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BASICS of CLINICAL TRIAL DESIGN MSc in Drug Development, Clinical Pharmacology and Translational Medicine BASICS of CLINICAL TRIAL DESIGN Janet Peacock.

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Presentation on theme: "BASICS of CLINICAL TRIAL DESIGN MSc in Drug Development, Clinical Pharmacology and Translational Medicine BASICS of CLINICAL TRIAL DESIGN Janet Peacock."— Presentation transcript:

1 BASICS of CLINICAL TRIAL DESIGN MSc in Drug Development, Clinical Pharmacology and Translational Medicine BASICS of CLINICAL TRIAL DESIGN Janet Peacock Professor of Medical Statistics Division of Health and Social Care Research

2 Content  Study question  Comparison groups  Randomisation  Blinding and placebos  Primary and secondary outcomes  Analysis populations  Choosing outcomes I gratefully acknowledge use of slides from IRM marked with a **

3 Quiz Find the best answer: 1.Type 1 error is when: b 2.Type 2 error is when: c 3.A non-significant finding in a phase 3 trial means: h 4.If the clinically important difference is increased: g 5.If the outcome is a mean rather than a proportion: g 6.A statistically significant difference in a superiority trial means: i 7.Power of a study is: k 8.Significance level is: e 9.If an equivalence design is used rather than superiority: f 10.If groups of individuals are randomised: f aa significant difference is found in the study sample when there is a real difference in the population ba significant difference is found in the study sample when there is no difference in the population cno significant difference is found in the study sample when there is a real difference in the population dno significant difference is found in the study sample when there is no difference in the population eUsually set at 5% fthe sample size is increased gthe sample size is reduced hthe study cannot prove efficacy ithe new treatment works j1-type 1 error k1-type 2 error

4 Planning a Study Question 1: What is the Study Question?  Phase I: How is the drug/treatment handled by the human body?  Healthy volunteers or unresponsive patients  Phase II: What is the dose response curve?  small group of patients  Phase III: Is the treatment better than placebo/std treatment?  large patient population  Phase IV: What are the long-term effects, are there any drug interactions?  post-marketing, large samples, long follow-up ** I gratefully acknowledge use of this slide from from IRM

5 Planning a Study Question 2: Study Population?  First specify inclusion exclusion criteria: The results can only be generalized to patients who are similar to study participants Patient Characteristics Diagnostic test results (standardized) Disease Duration Disease Severity  Consider prevalence and patient numbers to calculate approximate sample size to achieve  Need to consider compliance and attrition  Multi-center collaborations increase the target population but introduce noise ** I gratefully acknowledge use of this slide from from IRM

6 Comparison groups To discuss:  Why do we need a comparison group for a trial of a new treatment?  How could we use a historical control group? Any problems?

7 Comparison groups  Need concurrent comparison group  Avoids changes over time in:  Other treatments patients receive as these may change over time  Other services & treatment by clinical staff where practice changes and staff change  Behaviours due to secular/cultural influences eg media campaigns or media education etc

8 Allocation to treatment groups To discuss:  Is it okay to let subjects choose between either of 2 new treatments and then compare the groups?  Could this cause any problems?

9 Randomisation  Allocation needs to be unbiased  ie not affected by patient characteristics  Use random allocation by computer program to do this  To ensure similar numbers per group use ‘block randomisation’  Not predictable to recruiting clinicians/researcher else may affect their actions

10 Block randomisation  Used to ensure no. subjects in each group is similar  Random allocation determined in discrete blocks so that within each block there are equal numbers in each group  Example using blocks of size 4, and 2 treatments A and B

11 Stratification  Used when it is important to have balanced random allocation in specific sub-groups defined by specific prognostic factors eg age, sex, severity of disease etc  For example in a trial conducted in several centres it may be important to ensure that the numbers on each treatment are similar within each centre  This is achieved by using a separate randomization list within each centre

12 Minimization  Non-random way of allocating subjects to treatments that maintains balance in several specific prognostic factors  Can be useful in a small trial where random allocation may by chance produce imbalance in key factors (less likely in large trials)  For an example see Altman and Bland BMJ 2005;330:843

13 Blinding & placebos Discussion:  Does it matter if patients know what treatment there are receiving?  When might it matter most & least?  Should clinicians/researchers be blind to treatment? Why?

14 Blinding & placebos Blinding:  Psychological effects in patients and assessors  Randomization makes blinding possible  Single, double-blind  Placebos  single dummy (identical inert treatment)  double dummies (used for blinding when 2 treatments have different modes eg liquid compared to tablet)

15 Primary, secondary outcomes PRIMARY OUTCOME  Used to determine whether treatment is effective  Usually only have one  Usually a measure of efficacy SECONDARY OUTCOMES  Used to look at other effects, positive (efficacy) and negative (safety [adverse events] or side effects)  Usually several

16 Analysis population in RCTs?  Intention to treat  In original randomised groups  Adherers: ‘per protocol’  Receive full protocol  Fully compliant  Treatment received  Regardless of allocation

