STATISTICS 542 Introduction to Clinical Trials CLINICAL TRIAL

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

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” 542 -03 -#2

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 542 -03 -#3

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 542 -03 -#4

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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 542 -03 -#6

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. . 542 -03 -#7

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 1 542 -03 -#8

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 542 -03 -#9

Dose-response curves used in simulations (1) 542 -03 -#10

Dose-response curves used in simulations (2) 542 -03 -#11

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 542 -03 -#12

Summary of Designs Considered (2) (Storer, Biometrics 45: 925 -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 542 -03 -#13

Summary of Designs Considered (3) (Storer, Biometrics 45: 925 -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 542 -03 -#14

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 542 -03 -#15

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 542 -03 -#16

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. 542 -03 -#17

Phase II Design (4) (Why 14 failures? ) • Compute probability of consecutive failures Patient 1 2 3 --8 --14 Prob 0. 8 0. 64 (0. 8 x 0. 8) 0. 512 (0. 8 x 0. 8) --0. 16 --0. 044 • If drug 20% effective, there would be ~95. 6% chance of at least one success • If 0/14 success observed, reject drug 542 -03 -#18

Phase II Design (5) • Stage I Sample Size Table I Rejection Error 5 5% 59 10% 45 10 29 22 Effectiveness (%) 15 20 25 40 50 19 14 11 6 5 15 11 9 5 4 542 -03 -#19

Stage II Sample Size (1) • Based on desired precision of effectiveness estimate r 1 = # of successes in Stage 1 n 1= # of patients in Stage 1 Now precision of total sample N=(n 1 + n 2) Let 542 -03 -#20

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 (n 2) based on desired precision 542 -03 -#21

Additional Patients for Stage II (n 2) (Rejection Rate 5% for Stage I) 542 -03 -#22

Additional Patients for Stage II (n 2) (Rejection Rate 5% for Stage I) We might require 10% precision with 20% desired effectiveness. Assuming 4 or 5 successes in the first stage. . n 1 = 14 n 2 = 11 N = 25 We will use estimate p (= r/N) to design a Phase III study where r = r 1 + r 2. 542 -03 -#23

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 542 -03 -#24

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 1950 s • 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 542 -03 -#25

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 542 -03 -#26

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 542 -03 -#27

Choice of Control Group • Goals of Controlled Clinical Trials • Types of Control Groups • Significance of Control Group • Assay Sensitivity 542 -03 -#28

Considerations in Choice of Control Group • Available standard therapies • Adequacy of the control evidence for the chosen design • Ethical considerations 542 -03 -#29

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 542 -03 -#30

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 542 -03 -#31

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 542 -03 -#32

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 542 -03 -#33

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 542 -03 -#34

Changes in Definitions 542 -03 -#35

Time Trend Age-adjusted Death Rates for Selected Causes: United States, 1950 -76 542 -03 -#36

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 542 -03 -#37

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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 542 -03 -#39

PRAISE I vs. PRAISE II Placebo arms 542 -03 -#40

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 542 -03 -#41

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 542 -03 -#42

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” 542 -03 -#43

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 & Selection Bias Chance, Selection Bias, & Time Bias 2. Randomization produces valid statistical tests Reference: Byar et al (1976) NEJM 542 -03 -#44

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 542 -03 -#45

Bias of Non-RCT’s • Example - Peto (1979) Biomedicine Trials of anticoagulant therapy Design Effect 18 Historical #Patients 900 P<0. 05 Observed 15/18 50% 8 Concurrent 3000 5/8 50% 6 Randomized 3000 1/6 20% • Biases – False positives – Magnitude of effect 542 -03 -#46

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. 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 542 -03 -#47

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 542 -03 -#48

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 542 -03 -#49

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 542 -03 -#50

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 542 -03 -#51

Commonly Used Phase III Designs • • • Parallel Withdrawal Group/Cluster Randomized Consent Cross Over Factorial Large Simple Equivalence/Non-inferiority Sequential 542 -03 -#52

Parallel Design Screen Trt A Randomize Trt B • H 0: A vs. B • Advantage – Simple, General Use – Valid Comparison • Disadvantage – Few Questions/Study 542 -03 -#53

Fundamental Design Eligible Yes Consent No No Dropped Yes R A N D O M I Z E A B Comment: Compare A with B 542 -03 -#54

Examples of Parallel Designs • • • VEST CAST DCCT NOTT IPPB 542 -03 -#55

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 542 -03 -#56

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 542 -03 -#57

Examples of Run-In Trials • Cardiac Arrhythmia Suppression Trial (CAST) • Diabetes Control and Complications Trial (DCCT) • Physicians Health Study (PHS) 542 -03 -#58

