The document discusses the importance of randomized controlled trials (RCTs) in clinical research, emphasizing that only sufficiently large RCTs can adequately control for confounding variables to minimize bias. It also explores the challenges and ethical considerations involved in conducting RCTs, such as practical impossibilities in certain scenarios, and outlines key elements necessary for designing effective trials, including randomization, blinding, and sample size determination. Additionally, the text highlights the importance of intention-to-treat analysis and correctly addressing potential biases to ensure the validity of study findings.

1. A RANDOMIZED CONTROLLED
CLINICAL TRIAL

2. LEVELS OF EVIDENCE FOR CLINICAL
RESEARCH STUDY DESIGNS
Schillaci et al. Hypertension. 2013;62:470

3. OBSERVATIONAL VS. RANDOMIZED TRIALS
• “There are known knowns; there are things
we know we know. We also know there are
known unknowns; that is to say, we know
there are some things we do not know. But
there are also unknown unknowns--the ones
we don’t know we don’t know.”
- Donald Rumsfeld

4. OBSERVATIONAL VS. RANDOMIZED TRIALS
• Observational Studies
– Distribution of baseline factors that may impact outcome
(e.g., age, meds, comorbidities) vary in study groups
• Known knowns: known to impact outcome, collected
– Statistical adjustment, matching
• Known unknowns: known to impact outcome, can’t be collected
• Unknown unknowns: don’t know impact outcome, not collected
• Randomized Trials
– All factors (known and unknown) that may impact
outcome equally distributed among study groups

5. RANDOMIZED CONTROLLED TRIAL
• Only randomized trials of sufficient size can
adequately control for known and unknown
confounding variables to minimize bias
• No substantive differences between groups
except study intervention (randomly assigned)
– Difference between groups in predefined outcome
can be attributed to the intervention being studied
Hennekens & Buring Epidemiology in Medicine. 1987

6. DO WE ALWAYS NEED AN RCT TO
DOCUMENT BENEFIT OF AN INTERVENTION?
• “Perception that parachutes are a successful
intervention based largely on anecdotal evidence”
• No RCTs identified in systematic review
– Under exceptional circumstances apply common sense
BMJ 2003;327:1459

7. RCT MAY NOT BE POSSIBLE OR PRACTICAL
• Not ethical/possible to assign intervention
– Cigarette smoking and lung cancer
– H. pylori infection and ulcers
• Impractically large sample size
– Very low-incidence outcome
• e.g., rare side effect of medication
• Impractically long duration
– Outcome requires many years to develop
• e.g., development of cancer

8. RANDOMIZED CONTROLLED TRIALS
First Steps
• Clinically relevant question
– Greatest impact if limited information or high
variability in care or outcomes
– Can be answered by properly designed RCT
• Feasible to perform at your center(s)

9. RANDOMIZED CONTROLLED TRIALS
First Steps
• Clinically relevant question
– Greatest impact if limited information or high
variability in care or outcomes
– Can be answered by properly designed RCT
• Feasible to perform at your center(s)
• Systematic review
– Identify available information
– Justify importance of question
– Help design study

10. RANDOMIZED CONTROLLED TRIALS
First Steps
• Define key elements of study
– Population
– Intervention
– Comparator
– Outcome
• State primary hypothesis
• Expected result for primary outcome in population
– e.g., in patients with cirrhosis fewer deaths with
new intervention vs. control

11. STUDY DESIGN

12. RANDOMIZATION
• Generate sequence of allocation
– Computer generated, random numbers table
– Randomize in blocks
• Other features of randomization include
– Concealed allocation
– Non-manipulable allocation schedule
• Off-site randomization schedule ideal
– Stratification
• Most important factor(s) that may impact endpoint

13. CONCEALED ALLOCATION
• Concealed allocation is an extension of
randomization
• When obtaining informed consent to enroll
a patient into a trial, the investigator does
not know if the next patient will get new
treatment or control

14. CONCEALED ALLOCATION
• RCT comparing new therapy vs. placebo for
abdominal pain in irritable bowel syndrome
• Investigator interviews the next eligible
patient, who complains of long-term severe,
unrelenting symptoms that have never
responded to previous medical therapy
• Next patient to enter trial will get placebo

