Abstract

Directly eliciting individuals' subjective beliefs via surveys is increasingly popular in social science research, but doing so via face-to-face surveys has an important downside: the interviewer's knowledge of the topic may spill over onto the respondent's recorded beliefs. Using a randomized experiment that used interviewers to implement an information treatment, we show that reported beliefs are significantly shifted by interviewer knowledge. Trained interviewers primed respondents to use the exact numbers used in the training, nudging them away from higher answers; recorded responses decreased by about 0.3 standard deviations of the initial belief distribution. Furthermore, respondents with stronger prior beliefs were less affected by interviewer knowledge. We suggest corrections for this issue from the perspectives of interviewer recruitment, survey design, and experiment setup.

Introduction

Demographic research has increasingly made use of individuals' subjective expectations about probabilities and the distributions of variables. Such subjective expectations are important drivers of demographic phenomena such as fertility (Delavande 2008; Mac Dougall et al. 2013; Shapira 2017) and migration (McKenzie et al. 2013; Shrestha 2020), and can help us understand their trends and underlying determinants. Furthermore, subjective expectations are related to objective probabilities and can be used to help forecast future trends, for example in the case of mortality rates (Perozek 2008).

However, the face-to-face surveys commonly used to measure subjective beliefs in developing countries have a potential weakness: respondents' recorded beliefs may be affected by what interviewers know about the phenomenon in question. These surveys sometimes measure subjective beliefs by directly asking about percentage chances (Hurd and McGarry 1995; Lillard and Willis 2001; McKenzie et al. 2006), but they often use visual aids (Attanasio et al. 2005, Delevande et al. 2011a; Delavande and Kohler 2009) or ask how many of a fixed number of people would have something happen to them (Aguila et al. 2014; De Mel et al. 2008). All three approaches rely heavily on the interviewer to explain the question and encourage the respondent to give a valid answer. These interviewer-subject interactions raise the specter of interviewer effects, particularly the potential influence of interviewer knowledge on subjects' recorded beliefs.

The effect of interviewer characteristics on survey responses has been documented across a wide range of contexts. Examples of these characteristics are race and ethnicity (Adida et al. 2016; Anderson et al. 1988; Cotter et al. 1982; Davis 1997; Dionne 2014; Finkel et al. 1991; Reese et al. 1986), religion (Blaydes and Gillum 2013), gender (Becker et al. 1995; McCombie and Anarfi 2002), and social or cultural proximity (Weinreb 2006). Respondents may also infer the purpose of the study from interviewers and change their answers as a result, a pattern known as experimenter demand effects (de Quidt et al. 2018; Orne 1962; Zizzo 2010). This body of research has shown the importance of social interactions in the interview setting for recorded survey responses and the effect of interviewer characteristics on these interactions. An extensive literature has also explored the methodology of subjective belief elicitation (Delavande 2014). However, to our knowledge, no previous study has explored the role of interviewer knowledge in driving survey responses.

Leveraging a randomized experiment in Malawi that used interviewers to implement an information treatment, we show that interviewer knowledge has an effect on respondents' recorded beliefs. The experiment was designed to investigate how information about the true transmission rate of HIV affects risk-taking (Kerwin 2020). Interviewers were taught the true HIV transmission rate midway through the baseline survey in order to conduct the information treatments for the study. The study respondents were randomly divided into control surveys, which happened before the interviewers learned the information, and treatment surveys, which happened afterward. We use data from the baseline surveys, when treatment-group respondents had not yet been taught the risk information themselves but were interviewed by people who had been taught it.

Interviewer knowledge matters for recorded risk perceptions. Comparing the baseline surveys across study arms, we find that interviewers who were exposed to the information treatment elicited lower HIV transmission rate perceptions from respondents. Reported beliefs were significantly shifted by the interviewers' knowledge, with their estimated rates decreasing by about nine percentage points, or roughly 0.3 standard deviations of the control-group belief distribution. This result can help explain the puzzling finding that people's preferences and beliefs appear to be very unstable in panel surveys (Chuang and Schecter 2015; Mueller et al. 2019). If recorded responses are heavily shaped by interviewers' knowledge and beliefs, then people's answers may appear to be much more unstable than they really are.

In addition to shedding light on the role of interviewer knowledge in driving survey responses, our study also builds on the previous literature on interviewer effects by isolating the causal effect of a specific interviewer characteristic: knowledge. Past studies of interviewer effects have been able to exploit the exogenous assignment of interviewers to respondents but have been limited by the fact that the interviewer characteristics in question are both fixed and correlated with other attributes. For example, race is correlated with income and socioeconomic status, and a wide range of interviewer characteristics can all affect responses simultaneously (Di Maio and Fiala 2019). Because interviewers in our study were exogenously shocked with new information about HIV transmission rates, we can isolate the causal effect of knowledge alone. This is the first study we are aware of that has been able to identify the causal effect of a single interviewer characteristic. Isolating the effect of knowledge is possible because knowledge, unlike the other characteristics that are typically studied, is malleable and can be changed quickly; by contrast, even many nonfixed traits (such as education levels) can be changed only slowly, and others (such as age) cannot be changed at all.

We can identify several channels through which interviewers' knowledge affects recorded risk perceptions. First, interviewers who underwent the training primed respondents to give answers that match the exact training content. The training explained that the annual transmission rate of HIV between an HIV-positive spouse and an HIV-negative spouse who have regular unprotected sex is 10%. Consistent with a priming story, treatment group respondents are 4.3 percentage points more likely to (incorrectly) report that the per-act probability of HIV transmission is exactly 10%.

A related mechanism by which interviewer knowledge affects recorded risk perceptions is through nudging respondents to give lower answers. Evidence for this comes from an aspect of the survey design: if a respondent answered exactly 50% for any risk perception question, interviewers were taught to follow up to see whether the respondent was simply unsure; if so, the interviewer asked the respondent for their best guess, following Hudomiet et al. (2011). Interviewers who underwent the training were less likely to elicit higher numbers when asking respondents to provide a best guess in this situation. This finding suggests that interviewers who were exposed to the information treatment nudge participants away from higher answers. The same pattern could also affect the initial responses to the questions.

