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Policy Research Working Paper

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6823

The Heterogeneous Effects of HIV Testing
Sarah Baird
Erick Gong
Craig McIntosh
Berk Özler

Public Disclosure Authorized

Public Disclosure Authorized

WPS6823

The World Bank
Development Research Group
Poverty and Inequality Team
March 2014

Policy Research Working Paper 6823

Abstract
An extensive multi-disciplinary literature examines theeffects of learning one’s HIV status on subsequent risky
sexual behaviors. However, many of these studies rely
on non-experimental designs; use self-reported outcome
measures, or both. This study investigates the effects
of a randomly assigned home based HIV testing andcounseling (HTC) intervention on risky sexual behaviors
and schooling investments among school-age females
in Malawi. The study finds no overall effects on HIV,
Herpes Simplex Virus (HSV-2), or achievement testscores at follow-up. However, among the small group ofindividuals who tested positive for HIV, a large increasein the probability of contracting HSV-2 is found, withthis effect stronger among those surprised by their test
results. Similarly, those surprised by HIV-negative test
results see a significant improvement in achievement testscores, consistent with increased returns to investments
in human capital. The finding of increased HSV-2
prevalence among HIV-positive individuals suggests thatthe conventional wisdom that those who learn they are
HIV-positive will adopt safer sexual practices should betreated with caution.

This paper is a product of the Poverty and Inequality Team, Development Research Group. It is part of a larger effort by
the World Bank to provide open access to its research and make a contribution to development policy discussions aroundthe world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org. The authors may becontacted at bozler@worldbank.org.

The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development
issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry thenames of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely thoseof the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank andits affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.

Produced by the Research Support TeamThe Heterogeneous Effects of HIV Testing *Sarah Baird, University of Otago/George Washington University
Erick Gong, Middlebury College
Craig McIntosh, University of California San Diego
Berk Özler, The World Bank/University of Otago

Keywords: HIV Prevention; HTC; information; risky sexual behavior
JEL Codes: I15, I25*

We thank members of the SIHR field team for excellent project management, data collection, and research
assistance; Jishnu Das, David Evans, Richard Jessor, Steve Luby, and seminar participants at Middlebury College,
Monash University, University of Colorado, University of Otago, and The World Bank for comments anddiscussions; Global Development Network, Bill & Melinda Gates Foundation, National Bureau of Economic
Research Africa Project, World Bank’s Research Support Budget, and several World Bank trust funds (Gender
Action Plan, Knowledge for Change Program, and Spanish Impact Evaluation fund) for funding. The findings,
interpretations, and conclusions expressed in this article are entirely those of the authors. They do not necessarily
represent the views of the International Bank for Reconstruction and Development, the World Bank, or any funding
agencies. Please send correspondence to: bozler@worldbank.org

I. Introduction
HIV counseling and testing 1 is one of the pillars of HIV prevention (Potts et al. 2008).
Recently, the U.S. Preventive Services Task Force released a draft recommendation statement
suggesting that nearly everyone between the ages of 15-65 be screened for HIV (U.S.
Preventative Services Task Force 2012). One argument for universal HIV testing is due to recent
findings indicating that HIV-positive individuals who immediately receive antiretroviral therapy(ART) significantly reduce their transmission risk to uninfected partners and experience lower
morbidity and mortality rates than those receiving delayed treatment (Cohen et al. 2011). A
distinct argument suggests that HIV-positive individuals reduce risky sexual behaviors after
learning their serostatus (Cassell and Surdo 2007; Gersovitz 2010; Fonner et al. 2012), indicatingthat testing itself would be a means of decreasing subsequent sexual transmission of disease.
Despite the belief that increasing awareness of HIV status has prevention benefits, there are no
studies that have shown population level reductions in the incidence of HIV or other sexuallytransmitted infections (STIs) as a result of HIV testing (Potts et al. 2008). 2 Several studies inpublic health and economics have presented VCT impacts by HIV serostatus. These studies
generally show no effects of testing on sexual behavior or seroconversion for HIV-negative
individuals (Allen et al. 1992a; Weinhardt et al. 1999; Corbett et al. 2007; Thornton 2008;
Fonner et al. 2012), but available evidence suggests that HIV-positive individuals reduce risky
behaviors after testing (Allen et al. 1992b; Weinhardt et al. 1999; Boozer and Philipson 2000;
Thornton 2008; Delavande and Kohler 2012; Fonner et al. 2012). 3

1

HIV counseling and testing encompasses both voluntary counseling and testing (VCT) and home based HIV
testing and counseling (HTC).
2
Furthermore, there are no randomized controlled trials (RCT) that directly assess subsequent HIV transmission for
VCT vs. non-VCT. Kamb et al. (1998), using an RCT, assessed the effects of different modes of counseling for
HIV-negative individuals on STI incidence, but everyone received an HIV test and learned their serostatus. Morerecently, Project Accept (HPTN 043) is assessing the effectiveness of community-based VCT relative to standard
clinic-based VCT on community-level HIV incidence (http://www.cbvct.med.ucla.edu/overview.html). The
Voluntary HIV-1 Counseling and Testing Efficacy Study Group (2000) found significant decreases in risky activity
with non-primary partners for individuals and couples who received VCT.
3
de Paula et al. (2010) reports that an increase in the beliefs of being HIV-positive reduced extra-marital affairs
among married men in Malawi. Beegle, Poulin and Shapira (2012), using randomly assigned VCT in Malawi, findno effects on either sexual behavior or economic outcomes. Haile (2011) examines randomly assigned testing in
Ethiopia and also finds limited impacts on sexual behavior and if anything finds that getting a negative test actuallyleads to more risky behavior.

2

The interdisciplinary literature summarized above is mainly based on self-reported data, which
may be subject to social desirability bias (Allen et al. 2003; Minnis et al. 2009). 4 The possibilityof bias may be particularly relevant in the case of HIV testing interventions. In a prominent study
where offers of VCT were randomly assigned, those offered HIV tests self-report lessunprotected sex with casual partners 6 months after the intervention, however there was nocorresponding change in sexually transmitted infections (VCT Efficacy Study Group 2000). Reexamining the data, Gong (2013) finds suggestive evidence that the information provided in the
pre- and post-test counseling sessions appeared to alter the stigma of reporting risky sexual
behaviors at follow-up, leading to a potentially biased estimate of the actual behavior change.
Even objectively observed behavior such as the purchase of condoms in Thornton (2008) may besubject to this kind of bias. 5
In addition to these measurement limitations, the effects of testing are likely to display
considerable heterogeneity across individuals. One strand of the literature in economics has
focused primarily on the informational signal sent, suggesting that HIV tests should only have aneffect on those who are ‘surprised’ by their HIV serostatus. In this case, the greatest effect will
be found among those who believed they were HIV-negative (HIV-positive) but received apositive (negative) test result (Boozer and Philipson 2000). In fact, these two groups may haveoffsetting behavioral responses to testing, leading to small or no effects of testing on the entire
population: in the extreme, the average treatment effect may be relevant for no one.
While this hypothesis indicates that people will change behavior only as a result of receiving
new information, it does not tell us the direction in which behavior will change. The concept of‘fatalism’ suggests that responses may be non-monotonic: individuals may increase their risky
activity in response to increased HIV prevalence around them above a certain threshold (Kremer
1996; Kerwin 2012). Learning one’s own HIV-positive status can be seen as an extreme case,4

In economics, Gong (2013), which examines the effects of a randomly assigned VCT intervention on incident
gonorrhea and chlamydia, is a notable exception. In public health, two studies of women presenting at prenatal andpediatric outpatient clinics in Rwanda provide evidence on STI incidence for HIV-positive women (Allen et al.
1992a) and HIV seroconversion for the uninfected partner in cohabiting couples with serodiscordant results (Allen etal. 1992b), but both of these are prospective cohort studies comparing outcomes before and after VCT with norandomly assigned comparison group. The Voluntary HIV-1 Counseling and Testing Efficacy Study Group (2000)
states that their RCT was not powered to detect effects on STIs, while another RCT was designed to assess HIV
incidence among initially HIV-negative individuals and cannot comment on onward transmission from individuals
who were HIV-positive at baseline (Corbett et al. 2007).
5
Self-reported data in arguably less sensitive subjects, such as school enrollment (Baird and Özler 2012) and handwashing (Halder et al. 2010; Ram et al. 2010), have also been shown to be subject to social desirability bias.

