Using social contact data to improve the overall effect estimate of a cluster-randomized influenza vaccination program in Senegal
Gail E. Potter, Nicole Bohme Carnegie, Jonathan D. Sugimoto, Aldiouma Diallo, John C. Victor, Kathleen Neuzil, M. Elizabeth Halloran
UUsing social contact data to improve the overall effect es-timate of a cluster-randomized influenza vaccination pro-gram in Senegal
Gail E. Potter
The Emmes Company, Rockville Maryland, USA
Nicole Bohme Carnegie
Montana State University, Bozeman Montana, USA
Jonathan D. Sugimoto
Epidemiologic Research and Information Center, Veterans Affairs Puget Sound HealthCare System and Fred Hutchinson Cancer Research Center, Seattle Washington, USA
Aldiouma Diallo
Institut de Recherche pour le D ´eveloppement, Niakhar Senegal
John C. Victor
PATH, Seattle Washington, USA
Kathleen Neuzil
University of Maryland School of Medicine, Baltimore Maryland, USA
M. Elizabeth Halloran
University of Washington Department of Biostatistics and Fred Hutchinson Cancer Re-search Center, Seattle Washington, USA
Summary . This study estimates the overall effect of two influenza vaccination programsconsecutively administered in a cluster-randomized trial in western Senegal over the courseof two influenza seasons from 2009-2011. We apply cutting-edge methodology combin-ing social contact data with infection data to reduce bias in estimation arising from con-tamination between clusters. Our time-varying estimates reveal a reduction in seasonalinfluenza from the intervention and a nonsignificant increase in H1N1 pandemic influenza.We estimate an additive change in overall cumulative incidence (which was 6.13% in thecontrol arm) of -0.68 percentage points during Year 1 of the study (95% CI: -2.53, 1.18).When H1N1 pandemic infections were excluded from analysis, the estimated change was-1.45 percentage points and was significant (95% CI, -2.81, -0.08). Because cross-clustercontamination was low (0-3% of contacts for most villages), an estimator assuming nocontamination was only slightly attenuated (-0.65 percentage points). These findings areencouraging for studies carefully designed to minimize spillover. Further work is neededto estimate contamination – and its effect on estimation – in a variety of settings.
Keywords : additive hazards, cluster-randomized, contamination, interference, over-all effect, social network, spillover a r X i v : . [ s t a t . A P ] J un . Background Influenza is a seasonal respiratory infection that causes a substantial global burden ofmorbidity and mortality, particularly among children. One meta-analysis estimatedthat in 2018 the global burden of influenza among children under 5 was 109.5 millioninfluenza episodes, 870,000 hospital admissions for influenza virus-associated acute lowerrespiratory infection, and between 13,200 and 97,200 deaths (Wang et al., 2020).In this paper, we use state-of-the-art methodology to estimate the overall effect ofannual influenza vaccination of children age 6 months to 10 years —relative to poliovaccination—on the incidence of influenza in western Senegal. In one analysis of surveil-lance data in Senegal, 60% of laboratory-confirmed influenza cases were in children under5 years of age, and 75% were in children under 16 years. While the majority of the pop-ulation served by the surveillance clinics were children 0-15 years of age, this suggeststhat a vaccination campaign focusing on young children has the potential to prevent thebulk of influenza case burden on health clinics in Senegal (Niang et al., 2012).The study that produced the data analyzed in this paper was a cluster-randomizedtrial of 20 villages in the Niakhar Demographic Surveillance System (DSS) zone. Villageswere assigned to vaccination of children with either inactivated trivalent influenza vaccineor an inactivated polio vaccine as an active control. There is no national recommendationfor routine influenza vaccination in Senegal, hence off-study vaccination was expected tobe minimal. The trivalent influenza vaccine has been shown to be efficacious in reducinginfluenza infection in children in other settings (Madhi et al., 2014; Zimmerman et al.,2016); the Niakhar study was testing the effectiveness of widespread immunization ofchildren to reduce the community burden of influenza. The primary analysis for this trialanalyzed the total effect of the intervention (Diallo et al., 2019). The total effect is basedon comparing outcomes of treated people in treated villages to those of untreated peoplein control villages and accounts for protection conferred by receipt of the vaccine as wellas from reduction in exposure resulting from vaccination of others in the community. Inthis paper, we consider the overall effect of the intervention. The overall effect is basedon comparing the average outcome in treated villages to the average outcome in controlvillages, so takes