Restricted Randomization Designs in Clinical Trials

Restricted Randomization Designs in Clinical TrialsAuthor(s): Richard SimonSource: Biometrics, Vol. 35, No. 2 (Jun., 1979), pp. 503-512Published by: International Biometric SocietyStable URL: http://www.jstor.org/stable/2530354 .

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BIOMETRICS 35, 503-512 June, 1979

THE CONSULTANT'S FORUM

Restricted Randomization Designs in Clinical Trials

RICHARD SIMON

Biometric Research Branch, National Cancer Institute, Bethesda, Maryland 20205, U.S.A.

Summary

Though therapeutic clinical trials are often categorized as using either "randomization" or "historical controls as a basis for treatment evaluation, pure random assignment of treatments is rarely employed. lnstead various restricted randomization designs are used. The restrictions include the balancing of treatment assignments over time and the stratification of the assignment with regard to covariates that may affiect response. Restricted randomization designs for clinical trials di,ffier from those of other experimental areas because patients arrive sequentially and a balanced design cannot be ensured. The major restricted randomization designs and arguments concerning the proper role of stratification are reviewed here. The effiect of randomization restrictions on the validity of significance tests is discussed.

1. Introduction Determination of the method of assigning treatments in comparative clinical trials is an

important task of the statistician. Much of the traditional experimental design methodology is not directly applicable because patients arrive sequentially from very heterogeneous populations, and one cannot generally select patients to obtain a convenient balanced design. Randomization plays a key role in clinical trials. Randomization reduces or eliminates the bias in treatment comparisons that may result when responses of current patients are compared to those for "historical controls" (Byar, Simon, Friedewald, Schlesselman, De- Mets, Ellenberg, Gail and Ware 1976, Pocock 1979). Secondly, randomization eliminates the "selection bias" (Blackwell and Hodges 1957) that may result from the conscious or subcon- scious concurrent selection of patients for one treatment or another. Experimental randomization can also serve as a basis for inference (e.g., Lehmann 1959).

In clinical trials pure experimental randomization is often rejected in favor of various types of restricted designs. The restrictions are of two general types: blocking over time and stratification by covariates. Several new methods for blocking over time have been recently introduced, and these are reviewed in the next section. The proper role of stratification in clinical trials is an area of considerable controversy. These arguments are critically reviewed in Section 3. Recent developments in adaptive stratification methods are presented in Section 4. These stratification methods are adaptive in the sense that treatment assignment probabilities for a patient depend upon the covariate values of the treatment groups already formed by that point. They are not adaptive in the sense that treatment assignment is influenced by observed responses (Simon 1977). Special attention is given in Section 5 to the effect of

Key Words: Clinical trials; Stratification; Significance tests.

503



504 BIOMETRICS, JUNE 1979

randomization restrictions on the validity of significance tests. It is common to see clinical trials in which stratification is used in the design but ignored in the analysis. The eSect of such practlce is discussed.

2. Unstratified Restricted Randomization Often pure randomization is not used in clinical trials because it is desirable to have

treatment groups of approximately equal size both for interim and final analyses. Randomi zations are usually 'Sblocked" so that after every bT patients, each of the T treatments have been assigned to b patients. Blocking is also viewed as a protection against unknown time trends in the characteristics of arriving patients. The block size bT is generally much smaller than the number of patients to be treated. Blocked randomizations are more susceptible to selection bias because physicians entering patients have a greater probability of guessing which is the next treatment to be assigned and this could influence their choice of whether to enter a patient. For example, the last treatment of a block can be predicted with certainty if one has counted the treatments assigned and has determined the block size. Blackwell andn Hodges ( 1957) and Stigler ( 1969) have studied the effect on selection bias of various blocking strategies. They assume that two treatments are to be allocated to each of N patients. Thus, the block consists of 219 patients. The design in which all C(2N, N) sequences of the two treatments are equally likely is called the "random allocation" design. The design in which treatments are assigned randomly until one treatment has been assigned to N patients and then the other treatment is assigned to the remaining patients has been called the "truncated binomial" design. Blackwell and Hodges (1957) show that the truncated binomial design minimizes the maximum expected number of correct guesses. Stigler (1969) and Wei (1978a) show that the random allocation design is preferable in some senses other than minimax.

