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STATISTICS 542 Introduction to Clinical Trials CLINICAL TRIAL DESIGN

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Title: STATISTICS 542 Introduction to Clinical Trials CLINICAL TRIAL DESIGN


1
STATISTICS 542Introduction to Clinical Trials
CLINICAL TRIAL DESIGN
2
Types of Clinical Research
  • 1. Case Reports
  • Anecdotal ? Problem
  • 2. Observational
  • a. Case Control/Retrospective (lung cancer)
  • b. Cross Sectional (WESDR) Beaver Dam
  • c. Prospective (Framington) WESDR-II
  • ? Risk Factor Associations
  • 3. Drug Development
  • (Phase 0, Phase I, Phase II)
  • ? Dose and activity
  • 4. Experimental (Clinical Trial) Phase III
  • ? Effect

3
Phases of Clinical Trials (Cancer) 1
  • Phase 0 - Preclinical
  • Preclinical animal studies
  • Looking for dose-response
  • Phase I
  • Seeking maximum tolerated dose (MTD)
  • Patients usually failed other alternatives
  • Phase II
  • Estimate of drug activity
  • Decide if drug warrants further testing (Phase
    III)
  • Estimate of serious toxicities

4
Phases of Clinical Trials (Cancer) 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

5
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6
Design
  • The choice of design depends on the goal of the
    trial
  • Choice also depends on the population, knowledge
    of the intervention
  • Proper design is critical, analysis cannot rescue
    improper design

7
Phase I Design
  • Typical/Standard Design
  • Based on tradition, not so much on statistical
    theory
  • Dose escalation to reach maximum tolerated dose
    (MTD)
  • Dose escalation often based on Fibonacci Series
  • 1 2 3 5 8 13 . . . .

8
Typical Scheme
  • 1. Enter 3(5) patients at a given dose
  • 2. If no toxicity, go to next dosage and repeat
    step 1
  • 3. a. If 1 patient has serious toxicity, add 3
    more
  • patients at that does (go to 4)
  • b. If 2/3 have serious toxicity, consider MTD
  • 4. a. If 2 or more of 6 patient shave toxicity,
    MTD reached (perhaps)
  • b. If 1 of 6 has toxicity, increase dose and go
    back to step 1

9
Standard Phase I Design
  • Designed to find dose where 1/3 of patients
    experience dose limiting toxicity (DLT)
  • Standard escalation design tends to underestimate
    target dose
  • Ref Storer, Biometrics, 1989

10
Dose-response curves used in simulations (1)
11
Dose-response curves used in simulations (2)
12
Summary of Designs Considered (1)(Storer,
Biometrics 45925-37, 1989)
  • A. Standard
  • Observe group of 3 patients
  • No toxicity? increase dose
  • Any toxicity ? observe 3 or more
  • One toxicity out of 6 ? increase dose
  • Two or more toxicity ? stop
  • B. 1 Up, 1 Down
  • Observe single patients
  • No toxicity ? increase dose
  • Toxicity ? decrease dose

13
Summary of Designs Considered (2)(Storer,
Biometrics 45925-37, 1989)
  • C. 2 Up, 1 Down
  • Observe single patients
  • No toxicity in two consecutive ? increase dose
  • Toxicity ? decrease dose
  • D. Extended Standard
  • Observe groups of 3 patients
  • No toxicity ? increase dose
  • One toxicity ? dose unchanged
  • Two or three toxicity ? decrease dose

14
Summary of Designs Considered (3)(Storer,
Biometrics 45925-37, 1989)
  • E. 2 Up, 2 Down
  • Observe groups of 2 patients
  • No toxicity ? increase dose
  • One toxicity ? dose unchanged
  • Both toxicity ? decrease dose
  • B, C, D, E - fixed sample sizes ranging from 12
    to 32 patients
  • Can speed up process to get to target dose range