15. CONCEALED ALLOCATION
• Investigator thinks that placebo is unlikely
to relieve abdominal pain in this patient
– Investigator may subconsciously try to
convince patient not to enroll in the trial
• Consequence: patients with severe
abdominal pain will NOT be evenly divided
between new therapy and placebo groups

16. STRATIFICATION
• To assure baseline factor(s) that impact study
outcome equally distributed in study groups
– Especially useful in smaller trials
• Choose factor(s) that have greatest impact on
primary outcome
– Aspirin use in MI study
• Separate randomization schedules for patients
with and without factor

17. RANDOMIZATION
Block Size (e.g., 4, 10, 20; Random)
• Assures equal number in each study arm for
every successive block of patients enrolled
– Prevents unequal numbers in study arms
– Prevents differences in distribution over time
• e.g., study intervention mostly early, comparator mostly later
– Disadvantage: if block size figured out, next
allocation may be predictable (unconcealed)—
selection bias
• Larger block sizes; random sequences of block sizes

18. BLINDING
• Not known if subject getting new therapy or control
– Subjects
– Healthcare providers making management decisions
– Investigators collecting/analyzing data
• Prevents bias in management decisions and in
assessment of outcomes by subject or investigator
– Knowledge receiving placebo or active drug may influence
• Administration of another therapy that my impact outcome
• Assessment of symptoms, signs (endpoints)

19. BLINDING
• Identical appearing therapies
– Real vs. sham surgery/procedure
• Surgical team uninvolved in further care/assessment
• Double-dummy
– Subjects receive identical active and control
therapy together
• Side effect of a therapy may unblind subjects
– Assess whether unblinded

20. TREATMENT EFFECT OVERESTIMATED
WITHOUT RANDOMIZATION AND BLINDING
Treatment
Placebo
Treatment
Placebo
Treatment
Placebo
0
5
10
15
20
25
30
35
Not
Randomized Randomized
Concealed
Allocation;
Blinded
ase
Fatality
Rates
Chalmers, et al. N Engl J Med 1983; 309: 1358

21. PATIENT POPULATION
• Inclusion and exclusion criteria
– Broad: exclude few, more generalizable
– Restricted: exclude many, less generalizable
• Prospectively screen consecutive patients
with condition of interest
– Skipping patients may introduce bias
• Screening log
– Subjects screened, but not enrolled
• Brief characteristics, reason not enrolled
– ?Differences from those enrolled
– Is study generalizable?

22. STUDY INTERVENTIONS
• Define all aspects of study interventions so
uniform in trial, able to be reproduced
• Control
– Placebo control
• Best to define efficacy of study therapy
• May not be ethical, practical
– Can’t withhold standard care if documented effective
– Active control (a current standard)
• Hypothesis: new therapy superior, non-inferior, or
equivalent to active control

23. ENDPOINTS
• What do you want to achieve with the new
intervention
– Primary endpoint
– Additional endpoints
– Surrogate vs. clinical endpoints
• Surrogate endpoint: measure of treatment effect
felt likely to correlate with clinical endpoint
• e.g., gastric acid inhibition for ulcer prevention

24. CLINICALLY MEANINGFUL
ENDPOINTS PREFERRED
• Which study endpoint would alter practice?
– Lab test (CRP) or clinical outcome (death)
• Studies of intermediate/surrogate endpoints
may indicate areas for further research, but
generally don’t alter patient management
• Some surrogate endpoints are accepted as
“true” indicators of clinical outcomes
– e.g., blood pressure, cholesterol, colon polyps

25. SAMPLE SIZE
DETERMINATION

26. SAMPLE SIZE DETERMINATION
Assumptions for Superiority Study
• Primary endpoint result for the intervention
• Primary endpoint result for the comparator
– Assumptions based on available data, clinical judgment
• Hypothesized difference should be clinically meaningful, realistic
• α
– p = 0.05
– probability of finding difference when doesn’t exist (type I)
• Power (1 – β)
– Probability of finding difference when does exist
• e.g., 80%, 90%
• β: probability of not finding a difference when does exist (type II)

27. SAMPLE SIZE DETERMINATION
Why Did They Stop the Study When They Did?
• RCT: Wonderdrug vs. placebo in pancreatic cancer
• Primary endpoint: 5-yr survival
– Wonderdrug: 50%
– Placebo: 10%
– P-value (α = 0.05)
– 90% power to detect 40% difference between
Wonderdrug and placebo
• 52 patients required (if 1:1 randomization)