The strength of respondents' prior beliefs may affect how much interviewer knowledge matters. The effect of interviewer training is smaller for more-educated respondents, falling to zero for respondents who reached at least Form 2 (10th grade) in school, perhaps because students in Malawi learn about HIV transmission during Form 2 and are exposed to a narrative that claims HIV is highly contagious. Although the information taught during Form 2 diffuses through the population as a whole, more-educated respondents are exposed to it directly and thus likely feel more certain about their beliefs. This makes them less susceptible to the interviewer's nudges to report lower risk beliefs.

We suggest several ways to correct for interviewer knowledge effects. Interviewer recruitment for face-to-face surveys should try to match the characteristics of the interviewers and the survey respondents, and interviewer training should emphasize the possibility of unintentional spillovers and the need to treat all respondents consistently. When designing information experiments, researchers should consider running baseline surveys simultaneously for the treatment and control groups or providing the information treatment separately from the survey interviews to mitigate spillovers, although these approaches have their own drawbacks. Even when no information is provided, knowledge spillovers remain likely. Because interviewers can vary widely in their knowledge and beliefs, teaching them about topics relevant to the survey may improve data quality. One promising avenue is to eliminate the interaction between interviewer and respondent by performing surveys via audio computer-assisted self-interviewing (ACASI), which can work even in contexts with low literacy and numeracy. However, ACASI may lead to lower data quality than face-to-face interviews; further work in this area would be invaluable.

Background

Subjective Expectations and Demographic Decisions

Subjective expectations play a key role in driving demographic patterns and people's responses to them. They drive contraception choices and fertility (Delavande 2008; Mac Dougall et al. 2013; Shapira 2017) as well as migration (McKenzie et al. 2013; Shrestha 2020). Perceived mortality risks affect whether people engage in life-threatening activities (see, e.g., Delavande and Kohler [2016] for HIV; León and Miguel [2017] for transportation choices; and Bennear et al. [2013] and Keskin et al. [2016] for water safety) and thus affect actual mortality rates. The effects of subjective expectations often spill over between demographic choices and other domains. For example, women's education and career decisions depend on their beliefs about the costs of raising children—which can differ sharply from reality (Kuziemko et al. 2018). Similarly, women tend to systematically underestimate their fecundity at young ages and overestimate it at older ages (Mahony 2011).1

Data on people's subjective expectations are also a potentially useful tool for demography research. Subjective mortality probabilities may be useful predictors of actual mortality rates (Perozek 2008) and are correlated with known predictors of mortality (Delavande et al. 2017), although some evidence suggests that people's subjective mortality beliefs have systematic biases (Elder 2013). Despite their limitations, subjective mortality beliefs may still be valuable: people form them using risk factors that objective mortality rates cannot account for, such as parental health and longevity, and they affect risk-taking behaviors (Dormont et al. 2018). Similarly, self-rated health is a useful predictor of mortality (Burström and Fredlund 2001). Subjective beliefs about health can help forecast future mortality rates: they are available earlier than objective predictors of mortality, and they predict mortality even conditional on objective measures of health status (Idler and Benyamini 1997).

There is a crucial distinction between individuals' subjective expectations about risks and other variables and the true values of these figures. Much social science research assumes that people know the true values of numbers, but recent research has focused on measuring people's perceptions, which can be quite different from the truth (Manski 2004). Consider the case of subjective expectations about mortality rates, which can differ from true population-average mortality rates in three key ways (Delavande and Rohwedder 2011). First, they measure a variable that has not yet been observed because the population answering the survey questions is still alive. Second, they may be measured with error relative to the person's true beliefs. Third, they reflect individuals' beliefs about what will happen rather than the truth.

The HIV Epidemic in Malawi

Our study uses data on people's perceptions of HIV risks in Malawi. Malawi has been dealing with a severe HIV epidemic for several decades, and the disease has had major effects on its population. The prevalence of the virus has been stable at about 10% of the population for roughly the past decade (National Statistical Office [NSO] Malawi and ICF 2017).2 The expansion of access to antiretroviral treatment (ART) for HIV has drastically improved the situation for HIV-positive people in recent years. Starting in 2016, Malawi implemented a universal test-and-treat policy, so that all HIV-positive people had access to ART (Alhaj et al. 2019). Testing rates are still low for men, but most women get access to treatment because there is strong pressure to accept the nominally voluntary HIV tests during antenatal care visits (Angotti et al. 2011).3 Even with the expansion of access to treatment, however, HIV is still a major issue in people's lives.

The large scale of Malawi's HIV epidemic has led to extensive research by social scientists on how it impacts people's lives. Most prominently, this includes the Malawi Longitudinal Study of Families and Health (MLSFH), which has been collecting demographic, socioeconomic, and health information on the same households since 1998. The MLSFH also embeds a novel ethnographic study, the Malawi Journals Project (MJP), in which Malawians record everyday conversations about HIV/AIDS.

Subjective Expectations About HIV in Malawi

An important focus of research on HIV in Malawi has been on measuring people's subjective beliefs about the disease and understanding how those beliefs affect their behavior. The MLSFH measures both people's perceptions about HIV and their sexual activity, and has an embedded experiment in which respondents were incentivized to learn their HIV status (Fedor et al. 2015; Thornton 2008). It was also used as a platform to design and study an innovative technique for capturing subjective probabilities using visual aids (Delavande and Kohler 2009). This work is an important part of a literature showing that eliciting subjective probability beliefs is feasible in low- and middle-income settings (Attanasio 2009; Delavande 2014; Delavande et al. 2011b).

