The use of antilymphocyte antibodies also has disadvantages. These agents may induce an antibody response against the host, which can limit their use to a single course of therapy. They also cause profound immunosuppression that may unleash deadly viral infections or virus-associated lymphomas. The cost of antilymphocyte antibody treatment (several thousand dollars per course) adds substantially to the overall cost of renal transplantation. Thus, the optimal use of antilymphocyte antibodies in renal transplantation is not established, and practice varies considerably among transplantation centers.

Some centers use antilymphocyte antibodies only to treat acute rejection; others use induction therapy in all patients. Still others use induction therapy only in patients at high risk for acute rejection and treat acute rejection as needed in the remaining patients. To clarify the efficacy of induction therapy, Szczech and colleagues [7, 8] have published two articles, one of which appears in this issue. In each of these papers, the authors report results obtained with a different type of meta-analysis used to combine results from randomized, controlled trials. It is worthwhile to compare the methods used in these two studies and to contrast their results.

The first of the two papers [7] used meta-analysis of aggregate (summary) data from published reports of seven randomized, controlled trials that included a total of 794 patients. This analysis examined a categorical outcome (graft loss versus survival) at 2 years of follow-up and assessed treatment effect as the odds ratio for graft loss in the induction therapy group compared with the control group. Odds ratios ranged from 0.50 to 1.57 in the individual studies, and the therapeutic efficacy of antilymphocyte antibody was not statistically significant in any single study. In contrast, the pooled odds ratio was 0.66 (95% CI, 0.45 to 0.96; P = 0.03), indicating a statistically significant beneficial effect across the combined studies. The authors could assess neither therapeutic benefit beyond 2 years nor whether benefit was greater in high-risk patients.

The second paper used meta-analysis of individual patient (primary) data provided by the original investigations on 628 patients from five of seven randomized trials [8]. Two investigators also provided additional follow-up data on patient and graft survival. By assembling individual patient data, Szczech and colleagues gained enough information to estimate 5-year graft survival curves and estimate the effects of different patient characteristics on treatment effect (treatment interactions). The primary analysis used time to graft loss as the outcome and assessed the treatment effect by using the hazard rate ratio for graft loss in a proportional hazards regression analysis. The overall rate ratio over 5 years was 0.82 in the induction therapy group (CI, 0.62 to 1.09; P = 0.17), suggesting that initial induction therapy was not effective over the longer term. In additional analyses, Szczech and colleagues reported a significant benefit of induction therapy on graft survival in the first 2 years of follow-up but not in the interval from 2 to 5 years of follow-up. They also reported that benefit was stronger in presensitized patients (a high-risk group, defined below) than in patients who were not presensitized. This information gives a more detailed picture of the effect of induction therapy than did the information in the first article. What are the methodologic differences between the two studies? What are the advantages of meta-analysis of individual patient data? And what are the clinical implications?

The opportunity to collect additional follow-up data from clinical trials is widely accepted as a rationale for meta-analysis done by using individual patient data [9-11]. Often, data collection continues after the original study period has ended to determine long-term safety and efficacy. If meta-analysis makes it possible to assess a definitive "hard" end point (such as graft loss) over the long term where individual trials have measured a surrogate "soft" outcome (such as acute rejection) in the short term, additional follow-up is vital to obtain outcomes sufficient for a clinically meaningful analysis. With individual patient data, the availability of event times makes it possible to estimate survival curves, providing a continuous view of how risk changes over time. If the hazard rates are proportional over time, it is appropriate to describe a single treatment effect over the entire duration of follow-up. If hazard rates are not proportional, however, then the period of follow-up must be divided into intervals in which the assumption of proportional hazards is satisfied. Survival analysis must then be performed in each interval separately, and treatment effects must be ascribed to different periods of follow-up.

In the meta-analysis by Szczech and colleagues that used individual patient data, the benefit of induction therapy seemed to change during follow-up. The overall data did not satisfy the assumption of proportional hazards, and the authors therefore used separate models for the two intervals. Consistent with the findings of the meta-analysis of group data [7], a significant beneficial effect of anti-lymphocyte antibody was seen in the first 2 years but not in the interval from 2 to 5 years. Szczech and colleagues concluded that the benefit of induction therapy is strongest during the first 2 years after renal transplantation and wanes after 2 years.