into account the effect of the community intervention on both treatedand untreated people (Halloran et al., 1991).The total and overall effects are of interest scientifically because of the presence ofinterference in infectious disease processes. Interference —when one person’s treatmentcan affect another’s outcome—is both a boon to disease prevention and a classic infer-ential problem in infectious disease research. The benefit: the very nature of the processinduces dependence between people’s outcomes, and treating one person may preventanother’s infection. The drawback: observations are no longer independent, and mostmainstream causal inference tools cannot account for the induced dependence. The mainapproach to dealing with interference is to use cluster-randomized trials (CRT), whichallow for dependence within cluster. The assumption of no interference that would bemade in a traditional individually-randomized controlled trial is thus weakened to partialinterference —an assumption of no interference between clusters (Sobel, 2006). Viola-tion of the partial interference condition is referred to as contamination (Hudgens andHalloran, 2008).Typical methods for estimating the overall effect assume partial interference (e.g., Hal-2oran and Struchiner (1991); Liu and Hudgens (2014)). However, for socially contagiousoutcomes such as infectious diseases, partial interference will not be satisfied if membersof treated clusters come in contact with people from untreated clusters (and vice-versa).Recent methodological developments have explored incorporation of measured contam-ination data into estimation and testing methods to explicitly adjust for interference.See Halloran and Hudgens (2016) and S¨avje et al. (2020) for reviews of recent efforts todevelop causal inference methods that account for partial interference as well as moregeneral forms of interference. Some of these methods incorporate detailed social networkstructure (Eckles et al., 2016; Toulis and Kao, 2013; Aronow et al., 2017; Ugander et al.,2013), but such detailed network data is not always available or easy to obtain. In thisstudy, the complete social network was not observed, but information was collected onrates of contacts within and between villages. Most relevant to this data structure andto our interest in the overall effect is a method developed by Carnegie et al. (2016). It iswell known that when contamination is present, the overall effect estimate is attenuated.The authors developed a method to explicitly incorporate measured contamination datainto the estimation procedure and demonstrated that this adjustment removes the at-tenuation of the overall effect estimate. We apply this method to estimate the overalleffect accounting for cross-cluster contamination and compare it to the estimate thatwould be obtained assuming partial interference.This paper continues as follows. In Section 2, we describe the data; in Section 3 wedescribe the causal model and data preparation. The results of causal effect estimationare given in Section 4, and implications and limitations are discussed in Section 5.
2. Data Collection
The data were collected in a cluster-randomized clinical trial conducted in the NiakharDemographic Surveillance System (DSS) zone from 2009-2011. This study, ClinicalTri-als.gov NCT00893906, is closed, and the primary results for the first year of the trialhave been published (Diallo et al., 2019). Among thirty villages in the Niakhar DSSzone, twenty were selected as clusters for inclusion in the trial and randomized in a 1:1ratio to receive a blinded vaccination campaign of either inactivated trivalent influenzavaccine (TIV) or inactivated poliovirus vaccine (IPV) as an active control. From hereon, villages that received TIV will be referred to as “treated” and those that receivedIPV as “control”. The same villages were followed for two influenza seasons (2009-2010and 2010-2011). Different formulations of trivalent influenza vaccine were given duringthe two years; the second formulation included the H1N1 2009 “swine” pandemic strainof influenza, but the first formulation did not.Within each treatment group the goal was to vaccinate up to 5,000 children 6 monthsto 10 years of age in the following approximate numbers per age-group: 1,270 children6-35 months of age; 2,835 children 36 months to 8 years of age; and 895 children 9-10 years of age. Vaccinees received age-specific doses. In villages assigned to receiveinfluenza vaccine, 3,906 (78.1% of target number for vaccination) were vaccinated withDose 1, while 3,843 (76.9% of the target) of those in control villages were. These numberscomprised 66.6% and 66.2% of age-eligible children, respectively.The primary outcome of the study was laboratory-confirmed symptomatic influenza3nfection. A combination of active and passive surveillance was used for the primaryoutcome in the Niakhar