3where the cost of risky sex becomes zero for the infected individual who may become fatalistic
because she has ‘nothing to lose’. Gong (2013) presents a simple model to suggest that theeffects of HIV testing are, a priori, ambiguous: the response of a utility maximizing individual to
new information about HIV infection will depend on her prior beliefs of HIV infection and thedegree to which altruism affects her behavior. Given the widely documented ‘transactional’
nature of risky sexual activity in Malawi (Poulin 2007; Swidler and Watkins 2007), the setting
for this study, one might expect the direct benefits of risky activity to be high and altruism
towards casual partners to be low for some individuals. In such circumstances, it is possible that
individuals who find out that they are infected with HIV may increase their risky sexual activity.
Economic theory also suggests the possibility of changes for a broader set of behaviors in
response to testing. For instance, if learning one’s HIV status leads to changes in subjective life
expectancy, this may lead to changes in consumption, savings, and investments in human capital(Thornton 2012) – changes that are also likely to be moderated by people’s beliefs about HIV
infection prior to testing (Yeatman 2009, Goldstein et al. 2013).
In this paper, we utilize objective outcome measures within a home based HIV testing andcounseling (HTC) experiment to test these hypotheses among young females in Malawi.
Specifically, we are interested in the effects of HTC on two outcomes: risky sexual behavior andinvestments in human capital. We first examine the overall effect of HIV testing on the
population, and then motivated by theory, examine both the effects of testing by HIV-status (i.e.
the effects of an HIV-negative/positive test), as well as the effects of being surprised by the test
result.
In order to minimize the risk of bias from self-reports, we use HSV-2 as our primary outcome
measure for sexual behavior and achievement tests in mathematics, English reading
comprehension, and Raven’s Colored Progressive Matrices as our primary measure ofinvestments in human capital. 6 We also collected data on the participants’ prior beliefs regarding
HIV infection.
Overall, we find no significant effects of testing on HIV, HSV-2, or test scores. The lack of an
overall effect is consistent with the existing literature that finds no effects among those who were6

In our sample of young females, we consider marginal investments in schooling to be the most important long-term
decision, and focus on changes in achievement test scores to capture this effect.

4HIV-negative at baseline – the group that constitutes 95% of our sample. However, the HSV-2
prevalence at follow-up among the small group of young women who received HIV-positive test
results was 23 percentage points higher than HIV-positive individuals who did not receive HIV
tests. While this result warrants some caution given the small sample size (N=73), the finding is
at odds with most previous studies, which suggest that those who learn they are HIV-positive
adopt safer sex practices. 7
Consistent with economic theory, the perverse effect of testing is stronger among thosesurprised by HIV-positive tests, i.e. those who reported no chance of being infected with HIV atbaseline. Also in line with theory, we find that testing can increase investments in one’s own
human capital. Those surprised by HIV-negative tests, i.e. those who report some chance of HIV
infection at baseline but discover that they are HIV-negative, perform significantly better inachievement tests – a finding supported by an increase in self-reported school enrollment among
the same subgroup.
Our results suggest that home based HIV testing and counseling can lead to important changes
in human capital investments by providing vital health information and add to a larger literatureon the effects of information-interventions (Nguyen 2008; Dupas 2010; Jensen 2010; Goldstein
et al. 2013; Oster, Shoulson, and Dorsey 2013). Furthermore, our finding of increased STI risk
among HIV-positive individuals who receive HIV tests serves as a caution to the assumption thatsuch individuals will adopt safer sexual practices upon learning their serostatus. Finally, ourstudy points to the importance of using objective outcome measures rather than self-reported
behavior change when studying treatments that may differentially alter social desirability bias.
In the next section, we describe the setting of our study. Sections III and IV describe themethods and our findings. Section V provides a concluding discussion that includes thelimitations of our study.

7

The lone exception is a recent study by Gong (2013), who used biomarker data from a VCT experiment in a highrisk urban sample in Kenya and Tanzania and found a similar increase in STI incidence among those infected withHIV.

5

II. Setting
Malawi, which is a small and poor country in southern Africa, is the setting for this study. 81%
of its population of 15.3 million lived in rural areas in 2009, with most people relying on
subsistence farming. The country is poor even by African standards: Malawi’s 2008 GNI per
capita figure of $760 (PPP, current international $) is less than 40 percent of the Sub-SaharanAfrican average of $1,973 (World Development Indicators 2010). As of 2007, the prevalence of
HIV was estimated to be between 11.0% and 12.9% among adults aged 15-49 – the ninth-highest
HIV prevalence in the world (UNAIDS 2008). The gender gap in HIV prevalence among young
adults, aged 15-24, is startling: prevalence was more than four times higher for females thanmales in 2004 (9.1% vs. 2.1%) (National Statistical Office (Malawi) and ORC Macro 2004).
The study took place in Zomba District, in Southern Malawi. Zomba District is divided into
550 enumeration areas (EAs), which are defined by the National Statistical Office of Malawi andcontain an average of 250 households spanning several villages. In 2007, 176 EAs in urban andrural areas of Zomba were selected to form the sample of a cash transfer experiment. In each ofthese EAs, all dwellings were visited to obtain a full listing of never-married females, aged 1322. From this sampling frame, 3,796 school-age girls aged 13-22 were selected for inclusion toform the impact evaluation sample of the cash transfer experiment. This sample of approximately
22 girls per EA included two strata: those who were enrolled in school at time of listing andthose who were out of school. Of the 176 EAs in the overall study, 88 were assigned to thetreatment group where program participants were offered cash transfers. The other 88 wereassigned to the comparison group, which received nothing. 8 This study assesses the impact of arandomly assigned home-based HIV testing and counseling (HTC) intervention (discussed in
more detail in the Methods section below) within the 88 EAs in the comparison group.

8

For more details on the cash transfer experiment and its impact evaluation, please refer to Baird, McIntosh andÖzler (2011).

6

III. Methods
52 of the 88 EAs in the comparison group of the larger experiment were randomly assigned toreceive HTC between the months of June and September in 2009. 9 Then, between the months ofMarch and August 2010, i.e. after an average of approximately 10 months, all 88 EAs were
offered HTC. The sample used in this paper therefore consists of 1948 females in 88 comparison
EAs, of which 1122 in 52 EAs were offered HTC in 2009, with everyone offered HTC in 2010.
In the remainder of this paper we refer to the group that was offered testing and counseling in2009 as the HTC group, and those who were offered HTC only in 2010 as the control group.
HTC took place at the homes of the core respondents where they were invited to receive
counseling and rapid testing for HIV, HSV-2, and syphilis by a trained counselor. 10 Overall
acceptance of HTC was high at 98%, with no differences between the two study arms. Malawian
nurses and counselors certified in conducting rapid HIV tests through the Ministry of Health HIV
Unit HCT Counselor Certification Program conducted HTC. Testing and counseling was
performed in a private location at or near the participant’s house. Whole blood samples wereobtained using a finger-stick. The teams conducting HTC at follow-up were blinded to thetesting treatment status of the subjects and were independent of the survey teams that conductedhousehold surveys and administered achievement tests (discussed below). 11 Ethics review
committees at the National Health Sciences Research Council (Malawi), the University ofCalifornia at San Diego (USA), and George Washington University (USA) approved the study
design. Further details of the HTC procedures can be found in Appendix A.

