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Randomization
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Randomization

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  • 1. Randomization Dr. Bhaswat S. Chakraborty
  • 2. Randomization
  • 3. Why Randomize in Controlled Tials?1. To guard against any use of judgment or systematic arrangements leading to one treatment getting “better condition” to succeed2. To provide a basis for the standard methods of statistical analysis such as significance tests
  • 4. Some Problems With Uncontrolled Trials Uncontrolled trials have to potential to provide a very distorted view of therapy comparison  Especially in the hands on over enthusiastic or unscrupulous investigator  E.g. cancer trials (Laetrile or Interferon therapy) It would be almost impossible to reproduce the results of an uncontrolled trial to any certainty Recommendation from such trials are often enthusiastic but may prove totally unrealistic
  • 5. Problems With Historical Controls  No way of ensuring that the comparison is fair  Treatment and control groups can differ in many features other than the treatment itself  No guarantee that any improvement in patients response is actually due to new treatment  Historical control group less like to have clearly define I/E criteria  Type of the patients in historical control may be different  The quality of recorded for historical control data always inferior (since the patients were not intended to be in the trial)  Criteria of response may be different between the two groups
  • 6. Problems With Historical Controls  Historical data are often of poorer quality so that reporting of prognostic factors may not be consistent  One may have only a sketchy idea of which patient factors are important and some essential factors may go undetected  Prognostic factors can only adjust for patient selection, whereas bias due to changes in experimental environment will remain  The analysis techniques are quite complex and involve certain assumptions, which may not be fulfilled. The methods may be clear to only a skilled data analyst not to may clinicians  To propose that poor design can be corrected for by subtle analysis techniques is not scientific
  • 7. Problems with Concurrent Non- RandomizedControls Systematic Assignment  E.g. Date of Birth, alternate assignment  The main problem with this arrangement would investigators would know advance a patient would receive Judgment Assignment  E.g. Investigator is allow to exercise his judgment to assign a treatment  He may favour one particular treatment to more serious cases to make it look inferior
  • 8. Criteria for Randomization1. Unpredictability  Each participant has the same chance of receiving any of the interventions.  Allocation is carried out using a chance mechanism so that neither the participant nor the investigator will know in advance which will be assigned2. Balance  Treatment groups are of a similar size & constitution, groups are alike in all  important aspects and only differ in the intervention each group receives3. Simplicity  • Easy for investigator/staff to implement
  • 9. Simple Randomization This method is equivalent to tossing a coin for each subject that enters a trial, such as Heads = Active, Tails = Placebo. The random number generator is generally used. It is simple and easy to implement and treatment assignment is completely unpredictable. However, imbalanced randomization can happen in smaller trials, reducing statistical power.  E.g., In trial of 10 participants, treatment effect variance for 5-5 split relative to 7-3 split is (1/5+1/5)/(1/7+1/3)=.84, so 7-3 split is only 84% as efficient as 5-5 split.  Even if treatment is balanced at the end of a trial, it may not be balanced at some time during the trial. For example, the trial may be balanced at end with 100 participants, but the first 10 might be AAAATATATA.
  • 10. Block Randomization Block randomization is balanced within each block The basic idea of block randomization  divide potential patients into m blocks of size 2n  randomize each block such that n patients are allocated to A and n to B  then choose the blocks randomly Example: Two treatments of A, B and Block size of 2 x 2= 4  Possible treatment allocations within each block are (1) AABB, (2) BBAA, (3) ABAB, (4) BABA, (5) ABBA, (6) BAAB  Block size depends on the number of treatments, it should be short enough to prevent imbalance, and long enough to prevent guessing allocation in trials
  • 11. Block Randomization..  The block size is not stated in the protocol – blind the investigator to the block size  In open-label trials, the sequence becomes somewhat predictable (e.g. 2n= 4): B A B ? Must be A. A A ? ? Must be B B. This could lead to selection bias. The solution to avoid selection bias is  Do not reveal blocking mechanism  Use random block sizes If treatment is double blinded, selection bias is not likely  Note if only one block is requested, then it produces a single sequence of random assignment, i.e. simple randomization
  • 12. The Urn Design The urn design is the most widely studied member of the family of adaptive biased-coin designs Such designs are a compromise between designs that yield perfect balance in treatment assignments and complete randomization which eliminates experimental bias The urn design forces a small-sized trial to be balanced but approaches complete randomization as the size of the trial (n) increases. The urn design is not as vulnerable to experimental bias as are other restricted randomization procedures
  • 13. The Urn Design..
