Inferior
)
Modified from Fleming, 1990
12
Considerations in Choice of
Control Group
• Available standard therapies
• Adequacy of the control evidence for
the chosen design
• Ethical considerations
13
Significance of Control Group
•
•
•
•
•
•
•
Inference drawn from the trial
Ethical acceptability of the trial
Degree to which bias is minimized
Type of subjects
Kind of endpoints that can be studied
Credibility of the results
Acceptability of the results by regulatory
authorities
• Other features of the trial, its conduct, and
interpretation
14
Type of Controls
• External
– Historical
– Concurrent, not randomized
• Internal and concurrent
– No treatment
– Placebo
– Dose-response
– Active (Positive) control
• Multiple
– Both an Active and Placebo
– Multiple doses of test drug and of an active control
15
Use of Placebo Control
• The “placebo effect” is well documented
• Could be
– No treatment + placebo
– Standard care + placebo
• Matched placebos are necessary so patients and
investigators cannot decode the treatment
assignment
• E.g. Vitamin C trial for common cold
– Placebo was used, but was distinguishable
– Many on placebo dropped out of study
– Those who knew they were on vitamin C
reported fewer cold symptoms and duration than
those on vitamin who didn't know
16
Historical Control Study (1)
• A new treatment used in a series of subjects
• Outcome compared with previous series of
comparable subjects
• Non-randomized, non-concurrent
• Rapid, inexpensive, good for initial testing of new
treatments
• Two sources of historical control data:
• Literature  Subject to publication bias
• Data base
17
Historical Control Study (2)
• Vulnerable to bias
• Changes in outcome over time may come from
change in:
– underlying patient populations
– criteria for selecting patients
– patient care and management peripheral
to treatment
– diagnostic or evaluating criteria
– quality of data available
18
Changes in Definitions
19
Time Trend
Age-adjusted Death Rates for Selected Causes: United States, 1950-76
20
Stat Bite
Cancer and Heart Disease Deaths
Cancer and heart disease are the leading causes of death in the United States. For people less than
age 65, heart disease death rated declined greatly from 1973 to 1992, while cancer death rates declined
slightly. For people age 65 and older, heart disease remains the leading killer despite a reduction in
deaths from this disease. Because cancer is a disease of aging, longer life expectancies and fewer
deaths from competing causes, such as heart disease, are contributing to the increasing cancer
incidence and mortality for those age 65 and older
JNCI 87(16): 1206, 1995
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22
Historical Control Study (3)
• Tend to exaggerate the value of a new treatment
• Literature controls particularly poor
• Even historical controls from a previous trial in
the same institution or organization may still be
problematic
– Pocock (1977, Brit Med J)
– In 19 studies where the same treatment was used in
two consecutive trials, differences in survival ranged
from 46 to 24 , with four differences being statistically
significant
• Adjustment for patient selection may be made, but
all other biases will remain
23
PRAISE I vs. PRAISE II
Placebo arms
24
Concurrent Controls
• Not randomized
• Patients compared, treated by
different strategies, same period
• Advantage
– Eliminate time trend
– Data of comparable quality
• Disadvantage
– Selection Bias
– Treatment groups not comparable
• Covariance analysis not adequate
25
Biases in Concurrent Control Study
• Types
– Magnitude of effects
– False positive
• Sources
• Patient selection
– Referral patterns
– Refusals
– Different eligibility criteria
• Experimental environment
– Diagnosis/staging
– Supportive care
– Evaluation methods
– Data quality
26
Randomized Control
Clinical Trial
• Reference: Byar et al. (1976)
New England Journal of Medicine
• Patients assigned at random to either
treatment(s) or control
• Considered to be “Gold Standard”
27
Advantages of Randomized
Control Clinical Trial
1. Randomization "tends" to produce comparable
groups
Design
Randomized
Concurrent
(Non-randomized)
Historical
(Non-randomized)
Sources of Imbalance
Chance
Chance & Selection Bias
Chance, Selection Bias,
& Time Bias
2. Randomization produces valid statistical tests
Reference: Byar et al (1976) NEJM
28
Disadvantages of Randomized
Control Clinical Trial
1. Generalizable Results?
– Subjects may not represent general
patient population – volunteer effect
2. Recruitment
– Twice as many new patients
3. Acceptability of Randomization Process
– Some physicians will refuse
– Some patients will refuse
4. Administrative Complexity
29
Ethics of Randomization (1)
• Statistician/clinical trialist must sell benefits of
randomization
• Ethics MD should do what he thinks is best for his
patient
– Two MD's might ethically treat same patient quite differently
• Chalmers & Shaw (1970) Annals New York Academy of
Science
1.