9Details of the randomization for the HTC experiment can be found in Baird et al. (2012).
Rapid tests for syphilis were only performed during the first round of HTC as its prevalence in this sample wasfound to be less than 1%. The effects of this intervention should be considered noting that the subjects were invited
to receive counseling and testing not only for HIV but for HSV-2 and syphilis as well.
11
HTC counselors could deduce the HTC treatment status of the subjects who had tested positive for HIV or HSV-2
at baseline. To avoid unnecessary burdens on the subjects, re-testing for the previously positive test was avoided insuch circumstances, meaning that the HTC counselor could deduce that the individual had been tested before for theforegone STI test. Furthermore, to protect the privacy of all individuals, every individual in both the HTC andcontrol groups were visited at follow-up: those who had tested positive for only one STI were tested for the other,while those who had tested positive for both were given a short survey. The counselors were blinded to the treatment
status of everyone else, i.e. those in the HTC group who tested negative at baseline or those in the control group who
were not tested at baseline.
107The household survey data used in this paper were collected in two rounds, the second andthird wave of the overall study. 12 The first household survey used in this study was conducted
approximately 6 months prior to the first HTC data collection between October 2008 andFebruary 2009. The second follow-up household survey was conducted between February andJune 2010, just prior to the second round of the HTC testing. In addition to collecting data on thehousehold, more pertinent for this study were the detailed information collected on the selfreported schooling and sexual activity of the respondents, as well as their subjective probabilities
of being infected with HIV and their subjective life expectancies to ascertain prior beliefs andchanges in those beliefs as a result of receiving HTC. 13
Economic theory suggests that changes in subjective life expectancy may lead to changes inhuman capital investments. Perhaps the most critical investment that adolescents make is thelaborious work of building their own human capital. Because the returns from investments inschooling are largely realized in the distant future they appear particularly informative as tointer-temporal tradeoffs. To measure improvements in student achievement, mathematics andEnglish reading comprehension tests were developed and administered to all study participants attheir homes as part of the follow-up data collection effort in 2010. The tests were developed by ateam of experts at the Human Sciences Research Council according to the Malawian curricula
for these subjects for Standards 5-8 and Forms 1-2. 14 In addition, to measure cognitive skills, we
utilized a version of Raven’s Colored Progressive Matrices that was used in the Indonesia FamilyLife Survey (IFLS-2).
Objective measures of behavior change minimize the risk of social desirability bias in theestimated treatment effects. In addition, the intervention itself might change the self-reporting
bias of those receiving HTC. Thus, compared with self-reported sexual behaviors, biologicalmarkers of unprotected sex are likely to be preferable. 15 In this paper, we utilize biomarker dataon both HIV and HSV-2, collected during HTC. For educational outcomes, we utilize test scoredata on mathematics, English reading comprehension, and cognitive ability, as they are likely toprovide a more accurate measure of human capital investments than self-reported attendance or
12There was also a household survey conducted between October 2007 and January 2008 which served as a baseline
for the cash transfer intervention, but is not used for this analysis.
13
These surveys, as well as the achievement tests described below, are available from the authors upon request.
14
In Malawi, there are eight grades in primary school (Standard 1-8) and four in secondary school (Form 1-4).
15
However, such proxies are also imperfect surrogates for HIV transmission (Padian et al. 2011).

8

educational expenditures. The percentages of correct answers across these three tests wereaveraged to create an overall percentage of correct answers and standardized to serve as ourprimary outcome.
We supplement these objective measures of behavior with self-reported data from thehousehold survey. We use the subjective likelihood of HIV infection at baseline to examine theheterogeneity of HTC impacts by prior beliefs. 16 Finally, we examine impacts on the following
self-reported outcomes: subjective probability of HIV infection, perceived life expectancy,
sexual behaviors, and school enrollment at follow-up. Given the caveats regarding the potentialof bias in impact estimates on self-reported behaviors, we use these secondary outcomes tocomplement our findings of HTC effects on STIs and test scores.
In a randomized experiment with multiple rounds of data collection, the internal validity of thefindings depends crucially on whether the randomization was conducted properly and whether
attrition from the study sample was independent of treatment status. Table 1 presents a summaryof baseline demographic characteristics, and measures of sexual behavior and education. Overall,
the samples in the two arms are similar, with no difference between them that is statisticallysignificant at the 5% level out of 16 comparisons, and two differences (female-headed household
and never had sex) significant at the 10% level. The average age at baseline is just under 17 andmore than three-quarters of the sample reported being enrolled in school – with the mean highest
grade attended being Standard 8, i.e. the last year of primary school in Malawi. Less than aquarter of the sample reported being sexually active during the 12 months prior to baseline datacollection, and thus, not surprisingly, less than 10% report any chance of being infected with
HIV. Appendix Table B1 examines whether there is any differential attrition between the twostudy arms. The analysis indicates that the attrition in the control group is around 15% andtreatment status is orthogonal to attrition from the sample.

16

Self-reports at baseline may still suffer from social desirability bias, but such misreporting should be orthogonal totreatment status as HTC was randomly assigned and both groups were untreated at baseline.

9

Table 1: Baseline BalanceControlAge

HTC

p-value(controlHTC)
0.687

16.65016.709(2.215)(2.198)=1 if Live Inside 16km
0.604
0.575
0.841
(0.489)(0.495)=1 if Live Outside 16km
0.092
0.097
0.930
(0.289)(0.295)=1 if Live in Urban Area
0.305
0.328
0.874
(0.461)(0.470)Asset Index
0.179
0.421
0.535
(2.429)(2.595)=1 if Female Headed
0.432
0.367
0.053
Household(0.496)(0.482)=1 if in School
0.750
0.802
0.103
(0.434)(0.398)Highest Grade
8.188
8.407
0.199
(1.993)(1.981)=1 if Ever Married
0.090
0.075
0.412
(0.287)(0.264)=1 if Ever Pregnant
0.180
0.169
0.652
(0.384)(0.375)=1 if Never Had Sex
0.576
0.639
0.097
(0.495)(0.480)=1 if Sexually Active in Past
0.233
0.218
0.583
12 months(0.423)(0.413)
Number of Partners in Past
0.240
0.231
0.760
12 Months(0.442)(0.458)=1 if Engage in Risky Sex
0.186
0.171
0.551
(0.389)(0.377)=1 if Partner Over 25
0.035
0.034
0.943
(0.184)(0.183)=1 if Any Chance Infected
0.079
0.088
0.611
with HIV Now(0.271)(0.283)
Number of observations
720
961
Notes: Column (1) shows the baseline means for the control
group while column (2) shows the means for the tested group.
Column (3) presents the p-value on the difference between
the two means. All variables are weighted to make them
representative of the target population in the study EAs withrobust standard errors clustered at the EA level to calculate
the p-value.

We estimate the overall effects of HTC on HIV and HSV-2, educational achievement, andsome selected self-reported outcomes using an intention-to-treat (ITT) estimator. We use a linear
probability model: 17

(1)

17

Probit specifications generate similar estimates when compared to our main results.