As a means of limiting selection bias while maintaining treatment groups of approximately equal size, Efron ( 1971 ) introduced the "biased coin" design. At each point in the trial one assigns with probabilityp > 1/2 that treatment which has been assigned previously to the fewest number of patients. If the number of assignments are equal at any point, each of the two treatments are assigned with equal probability. Pocock (1979) has discussed guidelines for the selection of the bias p.

Wei ( 1978b) has introduced an "adaptive biased coin design" in which the degree of bias depends upon the magnitude of imbalance and upon the number of patients treated. After N patients have been treated, assume that NA(NB) were assigned treatment A (B). Wei proposes to assign treatment B to the (N + 1 )st patient with probability p(DN/N), where DN = NA-NB and P is a monotonic non-decreasing function of its argument. If the function p(x) is continuous, then the adaptive biased coin design behaves more like pure randomiza° tion asymptotically in N; for example, selection bias is asymptotically zero. A relatively simple case of the adaptive bias coin design has p(x) = (1 + x)/2, that is p = NA/N. This has an urn interpretation (Wei 1977, 1978c)5 and has the property that treatment assignments are asymptotically uncorrelated.

If treatment assignment is not stratified by prognostic factors, or if many patients are expected in each stratum, then a conventional block design with large block size will be adequate for controlling selection bias. This is particularly true for multi-institution studies in which institution is not a stratification factor, because investigators at any one institution will not be aware of the most recent assignments to patients elsewhere. Nevertheless, use of large block sizes may result in very unequal sample sizes among the treatment groups for interim analyses. Thus, the more recent methods are of value in these circumstances. For stratified studies in which limited numbers of patients are expected in each stratum, conven-



RESTRICTED RANDOMIZATION 505

tional block designs with long block lengths are not adequate. In such multi-institution studies, short block lengths can be used if institution is not a stratification variable. Other wise, the designs of Efron or Wei are best employed. The cost involved in these more recent designs is the additional complexity in producing the list of treatment assignments. This list is however produced once at the start of the study, and is used thereafter in a straightforward manner.

3. stratification The concept of stratified randomization is of some controversy to medical statisticians.

Stratification has generally meant that patients are partitioned into mutually exclusiv subsets defined by initial characteristics, or covariates, thought to influence response. If stratification factor i has Li levels, then the number of strata equals the product of the Li. Treatment assignment is performed separately for each stratum using a blocked or biased coin type of randomization. These randomizations are prepared independently for each stratum. This class of designs shall be referred to as conventional stratification designs.

Sedransk (1973) studied a related design in which the blocked randomizations for each stratum are not prepared independently. The set of first assignments in each stratum constitutes a 1/T replicate of the T by lILi factorial design with one high order interaction confounded. The set of second assignments constitutes another 1/T replicate of this factorial design with the same interaction confounded. The first T assignments correspond to all T of these fractional replicates. Each block of T corresponds to a new randomly selected high order interaction to be confounded. Sedransk refers to this design as "factorial stratiD fication.99

A widely accepted objective of stratification is to ensure that the treatment groups are '6comparable" with regard to factors other than treatment that may affect response. This viewpoint was expounded by Hill ( 1960) for clinical trials, and has been widely accepted. To many statisticians, the notion of comparability is vague and problematical. It would seem that factors thought to affect response should be included in the design and analysis to the extent possible, rather than absorbed as experimental variability as the term "comparability" . .

lMp ileS.

In an extensive paper on clinical trials9 Peto, Pike, Armitage9 Breslow9 Cox, Howard, WIantel, McPherson, Peto and Smith (1976) dismiss stratification as a complication rendered unnecessary by the development of methods of analysis that adjust for covariates. This theme was repeated in an editorial entitled "Randomized clinical trials'9 in the British Medical Journal (19779 6071, 1238-1239).

