Download Design and Analysis of Clinical Trials

Design And Analysis Of
Clinical Trials
Martin L. Lesser, Ph.D.
Biostatistics Unit
Feinstein Institute for Medical Research
North Shore – Long Island Jewish
Health System
CME Disclosure Statement
• The North Shore LIJ Health System adheres to the ACCME's new
Standards for Commercial Support. Any individuals in a position to
control the content of a CME activity, including faculty, planners and
managers, are required to disclose all financial relationships with
commercial interests. All identified potential conflicts of interest are
thoroughly vetted by the North Shore-LIJ for fair balance and
scientific objectivity and to ensure appropriateness of patient care
recommendations.
• Course Director, Kevin Tracey, has disclosed a commercial interest in
Setpoint, Inc. as the cofounder, for stock and consulting support. He
has resolved his conflicts by identifying a faculty member to
conduct content review of this program who has no conflicts.
• The speaker, Martin L. Lesser, PhD, has no conflicts.
2
Types of Clinical Trials
Phase I - exploratory; assessment of toxicity;
determination of safe dosage;
pharmacokinetics
Phase II - evaluation of efficacy in a select group of
patients; estimation of treatment effect
Phase III - comparative trial; hypothesis testing
Phase IV - establish new indication;
post-marketing surveillance
Phase I Designs
• “3+3” dose escalation design for determining
maximum tolerated dose (MTD)
• Fixed multiple dose design (e.g., randomize 5
subjects to each of 5 doses)
• Goal: design should protect subjects from harm,
especially in a trial for which safe dosing,
pharmacokinetics, and potential toxicities are
unknown or poorly understood
X1=# of DLTs in first cohort of 3
X2=# of DLTs in first cohort of 3
DLT=dose limiting toxicity
Source: Jovanovic, et al.
2004
Phase II Designs
• Applied to a specific disease entity
• Fixed dose is used
• Simple primary outcome: response,
measurement of some parameter
• Single arm, open label (traditional)
• Single arm, blinded evaluator (uncommon)
• Simon 2-stage design
• Randomized Phase II trial (for selection of best
therapy)
Simon 2-Stage Optimal Design
• H0: p ≤ p0 vs. HA: p ≥ p1
• Where response rate ≤ p0 is uninteresting and response
rate ≥ p1 is the desired target
• Simon’s “Optimal Design”: Observe n1 subjects in stage
1. If response rate r1≤ a1/n1, then stop the trial and reject
the drug.
• If r1> a1/n1, then study an additional n2 subjects in stage
2, for a total of n=n1+n2. If the “total” response rate r ≤
a/n, then reject the drug. If r > a/n, then consider the
drug for further testing and Phase III trials.
Simon: Controlled Clin Trials, 10:1-10, 1989.
Simon 2-Stage Optimal Design
(cont’d)
• For given α, β, p0, and p1, this design minimizes EN(p0),
the expected number of subjects studied under H0 .
• Example: Let α=0.05 β=0.20 p0= 0.30 p1= 0.45
Stage 1: Enter 27 subjects; stop trial and reject drug
if r1≤ 9/27.
If r1 > 9/27, then go on to Stage 2.
Stage 2: Enter 54 additional subjects (total=81).
If r ≤ 30/81, then reject the drug.
If r > 30/81, then trial is favorable toward drug.
Note: E(N(p0)) = 41.7. Prob(early termination)=0.73
Simon 2-Stage Minimax Design
• Similar to the 2-stage optimal design
• Minimizes the maximum total sample size (n) among all
optimal designs
• Minimax design is attractive when subject accrual is low
• Previous example worked with minimax:
r1≤ 16/46, r ≤ 25/65, EN(p0)=49.6, PET(p0)=0.81
(Optimal design had n=81.)
Phase III Trials
Design Considerations
 Purpose of study; What is the question?
- Primary and secondary questions
- Operationalizing the question (definition of response,
survival, pain, quality of life, etc.)