17 Intention to treat (ITT) in RCTs  Analyse according to original randomised groups even if subjects drop-out/refuse/switch treatments  Preserves comparability between groups: unbiased  Difference can be directly attributed to treatment  Tests offer rather than receipt of treatment  Conservative (bias to null) if non-compliance  Usually the main analysis

18 Per protocol analysis in RCTs  Receive full protocol & fully compliant (omit others)  Reflects what happens in practice  May be biased as groups no longer comparable  patients not included likely to be different  ie difference not necessarily due to treatment  May be useful as a contributory/explanatory analysis but not usually main analysis

19 Treatment received in RCTs  Regardless of allocation  Real world  Likely to be biased  May be relevant with adverse events

20 Choosing outcomes  Suitable  Continuous vs dichotomous, time to event  Sizes of differences thought to be clinically meaningful  Consequences of too small or too big a study  Presenting proportions

21 Dichotomisation of continuous data?  Statisticians may raise objections when researchers turn continuous data into dichotomous data  …because it throws data away .. and so loses power, precision, obscures/changes relationships Subject no. Birthweight (g)LBW (BW<2500g; 0=no, 1=yes)

22 So why do doctors and researchers dichotomise?  Clinical Practice: cut-offs commonly used to define point at which treatment starts eg  anti-hypertensive treatment commonly starts when diastolic blood pressure ≥90mmHg  statins may be given if cholesterol level above say 5.3  Epidemiological/clinical research: cut-offs used to indicate poor outcome eg  low birthweight (<2500g) widely used as indicator of poor outcome of pregnancy at population level  specific cut-off for pain scores used as indication patient has ‘responded’ to pain treatment

23 Some statistical research: motivation RCT in diabetic pregnant women to reduce percentage of babies large-for-gestational age (LGA) Outcome: % LGA babies: currently 15% Reduction to 12% considered clinically relevant Required sample size is 2791 in each group Ie a total of 5582, with  =5%, 1-  =90% Not feasible But...large-for-gestational age is based on dichotomising continuous variable, birthweight-for-gestation (z score)

24 Tail area in Normal distribution For Normal distribution can calculate % above given cut-off given mean and SD Use this principle to base study design on a continuous variable BUT also allows calculation of %

25 What do we mean by shift in means? Difference in means is directly related to a given difference in %s below a cut- off ‘Distributional method’ allows calculation of both differences in means and differences in %s without loss of precision Ref: Peacock et al Statistics in Medicine 2012

26 Is study now feasible? Relative change in LGA (%) % LGA in treated women (vs 15% in untreated) Equivalent change in mean in SDs Total SS for change in means (2xn) Total SS for change in proportions (2xn) 30% 25% 20% 10.50% 11.25% 12.00%  The table above shows the required sample size is much less when considering comparison of means rather than comparison of proportions  The study was then feasible

27 Results…. Can now get difference in means with 95% CI plus difference in proportions with derived 95% CI so meet needs of both stakeholders while maintaining statistical rigour

28 Estimates for proportions data in 2 groups, p1, p2  Difference in proportions: p1-p2  Ratio of proportions: p1/p2  Ratio of odds: p1/(1-p1) p2/(1-p2)  Number needed to treat:1/(p1-p2) Which to use?

29 Choosing the estimate to report for proportions data in 2 groups  Difference in proportions:  when absolute differences are of interest  Ratio of proportions:  When relative differences matter eg if comparing effects for lots of factors  Ratio of odds:  Case-control study – it’s all you can do (plus logistic regression)  Number needed to treat:  RCT and interested in how many patients need to treat to get positive outcome in one  Use as subsidiary to p1-p2 or p1/p2  Don't just report NNT

30 Calculating NNT  Suppose the proportions with successful outcome are:  p1=0.8 (treatment group)  p2=0.6 (placebo group)  p1 – p2 = 0.2  This is proportion of success over and above placebo  So for every one patient treated, 0.2 will be successful  So, need to treat five to get one success (1/0.2)  Hence NNT=1/(p1-p2) = 5 here

31 Sample size and power (1) What happens if a study comparing 2 groups is too small?  Eg.in a small drug trial, difference between new & old drug is not significant – it’s hard to know if: i) new drug really doesn’t work or ii) trial is too small to show a difference

32 Sample size and power (2)  Need to know study question & design before doing calculations (+ draft protocol)  Need idea of what size of effects we expect/hope to find  Want good precision for estimates  Want to minimise chance of drawing wrong conclusion, due to: i) poor precision ii) false positive (type 1 error) iii) false negative (type 2 error)

33 Type 1 error  We conclude there is a difference between the groups (ie get a significant finding) when there is no difference in the underlying population  ie by chance we get an unusual sample  This is defined by the cut-off for significance and is usually set at 0.05 or 5% -- known as the significance level  Note: this means we get a false significant result on average 1/20 times Avoid by careful analysis: i) choice of significance level ii) define questions in advance – no fishing!