10where Yij is the outcome of interest for individual i in treatment cluster j, 𝐻𝑇𝐶𝑗 is an indicatorof whether the cluster is randomly assigned to receive HTC in 2009, and 𝑋𝑖𝑗𝑘 is a set of K

individual-level baseline characteristics. This small set of controls, 𝑋𝑖𝑗𝑘 , includes age, anindicator for never having had sex, and school enrollment status at baseline, all of which aredemeaned and fully interacted with the treatment indicator. These baseline controls areprognostic of STI status at follow-up and orthogonal to treatment assignment, and thus they
substantially improve the precision of our estimates. 18 The error terms, 𝜀𝑖𝑗 , are clustered at the

EA level, which accounts both for the design effect of our EA level treatment and theheteroskedasticity inherent in the linear probability model. Age- and stratum-specific samplingweights are used to make the results representative of the target population in the study area.
We also estimate the effect of HTC separately for those receiving HIV-positive and HIVnegative test results, as we expect behavioral responses to differ by HIV status. 19 Under the ideal
study design to address this question, we would compare individuals who are HIV-positive(negative) at baseline and receive HTC to control individuals who have the same HIV-status atbaseline but are not informed of their status. However, the design of this study forewent
collecting samples from individuals without informing them of the test results, meaning thatbaseline HIV status is observed only in the HTC group. 20 Since we do not observe baseline HIV
18

While our primary analysis includes adjustments using covariates measured at baseline, we also present
unadjusted estimates of HTC effects for full transparency. To select the baseline covariates for adjustment, we ran a
stepwise regression using 13 explanatory variables that theory suggests should be predictive of HSV-2 status at
follow-up and retained those variables that were significant at the 10% level. In the absence of a pre-analysis plan,
this procedure largely removes the potential for ad hoc specification searching. The interacted adjustment produces,
asymptotically and for finite samples, the most precise average treatment effect (Lin 2013).
19
Appendix Tables B2 and B3 show baseline balance for these two sub-groups.
20
Both types of study designs can be found in the existing literature. Corbett et al. (2007) reports collecting venousor finger-prick blood or oral mucosal transudate for anonymous HIV testing from all employees at the 22 businesses
that were recruited for their study. Similarly, an ongoing study assessing the impacts of HIV testing by Duflo,
Dupas, and Sharma also utilized anonymous linked testing of all study participants at baseline(http://www.povertyactionlab.org/node/5649). On the other hand, The Voluntary HIV-1 Counseling and Testing
Efficacy Study Group (2000) thought neither collecting serum and testing for HIV without giving the individuals theresults at baseline, nor testing for HIV but not providing counseling to be ethical. Thornton (2008) overcomes thisidentification problem by collecting blood samples from the entire sample and providing randomly varying levels of
incentives for individuals to come back and learn their test results two to four months after sample collection and byrandomizing the location of the temporary centers where the study participants can obtain their results. However, it
is important to note that such estimates are local average treatment effects on those individuals who would have only
learned their results due to the incentive and would not have otherwise. The introduction of HIV incidence assays,
which can detect recent infections, may also provide further improvements in this area. As described in detail below,

11status for individuals in the control group, we cannot form the true counterfactual comparisongroup. Instead, we present analysis by HIV status using the observed status at baseline for thetreatment group, and at follow-up for the comparison group. Because the difference between theestimator we wish to construct and the one we can construct is unobserved but still well defined,
its extreme values can be calculated with no assumptions beyond simple random assignment.
Below, we provide an informal description of how we estimate HTC effects on HSV-2 bybaseline HIV-serostatus. Appendix C formally defines our estimator and describes thecalculation of the bounds within which the true ITT lies.
Individuals in the control group who tested HIV-positive at follow-up fall into two sub-groups:
those who were HIV-positive at baseline and those who became infected with HIV between
baseline and follow-up. 21 This implies that the counterfactual HSV-2 prevalence for the HTC
treatment is contaminated by the presence of HIV-seroconverters: we would like to observe thefollow-up HSV-2 prevalence among only those who were HIV-positive at baseline in the control
group, but instead we observe it among them and HIV seroconverters. The bias caused by thislatter group is a function of two quantities: its size in our sample and the HSV-2 prevalence
among them. We can estimate the former by calculating the difference between the HIVprevalence in the control group at follow-up and the HIV prevalence in the treatment group atbaseline. Both of these groups are untested, and the samples are comparable due to random
assignment into treatment. Using only this quantity, we can then calculate bounds for how large
the bias caused by HIV-seroconverters to the impact estimates of HSV-2 can possibly be, under
two extreme scenarios: (i) all of the HIV-seroconverters are HSV-2 positive in the follow-up; or(ii) none of them are.

IV. Results
Table 2 presents our main findings. It first reports estimates for outcomes objectively measured
at follow-up (HIV, HSV-2, and achievement test results, unadjusted and adjusted, in columns 16), and then for outcomes measured using self-reports (beliefs on HIV infection, subjective life
our empirical approach allows us to estimate the intention-to-treat (ITT) effect and provide bounds on the value ofthe true ITT by simply offering testing in some clusters and not in others.
21
The description we provide here is for the case of the HIV-positive group, but the argument is symmetric for theestimator for the HIV-negative group.

12expectancy, sexual behavior, and school enrollment – all adjusted estimates – in columns 7-12).
Panel A contains HTC impacts on the entire sample and shows that HTC had no statisticallysignificant effect on the prevalence of HIV, HSV-2, or test scores at follow-up. These null effects
are measured fairly precisely: we would have been able to detect a 2.7 percentage point effect on
HSV-2 prevalence (follow-up prevalence in the control group is 7.4%) and a 0.23 standard
deviation effect on test scores with 95% confidence. When we examine self-reported data, wefind no significant changes in subjective life expectancy, likelihood of HIV infection, selfreported school enrollment, or unsafe sex, although there is a small but statistically significant
increase in the likelihood of being sexually active during the past 12 months. Hence, overall, ourfindings suggest that the HTC intervention did not have any significant effects on STI risk orinvestments in human capital in the study population.
Panel A shows that the follow-up HIV prevalence in our sample of young women is fairly
small at approximately 5%, indicating that more than 95% of the HTC group received a HIVnegative test result at baseline. Panel B shows that the HTC impacts among this group are
generally very similar to those among the entire sample: HTC caused no changes in HSV-2 risk
or in achievement test scores among this group, although they assign a lower average probabilityof being infected with HIV at follow-up and report a slightly higher number of sexual partners
over the past 12 months.

13

Table 2: HTC Impacts on Objective and Self-Reported Outcomes
Panel A: HTC Impacts on the Entire Sample
Objective=1 if HIV
Positive

HTC
Number of observations
Mean in the control group
HTC
Number of observations
Mean in the control group
HTC
Number of observations
Mean in the control group(1)-0.006(0.011)
1,681
0.050

Self-Reported
Subjective=1 if Sex
Number=1 if HIV =1 if HSV-2 =1 if HSV-2 Achievement Achievement Likelihood Probability=1 if Engage
Active Past 12 Partners Past
Positive
Positive
Positive
Test Score
Test Score
Live to 50
in Risky Sex
of HIVMonths12 Months
Infection
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
(10)
(11)
-0.003
0.003
0.010
0.137
0.073
0.001
-0.1590.042
0.059*
0.024(0.010)(0.014)(0.014)(0.118)(0.099)(0.008)(0.222)(0.027)(0.034)(0.028)
1,681
1,680
1,680
1,660
1,660
1,673
1,673
1,671
1,671
1,669
0.050
0.074
0.074
0.000
0.000
0.041
5.370
0.353
0.360
0.332
Panel B: HTC Impacts on the HIV-Negative Sample-0.004
0.000
0.146
0.088
-0.010*-0.0970.040
0.057*
0.030(0.012)(0.013)(0.122)(0.104)(0.006)(0.227)(0.028)(0.033)(0.029)
1,607
1,607
1,591
1,591
1,602
1,602
1,600
1,600
1,600
0.065
0.065
0.004
0.004
0.033
5.331
0.338
0.346
0.319
Panel C: HTC Impacts on the HIV-Positive Sample
0.231*
0.246***-0.125-0.2330.291*-0.4230.109
0.133-0.030(0.137)(0.069)(0.230)(0.172)(0.162)(0.949)(0.098)(0.092)(0.079)
73
73
69
69
71
71
71
71
69
0.255
0.255
-0.069-0.069
0.192
6.140
0.629
0.629
0.579

=1 if inSchool(12)-0.007(0.022)
1,673
0.525-0.003(0.022)
1,602
0.534-0.060(0.135)71
0.356

Includes Controls
No
Yes
No
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of the target population in the study
EAs. The achievement test score is the average percent across math, English and cognitive tests (standardized). The subjective likelihood of HIV infection takes on a value from 0 to 1
where zero is no self-reported chance of HIV infection. Risky sex takes on a value of 1 if the respondent does not always use condoms with all partners, and is zero for those who always
use condoms or have not engaged in sexual activity in the past 12 months. Regressions that include controls include the following: age, an indicator for never having had sex, and school
enrollment status at baseline, all of which are demeaned and fully interacted with the treatment indicator. Parameter estimates statistically different than zero at 99% (***), 95% (**), and
90% (*) confidence.