A core finding of the work on subjective beliefs about HIV in Malawi is that people substantially overestimate their likelihood of being HIV-positive (Anglewicz and Kohler 2009; Bignami-Van Assche et al. 2007). Relatedly, they also overestimate the transmission rate of the virus by several orders of magnitude (Delavande and Kohler 2016; Kerwin 2020). Extensive research has tried to understand how people form these beliefs, and one channel is through HIV testing. Malawians who learn that they are HIV-positive lower their beliefs about the transmission rate of the virus (Delavande and Kohler 2012), perhaps because they realize they have not yet transmitted the virus to their sex partners. Qualitative evidence from the MJP supports this quantitative finding. Kaler and Watkins (2010) found that people are ambivalent about testing: they think that it will always lead to a positive result, followed by death. They also found that as a result of thinking that HIV tests mostly turn out positive, people overestimate the transmission rate of HIV.

Information from HIV tests spreads beyond the person being tested. Spouses typically tell each other about their HIV test results, although HIV-positive women are less likely to share their status (Anglewicz and Chintsanya 2011). More broadly, subjective expectations about HIV risks spread through social networks (Helleringer and Kohler 2005; Kohler et al. 2007). People also draw inferences about HIV risks from their own experiences. For example, when young women marry, they are more likely to think they are at risk of contracting HIV in the future, possibly because they know or suspect that their husbands are unfaithful (Grant and Soler-Hampejsek 2014).

Another line of research has shown that subjective expectations about HIV matter: people respond to their perceived risks of being HIV positive. Perceived HIV status, rather than actual status, drives condom use for women, even when actual status is known (Anglewicz and Clark 2013). Ethnographic evidence from the MJP has shown a similar pattern for men: they assume that they are HIV positive even with no medical evaluation or signs of AIDS, which drives further risky behavior (Kaler 2003; Kaler et al. 2015). Many people are uncertain about their HIV status, and this uncertainty affects their fertility intentions (Trinitapoli and Yeatman 2011).

In addition to changing their behavior in response to their perceived HIV status, people also respond to their perceived chance of contracting the disease. Grant and Soler-Hampejsek (2014) showed that women may use divorce to protect themselves if they believe they are at high risk of contracting HIV, mirroring the finding by Anglewicz and Reniers (2014) that HIV-positive people have higher rates of widowhood and divorce. Women who anticipate that they will contract HIV in the future invest more in their children's education (Grant 2008). The causal effect of risk perceptions on behavior also holds for probabilistic beliefs of the kind studied in this paper (Delavande and Kohler 2016; Kerwin 2020).

Data and Empirical Design

We use data from an experiment designed to study the effects of risk perceptions on risk-taking behavior (Kerwin 2020) that was conducted in the Zomba District of Malawi from August to December 2012. The experiment randomly assigned one-half of respondents (stratified by distance to the trading center and gender) to receive information about HIV transmission risks at the end of the baseline survey. Treatment-group participants were read an information script that explained the actual HIV transmission rate for couples with one infected partner that have regular unprotected sex (about 100 times per year, on average). The true transmission rate is 10% per year (Wawer et al. 2005), far below what Malawians typically believe. In our sample, the average risk belief is about 90% per year, and nearly one-half of our sample thinks that the transmission rate from just a single exposure is 100%.

The risk information was provided by the survey interviewers, using a script and a set of visual aids that were built into the treatment-group surveys. The interviewers themselves were taught the risk information and how to conduct that survey module via a two-day training session that took place halfway through the baseline data collection. All the control-group surveys were scheduled to occur before this training session to minimize the risk of contaminating the control villages, following Godlonton et al. (2016).

The interviewers seem to have been unaware of the actual HIV transmission rate prior to the training session, and thus it likely strongly shifted their beliefs about HIV risks. Although we lack direct data on their beliefs prior to the information session, two sources of evidence support this claim. First, the interviewers all lived in or close to the study area, so the pre-training data for the control group is a reasonable proxy for their beliefs. Less than 2% of our control group thought the annual risk of HIV transmission was below 20% at baseline. A second piece of evidence comes from the training session itself. The interviewers expressed surprise at the information they were taught, and many were initially reluctant to believe it. To help convince them, project staff had to show them the original research study (Wawer et al. 2005) as well as the section of the Malawi National AIDS Commission website that listed the HIV transmission rate.

The fact that the interviewers were taught new information just before they started to survey the randomly assigned treatment group allows us to study how that information affected survey responses. We use the interviewer training session as a treatment and study how that changes the recorded baseline beliefs of respondents. Comparing the baseline beliefs between the treatment and control groups allows us to estimate the effect of interviewer knowledge on recorded risk beliefs. Figure A1 in the online appendix shows the timeline of the experiment.

Our principal outcome measure is respondents' recorded subjective risk beliefs on the baseline surveys. This variable was collected by asking respondents to estimate proportions of a fixed number of people—for example, “If 100 men, who do not have HIV, each have sex with a woman who is HIV-positive tonight and do not use a condom, how many of them do you think will have HIV after the night?” The questions cover transmission rates per act and per year for both protected and unprotected sex. Respondents picked integers between 0 and 100 in response to each question.4 The exact wording of all four questions is shown in Figure A2 in the online appendix. This style of question to assess expectations has also been tested and validated by previous research in Malawi (Chinkhumba et al. 2014; Godlonton et al.2016; Kerwin et al. 2011).5 Interviewers had no incentive to record specific answers to this question but instead were incentivized to record answers accurately: random back-checks were used to check that surveys were actually conducted and responses were recorded correctly.

Our sample of respondents includes 1,292 individuals from 70 villages who have both valid baseline and endline survey data. Baseline demographic statistics for the treatment and control groups can be found in Table A1 in the online appendix; the two study arms were balanced on observable exogenous variables. The experiment we use was not designed to study the interviewers, and so we have very limited data on their characteristics based on administrative records. Of the 14 interviewers in our sample, half are female and half male. The even gender split was chosen intentionally to facilitate gender-matched interviews: all male respondents were interviewed by men, and all women were interviewed by women. All interviewers had completed secondary school (a screening requirement imposed during hiring), and most had graduated recently (and thus they were in their 20s). They were recruited from the local area but were not assigned to survey anyone they knew personally.