28. SAMPLE SIZE DETERMINATION
Assumptions for Non-Inferiority Study
• Determine non-inferiority margin
– Clinical: maximal difference that would be considered
clinically non-inferior
• Not unacceptably worse than the control
– Statistical: maintain benefit above placebo
• Control is 20% more efficacious than placebo
• Margin of 10% retains half control treatment effect
• Margin (e.g., control – test drug = 3%) less than
upper bound of CI of difference observed in study
– Difference = 0% (95% CI -5% to 5%): Not non-inferior
– Difference = 0% (95% CI -1% to 1%): Non-inferior

29. SAMPLE SIZE DETERMINATION
Non-Inferiority Study
• Determine non-inferiority margin
– Clinical: maximal difference that would be considered
clinically non-inferior
• Not unacceptably worse than the control
– Statistical: maintain benefit above placebo
• Control is 20% more efficacious than placebo
• Margin of 10% retains half control treatment effect
• Margin (e.g., control – test drug = 3%) less than
upper bound of CI of difference observed in study
– Difference = 0% (95% CI -5% to 5%): Not non-inferior
– Difference = 0% (95% CI -1% to 1%): Non-inferior
Potential reasons to do non-inferiority study
• New intervention has some other advantage that would recommend
it if efficacy similar (non-inferior) to current standard therapy
• e.g., cheaper, safer, easier to use (pill vs. enema), more readily
available (oral rehydration vs. IV fluids); commercial

30. NON-INFERIORITY STUDY: FDA EXAMPLE
• New thrombolytic (R) vs. approved therapy (S)
– Outcome: Mortality
• New thrombolytic must retain ≥50% benefit of
approved therapy to be acceptable alternative
• Mortality difference S vs. placebo
– 2.6% (lower bound 95% CI = 2.1%)
• Study has to rule out 1.05% increase in mortality
with R compared to S
– 95% CI of difference in mortality for R vs. S < 1.05%
• Accept 1.05% increase as not unacceptably worse
http://www.fda.gov/downloads/Drugs/GuidanceComplianceRegulatoryInformation/Guidances/UCM202140.pdf

31. IS THE SAMPLE SIZE FEASIBLE
• Review medical records at study center(s) to
– Determine number who meet enrollment criteria
– Confirm assumptions about outcomes
• “Preparatory to research” review doesn’t require IRB
approval of the protocol
– “This type of access is limited to a review of data to assist
in formulating a hypothesis, determining the feasibility of
conducting the study . . . or other similar uses that precede
the development of an actual protocol.”
– Submit Request for Access form

32. 32
POPULATIONS FOR ANALYSIS
Intention to Treat Analysis
All randomized patients are included in final
data analysis
Per Protocol Analysis
Only patients who complete the trial according
to protocol are analyzed

33. POPULATIONS FOR ANALYSIS
• Intention-to-treat population
– All patients randomized regardless of follow-up
or receipt of study intervention
• Per-protocol population excludes those who
– Did not receive sufficient study intervention
– Did not return for adequate follow-up
– Had major violations of inclusion criteria
• e.g., did not have the disease being studied
– Had major violations during the study
• Took non-study PPI during PPI vs. placebo study

34. INTENTION-TO-TREAT ANALYSIS
Example
• Comparison of radiology procedure (TIPS)
vs. drug (β-blocker) for prevention of
recurrent variceal bleeding with death as the
primary endpoint
• If a patient is randomized to get TIPS and
dies from bleeding before the procedure
can be done, should the patient be included
in the final data analysis?