The viewpoint of Peto et al. (1976) appears to be based upon three underlying beliefs. First, the increase in expected power of significance tests resulting from the use of stratification is minor. Second, stratification is logistically inconvenient and may discourage investigators from even using randomization. Third, it is only for small clinical trials that absence of stratification is likely to result in having the treatment effect confounded with a covariate eSect, and small trials are criticized by those authors.

Though the paper by Peto et al. is of great value for clarifying the most critical statistical components of clinical experimentation, its position on stratification is not entirely satisfac- tory. Small single institution clinical trials are often of great importance because they can represent the best ideas of a few individuals rather than the compromise of a large committee. Even large studies are small at the time of interim analyses, and expected power is not the most relevant power consideration. Prospective stratification can be viewed as an insurance policy against low probability events that can ruin the study (Lasagna 1976).



506 BIO METRICS, JUN E 1979 The use of prospective stratification also tends to avoid situations in which conclusions of a-study are not convincing to the medical community because of suspicion of an analysis used to adjust for a lack of comparability. This is a very real concern, for the term 6'adjustment" itself often elicits skepticism. The validity of an adjustment technique does depend on the adequacy of the assumed statistical model. Even with simple types of adjustment procedures, there may be great ambiguity concerning which variables to adjust for. Adjustment for all variables may entail considerable loss of power, and selection of adjusting variables by stepwise procedures or informal methods can result in an arbitrariness in the resulting conditional significance level.

4. Adclptive Stratification Conventional and factorial stratification designs become ineSective when the number of strata becomes too large for the sample size (Pocock and Simon 1975). In many medical areas there are numerous factors thought to aSect response. Stratification by a single risk score that accounts for the eSect of all known covariates has been suggested by several individuals (e.g., Miettinen 1976). This suggestion has some merit where data is available for the determination of such a risk function. In the past several years9 a class of adaptive stratification methods have also been proposed for situations in which there are many prognostic factors (Harville 1974, Taves 1974, Pocock and Simon 1975, Efron 1976, Wei 1978d).

Pocock and Simon (1975) introduced the following method. At any point in the trial suppose that a treatment assignment must be made for a new patient. Let Xi, denote the number of previous patients who were assigned treatment k who had variable i at the same level as the new patient. If the new patient were assigned treatment t, the integers {XEk} would change in the following way:

Xik = Xik if t + k and = Xik + 1 if t = k. Let sF(t) denote some function that measures "lack of balance" for the resulting {XEkt} for fixed t. For example,

F(t) = z wi Var[Xilt, Xi2ts * * * 9 XiTt]

where T denotes the number of treatments being studied, Var denotes the §ample variance function, and wi denotes the relative importance of variable i. There are many other possibilities for the function F including the weighted sum of ranges of the (Xist) or the function

F(t) = E wi Var[Xilt/Nlts Xi2t/N2t, . . ., XiTt/NTt] l

where Nst denotes the total number of patients that have been assigned treatment k up to and including the current patient who is tentatively assigned treatment t. The conditional bias in estimating a treatment contrast by an unadjusted linear combination of treatment group means can be shown to be proportional to this latter function. The basic idea in the approach described is that imbalance is measured marginally for each variable and summed over the variables. The procedure of Pocock and Simon is applied by se_cting an imbalance function F and a set of non-negative constants pl, p2, S ., PT such that 2: Pk = 1. At any point in the trial the treatment for a new patient is determined by ranking the treatments based on the F values. The treatment with the smallest F value gives




the least marginal imbalance and is preferred in that sense. The treatment with the kth smallest rank is assigned with probability Pk Pocock and Simon (1975) proposed several reasonable methods for specifying the treatment assignment probabilities pl, . ., PT Klotz (1978) has shown how to specify these probabilities so as to maximize the entropy of the assignment (-E pklnpk) subject to a constraint on the expected imbalance.

Taves (1974) proposed a method that he called "Minimization" for two treatments. "Minimization" is equivalent to using the range imbalance function with constants pl = 1, P2 = 0. Freedman and White (1976) showed that for some imbalance functions the calcu- lations required are very simple, and the provisional quantities Xikt are not needed. Harville (1974) and Zelen (1974) described related approaches to sequential design. Zelen's method, recently reviewed by Pocock (1979), is a hybrid of conventional and adaptive stratification specifically for multi-institution studies.

