The randomized controlled clinical
trial is the standard by which all trials are judged. In the
simplest case, randomization is a process by which each participant
has the same chance of being assigned to either intervention or
control. An example would be the toss of a coin, in which heads
indicates intervention group and tails indicates control group.
Even in the more complex randomization strategies, the element of
chance underlies the allocation process. Of course, neither trial
participant nor investigator should know what the assignment will
be before the participant’s decision to enter the study. Otherwise,
the benefits of randomization can be lost. The role that
randomization plays in clinical trials has been discussed in Chap.
5 as well as by numerous authors
[1–12]. While not all accept that randomization is
essential [10, 11], most agree it is the best method for
achieving comparability between study groups, and the most
appropriate basis for statistical inference [1, 3].
Fundamental Point
Randomization tends to produce study groups
comparable with respect to known as well as unknown risk
factors, removes
investigator bias in the allocation of participants,
and guarantees that statistical
tests will have valid false positive error rates.
Several methods for randomly allocating
participants are used [6,
9, 12–14]. This
chapter will present the most common of these methods and consider
the advantages and disadvantages of each. Unless stated otherwise,
it can be assumed that the randomization strategy will allocate
participants into two groups, an intervention group and a control
group. However, many of the methods described here can easily be
generalized for use with more than two groups.
Two forms of experimental bias are of
concern. The first, selection
bias, occurs if the allocation process is predictable
[5, 15–18]. In this
case, the decision to enter a participant into a trial may be
influenced by the anticipated treatment assignment. If any bias
exists as to what treatment particular types of participants should
receive, then a selection bias might occur. All of the
randomization procedures described avoid selection bias by not
being predictable. A second bias, accidental bias, can arise if the
randomization procedure does not achieve balance on risk factors or
prognostic covariates. Some of the allocation procedures described
are more vulnerable to accidental bias, especially for small
studies. For large studies, however, the chance of accidental bias
is negligible [5].
Whatever randomization process is used,
the report of the trial should contain a brief, but clear
description of that method. In the 1980s, Altman and Doré
[15] reported a survey of four
medical journals where 30% of published randomized trials gave no
evidence that randomization had in fact been used. As many as 10%
of these “randomized” trials in fact used non-random allocation
procedures. Sixty percent did not report the type of randomization
that was used. In one review in the 1990s, only 20–30% of trials
provided fair or adequate descriptions, depending on the size of
the trial or whether the trial was single center or multicenter
[18]. More recently, a review of
253 trials published in five major medical journals after the
release of the Consolidated Standards for Reporting Trials
(CONSORT) [19] recommendations
found little improvement in reports of how randomization was
accomplished [20]. Descriptions
need not be lengthy to inform the reader, publications should
clearly indicate the type of randomization method and how the
randomization was implemented.
Fixed Allocation Randomization
Fixed allocation procedures assign the
interventions to participants with a prespecified probability,
usually equal, and that allocation probability is not altered as
the study progresses. A number of methods exist by which fixed
allocation is achieved [6,
9, 12, 14,
21–25], and we will review three of these—simple,
blocked, and stratified.
Our view is that allocation to
intervention and control groups should be equal unless there are
compelling reasons to do otherwise. Peto [7] among others, has suggested an unequal
allocation ratio, such as 2:1, of intervention to control. The
rationale for such an allocation is that the study may slightly
lose sensitivity but may gain more information about participant
responses to the new intervention, such as toxicity and side
effects. In some instances, less information may be needed about
the control group and, therefore, fewer control participants are
required. If the intervention turns out to be beneficial, more
study participants would benefit than under an equal allocation
scheme. However, new interventions may also turn out to be harmful,
in which case more participants would receive them under the
unequal allocation strategy. Although the loss of sensitivity or
power may be less than 5% for allocation ratios approximately
between 1/2 and 2/3 [8,
21], equal allocation is the most
powerful design and therefore generally recommended. We also
believe that equal allocation is more consistent with the view of
indifference or equipoise toward which of the two groups a
participant is assigned (see Chap. 2). Unequal allocation may indicate
to the participants and to their personal physicians that one
intervention is preferred over the other. In a few circumstances,
the cost of one treatment may be extreme so that an unequal
allocation of 2:1 or 3:1 may help to contain costs while not
causing a serious loss of power. Thus, there are tradeoffs that
must be considered. In general, equal allocation will be presumed
throughout the following discussion unless otherwise
indicated.
Simple Randomization
The most elementary form of
randomization, referred to as simple or complete randomization, is
best illustrated by a few examples [9, 12]. One
simple method is to toss an unbiased coin each time a participant
is eligible to be randomized. For example, if the coin turns up
heads, the participant is assigned to group A; if tails, to group B. Using this procedure, approximately
one half of the participants will be in group A and one half in group B. In practice, for small studies,
instead of tossing a coin to generate a randomization schedule, a
random digit table on which the equally likely digits 0 to 9 are
arranged by rows and columns is usually used to accomplish simple
randomization. By randomly selecting a certain row (column) and
observing the sequence of digits in that row (column) A could be assigned, for example, to
those participants for whom the next digit was even and
B to those for whom the
next digit was odd. This process produces a sequence of assignments
which is random in order, and each participant has an equal chance
of being assigned to A or
B.
For large studies, a more convenient
method for producing a randomization schedule is to use a random
number producing algorithm, available on most computer systems. A
simple randomization procedure might assign participants to group
A with probability
p and participants to group
B with probability
1 − p. One computerized process for simple
randomization is to use a uniform random number algorithm to
produce random numbers in the interval from 0.0 to 1.0. Using a
uniform random number generator, a random number can be produced
for each participant. If the random number is between 0 and
p, the participant would be
assigned to group A;
otherwise to group B. For
equal allocation, the probability cut point, p, is one-half (i.e., p = 0.50). If equal allocation between
A and B is not desired (p ≠ 1/2), then p can be set to the desired proportion
in the algorithm and the study will have, on the average, a
proportion p of the
participants in group A.
This procedure can be adapted easily
to more than two groups. Suppose, for example, the trial has three
groups, A, B and C, and participants are to be
randomized such that a participant has a 1/4 chance of being in
group A, a 1/4 chance of
being in group B, and a 1/2
chance of being in group C.
By dividing the interval 0 to 1 into three pieces of length 1/4,
1/4, and 1/2, random numbers generated will have probabilities of
1/4, 1/4 and 1/2, respectively, of falling into each subinterval.
Specifically, the intervals would be <0.25, 0.25–0.50, and
≥0.50. Then any participant whose random number is less than 0.25
is assigned A, any
participant whose random number falls between 0.25 and 0.50 is
assigned B and the others,
C. For equal allocation,
the interval would be divided into thirds and assignments made
accordingly.
The advantage of this simple
randomization procedure is that it is easy to implement. The major
disadvantage is that, although in the long run the number of
participants in each group will be in the proportion anticipated,
at any point in the randomization, including the end, there could
be a substantial imbalance [23].
This is true particularly if the sample size is small. For example,
if 20 participants are randomized with equal probability to two
treatment groups, the chance of a 12:8 split (i.e., 60%
A, 40% B) or worse is approximately 50%. For
100 participants, the chance of the same ratio (60:40 split) or
worse is only 5%. While such imbalances do not cause the
statistical tests to be invalid, they do reduce ability to detect
true differences between the two groups. In addition, such
imbalances appear awkward and may lead to some loss of credibility
for the trial, especially for the person not oriented to
statistics. For this reason primarily, simple randomization is not
often used, even for large studies. In addition, interim analysis
of accumulating data might be difficult to interpret with major
imbalances in number of participants per arm, especially for
smaller trials.
