4. Why Randomize in Controlled Tials?
1. To guard against any use of judgment or
systematic arrangements leading to one
treatment getting “better condition” to
succeed
2. To provide a basis for the standard methods
of statistical analysis such as significance
tests
5. 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
6. 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
7. 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
8. Problems with Concurrent Non- Randomized
Controls
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
9. Criteria for Randomization
1. 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 assigned
2. Balance
Treatment groups are of a similar size & constitution, groups
are alike in all
important aspects and only differ in the intervention each
group receives
3. Simplicity
• Easy for investigator/staff to implement
10. 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.
11. 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
12. 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
13. 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
15. 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
16.
17. Impact of Treatment Imbalance & Selection
Bias
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
18. Impact of Treatment Imbalance & Selection
Bias..
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
19. 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
20.
21. Unequal Randomization and Power
1
0.8
1
0.6
0.75
0.4
0.5 m
0.2 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
22. Double Blind (Masked) Studies
Neither the patient nor those
responsible for his care and
evaluation know which treatment he
is receiving
23. 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
24. 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
25. 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
26. 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
28. Case Study: RCT comparing tamoxifen and
anastrozole
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
29. 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