34 Type 2 error  We conclude there is no difference when in fact there is a difference in the underlying population  100%-type 2 error is the power of the study and is usually set at ≥80%, preferably ≥90% Avoid by good design: i)Choose right outcome ii) Large enough sample for question iii) ie high power

35 Pragmatics  Sometimes sample size is constrained by time, and/or cost, and/or availability of subjects etc  In this case sample size calculations should still be presented to show that aims of study can still be achieved  If aims can’t be achieved then it may not be good to do study unless data can be pooled with other study data (meta-analysis)

36 What is a clinically important or clinically meaningful difference?  Sample size calculations for comparative studies need estimate of size of difference that would be considered important  ie size of difference that researcher would not want to fail to detect in his/her study  Researcher’s decision not statistician’s one  Can be difficult to decide on:-  consult literature  other studies  colleagues.... if unsure

37 Trial phases and design  Early phase trials:  Looking at tolerance/toxicity and may involve human volunteers or animals (phase 1) & may be uncontrolled  ‘First-in-man’ studies may be uncontrolled or small controlled studies (phase 2) & test feasibility/dose/side effects/safety  Conducted prior to large & conclusive phase 3 trial if drug/treatment is ‘promising’ in early trials  Phase 3:  What we have mostly referred to here ie where treatments are randomly allocated in a way that mirrors how the treatment will be used  Usually tests efficacy  Phase 4:  Post-marketing surveillance - safety

38 Trial designs So far considered 2-group situation where looking at superiority. Other situations are:  Cross-over trials  Two or more treatments are compared in a random order within individuals  Can only be used for chronic conditions such as pain  Sequential trials:  Specifically designed where 2 parallel groups are treated and studied but the trial stops when either a clear benefit emerges or there is no possibility of a difference  Equivalence trials/non-inferiority:  Used when trialing a new drug that is expected to be at least as good as an existing one but has benefits such as fewer side effects or cheaper  Needs specific design and generally needs larger sample than conventional (superiority) designs

39 Design: What is the hypothesis? 1.Superiority: Objective  To determine whether there is evidence of statistical difference in the comparison of interest between 2 treatments: A: treatment of interestB: placebo or active control Null (H 0 ): The mean response is the same for the 2 treatments ie A=B Alternative (H 1 ): The mean response is different for the 2 treatments ie A  B (either A>B or B>A) ** I gratefully acknowledge use of this slide from from IRM

40 2.Equivalence: Objective  To demonstrate that 2 treatments have no clinically meaningful difference Null (H 0 ): The 2 treatments have different mean responses such that: ie either (A-B) ≤ -d or (A-B) ≥ +d implies: A not equivalent to B Alternative (H 1 ): The 2 treatments means are the same such that: ie either –d < (A-B) < +d implies A equivalent to B Design: What is the hypothesis? d = largest difference clinically acceptable ** I gratefully acknowledge use of this slide from from IRM

41 3.Non-Inferiority: Objective  To demonstrate that a given treatment A is not clinically inferior to another, B (maximum allowable clinically meaningful difference=d) Null hypothesis H 0 : A given treatment is inferior with respect to the mean response ie A-B ≤ -d Alternative hypothesis H 1 : A given treatment is non-inferior with respect to the mean response ie A-B > -d Design: What is your Hypothesis ** I gratefully acknowledge use of this slide from from IRM

42 Interim Analysis  Interim analysis: analysis conducted before specified full sample size reached  Purpose: may allow trial to stop early if:- * strong evidence for superiority of either treatment * safety concerns * futility  Timing MUST be specified in protocol  Need to allow for additional testing of treatment difference in sample size calculations (‘spending p’) ** I gratefully acknowledge use of this slide adapted from IRM

43 Predictive Biomarker Validation* *S.J. Mandrekar & D.J. Sargent. Clinical Oncology, 2009 A validated predictive marker can prospectively identify individuals who are likely to have a given clinical outcome. Retrospective Validation ** I gratefully acknowledge use of this slide from from IRM

44 Predictive Biomarker Validation Prospective Validation ① Targeted or Enrichment Design ② Unselected or all-comers Design a)Marker Based Design b)Sequential Testing Strategy Design c)Hybrid Design ** I gratefully acknowledge use of this slide from from IRM

45 Predictive Biomarker Validation ① Targeted or Enrichment Design There is preliminary evidence that only patients who express a marker will benefit from the study treatment. All patients are screened, only biom ✚ patients recruited. Appropriate when therapy has modest benefit on biom− patients, but cause sig. toxicity. Also if treating biom− is ethically impossible ** I gratefully acknowledge use of this slide from from IRM

46 ② Unselected or All-Comers Designs a)Marker-based designs Marker status used as stratification factor, and randomize patients within each marker group. -Only patients with valid marker result randomized -Sample size prospectively specified per marker group Predictive Biomarker Validation ** I gratefully acknowledge use of this slide from from IRM

47 References & further reading  Janet Peacock & Philip Peacock THE OXFORD HANDBOOK OF MEDICAL STATISTICS Oxford University Press 2010 ( chapter 1, p6-23 [clinical trials], [sample size])  Janet Peacock & Sally Kerry PRESENTING MEDICAL STATISTICS FROM PROPOSAL TO PUBLICATION Oxford University Press 2006 (chapter 3, p19-24 for how to do sample size calculations in Stata)


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