14

However, when we examine the effects of HTC on those who tested HIV-positive at baseline,
the story is starkly different (Panel C). Among the 73 HIV-positive individuals in our sample, thefollow-up prevalence of HSV-2 is 23.1 percentage points higher in the HTC group than thecontrol group mean of 25.5% -- statistically significant at the 10% level. 22 Self-reports suggest
changes in subjective beliefs as well: those in the HTC arm who receive HIV-positive tests
assign a higher average probability to being HIV-positive at follow-up. 23 The self-reported
outcomes on sexual behavior suggest some increase in sexual activity and the number of partners
during the past 12 months but none of these variables is statistically significant. We do not findany significant effects on test scores. 24
As described earlier, our naïve estimator of HTC impacts by baseline HIV status is biased by
the presence of HIV-seroconverters among the counterfactual group at follow-up. To assess
whether the HTC effect on HSV-2 prevalence among the HIV-positive subgroup is robust to thisissue, we conduct a bounding exercise, which was summarized in the previous section andformally outlined in Appendix C. 25 While the lower and upper bounds for the true ITT estimate
can be calculated analytically, in order to provide standard errors on the bounds we calculatethem empirically. We do this by repeatedly and randomly excluding the expected number ofHIV-seroconverters from our analysis and recalculating the HTC effect on HSV-2. The baseline
HIV prevalence in the HTC group is 3.96% while the follow-up HIV prevalence in the control
group is 5.03%. Neither of these figures is affected by HTC as they both reflect prevalence rates
in each study arm prior to HTC. The difference between these two figures, which is equal to the22

The adjusted estimate is very similar at 24.6 percentage points and significant at the 1% level.
While the average HTC effect on beliefs of HIV infection is strong and statistically significant, 43% of those who
received HIV-positive test results reported no (zero) chance of being infected with HIV at the follow-up survey.
This finding is unlikely to be due to the testing procedures. As detailed in Appendix A, those who tested positive
with one rapid test received a second independent test using a different test kit. On the very unlikely event that thetwo test results were discordant, a third test was administered to break the tie. It is consistent with two other studies
from Malawi, both of which find that approximately 40% of individuals who received HIV-positive test results
through a VCT intervention reported no likelihood of being infected in a follow-up survey (Thornton 2012;
Delavande and Kohler 2012).
24
The reader should note the limited statistical power of the impact analysis among this subgroup due to its small
size in our sample. We have a total of 73 HIV-positive individuals in our analysis, which is similar in size toThornton (2012) who uses a sample of 79 HIV-positive individuals, and Delavande and Kohler (2012) who use asample of 97 HIV-positive individuals. Gong (2013), using data on an older sample of people who were seeking
HIV-related services, analyzes a sample of 465 HIV-positive individuals.
25
We do not present the results of the bounding exercise for the HIV-negative group because the small number ofHIV-seroconverters forms a negligible share of the sample of 1,607 HIV-negative individuals and, hence, does notbias our estimates in any meaningful way.
23

15

estimated HIV incidence rate, implies that, of the 40 individuals in the control group who tested
HIV-positive at follow-up, 32 are expected to have been HIV-positive at baseline and eight tohave seroconverted between the two HTC rounds. To estimate a lower bound HTC effect, we
randomly exclude eight HSV-2-negative individuals from the control group, rerun the adjusted
regression described in equation (1), record the ITT estimate 𝛽 and its standard error, and repeat

this 500 times. 26 Repeating the same exercise, this time randomly excluding eight HSV-2-

positive individuals from the control group 500 times, yields the upper bound ITT estimate.
Table 3 presents the results and shows that the lower bound estimates of the HTC effect is
0.224 while the upper bound estimate is 0.328 – both statistically significant at the 1% level(columns 2 & 3). Hence, under the assumption of baseline balance in HIV prevalence between
the HTC and control groups, the true HTC effect on HSV-2 prevalence among the HIV-positive
sample in this study must lie somewhere between 22.4 and 32.8 percentage points and thepotential bias caused by the seroconverters cannot be large enough to overwhelm the perverse
effect of HIV testing. The naïve ITT estimate of 0.246 (column 1) reported in Panel C of Table 2
is robust to extreme assumptions about the HSV-2 status of HIV-seroconverters.
The above bounding exercise simply requires us to assume the randomization led to baselinebalance of HIV prevalence. We can examine how imbalanced HIV prevalence would have to be
between the HTC and the control group to explain away our results. To estimate this, we simply
extend the calculation of the lower bound estimate described above. We remove a randomly
selected number of HSV-2 negative individuals from the control group and rerun the adjusted
regression (equation 1); we keep removing individuals until we no longer are able to reject thenull of no effect of HTC at the 10% level. We find that it would take 22 HIV-seroconverters who
are all HSV-2 negative in order to fail to estimate significant effects of HIV-positive tests onfollow-up HSV-2 rates. 22 HIV-seroconverters implies that HIV-prevalence at baseline for thecontrol group would have been 2.28% compared to 3.96% in the HTC treatment arm.

26

This simulation produces an average HIV prevalence of 4.03% in the control group at baseline – very close to the
3.96% figure in the HTC group at baseline.

16

Table 3: Bounding HTC Impacts on HSV-2 for the HIV-Positive Sample
Lower Bound
Upper Bound
ITT
ITT
(1)
(2)
(3)
HTC
0.246***
0.224***
0.328***(0.069)(0.072)(0.068)
Number of Observations
73
65
65
Notes: Estimated ITT in column 1 is identical to the estimate in column 2, Panel
C of Table 2. To estimate the lower bound ITT, we randomly exclude 8 HSV-2negative individuals from the control group, which is the expected number of
HIV seroconverters in the control group, rerun the regression described inequation (1), record the ITT estimate β and its standard error, and repeat this
500 times. The mean values of the coefficient estimate and its standard error arereported in column 2. Repeating this simulation exercise, this time randomly
excluding 8 HSV-2-positive individuals from the control group, we calculate theupper bound ITT, which is reported in column 3. Please see details in Results
section and Appendix C. Regressions are OLS models with robust standard
errors clustered at the EA level. All regressions are weighted to make them
representative of the target population in the study EAs. All regressions
include the following controls: age, an indicator for never having had sex, andschool enrollment status at baseline, all of which are demeaned and fullyinteracted with the treatment indicator. Parameter estimates statisticallydifferent than zero at 99% (***), 95% (**), and 90% (*) confidence.
Estimated ITT

We conclude our empirical analysis by testing the hypothesis that the effects of HIV-positive(negative) tests should be concentrated among those who considered themselves at no (some)risk of HIV at baseline because HTC should lead to behavior change only if it is providing new
information. 27 Table 4 provides support for this hypothesis. Panel A presents HTC effects for
those surprised by their HIV-negative status: the first four columns show the effects on HSV-2
and test scores (unadjusted and adjusted) while the remaining columns show effects on the selfreported outcome measures (adjusted) presented in Table 2. 28 We find an economicallymeaningful and statistically significant increase in achievement test scores in this subgroup: theunadjusted and adjusted estimates of HTC impact on test scores are 0.487 and 0.400 standard
deviations, respectively – both significant at the 5% level. Self-reported outcomes point to therevelation of new, important information on health and increased investment in schooling amongas potential channels for this finding: the young women in this subgroup are 12.3 percentage
27