35. POPULATIONS FOR ANALYSIS
• Choose the most conservative analysis
– Less likely to favor intervention, be overly optimistic
• Superiority study
– Per-protocol assesses intervention under optimal
circumstances (not real world, ignores study quality)
• e.g., excluded if non-adherence, protocol violations, drop-out
– ITT avoids bias to treatment difference and superiority
• Non-inferiority study
– ITT can bias to no treatment difference (non-inferiority)
• e.g., non-adherence, drop-outs, misclassified subjects/endpoints
– Per protocol analysis should be included

36. COMPLETE FOLLOW-UP OF PATIENTS
Another Requirement for High Methodologic Quality
• If numerous patients are lost to follow-up,
results of the trial may not be accurate
– Predefine method to deal with such patients
• Last observation carried forward
• Imputation methods
• Re-calculate results assuming that patients lost to
follow-up in new treatment group had bad outcome
and patients lost to follow-up in control group had
good outcome

37. RECRUITMENT AND RETENTION
• Engagement, communication with participants
before and throughout trial
– Brochures, ads, social media, phone/text/email/websites
• Reminders for study personnel and participants
• Benefits of participation for subjects
– Societal, personal, financial reimbursement for time
• Benefits of participation for research personnel
– Academic (e.g., authorship), financial
• Identify and minimize barriers to participation
– Easy access to study personnel and activities
• Participation as non-onerous as possible

38. STUDY ANALYSIS
• Predefine presentation of data
– Proportions vs. time-to-event curves
– Mean vs. median
• Predefine statistical analyses
– Comparisons for primary, additional outcomes
– Subgroup analyses
– Other analyses
• e.g., multivariable analyses, sensitivity analyses

39. COMPARING THE
STUDY GROUPS

40. P-VALUE: DID DIFFERENCE BETWEEN TREATMENT
AND CONTROL OCCUR DUE TO CHANCE?
• Null hypothesis
– “True” proportion of success with treatment
equals “true” proportion of success with control
• If the null hypothesis correct and treatments
are equally effective, p-value indicates
– Probability of observing a difference between
treatment and control at least this large
• Probability that difference at least this large is
due to chance

41. • A small p-value (< 0.05) means finding a
difference at least this large is unlikely if
the null hypothesis (treatments equally
effective) is true
– Reject the null hypothesis
P-VALUE: DID DIFFERENCE BETWEEN TREATMENT
AND CONTROL OCCUR DUE TO CHANCE?

42. • Increased chance comparisons “significant”
• Type 1 error: 2 endpoints: ~10%; 10 endpoints: ~40%
– Process to control rate of false positives
• Single primary outcome, limited additional outcomes
• Correct for multiplicity
– Bonferroni (p/# analyses: 0.05/10 = 0.005)
– Hierarchical testing (predefined sequence, stop when p>0.05)
– Other techniques
• Provide results without claims of “significance”
– Don’t perform many analyses stating significance is p<0.05
for all analyses
P-VALUE WITH MULTIPLE COMPARISONS
http://www.fda.gov/downloads/Drugs/GuidanceComplianceRegulatoryInformation/Guidances/UCM536750.pdf

43. 95% CONFIDENCE INTERVALS
A More Precise Tool to Assess the Results
• New therapy vs. control
– Absolute difference = 9%, 95% CI 4 – 14%
– If trial repeated 100 times, difference would
be between 4% and 14% in 95 of 100 trials

44. • Tighter the interval around the observed
result, the more precise the estimate
– Difference = 0%: -30% to 30% vs. -1% to 1%
95% CONFIDENCE INTERVALS
A More Precise Tool to Assess the Results

45. • Tighter the interval around the observed
result, the more precise the estimate
– Difference = 0%: -30% to 30% vs. -1% to 1%
• If bounds of 95% CI
– Both >0 (for absolute difference) or >1 (for RR) of
new therapy vs. control
• Consistent with new treatment more efficacious
– Difference=20%, 10-20%; RR=2.5, 1.5-3.5
95% CONFIDENCE INTERVALS
A More Precise Tool to Assess the Results

46. • Tighter the interval around the observed
result, the more precise the estimate
– Difference = 0%: -30% to 30% vs. -1% to 1%
• If bounds of 95% CI
– Both >0 (for absolute difference) or >1 (for RR) of
new therapy vs. control
• Consistent with new treatment more efficacious
– Difference=20%, 10-20%; RR=2.5, 1.5-3.5
– Cross 0 (for absolute difference) or 1 (for RR)
• Consistent with new treatment better or worse
– Difference=5%, -5% to 15%; RR=1.2, 0.6 to 2.0
95% CONFIDENCE INTERVALS
A More Precise Tool to Assess the Results