Empirical Strategy

To study the effect of interviewer knowledge on respondents' recorded risk beliefs, we compare the recorded baseline beliefs of the treatment and control groups. Our main regression specification is Eq. (1), where Yi is either a measure of risk beliefs at baseline or an indicator variable for specific values of the risk belief at baseline. The dummy variable Ti takes a value of 1 for respondents in the treatment group and 0 otherwise. Our treatment is thus defined as having been interviewed at baseline by a more-knowledgeable interviewer. We control for sampling strata fixed effects, Zi, and interviewer fixed effects, Ii; the latter allow us to rule out the possibility that interviewer characteristics other than knowledge are driving our results. We also control for Wi, a sexual activity index based on the first five variables in the balance table (see the section Alternative Explanations for further discussion). All standard errors are adjusted for clustering by village.

Yi=α+βTi+Ziη+Iiγ+δWi+εi.
(1)

To understand the mechanisms behind the effects, we interact the treatment indicator with respondent characteristics (Eq. (2)). We de-mean all covariates before interacting them with the treatment indicator, so the main effect of the treatment can still be interpreted as the sample-average treatment effect (Imbens and Rubin 2015:247).

Yi=α+βTi+γTi×Xi+δXi+Ziη + Iiγ+δWi+εi.
(2)

Results

Main Estimates

Interviewers exposed to the information treatment elicit lower risk perceptions. Figure 1 shows the daily average recorded risk beliefs for the treatment and control groups over time. The first group of observations represents the control-group beliefs at baseline, when neither the interviewers nor the respondents knew the content of the information treatment. After those surveys were complete, the interviewers learned the content of the information treatment (vertical dashed line) and then conducted the baseline treatment surveys. We can see that risk beliefs of the treatment group are lower than those of the control group.

There are five days with control-group baseline data after the information treatment. These are cleanup baseline surveys for the control group that were conducted after the bulk of the baseline control-group surveys were finished and that took place after the interviewer training session. This happened when respondents were not available at the initially scheduled baseline interview. The distribution of beliefs for these observations is closer to that of the treatment group than to the rest of the control group, lending support to the idea that interviewer knowledge specifically—and not some other factor that is imbalanced across study arms—is causing the mean difference between baseline treatment and control recorded beliefs.

Further support for the idea that the change in beliefs is due to interviewer knowledge is evident in the endline risk beliefs. First, the endline risk beliefs allow us to reject the possibility that the treatment group simply accidentally received the risk information prior to answering their baseline survey questions. The direct information treatment effect on risk beliefs (the gap between the endline risk beliefs for the treatment and the control groups) is much larger than the treatment-control difference at baseline.

Second, the control-group endline beliefs are very similar to the treatment-group baseline beliefs, which is completely consistent with a model in which recorded beliefs are moved by interviewer knowledge. Neither the treatment group at baseline nor the control group at endline had been directly told the information about HIV transmission risks, but both were interviewed by interviewers who did know the information. As a result, both sets of risk beliefs are shifted downward relative to the control-group baseline beliefs, and they also have similar average values to one another.

Table 1 presents our main results numerically. Each column represents a measure of a different HIV transmission risk: measured per act or per year, and when using condoms or having unprotected sex. For all four measured risk beliefs, the coefficient on the treatment (interviewer training) is negative and significant. In the case of the per-act transmission risk for unprotected sex, the coefficient is 9.3 percentage points, or about 0.3 standard deviations. The magnitude of the effect is relatively large, especially considering that it is an unintentional spillover: respondents were not directly exposed to the information treatment. As shown in Figure 1, the effect at endline, when participants themselves were exposed to the information treatment, was larger: 38.4 percentage points for the perceived per-act transmission risk for unprotected sex.

Participants in the control group had average risk beliefs that were substantially larger than the true risk of HIV transmission in each one of those cases. For example, the true value of the per-year transmission rate for unprotected sex is about 10% (Wawer et al. 2005), but the average respondent in the control group thought the risk was 83%, and well over one-half of respondents thought the risk was 100%. Baseline beliefs for the control group have the correct ordering in terms of which risk is higher, but all the average levels are higher than the true infection risks.

Interviewer training decreased recorded risk beliefs for all four measures, even though the training discussed only the per-year risk for unprotected sex, shown in column 2 of Table 1. Column 1 shows an effect of 9.3 percentage points (0.35 SD); columns 2 and 4 show effects of 4.8 and 7.9 percentage points, respectively (0.28 SD each). Column 3 shows the smallest effect, at 2.7 percentage points (0.12 SD), corresponding to the per-act, condom-protected transmission risk.6 This variable has the lowest control-group mean overall, so a smaller effect is not surprising, and we can still reject a zero treatment effect. Moreover, the risks of condom-protected sex are simply scaled-down versions of the risks from unprotected sex, so changes in those variables should be smaller.

The fact that interviewer knowledge changes responses for risk beliefs that were not explicitly targeted suggests that interviewers internalized the information and actually changed their beliefs about transmission risk, as opposed to memorizing the one figure that was presented to them. Interviewers knew that the four measures of transmission risk were related, and when they adjusted their beliefs for one, it affected their beliefs for all the others. Thus the threat of interviewer knowledge effects appears to be quite general: knowledge spillovers occur not only with directly provided information but also with the implications of the information.

Alternative Explanations

Interviewer Experience

Another potential explanation for our findings is interviewer experience. The trajectory of the pretreatment trend in the first portion of Figure 1, if extended, would intersect the level of recorded risk beliefs in the second portion. This could have happened if interviewers improved over time at asking the relatively complicated questions on the subjective expectation module. Our basic results in Table 1 do not rule out the possibility that the estimated treatment effects are due to interviewer experience alone.

To examine this possibility in further detail, we present a set of regression discontinuity (RD) plots in Figure 2. These graphs are produced using the Calonico et al. (2015) rdplot Stata command to automatically bin the data and fit polynomial curves on either side of the discontinuity. The binned averages are shown using dark gray dots, with black lines for the polynomial fits. The light gray regions show 95% confidence intervals for the bin-specific averages.

We also show the estimated treatment effects from RD models in Table 2, using the rdrobust Stata command (Calonico et al. 2017). This command automatically selects data-driven bandwidths and computes robust bias-corrected p values (Calonico et al. 2014).

