Methods of randomization in controlled clinical trials

Research

Seminars

Methods of Randomization in Controlled Clinical Trials MELVIN L. MOESCHBERGER, PhD,* JILL A. WILLIAMS, BA,t CHARLES G. BROWN, MD*

In this second article of a series exploring design and analysis issues in controlled clinical trials in emergency medicine, we will provide the case for randomization in clinical trials and review the various methods involved in simple randomization. In addition, the practical problems of simple randomization will be discussed including the feasibility of randomization, the possibility of an unequal number of patients being allocated to the experimental and control groups, and the potential imbalance of important patient characteristics or prognostic variables among subjects in the groups. Finally, some more elaborate randomization schemes will be presented to aid in overcoming these problems. We emphasize that the realities of clinical research place obvious restrictions on the conduct of many studies. As we develop this idealized scheme, one must keep in mind that some compromises may be required. Such compromises, of course, may weaken the impact of the research and influence the interpretation of the results of the clinical trial. THE CASE FOR RANDOMIZATION Historically, the medical profession has evaluated the efficacy and efficiency of various therapeutic interventions in a somewhat subjective and haphazard fashion. Case reports and clinical series, though extremely important in their own right, do not provide the broad base from which an inference from a sample to a large population can be made.’ The fact that a particular person who underwent prophylactic antibiotic therapy did not develop a wound infection following the repair of a laceration should not convince one that such treatment alone would be successful in all patients. Individual differences with regard to susFrom the *Department of Preventive Medicine, TBiometrics Laboratory, and *Division of Emergency Medicine, Ohio State University, Columbus, Ohio. Manuscript

received

January

16, 1985; accepted

March 1, 1985.

Address reprint requests to Dr. Brown: Division of Emergency Medicine, Rhodes Hall, University Hospitals, 450 West 10th Avenue, Columbus, OH 43210-1228.

ceptibility to infection, the adequacy of local wound care, the location of the wound, and the mechanism of the wound must also be considered. Although it may appear desirable to measure the effect of a treatment on an entire population, this, of course, is extremely impractical and usually impossible. Controlled clinical trials serve as an adequate scientific compromise between simply examining case reports and studying an entire population. Understanding sampling methods is essential to carrying out a controlled trial. It is desirable for the sample that is selected for inclusion in the study to be representative of the population of interest (target population). If the sample is not representative, conclusions can only be drawn back to the sample itself. This would be of little interest in most clinical trials. Samples that are representative of the target population help to ensure that the results discovered in the setting in which a particular trial was conducted will also hold true in similar clinical settings. Such ability of results to be generalized (external validity) allows other clinicians to use the results of the trial in their patient management and treatment. Investigators must be cautious in not over-interpreting the results of a clinical trial because, in certain instances, samples may not be representative. One situation in which this problem occurs is when self-selection bias of patients is present. Feinsteir? describes this self-selection bias: “Before a person can become a statistical unit in a study of disease, he must traverse a long and intricate series of directional transitions that lead him from his medical anonymity at home to his statistical inclusion in a collection of data.” Following onset of disease, an individual must recognize symptoms or other maladies that encourage the person to seek medical attention. The physician may or may not correctly diagnose the disease. If the disease is suspected or diagnosed the patient may be referred to specialists who in turn may choose the hospital to be used for further testing. Hospitals differ in the extent of diagnostic facilities available. Such factors along with relevant demographic characteristics 467

