OBJECTIVES: To consider methods and related evidence for evaluating bias in non-randomised intervention studies. DATA SOURCES: Systematic reviews and methodological papers were identified from a search of electronic databases; handsearches of key medical journals and contact with experts working in the field. New empirical studies were conducted using data from two large randomised clinical trials. METHODS: Three systematic reviews and new empirical investigations were conducted. The reviews considered, in regard to non-randomised studies, (1) the existing evidence of bias, (2) the content of quality assessment tools, (3) the ways that study quality has been assessed and addressed. (4) The empirical investigations were conducted generating non-randomised studies from two large, multicentre randomised controlled trials (RCTs) and selectively resampling trial participants according to allocated treatment, centre and period. RESULTS: In the systematic reviews, eight studies compared results of randomised and non-randomised studies across multiple interventions using meta-epidemiological techniques. A total of 194 tools were identified that could be or had been used to assess non-randomised studies. Sixty tools covered at least five of six pre-specified internal validity domains. Fourteen tools covered three of four core items of particular importance for non-randomised studies. Six tools were thought suitable for use in systematic reviews. Of 511 systematic reviews that included non-randomised studies, only 169 (33%) assessed study quality. Sixty-nine reviews investigated the impact of quality on study results in a quantitative manner. The new empirical studies estimated the bias associated with non-random allocation and found that the bias could lead to consistent over- or underestimations of treatment effects, also the bias increased variation in results for both historical and concurrent controls, owing to haphazard differences in case-mix between groups. The biases were large enough to lead studies falsely to conclude significant findings of benefit or harm. Four strategies for case-mix adjustment were evaluated: none adequately adjusted for bias in historically and concurrently controlled studies. Logistic regression on average increased bias. Propensity score methods performed better, but were not satisfactory in most situations. Detailed investigation revealed that adequate adjustment can only be achieved in the unrealistic situation when selection depends on a single factor. CONCLUSIONS: Results of non-randomised studies sometimes, but not always, differ from results of randomised studies of the same intervention. Non-randomised studies may still give seriously misleading results when treated and control groups appear similar in key prognostic factors. Standard methods of case-mix adjustment do not guarantee removal of bias. Residual confounding may be high even when good prognostic data are available, and in some situations adjusted results may appear more biased than unadjusted results. Although many quality assessment tools exist and have been used for appraising non-randomised studies, most omit key quality domains. Healthcare policies based upon non-randomised studies or systematic reviews of non-randomised studies may need re-evaluation if the uncertainty in the true evidence base was not fully appreciated when policies were made. The inability of case-mix adjustment methods to compensate for selection bias and our inability to identify non-randomised studies that are free of selection bias indicate that non-randomised studies should only be undertaken when RCTs are infeasible or unethical. Recommendations for further research include: applying the resampling methodology in other clinical areas to ascertain whether the biases described are typical; developing or refining existing quality assessment tools for non-randomised studies; investigating how quality assessments of non-randomised studies can be incorporated into reviews and the implications of individual quality features for interpretation of a review's results; examination of the reasons for the apparent failure of case-mix adjustment methods; and further evaluation of the role of the propensity score.

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Evaluating non-randomised intervention studies.

The Analysis of Variance.

In biomedical research, a common question posed by investigators is whether or not an outcome of interest differs significantly between multiple independent groups of subjects in the study sample. For example, in a randomized clinical trial focusing on differences in a parameter of cardiovascular health such as systolic blood pressure or heart rate that is measured on a continuum, one might make the comparison of those who received a placebo, those who received a particular active drug, and those who received a different active drug. Another example of a multiple group comparison might arise in an observational study when comparisons between categories of race or ethnicity are of interest. The statistical problem that arises from the use of multiple comparisons tests is that any subsequent tests of hypotheses will be performed on the outcome with the same data on which the global test was performed. This can result in an uncontrolled type I error rate (the rate of rejecting the null hypothesis when it should not be rejected). These tests can produce this statistical problem, which can be encountered in analyses of multiple treatment or exposure groups, multiple end points, or multiple interim analyses. This problem has been addressed from a broad perspective.1 The present report, however, will focus on the statistical analysis strategies used when the global or omnibus test of differences on a continuous outcome across the multiple groups has been performed and statistical tests contrasting subgroups are then conducted. It serves as a follow-up to an earlier article 2 in the series of statistical tutorials in Circulation that addressed the use of the ANOVA in performing the global test of hypothesis for a continuous outcome. These statistical tests are often referred to as multiple comparisons procedures (MCPs). We will first present a brief review of the statistical foundations of 1-factor ANOVA and then will describe the 2 main types of MCPs with specific reference to the more commonly used MCPs. Finally, we will show a worked example of an analysis of data from a study of heart size in animals exposed to different conditions of physical exercise that will illustrate the use of 1-factor ANOVA with supplementary MCPs. Review of 1-Factor ANOVA

