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To the Editor: The article by Zenilman et al1 found that self-reported condom use was not associated with the incidence of sexually transmitted diseases (STD) in a high-risk Baltimore cohort. Their design and analysis, however, have important limitations that may affect their findings. Type of STD The validity of self-reported condom use can best be assessed if the STD outcome is closely tied to unprotected coitus. Gonorrhea is probably the most sensitive and rapidly responsive marker for unprotected sex.2 Consequently, a study that used gonorrhea as an outcome measure would be more convincing than one that considered a variety of diseases for which condoms may have different protective effects. When we assessed the association between prospectively recorded condom use and incident gonorrhea in a cohort in Cameroon,3 the level of self-reported use was closely and directly related to the risk of gonorrhea. Loss to Follow-up Bias from selective loss to follow-up can plague any prospective study. The authors do not describe features of the full cohort at enrollment, but only summarize the characteristics of those participants who returned for a follow-up visit. Although the authors state that those who returned were not significantly different from those who did not return, the data are not presented. People who do not return for follow-up visits may differ in important ways from people who return.4 Because 48% of those enrolled in this study did not return, a more complete evaluation of selection bias could compare those who returned for follow-up and those who did not. At a minimum, a comparison of prevalent STD and condom use at baseline would be helpful. Timing of Outcome and Exposure In this study, the time periods for disease incidence (from enrollment until follow-up 3 months later) and exposure (30 days before follow-up) were not the same. If an individual became infected with an undetected STD anytime after enrollment and before the beginning of the 30 days for which information on condom use was obtained, an interval that averaged 3.4 months (average duration between enrollment and follow-up was 4.4 months), she/he would be misclassified in terms of the timing of incident STD. Given that the exposure period of interest was the 30 days before the clinic visit, the participants might have been asked to return in 30 days, making the time periods equivalent. Misclassification of Outcome Although it is unlikely that incident disease was grossly misclassified, it does not have to be extreme for the odds ratios to be biased.4 To gauge the level of misclassification of disease, the authors might report how many men and women with STD at baseline did not return for treatment and were potentially still infected during follow-up, report how many of those who returned for treatment received the entire treatment, report how many at follow-up had asymptomatic infection, and test whether results changed when those with STD at baseline were dropped from the analysis. None of these approaches would provide a gold standard, but together they would provide some reassurance. Misclassification of Exposure Condom use was assessed retrospectively which, as acknowledged by the authors, opens the measure to a variety of errors. Evidence suggests—and intuition supports—that prospective recording of sexual activity using coital logs is more accurate.5 Analytic Approach In the regression models used, adding more variables generally improves prediction, but they should not include covariates that are merely correlated with the exposure.4 Specifically, STD status at baseline, which was correlated with condom use at baseline, should have been excluded if people who used condoms at baseline were also more likely to use condoms during follow-up. If this is true, then STD status at baseline could be a proxy for condom use during follow-up, and the effect of follow-up condom use in the model may be reflected in the baseline STD status variable and the condom variable. The factor for STD status at baseline had the highest odds ratio (3.1) of any variable in the model; the effect of condom use may have been different if that variable were excluded. Instead of a “kitchen-sink” approach in which all possible and interesting risk factors for human immunodeficiency virus are included as covariates, a more parsimonious predictive model including only demonstrated risk factors and confounders of the relationship between condom use and the outcome variable would be helpful. The odds ratio for condom use in the model estimates the relative risk of infection after all other variables are controlled, and the amount of variance left to be explained after controlling these risk factors for STD is not likely to be appreciable. If the number of covariates were reduced, more than three strata of condom use could be included in the model. The trichotomization used (always, sometimes, never) does not reflect the true variability in condom use; the second category could range from 1–99% condom use, and is likely to hide any dose-response effects evident in the exposure. More accurate data from a coital log would allow finer stratification of condom exposure, or better yet, a continuous variable, leading to a more accurate assessment of STD risk according to level of condom use. Conclusion Given the limitations cited, we are not surprised the authors found no association between self-reported condom use and incident STD. With the probable misclassification of exposure and outcome, their measures were stacked in favor of the null hypothesis. Most studies, often with better measures of condom use, have found that condoms provide substantial protection against incident STD.3,6–11
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Weir et al. (1996) studied this question.
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