542-03-#1 STATISTICS 542 Introduction to Clinical Trials CLINICAL TRIAL DESIGN.

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STATISTICS 542STATISTICS 542

Introduction to Clinical TrialsIntroduction to Clinical Trials

CLINICAL TRIAL DESIGNCLINICAL TRIAL DESIGN

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Types of Clinical ResearchTypes of Clinical Research1. Case Reports

Anecdotal Problem

2. Observationala. Case Control/Retrospective (lung cancer)b. Cross Sectional (WESDR) Beaver Damc. 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”

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Phases of Clinical Trials (Cancer) [1]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

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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

Phases of Clinical Trials (Cancer) [2]Phases of Clinical Trials (Cancer) [2]

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Phase I DesignPhase I DesignTypical/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 . . . .

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Typical SchemeTypical Scheme1. 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

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Standard Phase I DesignStandard 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

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Dose-response curves used in simulations (1)

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Dose-response curvesused in simulations (2)

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Summary of Designs Considered (1)Summary of Designs Considered (1)(Storer, Biometrics 45:925-37, 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

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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

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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 patientsCan speed up process to get to target dose range

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Phase II Design (1)Phase II Design (1)

References:Gehan (1961) Journal of Chronic DisordersFleming (1982) BiometricsStorer (1989) Statistics in Medicine

• Goal– Screen for therapeutic activity– Further evaluate toxicity– Test using MTD from Phase I– If drug passes screen, test further

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• 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

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Phase II Design (3)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 anddeclare true drug response 20%

3. If 1+/14 responses, add 15-40 more patients

4. Estimate response rate & C.I.

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Phase II Design (4)Phase II Design (4)(Why 14 failures?)(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 Prob1 0.82 0.64 (0.8 x 0.8)3 0.512 (0.8 x 0.8 x

0.8)--- ---8 0.16--- ---14 0.044

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• 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

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Stage II Sample Size (1)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

111 /nrp ˆ

1n

)p̂(1p̂)p̂SE( 11

1

N

)p(1p)pSE( **

*

ˆˆˆ

1*pp ˆˆ

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Stage II Sample Size (2)Stage II Sample Size (2)

)p̂1.15SE(p̂p̂11

*

To be conservative, Gehan suggested

upper 75% confidence limit from first sample

• Thus, we can generate a table for size ofsecond stage (n2) based on desired precision

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Additional Patients for Stage II (nAdditional Patients for Stage II (n22))

(Rejection Rate 5% for Stage I)(Rejection Rate 5% for Stage I)Therapeutic Effectiveness (%)Required

Precision(SE)

Number ofSuccesses

Stage I5 10 15 20 25 30

n1 59 29 19 14 11 9

1 0 4 30 45 60 70

2 0 17 45 63 78 87

3 0 28 58 76 87 91

4 0 38 67 83 89 91

+1 SE

5%

5 0 46 75 86 89 91

1 0 0 0 1 7 11

2 0 0 0 6 12 15

3 0 0 1 9 14 16

4 0 0 3 11 14 16

+1 SE

10%

5 0 0 5 11 14 16

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Additional Patients for Stage II (nAdditional Patients for Stage II (n22))

(Rejection Rate 5% for Stage I)(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.

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Phase II TrialsPhase 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

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• 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

Phase III IntroductionPhase III Introduction

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Phase III DesignPhase 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

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Purpose of Control GroupPurpose 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

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Choice of Control GroupChoice of Control Group

• Goals of Controlled Clinical Trials

• Types of Control Groups

• Significance of Control Group

• Assay Sensitivity

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Goals of Controlled Goals of Controlled Clinical Trials (1)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

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Goals of Controlled Goals of Controlled Clinical Trials (2)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

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Superiority vs NoninferioritySuperiority vs Noninferiority

1.0

( )

( )

( )

.8 1.25

Benefit HarmRR

Better Worse

RR

Active Control

Placebo

Harm

Non-significant

Benefit

( )

( )

( )

1.0Standard

Plbo

Worse

Non-Inferior

BetterModified from Fleming, 1990

X

X

X

X

X

X

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Considerations in Choice of Considerations in Choice of Control GroupControl Group

• Available standard therapies

• Adequacy of the control evidence for the chosen design

• Ethical considerations

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Significance of Control GroupSignificance 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

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Type of ControlsType 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

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Use of Placebo ControlUse 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

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• 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 newtreatments

• Two sources of historical control data:• Literature Subject to publication bias• Data base

Historical Control Study (1)Historical Control Study (1)

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• 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


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Changes in DefinitionsChanges in Definitions

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Time TrendTime TrendAge-adjusted Death Rates for Selected Causes: United States, 1950-76