The opportunity to assess treatment interactions is less often recognized as a reason to conduct meta-analyses with individual patient data. Treatment interactions occur when treatments are more effective in one group of patients than in another. The appropriate analysis with which to detect an interaction is a regression analysis that includes terms for the treatment effect, the patient characteristic, and the interaction. Significance of the interaction term is evidence that the treatment effect is different in patients with certain distinguishing characteristics. If an interaction is detected, it can be illustrated by comparing the randomized groups separately in subgroups of patients with and without the characteristic. Many researchers mistakenly search for interactions by searching for significance in subgroup comparisons. This approach can be dangerous because it leads to multiple tests of the same hypothesis and thus to a higher likelihood of a false-positive finding [12]. If an interaction is detected, reporting a single treatment effect for the entire patient population is inappropriate. The magnitude of the treatment effect measured across the entire patient population simply reflects the proportion of patients with and without the characteristic.

More generally, an interaction indicates that treatment effect is related to the presence of a particular characteristic or risk factor in the entire study population. This is not to be confused with confounding, which indicates that the measured treatment effect is biased by unequal distribution of risk factors among the treatment groups. Confounding occurs when a risk factor is correlated with the outcome and is not balanced between the treatment groups. In a randomized trial (and therefore in a meta-analysis of randomized trials), treatment effects typically are not confounded with other factors because randomization distributes risk factors similarly in the treatment groups. But interactions can and do occur in well-balanced, randomized groups and should be explored.

One way to detect treatment interactions in meta-analyses of group data is with a technique called meta-regression analysis, in which the treatment effect in each study is related to an aggregate measure of the risk factors in that study. The slope coefficient in such a regression is the measure of the interaction. However, this approach has sufficient statistical power only if variation in the aggregate measure of the risk factor across studies is large and the total number of studies in the meta-analysis is large. Furthermore, meta-regression evaluates only factors that vary among studies. Evaluating the effect of factors that vary among patients within a study requires individual patient data. Using aggregate measures of risk factors to approximate variation among patients may be misleading because adverse outcomes are often highly concentrated in high-risk patients whose distribution cannot be determined from aggregate measures; this leads to an effect known as ecological bias [13, 14].

In their individual patient-data meta-analysis, Szczech and colleagues detected a significant interaction of induction therapy with presensitization. Presensitization refers to the presence of antibodies against human lymphocytes in the recipient before transplantation and has long been considered a risk factor for graft loss. In this study, presensitization was defined as panel reactivity greater than 20% (recipient antilymphocyte antibodies to more than 20% of a panel of blood donors). In the meta-analysis, the benefit of induction therapy was greater in presensitized patients than in patients who were not presensitized. The clinical implication of this interaction is that treatment recommendations for anti-lymphocyte antibody induction therapy should take into account the patient's panel reactive antibody level. Because no other significant interactions were detected, it might be reasonable to conclude that presensitized patients should receive induction therapy and other patients should not. It was not possible to detect this interaction through meta-regression analysis because panel reactivity levels were not consistently reported across studies and because the statistical power for these analyses, with only seven clinical trials, would have been low.

Individual patient-data meta-analysis of antilymphocyte antibody induction therapy therefore has shown two important findings that were not detected in the meta-analysis of group data: The beneficial effect of this therapy seems to be greater during the first 2 years of follow-up, and presensitized patients benefit more than patients who are not presensitized. These findings, together with information about risks and costs, could be used to develop clinical guidelines for the use of induction therapy in renal transplantation.

Individual patient-data meta-analysis has drawbacks, too. External validity can be compromised if patients in all of the clinical trials are not included. The individual patient-data meta-analysis of induction therapy by Szczech and colleagues included data on only five of the seven trials from the meta-analysis of group data. The authors carefully compared results from the two unavailable studies with those from the five available ones and found no important differences. Such sensitivity analysis is crucial; although publication bias is always a threat to the validity of meta-analysis, retrieval bias is an additional danger when individual data are used. In addition, individual patient-data meta-analysis can be expensive, sometimes requiring several investigators, 2 or 3 years, and tens to hundreds of thousands of dollars to complete. These barriers make this technique affordable only for the handful of clinical problems that merit the investment of such resources. Consequently, we believe that protocols and computer programs to simplify methods for conversion and combining of clinical trials data are needed [15]. The front-end work required to create such programs would be substantial, but the availability of these programs would permit the distillation of important additional meaning now "locked up" in hard-earned clinical trials data and, ultimately, would increase our ability to translate clinical trial results into practice.