Some
investigators incorrectly believe that an alternating assignment of
participants to the intervention and the control groups (e.g.,
ABABAB …) is a form of
randomization. However, no random component exists in this type of
allocation except perhaps for the first participant. A major
criticism of this method is that, in a single-blind or unblinded
study, the investigators know the next assignment, which could lead
to a bias in the selection of participants. Even in a double-blind
study, if the blind is broken on one participant as sometimes
happens, the entire sequence of assignments is known. Therefore,
this type of allocation method should be avoided.
Blocked Randomization
Blocked randomization, sometimes
called permuted block randomization, was described by Hill
[4] in 1951. It avoids serious
imbalance in the number of participants assigned to each group, an
imbalance which could occur in the simple randomization procedure.
More importantly, blocked randomization guarantees that at no time
during randomization will the imbalance be large and that at
certain points the number of participants in each group will be
equal [9, 12, 26]. This
protects against temporal trends during enrollment, which is often
a concern for larger trials with long enrollment phases.
If participants are randomly assigned
with equal probability to groups A or B, then for each block of even size
(for example, 4, 6 or 8) one half of the participants will be
assigned to A and the other
half to B. The order in
which the interventions are assigned in each block is randomized,
and this process is repeated for consecutive blocks of participants
until all participants are randomized. For example, the
investigators may want to ensure that after every fourth randomized
participant, the number of participants in each intervention group
is equal. Then a block of size 4 would be used and the process
would randomize the order in which two A’s and two B’s are assigned for every consecutive
group of four participants entering the trial. One may write down
all the ways of arranging the groups and then randomize the order
in which these combinations are selected. In the case of block size
4, there are six possible combinations of group assignments:
AABB, ABAB, BAAB, BABA, BBAA, and ABBA. One of these arrangements is
selected at random and the four participants are assigned
accordingly. This process is repeated as many times as
needed.
Another method of blocked
randomization may also be used. In this method for randomizing the
order of assignments within a block of size b, a random number between 0 and 1 for
each of the b assignments
(half of which are A and
the other half B) is
obtained. The example below illustrates the procedure for a block
of size four (2As and 2Bs). Four random numbers are drawn between 0
and 1 in the order shown.
|
Assignment
|
Random number
|
Rank
|
|---|---|---|
|
A
|
0.069
|
1
|
|
A
|
0.734
|
3
|
|
B
|
0.867
|
4
|
|
B
|
0.312
|
2
|
The assignments
then are ranked according to the size of the random numbers. This
leads to the assignment order of ABAB. This process is repeated for
another set of four participants until all have been
randomized.
The advantage of blocking is that
balance between the number of participants in each group is
guaranteed during the course of randomization. The number in each
group will never differ by more than b/2 when b is the length of the block. This can
be important for at least two reasons. First, if the type of
participant recruited for the study changes during the entry
period, blocking will produce more comparable groups. For example,
an investigator may use different sources of potential participants
sequentially. Participants from these sources may vary in severity
of illness or other crucial respects. One source, with the more
seriously ill participants, may be used early during enrollment and
another source, with healthier participants, late in enrollment
[3]. If the randomization were not
blocked, more of the seriously ill participants might be randomized
to one group. Because the later participants are not as sick, this
early imbalance would not be corrected. A second advantage of
blocking is that if the trial should be terminated before
enrollment is completed, balance will exist in terms of number of
participants randomized to each group.
A potential, but solvable problem with
basic blocked randomization is that if the blocking factor
b is known by the study
staff and the study is not double-blind, the assignment for the
last person entered in each block is known before entry of that
person. For example, if the blocking factor is 4 and the first
three assignments are ABB,
then the next assignment must be A. This could, of course, permit a bias
in the selection of every fourth participant to be entered.
Clearly, there is no reason to make the blocking factor known.
However, in a study that is not double-blind, with a little
ingenuity the staff can soon discover the blocking factor. For this
reason, repeated blocks of size 2 should not be used. On a few
occasions, perhaps as an intellectual challenge, investigators or
their clinic staff have attempted to break the randomization scheme
[27]. This curiosity is natural
but nevertheless can lead to selection bias. To avoid this problem
in the trial that is not double-blind, the blocking factor can be
varied as the recruitment continues. In fact, after each block has
been completed, the size of the next block could be determined in a
random fashion from a few possibilities such as 2, 4, 6, and 8. The
probabilities of selecting a block size can be set at whatever
values one wishes with the constraint that their sum equals 1.0.
For example, the probabilities of selecting block sizes 2, 4, 6,
and 8 can be 1/6, 1/6, 1/3, and 1/3 respectively. Randomly
selecting the block size makes it very difficult to determine where
blocks start and stop and thus determine the next assignment.
A disadvantage of blocked
randomization is that, from a strictly theoretical point of view,
analysis of the data is more complicated than if simple
randomization were used. Unless the data analysis performed at the
end of the study reflects the randomization process actually
performed [26, 28–30] it may
be incorrect since standard analytical methods assume a simple
randomization. In their analysis of the data most investigators
ignore the fact that the randomization was blocked. Matts and
Lachin [26] studied this problem
and concluded that the measurement of variability used in the
statistical analysis is not exactly correct if the blocking is
ignored. Usually the analysis ignoring blocks is conservative,
though it can be anticonservative especially when the blocks are
small (e.g. a block size of two). That is, the analysis ignoring
blocks will have probably slightly less power than the correct
analysis, and understate the “true” significance level. Since
blocking guarantees balance between the two groups and, therefore,
increases the power of a study, blocked randomization with the
appropriate analysis is more powerful than not blocking at all or
blocking and then ignoring it in the analysis [26]. Also, the correct treatment of blocking
would be difficult to extend to more complex analyses. Being able
to use a single, straightforward analytic approach that handles
covariates, subgroups, and other secondary analyses simplifies
interpretation of the trial as a whole. Performing the most correct
analysis is even more problematic for adaptive designs, as
discussed in the next section.
Stratified Randomization
One of the objectives in allocating
participants is to achieve between group comparability of certain
characteristics known as prognostic or risk factors [12, 31–44]. These
are baseline factors which correlate with subsequent participant
response or outcome. Investigators may become concerned when
prognostic factors are not evenly distributed between intervention
and control groups. As indicated previously, randomization tends to
produce groups which are, on the average, similar in their entry
characteristics, known or unknown, or unmeasured. This is a concept
likely to be true for large studies or for many small studies when
averaged. For any single study, especially a small study, there is
no guarantee that all baseline characteristics will be similar in
the two groups. In the multicenter Aspirin Myocardial Infarction
Study [45] which had 4,524
participants, the top 20 cardiovascular prognostic factors for
total mortality identified in the Coronary Drug Project
[43] were compared in the
intervention and control groups and no major differences were found
(Furberg CD, unpublished data). However, individual clinics, with
an average of 150 participants, showed considerable imbalance for
many variables between the groups. Imbalances in prognostic factors
can be dealt with either after the fact by using stratification in
the analysis (Chap. 18) or can be prevented by using
stratification in the randomization. Stratified randomization is a
method which helps achieve comparability between the study groups
for those factors considered.
Stratified randomization requires that
the prognostic factors be measured either before or at the time of
randomization. If a single factor is used, it is divided into two
or more subgroups or strata (e.g., age 30–34 years, 35–39 years,
40–44 years). If several factors are used, a stratum is formed by
selecting one subgroup from each of them. The total number of
strata is the product of the number of subgroups in each factor.
The stratified randomization process involves measuring the level
of the selected factors for a participant, determining to which
stratum she belongs and performing the randomization within that
stratum.