DSS zone. In this geographic area, residences are organized incompounds, clusters of dwellings typically housing an extended family. For the twentyvillages randomized in the study, field workers visited compounds on a weekly basisto inquire about the occurrence of influenza symptoms. If the person had experiencedinfluenza-like illness (defined as fever or feverishness, cough, sore throat, nasal conges-tion, and/or rhinorrhea) in the past 7 days, then the field worker consented them intothe surveillance study and documented symptoms and epidemiologic data. Cases ofinfluenza-like illness were reported to the study center, and nasal and throat swab spec-imens were collected. In addition, individuals seeking medical care at any of the threeNiakhar DSS health posts at any time throughout the year were assessed by healthpost medical staff or a study physician to determine if the person had influenza-like ill-ness. These individuals were consented into the surveillance study, their symptoms weredocumented, and nasal and throat swab specimens were obtained for influenza testing.When individuals with influenza-like illness enrolled into the surveillance study, theyalso responded to a survey about their travel and social contact patterns during the priorthree days. For each day, the respondent provided the number of people she contacted inher own compound in the morning and the afternoon/evening. In addition, she indicatedyes or no to whether she had visited a list of locations: another compound (up to fivecould be identified in the survey), a market, mosque or church, field, school, sports fieldor public place, outside the study zone, or another location. For each location visited,the village identification code (and compound identification number, where applicable),the time of day visited (AM, PM, or both), and the number of persons the respondentspoke with during the visit were recorded. For additional details, refer to the examplesurvey form in the Appendix.Village of residence was recorded during quarterly censuses conducted by the NiakharDSS (Delaunay et al., 2002, 2013). If participants moved during the trial, their departuredate, arrival date, and village of their new residence were recorded. Those who moved asecond time had their departure date (but not residence after second move) recorded aswell. The cleaning that was performed after receiving the residence data from the DSSis described in the Appendix.
3. Analytic Methods
In this paper, we consider two estimators for the overall effect of influenza vaccinationrelative to polio vaccination. The first estimator assumes partial interference (i.e., nocontamination), and we refer to it as the no-contamination estimator . The second explic-itly accounts for interference generated by contacts to villages of the opposite treatmentassignment; we refer to this as the contamination-adjusted estimator .To account for contamination, we use the method developed in Carnegie et al. (2016).This approach uses an additive hazards model (Aalen, 1989) for the time to first eventbut includes a modified treatment variable to account for contacts occurring betweenclusters in a cluster-randomized trial. Typically, the treatment variable Z is a binaryindicator such that Z = 1 for participants from treated villages and Z = 0 for those from4ontrol villages. This is the treatment variable used to calculate the no-contaminationestimator. To account for interference between clusters, we use an alternate treatmentvariable M , which is the proportion of contacts of residents of the participant’s villagethat are with treated villages. It can be thought of as a village-level intensity of exposureto the treatment conditions, and will range from 0 (if all contacts reported in a villageare with control villages) to 1 (if all of the contacts reported in a village are withtreated villages). Note that if no contamination is present, then this modified treatmentvariable reduces to the binary treatment variable used to calculate the no-contaminationestimator.The additive hazards model used to obtain the no-contamination estimator for anindividual in cluster j is λ j ( t | Z ) = β ( t ) + β Z ( t ) z j , where z j is a binary treatment indicator for cluster j . The contamination-adjustedestimator is obtained from the following model for individual in cluster j : λ j ( t | M ) = β ( t ) + β M ( t ) m j , where m j is the total percentage of contacts of susceptibles in cluster j that are withtreated clusters. Note that m j is a cluster-level variable, but the model is an individual-level model, with individuals in the same cluster taking the same value for m j .The coefficient of interest in the additive hazards model—corresponding to the treat-ment variable—is potentially time-varying. For this reason, we report both that coeffi-cient (visually) and the difference in cumulative hazard of influenza