Panel a of Figure 2 shows the main comparison of interest: before versus after the training session, per-act HIV transmission risk beliefs for unprotected sex. Two conclusions are clear from the graph. First, the steep downward trend apparent in the first portion of Figure 1 is partly an artifact of fitting a linear trend to daily average risk beliefs as opposed to the underlying survey data. Fitting a flexible polynomial to the actual survey responses reveals a slight downward trend to the left of the discontinuity. There is some evidence for interviewer experience driving a downward trend in responses, but the pattern is not particularly strong.

Second, even accounting for trends in responses due to interviewer experience, we see a sharp jump in responses right at the time of the intervention. The polynomial fits differ by more than 10 percentage points, and the bin-average confidence intervals barely overlap. The numerical results (column 1 of Table 2, panel A) show that this jump is statistically significant: the RD estimate of the treatment effect is 15 percentage points, with a p value of .03.

Another way of assessing the role of interviewer experience is to compare the results with another complex survey module. The questions about sexual activity in the past week were collected using a retrospective sex diary originally developed by Kerwin et al. (2011). In this module, interviewers walked respondents through each of the previous seven days to record details about each sex act on each day as well as other events on that day. The other events included when they woke up and went to sleep, whether they or their partners were menstruating, and alcohol consumption. These other details were included to capture risk factors and to help respondents remember specifics about their sexual activity, similar to an event-history calendar (Belli et al. 2001) or a relationship-history calendar (Luke et al. 2011). This module was complicated to carry out and required the most attention when teaching interviewers to conduct the survey. If the complexity of the questions assessing HIV risk perceptions led to changing response patterns as interviewers gained experience, we might also expect a similar pattern for the sex diary questions.

Panel b of Figure 2 presents an RD plot for the number of sex acts in the past week, as reported on the sex diary module. The left side of the graph (before the HIV information training session) shows no clear trend, although a dip is visible just before the training session. Notably, this dip is matched on the right side of the graph, so that the confidence intervals for the bins just before and just after the discontinuity largely overlap. In column 2 of Table 2, panel A, we show numeric estimates of the size of this RD. Consistent with the graph, there is a small positive but statistically insignificant difference.

The HIV information training session occurred during a six-day gap in the data collection schedule. To assess whether a break in surveying could be creating the differences in the baseline responses, we look for discontinuities in responses between the end of the baseline survey and the beginning of the endline survey; there was a 10-day break in data collection between the two survey waves. Using the control-group data only, panel c of Figure 2 plots an RD for the recorded HIV risk perceptions in the baseline surveys (left side of the graph) versus the endline surveys (right side). The confidence intervals overlap, and the estimated difference (column 1 of Table 2, panel B) is nearly zero and statistically insignificant. We see similar null results for the number of sex acts in the past week from the sex diary, suggesting that a break in surveying per se does not appear to have effects on the recorded survey responses.

A potential threat to the identification of these RD estimates is that there could have been systematic sorting of respondents around the breaks in data collection. If different kinds of respondents were interviewed just before the training session versus just after, it would be incorrect to attribute the 15 percentage point drop in recorded risk beliefs to the effect of the training session. To test for this sort of systematic sorting, columns 3 and 4 of Table 2 present RD estimates for fixed respondent characteristics: gender and age. There are no statistically significant differences in either characteristic for the HIV information training session or for the end of the baseline.

Imbalance

A second potential explanation for the differences between the treatment and control-group beliefs at baseline is imbalance. Although our randomized experiment ensures that the two groups were balanced in expectation, for any given realization of the random assignment, it is possible for them to have differences (Frison and Pocock 1992). Those differences could in turn lead to different beliefs. A particular concern is how well balanced the groups are on sexual activity, which is correlated with risk beliefs (Smith and Watkins 2005). Although the sexual activity variables in panel A of Table A1 (online appendix) are balanced overall, the first five rows show higher values for the control group than for the treatment group. To test for an aggregate balance problem in these variables, we construct an alternate sexual activity index that uses those first five variables alone. The difference is not statistically significant (p = .149). However, even a statistically insignificant difference in this variable could lead to substantively important differences in the belief variables. To mitigate this concern, we control for this alternate sexual activity index in all our regression analyses. Our results do not depend on this choice: the main effects on beliefs from Table 1 are barely changed if we drop this control (Table A2, online appendix), or if we drop the interviewer fixed effects as well (Table A3, online appendix).

Another potential source of imbalance concerns variations in religion, ethnicity, and languages spoken across the two groups. HIV risk perceptions and sexual behavior vary widely by religious denomination in Malawi (Trinitapoli 2009; Trinitapoli and Regnerus 2006) and ethnicity-specific cultural activities, such as initiation rites, are ways that people learn about sexual health (Munthali and Zulu 2007). Administering surveys in an unfamiliar language can lead to item nonresponse and systematic measurement error (Andreenkova 2018). This could be an issue given that all our surveys were administered in Chichewa, but this concern is substantially mitigated by the fact that virtually all our subjects are fluent speakers of either Chichewa or the mutually intelligible language Chinyanja. In the 1998 Malawi census, 96% of households in the study area (TA Mwambo) reported that their most commonly used language was Chichewa or Chinyanja (Minnesota Population Center 2019).

Table A4 in the online appendix shows balance statistics for specific religious denominations as well as ethnic groups. Panel A shows that although the treatment is balanced in terms of the share of Christians and Muslims (Table A1, online appendix), there are important differences across study arms for some specific denominations. In contrast, the treatment is fairly balanced by ethnic group (panel B). However, this pattern may mask potential differences in language abilities within ethnic groups. Because the survey did not ask respondents whether they speak Chichewa at home or whether it was their first language, we use Chichewa-language literacy as a proxy for ability to speak the language. Table A5 in the online appendix shows balance statistics for literacy in Chichewa by ethnic group. There are no large differences, but the 2 percentage point difference for the “other” group is statistically significant.