15
Phase II Design (1)
  • References
  • Gehan (1961) Journal of Chronic Disorders
  • Fleming (1982) Biometrics
  • Storer (1989) Statistics in Medicine
  • Goal
  • Screen for therapeutic activity
  • Further evaluate toxicity
  • Test using MTD from Phase I
  • If drug passes screen, test further

16
Phase II Design (2)
  • Design of Gehan
  • No control (?)
  • Two stage (double sampling)
  • Goal is to reject ineffective drugs ASAP
  • Decision I Drug is unlikely to be effective in
    ? x of patients
  • Decision II Drug could be effective
  • in ? x of patients

17
Phase II Design (3)
  • Typical Gehan Design
  • Let x 20
  • That is, want to check if drug likely to work in
    at least 20 of patients
  • 1. Enter 14 patients
  • 2. If 0/14 responses, stop and
  • declare true drug response ?20
  • 3. If 1/14 responses, add 15-40
  • more patients
  • 4. Estimate response rate C.I.

18
Phase II Design (4)(Why 14 failures?)
  • Compute probability of consecutive failures
  • If drug ? 20 effective, there would be 95.6
    chance of at least one success
  • If 0/14 success observed, reject drug

Patient Prob 1 0.8 2 0.64 (0.8 x
0.8) 3 0.512 (0.8 x 0.8 x 0.8) --- --- 8 0.1
6 --- --- 14 0.044
19
Phase II Design (5)
  • Stage I Sample Size
  • Table I
  • Rejection Effectiveness ()
  • Error 5 10 15 20 25 40 50
  • 5 59 29 19 14 11 6 5
  • 10 45 22 15 11 9 5 4

20
Stage II Sample Size (1)
  • Based on desired precision of effectiveness
    estimate
  • r1 of successes in Stage 1
  • n1 of patients in Stage 1
  • Now precision of total sample N(n1 n2)
  • Let

21
Stage II Sample Size (2)
  • To be conservative, Gehan suggested
  • upper 75 confidence limit from first sample
  • Thus, we can generate a table for size of
  • second stage (n2) based on desired precision

22
Additional Patients for Stage II (n2)(Rejection
Rate 5 for Stage I)
23
Additional Patients for Stage II (n2)(Rejection
Rate 5 for Stage I)
We might require 10 precision with 20 desired
effectiveness. Assuming 4 or 5 successes in the
first stage .... n1 14 n2
11 ? N 25 We will use estimate p (
r/N) to design a Phase III study where r r1
r2.
24
Phase II Trials
  • Many most cancer Phase II trials follow this
    design
  • Many other diseases could there seems to be no
    standard non-cancer Phase II design
  • Might also randomize patients into multiple arms
    each with a different dose can then get a dose
    response curve

25
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
  • Rabies vaccine
  • Use of proper control group necessary due to
  • Natural history of most diseases
  • Variability of a patient's response to
    intervention

26
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

27
Purpose of Control Group
  • To allow discrimination of patient outcomes
    caused by experimental intervention from those
    caused by other factors
  • Natural progression of disease
  • Observer/patient expectations
  • Other treatment
  • Fair comparisons
  • Necessary to be informative

28
Choice of Control Group
  • Goals of Controlled Clinical Trials
  • Types of Control Groups
  • Significance of Control Group
  • Assay Sensitivity

29
Considerations in Choice of Control Group
  • Available standard therapies
  • Adequacy of the control evidence for the chosen
    design
  • Ethical considerations

30
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

31
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

32
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
  • 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

33
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

34
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

35
Changes in Definitions
36
Time Trend
Age-adjusted Death Rates for Selected Causes
United States, 1950-76
37
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
38
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39
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

40
PRAISE I vs. PRAISE IIPlacebo arms
41
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

42
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

43
Randomized ControlClinical 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

44
Advantages of Randomized Control Clinical Trial
  • 1. Randomization "tends" to produce comparable
    groups
  • Design Sources of Imbalance
  • Randomized Chance
  • Concurrent Chance Selection Bias
  • (Non-randomized)
  • Historical Chance, Selection Bias,
  • (Non-randomized) Time Bias
  • 2. Randomization produces valid statistical tests
  • Reference Byar et al (1976) NEJM