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(such as socio-economic variables) influence a particular patient’s likelihood of eventually becoming part of some scientific study. The series of transitions that Feinstein describes cannot possibly be regarded as random. In clinical emergency medical research this long series of transitions is not present to the extent that it is present in other clinical settings. Instead, patients often seek emergency medical care at the nearest hospital emergency department, and patients usually accept the physician who is on duty. Thus, the self-selection bias, although important to recognize, is less of a factor in many clinical trials in emergency medicine. The classic way to select a study sample such that the individuals chosen will be representative of the target population is to choose a simple random sample. Such a sample is chosen so that each member of the population will have an equal chance of being selected. Such a random selection of individuals, though not ensuring representativeness, minimizes the introduction of personal or circumstantial bias into a study population. The case for randomization is also evident upon examination of an important underlying assumption of classic parametric and nonparametric statistical tests. These statistical tests, which are designed to evaluate the efficacy of a therapeutic intervention from a probabilistic viewpoint. assume that a random sample was drawn during the course of the investigation from the target population. As random sampling provides us with a known probability for each member of the population being included in the study (or in the case of simple random sampling, the same probability of being selected), we are permitted to construct a probability distribution for any clinical endpoint of interest. Two critical assumptions required in formulating the probability distribution are that the sample observations are independent and identically distributed.j For example, sample observations in an investigation of the sequelae of streptococcal pharyngitis collected during a portion of the year in which there was an influenza outbreak will tend to be more correlated than sample observations collected during another part of the year. This correlation (lack of independence) changes the probability distribution of the test statistics, so that we may not be led to the well-known Z, t,~‘, or F distributions. In addition, if patient eligibility criteria are not well defined and strictly followed by the investigators during the course of a trial, then the distribution of the sample observations may be different (non-identically distributed). This is seen frequently in multi-center trials. If these assumptions are not satisfied, the probabilities that would be calculated using classic methods would be incorrect, and hence, the conclusions of the study might be invalid. Simple random sampling from the target population provides assurance that these assumptions are met. Another advantage of randomization is that patients

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with similar demographic and prognostic variables are assigned approximately equally to experimental and control groups when the sample size is large. If the clinician-investigator allocates patients to treatment groups in some convenient way (for example, selecting every other patient for the experimental treatment). or if patients choose the treatment they will receive, then imbalance of these important variables may occur, and the study results may be biased. Random assignment of patients to experimental and control groups tends to balance these important prognostic variables when the sample size is large. It is therefore important to ensure that both the clinician-investigator and the patient agree to accept any of the random treatment assignments before a patient is formally entered into a study. If either the clinician or the patient is unwilling to take this step. selection bias is introduced at this stage of the trial and may lead to an imbalance of important demographic and prognostic variables among patients in the treatment groups. Therefore, the validity of the trial may be seriously jeopardized. METHODS OF SIMPLE RANDOMIZATION The first step in obtaining a simple random sample is to identify the target population and, if possible. list the entire target population. In emergency medicine, as in many other clinical disciplines, it usually is not possible to list all members of the target population, as potential candidates will not even be identified before the study period has begun. In the absence of such a list, a randomized order of treatment assignments is prepared in advance. Pocock’ provides details related to implementing a randomization scheme. The simple randomization method usually used is equivalent to repeatedly tossing a coin or equivalent to drawing slips of paper with the numbers 0 (for control) and 1 (for experimental treatment) out of a hat to decide which of two treatments each patient should receive. In practice. this method is too crude and the investigator is open to criticism regarding lack of blinding and insufficient shuffling of the slips of paper in the hat.” In most clinical trials a randomization list is constructed from random number tables (a portion of which is presented in Table 16), or from random numbers generated by a computer. (The most extensive tabling effort in this regard was produced by the Rand random wheel The erating power ample. random

Corporation.’ They generated one million digits by designing an electronic roulette that was used solely for this purpose.) most frequently used method for randomly gennumbers is the multiplicative congruential (or residue) method,X which we illustrate in an exHere, one takes the “nth” number in the sequence R, to be

(X” x X,,) mod m which

is defined

as the remainder

when

X” x X,, is

TABLEl. 10 22 24 42 37 77 99 96 89 85 28 63 09 10 07 51 02 01 52 07 48 54 32 29 02 81 29 00 05 91 00 00 69 25 09 91 17 46 92 14 98 34 70 53 76 90 64 08 95 15

48 36 13 16 57 92 56 30 57 47 91 55 42 36 11 08 36 01 16 05 66 16 63 33 48 52 67 74 36 92 58 72 01 97 76 56 95 50 15 57 42 91 06 97 07 72 36 96 01 66