To account for potential differences in responses driven by these variations in religion and ethnicity, we add indicators for membership in each group to our regression. We also add indicators for a person being from a given ethnic group and also literate in Chichewa. The results are in Table A6 in the online appendix. The effects on measured risk beliefs are essentially unchanged: they remain statistically significant and are slightly larger, on average.

Spillovers

The similarity in responses between the treatment baseline and control endline surveys implies that interviewer knowledge drives our results rather than some other change that occurred at the time of the training session. This similarity could also have arisen through spillovers: if treatment-group respondents told control-group respondents about the information they learned, then we would expect a fall in control-group beliefs. To test for this possibility, we use social network data to count the number of total friends each respondent has as well as the number they have who live in treatment-group villages. We then estimate the following equation:

Yi=α+βTi+ηTotalFriendsi+γTreatedFriendsi+εi,
(3)

where Yi is the respondent's endline risk belief; we also run versions of the regression that break out the spillovers by study arm. Eq. (3) identifies spillover effects on endline beliefs because a respondent's number of treated friends is randomly assigned conditional on their total number of friends (Kremer and Miguel 2007). The results are available in Table A7 in the online appendix. We see no evidence of spillovers onto the control group. Spillovers could also have occurred if control-group respondents sought out information about HIV because they were asked about it. We cannot rule out this possibility, but it is unlikely to have generated the observed empirical pattern. To do so, the control group's information-seeking would need to have led to endline beliefs that were nearly identical to the (measured) baseline beliefs for the treatment group. This is unlikely because the treatment group did not have any time to seek out information about HIV risks prior to answering the baseline questions about risk beliefs.

Mechanisms

Our results show that being surveyed by a more-knowledgeable interviewer causes a decrease in recorded risk beliefs, and that this effect occurs not just for the risks that the interviewer was directly taught about but also for related risks. We explore three possible mechanisms for these spillovers between interviewer knowledge and the (recorded) beliefs of survey respondents.

Priming

Given that the surveys involve a face-to-face conversation between respondents and interviewers, interviewer knowledge could affect recorded responses via priming. We find evidence that trained interviewers primed respondents to give answers that matched the exact numbers used in the training. Table 3 shows regressions of indicator variables that take a value of 1 when respondents answered exactly 10% for each one of the risk belief questions; this is the exact figure that the interviewer training provided as the true value of the HIV transmission risk per year for unprotected sex. Interviewer training makes respondents more likely to answer exactly 10% for the per-act risk of unprotected risk (column 1), even though that is not the true risk.7 We therefore interpret this coefficient as the result of interviewers priming or nudging respondents toward lower responses to all risk belief questions, not just the one corresponding to the information treatment. However, we do not see an increase in reporting an answer of exactly 10% in column 2 (the annual risk), where it is the correct answer. A potential explanation is that respondents have extremely high priors for this figure: the average risk belief is 93%. In columns 3 and 4 (condom-protected sex risks), we see slight reductions in the chance that people report exactly 10%. Because those questions immediately followed the questions about unprotected sex risk, this could be explained by respondents updating their risk beliefs consistently: if condoms lower the risk by a factor X, and the unprotected-sex risk is 0.1, then the condom-protected risk is 0.1X.

These results are consistent with the literature on priming and anchoring, which has shown that mentioning numbers will induce people to give answers to subsequent questions that are more similar to those numbers (Newell and Shanks 2014). This can happen by directly suggesting a potential answer, exposing respondents to peers' responses (Tversky and Kahneman 1974), or even mentioning totally unrelated numbers (Chapman and Johnson 2002; Mussweiler et al. 2000).8 Although all three priming pathways are possible in our context, the first is the most likely. Interviewers were trained to encourage respondents to answer even if they were not sure, and one way they might have done so is to ask leading questions like, “Do you think it might be X%?” It is likely that interviewers who were exposed to the training were more likely to suggest 10% as a possible answer.

Encouraging Guesses

Another opportunity for interviewer knowledge to affect respondents' recorded beliefs comes from the structure of our subjective belief elicitation questions. These were designed such that whenever respondents answered 50% to any risk belief question, a follow-up question asked whether they really thought the answer was 50%, or whether they were just unsure. If respondents said they were just unsure, they were asked for their best guess. This approach was adapted from the U.S. Health and Retirement Survey (HRS), with the goal of reducing the use of 50% as a proxy for respondent uncertainty; see Hudomiet et al. (2011) for a discussion of this technique.

These follow-ups initiated another interaction between the interviewer and respondent, creating an additional opportunity for interviewer knowledge to spill over onto survey responses. Table 4 shows our exploration of that additional interaction, in the case of per-act transmission risks for unprotected sex. We create indicator variables for when respondents answered 50% (column 1) and for when they changed, decreased, or increased their answer when asked the follow-up question (columns 2–4). Columns 5 and 6 also show whether answers decreased or increased, restricting the sample to those respondents who initially answered 50%.

Respondents in the treatment and control groups are equally likely to answer 50% and equally likely to change their answer after the follow-up (column 2). However, respondents who were exposed to this additional interaction were significantly less likely to increase the answer after the follow-up question when they were interviewed by a trained interviewer, as shown in columns 4 and 6 of Table 4. Column 6 shows that conditional on initially answering 50%, respondents exposed to informed interviewers were almost 20 percentage points less likely to increase their answer. This magnitude is large, considering that only about 30% of those in the control group increased their answers after the follow-up question.

We interpret these results as additional evidence that interviewers who were exposed to the information treatment influenced the responses given by communicating the follow-up question in a way that nudged or primed respondents not to increase their answers. Such subtle communication could be anything from a change in tone of voice or body language to the choice of words.9 A specific possibility is that instead of asking whether the number could be more or less than 50%, they asked only if it could be less. We do not believe interviewers did this intentionally: they knew that the purpose of the intervention was to study the respondents' knowledge and behaviors, and their incentive was to record information accurately. Rather, we believe that interviewers inadvertently nudged respondents toward lower answers. Equally possible is that interviewers who were not exposed to the information treatment nudged respondents to provide higher answers, potentially stemming from their own (high) beliefs prior to the information treatment.