Adaptive stratification methods are very eSective in producing marginal balance of the treatment groups with regard to many variables. Logistically, however, they are less convenient than conventional stratification. With the latter, the sequence of assignments within each strata can be prepared at the start of the study. This is not possible for the adaptive designs, because the treatment assignment depends upon the values of the stratification variables for patients already entered on the study. It is necessary to use a computer or a programmable calculator for each patient being randomized, or to use a manual procedure that is quite simple, but more error prone than opening an envelope. It is possible to maintain a computer printout of the next treatment assignment for the next patient in each possible stratum. When a request for a treatment assignment occurs, it can be immediately satisfied, then the file is updated and the computer printout for each possible next patient prepared.

5. Relationship Between Design and Analysis

The rapid development of adaptive blocking and stratification designs, and analysis methods for covariate adjustment, has served to focus attention of medical statisticians on how the validity of an analytic method depends upon the design employed. For example, Bearman (1976) recently wrote in a clinical journal: ". . . the only logical basis that we know for making generalizations from data all rest on the foundation of randomization.... If any of you need my help, or that of any of my biostatistical colleagues, random assignment of patients will be a sine qua non, at least until the author of 'Minimization' provides his clarification of procedures and a mathematically logical basis for using such procedures." Bearman seems to mistake experimental randomization with random sampling of patients. Random sampling of patients is the basis for generalizations, though it is very rarely, if ever, employed. The relationship of design to analysis for clinical trials is however an area that requires clarification.

Lehmann (1959) distinguishes two approaches to significance testing. With the first, experimental randomization of treatments to patients is the basis for inference. With this approach, the significance tests used must be only those tests generated by the experimental randomization design actually employed; if blocking or stratification was used, they must be considered in determining the possible alternative assignments that generate the significance level. As the degree of blocking and stratification increases, the cardinality of the set of possible alternative assignments decreases. If there are M possible arrangements, the possible significance levels are 1/M, 2/M, 3/M, . . . . As M decreases the power of the test may severely decrease. For example, if M < 20 no result can be significant at the .05 level. In the limit, one obtains a systematic design, balanced with regard to many covariates but selected from a set of very few possible designs having such balance. Taves' "Minimization" method



508 BIOMETRICS, JUNE 1979 represents such a design. The methods of Pocock and Simon (1975), Efron (1976) and Wei (1978d) are not so extreme because they are less deterministic. It is possible, though cumbersome9 to perform the appropriate randomization test generated by a non-deterministic adaptive stratification design. One assumes that the patient responses, covariate values, and sequence of patient arrivals are all fixed. One then simulates on a computer the assignment of treatments to patients using the adaptive stratification design actually employed and the treatment assignment probabilities actually employed. Replication of the simulation generates the approximate null distribution of the test statistic adopted, and the significance level. One need not make the questionable assumption that the sequence of patient arrivals is random as long as the adaptive stratification method includes treatment assignment probabilities. Simulation, rather than replication, is used because the possible assignments are not equally likely and depend in a complicated manner upon the sequence of covariate values observed.