01 84 04 79 03 10 27 19 91 53 86 34 99 56 99 51 82 15 25 69 39 45 93 42 83 57 62 25 60 12 20 56 16 65 38 74 55 31 78 76 70 46 02 65 22 55 46 20 26 41

Random 50 65 83 30 99 69 29 19 43 68 95 09 39 11 73 27 13 40 39 76 12 84 23 70 30 22 05 73 42 64 47 98 57 79 34 25 63 85 96 27 75 39 82 49 95 22 74 03 83 04

11 73 60 93 75 07 05 77 42 57 78 61 69 29 36 65 82 92 16 28 45 92 63 01 62 95 91 92 13 18 11 84 97 48 73 95 49 84 34 65 23 76 77 14 15 10 12 58 79 93

Numbers 01 25 22 06 81 11 56 05 63 43 88 48 52 87 71 51 52 33 46 33 85 22 05 87 28 04 68 39 25 64 87 62 95 29 73 27 90 18 94 35 33 88 39 06 40 83 33 31 93 20

53 59 52 24 83 00 42 46 66 34 23 23 63 52 04 82 40 36 36 78 82 42 59 63 83 83 08 06 66 11 91 79 87 88 57 95 00 84 82 60 36 72 47 99 98 97 33 66 52 49

Adapted from Table X11.3-Random Co., 1966.

60 58 79 36 71 84 06 30 11 25 13 50 69 98 80 15 46 29 95 70 81 17 72 78 40 99 62 46 92 79 77 75 65 88 71 83 04 54 47 58 26 08 54 06 00 42 93 22 67 23

20 53 72 16 66 27 99 79 02 39 32 34 27 56 81 12 02 49 85 99 43 41 42 73 73 64 64 64 64 43 73 61 52 86 29 01 01 96 81 12 42 27 64 72 73 99 19 53 07 83

11 93 65 80 56 51 94 72 81 88 76 27 37 89 78 59 68 04 86 98 46 03 00 08 51 23 32 32 22 05 41 70 93 04 08 34 27 18 71 63 70 65 73 45 91 92 26 88 65 91

81 30 76 07 64 27 98 18 17 53 70 49 88 48 77 77 89 31 23 42 09 47 13 58 19 24 46 84 44 26 42 86 18 67 30 04 20 02 84 39 01 34 23 68 58 65 14 61 10 91

Units,from Handbook

64 99 39 85 03 75 87 87 45 06 99 62 97 23 23 45 36 27 21 69 17 07 36 73 73 87 90 67 40 76 20 32 98 91 88 02 04 30 61 66 63 47 21 35 74 83 88 64 59 13

of Tables

divided by m. To use this generator one must specify X (the multiplier), X0 (the starting value or seed), and m (the modulus). One choice of these values (X = 23, X, = 45 163 129, m = lo8 + 1 is easily implemented. Working from the basic method, we obtain R, = (X’ x X,) mod (IO8 + 1) = 38751957. Notice that the remainder of 23 x 45163129/10’ + 1 is 38751957. Similarly, we find the next two remainders to be: R2 = (X’

X

79 58 36 61 23 65 23 62 31 05 77 66 43 75 31 21 81 30 61 80 23 02 33 10 19 88 12 34 74 62 63 48 82 74 31 48 45 45 18 74 89 61 95 08 52 13 32 23 30 22

X,) mod (lo8 + 1) = 91295003 and

16 91 48 63 66 34 10 09 81 95 99 94 34 22 39 63 98 41 45 66 01 53 80 02 24 26 08 00 40 59 51 80 73 87 83 63 99 10 28 73 24 70 34 29 57 88 44 40 45 19

46 98 09 76 53 98 16 22 03 33 36 45 88 67 16 08 85 46 13 91 68 06 05 56 20 51 49 27 48 40 26 72 54 08 17 85 31 38 34 58 77 32 16 48 74 57 13 72 42 99

forProbabi/ityand

69 27 15 39 98 18 71 94 57 38 56 18 36 67 47 60 55 18 83 76 90 76 94 45 60 66 89 32 37 39 74 76 26 18 28 29 06 20 09 56 66 87 94 11 22 50 59 81 76 59