Within each stratum, the randomization
process itself could be simple randomization, but in practice most
clinical trials use some blocked randomization strategy. Under a
simple randomization process, imbalances in the number in each
group within the stratum could easily happen and thus defeat the
purpose of the stratification. Blocked randomization is, as
described previously, a special kind of stratification. However,
this text will restrict use of the term blocked randomization to
stratifying over time, and use stratified randomization to refer to
stratifying on factors other than time. Some confusion may arise
here because early texts on design used the term blocking as this
book uses the term stratifying. However, the definition herein is
consistent with current usage in clinical trials.
As an example of stratified
randomization with a block size of 4, suppose an investigator wants
to stratify on age, sex and smoking history. One possible
classification of the factors would be three 10-year age levels and
three smoking levels.
|
Age (years)
|
Sex
|
Smoking history
|
|---|---|---|
|
1. 40–49
|
Male
|
Current smoker
|
|
2. 50–59
|
Female
|
Ex-smoker
|
|
3. 60–69
|
Never smoked
|
Thus, the design has 3 × 2 × 3 = 18
strata. The randomization for this example appears in
Table 6.1.
Table
6.1
Stratified randomization with block size of
4
|
Strata
|
Age
|
Sex
|
Smoking
|
Group assignment
|
|---|---|---|---|---|
|
1
|
40–49
|
M
|
Current
|
ABBA
BABA…
|
|
2
|
40–49
|
M
|
Ex
|
BABA
BBAA…
|
|
3
|
40–49
|
M
|
Never
|
etc.
|
|
4
|
40–49
|
F
|
Current
|
|
|
5
|
40–49
|
F
|
Ex
|
|
|
6
|
40–49
|
F
|
Never
|
|
|
7
|
50–59
|
M
|
Current
|
|
|
8
|
50–59
|
M
|
Ex
|
|
|
9
|
50–59
|
M
|
Never
|
|
|
10
|
50–59
|
F
|
Current
|
|
|
11
|
50–59
|
F
|
Ex
|
|
|
12
|
50–59
|
F
|
Never
|
|
|
(etc.)
|
Participants who were between 40 and
49 years old, male and current smokers, that is, in stratum 1,
would be assigned to groups A or B in the sequences ABBA BABA .... Similarly, random
sequences would appear in the other strata.
Small studies are the ones most likely
to require stratified randomization, because in large studies, the
magnitude of the numbers increases the chance of comparability of
the groups. In the example shown above, with three levels of the
first factor (age), two levels of the second factor (sex), and
three levels of the third factor (smoking history), 18 strata have
been created. As factors are added and the levels within factors
are refined, the number of strata increase rapidly. If the example
with 18 strata had 100 participants to be randomized, then only
five to six participants would be expected per stratum if the study
population were evenly distributed among the levels. Since the
population is most likely not evenly distributed over the strata,
some strata would actually get fewer than five to six participants.
If the number of strata were increased, the number of participants
in each stratum would be even fewer. Pocock and Simon
[41] showed that increased
stratification in small studies can be self-defeating because of
the sparseness of data within each stratum. Thus, only important
variables should be chosen and the number of strata kept to a
minimum.
In addition to making the two study
groups appear comparable with regard to specified factors, the
power of the study can be increased by taking the stratification
into account in the analysis. Stratified randomization, in a sense,
breaks the trial down into smaller trials. Participants in each of
the “smaller trials” belong to the same stratum. This reduces
variability in group comparisons if the stratification is used in
the analysis. Reduction in variability allows a study of a given
size to detect smaller group differences in response variables or
to detect a specified difference with fewer participants
[22, 26].
Sometimes the variables initially
thought to be most prognostic and, therefore used in the stratified
randomization, turn out to be unimportant. Other factors may be
identified later which, for the particular study, are of more
importance. If randomization is done without stratification, then
analysis can take into account those factors of interest and will
not be complicated by factors thought to be important at the time
of randomization. It has been argued that there usually does not
exist a need to stratify at randomization because stratification at
the time of analysis will achieve nearly the same expected power
[7]. This issue of stratifying pre-
versus post-randomization has been widely discussed [35–38,
42]. It appears for a large study
that stratification after randomization provides nearly equal
efficiency to stratification before randomization [39, 40].
However, for studies of 100 participants or fewer, stratifying the
randomization using two or three prognostic factors may achieve
greater power, although the increase may not be large.
Stratified randomization is not the
complete solution to all potential problems of baseline imbalance.
Another strategy for small studies with many prognostic factors is
considered below in the section on adaptive randomization.
In multicenter trials, centers vary
with respect to the type of participants randomized as well as the
quality and type of care given to participants during follow-up.
Thus, the center may be an important factor related to participant
outcome, and the randomization process should be stratified
accordingly [33]. Each center then
represents, in a sense, a replication of the trial, though the
number of participants within a center is not adequate to answer
the primary question. Nevertheless, results at individual centers
can be compared to see if trends are consistent with overall
results. Another reason for stratification by center is that if a
center should have to leave the study, the balance in prognostic
factors in other centers would not be affected.
One further point might need
consideration. If in the stratified randomization, a specific
proportion or quota is intended for each stratum, the recruitment
of eligible participants might not occur at the same rate. That is,
one stratum might meet the target before the others. If a target
proportion is intended, then plans need to be in place to close
down recruitment for that stratum, allowing the others to be
completed.
Adaptive Randomization Procedures
The randomization procedures described
in the sections on fixed allocation above are non-adaptive
strategies. In contrast, adaptive procedures change the allocation
probabilities as enrollment progresses. Two types of adaptive
procedures will be considered here. First, we will discuss methods
which adjust or adapt the allocation probabilities according to
imbalances in numbers of participants or in baseline
characteristics between the two groups. Second, we will briefly
review adaptive procedures that adjust allocation probabilities
according to the responses of participants to the assigned
intervention.
Baseline Adaptive Randomization Procedures
Two common methods for adaptive
allocation which are designed to make the number of participants in
each study group equal or nearly equal are biased coin
randomization and urn randomization. Both make adaptations based
only on the number of participants in each group, though they can
be modified to perform allocation within strata in the same way as
blocked randomization, and operate by changing the allocation
probability over time.
The
Biased Coin Randomization procedure, originally discussed by
Efron [46], attempts to balance
the number of participants in each treatment group based on the
previous assignments, but does not take participant responses into
consideration. Several variations to this approach have been
discussed [47–63]. The purpose of the algorithm is basically
to randomize the allocation of participants to groups A and B with equal probability as long as the
number of participants in each group is equal or nearly equal. If
an imbalance occurs and the difference in the number of
participants is greater than some prespecified value, the
allocation probability (p)
is adjusted so that it is higher for the group with fewer
participants. The investigator can determine the value of the
allocation probability. The larger the value of p, the faster the imbalance will be
corrected, while the nearer p is to 0.5, the slower the correction.
Efron suggests an allocation probability of p = 2/3 when a correction is indicated.
Since much of the time p is
greater than 1/2, the process has been named the “biased coin”
method. As a simple example, suppose n A and n B represent the number of
participants in groups A
and B respectively. If
n A is less than n B and the difference exceeds a
predetermined value, D,
then we allocate the next participant to group A with probability p = 2/3. If n A is greater than n B by an amount of D, we allocate to group B with probability p = 2/3. Otherwise, p is set at 0.50. This procedure can be
modified to include consideration of the number of consecutive
assignments to the same group and the length of such a run. Some
procedures for which the allocation probability also depend on
differences in baseline characteristics, as discussed below, are
sometimes also called “biased coin” designs.
Another similar adaptive randomization
method is referred to as the Urn Design, based on the work of Wei
and colleagues [64–67]. This method also attempts to keep the
number of participants randomized to each group reasonably balanced
as the trial progresses. The name Urn Design refers to the
conceptual process of randomization. Imagine an urn filled with
m red balls and
m black balls. If a red
ball is drawn at random, assign the participant to group A, return
the red ball, and add one (or more than one) black ball to the urn.