due to the treatment.Because the cumulative hazard is low, this is approximately equal to the difference incumulative incidence due to treatment. The time-varying coefficients are visualized bydisplaying the value of their integrals, (cid:82) t β Z ( t ) dt and (cid:82) t β M ( t ) dt , as a function of time.These integrals represent the cumulative hazard difference over the time interval [0,t] andare estimated using the nonparametric approach proposed by Aalen (1989). Since thenonparametric estimation approach (based on step functions) produces curves that arenot always differentiable, the additive treatment effect is not explicitly estimated, butit is visualized as the slope of the curve (Aalen, 1989). Estimation is implemented withthe aalen function in the R package timereg to fit the additive hazards models (Scheikeand Zhang, 2011; R Core Team, 2017), and the R code used is provided in the Appendix.The effects are displayed together with confidence intervals based on robust (sandwich)standard errors which take into account the clustering; these are also provided by the aalen function.The estimand of interest, which we will denote β ( t ), is the population-averaged differ-ence in hazard of laboratory-confirmed symptomatic influenza infection associated witha change from 0% to 100% exposure to treatment. While ˆ β Z ( t ) is a consistent estimatorfor β ( t ) in the absence of contamination, Carnegie et al. (2016) proved that ˆ β M ( t ) is aconsistent estimator for β ( t ) in the presence of measured contamination.This additive hazards model for interference has a natural correspondence to a deter-ministic compartmental model such as an SIR model (Susceptible-Infectious-Recovered;see, e.g., Keeling and Rohani (2008)). This relationship results from the assumption ofthe compartmental model that the transmission rate is a product of the contact rate5nd the per-contact transmission probability. We provide further details on this re-lationship in the Appendix. This correspondence supports application of our methodto influenza, which is frequently modelled with an SIR or SEIR (Susceptible-Exposed-Infectious-Recovered) model (Coburn et al., 2009). Since the length of the exposurestate is irrelevant to modelling disease-free survival, this method gives identical resultsunder SIR and SEIR assumptions (Carnegie et al., 2016).While Cox regression is frequently used for survival analysis, the Cox proportionalhazards model does not share this natural correspondence to epidemic compartmentalmodels. Another advantage that the additive hazards model has over the proportionalhazards model is collapsibility, which implies that the treatment effect is the causal effectof interest whether or not covariates are included in the model.Analyses were performed separately for Year 1 and Year 2 of the study. Inputs to theadditive hazards model are the time to event (or censoring) for each person, infectionstatus, and the percentage of contacts to treated clusters. Calculation of time-to-eventfor each survey year is described in detail in the Appendix. One irregularity in datacollection is noteworthy: during Year 2 of the study, household surveillance was notperformed during a strike of field workers that lasted from Jan 3, 2011 through Feb 18,2011. This could introduce bias since the rate of reporting infections during householdvisits (as opposed to health posts) was higher in treated than control villages (87.5%and 83%, respectively). To prevent such bias, we analyzed a shorter time interval forYear 2 by censoring observations at the start of the strike. The full Year 2 estimates areincluded as a secondary analysis. The treatment exposure value for village j is the proportion of contacts that susceptiblepeople in village j made with people in treated clusters. For control villages, this variableis the percentage of contacts to treated villages (the contamination estimate itself). Fortreated villages, however, the treatment exposure value is one minus the percentage ofcontacts to people in control villages (i.e., one minus the contamination estimate).The contact survey defined a “contact” as a conversation occurring between twopeople in the same location. The contact survey collected numbers of contacts in variouslocations at two time points (AM and PM) for three consecutive days: the survey dayand the two prior days. Numbers of contacts recorded on the survey day are subjectto truncation bias because most surveys were administered in the morning and excludecontacts occurring after the time of the survey. Contact patterns for asymptomaticparticipants are included in the data since some participant’s symptoms began on theday of or the day before the survey. We analyze only data collected from the time pointtwo days before the survey date because this time point includes more reports fromasymptomatic people. Additionally, a social