17 98 17 44 95 60 19 59 74 86 86 66 32 68 56 75 32 59 14 98 22 46 34 83 95 56 76 83 93 97 08 22 57 91 29 88 11 65 92 87 96 58 97 39 98 49 74 24 46 51

91 25 92 05 11 27 41 55 08 76 50 37 01 99 48 69 24 42 99 81 90 82 22 41 26 61 88 26 76 22 79 23 50 28 03 09 52 55 22 35 99 94 02 84 78 08 49 93 35 68

Statistics.

41 34 48 35 68 06 87 68 43 23 58 26 76 33 10 21 48 98 87 36 47 63 87 53 12 47 15 13 39 22 95 60 86 22 57 97 05 87 54 63 84 08 58 28 00 37 23 56 43 16

94 02 30 37 77 59 38 69 78 00 59 95 17 94 56 33 19 52 36 02 34 84 28 98 80 78 36 62 04 09 47 86 25 71 97 30 42 27 17 07 20 36 32 78 59 65 51 48 28 52

62 93 49 71 12 90 44 69 25 08 90 52 30 01 97 49 01 71 23 51 59 58 35 46 50 76 86 98 45 71 81 84 40 65 05 55 18 28 44 61 04 32 69 80 39 55 97 56 02 27

59 96 34 34 17 65 01 01 33 15 10 18 01 51 73 44 18 58 49 85 19 15 90 55 00 79 64 94 76 50 81 63 80 42 99 53 05 16 13 60 88 42 97 28 91 65 47 89 34 19

03 53 03 15 17 51 34 46 11 81 63 02 50 12 58 25 86 58 56 14 32 10 60 74 16 71 51 79 66 06 74 79 15 46 84 68 90 81 74 74 04 77 59 78 19 71 38 16 91 54

62 40 20 70 68 50 88 00 25 79 15 08 82 63 59 39 52 50 43 61 21 66 69 11 76 47 26 60 61 45 26 31 99 97 16 48 20 54 84 95 55 00 48 82 61 43 92 93 72 82

07 95 81 04 33 53 40 45 66 83 95 47 72 58 77 00 55 30 50 04 93 46 12 35 58 80 59 67 34 68 07 61 20 74 88 55 08 75 13 18 85 02 84 67 89 61 26 52 47 23

Cleveland, Ohio: Chemical Rubber

R, = (X3 x X,) mod (10s + I) = 99785049. These three S-digit random numbers could also be regarded as 24 random digits. Round-off error soon becomes a major problem with this method because the numbers X” x Xn become larger than the calculator’s or computer’s capacity. Therefore, a simpler numerical algorithm for this multiplier and modulus was devised. For example, we could generate the above eight-digit random numbers (38751957, 91295003, and 99785049) in a much more simplistic and readily computable fashion as follows.

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Let R, be determined by taking the seed, X,, multiplying by 23, removing the left-most digits so as to leave another eight-digit number. and subtracting the removed digits from the latter eight-digit number. That is, 23 x X, = 23 x 45163129 = 1038751967 The left-most digits are 10, leaving 38751967 as the remaining eight-digit number. Therefore. R, = 38751967 - 10 = 38751957. Similarly, RZ is determined by taking the preceding eight-digit number, R,. multiplying it by 23, removing the left-most digits so as to leave another eight-digit number, and performing the subtraction described above. That is, 23 x R, = 23 x 38751957 = 891295011 The left-most digits is 8, leaving 91295011 as the remaining eight-digit number, so R, = 91295011 - 8 = 91295003. Finally, 23 x Rz = 23 x 91295003 = 2099785069 and R, = 99785069 - 20 = 99785049. Any reasonable number of random eight-digit numbers may be generated using this method. Dudewicz and Ralley9 provide a comprehensive study of 20 random (pseudo-random) number generators. Most computerized random number generators use m = 2” or m = 2’ - 1 (s is a positive integer), X (the multiplier) to be one of certain prime integers, and X, (the seed), a large odd integer. to.” For the purpose of illustration below we shall use random numbers from a random number table. Ideally, to enter a random number table, one would choose a random page (Table 1) by picking numbers out of a hat or using some other random scheme. Then, in like manner, one would choose a random row and column. Often, in practice, only one page appears and a “blind” starting point on that page is chosen by closing the eyes and placing the forefinger somewhere on the table. This is analogous to selecting the “seed.” Suppose we start with the 12th row and 15th column (Table I). Reading across we find the numbers: 50342749626694451866 In actual practice, one of the computerized randomnumber generators described previously will probably be used. For a trial with two “treatments” (P for placebo and T for experimental treatment), there are many ways 470

