# Response to correspondence on ‘Should Biomarker Estimates of HIV Incidence be Adjusted?’

doi: 10.1097/QAD.0b013e32832f3dbb

Correspondance

^{a}Department of Biostatistics, Johns Hopkins Bloomberg School of Public Health, Baltimore, Maryland, USA

^{b}Woodrow Wilson School of Public and International Affairs, Princeton University, Princeton, New Jersey, USA.

Received 14 April, 2009

Revised 2 June, 2009

Accepted 9 June, 2009

Correspondence to Ron Brookmeyer, PhD, Department of Biostatistics, Johns Hopkins Bloomberg School of Public Health, 615 N. Wolfe Street, Baltimore, MD 21205, USA. Tel: +1 410 955 3519; e-mail: rbrook@jhsph.edu

I thank Doctors Hargrove, McDougal, Welte, McWalter and Barnighausen for their perspectives on methods to improve HIV incidence estimation.

Dr Hargrove asserts that his HIV incidence adjustment procedure must be correct because it makes the biomarker incidence estimate match the ZVITAMBO cohort incidence estimate. The ZVITAMBO cohort is estimating HIV incidence strictly during the postpartum period because the ZVITAMBO mothers were recruited within 96 h of delivery and followed forward in time. We have previously shown that if there are time trends in HIV incidence, then the cross-sectional biomarker approach estimates a time weighted average of incidence prior to the point serum samples were collected; for the full theoretical development and the equations where it is shown that the weighting function is the backward recurrence time density which depends on the entire window period distribution including its tail, see ^{[1]}. Therefore, the biomarker cross-sectional approach estimates incidence over a period that may extend into the prepartum period whereas the cohort approach estimates incidence exclusively during the postpartum period among the ZVITAMBO mothers. It is very plausible that HIV incidence rates are different during prepartum and postpartum periods. Further, the ZVITAMBO investigators have documented that there were extensive HIV education and counseling programs instituted during the participants' follow-up visits ^{[2,3]}, which could well have contributed to further reducing HIV incidence over the postpartum period. Indeed, a study of the effectiveness of the education and counseling programs demonstrated improved HIV knowledge among the ZVITAMBO trial participants with increasing exposure to the program ^{[3]}.

The biomarker approach requires an accurate estimate of the mean window period of the BED assay. Hargrove *et al*. ^{[4]}, however, systematically excluded persons with window periods greater than approximately 1 year when calculating the mean window period of the BED assay (see Fig. 1 in ^{[4]}). Thus, their statistical analysis is biased because of selective exclusion of data with long window periods causing underestimation of the mean window period and overestimation of incidence. Hargrove should have censored persons who, at last follow-up, had not reached the absorbance cut-off rather than excluding such data points in their analysis. Examination of Fig. 1 in ^{[4]} suggests that, if the Hargrove analysis had not selectively excluded long window periods, the mean window period would be approximately 239 days instead of the reported mean of 187 days. A formal re-analysis of data in Fig. 1 in ^{[4]} is warranted. The cautionary warning here is that there may be a multitude of reasons as to why the cohort estimate of incidence may be different than the cross-sectional biomarker estimate. Hargrove's assertion that his HIV incidence adjustment procedure must be correct because it makes the biomarker incidence estimate match the ZVITAMBO cohort incidence estimate is flawed.

Hargrove, McDougal and Welte argue that my numerical example is not a fair evaluation of Hargrove's adjustment because it ‘did not allow a false-recent rate in the prevalent specimens’. But their argument is not correct because my example allowed the possibility for persons to be in the window period for 5 years (see Table 1 in ^{[5]}, and the description of community B in the footnotes), but yet Hargrove's adjustment still produces an HIV incidence rate that is less than one fifth of the correct value.

McDougal argues that my result that false positives counterbalance false negatives if the cut-off value is the mean window period (μ) had overlooked false positives who were infected more than 2 × μ = 374 days earlier. McDougal's criticism is not valid because my expression for false positives integrated over all window periods greater than μ, which obviously includes those greater than 2 μ. That is (for an explanation of notation, see ^{[5]}:

McDougal argues my thesis rests on the assumption that HIV infected people mount a BED response that crosses the cut-off within 3 years post infection. As shown by the above equation, the only assumption required to demonstrate that false positives = false negatives is that persons do not remain in the window period indefinitely, rather than that persons progress through the window in less than 3 years. Furthermore, McDougal's Eq. (2) for *P* _{t}/*P* _{0} is equal to 1 ^{[5]}, both McDougal's numerator and denominator in his Eq. (2) are equal; the numerator *P* _{t} is the product of the rate infections occur (*g*) multiplied by the time interval (*μ*) which is *g μ*; the denominator *P* _{0} is also equal to *g μ* because of the fundamental equation in epidemiology that prevalence is equal to incidence multiplied by mean duration.

Hargrove argues that Fig. 1 in his letter disproves my result. However, Hargrove's analysis uses a cut-off of 435 days that is not the mean window period of the 41 ZVITAMBO cases in his figure. Hargrove's 435-day figure was obtained by forcing the biomarker estimate of incidence to ‘match’ the ZVITAMBO cohort estimate and it is clearly not the mean of the data in his figure (e.g. Hargrove derived 435 days by setting the ZVITAMBO cohort incidence estimate of 3.4% equal to his formula (1).