If a black ball is drawn, assign the participant to group B, return
that ball, and add one (or more than one) red ball to the urn. This
process will tend to keep the number of participants in each group
reasonably close because, like the biased coin procedure it adjusts
the allocation probability to be higher for the smaller group. How
much imbalance there might be over time depends on m and how many balls are added after
each draw.
Since the biased coin and urn
procedures are less restrictive than block randomization, they can
be less susceptible to selection bias, but by the same token they
do not control balance as closely. If there are temporal trends in
the recruitment pool during enrollment, imbalances can create
difficulties. This happened in the Stop Atherosclerosis in Native
Diabetics Study (SANDS), a trial comparing intensive intervention
for cholesterol and blood pressure with less intensive intervention
in people with diabetes [68,
69]. Randomization was done using
a stratified urn design, but partway through the trial there was in
imbalance in the intervention groups at the same time new and more
aggressive guidelines regarding lipid lowering treatment in people
who had known coronary heart disease came out. The participants in
SANDS who met those guidelines could no longer be treated with the
less intensive regimen and no new participants with a history of
prior cardiovascular events could be enrolled. Not only was there a
possibility of imbalance between study groups, the sample size
needed to be reconsidered because of the lower average risk level
of the participants.
The most correct analysis of a
randomized trial from a theoretical point of view is based on
permutation distributions modeling the randomization process. For
adaptive procedures this requires that the significance level for
the test statistic be determined by considering all possible
sequences of assignments which could have been made in repeated
experiments using the same allocation rule, assuming no group
differences. How well population models approximate the permutation
distribution for adaptive designs in general is not well understood
[6, 14, 70]. Efron
[46] argues that it is probably
not necessary to take the biased coin randomization into account in
the analysis, especially for larger studies. Mehta and colleagues
[71] compared analyses ignoring
and incorporating biased coin and urn procedures and concluded that
the permutation distribution should not be ignored. Smythe and Wei
[30, 46] and Wei and Lachin [46, 66]
indicate conditions under which test statistics from urn designs
are asymptotically normal, and show that if this randomization
method is used, but ignored in the analyses, the p-value will be slightly conservative,
that is, slightly larger than if the strictly correct analysis were
done. Thus the situation for analysis of biased coin and urn
designs is similar to that for permuted block designs. Ignoring the
randomization is conservative, though not likely to be excessively
conservative. Unlike the permuted block design, however, strong
temporal trends can create problems for adaptive randomization, and
make the permutation-based analysis more important. Although the
biased coin method does not appear to be as widely used, stratified
urn procedures have been used successfully, as in the multicenter
Diabetes Control and Complication Trial [72, 73].
Minimization
In the Enforcing Underage Drinking
Laws (EUDL) randomized community trial, 68 communities in five
states were selected to receive either an intervention or a control
condition. Matched pairs were created using community
characteristics including population size, median family income,
percentage of the population currently in college, and percentages
that were black, Hispanic and spoke Spanish. The specific set of
pairings used was determined by sampling from all possible pairings
and selecting the set of pairs with the smallest Mahalanobis
distance measure. One community in each pair was then randomly
assigned to receive the intervention [74]. In this situation, all the communities to
be randomized and the key prognostic covariates are known in
advance. The treatment and control groups are guaranteed to be
well-balanced, and randomization provides a foundation for later
statistical inference using standard population models. This type
of a priori matching is a common feature of group-randomized trials
[75].
Unfortunately, this is almost never
possible in a clinical setting, where patients typically arrive
sequentially and must be treated immediately. To accommodate the
sequential nature of participant enrollment, some compromise
between manipulation of allocation to achieve balance of prognostic
covariates and a less restrictive treatment allocation must be
made. Stratified block designs can balance a small number of
selected prognostic covariates, and randomization will tend to
balance unselected as well as unmeasured covariates, but such
methods do not perform well when it is important to balance a large
number of prognostic covariates in a small sample. For such
settings, procedures which adapt allocation to achieve balance on
prognostic covariates have been developed.
The biased coin and urn procedures
achieve balance in the number of randomizations to each arm. Other
stratification methods are adaptive in the sense that intervention
assignment probabilities for a participant are a function of the
distribution of baseline covariates for participants already
randomized. This concept was suggested by Efron [46] as an extension of the biased coin method
and also has been discussed in depth by Pocock and Simon
[41], and others [47, 48,
51, 52, 59,
63, 76, 77]. In a
simple example, if age is a prognostic factor and one study group
has more older participants than the other, this allocation scheme
is more likely to randomize the next several older participants to
the group which currently has more younger participants. Various
methods can be used as the measure of imbalance in prognostic
factors. In general, adaptive stratification methods incorporate
several prognostic factors in making an “overall assessment” of the
group balance or lack of balance. Participants are then assigned to
a group in a manner which will tend to correct an existing
imbalance or cause the least imbalance in prognostic factors.
Proschan and colleagues [70]
distinguish between minimization procedures which are deterministic
[59, 68], as ‘strict minimization’, reserving the
term mimimization for the
more general procedure described by Pocock and Simon
[41] [see Appendix].
Generalization of this strategy exists for more than two study
groups. Development of these methods was motivated in part by the
previously described problems with non-adaptive stratified
randomization for small studies. Adaptive methods do not have empty
or near empty strata because randomization does not take place
within a stratum although prognostic factors are used. Minimization
gives unbiased estimates of treatment effect and slightly increased
power relative to stratified randomization [68]. These methods are being used, especially in
clinical trials of cancer where several prognostic factors need to
be balanced, and the sample size is typically 100–200
participants.
The major advantage of this procedure
is that it protects against a severe baseline imbalance for
important prognostic factors. Overall marginal balance is
maintained in the intervention groups with respect to a large
number of prognostic factors. One disadvantage is that minimization
is operationally more difficult to carry out, especially if a large
number of factors are considered. Although White and Freedman
[63] initially developed a
simplified version of the minimization method by using a set of
specially arranged index cards, today any small programmable
computer can easily carry out the calculations. Unlike blocked,
biased coin and urn procedures, however, the calculations for
minimization cannot be done in advance. In addition, the population
recruited needs to be stable over time, just as for other adaptive
methods. For example, if treatment guidelines change during a long
recruitment period, necessitating a change in the inclusion or
exclusion criteria, the adaptive procedure may not be able to
correct imbalances that developed beforehand, as with the SANDS
example cited above.
For minimization, assuming that the
order of participant enrollment is random and applying the
allocation algorithm to all permutations or the order can provide a
null distribution for the test statistic [14, 70].
Considerable programming and computing resources are required to do
this, and biostatisticians prefer to use conventional tests and
critical values to determine significance levels. Unfortunately,
for minimization there are no general theoretical results on how
well the standard analysis approximates the permutation analysis
[6, 14, 70], though
there are some simulation-based results for specific cases
[78].
General advice for stratified block
randomization and minimization is to include the baseline variables
used to determine the allocation as covariates in the analysis
[51, 79]. This seems to produce reliable results in
most actual trials using stratified block randomization, and in
most trials using minimization, though trials using minimization
designs rarely examine the permutation distribution. Proschan et
al. [70] however, report an
example of an actual trial using minimization for which
conventional analysis greatly overstated the significance of the
intervention effect relative when compared to the permutation
distribution. The use of unequal allocation contributed to the
discrepancy in this case, but the Proschan et al. recommend that
the permutation test be used to control type 1 error whenever
allocation is done using minimization. Several regulatory
guidelines make the similar recommendations [80–83].