Withdrawal Study I Trt A II Not Trt A - • H 0: How long should TRT A continue? • Advantage – Easy Access to Subjects – Show continued Tx Beneficial • Disadvantage – Selected Population – Different Disease Stage 542 -03 -#59

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 542 -03 -#60

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) 542 -03 -#61

Randomized Consent (Zelen, 1979 NEJM) Usual Order Screen Proposed Order Screen Consent 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% 2 x 542 -03 -#62

Cross Over Design H 0: 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) 542 -03 -#63

Factorial Design • Schema A vs. Placebo B vs. Placebo 542 -03 -#64

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. 53 542 -03 -#65

Physicians Health Study 542 -03 -#66

Physician Health Study 542 -03 -#67

Physicians Health Study 542 -03 -#68

Physicians Health Study 542 -03 -#69

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) 542 -03 -#70

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 noninferiority • 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” 542 -03 -#71

Possible outcomes in a non-inferiority trial (observed difference & 95% CI - Pocock) New Treatment Better New Treatment Worse 542 -03 -#72

Difference in Events Test Drug – Standard Drug 542 -03 -#73

Superior vs Non. Inferiority Designs Benefit Harm 1. 0 Placebo . 8 ( X ( ( 1. 25 ) Harm X ) Non-significant ) Benefit X Active Control Better Worse 1. 0 Standard ( X ( Better( X RR ) Worse ) Non-Inferior ) Modified from Fleming, 1990 542 -03 -#74

Non-Inferiority Challenges (1) • Requires high quality trial • Poor execution favors non-inferiority • Requires strong control; weak control favors non-inferiority 542 -03 -#75

Non-Inferiority Challenges (2) • Treatment margin somewhat arbitrary • Imputed Trt vs. Plbo effect – Uses historical control concept – Imputed estimate not very robust 542 -03 -#76

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 M. Romo Data Safety and Monitoring Board D. Julian (Chair), A. Bayés de Luna, D. L. De. Mets, C. D. Furberg, W. W. Parmley and L. Rydén Lancet 2002; 360: 752 -60 542 -03 -#77

Rationale • ACE (Angiotension Conversion Enzyme) inhibitors reduce mortality in high risk post MI patients • Agiotension II Receptor Blockers (ARBs) are an alternative because of more complete blockade • ACE may have better tolerability 542 -03 -#78

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) 542 -03 -#79

Captopril as Comparator • Captopril, an ACE inhibitor, has well documented benefits • Captopril 50 mg 3 times daily has indication for CHF worldwide • Widely used, available as generic 542 -03 -#80

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 542 -03 -#81

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 2504 2534 2432 2463 2390 2423 2344 2374 2301 2329 36 1285 1309 542 -03 -#82

Subgroup Analyses n Age <65 2170 65 -74 1840 >75 1467 Gender Female 1575 Male 3902 Diabetes Non-diabetic 4537 Diabetic 940 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 542 -03 -#83

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 542 -03 -#84

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 542 -03 -#85

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 542 -03 -#86

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 542 -03 -#87

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 542 -03 -#88

CAPRIE Risk Reduction by Major Outcomes 5. 2 Ischemic stroke 19. 2 MI Vascular death 7. 6 p = 0. 419 p = 0. 008 p = 0. 29 p = 0. 043 All events 8. 7 -40 -20 0 20 40 Percentage Relative Risk Reduction 542 -03 -#89

Sequential Design • Continue to randomize subjects until H 0 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) 542 -03 -#90

Classical Sequential Design (1) • Continue to randomize subjects until H 0 is either rejected or “accepted” • Classic Trt Better Net 20 Trt 0 Effect Continue Accept H 0 -20 Continue Trt Worse 100 200 300 No. of Paired Observations 542 -03 -#91

Classical Sequential Design (2) • Assumptions – Acute Response – Paired Subjects – Continuous Testing • Not widely used • Modified for group sequential designs 542 -03 -#92

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 542 -03 -#93

BHAT GSB 542 -03 -#94

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 542 -03 -#95

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 542 -03 -#96

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 542 -03 -#97

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 542 -03 -#98

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 542 -03 -#99

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 542 -03 -#100

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 542 -03 -#101

Unbiased Evaluation Subject Bias (NIH Cold Study) (Karlowski, 1975) Duration of Cold (Days) Blinded Unblinded Subjects Placebo 6. 3 8. 6 Ascorbic Acid 6. 5 4. 8 542 -03 -#102

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 542 -03 -#103

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 542 -03 -#104

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 542 -03 -#105

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 542 -03 -#106

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 542 -03 -#107

West Campus 542 -03 -#108