Appendix Tables B4 and B5 show baseline balance among these sub-groups.
We define this subgroup as those who reported some likelihood of being infected with HIV prior to participatingin HTC and found out otherwise. Similarly we define those surprised by their HIV-positive status as those whoreported no chance of being infected with HIV prior participating in HTC but tested positive.. . We find that the selfreported likelihood of being infected with HIV is positively and significantly associated with actual HIV-status atbaseline amongst those in the HTC sample. .
28

17

points less likely to think they are HIV-positive (compared to a control mean of 15.9%; pvalue=0.000) and 13.3 percentage points more likely to report being enrolled in school at followup (compared to a control mean of 29.5%; p-value=0.158). The impact estimates on HSV-2 arein the expected direction but not statistically significant.
Panel B presents HTC effects for those surprised by their HIV-positive status. The unadjusted
and adjusted HTC effects on HSV-2 prevalence in this subgroup are 0.299 and 0.215,
respectively – both significant at the 5% level. Individuals in this group are more than 50
percentage points more likely to think they are infected with HIV at follow-up (compared withless than 2% in the control group; p-value=0.000). The impact estimates for test scores are,again, in the expected direction but not statistically significant. We find no significant impacts on
any of the other self-reported outcomes. The reader should note, however, that the size of thissubgroup is small and the impact estimates are accordingly imprecise.

18

Table 4: HTC Impacts on Objective and Self-Reported Outcomes by Prior HIV Beliefs
Panel A: High Prior Beliefs of HIV Infection Before HTC and Tested Negative
Objective=1 if HSV-2
Positive

HTC
Number of observations
Mean in control(1)-0.029(0.040)143
0.091

Self-Reported=1 if HSV-2 Achievement Achievement
Test Score
Test Score
Positive(2)-0.039(0.030)
143
0.091

(3)
0.487**(0.217)142-0.299(4)0.400**(0.185)142-0.299Subjective
Likelihoodof HIV
Infection(5)-0.123***(0.031)143
0.159=1 if Sex
NumberProbability=1 if Engage
Active Past Partners Past
in Risky Sex
Live to 50
12 Months
12 Months(6)
0.219(0.592)
143
4.816

(7)
0.011
(0.080)
143
0.449

(8)
-0.029(0.084)
143
0.505

(9)
-0.005(0.079)143
0.421=1 if inSchool(10)
0.133(0.093)143
0.295

Panel B: Low Prior Beliefs of HIV Infection Before HTC and Tested Positive
HTC

0.299**
0.215**-0.010-0.166
0.524***
0.195-0.0350.009-0.1000.090(0.139)(0.098)(0.304)(0.288)(0.146)(1.242)(0.149)(0.155)(0.156)(0.209)Number of observations
53
53
50
50
51
51
51
51
49
51
Mean in control
0.218
0.218
-0.254-0.254
0.016
5.885
0.664
0.664
0.569
0.231
Includes Controls
No
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Yes
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of the target population in
the study EAs. The achievement test score is the average percent across math, English and cognitive tests (standardized). The subjective likelihood of HIV infection takes on avalue from 0 to 1 where zero is no self-reported chance of HIV infection. Risky sex takes on a value of 1 if the respondent does not always use condoms with all partners, and iszero for those who always use condoms or have not engaged in sexual activity in the past 12 months. Regressions that include controls include the following: age, an indicator
for never having had sex, and school enrollment status at baseline, all of which are demeaned and fully interacted with the treatment indicator. Parameter estimates statisticallydifferent than zero at 99% (***), 95% (**), and 90% (*) confidence

19

V. Concluding Discussion
We conducted a cluster randomized home based HIV testing and counseling intervention
among young females in Malawi to disentangle its effects on risky sexual behavior and humancapital investments. While HIV testing plays an unambiguously important role as a gateway to
ART and, hence, would have indirect effects on HIV transmission through suppressed
infectiousness after the start of therapy, its direct behavioral effects appear to be complex and not
uniformly protective. Our main finding is that while HTC has no overall effect on STI risk or
achievement test scores, it does have, consistent with economic theory, heterogeneous effects in
subgroups. Among those who discover that they are HIV-positive, the risk of HSV-2 infection at
follow-up increases substantially. On the other hand, individuals surprised by HIV-negative test
results experienced a significant improvement in achievement test scores.
Until very recently, the literature on the effects of HIV testing on subsequent sexual behavior
almost uniformly suggested that it caused HIV-positive individuals to become safer, not morerisky. However, this study and Gong (2013), which share random assignment of HIV testing andthe use of STI biomarkers as primary outcomes, come to the opposite conclusion. The sample inGong (2013) consists of male and female adults seeking HIV-related services in Kenya andTanzania in the mid-1990s, while our study examines a random sample of young females inMalawi in 2009. The common findings in these two studies, which utilize independent data setsfrom different countries, decades, and demographic groups, cast some doubt on the assumptionthat standard HIV testing interventions have direct prevention benefits through behavior change.
We suggest that caution is warranted in interpreting findings from testing studies that do not
simultaneously tackle both the endogeneity of testing and the risk of bias from self-reported
sexual behavior data.
The study's main finding, i.e. that HIV-positive tests lead to increases in HSV-2 rates
suggesting increases in unprotected sex, warrants some caution given that it is based on a small
sample size (N=73). One concern is that a small sample size increases the chance of baseline
imbalance for our primary outcome measures. Given the study design, whereby baseline STI
status is unknown in the control group, it is impossible to demonstrate balance for HIV and
HSV-2. However, we note that the main findings are robust to the inclusion of baseline
covariates that are prognostic of HSV-2 infection at follow-up. Another concern is that our20statistical inference relies on asymptotic theory, which may not hold at smaller samples such as
ours. To address this, we implement a non-parametric permutation test as defined by Anderson(2008) that does not rely on asymptotic theory (details in Appendix D). Using the same
specification as in Table 2, Panel C, Column 4, "HTC Impacts on the HIV-Positive Sample", wefind a p-value<.01, allowing us to reject the null of no effect at the 1% level - which is exactly
what we concluded earlier.
There are two additional limitations to this study. First, we do not have the ideal study design
required to assess testing impacts by HIV serostatus, which requires collecting blood samples
from all study participants at baseline but not informing the control group of their HIV
serostatus. We show that under random assignment of clusters to testing or no testing,researchers can obtain an ITT estimate for the causal effect of testing separately for HIV-positive(and negative) individuals and construct bounds around the true ITT effect. Secondly, the study
does not measure subsequent HIV transmission to sexual partners. If there is serosorting (i.e.
HIV-positive females pair with HIV-positive males upon learning their status) then the increasein HSV-2 infections we observe among HIV-positive females could occur without any effects on
the total number of new HIV infections. We find this to be unlikely in this study as our data
show no indications of such serosorting among HSV-2 seroconverters in the HTC arm. 29
Keeping these limitations in mind, our study makes some contributions to the literature. Using
survey questions designed to test several hypotheses regarding the effects of HIV testing, we findsupport for the hypothesis that the effects of testing are concentrated among those ‘surprised’ by
HIV test results, both in terms of sexual behavior and educational achievement, the latter ofwhich is consistent with increased effort and investment in human capital in anticipation of alonger, healthier life. This finding suggests that HIV tests can affect important investment
decisions among young individuals by revealing an HIV-negative status to those who previously
29

An examination of the answers of HIV-positive HSV-2 seroconverters to follow-up survey questions about theirsexual partners reveals that (i) all of them attach either ‘no likelihood or ‘low likelihood that their partners are HIVpositive; (ii) none of them think that their partner had other sexual partners while they were together; (iii) only halfof them report that their partner was ever tested for HIV; and (iv) they all had age appropriate partners. Furthermore,
the distributions of these variables are similar both among all of those in the VCT group who tested HIV-positive atbaseline and among those in the control group who tested HIV-positive at follow-up. Another possibility is that
individuals who found out they are HIV-positive switched to oral sex to protect their partners. We find this
explanation also unlikely since the self-reported likelihood of receiving oral sex by men is very small in Malawi –only 2% of rural men and 11% of urban men report ever having received oral sex. Furthermore, men substantiallyoverestimate the probability of HIV infection through oral sex, indicating that it would not necessarily be seen as
safer sex (Kerwin 2012; Kerwin, Thornton and Foley 2012).