Despite the appeal of improved balance
on more prognostic covariates, most biostatisticians approach
minimization and other dynamic allocation plans with caution. As
conditions vary considerably from trial to trial, it is expected
that the best choice for method of allocation also varies, with the
primary goal of avoiding a method which is poorly suited for the
given situation.
Response Adaptive Randomization
Response adaptive randomization uses
information on participant response to intervention during the
course of the trial to determine the allocation of the next
participant. Examples of response adaptive randomization models are
the Play the Winner [84] and the
Two-Armed Bandit [85] models.
These models assume that the investigator is randomizing
participants to one of two interventions and that the primary
response variable can be determined quickly relative to the total
length of the study. Bailar [86]
and Simon [87] reviewed the uses
of these allocation methods. Additional modifications or methods
were developed [88–94].
The Play the Winner procedure may assign
the first participant by the toss of a coin. The next participant
is assigned to the same group as the first participant if the
response to the intervention was a success; otherwise, the
participant is assigned to the other group. That is, the process
calls for staying with the winner until a failure occurs and then
switching. The following example illustrates a possible
randomization scheme where S indicates intervention success and F
indicates failure:
|
Assignment
|
Participant
|
||||||||
|---|---|---|---|---|---|---|---|---|---|
|
1
|
2
|
3
|
4
|
5
|
6
|
7
|
8
|
…
|
|
|
Group A
|
S
|
F
|
S
|
F
|
|||||
|
Group B
|
S
|
S
|
F
|
S
|
|||||
Another response
adaptive randomization procedure is the Two Armed Bandit method which
continually updates the probability of success as soon as the
outcome for each participant is known. That information is used to
adjust the probabilities of being assigned to either group in such
a way that a higher proportion of future participants would receive
the currently “better” or more successful intervention.
Both of these response adaptive
randomization methods have the intended purpose of maximizing the
number of participants on the “superior” intervention. They were
developed in response to ethical concerns expressed by some
clinical investigators about the randomization process. Although
these methods do maximize the number of participants on the
“superior” intervention, the possible imbalance will almost
certainly result in some loss of power and require more
participants to be enrolled into the study than would a fixed
allocation with equal assignment probability [92]. A major limitation is that many clinical
trials do not have an immediately occurring response variable. They
also may have several response variables of interest with no single
outcome easily identified as being the one upon which randomization
should be based. Furthermore, these methods assume that the
population from which the participants are drawn is stable over
time. If the nature of the study population should change and this
is not accounted for in the analysis, the reported significance
levels could be biased, perhaps severely [93]. Here, as before, the data analysis should
ideally take into account the randomization process employed. For
response adaptive methods, that analysis will be more complicated
than it would be with simple randomization. Because of these
disadvantages, response adaptive procedures are not commonly
used.
One application of response adaptive
allocation can be found in a trial evaluating extra-corporeal
membrane oxygenator (ECMO) in a neonatal population suffering from
respiratory insufficiency [95–99]. This
device oxygenates the blood to compensate for the inability or
inefficiency of the lungs to achieve this task. In this trial, the
first infant was allocated randomly to control therapy. The result
was a failure. The next infant received ECMO which was successful.
The next ten infants were also allocated to ECMO and all outcomes
were successful. The trial was then stopped. However, the first
infant was much sicker than the ECMO-treated infants. Controversy
ensued and the benefits of ECMO remain unclear. This experience
does not offer encouragement to use this adaptive randomization
methodology.
Mechanics of Randomization
The manner in which the chosen
randomization method is actually implemented is very important
[100]. If this aspect of
randomization does not receive careful attention, the entire
randomization process can easily be compromised, thus voiding any
of the advantages for using it. To accomplish a valid
randomization, it is recommended that an independent central unit
be responsible for developing the randomization process and making
the assignments of participants to the appropriate group
[27, 101]. For a single center trial, this central
unit might be a biostatistician or clinician not involved with the
care of the participants. In the case of a multicenter trial, the
randomization process is usually handled by the data coordinating
center. Ultimately, however, the integrity of the randomization
process will rest with the investigator.
Chalmers and colleagues
[102] reviewed the randomization
process in 102 clinical trials, 57 where the randomization was
unknown to the investigator and 45 where it was known. The authors
reported that in 14% of the 57 studies, at least one baseline
variable was not balanced between the two groups. For the studies
with known randomization schedules, twice as many, or 26.7%, had at
least one prognostic variable maldistributed. For 43 non-randomized
studies, such imbalances occurred four times as often or in 58%.
The authors emphasized that those recruiting and entering
participants into a trial should not be aware of the next
intervention assignment.
In many cases when a fixed proportion
randomization process is used, the randomization schedules are made
before the study begins [103–107]. The
investigators may call a central location, and the person at that
location looks up the assignment for the next participant
[103]. Another possibility, used
historically and still sometimes in trials involving acutely ill
participants, is to have a scheme making available sequenced and
sealed envelopes containing the assignments [106]. As a participant enters the trial, she
receives the next envelope in the sequence, which gives her the
assignment. Envelope systems, however, are more prone to errors and
tampering than the former method [27, 101]. In
one study, personnel in a clinic opened the envelopes and arranged
the assignments to fit their own preferences, accommodating friends
and relatives entering the trial. In another case, an envelope fell
to the bottom of the box containing the envelopes, thus changing
the sequence in which they were opened. Many studies prefer
web-based or telephone systems to protect against this problem. In
an alternative procedure that has been used in several double-blind
drug studies, medication bottles are numbered with a small
perforated tab [105]. The bottles
are distributed to participant in sequence. The tab, which is coded
to identify the contents, is torn off and sent to the central unit.
This system is also subject to abuse unless an independent person
is responsible for dispensing the bottles. Many clinical trials
using a fixed proportion randomization schedule require that the
investigator access a website or call the central location to
verify that a participant is eligible to be in the trial before any
assignment is made. This increases the likelihood that only
eligible participants will be randomized.
For many trials, especially
multicenter and multinational trials, logistics require a central
randomization operations process. Web-based approaches to
randomization and other aspects of trial management predominate now
[108]. In some cases, the clinic
may register a participant by dialing into a central computer and
entering data via touchtone, with a voice response. These systems,
referred to as Interactive Voice Response Systems or IVRS, or
Interactive Web Response Systems, IWRS, are effective and can be
used to not only assign intervention but can also capture basic
eligibility data. Before intervention is assigned, baseline data
can be checked to determine eligibility. This concept has been used
in a pediatric cancer cooperative clinical trial network
[109] and in major multicenter
trials [110, 111].
Whatever system is chosen to
communicate the intervention assignment to the investigator or the
clinic, the intervention assignment should be given as closely as
possible to the moment when both investigator and participant are
ready to begin the intervention. If the randomization takes place
when the participant is first identified and the participant
withdraws or dies before the intervention actually begins, a number
of participants will be randomized before being actively involved
in the study. An example of this occurred in a non-blinded trial of
alprenolol in survivors of an acute myocardial infarction
[112]. In that trial, 393
participants with a suspected myocardial infarction were randomized
into the trial at the time of their admission to the coronary care
unit. The alprenolol or placebo was not initiated until 2 weeks
later. Afterwards, 231 of the randomized participants were excluded
because a myocardial infarction could not be documented, death had
occurred before therapy was begun, or various contraindications to
therapy were noted. Of the 162 participants who remained, 69 were
in the alprenolol group and 93 were in the placebo group. This
imbalance raised concerns over the comparability of the two groups
and possible bias in reasons for participant exclusion. By delaying
the randomization until initiation of therapy, the problem of these
withdrawals could have been avoided.
Problems of implementation can also
affect the integrity of the randomization procedure. Downs and
colleagues [101] relate their
experiences with problems caused by errors in programming,
incomplete and missing data for stratification variables, and other
problems. They also recommend testing of the proposed procedure
before the trial begins, and monitoring of the allocation after it
begins.