Adjustments of the type proposed by McDougal and Hargrove are not warranted under the assumption that persons do not remain in the window period indefinitely, and the mean window period is correctly estimated. Under that assumption, the McDougal adjustment does not improve upon the accuracy of the simple unadjusted incidence estimate; the Hargrove adjustment produces a biased incidence estimate. However, if a fraction of persons remain in the window period indefinitely and never cross the BED threshold, then at least theoretically an adjustment is necessary as I previously stated ^{[5]}. Two issues, though, deserve special attention in that situation with permanent ‘nonprogressors’. First, when using antibody-based assays for recent infection (such as the BED or the detuned assays), it is necessary to exclude persons with AIDS or on antiretroviral therapy from being counted in the window period. This brings into focus a conceptual problem, how can persons remain in the window indefinitely if window periods are terminated at the onset of AIDS or antiretroviral therapy (whichever comes first) regardless of the optical density (OD) level? To illustrate, suppose 98% of persons are progressors who ultimately cross the BED threshold, and 2% are nonprogressors who never cross the threshold but ultimately either develop AIDS or begin antiretrovirals; and further suppose the mean window period of the progressors is 0.5 years; and the mean time to AIDS or antiretroviral therapy (whichever comes first) among the nonprogressors is 10 years. Then, the overall mean window period for this mixture population of progressors and nonprogressors is 0.98 × 0.5 + 0.02 × 10 = 0.69 years. There are two important points here. The first is that if persons with AIDS or on antiretroviral therapy are not counted in the window period, as is appropriate, then persons cannot remain in the window indefinitely except for ‘elite suppressors’, which refers to the phenomena that some untreated HIV infected persons would never develop AIDS. Second, the mean window period in the biomarker incidence calculation should account for all window periods including those that may have been truncated due to the onset of AIDS or antiretroviral therapy (e.g. the overall mean of 0.69 year in the illustrative numerical example should be used in a biomarker calculation).

Putting aside for the moment the conceptual problem as to whether persons can remain in the window indefinitely (assay nonprogressors) that I discussed in the preceding paragraph, the assertion by Welte and colleagues that the probability of being an assay nonprogressor is over 5% deserves additional response. Assay nonprogressors could include that subset of infected persons who are elite suppressors and not on antiretrovirals. Careful examination of the data, Welte and colleagues cite to support their assertion reveals they are confusing two quantities, the proportion who remain in the window indefinitely (the ‘nonprogressors’), and, the proportion of those infected for at least 2 μ days who are in the window period. The latter quantity was called *ε* by Hargrove ^{[4]} and it's that quantity given in the three publications cited by Welte to support their assertion about permanent assay nonprogressors: the 5.2% figure from the Hargrove study ^{[4]}, the 5.6% figure from the McDougal study ^{[6]}, and the 1.69% figure from the South African study ^{[7]} refer to the proportions in the window among those infected for at least 374 days, 306 days and 306 days, respectively. Those figures do not refer to the proportions who remain in the window period indefinitely as asserted by Welte. We can only infer from those three studies that the proportions of persons who remain in the window indefinitely are in fact *less* than those cited figures. There are additional sources of data informative about the proportion of persons who are permanent nonprogressors. First, Parekh *et al*. ^{[8]} published the survival curve for window periods for subtypes B and E (Fig. 7 in ^{[8]}). Their survival curve reaches zero by 500 days suggesting the proportion of nonprogressors (persons permanently in the BED window) is zero. Second, McDougal cites in his letter new data on 27 specimens with at least 3 years of follow-up indicating 0% (0 out of 27) remain in the window period indefinitely. Other reports have suggested elite suppressors could be 2% or less of the infected population ^{[9]}. In summary, the available data do not support Welte's assertion that the proportion of persons who remain in the window period indefinitely (‘nonprogressors’) is over 5%.

The Hargrove adjustment can only be justified, and approximately at best, if *ε* in his formula (Eq. (3) in ^{[4]}), which he estimates as 5.2% is instead replaced by the proportion who remain in the window period indefinitely as I previously noted ^{[5]}. The critical distinction here and perhaps the heart of the debate is that *ε* in Hargrove's formula, also called the long-term false positive rate over 2 μ days by some investigators, should instead be substituted with a different quantity that quantity being the proportion who remain in the window period indefinitely, to make the formula even approximately correct. However, as discussed above, available data does not support the assertion that 5.2% of persons remain in the window period indefinitely. Users of the Hargrove adjustment will underestimate HIV incidence rates.

As HIV incidence methods become both more innovative and more complicated, we need to increase the transparency of assumptions underlying them to help users of these methods make informed decisions about their validity. In this regard, it would be helpful if researchers can agree on uniform terminology, including those in this exchange of correspondence such as ‘*ε*’, long-term specificity and, ‘assay nonprogressors’. It is important not to blur the distinction between ‘window periods greater than 2 μ days’ and ‘assay nonprogressors’ who are indefinitely in the window. ‘Long-term specificity’ is especially ambiguous because, without further description, it is unclear if the term refers to a 1-year time frame, a 1 μ time frame, a 2 μ time frame, or permanent nonprogressors.

Additional follow-up studies are needed to improve upon previous studies of the BED window period distribution. It is imperative that these studies follow good statistical practice by appropriately censoring observations that have not reached the absorbance cut-off at last follow-up, not deleting long window periods from the analysis, and not extrapolating window periods beyond the range of follow-up.

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