Pregnancy and HIV disease progression: methodological concerns.

To the Editor—We thank Tai et al. [1] for their recent article in the Journal. We read the article with great interest. The authors noted a substantial reduction in the risk of AIDS or AIDS-related death associated with pregnancy among HIV-positive women attending clinics in Tennessee. Although we recognize the substantial effort expended to control for confounding in this study, several methodologic issues urge caution in interpreting the otherwise welcome findings of these authors. First, we are troubled by the definition and classification of exposure in this study. In these analyses, all person-time contributed by a woman who became pregnant at any point during follow-up— including person-time contributed both before and after the period of actual pregnancy—was considered to be time exposed. As a result, “exposed” person-time is, in fact, a mix of exposed and unexposed person-time. Furthermore, the unexposed person-time included as “exposed” time is in fact “immortal persontime,” because these “exposed” women are necessarily alive and free of disease progression until the beginning of pregnancy. Although the authors note this latter concern in their discussion, and although this misclassification should not influence analyses in which follow-up began after pregnancy, other analyses may well have been affected. An additional concern is the authors’ decision to designate CD4 lymphocyte counts obtained up to 365 days after the initial clinic visit as “baseline” measurements. CD4 lymphocyte counts can change dramatically within a year of follow-up, depending on whether or not individuals are receiving antiretroviral therapy (ART); therefore, such counts are a potentially inaccurate measurement of the true CD4 lymphocyte count at baseline. An analytic approach that could help to address both of these concerns is to allow exposure and the CD4 lymphocyte count, as well as other key confounders, to vary throughout follow-up. Because the CD4 lymphocyte count and other confounders (including ART received) may vary with time, exposure, and each other, the use of marginal structural models (MSMs) may be necessary to obtain an unbiased estimate of effect. Regardless of whether MSMs are required, controlling for time-varying exposure and confounders may yield dramatically different results. For example, in a study analogous to that of Tai et al. [1], Hernan et al. [2] reported rate ratios of 2.3 (1.9 –2.8) in a model controlling only for baseline confounders, but they reported rate ratios of 0.4 (0.3– 0.5) in a model accounting for time-dependent confounding and 0.7 (0.6 –1.0) in the appropriate MSM. We also are concerned about the inclusion criteria used for the study. Given the authors’ focus on the highly active antiretroviral therapy (HAART) era, it is not immediately clear why 75 women who received non-HAART ART and 144 nonpregnant women (23% of that population) who received no ART at all were included in the analysis. The beneficial effect of HAART with regard to prevention of AIDS events and death is well established; differences between the 2 populations may therefore be partly attributable to differences in ART received rather than to any effects of pregnancy. A related issue is that the women who became pregnant and the women who did not become pregnant are different enough that they are not interchangeable—that is, comparisons between them cannot form the basis for valid causal inference. Table 1 in the article by Tai et al. [1] shows large, presumably clinically significant differences between the 2 groups with regard to a number of key variables known to affect time to development of AIDS; these variables include receipt of ART (see above), subject age (median age, 25 years for pregnant women vs. 36 years for nonpregnant women), and CD4 lymphocyte count (median count, 450 cells/mm3 for pregnant women vs. 352 cells/mm3 for nonpregnant women). Similarly, in the matched analysis, only 81 (58%) of pregnant women were successfully matched to a nonpregnant woman, despite a wide CD4 matching range ( 100 cells/mm3), again suggesting limited exchangeability between the groups. It would be helpful, given the inclusion of a propensity score analysis in their report, if the authors could provide the propensity score histograms for the 2 study groups. In a qualitative sense, if these curves overlap substantially, then there is some evidence for exchangeability between pregnant and nonpregnant women; if the curves do not overlap, then the basis for counterfactual inference is more questionable. We believe that the aforementioned concerns urge caution in the interpretation of the important findings of Tai and colleagues. However, we wish to emphasize that we are advocating skepticism, not cynicism; the remarkable consistency seen across subanalyses in this study urges deeper investigation of these issues.