2.
3.
If MD "knows" best treatment, should not participate in trial
If in doubt, randomization gives each patient equal chance to
receive one of therapies (i.e. best)
More ethical way of practicing medicine
30
Ethics of Randomization (2)
• Byar et al. (1976) NEJM
1. RCT  honest admission best is not
known!
2. RCT is best method to find out!
3. Reduces risk of being on inferior
treatment
4. Reduces risk for future patients
31
Ethics of Randomization (3)
• Classic Example Reference: Silverman (1977) Scientific Amer
1. High dose oxygen to premature infants was
common practice
2. Suspicion about frequency of blindness
3. RCT showed high dose cause of blindness
32
Comparing Treatments
• Fundamental principle
• Groups must be alike in all important aspects and only differ in the
treatment each group receives
• In practical terms, “comparable treatment groups” means
“alike on the average”
• Randomization
• Each patient has the same chance of receiving any of the
treatments under study
• Allocation of treatments to participants is carried out using a
chance mechanism so that neither the patient nor the physician
know in advance which therapy will be assigned
• Blinding
• Avoidance of psychological influence
• Fair evaluation of outcomes
33
Randomized Phase III
Experimental Designs
Assume:
• Patients enrolled in trial have satisfied eligibility
criteria and have given consent
• Balanced randomization: each treatment group will
be assigned an equal number of patients
Issue
• Different experimental designs can be used to
answer different therapeutic questions
34
Commonly Used Phase III Designs
•
•
•
•
•
•
•
•
Parallel
Group/Cluster
Randomized Consent
Cross Over
Factorial
Large Simple
Equivalence/Non-inferiority
Sequential
35
Parallel Design
Screen
Trt A
Randomize -
Trt B
• H0: A vs. B
• Advantage
– Simple, General Use
– Valid Comparison
• Disadvantage
– Few Questions/Study
36
Fundamental Design
Eligible
Yes
Consent
No
No
Dropped
Dropped
Yes
R
A
N
D
O
M
I
Z
E
A
B
Comment: Compare A with B
37
Examples of Parallel Designs
•
•
•
•
•
VEST
CAST
DCCT
NOTT
IPPB
38
Run-In Design
Problem:
• Non-compliance by patient may seriously impair
efficiency and possibly distort conclusions
Possible Solution: Drug Trials
• Assign all eligible patients a placebo to be taken for a
“brief” period of time. Patients who are “judged”
compliant are enrolled into the study. This is often
referred to as the “Placebo Run-In” period.
• Can also use active drug to test for compliance
39
Run-In Design
Screen &
Consent
R
A
Run-In
Satisfactory N
Period
D
O
M
I
Unsatisfactory
Z
E
A
B
Dropped
Note: It is assumed that all patient entering the run-in
period are eligible and have given consent
40
Examples of Run-In Trials
• Cardiac Arrhythmia Suppression
Trial (CAST)
• Diabetes Control and Complications
Trial (DCCT)
• Physicians Health Study (PHS)
41
Cluster Randomization Designs
• Groups (clinics, communities) are randomized to treatment or control
• Examples:
• Community trials on fluoridization of water
• Breast self examination programs in different clinic setting in USSR
• Smoking cessation intervention trial in different school district
in the state of Washington
• Advantages
• Sometimes logistically more feasible
• Avoid contamination
• Allow mass intervention, thus “public health trial”
• Disadvantages
• Effective sample size less than number of subjects
• Many units must participate to overcome unit-to-unit variation,
thus requires larger sample size
• Need cluster sampling methods
42
Randomized Consent Design
Zelen (NEJM, 1979)
Group I: Regular Care
(TRT A)
Patient
Randomize
Group II:
Experimental
(TRT B)
NO
(TRT A)
Consent
YES
(TRT B)
43
Randomized Consent
(Zelen (1979) NEJM)
Usual Order
Screen
Proposed Order
Screen

Consent

Randomize

Randomize

Consent
(from Exp. Group only)
• Advantages
– Easier Recruitment
• Disadvantages
– Need Low Refusal Rate
– Control Must Be Standard
– Unblinded
– Ethical?
