Download The role of randomization in clinical trials

STATISTICS I N MEDICINE, VOL. 1, 345-352 (1982)
THE ROLE OF RANDOMIZATION
IN CLINICAL TRIALS
PETER ARMITAGE
Dt.partment of Bromaihemarics, Pusry S l r t w , Uniwrsilj of Oxford, Oxford OX1 2 J 2 , England
SUMMARY
Random assignment of treatments is an essential feature of experimental design in general and clinical trials
in particular. It provides broad comparability of treatment groups and validates the use of statistical methods
for the analysis of results. Various devices are available for improving the balance of prognostic factors across
treatment groups. Several recent initiatives to diminish the role of randomization are seen as being potentially
misleading. Randomization is entirely compatible with medical ethics in circumstances when the treatment of
choice is not clearly identified.
K E Y WORDS
Austin Bradford Hill Data-dependent allocation Historical controls
Permuted blocks Prognostic variables Randomization
Medical ethics
1. INTRODUCTION
Clinical trials come in all shapes and sizes, but if they have one single necessary attribute, a sine qua
non, it is surely the element of randomization which enters into the assignment of treatment to
individual patients.
Randomization, as a basic principle of experimental design, was developed by R. A. Fisher in
the 1920s, although Stigler’ has noted the important contribution made by the philosopher C . S.
Peirce in the design of experiments in psychology, The successful implementation of randomized
trials in medicine, in the 1940s, is largely due to the advocacy and example of Sir Austin Bradford
Hill. Many of Hill’s expository papers, together with reports of the early trials which he and others
conducted for the (British) Medical Research Council, are to be found in Reference 3 (see also
p. 369 of this issue).
Of course, the realization that the evaluation of therapeutic and prophylactic measures requires
carefully controlled studies has a much longer h i ~ t o r y There
.~
are a number of fascinating
forerunners of randomization, in which investigators have sought to impose a deliberate, rather
than a haphazard, system of treatment allocation. The idea of assigning two treatments to
alternate patients has an obvious appeal. It was used by Fibiger5 in a trial of therapeutic serum
against diphtheria. It was advocated also by Pearson6 for the assessment of typhoid immunization. This example is particularly interesting, in view of Karl Pearson’s apparent lack of interest
in experimental design later in his career. Pearson had been asked to interpret non-experimental
data on results of various forms of immunization used in the British Army. Not surprisingly, he
found this a difficult task, and wrote:
If further experimental inoculations were made . . . . the greatest care ought to be taken
to get homogeneous material, that is, men of like caution, subjected to the same
0277-67 15/82/04034548$01 .OO
0 1982 by John Wiley & Sons, Ltd.
Received 25 April 1982
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PETER ARMITAGE
environment. Assuming that the inoculation is not more than a temporary inconvenience, it would seem to be possible to call for volunteers, but while keeping a register
of all men who volunteered, only to inoculate every second volunteer. In this way any
spurious effect really resulting from a correlation between immunity and caution would
be got rid of.
Another tantalizing approach was to form two or more ‘comparable’ groups of patients and
then to allocate each group to one treatment by a random act such as the toss of a coin. van
Helmont’, a medicinal chemist, in a challenge to the Schoolmen who advocated a purely
theoretical rather than an empirical approach to therapeutics, wrote:
Let us take out of the hospitals, out of the Camps, or from elsewhere, 200, or 500 poor
People, that have Fevers, Pleurisies, &c. Let us divide them into halfes, let us cast lots,
that one half of them may fall to my share, and the others to yours; . . . we shall see how
many funerals both of us shall have: But let the reward of the contention or wager, be 300
florens, deposited on both sides.
Amberson, McMahan and Pinner8 followed this procedure in a trial of sodium gold
thiosulphate in the treatment of pulmonary tuberculosis. Twenty-four patients were divided into
two groups of twelve, members of the two groups being ‘individually matched’. The active
treatment and a placebo were assigned to the two groups ‘by the flip of a coin’.
The procedure advocated by van Helmont and adopted by Amberson et al. suffers from two
related defects. First, there is no guarantee that the two groups, however carefully matched, d o not
differ substantially in some important characteristics which were ignored in the matching.