 Patient population
- Target population, sampling frame
- Inclusion/exclusion criteria
- Comparability of patients, equivalent baseline workups
Design Considerations
(continued)
• Treatment Plan
• Blinding
• Use of Placebo Control
• Criteria for evaluation of treatment effect
(comparability of patient follow-up)
Design Considerations
(continued)
 General study design structure for comparative
studies
-
randomized controls
concurrent non-randomized controls
historical controls (Phase II and III)
patient as own control (cross-over design)
Randomized Controls
Advantages
Reduces or eliminates bias because
chance, alone, determines assignment
Assures that most statistical methods
will be valid
Disadvantages
Can be expensive, labor intensive
Patients may refuse randomization,
resulting in bias
Potential ethical problems
May upset the patient-physician
relationship
Not feasible if contamination is likely
Concurrent Non-Randomized
Controls
Advantages
Useful when randomization is not feasible
Useful in group or community
interventions
Usually less cost/effort than randomized
trials
Disadvantages
Assignment to treatment may be biased
May require matching or post-hoc
adjustments
Historical Controls
Advantages
Data already exist
Relatively inexpensive
Ethical problems of randomization are
avoided
Often requires fewer patients on new
treatment
Disadvantages
HCs and current group subjects may
differ on:
Method/criteria for selection
Diagnostic and/or follow-up criteria
Disease epidemiology, etiology, or
natural history may have changed
Difficult to protect against unknown biases
Some data elements may not be available
in the HC era
Patient As Own Control
Advantages
Reduces variance, often resulting in
smaller required sample sizes
Disadvantages
Only useful in certain disease settings
May introduce "order" effects
Nature of intervention may be influenced
by results of first study period
Design Considerations
(continued)
• Blinding
• Placebo control
• Stratification
• The process of randomization
• Handling dropouts and non-compliance
• Statistical methods for data analysis
• Sample size and power
• Interim analysis and early stopping
Blinding
• Any attempt to make study participants unaware of which
treatment is offered
• Is indicated when the occurrence and reporting of outcomes
can be easily influenced by knowledge of treatment
(subjective responses, behavior change)
• May be either single blind or double blind
• Blinding is not always feasible
• Blinding may be unsuccessful (ability to break the blind)
Placebo Control
•
Appropriate when no effective standard treatment exists
for the control group
•
Makes subject’s attitudes to the trial as similar as
possible in the treatment and control groups
•
Major uses:
− Controls for psychological factors
− Maintains double blind design
− Controls for spontaneous disease variability
•
Ethical issues:
- May be unethical to withhold treatment in order to
administer placebo
Stratification
 Randomization does not guarantee that
prognostic factors will be evenly distributed
between treatment groups
 Imbalance can be partly addressed by
stratification prior to randomization
 Imbalance can also be addressed by covariate
adjustment at the time of analysis
Stratification: An Example
NO STRATIFICATION
Response Rate
Low Risk High Risk
Chemo
Randomize
RT
27 (30% ) 62 (70% )
89
Chemo 25%
56 (80% ) 38 (20% )
94
RT 64%
83
100
183
Observed difference is confounded by the prognostic factor
RANDOMIZE WITHIN STRATA
Chemo
Randomize
within
Low Risk
n=83
40 (45% )
RT
43 (46% )
Response
Rate
Chemo 25%
Chemo
Randomize
within
High Risk
n=100
49 (55% )
RT 64%
RT
51 (54% )
Observed difference is not confounded by the prognostic factor
The Process of Randomization