Recommendations
For large studies involving more than
several hundred participants, the randomization should be blocked.
If a large multicenter trial is being conducted, randomization
should be stratified by center. Randomization stratified on the
basis of other factors in large studies is usually not necessary,
because randomization tends to make the study groups quite
comparable for all risk factors. The participants can still, of
course, be stratified once the data have been collected and the
study can be analyzed accordingly.
For small studies, the randomization
should also be blocked, and stratified by center if more than one
center is involved. Since the sample size is small, a few strata
for important risk factors may be defined to assure that balance
will be achieved for at least those factors. For a larger number of
prognostic factors, the adaptive stratification techniques should
be considered and the appropriate analyses performed. As in large
studies, stratified analysis can be performed even if stratified
randomization was not done. For many situations, this will be
satisfactory.
Appendix: Adaptive Randomization Algorithm
Adaptive randomization can be used for
more than two intervention groups, but for the sake of simplicity
only two will be used here. In order to describe this procedure in
more detail, a minimum amount of notation needs to be defined.
First, let
x ik = the number of participants
already assigned intervention k
(k = 1, 2) who have the same level of
prognostic factor i
(i = 1, 2, … , f) as the new participant.
and define
The x t ik represents the change in
balance of allocation if the new participant is assigned
intervention t. Finally,
let
B(t) = function of the x t ik ’s, which measures the “lack
of balance” over all prognostic factors if the next participant is
assigned intervention t.
Many possible definitions of
B(t) can be identified. As an
illustrative example, let
where w i = the relative importance of
factor i to the other
factors and the range is the absolute difference between the
largest and smallest values of x t i1 and x t i2 .
The value of B(t) is determined for each intervention
(t = 1 and t = 2). The intervention with the
smaller B(t) is preferred, because allocation of
the participant to that intervention will cause the least
imbalance. The participant is assigned, with probability
p > 1/2, to the
intervention with the smaller score, B(1) or B(2). The participant is assigned, with
probability (1 − p), to the intervention with the larger
score. These probabilities introduce the random component into the
allocation scheme. Note that if p = 1 and, therefore, 1 − p = 0, the allocation procedure is
deterministic (no chance or random aspect) and has been referred to
by the term “minimization” [51,
59].
As a simple example of the adaptive
stratification method, suppose there are two groups and two
prognostic factors to control. The first factor has two levels and
the second factor has three levels. Assume that 50 participants
have already been randomized and the following table summarizes the
results (Table 6.A1).
Table
6.A1
Fifty randomized participants by group and
level of factor (x
ik
’s)a
|
Factor
|
1
|
2
|
Total
|
|||
|---|---|---|---|---|---|---|
|
Level
|
1
|
2
|
1
|
2
|
3
|
|
|
Group
|
||||||
|
1
|
16
|
10
|
13
|
9
|
4
|
26
|
|
2
|
14
|
10
|
12
|
6
|
6
|
24
|
|
30
|
20
|
25
|
15
|
10
|
50
|
|
In addition, the function B(t) as defined above will be used with
the range of the x
ik ’s as the
measure of imbalance, where w 1 = 3 and w 2 = 2; that is, the first factor
is 1.5 times as important as the second as a prognostic factor.
Finally, suppose p = 2/3
and 1 − p = 1/3.
If the next participant to be
randomized has the first level of the first factor and the third
level of the second factor, then this corresponds to the first and
fifth columns in the table. The task is to determine B(1) and B(2) for this participant as shown below.
- 1.
Determine B(1)
- (a)
Factor 1, Level 1Kx 1kx 1 1kRange (x 1 11 , x 1 12 )Group11617
= 321414 - (b)
Factor 2, Level 3Kx 2kx 1 2kRange (x 1 21 , x 1 22 )Group145
= 1266Using the formula given, B(1) is computed as 3 × 3 + 2 × 1 = 11.
- (a)
- 2.
Determine B(2)
- (a)
Factor 1, Level 1Kx 1kx 2 1kRange (x 2 11 , x 2 12 )Group11616
= 121415 - (b)
Factor 2, Level 3Kx 2kx 1 1kRange (x 1 21 , x 1 22 )Group144
= 3267Then B(2) is computed as 3 × 1 + 2 × 3 = 9.
- (a)
- 3.
Now rank B(1) and B(2) from smaller to larger and assign with probability p the group with the smaller B(t).tB(t)Probability of assigning t2B(2) = 9p = 2/31B(1) = 111 − p = 1/3Thus, this participant is randomized to Group 2 with probability 2/3 and to Group 1 with probability 1/3. Note that if minimization were used (p = 1), the assignment would be Group 2.
References
1.
Armitage P. The role of
randomization in clinical trials. Statist Med 1982;1:345–352.CrossRef
2.
Brown BW. Statistical
Controversies in the Design of Clinical-Trials—Some Personal Views.
Control Clin Trials
1980;1:13–27.CrossRef
3.
Byar DP, Simon RM, Friedewald
WT, et al. Randomized Clinical Trials. N Engl J Med
1976;295:74–80.CrossRef
4.
Hill AB. The Clinical Trial.
Brit M Bull
1951;7:278–282.
5.
Lachin JM. Statistical
properties of randomization in clinical trials. Control Clin Trials
1988;9:289–311.CrossRef
6.
Lachin JM, Matts JP, Wei LJ.
Randomization in clinical trials: Conclusions and recommendations.
Control Clin Trials
1988;9:365–374.CrossRef
7.
Peto R. Clinical trial
methodology. Biomedicine
1978;28:24–36.
8.
Peto R, Pike MC, Armitage P,
et al. Design and analysis of randomized clinical trials requiring
prolonged observation of each patient. I. Introduction and design.
British Journal of Cancer
1976;34:585.CrossRef
9.
Pocock SJ. Allocation of
Patients to Treatment in Clinical Trials. Biometrics 1979;35:183–197.CrossRef
10.
Royall RM. Ethics and
statistics in randomized clinical trials. Statistical Science
1991;6:52–62.MathSciNetCrossRefMATH
11.
Weinstein MC. Allocation of
Subjects in Medical Experiments. N
Engl J Med 1974;291:1278–1285.CrossRef
12.
Zelen M. The randomization
and stratification of patients to clinical trials. J Chronic Dis
1974;27:365–375.CrossRef
13.
Bather JA. On the allocation
of treatments in sequential medical trials. International Statistical Review/Revue
Internationale de Statistique 1985;1–13.
14.
Kalish LA, Begg CB.
Treatment allocation methods in clinical trials: a review.
Statist Med
1985;4:129–144.CrossRef
15.
Altman DG, Dore CJ.
Randomisation and baseline comparisons in clinical trials.
Lancet
1990;335:149–153.CrossRef
16.
Stigler SM. The use of
random allocation for the control of selection bias. Biometrika 1969;56:553–560.MathSciNetCrossRefMATH
17.
Wei LJ. On the Random
Allocation Design for the Control of Selection Bias in Sequential
Experiments. Biometrika
1978;65:79–84.MathSciNetCrossRefMATH
18.
Williams DH, Davis CE.
Reporting of assignment methods in clinical trials. Control Clin Trials
1994;15:294–298.CrossRef
19.
Moher D, Schulz KF, Altman
DG. The CONSORT statement: revised recommendations for improving
the quality of reports of parallel-group randomised trials.
The Lancet
2001;357:1191–1194.CrossRef
20.
Mills EJ, Wu P, Gagnier J,
Devereaux PJ. The quality of randomized trial reporting in leading
medical journals since the revised CONSORT statement. Contemp Clin Trials
2005;26:480–487.CrossRef
21.