Secondly, there is no way of measuring the relevant random error, since we cannot tell by how
much the responses in the two groups might have differed if the treatments had been identical. In
modern jargon, there is inadequate ‘replication’. These problems would have been avoided if the
design had permitted several independent acts of random allocation rather than a single one.
2. THE BENEFITS OF RANDOMIZATION
The precise way in which random assignment is carried out will depend on the broad design of the
trial. In many trials, treatments are compared ‘between subjects’, with each subject receiving one
of the rival treatments, the assignment being made by an independent random choice for each
subject. In crossover trials, each patient receives two or more treatments on different occasions, the
order of administration being assigned at random for each subject. Other variants are discussed in
Section 3. All these schemes lead to the following desirable consequences, none of which are likely
to be fulfilled without randomization:
(i) The treatments are compared under broadly similar circumstances. In a between-subject
trial, for example, the patients allotted to each treatment group will have similar distributions of
prognostic factors. Of course, for any given baseline variable the distributions in different
treatment groups will not be exactly the same, unless some deliberate act of balancing has been
performed. Moreover, if a large number of baseline variables are studied, one or more may exhibit
a marked lack of balance, purely by chance. But it is unlikely that the baseline variable that best
predicts therapeutic response will be seriously unbalanced, and unlikely that the distributions of
response will vary widely from group to group unless they are really affected by choice of
treatment.
(ii) Random assignment permits the use of probability theory to express the extent to which any
difference in response between treatment groups is likely to be due to chance. The italicized word
RANDOMIZATION IN CLINICAL TRIALS
347
‘unlikely’ in the last paragraph can therefore be given a strictly quantitative interpretation. The
probability theory underlying many of the most familiar statistical methods, such as t tests,
requires certain assumptions (such as normality of distributions of responses). But these are not
essential. The mere act of randomization is enough to support the use ofdistribution-free methods,
which in practice are likely to give much the same results as those requiring distributional
assumptions.
(iii) Random assignment permits, although it does not ensure, the various devices for masking
the identity of treatments, including the possible use of a placebo, which are often essential for an
unbiased assessment of efficacy. It is difficult to see how these important procedures could be
introduced if treatments were to be assigned in a deterministic, non-random fashion. It is essential
that assignment should be made after entry of a patient into the trial, so that the decision whether
or not to enter a patient is uninfluenced by a knowledge of the treatment to be used. It follows that
assignments to be made in the future should not be made known until they are needed; open lists,
for example, should be avoided. One well-used approach is to keep each assignment in a sealed
envelope bearing the serial number of the patient on the outside. In many multicentre trials the
assignment is made by telephone from the co-ordinating centre. In some drug trials the
medicaments needed for each patient are prepared in advance by a pharmacist, so that each pack
carries merely the patient’s serial number.
Points (i) and (ii) are closely related, and are in no way peculiar to clinical experimentation. In
his first extended treatment of experimental design, Fisher9 emphasized the role of randomization
in providing a proper estimate of random error, and the consequent validity of the significance
tests to be applied--essentially point (ii) above. Hill tended to emphasize (i). He also’O stressed the
objectivity of randomization:
. . . having used a random allocation, the sternest critic is unable to say when we
eventually dash into print that quite probably the groups were differentially biased
through our predilections or through our stupidity.
3. OTHER DEVICES
The simple randomization schemes envisaged above can be performed by the construction of an
allocation list before the start of the trial, using random sampling numbers. In many trials, variants
of these simple methods are introduced.
3.1 Permuted blocks
Although simple randomization is likely to provide satisfactory balance between treatment groups
in the distribution of important prognostic factors, imbalances will occur from time to time, and
the investigator may wish to reduce the play of chance by ensuring a high degree of similarity
between the groups. The device known now as ‘permuted blocks’ was, I believe, first described by
Hill. Within each of a number of ‘strata’, or subgroups defined by prognostic variables, the
allocation is such that the numbers allotted to different treatments are equalized within each
‘block’ of a certain size. For exampIe, within two treatments, it might be arranged that each block
of eight patients in any one stratum contains four allocations to one treatment and four to the
other, the particular permutation being entirely random.
This device mimics the use of randomized blocks in agricultural experimentation, the
agricultural ‘blocks’ being analogous to the clinical strata, rather than to the blocks which are
permuted. There is the difference that in agriculture the blocks are of fixed size, whereas in clinical
trials the strata are initially of unknown size: the balancing therefore has to be done in a sequential
manner.
