Assessing Non-Consent Bias with Parallel Randomized and Nonrandomized Clinical Trials

J Clin Epidemiol Vol. 50, No. 7, pp. 823–828, 1997 Copyright  1997 Elsevier Science Inc.

0895-4356/97/$17.00 PII S0895-4356(97)00068-1

Assessing Non-Consent Bias with Parallel Randomized and Nonrandomized Clinical Trials Sue M. Marcus* Biostatistics Section, Division of Clinical Pharmacology, Jefferson Medical College, Philadelphia, Pennsylvania 19107 ABSTRACT. In some randomized clinical trials, a large proportion of patients eligible for randomization may withhold consent to be randomized. When the subjects in the randomized trial differ from the eligible population with respect to characteristics that are associated with the magnitude of the treatment effect, there may be nonconsent bias, i.e., the treatment effect for those in the randomized trial may not reflect the treatment effect for the eligible population. In response to this problem, some investigators have conducted, in addition to the randomized trial, a separate nonrandomized but otherwise identical trial consisting of those patients who are eligible for randomization, but instead choose their own treatment. Observed baseline covariate data can be used to adjust for differences between the randomized population and the eligible population when estimating the treatment effect for the eligible population. After adjusting, different outcomes for the randomized versus nonrandomized treated groups and/or the randomized versus nonrandomized control groups reflect the presence of hidden non-consent bias resulting from differences between the trial population and the eligible population with respect to unobserved covariates. A sensitivity analysis can display how hidden non-consent bias can account for an imbalance in the treatment groups with respect to an unobserved covariate. A parallel randomized and nonrandomized trial which compares adenoidectomy versus medical treatment for children with recurrent otitis media [Paradise et al. Efficacy of adenoidectomy for recurrent otitis media in children previously treated with tympanostomy-tube placement. J Am Med Assoc 1990; 263: 2066–2073] is used as an illustration. j clin epidemiol 50;7:823–828, 1997.  1997 Elsevier Science Inc. KEY WORDS. Clinical trials, observational studies, generalizability, covariance adjustment, bias, treatment effect, consent for randomization, sensitivity analysis

INTRODUCTION In some randomized clinical trials, a large proportion of patients eligible for randomization may have a preference for one treatment over the other and consequently may withhold consent to be randomized. This may occur when one treatment is more invasive or risky, but possibly more beneficial (e.g., surgery versus medical treatment). In the Coronary Artery Surgery Study (CASS) comparing coronary bypass surgery versus medical treatment, almost two-thirds of the 2099 patients meeting the eligibility criteria refused to be randomized [1]. It has been recognized in the clinical trials literature that low participation rates of the eligible population in the randomized trial can lead to a difference between the population that enters the randomized trial and the pool of eligible subjects [1–15]. Feinstein [14] cautions that ‘‘regardless of how well the comparison is conducted within the trial, the relatively small proportion of eligible *

Address for correspondence: Sue M. Marcus, Ph.D., Jefferson Medical College, Division of Clinical Pharmacology, Biostatistics Section, 125 S. 9th Street, Suite 403, Philadelphia, PA 19107. Accepted for publication on 8 April 1997.

patients under investigation may not represent the population for whom the results are intended.’’ For example, Ware [4] advised that many randomized trials for coronary artery disease (CAD) have low participation rates, so extrapolation to the underlying CAD patient population is limited. When the subjects in the randomized trial differ from the eligible population with respect to characteristics that are associated with the magnitude of the treatment effect, there may be non-consent bias, e.i., the treatment effect for those in the randomized trial may not reflect the treatment effect for the eligible population. Mitchell reported that in a randomized trial studying trinolol after myocardial infarction, those in the randomized trial were more severely ill than those not entered and consequently the trial results may be difficult to extrapolate to the population who met the eligibility criteria [2,3]. Generally, only those who are randomized are analyzed, since randomization assures, on average, equal distribution between the treated and control groups of prognostic factors affecting response. Nonetheless, it has been asserted in the clinical trials literature that the addition of a nonrandomized trial enhances generalizability of the results from the