The alternative to using the randomization distribution to generate the significance level is adoption of a hypothetical model. This approach often involves a random sampling assumption. For example, the usual normal linear model entails the assumption that conditional upon observed covariates and treatment, the responses are a random sample from an infinite population. Most two sample rank tests do not hypothesize a parent population, but do assume that conditional upon the order statistics for the combined samples, the observa- tions are iid random variables. The assumption of random sampling of experimental units from a parent population is almost never true, but plays the role of a theoretic construct to assist in the interpretation of results. It is common to see clinical trials in which conventional stratification is used in treatment assignment, but the stratification variables are ignored in the rank-tests used for analysis. In such cases, experimental randomization does not form a basis for the significance level. If the design employed is not consistent with the assumptions of the model used for analysis, then the resulting significance level may be distorted. For unstratified block or bias coin designs, Efron (1971) showed that asymptotically the significance level can be consid- erably overestimated if the analysis assumes that pure randomization was used. Anti- conservatism is also possible in a block design with small block length. Forsythe and Stitt (1977) considered the stratified case in an empirical sampling study. Normal random variables were generated from a linear model relating response to treatment and a single covariate. They evaluated the significance level and power of a two-sample t-test using either experimental randomization or Taves' Minimization. They found that Minimization produced a significance level of .013 rather than the nominal .05 of the test. They also found that the power of the t-test was less for Minimization than for randomization for moderate departures from the null hypothesis, though it was equivalent to or greater than the power for randomization when the treatment diSerences were large. Feinstein and Landis (1976) and Green and Byar (1978) showed that these considerations also apply to conventional stratification. Forsythe and Stitt also performed their empirical sampling studies using the analysis of covariance to compare the treatments after adjusting for the eSect of the covariate. In this case, the significance level resulting from Minimization was equal to the nominal level of the test. The analysis of covariance resulting from Minimization was more powerful than that resulting from randomization, though the diSerences were not great. This same topic was discussed in the 1930's in a series of papers by Barbacki and Fisher (1936), Student (1937) and Pearson (1938) concerning the role of randomization in agricultural experimentation. It was Student's position that if one balanced the experiment with regard to factors thought to aSect response, then the diSerence in treatment means would generally be a more precise estimator of the true treatment diSerence, though an unbiased



RESTRICTED RANDOMIZATION so9

estimator of the standard error of the diSerence would not be known and would generally be smaller than that conventionally calculated from the data under the assumption of experimental randomization. Student thus asserted that the true significance level of the t test would be less than the nominal level, but he saw nothing to be gained by believing once in 20 times that a diSerence exists when it does not. He felt that the gain in precision of the estimator of treatment diSerence would lead to less confusion in the interpretation of similar experiments performed at diSerent locations.

Using a correct model, the omission from the analysis of covariates used for stratification distorts the significance level only if the omitted covariates do influence response. Consider, for example, the analysis of the linear model relating response to treatment and covariates where the errors are independent and normally distributed with mean zero and variance C2, For estimating C2 one must take into account the covariates. It does not matter whether one stratified by other spurious variables or even whether one randomized at all if the model is correct. One generally randomizes in order that potential biases are identically distributed among the treatment groups and can be absorbed into the error term. If there are stratification variables that do eSect response and are not explicitly included in the model, then the estimator of C2 will be biased. In general an over-estimate Of C2 will result. Using an important covariate for stratification and ignoring it in the analysis yields an estimator of treatment eSect (e.g., [1-g2) having increased precision compared to the estimator obtained by not even stratifying for the covariate, but the estimator Of C2 iS positively biased. Green and Byar (1978) have shown that this results in decreased power for testing t1 = t2 for local alternatives but increased power for large treatment eSects. The local decrease in power results from the bias in the estimator Of C2, The increase in power for large treatment eSects results from the increased precision of the estimator [1-[2.

The studies described above may be interpreted to imply that the eSect of stratifying by a covariate and then ignoring it in the analysis are not severe. These conclusions were derived for fairly simple models however, and do not apply to all conceivable restricted designs. Consider for example the following experiment. A scientist wishes to evaluate two nutrient additives A and B for plant growth. The experiment is performed in a laboratory that is long on the east-west axis and narrow on the north-south axis. There is a single window at the east end of the laboratory. Because sunlight is the only known covariate, the scientist uses a design completely balanced with regard to distance of each plant from the window. He lines up all plants receiving one nutrient equally spaced along the north wall, and does similarly for the plants receiving the other nutrient along the south wall. Whether all plants along the north wall receive nutrient A or B is determined by a single toss of a fair coin. Unknown to the scientist is a temperature gradient in the room which adversely eSects the growth of plants along the south wall compared to plants along the north wall. If the adverse eSect of the temperature gradient is sufficiently strong, then the true significance level of a test of the null hypothesis of no nutrient eSect may be 1.0 rather than a nominal 0.05.