47. Success
(Small Study)
Success
(Large Study)
Treatment 13/26 (50%) 1000/2000 (50%)
Control 10/26 (38%) 973/2000 (48.7%)
p-value 0.40 0.40
Difference 12% 1.3%
95% CI -15% to 38% -1.8% to 4.4%
Interpretation Large effect size;
high uncertainty
Small effect size;
low uncertainty
Connor. AJG 2004;99:1638
95% CONFIDENCE INTERVALS
A More Precise Tool to Assess the Results

48. SUBGROUP ANALYSES
• Does intervention behave differently in
subset of population
– e.g., men vs. women, old vs. young
• Should be pre-defined and justified
– Post hoc more risk of bias since results known
• Less power than overall analysis
– More analyses increases chance of significance
occurring by chance
– Smaller number in each subgroup

49. SUBGROUP ANALYSES
• Don’t assess if treatment effect is significant in
each subgroup
– Don’t compare outcome for new therapy vs. control
in each subgroup
• If baseline assumptions about results for
outcomes in sample size calculation were
correct, wouldn’t expect smaller subgroups to
show significant difference even if treatment
effect exactly the same as in overall group

50. SUBGROUP ANALYSES
• Don’t assess if treatment effect is significant in
each subgroup
– Don’t compare outcome for new therapy vs. control
in each subgroup
• If baseline assumptions about results for
outcomes in sample size calculation were
correct, wouldn’t expect smaller subgroups to
show significant difference even if treatment
effect exactly the same as in overall group
Study of New Therapy vs. Control
• 200 subjects to show 20% difference (50% vs. 30%)
• Overall: 50/100 (50%) vs. 30/100 (30%) p=0.01
• Men: 20/40 (50%) vs. 12/40 (30%) p=0.11
• Women: 30/60 (50%) vs. 18/60 (30%) p=0.04

51. SUBGROUP ANALYSES
Compare Treatment Effects in Subgroups
• Is treatment effect (e.g., RR of death for new
therapy vs. control) different for old vs. young?
– Is there a treatment by subgroup interaction?
– Qualitative interaction
• Treatment effects in opposite direction
– e.g., RR < 1 for old; RR > 1 for young
– Quantitative interaction
• Treatment effects of different magnitude--statistically
heterogeneous (interaction test p < 0.05)
• e.g., old: RR = 0.4, 0.1-1.0; young: RR = 0.9, 0.7-1.2

52. DATA SAFETY MONITORING BOARD
• Independent, external experts
– No involvement, conflicts related to study
• Periodic assessments
– Data quality, timeliness; trial site performance
– Recruitment, accrual and retention
– Safety and efficacy outcomes (risk-benefit)
– Factors external to the study
• New data may impact safety or ethics of study
• Make recommendations to continue, modify, or
terminate study

53. DATA SAFETY MONITORING BOARD
• Independent, external experts
– No involvement, conflicts related to study
• Periodic assessments
– Data quality, timeliness; trial site performance
– Recruitment, accrual and retention
– Safety and efficacy outcomes (risk-benefit)
– Factors external to the study
• New data may impact safety or ethics of study
• Make recommendations to continue, modify, or
terminate study
• “Ensures that a clinical trial is stopped if the
benefit-risk balance for participants or the
expected value to society no longer justifies
continuing” Lewis et al. JAMA 2016;316:2359

54. INTERIM ANALYSIS
Predefined Formal Data Analysis Partway Through Trial
• Efficacy: outcome assumptions used in sample size
determination may be inexact/uncertain
– Modify study (adaptive design)
– Stop study (may have predefined stopping rules)
• Futility: no possibility can document benefit
• Efficacy: unequivocal benefit in clinically important outcome
– Very conservative p-value (e.g., 0.001)
• Prevents incorrect conclusion (vs. p-value closer to 0.05)
• Minimal α spending with multiple comparisons
• Final significant p-value only slightly below 0.05

55. INTERIM ANALYSIS
Predefined Formal Data Analysis Partway Through Trial
• Efficacy: outcome assumptions used in sample size
determination may be inexact/uncertain
– Modify study (adaptive design)
– Stop study (may have predefined stopping rules)
• Futility: no possibility can document benefit
• Efficacy: unequivocal benefit in clinically important outcome
– Very conservative p-value (e.g., 0.001)
• Prevents incorrect conclusion (vs. p-value closer to 0.05)
• Minimal α spending with multiple comparisons
• Final significant p-value only slightly below 0.05
• Safety: Concern/uncertainty about therapy’s safety
– Stop study if unacceptable risk-benefit balance
– Add additional monitoring, therapies, safeguards