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randomized trial population to the population of subjects who meet the eligibility requirements [1,2,8–13]. This paper clarifies the ways in which parallel randomized and nonrandomized clinical trials can provide useful information for assessing non-consent bias. The conclusions are justified by causal inference based upon mathematical foundations in the area of observational studies laid down by Cochran [16,17], Cochran and Rubin [18], Holland [19], Rubin [20–23], Rosenbaum and Rubin [24–27], and Rosenbaum [28,29]. The formal inference is technical and consequently has been placed in the appendix so it can be skipped without loss of continuity in reading the main body of the paper. A parallel randomized and nonrandomized trial that compares adenoidectomy versus medical treatment for children with recurrent otitis media [12] is used as an illustration. PARALLEL RANDOMIZED AND NON-RANDOMIZED CLINICAL TRIALS In parallel randomized and nonrandomized clinical trials, some patients who have met the eligibility requirements will give consent for randomization and will be randomized to treatment or control, while others will want to choose their own treatment. The latter group constitutes the nonrandomized ‘‘trial,’’ which differs from the randomized trial only in that these subjects have chosen their own treatment. Although the data from the randomized patients and those not randomized are kept separate, the randomized population combined with the nonrandomized population is a reflection of the population who meets the eligibility requirements. Both the baseline and outcome data from the nonrandomized trial provide valuable information for assessing non-consent bias. Observed baseline covariate data can be used to discover differences between the trial population and the eligible population that can be used to estimate the treatment effect for the eligible population. In addition, the outcome data can be used to test for the presence of hidden non-consent bias resulting from differences between the randomized population and the eligible population with respect to unobserved covariates. This will be described below. An example that will be discussed in this paper deals with data collected at the Children’s Hospital of Pittsburgh by Dr. Jack Paradise to study the efficacy of adenoidectomy versus medical treatment in 213 children previously treated with tympanostomy-tube placement because of persistent and/or recurrent otitis media who had again developed otitis media [12]. The analysis of the adenoidectomy data as an example for this paper was done solely with the intent of illustrating the statistical methodology for assessing nonconsent bias, so no clinical conclusions regarding the efficacy of adenoidectomy should be based on the work in this paper. (See [12] for a discussion of clinical recommendations regarding adenoidectomy versus medical treatment.) Of the 213 children who met the eligibility requirements

for this study, 99 had parental consent to be randomized and consequently were randomized to either the adenoidectomy group (n 5 52) or the control group (n 5 47). The remaining 114 children whose parents did not approve randomization were followed in a separate nonrandomized but otherwise identical trial where they were assigned adenoidectomy (n 5 47) or control (n 5 67) according to parental preference. The outcome used to illustrate the methodology in this paper is the number of weeks with otitis media for the first year in the trial, as calculated according to an algorithm based on the diagnoses at individual visits. OBSERVED GROUP DIFFERENCES If the randomized population is not representative of the eligible population, the estimate of the treatment effect derived from the randomized trial may not generalize to the eligible population, i.e., there may be non-consent bias. However, if the non-consent bias is overt, i.e., if imbalance in the treatment group composition can be attributed to a set of observed covariates x (e.g., severity of illness, age, etc.), it may be possible to adjust for x to compensate for the imbalance. This is standard epidemiological technique, but applied within the context of the parallel randomized and nonrandomized clinical trials where there may be differences between the nonrandomized treatment and control groups that can be adjusted for x (called strongly ignorable treatment assignment [24]) or differences between the randomized population and the eligible population that can be adjusted for x (strongly ignorable randomization consent). When the differences between the eligible population and the randomized population are the result of differences in x, the estimate of the treatment effect adjusted for x, which is derived from the randomized trial data will give an unbiased estimate of the treatment effect for the eligible population. (This follows from A1 in the appendix.) Similarly, if the differences between the eligible population and the randomized population and also between the nonrandomized treatment group and the nonrandomized control group can be attributed to differences in x, the estimate of the treatment effect adjusted for x, which is derived from both the randomized and nonrandomized data combined also gives an unbiased estimate of the treatment effect for the eligible population. (This is a consequence of A2 in the appendix.) Adjusting for observed group differences is illustrated with the adenoidectomy data. Table 1 gives descriptive statistics before adjustment for imbalance with respect to the four treatment groups. The unadjusted estimate of the treatment effect (the mean number of weeks for the treated minus the mean number of weeks for the controls) from the randomized trial was 23.60 ( p 5 0.04) with 95% CI: (27.13, 20.05) and from the nonrandomized trial was 22.22 ( p 5 .17) with 95% CI: (25.59, 1.17). Two covariates, race and the presence of persistent nasal