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to prepare the randomization list for treatment assignments. Perhaps the simplest method is to assign odd digits to P and even digits to T. Using the above random numbers by matching the odd and even digits with P and T, respectively, we would have: 50342749626694451866 PTPTTPTPTTTTPTTPPTTT. Therefore, for a sample of 20 individuals, 13 would be randomized to the experimental treatment group and seven to the placebo group. Another method to prepare the randomization list would be to assign numbers O-4 to P and 5-9 to T. Then, based on the same numbers from the random number table, the list would be: TPPPPTPTTPTTTPPTPTTT. Now 11 individuals would be randomized to the experimental treatment group and nine to the placebo group. Still another method would be to assign numbers l-5 to P and 6-9 and 0 to T. This leads to a perfectly balanced randomization. Such randomization lists should be constructed before the trial begins, and they should be made long enough to complete the entire trial. The primary advantage of these simple methods of randomization is that each eligible person for the study has an equal chance of being given the experimental treatment or placebo.” Another advantage is the simplicity and ease of generation of such lists. PRACTICAL PROBLEMS WITH SIMPLE RANDOMIZATION One major disadvantage of these simple randomization methods is patient imbalance in the treatment groups. This is seen very clearly in the first randomization sequence discussed, where 13 out of 20 persons would be assigned to the experimental treatment. In practice the imbalance may be even more severe. The randomization could have assigned I5 patients to treatment and five patients to the control group. However, this would not occur very often, as the probability of getting a 15-5 split is 0.02 (i.e., we would only expect such an extreme split two times out of 100). The fact that such a severe imbalance has an extremely small probability of occurring is little consolation to the investigator who is planning for a reasonably balanced division. In addition, imbalance in the number of patients in experimental and control groups decreases the efficiency of the statistical test employed. Thus, it may be desirable to modify the randomization process to ensure a balanced treatment assignment. Such modifications will be discussed in the next section. Another frequently occurring problem with simple randomization is that important demographic or prog-

MOESCHBERGER

nostic variables may not be balanced in the treatment groups when small sample sizes are used. For example, a randomized study designed to evaluate the therapeutic effectiveness of intravenous bretylium tosylatet3 as a first-line drug for patients in cardiopulmonary arrest had more patients presenting with ventricular fibrillation in the bretylium-treated group than in the saline-treated group, while in the saline-treated group more patients presented with electromechanical dissociation and pulseless idioventricular rhythm (rhythms less “responsive” to bretylium therapy). Though these differences were not statistically significant, imbalances of this type can bias the experiment in favor of one therapy over another. Several alternative randomization schemes that minimize important imbalances of crucial independent variables are presented in the next section. Finally, ethical problems related to the randomization process have also been raised.14 Rimm and Bortin15 state that a randomized clinical trial employs “a code of ethics which transcends that which usually governs the doctor-patient relationship. The physician seeks scientific evidence about a therapeutic strategy, although in the process he knows that he may not be offering the patient the best available therapy.” Lebacqz16 argues that sometimes an alternative form of control group (one not necessarily based on randomization) should be used. She questions whether or not the scientific advantage of randomization is more important than patient choice of treatment. On the other hand, Hill” argues that if the efficacy of an experimental drug or treatment is not well established it would be unethical not to perform a controlled trial with randomization. In emergency medicine, critical care medicine, and traumatology, the randomized trial seems feasible in most treatment comparisons. One exception that surfaces involves emergency surgery. In this instance, patient numbers are likely to be small and the skill of the surgeon becomes quite a critical factor. A randomized trial performed by different surgeons may not provide the proper control for a valid comparison of surgical methods.t8 Participating surgeons should be equally skilled with the methods being compared. If they are not, then bias may be present in favor of the simpler procedure or a more popular procedure. It is important to note that randomization is not a panacea for lack of experimental control in a clinical trial. (More detail will be provided on these issues in a later article of this series.) SCHEMES TO REMEDY THE PROBLEMS WITH SIMPLE RANDOMIZATION As previously mentioned, treatment balance may, in some instances, not be perfectly achieved using simple

