In a recent issue of AIDS, Denneman et al.  report longitudinal weight-for-age and length-for-age z-scores of HIV-exposed children by tenofovir (TDF) exposure status. Although data on the long-term effects of antiretroviral (ARV) exposure in utero are critical at this time of rapid global expansion of HIV treatment, disentangling the effects of perinatal exposures on child health is methodologically fraught [2,3]. In turn, we are concerned that several issues from the abovementioned report require careful consideration.
First, in this retrospective study, ARV exposures appear to have been highly heterogeneous. Nonetheless, Denneman et al.  provide limited information regarding drug combinations used in the non-TDF-exposed group and no information on those combined with TDF among the children comprising the TDF-exposed group. In particular, the lack of clarity on concurrent use of boosted protease inhibitors is a major limitation. Recent data from the IMPAACT-PROMISE P1084s substudy have raised concerns regarding the specific effect of protease inhibitor exposure on infant bone health, rather than TDF . In the current analysis, the majority of TDF-exposed children appear to have been born preterm, although the exact number is not provided. Premature delivery is more commonly associated with the use of protease inhibitors than TDF [5,6]. Ideally, TDF growth associations should be stratified by use of protease inhibitor, although the unusually small sample size (TDF-exposed group n = 9) might preclude this.
Second, Denneman et al.  appear to have used WHO Child Growth Standards for all infants irrespective of gestation at birth . This introduces a substantial risk of outcome misclassification, which would not be fully addressed by the approach of adjusting for prematurity in the regression model. Even appropriate for gestational age (AGA), preterm infants display growth patterns that are different to those of term AGA infants . Postnatal preterm growth standards generated by the INTERGROWTH-21st project have recently been released, and are recommended for use until at least 64 weeks’ postmenstrual age ; after this, the IG21-preterm postnatal and WHO growth references converge . Indeed, the ‘catch-up’ growth depicted among the TDF-exposed children in the figure (with z-scores converging toward 12 months of age in the figure) appears strikingly similar to the rapid postnatal ‘catch-up’ growth of preterm infants generally .
Third, the analysis may not have adequately addressed the substantial risks of confounding in this context, with potentially inappropriate adjustments in the regression model. ARV prescribing patterns change frequently over time, and with the shorter follow-up time demonstrated for the TDF-exposed group (the figure implies 20 months compared with 40 months in the non-TDF exposed group), the question arises as to whether the TDF-group represent a more recent cohort. Yet no information is provided on time periods or indications for regimen with no apparent attempt to adjust for potential confounding by indication . Denneman et al.  do adjust for other variables, including low birth weight (LBW) and preterm delivery. LBW is a heterogeneous construct, which incorporates small-for-gestational age term and preterm infants as well as appropriate AGA preterm infants . LBW as a variable is therefore likely to be highly collinear with preterm delivery; if adjustment for a binary classification of birth weight is necessary, small for gestational should be used in conjunction with gestational age, in keeping with international trends . However, in this specific analysis, it is questionable if any adjustment for birth weight and gestational age was appropriate as both are potential intermediates on the causal pathway between TDF exposure and infant growth . Given that the research question relates to the overall effects of TDF on growth and not only the direct effects, stratification by birthweight and gestational age is unnecessary. More importantly, conditioning on (adjusting for) an intermediate can introduce substantial bias and even lead to paradoxical results, as has been extensively demonstrated in the well known ‘birth weight paradox’ where maternal smoking can appear protective among infants with LBW .
Taken together, we feel these methodological concerns indicate that the conclusions of Denneman et al.  may be viewed with special caution. Investigating the potential risks associated with early life exposure to different ARV agents is crucial, but attributing causality in studying perinatal exposures is complex. In turn, we recommend specific methodological rigor before attributing adverse consequences to any particular ARV agent.
Research supported by PEPFAR through NICHD under Cooperative Agreement 1R01HD074558, the Elizabeth Glaser Pediatric AIDS Foundation, South African Medical Research Council, the Fogarty Foundation (NIH Fogarty International Center Grant #5R25TW009340), and the Office of AIDS Research. J.J. is supported by NICHD K23HD070760.
Conflicts of interest
There are no conflicts of interest.
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