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TABLE 1. Weeks per year with otitis media by treatment

group Randomized

n Mean SD

Nonrandomized

Treated

Control

Treated

Control

52 10.18 8.43

47 13.78 9.17

46 11.19 7.23

67 13.41 9.78

obstruction, emerged as candidates for adjustment on the basis of their association with the outcome and differences between the randomized and nonrandomized populations and between the nonrandomized treated and nonrandomized control groups. (In the randomized trial, 10% were nonwhite, however 24% of the nonrandomized subjects were non-white. In addition, 82% of the nonrandomized control group had no persistent nasal obstruction versus 66% of the nonrandomized adenoidectomy group.) The estimate of the treatment effect for the eligible population, covariance-adjusted for race and persistent nasal obstruction using both the randomized and nonrandomized data was 23.05 (p 5 0.02) with 95% confidence interval (25.55, 25.55). The estimate using the randomized data only was 23.57 ( p 5 0.06) with 95% confidence interval (27.29, 0.15). The estimate using the nonrandomized data only was 22.56 ( p 5 0.15) with 95% confidence interval (24.88, 20.58). UNOBSERVED GROUP DIFFERENCES When the randomized population differs from the eligible population with respect to known covariates, adjustment can reduce non-consent bias, but hidden non-consent bias due to imbalances with respect to an unobserved covariate may remain. For example, the investigators of the adenoidectomy study reported that while the randomized trial showed the adenoidectomy to be effective, results in the nonrandomized trial ‘‘also generally favored adenoidectomy subjects but were less conclusive,’’ perhaps because the parents of the children less severely affected at baseline tended to choose the medical treatment [12]. Thus, there is the possibility of hidden non-consent bias, i.e., unobserved baseline differences in disease severity may explain differences in outcome for the randomized and nonrandomized adenoidectomy and medical treatment groups. The addition of the nonrandomized trial gives information that makes it possible to detect hidden non-consent bias. If the outcome for the randomized treatment group differs from that of the nonrandomized treatment group and/or the outcome for the randomized control group differs from that of the nonrandomized control group, after adjusting for the observed covariates x, then there is evidence of hidden non-consent bias due to a treatment group imbal-

ance with respect to an unobserved covariate. (This is a consequence of A3 in the Appendix.) In the adenoidectomy trial, the nonrandomized controls did slightly better than the randomized controls (13.41 versus 13.78 weeks with otitis media, on average), which is consistent with the speculation that the nonrandomized controls tended to be less severely affected at baseline. Furthermore, the nonrandomized treated subjects did slightly worse than the randomized treated subjects (11.19 versus 10.18 weeks with otitis media), which may reflect a tendency for those subjects who were more severely affected at baseline to choose the surgical treatment. Thus, there is a concern that the estimate of treatment effect derived from the randomized trial may (slightly) overestimate the effect of the treatment for the eligible population due to hidden non-consent bias. To test formally for evidence of hidden non-consent bias, analysis of covariance was used to compare outcomes for the randomized versus nonrandomized treatment groups (p 5 0.42) and for the randomized versus nonrandomized control groups (p 5 0.78) after adjusting for x. Thus, there is no evidence of significant hidden non-consent bias. SENSITIVITY TO HIDDEN NON-CONSENT BIAS When adjustment for the known covariates is not sufficient to remove all non-consent bias, adjustment for both the observed covariates and an unobserved covariate u might be sufficient to eliminate hidden non-consent bias. However, further adjustment is not possible, since the information about the unobserved covariate is unavailable. Nevertheless, it is possible to consider how much hidden non-consent bias could explain the differing outcomes in the four treatment groups (randomized treated, randomized control, nonrandomized treated, and nonrandomized control). Although the treatment effect for the randomized population may be significant after adjusting for observed baseline group differences, the treatment effect for the eligible population may not be significant due to unobserved differences between the randomized population and the eligible population. If a slight treatment group imbalance can lead to a change in the inference, then the study is highly sensitive to hidden non-consent bias. On the other hand, if a change in inference is consistent only with an extreme imbalance, then the study is insensitive to hidden non-consent bias. Methodology for assessing sensitivity to hidden bias in observational studies given by Marcus [30] can be used to evaluate the sensitivity of the conclusions of the randomized trial to hidden non-consent bias. Table 2 gives the results of this analysis for the adenoidectomy data, which assumes that treatment group imbalance is due to an unobserved binary covariate u that indicates whether the patient is severely ill at baseline. The first two columns of Table 2 give values that correspond to assumptions about the impact of the baseline severity of illness of