56. TRIAL REGISTRATION

57. PURPOSE OF TRIAL REGISTRATION
International Committee of Medical Journal Editors (ICMJE)
• Prevent selective publication and selective
reporting of research outcomes
• Prevent unnecessary duplication of research
• Help public know of planned or ongoing
trials into which they might want to enroll
• Give ethics review boards considering
approval of new studies a view of similar
work and data relevant to the research
http://icmje.org/recommendations/browse/publishing-and-editorial-issues/clinical-trial-registration.html

58. CLINICAL TRIAL DEFINITION
• ClinicalTrials.gov
– Participants receive intervention per protocol
• Drug, device, procedure, diet, brochure, video
– Outcomes measured to determine safety, efficacy
• ICMJE (Medical Journal Editors)
– Prospectively assigns people to an intervention, with or
without concurrent comparison, to study the cause-and-
effect relationship between a health-related intervention
and a health outcome
• NIH
– Human subject(s) prospectively assigned to intervention
to evaluate the effects on health-related biomedical or
behavioral outcomes
https://clinicaltrials.gov/ct2/about-studies/learn; http://icmje.org/recommendations/browse/publishing-and-editorial-issues/clinical-trial-registration.html;
https://oir.nih.gov/sourcebook/intramural-program-oversight/intramural-data-sharing/guide-fdaaa-reporting-research-results/nih-definition-clinical-trial

59. CLINICAL TRIAL DEFINITION
• ClinicalTrials.gov
– Participants receive intervention per protocol
• Drug, device, procedure, diet, brochure, video
– Outcomes measured to determine safety, efficacy
• ICMJE (Medical Journal Editors)
– Prospectively assigns people to an intervention, with or
without concurrent comparison, to study the cause-and-
effect relationship between a health-related intervention
and a health outcome
• NIH
– Human subject(s) prospectively assigned to intervention
to evaluate the effects on health-related biomedical or
behavioral outcomes
https://clinicaltrials.gov/ct2/about-studies/learn; http://icmje.org/recommendations/browse/publishing-and-editorial-issues/clinical-trial-registration.html;
https://oir.nih.gov/sourcebook/intramural-program-oversight/intramural-data-sharing/guide-fdaaa-reporting-research-results/nih-definition-clinical-trial
Clinical Trial
• Prospective
• Assignment of intervention
• Measurement of health outcomes after intervention

60. WHY REGISTER A CLINICAL TRIAL
• Required by law (U.S. FDA)
– Controlled clinical investigations of FDA-regulated
drug, biologic, or device other than Phase 1
(drugs/biologics) or small feasibility studies
• Enable publication (ICMJE)
– All interventional studies, including Phase 1
• Ethical (e.g., WHO, Declaration of Helsinki)
– “The registration of all interventional trials is a
scientific, ethical and moral responsibility” (WHO)
https://clinicaltrials.gov/ct2/manage-recs/background

61. REPORTING TRIALS

62. GUIDELINES FOR REPORTING TRIALS
• Ensures all important elements of study are
included and reported appropriately
• CONSORT guidelines
– Framework for reporting RCTs
– Required by many journals
– Checklist for the content of the title, abstract,
introduction, methods, results, and discussion
– CONSORT flow diagram
CONSORT=Consolidated Standards of Reporting Trials

64. RANDOMIZED CONTROLLED TRIALS
• Best design to minimize bias in assessment
of an intervention
– Factors to provide high methodologic quality
• e.g., concealed allocation, blinding, complete f/u
• Predefined outcomes, sample size, analyses
• Pre-trial registration ensures no change
from original design without explanation
• Reporting guidelines ensure all important
elements provided in publication

65. ASSESSMENT OF RCT

66. BACKGROUND AND HYPOTHESIS
• Background
– Relevance, importance, novelty of topic
– Rationale clear
• Hypothesis
– Primary hypothesis stated