45
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

46
Bias of Non-RCTs
  • Example - Peto (1979) Biomedicine
  • Trials of anticoagulant therapy
  • Design Patients P
  • 18 Historical 900 15/18 50
  • 8 Concurrent 3000 5/8 50
  • 6 Randomized 3000 1/6 20
  • Biases
  • False positives
  • Magnitude of effect

47
Ethics of Randomization (1)
  • Statistician/clinical trialist must sell benefits
    of randomization
  • Ethics Þ 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. If MD "knows" best treatment, should not
    participate in trial
  • 2. If in doubt, randomization gives each patient
    equal chance to
  • receive one of therapies (i.e. best)
  • 3. More ethical way of practicing medicine

48

Ethics of Randomization (2)
  • Byar et al. (1976) NEJM
  • 1. RCT Þ 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

49
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

50
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
    meansalike on the average
  • Randomization
  • Each patient has the same chance of receiving any
    of thetreatments 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

51
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

52
Commonly Used Phase III Designs
  • Parallel
  • Withdrawal
  • Group/Cluster
  • Randomized Consent
  • Cross Over
  • Factorial
  • Large Simple
  • Equivalence/Non-inferiority
  • Sequential

53
Parallel Design
  • Screen
  • Trt A
  • Randomize -
  • Trt B
  • H0 A vs. B
  • Advantage
  • Simple, General Use
  • Valid Comparison
  • Disadvantage
  • Few Questions/Study

54
Fundamental Design
R A N D O M I Z E
Yes
Yes
A
Eligible
Consent
No
B
No
Dropped
Dropped
Comment Compare A with B
55
Examples of Parallel Designs
  • VEST
  • CAST
  • DCCT
  • NOTT
  • IPPB

56
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

57
Run-In Design
R A N D O M I Z E
Screen Consent
Run-In Period
Satisfactory
A
B
Unsatisfactory
Dropped
Note It is assumed that all patient entering the
run-in period are eligible and have given consent
58
Examples of Run-In Trials
  • Cardiac Arrhythmia Suppression Trial (CAST)
  • Diabetes Control and Complications Trial (DCCT)
  • Physicians Health Study (PHS)

59
Withdrawal Study
  • I Trt A
  • Trt A -
  • II Not Trt A
  • H0 How long should TRT A continue?
  • Advantage
  • Easy Access to Subjects
  • Show continued Tx Beneficial
  • Disadvantage
  • Selected Population
  • Different Disease Stage

60
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 districtin 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

61
Randomized Consent DesignZelen (NEJM, 1979)
  • Group I Regular Care
  • (TRT A)
  • Patient Randomize
  • Group II
  • Experimental Consent
  • (TRT B)

NO (TRT A)
YES (TRT B)
62
Randomized Consent (Zelen, 1979 NEJM)
  • Usual Order Proposed Order
  • Screen 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

63
Cross Over DesignH0 A vs. B
  • Scheme
  • Period
  • Group I II
  • AB 1 TRT A TRT B
  • BA 2 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)

64
Factorial Design
  • Schema

A vs. Placebo
B vs. Placebo
65
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

66
Physicians Health Study
67
Physician Health Study
68
Physicians Health Study
69
Physicians Health Study
70
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
  • Is not worse that the standard by more than some
    margin
  • Would have beaten placebo if a placebo arm had
    been included (regulatory)

71
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
  • Small sample size, leading to low power and
    subsequently lack of significant difference, does
    not imply equivalence

72
Possible outcomes in a non-inferiority trial
(observed difference 95 CI - Pocock)

? New Treatment Better New Treatment Worse ?
73

Difference in Events Test Drug Standard Drug
74
Superior vs NonInferiority Designs
?
Benefit
Harm
RR
1.0
.8
1.25
Placebo
)
(
Harm
X
)
X
(
Non-significant
)
Benefit
X
(
Active Control
?
?
Better
Worse
RR
1.0 Standard
)
X
(
Worse
)
(
X
Non-Inferior
)
(
Better
X
Modified from Fleming, 1990
75
Non-Inferiority Challenges (1)
  • Requires high quality trial
  • Poor execution favors non-inferiority
  • Requires strong control weak control favors
    non-inferiority