Brittain E, Schlesselman JJ.
Optimal Allocation for the Comparison of Proportions. Biometrics
1982;38:1003–1009.CrossRef
22.
23.
Lachin JM. Properties of
simple randomization in clinical trials. Control Clin Trials
1988;9:312-326.CrossRef
24.
Louis TA. Optimal allocation
in sequential tests comparing the means of two Gaussian
populations. Biometrika
1975;62:359–369.MathSciNetCrossRefMATH
25.
Louis TA. Sequential
Allocation in Clinical Trials Comparing Two Exponential Survival
Curves. Biometrics
1977;33:627–634.MathSciNetCrossRef
26.
Matts JP, Lachin JM.
Properties of permuted-block randomization in clinical trials.
Control Clin Trials
1988;9:327–344.CrossRef
27.
Schulz KF, Grimes DA.
Allocation concealment in randomised trials: defending against
deciphering. The Lancet
2002;359:614–618.CrossRef
28.
Kalish LA, Begg CB. The
impact of treatment allocation procedures on nominal significance
levels and bias. Control Clin
Trials 1987;8:121–135.CrossRef
29.
Matts JP, McHugh RB.
Analysis of accrual randomized clinical trials with balanced groups
in strata. J Chronic Dis
1978;31:725–740.CrossRef
30.
Smythe RT, Wei LJ.
Significance tests with Restricted Randomization Design.
Biometrika
1983;70:496-500.MathSciNetCrossRefMATH
31.
Ducimetiere P.
Stratification; in Boissel JP, Klimt CR (eds): Multi-Center
Controlled Trials, Principles and Problems. Paris, Institut
National de la Sante et de la Recherche Medicale, 1979.
32.
Feinstein AR, Landis JR. The
role of prognostic stratification in preventing the bias permitted
by random allocation of treatment. J Chronic Dis
1976;29:277–284.CrossRef
33.
Fleiss JL. Multicentre
clinical trials: Bradford Hill’s contributions and some subsequent
developments. Statist Med
1982;1:353–359.CrossRef
34.
Green SB, Byar DP. The
effect of stratified randomization on size and power of statistical
tests in clinical trials. J
Chronic Dis 1978;31:445–454.CrossRef
35.
Grizzle JE. A note on
stratifying versus complete random assignment in clinical trials.
Control Clin Trials
1982;3:365–368.CrossRef
36.
Mantel N, McHugh R, Matts J.
Pre-Stratification or Post-Stratification. Biometrics 1984;40:256–258.
37.
McHugh R, Matts J.
Post-Stratification in the Randomized Clinical Trial. Biometrics 1983;39:217–225.MathSciNetCrossRefMATH
38.
Meier P. Stratification in
the design of a clinical trial. Control Clin Trials
1981;1:355–361.CrossRef
39.
Palta M, Amini SB.
Consideration of covariates and stratification in sample size
determination for survival time studies. J Chronic Dis
1985;38:801–809.CrossRef
40.
Palta M, Amini SB. Magnitude
and likelihood of loss resulting from non-stratified randomization.
Statist Med
1982;1:267–275.CrossRef
41.
Pocock SJ, Simon R.
Sequential Treatment Assignment with Balancing for Prognostic
Factors in the Controlled Clinical Trial. Biometrics 1975;31:103–115.CrossRef
42.
Simon R. Restricted
Randomization Designs in Clinical Trials. Biometrics 1979;35:503–512.MathSciNetCrossRef
43.
The Coronary Drug Project
Research Group: Factors influencing long-term prognosis after
recovery from myocardial infarctionΓÇöThree-year findings of the
Coronary Drug Project. J Chronic
Dis 1974;27:267–285.CrossRef
44.
Zelen M. Aspects of the
planning and analysis of clinical trials in cancer. A Survey of
Statistical Design and Linear Models Amsterdam: North-Holland
1975.
45.
Aspirin Myocardial
Infarction Study Research Group: A randomized, controlled trial of
aspirin in persons recovered from myocardial infarction.
JAMA
1980;243:661–669.CrossRef
46.
Efron B. Forcing a
Sequential Experiment to be Balanced. Biometrika 1971;58:403–417.MathSciNetCrossRefMATH
47.
Atkinson AC. Optimum biased
coin designs for sequential clinical trials with prognostic
factors. Biometrika
1982;69:61–67.MathSciNetCrossRefMATH
48.
49.
Begg CB. On Inferences from
Wei’s Biased Coin Design for Clinical Trials. Biometrika 1990;77:467–478.MathSciNetCrossRefMATH
50.
Efron B. Randomizing and
balancing a complicated sequential experiment. Biostatistics
Casebook 1980;19–30.
51.
Forsythe AB, Stitt FW.
Randomization or minimization in the treatment assignment of
patient trials: validity and power of tests. Health Sciences
Computing Facility, University of California, 1977.
52.
53.
Halpern J, Brown BW.
Sequential treatment allocation procedures in clinical trials-with
particular attention to the analysis of results for the biased coin
design. Statist Med
1986;5:211–229.CrossRef
54.
Hannigan JF, Brown BW.
Adaptive Randomization Biased Coin-Design: Experience in a
Cooperative Group Clinical Trial. 74. 1982. Department of
Statistics, Stanford University.
55.
Klotz JH. Maximum Entropy
Constrained Balance Randomization for Clinical Trials. Biometrics 1978;34:283–287.CrossRef
56.
Raghavarao D. Use of
distance function in sequential treatment assignment for prognostic
factors in the controlled clinical trial. Calcutta Statist Assoc Bull
1980;29:99–102.CrossRef
57.
Smith RL. Sequential
Treatment Allocation Using Biased Coin Designs. J R Stat Soc Series B Stat Methodol
1984;46:519–543.MathSciNetMATH
58.
Soares JF, Jeff Wu CF. Some
restricted randomization rules in sequential designs. Commun StatTheory Methods
1983;12:2017–2034.MathSciNetCrossRefMATH
59.
Taves DR. Minimization: a
new method of assigning patients to treatment and control groups.
Clinical pharmacology and
therapeutics 1974;15:443.CrossRef
60.
Wei LJ. A class of treatment
assignment rules for sequential experiments. Commun Stat Theory Methods
1978;7:285–295.MathSciNetCrossRefMATH
61.
Wei LJ. The Adaptive Biased
Coin Design for Sequential Experiments. Ann Stat 978;6:92–100.
62.
Wei LJ. A class of designs
for sequential clinical trials. J
Am Stat Assoc 1977;72:382–386.CrossRef
63.
White SJ, Freedman LS.
Allocation of patients to treatment groups in a controlled clinical
study. Br J Cancer 1978;37:849.CrossRef
64.
Wei LJ. An application of an
urn model to the design of sequential controlled clinical trials.
J Am Stat Assoc
1978;73:559–563.MathSciNetCrossRefMATH
65.
Wei LJ, Smythe RT, Smith RL.
K-treatment comparisons with restricted randomization rules in
clinical trials. Ann Stat
1986;265–274.
66.
Wei LJ, Lachin JM.
Properties of the urn randomization in clinical trials.
Control Clin Trials
1988;9:345–364.CrossRef
67.
Wei LJ, Smythe RT, Lin DY,
Park TS. Statistical inference with data-dependent treatment
allocation rules. J Am Stat
Assoc 1990;85:156–162.MathSciNetCrossRef
68.
Birkett NJ. Adaptive
allocation in randomized controlled trials. Control Clin Trials
1985;6:146–155.CrossRef
69.
Russell M, Fleg JL, Galloway
W, et al. Examination of lower targets for low-density lipoprotein
cholesterol and blood pressure in diabetes—the Stop Atherosclerosis
in Native Diabetics Study (SANDS). American Heart Journal
2006;152:867–875.CrossRef
70.