Interviewer Knowledge and Respondent Priors

If interviewer knowledge spillovers indeed operate through nudges and priming that take place during the survey interview, we would expect the effects to be smaller for respondents who are more confident in their beliefs. Because our outcomes are measured at the baseline survey, we do not have direct measures of respondents' beliefs in the absence of the knowledge spillovers. However, some of their other characteristics may be useful proxies. Table 5 examines treatment effect heterogeneity by a range of respondent characteristics, estimated using Eq. (2). We observe significant heterogeneity by years of schooling and total assets.

These characteristics are correlated with one another, and thus we may be finding spurious heterogeneity by some characteristics due to omitted variable bias. Therefore, we include all eight interactions in column 9 and add interactions with additional characteristics as well in column 10. In our preferred specification, column 10, only the interaction between treatment and years of schooling remains significant.10 The positive coefficient for years of schooling means that the main treatment effect (the effect of having a more knowledgeable interviewer) is smaller in magnitude for those with more education.

To further explore this finding, we run another set of regressions with the dependent variable being beliefs about HIV transmission risks per unprotected sex act and the independent variables including the treatment interacted with seven different measures of schooling: years of schooling, having completed at least Form 1 or Form 2, and having completed Forms 1–4.11 The regression results can be found in Table A9 in the online appendix. The results suggest that the treatment effects are lowest for people who reached Form 2. Although our survey respondents were all adults, most had not attended secondary school. Just 20% had completed Form 1, and only 17% had completed Form 2.

Form 2 is the point at which students in Malawi are most exposed to information on HIV transmission and sexual health.12 NGOs in Malawi also tend to target students of this age for HIV-prevention interventions; in other African countries, it is also common to target HIV-prevention campaigns toward students early in secondary school (Gallant and Maticka-Tyndale 2004). The narrative to which students in Malawi are exposed in these lectures and courses is that HIV is highly contagious, which should lead to high risk beliefs and high certainty about those beliefs.13

Other people have likely heard about the information provided to students in Form 2—for example, by hearing about it from their friends. Other institutions such as NGOs and church groups attempt to teach about HIV transmission, and so other people may also have strong priors about HIV transmission risks. However, direct exposure to this information in school could lead people to be more certain about it and thus less susceptible to nudges by interviewers.14

Preventing and Mitigating Interviewer Knowledge Effects

Researchers can combat the potential spillover of interviewer knowledge onto recorded subjective beliefs in a variety of ways. First, researchers can try to alter how interviewers are recruited and trained. Recruitment matters because these spillovers can occur whenever interviewers and respondents differ in their knowledge levels. Researchers should recruit interviewers who match the respondent population as closely as possible, particularly in terms of education and exposure to information relevant to the survey questions. This will prevent knowledge effects, assuming that the effect we measure is driven by gaps between interviewers' and respondents' knowledge. Controlling for interviewer fixed effects can help eliminate the effects of any remaining knowledge differences by purging the results of any interviewer-specific patterns. The survey design should also include exact scripts for asking belief questions to minimize selective nudges by the interviewer. Training sessions should emphasize the potential for these spillovers and coach interviewers on how to avoid them.

Second, the problem can be tackled through changes in the design of experiments when studies involve information treatments. Possible solutions include either running the baseline surveys simultaneously across the treatment and control groups or separating the information treatment from the survey data collection entirely. Each strategy has important potential drawbacks. Running simultaneous surveys across study arms creates the possibility that respondents will be given the wrong version of the survey and thus be unintentionally exposed to the information treatment, creating a far worse contamination problem. Running the information treatment separately from the survey—for example, via village meetings—can make it difficult to prevent nontargeted people from receiving the information. For example, diagrams that are distributed as handouts could potentially make their way into the hands of control-group subjects. Thus incorporating information treatments into surveys is likely to minimize information spillovers, not exacerbate them, but at the cost of yielding potentially biased measurements of respondent beliefs. If accurate measures of respondent beliefs are not a main goal of the study, this may be an acceptable risk. For example, if the goal of an experiment is to see how much an information treatment shifts behaviors, then mismeasured beliefs are not a problem even if they affect only one of the study arms. Even when examining treatment effects on risk beliefs is an important goal of the study, interviewer knowledge contamination is a problem only if it interacts with the actual treatment. Apart from information experiments, knowledge spillovers are likely to occur simply because interviewers differ in their knowledge and beliefs. Providing interviewers with a basic level of knowledge about important survey topics could help them do their jobs better and lead to better-quality data.

A third solution to this issue is to collect subjective expectations in a way that avoids any direct interaction with interviewers, such as by using computer-assisted self-interviewing (CASI). This would eliminate any possibility of interviewer knowledge spilling over onto respondents' survey responses. Research on CASI has shown it to be effective in low-literacy settings (Hahn et al. 2003; van de Wijgert et al. 2000). Important limitations exist, however: participants may not be able to clarify questions (NIMH 2007), computers may be received with suspicion in certain settings (Hewett et al. 2004; Mensch et al. 2003), and bystander presence might affect results and should be recorded or controlled (Aquilino et al. 2000). Potdar and Koenig (2005) argued that CASI will not yield more-honest answers if people are not comfortable using computers. In low-literacy settings, audio computer-assisted self-interviewing (ACASI) may work well; Rumakom et al. (2005) showed that it outperforms self-administered questionnaires. However, Soler-Hampejsek et al. (2013) tested ACASI for collecting data on sexual activity in Malawi and find that it still leads to high rates of inconsistency in responses. Similarly, Mensch et al. (2008) showed that face-to-face interviews generate lower rates of inconsistencies in responses than ACASI, as well as stronger correlations between reported sexual behavior and biomarkers for HIV infection. To improve the quality of subjective expectation data in developing countries, more work on adapting CASI and ACASI to overcome these limitations is needed. One promising approach is to use computer tablets to have respondents play simple games that convey information; Tjernström et al. (2019) showed that this approach is successful in a population of Kenyan farmers.

Conclusion

Leveraging a randomized experiment that used interviewers to measure subjective HIV transmission risks and provide information to treatment group participants, we find that interviewer knowledge affects the recorded values of survey respondents' subjective beliefs. This information spillover occurs not only for the information directly given to the interviewers but also for other related risks.