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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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• 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

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PRAISE I vs. PRAISE IIPRAISE I vs. PRAISE IIPlacebo armsPlacebo arms

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Concurrent ControlsConcurrent 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

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Biases in Concurrent Control StudyBiases 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

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Randomized ControlRandomized ControlClinical TrialClinical 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”

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Advantages of Randomized Advantages of Randomized Control Clinical TrialControl Clinical Trial

1. Randomization "tends" to produce comparable groups

Design Sources of Imbalance

Randomized ChanceConcurrent 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

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Disadvantages of Randomized Disadvantages of Randomized Control Clinical TrialControl 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

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Bias of Non-RCT’sBias of Non-RCT’s• Example - Peto (1979) Biomedicine

Trials of anticoagulant therapy

Design #Patients P<0.05 Observed

Effect

18 Historical 900 15/18 50%

8 Concurrent 3000 5/8 50%

6 Randomized 3000 1/6 20%

• Biases– False positives

– Magnitude of effect

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Ethics of Randomization (1)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. 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

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• 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

Ethics of Randomization (2)Ethics of Randomization (2)

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Ethics of Randomization (3)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

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Comparing TreatmentsComparing 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

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Randomized Phase III Randomized Phase III Experimental DesignsExperimental 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

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Commonly Used Phase III DesignsCommonly Used Phase III Designs

• Parallel

• Withdrawal

• Group/Cluster

• Randomized Consent

• Cross Over

• Factorial

• Large Simple

• Equivalence/Non-inferiority

• Sequential

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Parallel DesignParallel DesignScreen

Trt A

Randomize -

Trt B

• H0: A vs. B

• Advantage– Simple, General Use– Valid Comparison

• Disadvantage– Few Questions/Study

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Fundamental DesignFundamental Design

Eligible Consent

RANDOMIZE

No No

DroppedDropped

Yes Yes

B

A

Comment: Compare A with B

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Examples of Parallel DesignsExamples of Parallel Designs

• VEST• CAST• DCCT• NOTT• IPPB

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Run-In DesignRun-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

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Run-In DesignRun-In Design

Screen & Consent

Run-In Period

RANDOMIZE

Unsatisfactory

Dropped

B

A

Note: It is assumed that all patient entering the run-in period are eligible and have given consent

Satisfactory

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Examples of Run-In TrialsExamples of Run-In Trials

• Cardiac Arrhythmia Suppression Trial (CAST)

• Diabetes Control and Complications Trial (DCCT)

• Physicians Health Study (PHS)

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Withdrawl StudyWithdrawl 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

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Cluster Randomization DesignsCluster 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

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Randomized Consent DesignRandomized Consent DesignZelen (Zelen (NEJM, 1979)NEJM, 1979)

Group I: Regular Care(TRT A)

Patient RandomizeGroup II: Experimental Consent

(TRT B)

NO(TRT A)

YES(TRT B)

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Randomized ConsentRandomized Consent (Zelen (1979) NEJM)

Usual Order Proposed OrderScreen 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

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Cross Over DesignCross Over DesignHH00: A vs. B: A vs. B

Scheme Period

Group III

AB 1 TRT A TRT BBA 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)

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Factorial DesignFactorial Design

• SchemaFactor I

Placebo Trt B

Factor IIPlacebo N/4 N/4

Trt A N/4 N/4

B vs. Placebo

A vs. Placebo

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Factorial DesignFactorial 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

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Physicians Health StudyPhysicians Health Study

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Physician Health StudyPhysician Health Study

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Superiority vs. Superiority vs. Non-Inferiority TrialsNon-Inferiority Trials

Superiority Design: Show that new treatment is better than the control or standard (maybe a placebo)

Non-inferiority: Show that the new treatmenta) Is not worse that the standard by more than

some margin

b) Would have beaten placebo if a placebo arm had been included (regulatory)

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Equivalence/Non-inferiority TrialEquivalence/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”

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Difference in EventsTest Drug – Standard Drug

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Active Control DesignActive Control Design

1.0

( )

( )

( )

.8 1.25

Benefit HarmRR

Better Worse

RR

Active Control

Placebo

Harm

Non-significant

Benefit

( )

( )

( )

1.0Standard

Plbo

Worse

Non-Inferior

BetterModified from Fleming, 1990

X

X

X

X

X

X

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Non-Inferiority Challenges (1)Non-Inferiority Challenges (1)

• Requires high quality trial

• Poor execution favors non-inferiority

• Requires strong control; weak control favors non-inferiority

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Non-Inferiority Challenges (2)Non-Inferiority Challenges (2)