67. BACKGROUND AND HYPOTHESIS
• Background
– Colonoscopy with sedation extremely common
– Guidelines suggest diphenhydramine if difficult to
sedate with standard benzodiazepine/opioid
• No studies assessed this practice
• Hypothesis
– Introduction
• Goal is to determine if diphenhydramine superior to
continued midazolam in difficult-to-sedate patients
– Statistics
• Hypothesis: diphenhydramine is superior in achieving
adequate moderate sedation in difficult-to-sedate patients

68. TRIAL REGISTRATION AND REPORTING
• Trial Registered
– e.g., Clinicaltrials.gov
• Trial reported per guidelines
– CONSORT for RCTs

69. TRIAL REGISTRATION AND REPORTING
• Trial Registered
– Methods
• Registered with ClinicalTrials.gov (NCT01769586)
• Trial reported per guidelines
– CONSORT flow diagram (Figure 1)
– No other mention of CONSORT
• Journal requires CONSORT checklist with submission

70. STUDY DESIGN
• Randomization
– Method of randomization stated
– Allocation concealed
– Block size
– Stratification
• Blinding
– Patients, caregivers, investigators
– Method of blinding stated (e.g., double-dummy)

71. STUDY DESIGN
• Randomization
– Computer generated by uninvolved individual
– Allocation concealed (opaque covering)
– Block size: not stated
– Stratification: Not stated (presume not done)
• Blinding
– Patients, caregivers, investigators blinded
• Person giving drug unblinded (not otherwise involved)
– Better if coded syringes from central location
– Method of blinding: identical syringes

72. STUDY DESIGN
• Population
– Inclusion, exclusion criteria clearly stated
• Broad vs. restrictive
– Consecutive patients enrolled
• Intervention and Control
– Characterized fully
– Clinically appropriate
• Simulate standard practice
• Control is an acceptable standard of care

73. STUDY DESIGN
• Population
– Inclusion, exclusion criteria clear
• Broad in that virtually anyone undergoing colonoscopy
who was difficult to sedate
– Consecutive patients enrolled
• Yes, but only days when 2 investigators available
• Intervention and Control
– Characterized fully: Yes
– Clinically appropriate
• Simulate standard practice and control acceptable
standard of care: Yes

74. STUDY DESIGN
• Primary and additional outcomes defined
– Clinically relevant
– Appropriately measured
• Sample size assumptions, calculation
– Superiority vs. non-inferiority study
– Assumptions reasonable

75. STUDY DESIGN
• Primary and additional outcomes defined
– Adequate sedation is clinically relevant
• Patient and endoscopist assessment most relevant?
– All patients could receive more meds if not adequately sedated
– MOAA/S valid instrument to measure sedation
• ?difference in MOAA/S performance with different drugs
• Sample size assumptions, calculation
– Superiority study
– Outcome assumptions not well justified
• Based on “clinical experience”
• 20% difference reasonable--clinically meaningful

76. ANALYSES
• Population
– ITT vs. per-protocol
– Full accounting of subjects
• Primary and additional analyses
– Predefined analyses presented
• Appropriate statistical comparisons
• Magnitudes and precision of effect
• Subgroup analyses (choice of subgroups justified)
• Other analyses: e.g., sensitivity, multivariable
– Post hoc analyses

77. ANALYSES
• Population
– ITT
– Full accounting of subjects: Yes (no drop-outs)
• Primary and additional analyses
– Predefined analyses presented
• Appropriate statistical comparisons
• Magnitudes and precision of effect
– 95% CIs of difference for all; p-value for primary outcome
• Subgroup analyses (choice of subgroups justified)
– Reasons given; ORs of subgroups compared (interaction test >0.05)
– Multivariable analysis post hoc due to somewhat
unequal distribution of potential confounders

78. CONCLUSIONS
• Do results support conclusions
• Limitations discussed
– Potential sources of bias
– Magnitude and precision of results
– Generalizability
• Results placed in context of current knowledge
and practice
– Consider outcomes not studied
• e.g., cost, availability, ease of use, other risks
– Consider other relevant evidence outside study

79. CONCLUSIONS
• Do results support conclusions: yes
• Limitations discussed
– Potential sources of bias: probably not
– Magnitude and precision of results: Not precision
– Generalizability: Yes
• Results placed in context of current knowledge
and practice
– Consider outcomes not studied
• No (safety, time to d/c, willingness to repeat studied)
– Other relevant evidence outside study
• Prior study; information on the drugs