We identify several channels through which these effects happen. They are evident at various points in the survey, including the follow-up questions triggered by respondents answering 50%. This result suggests that additional interactions between interviewers and respondents present the potential for more spillovers. Our evidence suggests that interviewer effects work via priming or nudging rather than interviewers directly revealing information.

We find that interviewer effects are weaker for more-educated people, possibly because those respondents received information about HIV transmission directly at school. This could make them more certain about their prior beliefs than those who heard information secondhand, even if the level of those beliefs is not different across education levels.

Our results have important implications for demographers as well as other social scientists who study subjective expectations themselves or phenomena that are driven by people's subjective beliefs. Subjective expectations have proven to be useful tools for understanding and forecasting the main demographic processes of fertility, mortality, and migration, but these uses rely on being able to measure them correctly. Researchers need to be aware of the possibility that interviewer knowledge will spill over onto respondents' recorded beliefs, which could have substantive effects on results that use those beliefs. Although our findings relate to HIV risk beliefs, interviewer knowledge effects could occur for any subjective expectation where the interviewer knows more than the respondent—including other diseases such as Ebola or COVID-19, and also other domains where subjective expectations play a role, such as conception probabilities, mortality rates, and the returns to migration. Our results were obtained in a setting where interviewers were evaluated based on recording responses correctly; these results may not generalize to settings where interviewers have some interest in recording specific responses.

We suggest methods for correcting this problem at several points during the course of a research project. These include mindful recruiting of interviewers to match the knowledge levels of the respondent population, emphasizing the potential for spillovers in training, and designing the experiment in such a way that interviewers survey both study arms while having the same information set. The most promising way to avoid interviewer knowledge effects is to collect data via CASI or ACASI to reduce the scope of interaction between respondent and interviewer, but both methods have issues with data quality. Interviewer knowledge effects are therefore likely to remain an issue for measuring subjective beliefs in developing-country settings for the foreseeable future.

Acknowledgments

We thank Adeline Delavande, Audrey Dorélien, Jennifer Johnson-Hanks, Maxwell Mkondiwa, Stacy Pancratz, Rebecca Thornton, Emilia Tjernström, Jenny Trinitapoli, Susan Watkins, Rob Warren, Bob Willis, Elizabeth Wrigley-Field, and four anonymous reviewers for their helpful comments and suggestions. This research was supported in part by an NIA training grant to the Population Studies Center at the University of Michigan (T32 AG000221). The authors gratefully acknowledge support from the Minnesota Population Center (P2C HD041023) funded through a grant from the Eunice Kennedy Shriver National Institute for Child Health and Human Development (NICHD). All errors and omissions are our own.

Notes

1

In addition to uncertainty about their material circumstances, people may also be uncertain about their own futures or the correct course of action; periods of uncertainty can cause intersections between aspects of people’s lives that usually seem separate, such as work and romantic relationships (Johnson-Hanks 2017). This uncertainty about the correct course of action is itself shaped by uncertainty about material facts, such as the risks of mortality and miscarriage (Trinitapoli and Yeatman 2018).

2

A small apparent drop (to a prevalence of 9%) in the 2015 DHS was the result of a change in methodology; measured on a consistent basis, the prevalence was essentially unchanged from the 2011 survey.

3

This is part of a systematic pattern of HIV prevention efforts targeting women and excluding men (Watkins 2011).

4

For the per-year question about unprotected sex, the correct answer is 10; for the per-act equivalent, the closest possible answer to the truth is 0. In the absence of condom failures, the correct answer for both the per-year and per-act condom-protected sex questions is 0.

5

These questions measure the respondents’ perceived risk of contracting HIV from various sexual behaviors, not their perceived probability of currently being HIV positive. Our measured probabilities are comparable to other measurements from Malawi. For example, Delavande and Kohler (2012) found a mean per-act risk for unprotected sex of 87%, compared with 83% in our data.

6

The results in Table 1 are qualitatively identical if we omit the sexual activity index or the interviewer fixed effects from the controls (Tables A2 and A3, online appendix).

7

The information treatment mentioned only the annual transmission risk for unprotected sex, and the figure provided for the true risk was 10%. The true transmission risk per act is approximately 0.1%.

8

Similarly, Delavande et al. (2017) found that subjective beliefs are affected by the exact wording of the question—in that research, framing a question as being about mortality versus survival.

9

Ideally, we would have directly observed some interviews to measure the microprocesses that drove the knowledge spillovers. We do not do this for two reasons. First, the study was not designed to measure these spillovers. Second, direct participation in the survey by outsiders, especially White foreigners, can itself affect respondents’ behaviors (Cilliers et al. 2015).

10

The standard errors in this specification may be overstated because of multicollinearity between age, years of schooling, and years sexually active. Table A8 in the online appendix shows that the condition number for the three variables is nearly 18; a figure greater than 10 can indicate that coefficients are unstable. However, the variance inflation factors are all well below the usual cutoff of 10.

11

Form 1 in Malawi is the equivalent of ninth grade in the United States.

12

HIV education was moved from other subjects into a course called life skills in the early 2000s (Chamba 2009). When this change was initially rolled out in 2001–2002, HIV was included only in the secondary school life-skills curriculum. The current life skills curriculum in upper primary school (grades P5–P8) is supposed to include HIV education, but there are many constraints to implementation (Chirwa and Naidoo 2014). Based on conversations with Ministry of Education officials in Malawi in 2012, at that time HIV education was done only in secondary schools. An examination of the textbooks for the secondary-school life skills courses revealed HIV content in all four grades, but HIV transmission risks were covered only in Form 2 (Kadyoma et al. 2012).

13

This idea is supported by the correlation between risk beliefs and schooling for the control group: more schooling is associated with higher priors (see Table A10, online appendix).

14

Another potential explanation for the fact that more-educated people respond less to the treatment is that education may make people more confident and better able to withstand influence from outsiders. We cannot directly test this explanation against the effect of HIV education on the strength of people’s priors.

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