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PETER ARMITAGE
Three points should be noted:
(i) It is pointless to have separate lists for different strata unless these are balanced by permuted
blocks or some equivalent device.
(ii) If permuted-block allocation is used, the comparison between treatments will be ‘within
strata’ and therefore more precise than would otherwise be the case. The statistical analysis should
take this increased precision into account.
(iii) Even if permuted blocks are not used, the extra precision referred to in (ii) can be largely
achieved by the sort of analysis mentioned in (ii)-allowing for the effects of the relevant
prognostic variables. It is, in fact, a matter of some debate whether stratification by design, using
permuted blocks, has any appreciable advantage over stratification in the analysis without use of
permuted blocks. The near-equality of numbers achieved by permuted blocks is certainly
advantageous, but the advantage is likely to be marginal except in quite small trials, and may be
outweighed by the nuisance of keeping separate randomization lists and the consequently
increased risk of errors of assignment. In multicentre trials, one natural system of strata is that of
the centres themselves, and there may be a special case for using permuted blocks within each
centre so that no centre ends the trial with highly disproportionate numbers on different
treatments: a diplomatic rather than a statistical reason.
3.2 Data-dependent allocation
In recent years a number of proposals have been made for the use of dynamic systems of
allocation, in which the assignment to be made for any one patient depends in some way on the
previous course of events. A distinction should be made between (i) schemes aiming to provide a
better balance of prognostic factors, and (ii) those designed to ensure that more patients are
assigned to the more effective treatments.
(i) Balance of prognostic factors
This is, of course, the aim of permuted blocks, but this method can be criticized for being
insufficiently random. If the block size is constant and known, the last assignment in a block must
be determined by the earlier assignments, and in many blocks the determinacy will extend to earlier
assignments. Efron’ introduced an additional random element by allowing the probabilities of
allocation to fluctuate adaptively, so that an under-represented treatment had a higher chance of
being chosen at any stage. There are many variants of these so-called ‘biased-coin’ schemes, but
they seem to have little advantage over permuted blocks if treatments are adequately masked.
When there are many prognostic variables to be balanced, permuted blocks and biased-coin
methods are inconvenient because they require different randomization schemes for each of a large
number of combinations of baseline factors. Taves’ suggested an approach called ‘minimization’,
whereby the treatment to be received by a particular patient is chosen so as to minimize some index
of discrepancy between the characteristics of the treatment groups. Variants of this approach,
introducing the sort of randomness characteristic of biased-coin designs, have been described by
Pocock and Simon,14 Begg and I g l e ~ i c z ’and
~ Atkinson,16 among others. The two latter papers
use methods which are theoretically complex but could be implemented by an appropriate use of a
microcomputer.
(ii) Concentration on the most eflectiue treatments
If the response to treatment of an individual patient becomes known with only a short time-lag
after the start of treatment, the cumulative results can be updated so that the apparently more
effective treatments can be identified. Many authors have argued that, ethically, higher
RANDOMIZATION IN CLINICAL TRIALS
349
proportions of patients should be placed on the apparently better treatments than on those which
appear to be inferior. There are very many ways in which this adaptive allocation could be carried
out. For binary responses (successifailure), Zelen” suggested the ‘play-the-winner’ rule, whereby
treatment is changed each time a failure occurs. Many authors have studied this problem from the
point of view of decision theory, the object being to minimize the number of patients, in the trial
and perhaps in a larger group to be treated in future, who receive an inferior treatment. An optimal
solution is likely to involve a gradual shift from 50 : 50 allocation between two treatments at the
outset, to an overwhelming preponderance on the apparently better treatment at some later stage.