  • 14. Stratified Randomization An RCT may not be considered valid if it is not well balanced across prognostic factors  E.g., Age Group: < 40, 41-60, >60; Sex: M, F; Total number of strata = 3 x 2 = 6 Stratification can balance subjects on baseline covariates, tend to produce comparable groups with regard to certain characteristics (e.g., gender, age, race, disease severity)thus produces valid statistical tests The block size should be relative small to maintain balance in small strata. Increased number of stratification variables or increased number of levels within strata leads to fewer patients per stratum. Large clinical trials without IAs don’t use stratification. Unlikely to get imbalance in subject characteristics in a large randomized trial
  • 15. Impact of Treatment Imbalance & SelectionBias First order selection bias – when patients select their own treatments or treatments are assigned based on patient characteristics, such as disease severity  eliminated by randomization, but subconsciously or otherwise, an investigator uses advance knowledge of upcoming treatment allocations as the basis for deciding whom to enroll  e.g., patients more likely to respond may be preferentially enrolled when the active treatment is due to be allocated, and patients less likely to respond may be enrolled when the control group is due Second order selection bias – if upcoming allocations can be observed in their entirety  allocation concealment minimizes the ability to observe upcoming allocations, yet upcoming allocations may still be predicted (imperfectly), or even determined with certainty, if at least some of the previous allocations are known, and if restrictions (such as randomized blocks) were placed on the randomization Third order selection bias– prediction but not observation of upcoming allocations  controlled by perfectly successful masking  the smaller the block sizes, the more accurately one can predict future treatment assignments in the same block as known previous assignments
  • 16. Impact of Treatment Imbalance & SelectionBias.. For most randomization procedures, the treatment imbalance may affect statistical power However, treatment imbalance must be substantial before power is more than trivially affected Expected selection bias associated with a randomization procedure is a function of the predictability of the treatment allocations and is readily evaluated for any sequence of treatment assignments In an unmasked study, the potential for selection bias may be substantial with highly predictable sequences
  • 17. Unequal Randomization When two or more treatments under evaluation have a cost difference  substantial cost savings can be achieved by adopting a smaller randomization ratio such as a ratio of 2:1, with only a modest loss in statistical power Another scenario – when one arm saves lives and the other such as placebo/medical care only does not Generally, randomization ratio of 3:1 will lose considerable statistical power
  • 18. Unequal Randomization and Power 10.8 10.6 0.750.4 0.5 m0.2 0.33 0 0.25 0 20 40 60 80 100 120 140 160 180 200 Sample size m is number of patients experimental over control
  • 19. Double Blind (Masked) Studies Neither the patient nor those responsible for his care and evaluation know which treatment he is receiving
  • 20. Conduct of Double Blind Studies Matched Placebos  Oral placebo which is identical in all respects to the active oral drug except the absence of active ingredient Coding of randomization  The randomization list must be prepared by statistician (preferably)  A pharmacist then makes up identical packages containing active drug or placebo for each patient  Have a simple coding system linking the drug packages to randomization list
  • 21. Conduct of Double Blind Studies .. Breaking the code  Interim analysis may not need breaking the code  DMC decides the future course of the trial based on IA results  Code must be broken correctly Objective evaluation of side effect  In case of SAEs or clear failure of response the investigator may have to be given the broken code for ethical reasons Other types of double blind studies  E.g. Two blinded packages of active drugs  More complex situation where two drugs have different dosing schedules  Package 1 contains Once-daily 200mg + Placebo  Package 2 contains two conventional 100mg tablet
  • 22. When is Blinding Possible Ethics : The double-blind procedure should not result in any harm or undue risk to a patient Practicality : For some treatments it would be totally impossible to arrange a double-blind trial Avoidance of bias: One needs to assess just how serious the bias might be without blinding Compromise: Sometimes partial blinding (e.g. independent blinded evaluators) can be sufficient to reduce bias in treatment comparison
  • 23. Blinding.. Placebos are commonly used as an inactive treatment to achieve double blinding. Active placebos, with which symptoms or side effects are imitated, can also be used. Placebos are justly used when no existing effective treatment is available. If the blinding of the placebo arm is not effective then the protection against expectation effects, biased assessment, contamination, and co- intervention are all lost.  The observed superiority of a new treatment over placebo could merely be a consequence of loss of this control—and an ineffective new treatment would spuriously seem to be superior. It is not sufficient that trials describe themselves as double blind. It is also important that the efficacy of the blinding is actually assessed. In other words, an assessment of the face validity of the double blinding is needed. Success of blinding challenges the notion that placebo controlled trials inherently possess assay sensitivity
  • 24. Blinding
  • 25. Case Study: RCT comparing tamoxifen andanastrozole For gynecomastia and breast pain reduction Development of bicalutamide- related breast changes Optimum dose of tamoxifen 20mg/day  for both prophylaxis and treatment and to assess any impact on prostate cancer control Anastrozole 1mg/day  does not appear to be viable management option for bicalutamide induced gynecosmastia and breast pain Examine the Randomization and Blinding
  • 26. References & Further Reading Stuart J Pocock’s Clinical Trials Statistical properties of randomization in clinical trials. Control Clin Trials. 1988 Properties of simple randomization in clinical trials. Control Clin Trials. 1988 Randomization in clinical trials: conclusions and recommendations. Control Clin Trials. 1988 Properties of permuted-block randomization in clinical trials. Control Clin Trials. 1988 Adaptive biased urn randomization in small strata when blinding is impossible. Biometrics. 1995

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