• Refusal Rate Dilution  Increase Sample Size
15% 
2x
44
Cross Over Design
H0: A vs. B
Scheme
Period
Group
AB
BA
I
1 TRT A
2 TRT B
II
TRT B
TRT A
• Advantage
– Each patient their own control
– Smaller sample size
• Disadvantage
– Not useful for acute disease
– Disease must be stable
– Assumes no period carry over
– If carryover, have a study half sized
(Period I A vs. Period I B)
45
Factorial Design
• Schema
Factor I
Placebo
Trt B
Placebo
N/4
N/4
Trt A
N/4
N/4
A vs. Placebo
Factor II
B vs. Placebo
46
Factorial Design
• Advantages
– Two studies for one
– Discover interactions
• Disadvantages
– Test of main effect assumes no interaction
– Often inadequate power to test for interaction
– Compliance
• Examples
– Physicians' Health Study (PHS) NEJM 321(3):129-135, 1989.
– Final report on the aspirin component
– Canadian Cooperative Stroke Study (1978) NEJM p. 53
47
Physicians Health Study
48
Physician Health Study
49
Physicians Health Study
50
Physicians Health Study
51
Superiority vs.
Non-Inferiority Trials
Superiority Design: Show that new treatment
is better than the control or standard
(maybe a placebo)
Non-inferiority: Show that the new treatment
a) Is not worse that the standard by more than
some margin
b) Would have beaten placebo if a placebo arm
had been included (regulatory)
52
Equivalence/Non-inferiority Trial
• Trial with active (positive) controls
• The question is whether new (easier or cheaper)
treatment is as good as the current treatment
• Must specify margin of “equivalence” or non-inferiority
• Can't statistically prove equivalency -- only show that
difference is less than something with specified
probability
• Historical evidence of sensitivity to treatment
• Sample size issues are crucial
• Small sample size, leading to low power and
subsequently lack of significant difference, does not
imply “equivalence”
53
Difference in Events
Test Drug – Standard Drug
54
Active Control Design

Benefit
Harm
1.0
Placebo
.8
1.25
(
X
(
(
) Harm
X
) Non-significant
) Benefit
X

Active Control

Better
Worse
1.0
Standard
(
X
(
Better(
X
RR
RR
Plbo
X
) Worse
) Non-Inferior
)
Modified from Fleming, 1990
55
Non-Inferiority Challenges (1)
• Requires high quality trial
• Poor execution favors non-inferiority
• Requires strong control; weak
control favors non-inferiority
56
Non-Inferiority Challenges (2)
• Treatment margin somewhat
arbitrary
• Imputed Trt vs. Plbo effect
– Uses historical control concept
– Imputed estimate not very robust
57
OPTIMAAL
OPtimal Trial In Myocardial infarction with the
Angiotensin II Antagonist Losartan
Steering Committee
J. Kjekshus (Chair), K. Dickstein (Coordinator),
S. G. Ball, A. J. S. Coats, R. Dietz, A. Kesäniemi, E. S. P. Myhre,
M. S. Nieminen, K. Skagen, K. Swedberg, K. Thygesen, H. Wedel,
R. Willenheimer, A. Zeiher, J. C. Fox and K. Kristianson
Endpoint Committee
J. G. F. Cleland and M. Romo
Data Safety and Monitoring Board
D. Julian (Chair), A. Bayés de Luna, D. L. DeMets,
C. D. Furberg, W. W. Parmley and L. Rydén
Lancet 2002; 360:752-60
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Rationale
• ACE inhibitors reduce mortality in
high risk post MI patients
• Selective Angiotensin II Receptor
Antagonists are an alternative
because of more complete blockade
of tissue RAAS
• Better tolerability
59
Hypothesis
Losartan (50 mg) is superior or non-inferior
to captopril (150 mg) in decreasing all-cause
mortality in high-risk patients following AMI
Study design
• Double-blind, randomized, parallel,
investigator initiated, no placebo control
• Event driven (all-cause death = 937)
• Multicentre (Denmark, Finland, Germany,
Ireland, Norway, Sweden, UK)
60
Captopril as Comparator
• Captopril has well documented
benefits
• Captopril 50 mg 3 times daily has
indication for CHF and AMI
worldwide
• Widely used, available as generic
61
Statistical Methods
• 937 deaths required for 95% power to
detect a 20% difference between groups
• Non-inferiority margin of 10% chosen