Though it is difficult to produce a convincing clinical example of the type described above, the example presented demonstrates that use of some types of stratification with an incorrect hypothetical model for analysis may result in severe accidental bias (Efron 1971), and not merely in a conservative significance level. Accidental bias can be viewed as a measure of the maximum distortion of the significance level achievable with a treatment assignment method. Consider the actual proportion of time that the null hypothesis is rejected in repetitions of the treatment assignment with a fixed sequence of patients (and their responses) when there is no treatment eSect. If nature selects the patient sequence in the most unfavorable possible way (i.e., to maximize the rejection frequency), then the resulting true significance level is a measure of accidental bias of the allocation method. Totally systematic



510 BIOMETRICS, JUNE 1979 designs are very susceptible to accidental bias. It is possible that the accidental bias decreases rapidly when any randomrless is introduced into a systematic design (Efron 1978, Personal Communication). This is the case for the unstratified biased coin design (Efron 197l)s but further research is required for stratified designs.

6 . Con cllls ions The objective of this paper has been to review some reGent developments in statistical designs for clinical trials and to point out advantagess disadvantages and open questions associated with these methods. For very large clinical trials, a stratified design is not necessary for ensuring reasonable balance with regard to prognostie factors in the final analysis9 but may be important for interim analyses. Even if a stralified design is not useds i is useful to specify at the outset what covariates will be accounted for in the main analysis. Doing so avoids the ambiguity of significance levels resulting from ransacking the data. Supplementary analyse§ of subsets of patients would follow the main evaluation and be recognized as having a decreased level of reliability. The most preferable situation is to have prior information based upon large definitive studies where at most only a few variables exert important independent contributions to prognosis. These variables can then be used to define a conventional stratified design. lFor such a design one of the recent methods of blocking within stratum can be recommended to control patient selection bias while maintaining balance for interim analyses better than is achieved by truncated binomial or random allocation blocking or by Sedranskgs design. For multi-institutional studies with minimal stratification, it is desirable to use institution as a stratification factor in a conventional design.

When there are too many variables thought to ini[luence response to encompass in a conventional designg two alternatives are available. F:irst, one may use a conventional design omitting some of the variables. One would attempt to ineorporate the omitted variables in the final analysis only if their distribution among the treatment groups appears to bias the comparison or if the data suggests that they are important. This approach has the advantages of logistical and analytic simplicity. Alternatively, one can utilize an adaptive stratification design (or a hybrid as suggested by Zelen 1974) to account for the variables of presumed importance. lChe major advantage of this approach is as stated by Brown (1978): *6,, . there is much to be gained in persuasiveness or credibility by presentation of data that show the numbers of patients assigned to the several treatments to be closely balanced with regard to the variables commonly felt to be related to the course of the disease and the response to treatment. INo amount of post stratification and covariance analysis . . . will be as convincing as the demonstration that the groups were balanced in the beginning. s The main disadvantages of adaptive stratification are logistie complexity and possible loss of power of significance testsO

Resume Bien que les essais therapeutiques sur l'homme soSent souvent classes comme soit "rando mise's" soit reposant sur des "te'moins historiquement connus" en ce qui concerne la base de l'e'valuation du traitenlent on emploSe rarement l'attribution entieren1ent ale'atoire des traite ments. En place on utilise divers plans de randomisation restreinte. Les restrictions comportent l'e'quilibrage de l'attribution des traitements en fonction du temps et la stratitcation de l'attribution en ce qui concerne les covariates qui pourraient modifer la re'ponse. Les plans randomises restreints pour les essais cliniques di.erent de ceux des autres chanlps experimentaux




du fait que les malades arrivent sequentiellement et qu'un plan equilibre ne peut etre assure. Les plus importants plans randomises restreints et les arguments concernant le rozle propre a la stratification sont passes en revue. On discute l'effiet des restrictions de randomisation sur la validite des tests de signification.

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Dermatology 67, 679-681. Blackwell, D. and Hodges, J. L., Jr. (1957). Design for the control of selection bias. Annals of

Mathematical Statistics 28, 449-460. Brown, B. W., Jr. (1978). Statistical controversies in the design of clinical trials. Technical Report No.