I do not believe that schemes of this sort have been at all widely used. Although ethically
attractive, they are in a sense statistically inefficient since widely discrepant group sizes are less
efficient for the estimation of differences between groups than are equal group sizes. Perhaps more
important, the characteristics ofpatients entered into a trial are likely to fluctuate during the intake
period, particularly if allocation proportions are changing. It will then be very difficult to carry out
a valid statistical analysis. Finally, the ethical argument is far from straightforward: is it ethical to
place 1 patient in 20 on a clearly inferior treatment? Some of these issues are discussed further by
Simon. l 8
3.3 Group allocation
We have assumed so far that a random assignment is made either for an individual patient or for a
particular course of treatment to be given to the patient. Occasionally, there will be a special
advantage in arranging that a group of patients receive the same treatment. If medical care is
delivered in stressful circumstances, as perhaps in a casualty department, it may be impracticable
to arrange for individual randomization, but quite feasible to use the same regime for a fixed
period of time during which many patients will be treated. Again, it may be politic to ensure that all
subjects in a group receive the same treatment. In general practice trials, each practitioner may
wish to have uniformity of treatment within his group of patients; features of medical care in
hospitals, such as nursing routine, may have to be applied uniformly within a ward; in a dental
caries trial the same toothpaste may have to be used by all members of the household.
The essential point to remember here is that the units which are randomly assigned to treatments
are now the groups, rather than the individual patients, and (as noted in connection with the trial
by Anderson et al. in Section 1) considerations of replication require that the number of groups
should not be too small, even when the groups each contain a large number of patients. The
statistical analysis of studies of this sort is discussed by Simon.”
4. ARGUMENTS AGAINST RANDOMIZATION
Although the case for randomization was presented forcefully and persuasively by Hill and others
in the 1940s, 1950s and 1960s, the argument still rumbles on. Certainly the practice ofclinical trials
is much less firmly established in some countries than in others, and no doubt the ethical issues
(discussed in Section 5 ) present themselves in different lights when viewed against different
traditions of medical practice. Some doubts about randomization have been revived during the
last decade, and one or two different strands in the debate need to be distinguished.
Gehan and Freireich,20writing particularly about cancer trials, argue for a greater reliance on
historical controls. They are concerned partly with the element of artificiality introduced into
medical practice in a controlled trial. They also argue that a large set of historical controls can
improve precision: if 50 patients are available for testing a new treatment against a widely-used
standard, a comparison of all 50 on the new treatment against an effectively infinite number on the
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standard will have less random error than a comparison of 25 againt 25. They admit that
retrospective comparisons may introduce bias, but argue that disparities in baseline characteristics
can be allowed for by appropriate statistical techniques.
I believe that this view seriously underestimates the danger of relying on historical controls.
Adjustments for baseline differences may well allow properly for discrepancies in the chosen
variables, but they provide no safeguard against possible disparities in other respects. Not only
may the comparisons be biased, but there is no way of measuring the extent of the bias.
A special case can perhaps be made for non-randomized designs in Phase I1 studies, particularly
in the early investigation of chemotherapeutic agents against cancer. These studies are necessarily
small, since the aim is to select for further study only the small proportion of agents which show
initially promising results. Since the sampling error is necessarily large, it may be worthwhile to
reduce this by using historical rather than simultaneous controls, even at the risk of introducing
bias. It must be remembered that Phase I1 trials are screening procedures, rather than comparative
studies with the authority of Phase 111 trials.
A different approach has been advocated, particularly by workers in medical computing: the use
of large databases recording the baseline characteristics, treatment received and responses
observed for large numbers of patients.’ If a new treatment is to be evaluated, the proposal is that
it should be used on a group of patients each of whom would be matched for relevant
characteristics with a patient who previously received a standard treatment, and whose data are on
file. The dangers of this approach have been expounded by Dambrosia and EllenbergZ2and
B ~ a rAll
. ~the~ reservations previously expressed about historical controls apply here, and there is
additional concern about the difficulty of maintaining uniform and reliable standards of data
recording in data collected routinely from several sources over a long period of time.
Aspden, Jackson and WhitehouseZ4advocate the use of mathematical models describing the
transition of cancer patients from one clinical state to another, so that treatments can be assessed
by comparing the proportions of patients who, at various times, are currently in specific states.
Underlying their approach is a reliance on historical comparisons between non-randomized
groups, and there seems no reason to believe that this is any more well-founded than in the other
situations described here.
5. ETHICAL ISSUES
‘The first step in . . . a trial is to decide precisely what it is hoped to prove, and secondly to consider
whether these aims can be ethically fulfilled. It need hardly be said that the latter consideration is
paramount and must never, on any scientific grounds whatever, be lost sight of. If a treatment
cannot ethically be withheld then clearly no controlled trial can be instituted.’