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TABLE 2. Sensitivity analysis for adenoidectomy study

Mean difference in outcome for severely ill versus not severely ill (weeks/year) 0.00 0.15 0.30 0.50 0.65 0.80

Mean difference in treatment effect severely ill versus not severely ill (weeks/year)

Non-consent bias (weeks/year)

p-Value

0.00 0.10 0.20 0.20 0.30 0.40

0.0 0.2 0.4 0.6 0.8 1.0

0.044 0.057 0.074 0.093 0.117 0.145

the outcome and treatment effect. Each scenario specified by the first two columns of Table 2 corresponds to an upper limit for the expected non-consent bias (third column of Table 2) and the p-value (derived from the randomized cohort) for significance of the treatment effect (fourth column of Table 2). The values in the first two columns were chosen so as to provide a range of p-values (from significant to nonsignificant). These values can be interpreted in two ways. One way is to consider a practical interpretation. For example, the impact of an additional week per year with otitis media can be conceived of in terms of suffering of the child, loss of work for parents, etc. Another way to assess the magnitude of these values is to measure them in terms of standard deviations of the outcome; for example, a change of 0.2, 0.5, and 0.8 standard deviations due to the unobserved covariate can be considered as small, moderate, or large impact, respectively. Since a full week per year is less than 0.2 standard deviation for the outcome, the column-one and column-two values, which are all fractions of a week, appear to be quite small. The analysis displayed in Table 2 suggests that the study is highly sensitive to non-consent bias, i.e., the estimate of the treatment effect changes from significant to non-significant even if the imbalance with respect to u has a neglible effect on the outcome or treatment effect, e.g., if adjustment for u changes the estimate of the outcome or the treatment effect by only a fraction of a week/year (a small amount relative to the standard deviation of the outcome). In summary, there does not appear to be much non-consent bias in the estimate of the treatment effect due to imbalance with respect to measured covariates. Moreover, there is no evidence of hidden non-consent bias. However, since this study is sensitive to small hidden non-consent bias, it is possible that the estimate of the treatment effect derived from the randomized trial slightly over-estimates the treatment effect for the eligible population if the parents of those children who were less severely affected at baseline refused randomization for their children. As pointed out by a reviewer, this ‘‘seems to be logical and indeed expected even without the sensitivity analysis.’’ The sensitivity anal-

ysis, however, is useful in quantifying the magnitude of hidden non-consent bias that is consistent with this conclusion. CONCLUDING ADVICE FOR THE INVESTIGATOR (1) If there is a concern that the those who enter the randomized trial may differ from the entire population who meet the eligibility requirements, the addition of the nonrandomized trial gives valuable information for assessing nonconsent bias. (2) It is worthwhile to collect baseline characteristics, even when it is not feasible to follow the nonrandomized group through the end of the trial. Baseline covariate data can be useful in detecting differences between those in the randomized trial and those who are eligible for the trial. (3) If the randomized versus nonrandomized treatment groups are similar at baseline, non-consent bias is less likely to be a threat. However, if the treatment groups differ before treatment, baseline covariates can be used to adjust for imbalances with respect to these characteristics. (4) Adjustment can be accomplished through the use of any of the methods of adjustment for observational studies [17]: covariance adjustment, direct adjustment by subclassification, and matching methods. (5) Covariates for adjustment may be chosen in several different ways. Possible candidates are those covariates that are highly correlated with the outcome, those covariates that differ between the randomized population and the nonrandomized population, covariates that differ between the nonrandomized treatment group and the nonrandomized control group, and covariates that are considered to be confounders on the basis of previous research. For a general discussion of choosing covariates in the analysis of clinical trials, see [31]. (6) When the unadjusted and adjusted treatment effect estimates are similar, non-consent bias may not be a problem. When they differ, this may be a sign of a treatment by covariate interaction, i.e., the effect of the treatment may be different for subjects with differing values of the covariate. Consequently, generalizability of the results from the randomized trial to other populations may be misleading. (7) Outcome data for the