based on placebo-controlled trials of
ACE-inhibitors
• Analysis by Intention-to-Treat and Cox
regression model
62
All-cause death
25
losartan (n=499 events)
captopril (n=447 events)
Event rate (%)
20
15
10
5
Relative Risk = 1.13 (0.99 to 1.28); p=0.069
0
0
losartan (n) 2744
captopril (n) 2733
6
12
18
Month
24
30
36
2504
2534
2432
2463
2390
2423
2344
2374
2301
2329
1285
1309
63
Subgroup Analyses
n
Age
<65
2170
65-74
1840
>75
1467
Gender
Female
1575
Male
3902
Diabetes
Non-diabetic
4537
Diabetic
940
Killip class
Killip class 1
1735
Killip class 2
3131
Killip class 3-4
609
Heart failure
No heart failure
1060
Heart failure
4417
Infarct location
Infarct ant/lat
3821
Infarct inf/post
1152
Prior MI
No prior MI
4479
Prior MI
998
Thrombolytic use No thromb use
2499
Thromb use
2978
-blocker use
No -blocker use 1171
-blocker use
4306
Overall
5477
Hazard ratio (95% CI)
0.6
losartan better
1
1.5
2
captopril better
64
Effect of losartan
relative to placebo?
Rel. Risk % change
captopril vs. placebo*
0.805
losartan vs. captopril (OPTIMAAL) 1.126
losartan vs. putative
placebo (0.805 x 1.126)
0.906
- 19.5
12.6
- 9.4
* SAVE, AIRE. TRACE, SMILE, GISSI III, CONSENSUS II and ISIS IV
65
Non-Inferiority Methodology
a) Comparison: New Treatment vs. Standard
RRa
b) Estimate of standard vs. placebo RRb
(based on literature)
c) Imputed effect of New Trt vs. placebo (RRc)
RRc = RRa x RRb
66
Assay Sensitivity
• Ability to distinguish an effective treatment from a
less effective or ineffective treatment
• Different implications of lack of assay sensitivity
– Superiority trials
• Failing to show that the test treatment is superior
• Thus failing to lead to a conclusion of efficacy
– Non-inferiority trials
• Finding an ineffective treatment to be non-inferior
• Thus leading to an erroneous conclusion of efficacy
67
Assay Sensitivity in
Non-Inferiority Trials
• More critical
• Historical evidence of sensitivity to Trt effects
• Appropriate trial conduct
– The design of the non-inferiority trial be similar to that
of previous trials used to determine historical evidence
of sensitivity to Trt effects
– Conduct of the study is similar to the previous trials
– An acceptable margin of non-inferiority be defined,
taking into account the historical data
– The trial be conducted with high quality
68
Large, Simple Trial
• Advocated for common pathological conditions
• To uncover even modest benefits of intervention
• That are easily implemented in a large population
• Intervention unlikely to have different effects in
different patient subpopulations
• Unbiased allocation to treatments
• Unbiased and easily ascertained outcome
• Very limited data collection
69
CAPRIE
Design
Ischemic stroke, MI, atherosclerotic PAD
Clopidogrel
75 mg/day PO
Aspirin
325 mg/day PO
Completed Trial
(N = 9,577)
Completed Trial
(n = 9,566)
Source: CAPRIE Steering Comm. Lancet. 1996; 348:1329
70
CAPRIE
Risk Reduction by Major Outcomes
5.2
Ischemic stroke
19.2
MI
Vascular death
p = 0.419
p = 0.008
p = 0.29
p = 0.043
7.6
All events
8.7
-40
-20
0
20
40
Percentage Relative Risk Reduction
71
Sequential Design
• Continue to randomize subjects until H0 is
either rejected or “accepted”
• A large statistical literature for classical
sequential designs
• Developed for industrial setting
• Modified for clinical trials
(e.g. Armitage 1975, Sequential Medical Trials)
72
Classical Sequential Design (1)
• Continue to randomize subjects until H0 is either rejected or “accepted”
• Classic
Trt Better
Net
20
Trt
0
Effect
Continue

Accept H0
-20
Continue
Trt Worse
100
200
300
No. of Paired Observations
73
Classical Sequential Design (2)
• Assumptions
– Acute Response
– Paired Subjects
– Continuous Testing
• Not widely used
• Modified for group sequential designs
74
Beta-blocker Heart Attack Trial
(BHAT)
Design Features
Mortality Outcome
Randomized
Double-blind
Placebo-controlled
Extended follow-up
3,837 patients
Men and women
30-69 years of age
5-21 days post-M.I.