76
Non-Inferiority Challenges (2)
  • Treatment margin somewhat arbitrary
  • Imputed Trt vs. Plbo effect
  • Uses historical control concept
  • Imputed estimate not very robust

77
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 360752-60
78
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

79
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)

80
Captopril as Comparator
  • Captopril has well documented
  • benefits
  • Captopril 50 mg 3 times daily has
  • indication for CHF worldwide
  • Widely used, available as generic

81
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

82
All-cause death
0
Month
83
Subgroup Analyses
84
Effect of losartan relative to placebo?
Rel. Risk change captopril vs.
placebo 0.805 - 19.5 losartan vs. captopril
(OPTIMAAL) 1.126 12.6 losartan vs. putative
0.906 - 9.4 placebo (0.805 x 1.126)
SAVE, AIRE. TRACE, SMILE, GISSI III, CONSENSUS
II and ISIS IV
85
Non-Inferiority Methodology
  • Comparison New Treatment vs. Standard RRa
  • Estimate of standard vs. placebo RRb
  • (based on literature)
  • Imputed effect of New Trt vs. placebo (RRc)
  • RRc RRa x RRb

86
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

87
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

88
CAPRIEDesign
Ischemic stroke, MI, atherosclerotic PAD
Aspirin 325 mg/day PO
Clopidogrel 75 mg/day PO
Completed Trial (N 9,577)
Completed Trial (n 9,566)
Source CAPRIE Steering Comm. Lancet. 1996
3481329
89
CAPRIERisk Reduction by Major Outcomes
p 0.419 p 0.008 p 0.29 p 0.043
5.2
Ischemic stroke MI Vascular death All events
19.2
7.6
8.7
0
-40
-20
20
40
Percentage Relative Risk Reduction
90
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)

91
Classical Sequential Design (1)
  • Continue to randomize subjects until H0 is either
    rejected or accepted
  • Classic

Trt Better
Continue
Net Trt Effect
20
?
Accept H0
0
Continue
-20
Trt Worse
100
200
300
No. of Paired Observations
92
Classical Sequential Design (2)
  • Assumptions
  • Acute Response
  • Paired Subjects
  • Continuous Testing
  • Not widely used
  • Modified for group sequential designs

93
Beta-blocker Heart Attack Trial (BHAT)
  • Design Features
  • Mortality Outcome 3,837 patients
  • Randomized Men and women
  • Double-blind 30-69 years of age
  • Placebo-controlled 5-21 days post-M.I.
  • Extended follow-up Propranolol-180 or 240
    mg/day
  • Preliminary Report. JAMA 2462073-2074, 1981
  • Final Report. JAMA 2471707-1714, 1982

94
BHAT GSB
95
Therapeutic vs. Prevention Trials
  • Prevention Trials
  • Primary - Prevent disease
  • Secondary - Prevent recurrence
  • Therapeutic Trials
  • Treat disease
  • Basic fundamentals apply equally
  • Some differences exist
  • Complexity
  • Recruitment Strategies
  • Compliance
  • Length of Follow-up
  • Size

96
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

97
Masking or Blinding (1)
  • 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

98
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

99
Blinding or Masking (3)
  • 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

100
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

101
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

102
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

103
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

104
Unbiased Evaluation
  • Investigator Bias - (Taste Smell Study)
  • (Henkin et al, 1972 1976)
  • Single Blind Double Blind
  • Zinc 8/8 5/8
  • Placebo 0/8 7/8
  • Number of variables with significant
    improvement/Number of variables

105
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

106
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

107
Design Summary
  • Design used must fit goals of trial
  • RCT minimizes bias
  • Superiority vs. Non-Inferiority trial challenges
  • Use blinding when feasible to minimize bias after
    randomization

108
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