37, Division of Biostatistics, Stanford University, Stanford, California. Byar, D. P., Simon, R. M., Friedewald, W. T., Schlesselman, J. J., DeMets, D. L., Ellenberg, J. H.,

Gail, M. and Ware, J. H. (1976). Randomized clinical trials: Perspectives on some recent ideas. New England Journal of Medicine 295, 74-80.

Efron, B. (1971). Forcing a sequential experiment to be balanced. Biometrika 58, 403-417. Efron, B. (1976). Randomizing and balancing a complicated sequential experiment. In Technical

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permitted by random allocation of treatment. Journal of Chronic Diseases 29, 277-284. Forsythe, A. B. and Stitt, F. W. (1977). Randomization or minimization in the treatment assignment of

patient trials: Validity and power of tests. Technical Report No. 28, Health Sciences Computing Facility, University of California, Los Angeles, California.

Freedman, L. S. and White, S. J. (1976). On the use of Pocock and Simon's method for balancing treatment numbers over prognostic factors in the controlled clinical trial. Biometrics 32, 691-694.

Green, S. B. and Byar, D. P. (1978). The eSect of stratified randomization on size and power of statistical tests in clinical trials. Journal of Chronic Diseases 31, 445-454.

Harville, D. A. (1974). Nearly optimal allocation of experimental units using observed covariates values. Technometrics lb, 589-599.

Hill, A. B. (1960). Controlled Clinical Trials. Blackwell Scientific Publications, Oxford. Kiefer, J. (1959). Optimum experimental designs. Journal of the Royal Statistical Society, Series B 21,

272-319. Klotz, J. H. (1978). Maximum entropy constrained balance randomization for clinical trials. Biometrics

34, 283-287. Lasagna, L. (1976). Randomized clinical trials. New England Journal of Medicine 295, 1086-1087. Lehmann, E. L. (1959). Testing Statistical Hypotheses. John Wiley and Sons, Inc., New York. Miettinen, O. S. (1976). Stratification by a multivariate confounder score. American Journal of Epide-

miology 104, 609-620. Pearson, E. S. (1938). Some aspects of the problem of randomization. II. An illustration of 'Student's'

inquiry into the eSect of 'balancing' in agricultural experiments. Biometrika 30, 159-179. Peto, R., Pike, M. C., Armitage, P., Breslow, N. E., Cox, D. R., Howard, Sf V., Mantel, N.,

McPherson, K., Peto, J. and Smith, P. G. (1976). Design and analysis of randomized clinical trials requiring prolonged observation of each patient. I. Introduction and design. British Journal of Cancer 34, 585-612.

Pocock, S. J. (1979). Allocation of patients to treatment in clinical trials. Biometrics 35, 183-197. Pocock, S. J. and Simon, R. (1975). Sequential treatment assignment with balancing for prognostic

factors in the controlled clinical trial. Biometrics 31, 103-115. Sedransk, N. (1973). Allocation of sequentially available units to treatment groups. Proceedings of the

39th International Statistical Institute, Book 2, 393-400. Simon, R. (1977). Adaptive treatment assignment methods and clinical trials. Biometrics 33, 743-749. Stigler, S. M. (1969). The use of random allocation for the control of selection bias. Biometrika 56, 553-

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512 BIO METRICS, JUN E 1979

Wei, L. J. (1977). A class of designs for sequential clinical trals. Journal of the American Statistical Association 72, 382-386.

Wei, L. J. (1978a). On the random allocation design for the control of selection bias in sequential experiments. Biometrika 65, 79-84.

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Wei, L. J. (1978c). A class of treatment assignment rules for sequential experiments. Communications in Statistics Theoreticcsl Methods A 7(3), 285-295.

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Zelen, M. (1974). The randomization and stratification of patients to clinical trials. Journal of Chronic Diseases 27, 365-375.

Received January 1978; Revised February 1979



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Restricted Randomization Designs in Clinical Trials

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