• Treatment margin somewhat arbitrary

• Imputed Trt vs. Plbo effect – Uses historical control concept– Imputed estimate not very robust

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Steering CommitteeJ. 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 CommitteeJ. G. F. Cleland and M. Romo

Data Safety and Monitoring BoardD. Julian (Chair), A. Bayés de Luna, D. L. DeMets,

C. D. Furberg, W. W. Parmley and L. Rydén

OPtimal Trial In Myocardial infarction with the Angiotensin II Antagonist Losartan

OPTIMAALOPTIMAAL

Lancet 2002; 360:752-60

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RationaleRationale• 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

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HypothesisHypothesisLosartan (50 mg) is superior or non-inferior to captopril (150 mg) in decreasing all-cause mortality in high-risk patients following AMI

• Double-blind, randomized, parallel, investigator initiated, no placebo control • Event driven (all-cause death = 937)• Multicentre (Denmark, Finland, Germany,

Ireland, Norway, Sweden, UK)

Study designStudy design

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Captopril as ComparatorCaptopril 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

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Statistical MethodsStatistical 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

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All-cause deathAll-cause death

losartan (n) 2744 2504 2432 2390 2344 2301 1285

captopril (n) 2733 2534 2463 2423 2374 2329 1309

Month6 12 18 24 30 36

0

5

10

15

20

25E

ven

t ra

te (

%)

losartan (n=499 events)captopril (n=447 events)

Relative Risk = 1.13 (0.99 to 1.28); p=0.069

0

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Subgroup Analyses

0.6 1 1.5 2

losartan better captopril better

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 1060Heart failure 4417

Infarct location Infarct ant/lat 3821Infarct inf/post 1152

Prior MI No prior MI 4479Prior MI 998

Thrombolytic use No thromb use 2499Thromb use 2978

-blocker use No -blocker use 1171-blocker use 4306

Overall 5477

n Hazard ratio (95% CI)

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Effect of losartan Effect of losartan relative to placebo?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

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Non-Inferiority MethodologyNon-Inferiority Methodology

a) Comparison: New Treatment vs. StandardRRa

b) Estimate of standard vs. placebo RRb

(based on literature)

c) Imputed effect of New Trt vs. placebo (RRc)

RRc = RRa x RRb

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Assay SensitivityAssay 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

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Assay Sensitivity in Assay Sensitivity in Non-Inferiority TrialsNon-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

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Large, Simple TrialLarge, 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

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CAPRIECAPRIEDesign

Ischemic stroke, MI, atherosclerotic PAD

Clopidogrel75 mg/day PO

Aspirin325 mg/day PO

Completed Trial(N = 9,577)

Completed Trial(n = 9,566)

Source: CAPRIE Steering Comm. Lancet. 1996; 348:1329

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CAPRIECAPRIERisk Reduction by Major Outcomes

Ischemic stroke

MI

Vascular death

All events

Percentage Relative Risk Reduction

-40 -20 0 20 40

8.7

7.6

19.2

5.2 p = 0.419

p = 0.008

p = 0.29

p = 0.043

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Sequential DesignSequential 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)

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

•Classic

Net

Trt

Effect

100 200 300No. of Paired Observations

Trt Worse

Continue

Accept H0

Trt Better

Continue

-20

0

20

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Classical Sequential Design (2)Classical Sequential Design (2) • Assumptions

– Acute Response– Paired Subjects– Continuous Testing

• Not widely used

• Modified for group sequential designs

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Beta-blocker Heart Attack Trial Beta-blocker Heart Attack Trial (BHAT)(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 246:2073-2074, 1981

Final Report. JAMA 247:1707-1714, 1982

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BHAT GSB

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Therapeutic vs. Prevention TrialsTherapeutic 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

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Confounding BiasConfounding 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

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Blinding or Masking (1)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

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Blinding or Masking (2)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

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Masking or Blinding (3)Masking or Blinding (3)

• Keeping the identity of treatment assignments masked for:1. Subject2. Investigator, treatment team or evaluator3. 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

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Feasibility of MaskingFeasibility 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

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Reasons for Subject MaskingReasons 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

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Unbiased Evaluation 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

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Reasons for Reasons for Treatment Team Masking 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

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Unbiased EvaluationUnbiased 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

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Reasons for Evaluator Reasons for Evaluator (Third Party) Masking (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

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Reasons for Monitoring Reasons for Monitoring Committee MaskingCommittee 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

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Design SummaryDesign Summary

• Design used must fit goals of trial

• RCT minimizes bias

• Superiority vs. Non-Inferiority trial challenges

• Use blinding when feasible

542-03-#1 STATISTICS 542 Introduction to Clinical Trials CLINICAL TRIAL DESIGN.

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