simple randomization

permuted block randomization

unbalanced randomization

randomized consent form

Examples of permuted block randomization
- B=1 AAAABABAAAAAABBB
(11 A, 5 B)
- B=4 ABBA AABB BABA BABA
( 8 A, 8 B)
- B=6 AABABB ABABBA AAAB
( 9 A, 7 B)
Dropouts and Non-Compliance

Intention to Treat Principle
- analyze as randomized
- evaluates the effect of a treatment "policy"

Analyze as Treated Principle
- exclude dropouts
- adjust for compliance or dose received
- evaluates the effect of the "active ingredient"
(but in a possibly biased subset of patients)
Dropouts and Non-Compliance

Examples
- Patients with head and neck cancer
randomized to nasogastric feeding tube or
good oral nutrition;
- Outcome=weight;
- Some patients "cross-over" from NG tube
to oral nutrition arm
- Patients with familial polyposis randomized
to high fiber or low fiber diets;
- Outcome=number and size of new polyps;
- Some patients do not eat the required
amount of high fiber cereal; dose of fiber
varies from patient to patient
Example: RCT in Head and Neck Cancer
Assuming Full (100%) Compliance in Group A
Weight Gain (lbs.)
n=50
A
RANDOMIZE
B
NG
Feeding
Tube
µ=8.0, σ=3
7.57 ±
2.84
n=50
Best
Oral
Nutrition
µ=5.0, σ=3
4.61 ± 3.01
A vs. B
P<0.0001
Example: RCT in Head and Neck Cancer
Assuming 50% Compliance in Group A
Weight Gain (lbs.)
n=25
A1
n=50
RANDOMIZE
A
NG
Feeding
Tube
A2
Pull out NG
tube and
default to best
oral nutrition
µ=4.5, σ=3
B
Compliant with
NG tube
µ=8.0, σ=3
Best
Oral
Nutrition
µ=5.0,
σ=3
A1
6.39 ± 2.74
A1
A2
n=25
n=50
5.00 ± 2.42
7.78 ± 2.34
5.44 ± 2.81
B
5.66 ± 2.98
A vs. B (ITT)
A2 vs. B
A2 vs. A1+B
A1 vs. A2 vs. B
p=0.2098
p=0.0028
p=0.0009
p=0.0003
Statistical Methods Commonly Used
in the Analysis of Clinical Trials Data

Binary response data
- chi square, Fisher exact test
- multiple logistic regression

Survival, duration of response, and time until
event data
- Kaplan-Meier product limit method
- logrank test, Gehan-Wilcoxon test
- Cox proportional hazards regression

Continuous-type data
- analysis of variance
- ordinary multiple regression
Sample Size Considerations

Concept of power

Type of endpoint/outcome variable

Specification of clinically significant difference
of interest

Estimation and confidence intervals

Multiple endpoints, Bonferroni correction

Tables of sample size and power
Patient Flow in Clinical Trials
Available

Considered

Eligible

Consented

Enrolled

Compliant

Adequately Followed
Sample Size/ Power Sample
Suppose the response rate using standard therapy (A) is assumed to be
30%. The investigator would like to see an increase in the response rate to
at least 50% (with treatment B) in order for it to be considered clinically
useful. A trial of A vs. B would require 125 patients in each group in order to
have a 90% chance (power) of detecting a difference of this magnitude or
larger (two-tailed test, 5% significance level).
Other calculations:
n=93/group to achieve 80% power
n=56/group to achieve 90% power to detect
response rates of 30% vs. 60%
n=42/group to achieve 80% power to detect
response rates of 30% vs. 60%
n=184/group to achieve 90% power to detect
response rates of 30% vs. 35%
Interim Analysis and Early Stopping

Dangers of naive interim analysis
- increases Type I error rate (significance level)
- increases bias with respect to "expected" results
- data lags may influence interim results

Statistically sound stopping rules (i.e., rules that maintain
the Type I error rate and desired power)
- group sequential analysis (O'Brien-Fleming, Pocock,
Lan-Demets, etc.)
- curtailed sampling "individual" sequential testing
- conditional power

Early stopping depends on formal statistics as well as on
other factors
Example:
The BHAT Trial
(Beta-blocker Heart Attack Trial)
• Randomized, double-blind, placebo-controlled
trial to test the effect of propanolol (beta-blocker)
on total mortality
• n = 3837 patients randomized to propanolol or
placebo
• Trial was stopped 1 year early (on the 6th interim
analysis) using the O-F group sequential
approach when logrank X2 =2.82 > 2.23
O’Brien-Fleming Boundaries Applied to
the BHAT Trial