ET AL W METHODS

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randomization. Two approaches are suggested to remedy this potential problem. First, because there is nothing sacred about the first randomization list, one may continue generating randomization lists, before seeing any patients, until one with the desired balance is obtained. Of course, this is somewhat inefficient and may appear to lack scientific objectivity to some. The latter concern is only one of appearance, however, as the unbiased nature of patient allocation is still preserved. The crucial point is that the randomization lists are to be formulated before treating any of the patient pool. A second method is more organized. It forces balance in numbers of patients receiving the various treatments. This balance is achieved at pre-specified points in the sequence of patient assignments. To be specific, if we have two treatments, and we want balance after each pair of eligible patients is entered into the study, we would assign blocks of two patients the treatment sequence P T for random digits O-4 and T P for random digits 5-9. Using the random numbers generated earlier, 5034274962, we would have the following treatment the next 20 patients, TP

PT PT

PT TP

PT TP

sequence for

PT TP PT.

The basic problem with this randomization list is that a clinician who may be aware of the previous assignments (as in the case where blinding is not employed) may be able to predict the next treatment for a new patient. A method, in this same vein, that diminishes the problem of the investigator’s being able to predict the next treatment, uses blocks of four patients. For example, we would assign blocks of four patients the treatment sequence. PPTT PTPT PTTP TPPT TPTP TTPP

for for for for for for

digit digit digit digit digit digit

0, 1, 2, 3, 4, 5,

and ignore 6-9 in the treatment assignment. Again using the same random numbers generated earlier, 50342, we would have the following treatment the next 20 patients, TTPP

sequence for

PPTT TPPT TPTP PTTP.

Notice that after four patients are entered into the study, the treatment groups are perfectly balanced. 471

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This advantage is countered by the greater amount of sophistication and care required in constructing the randomization list. In general. balance may be achieved after entering _71i (k is a positive integer greater than 1) patients. In randomized trials it is also extremely desirable that treatment groups be similar with regard to relevant patient characteristics (prognostic variables). For example, in the bretylium trial introduced previously, the comparison groups for bretylium (B) and saline (S) could have been balanced with respect to the patients’ initial rhythm by employing a stratified restricted randomization. That is. a separate restricted randomization list as proposed earlier could be prepared for each stratum (level of initial rhythm condition).‘” To illustrate, we shall use the bretylium trial as an example. The initial patient rhythms, constituting the strata, were classified as ventricular fibrillation (VF), asystole (AS), electromechanical dissociation (EMD). and pulseless idioventricular rhythm (PIVR). For each stratum we could assign blocks of two patients the treatment sequence B-S for random digits O-4 and SB for random digits S-9. Using an extension of the random digits obtained from Table 1, and assuming more patients will enter the study with ventricular fibrillation than other types of initial rhythm. we will allocate patients to treatment for each stratum as follows. For patients with ventricular fibrillation, the random numbers and corresponding allocation to treatment will be 50 SBBS

3 BS

4 BS

2 BS

7 SB

4 BS

9 SB

62 SBBS.

For patients with asystole, electromechanical dissociation, and idioventricular rhythm, the treatment sequences will be, respectively. 6 6 SBSB

9 SB

4 4 BSBS,

51866 SBBS

SB

SBSB,

3 7 BSSB

2 BS

6 9 SBSB.