Propranolol-180 or 240 mg/day
Preliminary Report. JAMA 246:2073-2074, 1981
Final Report. JAMA 247:1707-1714, 1982
75
BHAT GSB
76
Confounding Bias
• Suppose you are interested in the effects of
a treatment T upon an outcome O in the
presence of a predictor P
• Randomization takes care of bias due to
factors P before treatment
• Blinding takes care of bias due to factors P
after treatment
77
Blinding or Masking (1)
• Assures that subjects are similar with regard
to post-treatment variables that could affect
outcomes
• Minimizes the potential biases resulting from
differences in management, treatment, or
assessment of patients, or interpretation of
results
• Avoids subjective assessment and decisions
by knowing treatment assignment
78
Blinding or Masking (2)
• No Blind
– All patients know treatment
• Single Blind
– Patient does not know treatment
• Double Blind
– Neither patient nor health care provider know
treatment
• Triple Blind
– Patient, physician and statistician/monitors do
not know treatment
• Double blind recommended when possible
79
Masking or Blinding (3)
• Keeping the identity of treatment assignments
masked for:
1. Subject
2. Investigator, treatment team or evaluator
3. Evaluation teams
• Purpose of masking: bias reduction
• Each group masked eliminates a different source
of bias
• Masking is most useful when there is a subjective
component to treatment or evaluation
80
Feasibility of Masking
• Ethics: The double-masking procedure should not
result in any harm or undue risk to a patient
• Practicality: It may be impossible to mask some
treatments
• Avoidance of bias: Masked studies require extra
effort (manufacturing look-alike pills, setting up coding
systems, etc.)
• Compromise: Sometimes partial masking, e.g.,
independent masked evaluators, can be sufficient to
reduce bias in treatment comparison
• Although masked trials require extra effort, sometimes
they are the only way to obtain an objective answer to
a clinical question
81
Reasons for Subject Masking
• Those on “no-treatment” or standard treatment
may be discouraged or drop out of the study
• Those on the new drug may exhibit a “placebo”
effect, i.e., the new drug may appear better when it
is actually not
• Subject reporting and cooperation may be biased
depending on how the subject feels about the
treatment
82
Unbiased Evaluation
Subject Bias (NIH Cold Study)
(Karlowski, 1975)
Duration of Cold (Days)
Blinded
Unblinded
Subjects
Subjects
Placebo
6.3
8.6
Ascorbic Acid
6.5
4.8
83
Reasons for
Treatment Team Masking
• Treatment decisions can be biased by knowledge of
the treatment, especially if the treatment team has
preconceived ideas about either treatment
• Dose modifications
• Intensity of patient examination
• Need for additional treatment
• Influence on patient attitude through enthusiasm
(or not) shown regarding the treatment
84
Unbiased Evaluation
. Investigator Bias - (Taste & Smell Study)
(Henkin et al, 1972 & 1976)
Zinc
Placebo
Single Blind
8/8*
0/8
Double Blind
5/8
7/8
*Number of variables with significant
improvement/Number of variables
85
Reasons for Evaluator
(Third Party) Masking
• If endpoint is subjective, evaluator bias will lead to
recording more favorable responses on the preferred
treatment
• Even supposedly “hard” endpoints often require
clinical judgment, e.g., blood pressure, MI
86
Reasons for Monitoring
Committee Masking
• Treatments can be objectively evaluated
• Recommendations to stop the trial for “ethical”
reasons will not be based on personal biases
• Sometimes, however, triple-mask studies are hard
to justify for reasons of safety and ethics
• A policy not recommended, not required by FDA
87
Design Summary
• Design used must fit goals of trial
• RCT minimizes bias
• Superiority vs. Non-Inferiority trial
challenges
• Use blinding when feasible
88