Proschan MA, Brittain E,
Kammerman L. Minimize the Use of Minimization with Unequal
Allocation. Biometrics
2011;67:1135–1141.MathSciNetCrossRefMATH
71.
72.
The DCCT Research Group: The
Diabetes Control and Complications Trial (DCCT): Design and
Methodologic Considerations for the Feasibility Phase. Diabetes 1986;35:530–545.
73.
The DCCT Research Group:
Diabetes Control and Complications Trial (DCCT): Results of
Feasibility Study. The DCCT Research Group. Diabetes Care 1987;10:1–19.
74.
Reboussin BA, Preisser JS,
Song EY, Wolfson M. Sample size estimation for alternating logistic
regressions analysis of multilevel randomized community trials of
under-age drinking. R Stat Soc Ser
A Stat Soc 2012;175:691–712.MathSciNetCrossRef
75.
Murray DM. Design and
Analysis of Group-randomized Trials. Oxford University Press,
1998.
76.
Gail MH, Wieand S,
Piantadosi S. Biased Estimates of Treatment Effect in Randomized
Experiments with Nonlinear Regressions and Omitted Covariates.
Biometrika
1984;71:431–444.MathSciNetCrossRefMATH
77.
Begg CB, Kalish LA.
Treatment Allocation for Nonlinear Models in Clinical Trials: The
Logistic Model. Biometrics
1984;40:409–420.CrossRef
78.
Aickin M. A Simulation Study
of the Validity and Efficiency of Design-Adaptive Allocation to Two
Groups in the Regression Situation. Int J Biostat 2009;5:Article 19.
79.
Kahan BC, Morris TP.
Improper analysis of trials randomised using stratified blocks or
minimisation. Statist Med
2012;31:328–340.MathSciNetCrossRef
80.
Committee for Proprietary
Medicinal Products (CPMP: Committee for Proprietary Medicinal
Products (CPMP): points to consider on adjustment for baseline
covariates. Statist Med
2004;23:701.
81.
FDA: International
Conference on Harmonization—Efficacy: Statistical principles for
clinical trials. U S Food and Drug Administration.
82.
Food and Drug
Administration: Guidance for industry: Adaptive design clinical
trials for drugs and biologics. Washington DC, USA: Food and Drug
Administration 2010.
83.
Green H, McEntegart DJ,
Byrom B, et al. Minimization in crossover trials with
non-prognostic strata: theory and practical application.
J Clin Pharm Ther
2001;26:121–128.CrossRef
84.
Zelen M. Play the Winner
Rule and the Controlled Clinical Trial. J Am Stat Assoc
1969;64:131–146.MathSciNetCrossRef
85.
Robbins H. Some aspects of
the sequential design of experiments. Bulletin of the American Mathematical
Society 1952;58:527–535.MathSciNetCrossRefMATH
86.
Bailar JC. Patient
assignment algorithms: an overview; in Proceedings of the 9th
International Biometric Conference, Boston, August 22-27, 1976:
Invited Papers: Biometric Society, 1976, pp 189–206.
87.
Simon R. Adaptive Treatment
Assignment Methods and Clinical Trials. Biometrics 1977;33:743–749.CrossRef
88.
Armitage P. The search for
optimality in clinical trials. International Statistical Review/Revue
Internationale de Statistique 1985;15–24.
89.
Bather JA. Randomized
Allocation of Treatments in Sequential Experiments. J R Stat Soc Series B Stat Methodol
1981;43:265–292.MathSciNetMATH
90.
91.
Nordbrock E. An Improved
Play-the-Winner Sampling Procedure for Selecting the Better of Two
Binomial Populations. J Am Stat
Assoc 1976;71:137–139.MathSciNetCrossRefMATH
92.
Simon R, Weiss GH, Hoel DG.
Sequential Analysis of Binomial Clinical Trials. Biometrika 1975;62:195–200.MathSciNetCrossRefMATH
93.
94.
Wei LJ. Exact two-sample
permutation tests based on the randomized play-the-winner rule.
Biometrika
1988;75:603–606.MathSciNetCrossRefMATH
95.
Bartlett RH, Roloff DW,
Cornell RG, et al. Extracorporeal Circulation in Neonatal
Respiratory Failure: A Prospective Randomized Study. Pediatrics 1985;76:479–487.
96.
O’Rourke PP, Crone RK,
Vacanti JP, et al. Extracorporeal Membrane Oxygenation and
Conventional Medical Therapy in Neonates With Persistent Pulmonary
Hypertension of the Newborn: A Prospective Randomized Study.
Pediatrics
1989;84:957–963.
97.
Paneth N, Wallenstein S.
Extracorporeal Membrane Oxygenation and the Play the Winner Rule.
Pediatrics
1985;76:622–623.
98.
Ware JH, Epstein MF.
Extracorporeal Circulation in Neonatal Respiratory Failure: A
Prospective Randomized Study. Pediatrics 1985;76:849–851.
99.
Ware JH. Investigating
Therapies of Potentially Great Benefit: ECMO. Stat Sci 1989;4:298–306.MathSciNetCrossRefMATH
100.
Pocock SJ, Lagakos SW.
Practical experience of randomization in cancer trials: an
international survey. Br J
Cancer 1982;46:368–375.CrossRef
101.
Downs M, Tucker K,
Christ-Schmidt H, Wittes J. Some practical problems in implementing
randomization. Clin Trials
2010;7:235–245.CrossRef
102.
Chalmers TC, Celano P,
Sacks HS, Smith H. Bias in Treatment Assignment in Controlled
Clinical Trials. N Engl J
Med 1983;309:1358–1361.CrossRef
103.
Beta-Blocker Heart Attack
Trial Research Group. A randomized trial of propranolol in patients
with acute myocardial infarction: I. mortality results.
JAMA
1982;247:1707–1714.
104.
CASS Principle
Investigators and Their Associates. Coronary artery surgery study
(CASS): a randomized trial of coronary artery bypass surgery.
Survival data. Circulation
1983;68:939–950.CrossRef
105.
Collaborative Group on
Antenatal Steroid Therapy. Effect of antenatal dexamethasone
administration on the prevention of respiratory distress syndrome.
Am J Obstet Gynecol
1981;141:276–287.
106.
Hypertension Detection and
Follow-up Program Cooperative Group: Five-year findings of the
hypertension detection and follow-up program: I. reduction in
mortality of persons with high blood pressure, including mild
hypertension. JAMA
1979;242:2562–2571.
107.
Multiple Risk Factor
Intervention Trial Research Group. Multiple risk factor
intervention trial: Risk factor changes and mortality results.
JAMA
1982;248:1465–1477.CrossRef
108.
Reboussin D, Espeland MA.
The science of web-based clinical trial management. Clin Trials 2005;2:1–2.CrossRef
109.
Krischer JP, Hurley C,
Pillalamarri M, et al. An automated patient registration and
treatment randomization system for multicenter clinical trials.
Control Clin Trials
1991;12:367–377.CrossRef
110.
Kjekshus J, Apetrei E,
Barrios V, et al. Rosuvastatin in Older Patients with Systolic
Heart Failure. N Engl J Med
2007;357:2248–2261.CrossRef
111.
SPORTIF Executive Steering
Committee for the SPORTIF: Ximelagatran vs warfarin for stroke
prevention in patients with nonvalvular atrial fibrillation: A
randomized trial. JAMA
2005;293:690–698.CrossRef
112.
Ahlmark G, Saetre H.
Long-term treatment with ß-blockers after myocardial infarction.
Eur J Clin Pharmacol
1976;10:77–83.CrossRef