Multiple Comparisons Procedures

THE RANDOMIZED CLINICAL TRIAL (RCT) IS THE ideal method for measuring treatment effects. Participants in clinical trials are randomly assigned to a treatment or control group. Randomization reduces biases by making treatment and control groups “equal with respect to all features,” except the treatment assignment. When randomization is performed correctly, differences in efficacy found by statistical comparisons can be attributed to the difference between the treatment and control. However, the RCT does not necessarily provide the final answer to treatment effectiveness, as there are many restrictions that limit generalizability. For example, RCTs are often restricted to patients with limited disease, comorbidity, and concomitant medications. Thus, RCTs generally demonstrate efficacy rather than effectiveness, where efficacy is the treatment effect under the restricted conditions of the RCT and effectiveness is the treatment effect under the conditions of usual practice. Observational, nonrandomized studies have a role when RCTs are not available, and, even when RCTs are available, to quantify effectiveness and other real world experiences. A contemporary example of this is the evaluation of drugeluting stents, for which RCTs have demonstrated shortterm efficacy for relatively healthy patients and observational studies are beginning to address long-term effectiveness and safety problems and use of clopidogrel in a broader array of patients. There are many approaches for making statistical inferences from observational data. Some approaches focus on study design, others on statistical techniques. However, even with the best of designs, observational studies, unlike the RCTs, do not automatically control for selection biases. Therefore, statistical methods involving matching, stratification, and/or covariance adjustment are needed. Lack of randomization in observational studies may result in large differences on the observed (and unobserved) participant characteristics between the treatment and control groups. These differences can lead to biased estimates of treatment effects. The goal of the statistical techniques that focus on observational data is to create an analysis that resembles what would occur had the treatment been randomly assigned. In RCTs, the balance is achieved on participant characteristics that occur before the treatment is administered. The success of randomization in creating balance can be assessed before any outcome measurements are taken. Therefore, in observational studies, the first goal of a statistical technique is to create balance between treatments on characteristics that are assessed before the actual treatment is administered. Once this balance has been achieved, outcome measurements can be ascertained and compared between groups. In practice, this goal is often difficult to achieve because the data available for observational studies usually contain measured patient characteristics that are obtained before, during, and after treatment administration, and it is often difficult to determine exactly which patient characteristics are pretreatment or not. Furthermore, there frequently are unmeasured characteristics that are not available, inadequately measured, or unknown. Thus, the statistical methods in observational studies need first to be judged based on their performance in creating a balance on background characteristics between treated and control groups and the impact of outcome data should play no role in this assessment. To adjust for pretreatment imbalances, 2 statistical approaches often used are analysis of covariance methods and propensity score methods. These 2 methods complement each other and generally should be used together rather than choosing between one or the other. Analysis of covariance refers here to standard statistical analyses that produce estimates of treatment effects adjusted for background characteristics (covariates), which are included explicitly in a statistical (regression) model. With observational studies, this technique can produce biased estimates of treatment effects if there is extreme imbalance of the background characteristics and/or the treatment effect

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Estimating treatment effects using observational data.

Existing obesity therapies are limited by safety concerns and modest efficacy reflecting a weight loss plateau. Here, we explore combination therapy with bupropion (BUP), a putative stimulator of melanocortin pathways, and an opioid antagonist, naltrexone (NAL), to antagonize an inhibitory feedback loop that limits sustained weight reduction. In vitro electrophysiologic experiments were conducted to determine the extent to which BUP+NAL stimulated hypothalamic pro-opiomelanocortin (POMC) neurons in mouse brain. A subsequent study further characterized the effect of combination BUP+NAL treatment on food intake in lean and obese mice. Finally, a randomized, blinded, placebo-controlled trial in obese adult subjects was conducted. Randomization included: BUP (300 mg) + NAL (50 mg), BUP (300 mg) + placebo (P), NAL (50 mg) + P or P+P for up to 24 weeks. BUP+NAL stimulated murine POMC neurons in vitro and caused a greater reduction in acute food intake than either monotherapy, an effect consistent with synergism. Combined BUP+NAL provided sustained weight loss without evidence of an efficacy plateau through 24 weeks of treatment. BUP+NAL completers diverged from NAL+P (P < 0.01) and P+P (P < 0.001) at week 16 and from BUP+P by week 24 (P < 0.05). The combination was also well tolerated. Translational studies indicated that BUP+NAL therapy produced synergistic weight loss which exceeded either BUP or NAL alone. These results supported the hypothesis that NAL, through blockade of β-endorphin mediated POMC autoinhibition, prevents the classic weight loss plateau observed with monotherapies such as BUP. This novel treatment approach (BUP+NAL) holds promise for the treatment of obesity.

Rational Design of a Combination Medication for the Treatment of Obesity

In many clinical trials there are multiple treatments under consideration which require multiple comparisons. Investigators are faced with the problems of Type I error control (experimentwise, familywise, or comparisonwise), maintenance of reasonable power for the study, and the selection of appropriate multiple comparison techniques to achieve these. This paper reviews briefly the various multiple comparison techniques available and discusses strategies for aiding investigators in applying these in settings typical in clinical trials (eg, confirmatory studies with placebo or positive controls or both). In a confirmatory setting, the treatment comparisons can often be divided into sets or families. Appropriate multiple comparison techniques, possibly differing across families, can then be applied within and across these. Study objectives can be better achieved by employing the strategies suggested.

Strategies for Dealing with Multiple Treatment Comparisons in Confirmatory Clinical Trials

Randomized controlled trials or studies are often considered the ideal way to evaluate the effectiveness of a treatment compared to a control. In such a study, the randomization procedure ensures that the subjects receiving the treatment and control are equal with respect to all conditions except for receiving the treatment or the control. Differences found by statistical comparisons of the results of such a study can be attributed to the effect of the treatment or how much the treatment differs from the control when all other things are held constant. Randomized controlled trials are not always possible, and even when possible they are often performed with such restrictions that they do not provide the true measure of the effectiveness of the treatment in the "real world" or under "conditions of usual practice." This article reviews the use of nonrandomized studies to measure effectiveness when a randomized control group is not available. Various types of nonrandomized studies are reviewed, along with their advantages and disadvantages. Often, these studies require statistical adjustments such as matching or covariance analysis to adjust for inequalities or to remove biases between the treatment and control groups; these are reviewed as well.

Measuring effectiveness. What to expect without a randomized control group.

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Strategies for Dealing with Multiple Treatment Comparisons in Confirmatory Clinical Trials

Measuring effectiveness. What to expect without a randomized control group.