and

Four groups (one for each stratum) of sealed envelopes would be prepared by an independent person (someone who would not be involved in seeing the patient pool and does not have any bias in the efficacy of the treatment), and each would contain the treatment allocation for one entering patient. The randomization could then be easily implemented by matching an entering patient’s characteristics (presenting rhythm) with one of the four groups, and then picking the top envelope to determine the appropriate treatment. Notice that the randomization lists for each

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stratum could be carried out in blocks of four, eight, or in general. in blocks of 2k as described earlier. As the number of prognostic and demographic variables for which the investigator wishes to achieve treatment balance increases. the total number of prognostic strata may increase to an unmanageable size. For example, in the bretylium study, if we had also wished to balance patients with respect to bystander cardiopulmonary resuscitation (CPR) (two levels). age (three levels). estimated length of arrest prior to arrival of emergency medical services (three levels). transit time to the hospital (three levels), and presenting rhythm (four levels), then we would need 2 x 3 x 3 x 3 x 4 or 216 strata. As the number of patients entered in the study will probably be fewer than 100. one can see the futility of assuring balance with respect to these variables with so many strata. A more parsimonious selection of strata is certainly needed. Thought given to these matters before the study is crucial and may reap huge dividends at the study’s conclusion. Prognostic strata should be chosen in conjunction with the investigator’s knowledge of the discipline. In particular, one wishes to balance on prognostic variables that have a direct impact on outcome or response variables. In the bretylium study, initial rhythm (four levels) and duration of arrest prior to arrival of emergency medical services (~4 minutes. 4-8 minutes. or >8 minutes) might be two variables related to the outcome of resuscitation. Often. the investigator must arrange the prognostic variables according to priority for use in stratified randomization. Another method that is used to attain approximate equality of treatment numbers for each type of patient is the “minimization” method. The method is best described by example. Consider a hypothetical bretylium study when 60 patients have already been entered and the next patient is ready to receive treatment. Table 2 exhibits the number of patients in each of the two treatment groups (B and S) according to the prognostic factors of initial rhythm and duration of arrest (notice that although duration of arrest was not recorded in the original paper. we have included it for illustration purposes). Suppose the next patient has electromechanical dissociation as the initial rhythm and has an arrest time of 6 minutes. Then for these factor levels one adds together the number of patients in the bretylium- and saline-treated groups, respectively. For B this sum is 4 + 16 = 20. and for S this sum is 5 + 14 = 19. Thus. the patient is assigned to the saline-treated group (i.~.. the group with the fewest patients for the given constellation of factors). Notice that if the next patient had presented with ventricular fibrillation and an arrest time of 12 minutes, then the sum for B would be 23 and 23 for S. Thus, the method of minimization cannot decide which treatment this patient should receive, so the pa-

MOESCHBERGER

TABLE 2. Numbers of Patients in the Bretylium Study

Assigned

to Treatment

Bretylium Initial rhythm Ventricular fibrillation Asystole Electromechanical dissociation Pulseless idioventricular rhythm Duration of arrest 14 minutes 4-8 minutes >8 minutes

Groups

Saline

15 6 4 5

16 5 5 4

6 16 8

9 14 7

ET AL n METHODS

OF RANDOMIZATION

SUMMARY In this second article of a series that explores design and analysis issues in controlled clinical trials in emergency medicine, we have discussed the case for randomization, reviewed the methods involved in simple randomization, highlighted some of the practical problems involved with randomization, and presented some modified randomization schemes intended to remedy these problems.