21

thought they might be infected with HIV. This finding also suggests that exposure to infection
risk and uncertainty about HIV status may cause young people to lower their investments in
education.
These insights regarding the information signal provided by HIV tests help explain the main
findings in Table 2. Among this young population, most individuals have no expectation of being
HIV-positive, so an HIV-negative test result does not surprise many. This is consistent withfinding no overall effect of HIV tests among the HIV-negative group while finding an
improvement in educational achievement once we limit our analysis to those surprised by an
HIV-negative test. Similarly, an HIV-positive test result is an unwelcome surprise to many in our
sample, which explains the large effects of tests on HSV-2 among the entire HIV-positive group.
The troubling perverse effect of HIV-positive test results on HSV-2 serves as a caution topractitioners and merits careful consideration in policy terms. Following the logic presented inGong (2013), this result is suggestive of high short-term benefits from risky activity and low
altruism towards marginal partners – a scenario consistent with transactional sex. If such
relationships are partially to blame for this finding, policies that reduce transactional sex may
also reduce these unwanted effects of HIV testing. Our results also suggest that standard testing
interventions, which simply convey HIV-status and provide brief pre- and post-test counselingsessions, may be insufficient to cause declines in risky sexual activity among those who find out
they are infected. Other types of post-test support may be needed to ensure that such individuals
are both linked to treatment and minimize the risk of transmission to others. Future RCTs thatexperiment with alternative means of informing, counseling, and providing post-test support tothose who receive HIV-positive test results can be useful in creating effective positive prevention
strategies among young people.

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Weinhardt, L.S., M. P. Carey, B. T. Johnson, and N. L. Bickham. 1999. “Effects of HIV
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27

Appendix A: Home Based HIV Testing and Counseling (HTC) Details

Between July and September, 2009, 52 of the 88 EAs in the comparison group of thelarger experiment were randomly sampled for inclusion in the data collection for biologicaloutcomes. Study participants in these EAs were visited at their homes and invited to receive
counseling and rapid testing for HIV, HSV-2, and syphilis by a trained counselor. 30 Then,between the months of March and August 2010, i.e. after an average of approximately 10
months, participants in all 88 EAs were visited at their homes and invited to receive counselingand rapid testing for HIV and HSV-2. All participants provided written informed consent.
Additional consent was obtained from parents or legal guardians of all unmarried girls under theage of 18, with assent obtained from the girls.
HTC was conducted by Malawian nurses and counselors certified in conducting rapid
HIV tests through the Ministry of Health HIV Unit HCT Counselor Certification Program. The
counselors were not the same individuals who conducted the survey questionnaires. Testing andcounseling were performed in a private location at or near the participant’s house. Whole blood
samples were obtained using a finger-stick. For HIV, the testing algorithm described in the
Malawi Ministry of Health guidelines was followed. The collected blood sample was first tested
using a Determine HIV/1-2TM assay (Inverness Medical, UK). If the test result was positive, thenthe sample was tested using a Uni-GoId® HIV assay (Trinity Biotech, Ireland). If these two test
results were discordant, then the sample was tested with SD BIOLINE HIV 1/2 3.0 assay(Standard Diagnostics, Inc., Korea) for a tie-breaker. Participants who tested positive on the
Determine plus either of the other two assays were interpreted to be HIV infected; those testingnegative on the Determine or negative on the other two assays were interpreted to be HIV
uninfected. Recognizing that HIV-negative participants could be in the window period, they
were counseled to be retested after 3 months if they had any risk factors for infection.
For HSV-2, we used the BiokitHSV-2 Rapid Test assay (Biokit USA, USA) following
the manufacturer’s instructions. The Biokit assay is a point-of-care test that is easy to use in thefield and produces results in minutes; however the results are dependent on the subjective
judgment of the tester. Therefore, all tests were reviewed by at least two readers. The tests were30

Prevalence rates for syphilis were below 1% during the initial testing, thus syphilis was not included during thesecond round of HTC.

28

read immediately by the tester who also photographed the test kit with a digital camera, and asecond study staff member interpreted the results from the photos blinded to the tester’sinterpretation. When the readers disagreed, the testing supervisor reviewed the photos to break
the ties.
Appendix B: Tables

Appendix Table B1: Attrition=1 if Have Survey=1 if Have Baseline =1 if Have Survey Data
Data, HIV data, andSurvey Data
and HIV Data
all Controls=1 if Respondent in Round 2
Sampled HTC EA
Control mean
Number of observations

0.031
0.005
0.007
(0.020)(0.027)(0.027)
0.906
0.849
0.852
1948
1948
1948
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All
regressions are weighted to make them representative of the target population in the study EAs.
Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*)
confidence.

29

Appendix Table B2: Baseline Balance Among the HIV-Positive
Samplep-value
HTC
Control(controlHTC)
0.351
18.600Age17.748(2.716)(2.869)0.366
0.445=1 if Live Inside 16km
0.629
(0.489)(0.505)0.060
0.631=1 if Live Outside 16km
0.104
(0.309)(0.241)
0.495
0.279
0.267
=1 if Live in Urban Area
(0.508)(0.448)0.319
0.639
Asset Index
0.027(2.352)(2.451)
0.305
0.792
0.671
=1 if Female Headed(0.411)(0.477)
Household
0.372=1 if in School
0.531
0.641
(0.505)(0.487)
8.911
8.834
0.898
Highest Grade(1.979)(2.357)
0.125
0.100
0.719
=1 if Ever Married(0.334)(0.304)0.344
0.502=1 if Ever Pregnant
0.427(0.482)(0.501)0.368
0.250=1 if Never Had Sex
0.217(0.417)(0.490)
0.344
0.455
0.370
=1 if Sexually Active in Past
(0.481)(0.506)
12 months
0.365
0.475
0.388
Number of Partners in Past
(0.529)(0.546)12 Months=1 if Engage in Risky Sex
0.303
0.330
0.811
(0.465)(0.477)0.165
0.013=1 if Partner Over 25
0.021(0.377)(0.144)
0.325
0.272
0.181
=1 if Any Chance Infected(0.390)(0.476)
with HIV Now
Number of observations
40
33
Notes: Column (1) shows the baseline means for the control
group while column (2) shows the means for the tested group.
Column (3) presents the p-value on the difference between thetwo means. All variables are weighted to make them
representative of the target population in the study EAs withrobust standard errors clustered at the EA level to calculate thep-value.