The principles expressed in these words by Hill’ have been reiterated since by many writers,
and there can scarcely be a clinical trial conducted today in which the participants do not
thoroughly satisfy themselves about the ethical propriety of the study. Of course, ethical
judgements are subjective, and it is not uncommon, in the planning of a multicentre trial, to find
disagreement among the investigators on ethical issues. If several treatments are to be compared a
particular investigator may be willing to use some but not all treatments, different selections being
preferred by different participants. Perceptions of precisely what randomized comparisons would
be ethical are likely to vary from one country to another, and will certainly change with the passage
in time as more information becomes available.
Hilllo quotes the following passage from an anonymous editorial in the British Medical Journal
(‘A comment that expresses what I feel and could not myself, I am sure, have put more clearly’):
RANDOMIZATION IN CLINICAL TRIALS
351
In treating patients with improved remedies we are, whether we like it or not,
experimenting on human beings, and a good experiment well reported may be more
ethical and entail less shirking of duty than a poor one.’
He remarks elsewhere’’ that ‘It may well be unethical. . . . not to institute a proper trial.’
Again, he argues” that ‘a trial should be begun at the earliest opportunity, before there is
inconclusive though suggestive evidence of the value of treatment. Not infrequently, however,
clinical workers publish favourable results on three or four cases and conclude their article by
suggesting that this is the method of choice, or that what is now required is a trial on an adequate
scale. They do not seem to realize that by their very publication they have vastly increased the
difficulties of that trial or, indeed, made it impossible.’ For this reason, T. C. ChalmersZ5has
vigorously argued in favour of randomization of the first patient, a view with which I agree except
perhaps for some of the early Phase I1 trials referred to in Section 4.
If a randomized trial has been started, and the responses of individual patients are analysed as
they accumulate, it may become more and more obvious that one treatment is better than another.
The investigators may then become convinced that continued randomization is unethical. It is
impossible to lay down rules by which such decisions should be arrived at. Many considerations
will be relevant: more than one response variable; side effects as well as therapeutic responses;
long-term as well as short-term benefit; ease of administration and perhaps costs. A formal
sequential analysis of the r e s ~ l t s is
~ ~likely
~ ~ ’to be useful in allowing for the effect of repeated
analysis of the data, but should be regarded as a guideline rather than an overriding stopping-rule.
It has sometimes been suggested that randomization of treatment for a given patient is justified
only if the doctor’s views about the preferable treatment for that patient are exactly balanced-a
situation which of course would never arise in practice. On this view, a single observation for one
patient would tip the scales one way or the other, and further randomization would be impossible.
This is, perhaps, the extreme ‘individual’ view in the distinction drawn by Lellouch and Schwartz”
between ‘individual’ and ‘collective’ethics. In practice there will be a wide range of situations in
which the doctor will feel quite justified in giving any of a number of treatments, because the
information about all the relevant issues is so scanty, and it will require a good deal of evidence to
make him feel that the treatment of choice is clearly identified. The doctor, in fact, will adopt an
attitude of collective ethics, permitting the collection of reliable data for the benefit to future
patients, provided that there is no clear indication that the interests of his present patients are
damaged.
Patients will normally be entered into a randomized trial only after their informed consent has
been sought and obtained. The extent to which this practice is a legal requirement, and the precise
nature of the informed consent varies from one country to another. The numbers of patients
available for a trial will therefore be depleted by those patients unwilling to take part, and the
relative efficacy of treatments may differ between the consenters and the non-consenters. In an
effort to diminish these disadvantages, Ze1enz9has suggested an alternative approach for a trial in
which a new treatment, N, is to be compared with a standard, S. The patients are randomized into
two groups: I, who will receive S, with no request for consent; and 11, who will be asked whether
they are prepared to receive N. In Group I1 the consenters receive N and the rest receive S.
A perfectly valid comparison is possible between Groups I and 11, since they have been formed by
random assignment. A difference between Groups I and I1 may safely be ascribed to the difference
between N and S, but if the proportion of consenters is low the treatment effect may be so diluted
by the non-consenters as to be undetectable. The treatment effect amongst the consenters can be
estimated fairly, although with impaired efficiency if the proportion of consenters is low. It is too
early to judge whether this device will be widely used in practice.
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PETER ARMITAGE
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