REFERENCES would be randomized into a group by one of the methods previously described. Though perfect balance is not always attained with respect to all prognostic or demographic variables, statistical techniques that adjust for such imbalances exist and will be discussed at length in another article of this series. The ethical criticisms leveled against randomization can only partially be answered, as the problem is basically philosophical in nature. In comparing two therapies, everyone would desire to place patients in the most promising treatment group. Unfortunately, at the start of the trial, the investigator usually does not know which treatment is best. One method intended to remedy this ethical problem has been proposed by Zelen.?O The following criteria must be met: 1) the treatment outcome is dichotomous (success or failure): 2) the patients enter the trial one at a time; and 3) the outcome of a particular patient may be observed relatively soon during the course of the trial. It is a modification of the “Play the Winner Rule” espoused by gamblers and investigated by some statisticians’1.2? and is particularly applicable to clinical trials in emergency medicine (i.e. short-term resuscitation trials). At the outset of the trial, the first patient is randomly placed in the experimental-treatment or control group. If the first patient’s outcome was successful then the next patient is automatically assigned to the same group. However, if the first patient’s outcome was a failure, then the second patient is assigned to the alternative group. Sequential patients are assigned in a like manner, according to the preceding patient’s outcome. For example, a sequence of patient outcomes for the experimental and control groups may be as follows: tient

Patient: Experimental treatment: Control:

123

4 5 6 7 8 9 10 11 12 13

S S F

SSSS SF

F S SF...

The statistical theory that is more complex than the standard test of equality of two proportions is developed by Zelen. 23The method of “adaptive technique” will be addressed in more detail in another article of this series.

1. Kempthorne 0. Why randomize? J Stat Plan Inference 1977;l :l-25. 2. Feinstein AR. Clinical biostatistics II: Statistics versus science in the design of experiments. Clin Pharmacol Therap 1970;11:282-292. RH, Fletcher SW, Wagner EH. Clinical Epide3. Fletcher miology. Baltimore: Williams and Wilkins, 1982. 4. Pocock SJ. Clinical Trials. New York: John Wiley and Sons, 1983. SH, Louis TA, (eds). Clinical Trials. New York: 5. Shapiro Marcel Dekker, 1983. 6. Beyer WH (ed). Handbook of Tables for Probability and Statistics. Cleveland, Ohio: Chemical Rubber Co., 1966. 7. Rand Corporation. A Million Random Digits with 100,000 Normal Deviates. Glencoe, Illinois: The Free Press, 1955. 8. Hull TE, Dobell AR. Random number generators. SIAM Rev 1962;4:230-254. 9. Dudewicz EJ, Ralley TG. The Handbook of Random Number Generation and Testing with TEST RAND Computer Code. American Sciences Columbus, Ohio, American Sciences Press, 1981. 10. SAS User’s Guide: Basics. Cary, North Carolina; SAS Institute Inc., 1982. 11. Fishman GS, Moore LR. A statistical evaluation of multiplicative congruential random number generators with modulus 231 - 1. J Am Stat Assoc 1982;77:129-136. 12. Armitage P. Statistical Methods in Medical Research. New York; John Wiley and Sons, 1971. 13. Nowak RM, Bodnar TJ, Dronen S, et al. Bretylium tosylate as initial treatment for cardiopulmonary arrest: Randomized comparison with placebo. Ann Emerg Med 1981; 10:404-407. 14. Bonchek LI. Are randomized trials appropriate for evaluating new operations? N Engl J Med 1979;301:44-45. 15. Rimm AA, Bortin M. (1978). Clinical trials as a religion. Biomedicine 1978;28:60-63. 16. Lebacqz K. Controlled clinical trials: Some ethical issues. Controlled Clin Trials 1980;1:29-36. 17. Hill AB. Medical ethics and controlled trials. Br Med J 1963;1:1043-1049. 18. van der Linden W. Pitfalls in randomized surgical trials. Surgery 1980;87:258-262. 19. White SJ, Freedman LS. Allocation of patients to treatment groups in a controlled clinical study. Br J Cancer 1978;37:849-857. and stratification of patients to 20. Zelen M. The randomization clinical trials. J Chronic Dis 1974;27:365-375. design of ex21. Robbins H. Some aspects of the sequential periments. Bull Am Mathematics Sot 1952;58:527-535. two-armed-bandit 22. ZSmith CV, Pyke R. The Robbins-lsbell problem with finite memory. Ann Mathematical Stat 1965;36:1375-1386. clinical 23. Zelen M. Play the winner rule and the controlled trial. J Am Stat Assoc 1969;64:131-146.