30

Appendix Table B3: Baseline Balance Among the HIV-Negative
Samplep-value
Control
HTC(controlHTC)
Age
16.592
16.630
0.811
2.172
2.133
=1 if Live Inside 16km
0.603
0.581
0.879
0.490
0.494
=1 if Live Outside 16km
0.091
0.097
0.910
0.288
0.296
=1 if Live in Urban Area
0.306
0.322
0.918
0.461
0.467
Asset Index
0.187
0.425
0.549
2.429
2.606
=1 if Female Headed
0.413
0.355
0.096
Household
0.493
0.479
=1 if in School
0.761
0.810
0.129
0.427
0.393
Highest Grade
8.149
8.392
0.149
1.966
1.979
=1 if Ever Married
0.089
0.073
0.417
0.284
0.261
=1 if Ever Pregnant
0.167
0.162
0.852
0.373
0.369
=1 if Never Had Sex
0.595
0.651
0.133
0.491
0.477
=1 if Sexually Active in Past
0.228
0.208
0.526
12 months
0.420
0.406
Number of Partners in Past
0.233
0.221
0.694
12 Months
0.437
0.452
=1 if Engage in Risky Sex
0.180
0.165
0.583
0.384
0.371
=1 if Partner Over 25
0.036
0.029
0.462
0.186
0.168
=1 if Any Chance Infected
0.074
0.078
0.772
with HIV Now
0.262
0.269
Number of observations
680
927
Notes: Column (1) shows the baseline means for the control
group while column (2) shows the means for the tested group.
Column (3) presents the p-value on the difference between thetwo means. All variables are weighted to make them
representative of the target population in the study EAs withrobust standard errors clustered at the EA level to calculate thep-value.

31

Appendix Table B4: Baseline Balance Among HIV-Positive
Individuals with Low Prior Beliefs of HIV Infection Before HTC
ControlAge

HTC

p-value(controlHTC)
0.699

18.41818.056(2.682)(3.003)=1 if Live Inside 16km
0.711
0.509
0.301
(0.461)(0.511)=1 if Live Outside 16km
0.124
0.090
0.758
(0.336)(0.293)0.401=1 if Live in Urban Area
0.165
0.208
(0.377)(0.501)
0.478
Asset Index-0.625-0.137(2.169)(2.381)0.635
0.399=1 if Female Headed
0.751(0.492)(0.440)Household=1 if in School
0.533
0.608
0.588
(0.508)(0.499)Highest Grade
8.605
8.664
0.932
(2.527)(2.078)=1 if Ever Married
0.156
0.090
0.446
(0.369)(0.293)0.288=1 if Ever Pregnant
0.404
0.271
(0.499)(0.454)0.315=1 if Never Had Sex
0.156
0.293
(0.369)(0.465)
0.249
0.500
0.073
=1 if Sexually Active in Past
(0.440)(0.511)
12 months
0.280
0.530
0.099
Number of Partners in Past
(0.523)(0.568)12 Months=1 if Engage in Risky Sex
0.218
0.341
0.347
(0.420)(0.484)=1 if Partner Over 25
0.031
0.190
0.136
(0.177)(0.401)24
Number of observations
29
Notes: Column (1) shows the baseline means for the control
group while column (2) shows the means for the tested group.
Column (3) presents the p-value on the difference between thetwo means. All variables are weighted to make them
representative of the target population in the study EAs withrobust standard errors clustered at the EA level to calculate thep-value.

32

Appendix Table B5: Baseline Balance Among HIV-Negative
Individuals with High Prior Beliefs of HIV Infection Before HTC
ControlAge

HTC

p-value(controlHTC)
0.869

17.57817.645(2.489)(2.395)=1 if Live Inside 16km
0.705
0.613
0.531
(0.460)(0.490)=1 if Live Outside 16km
0.147
0.093
0.513
(0.357)(0.292)0.295=1 if Live in Urban Area
0.148
0.281
(0.358)(0.459)0.881
Asset Index-0.164-0.086(2.518)(2.343)0.390
0.406=1 if Female Headed
0.468(0.491)(0.503)
Household=1 if in School
0.690
0.691
0.987
(0.466)(0.465)Highest Grade
8.077
8.541
0.277
(2.337)(2.452)=1 if Ever Married
0.169
0.093
0.227
(0.378)(0.292)0.551=1 if Ever Pregnant
0.254
0.206
(0.439)(0.407)0.620=1 if Never Had Sex
0.432
0.479
(0.499)(0.503)
0.350
0.362
0.875
=1 if Sexually Active in Past
(0.481)(0.484)
12 months
0.350
0.383
0.680
Number of Partners in Past
(0.481)(0.530)12 Months=1 if Engage in Risky Sex
0.254
0.271
0.806
(0.439)(0.447)=1 if Partner Over 25
0.070
0.081
0.819
(0.258)(0.274)79
Number of observations
64
Notes: Column (1) shows the baseline means for the control
group while column (2) shows the means for the tested group.
Column (3) presents the p-value on the difference between thetwo means. All variables are weighted to make them
representative of the target population in the study EAs withrobust standard errors clustered at the EA level to calculate thep-value.

33

Appendix C: Bounding the estimates of HTC impacts by HIV serostatus

Let
and

indicate the HSV-2 biomarker outcome at follow-up for an HIV-tested individual

for an HIV-untested individual. Then, define three exhaustive and mutually exclusive

groups based on HIV status in a previously untested population. These are, those who are

HIV-negative in both rounds, H i = 1 , those who are HIV-positive in both rounds, and,those who HIV seroconvert in between the two rounds if no testing occurred (throughout thisappendix we use a tilde to indicate quantities that are unobserved). Each of these three groups
has a population prevalence, where, and by the properties of randomization andthe fact that strata are defined in the absence of testing, these quantities are the same in thetesting treatment and control. We observe p1 as the prevalence rate in the treatment in thebaseline, p 0 as one minus the prevalence rate in the control at follow-up, and p S as thedifference between these two quantities.
The quantity that we wish to estimate is the causal effect of an HIV-positive test on the
HSV-2 prevalence rate, which would be given by: 31

While we can calculate the fraction of the sample p S that seroconverted in the control
group, we cannot tell which specific (HIV-positive at follow-up) individuals belong to this groupand hence we cannot separately measure the quantities
HSV-2 prevalence in these combined groups

or.

Therefore, what we are able to measure directly is the ‘Estimated’

31, only the:

The estimation of bounds for the causal effect of an HIV-negative test is similar and not detailed here.

34

This shows that the resulting estimand Fis a weighted average of the correct ITT and theincorrect estimate that we would get by subtracting the outcome among seroconverters from theoutcome among tested always-positives. This expression will equal the correct ITT either if(there are no seroconverters) or if(the seroconverters lookjust like the control always-positives). Hence, this expression gives us a way to understand how
this imperfect counterfactual distorts the quantity that we estimate relative to the true ITT.
We can do this by taking advantage of the binary nature of Yi . Specifically, we can plugin the extreme possible values of prevalence of HSV-2 in the follow-up for the seroconverters,
and rearrange the above expression to calculate the extreme bounds on the possible values of thetrue ITT given the other parameters:

Clearly, as p S → 0 these bounds converge to the estimated value, and ITT + E → ITT +* .
This technique is the analogue to Lee bounds (Lee 2009), where rather than facing attrition weface the addition of a new group whose outcomes may be different from those within the
counterfactual we wish to form. These bounds can be formed with no assumptions beyond
simple random assignment.

35

Appendix D: Non-Parametric Permutation Test

We follow Anderson (2008), and implement a non-parametric permutation test. Startingwith our HIV-positive sample (N=73), we randomly assign HTC treatment status to 40 of the
HIV-positive individuals, and the remaining 33 individuals are assigned to the control group.
Using this sample, we estimate equation 1 and collect the t-statistic for 𝛽̂ (the effect of an HIVpositive test on HSV-2). We repeat this 10,000 times and generate a distribution of t-statistics

from which we based our statistical inference on. Using this distribution and our original tstatistic from our estimation (t-statistic = 3.58) we calculate our p-value, which is less than .01.
This allows us to reject the null hypothesis of no effect of HTC on HSV-2 at the 1% level
without relying on large sample asymptotic properties.

36