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nonrandomized subjects can be used to test for hidden nonconsent bias. Any test that compares two groups adjusted for a set of covariates x can be used to check for differences between the randomized versus nonrandomized treatment groups and/or randomized versus nonrandomized control groups after adjusting for x. The choice of test depends upon the form of the outcome and the covariates x. For example, if the outcome is continuous, analysis of covariance is appropriate; when x is categorical, the Mantel-Haenszel test can be used for a categorical outcomes, the stratified logrank test can be used for survival data, and the stratified rank sum test can be used for continuous data. (8) A sensitivity analysis can give the range of inferences associated with varying amounts of non-consent bias. If a trial is insensitive to hidden non-consent bias, this gives further evidence that the adjusted estimate of the treatment effect generalizes to the eligible population. The author thanks Dr. Paul R. Rosenbaum, Dr. Walter W. Hauck, and the referees for helpful suggestions and is grateful to Dr. Jack L. Paradise for the use of the adenoidectomy data.

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14. 15.

16. 17. 18. 19. 20. 21. 22. 23.

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APPENDIX: CAUSAL INFERENCE For any individual in the trial population, let w 5 1 if the individual is randomized and w 5 0 if the individual is not randomized and let z 5 1 if the individual is in the treatment group and z 5 0 if the individual is in the control group. Each subject has two possible responses: the responses the subject would exhibit if given the treatment or the control. Denote the response that would have been observed if the subject had

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received the treatment by r 1 and the response that would have been observed if the patient had received the control by r 0 . The main objective is to estimate the mean treatment effect τ for the target population consisting of all subjects meeting the eligibility requirements, where τ 5 E(r 1 2 r 0 ). However, note that r 1 and r 0 cannot be observed for the same individual, i.e., the individual cannot receive both the treatment and the control. Both r 1 and r0 are random variables that theoretically have values for all patients in the target population, but the treatment response r 1 is observed for only those subjects in the trial population who receive the treatment and the control response r 0 is observed for only those subjects in the trial population who receive the control. Suppose that each subject has a vector x of observed baseline measurements. It is possible to estimate the regression of r 1 on x in the treated group E(r 1 |z 5 1, x), and the regression of r 0 on x in the controls, E(r0 | z 5 0, x); however E(r 1 |z 5 1, x) 2 E(r 0 |z 5 0, x) is not generally equal to the treatment effect at x, E(r 1 2 r0 | x) since those who receive the treatment may differ from those who receive the control, even after adjusting for x. Rosenbaum and Rubin [24] define treatment assignment to be strongly ignorable when (r1 , r 0 ) ⊥ z | x, where A ⊥ B |C is Dawid’s [31] notation for ‘‘A and B are conditionally independent given C.’’ Note that this condition holds for randomized trials, but not necessarily for nonrandomized trials. In this spirit, define a trial to have strongly ignorable randomization consent if (r1 , r 0 ) ⊥ w | x.

Then the following propositions follow from elementary properties of conditional independence [32]. A1: A trial has strongly ignorable randomization consent if and only if E(r 1 | w 5 1, z 5 1, x) 2 E(r 0 |w 5 1, z 5 0, x) 5 E(r1 2 r 0 |x) 5 τ (x). A1 says that strongly ignorable randomization consent corresponds to the situation where the estimate of the treatment effect using the randomized data will be an unbiased estimate of the treatment effect for the eligible population, after adjusting for x. A2: A trial has strongly ignorable randomization consent and strongly ignorable treatment assignment if and only if E(r 1 | z 5 1, x) 2 E(r 0 | z 5 0, x) 5 E(r 1 2 r 0 | x) 5 τ (x). A2 says that strongly ignorable randomization consent plus strongly ignorable treatment assignment correspond to the situation where the estimate of the treatment effect using both the randomized and nonrandomized data will be an unbiased estimate of the treatment effect for the eligible population, after adjusting for x. A3: If a trial has strongly ignorable randomization consent and strongly ignorable treatment assignment, then r 1 ⊥ w | z 5 1, x and r0 ⊥ w |z 5 0, x A3 says that if adjusting for x is sufficient to remove all nonconsent bias, then randomization consent and the outcome will be independent for the treated subjects and randomization consent and the outcome will be independent for the control subjects.