network analysis of these data found nodifference in numbers of contacts recorded the day before the survey vs. two days prior– so there is no evidence that the earlier time point is subject to recall bias (Potter et al.,2019).The survey did not elicit how many of the morning contacts were repeated in theafternoon/evening. We analyze contacts reported in the morning as treatment exposurerates were similar between morning and afternoon contacts (Appendix Table 4).6ur treatment exposure estimates take into account the percentage of contacts re-ported while the respondent was visiting treated villages (Section 3.2.1) and the per-centage of contacts reported in the respondent’s own home (compound) that occurredto visitors from treated villages (Section 3.2.2). For each village, we calculated the percentage of contacts reported while respondentsfrom that village were located in treated villages. The denominator was the sum ofcontacts reported by village residents; the numerator was the sum of those contactswhose reported location was a treated village. Contacts reported to villages that arenot in the trial were included in the denominator and are treated the same as contactsto control villages. The numerator included contacts reported in the respondent’s owncompound if the respondent was a resident of a treated village. For participants whomoved mid-study, the village of residence is the reported village of residence at the timeof the contact survey.We initially calculated treatment exposure rates using reports by asymptomatic peo-ple only, assuming that this would be more representative of behavior when uninfectedand that the symptomatic people would travel less. We compared these to the es-timates based on reports by symptomatic people and (counterintuitively) found thatsymptomatic reports included slightly higher rates of contacts to clusters of the oppositetreatment assignment (Appendix Tables 5 and 6). This is likely because cross-clustercontact rates are fairly low overall and because less data is available for asymptomaticreports, so the small amount of data from asymptomatic respondents includes fewer non-zero counts. Therefore we combined data from both asymptomatic and symptomaticpeople to estimate the treatment exposure variable more precisely.
The above approach assumes that the location of a contact reported by the respondentindicates the residence of the person contacted. As such it does not account for visitorsto one’s compound from a cluster of the opposite treatment assignment, so may under-estimate cross-cluster exposure. To incorporate exposure from visitors into the estimate,we will define some notation and first consider the estimates for people living in controlclusters. Suppose there are n j people living in cluster j , and let D i denote the numberof contacts reported by person i who lives in cluster j . Let T i denote the number of con-tacts person i has made in a location in a treated cluster. Let p j denote the proportionof contacts in cluster j to people from treated clusters. We have estimated this asˆ p j = (cid:80) n j i =1 T i (cid:80) n j i =1 D i We need to update the numerator to include contacts occurring within the respondent’sown compound to visitors from other clusters. We can use estimates reported by thesevisitors, rather than by respondents in cluster j , to obtain this information. Let V trt,j denote the total number of contacts reported by people in any treated cluster during their7isits to compounds in cluster j . While these contacts contribute to the denominatorin the above estimator, they do not contribute to the numerator (because they occurredwithin the respondent’s assigned cluster), but should. Therefore, when j is a controlcluster, our updated estimate incorporating this exposure is:ˆ p j = (cid:80) n j i =1 T i + V trt,j (cid:80) n j i =1 D i = (cid:80) n j i =1 T i (cid:80) n j i =1 D i + V trt,j (cid:80) n j i =1 D i The rationale for this adjustment is explained in detail in Potter et al. (2019), and anexplanation tailored to this setting is provided in the Appendix.An analogous update is needed for residents of treated clusters. For these respondentswe need to account for visits from members of control clusters. Letting V ctr,j denote thetotal number of contacts reported by people in any control cluster during their visits tocompounds in cluster j . When j is a treated cluster, our updated estimate incorporatingthis exposure is: ˆ p j = (cid:80) n j i =1 T i − V ctr,j (cid:80) n j i =1 D i = (cid:80) n j i =1 T i (cid:80) n j i =1 D i − V ctr,j (cid:80) n j i =1 D i The submitted contact surveys had a large number of missing fields, which, if not mod-elled appropriately, could create bias in the estimates of cross-cluster exposure. Forlocations visited outside the home two days before the survey, 24% are missing time ofday, 59% are missing the number of people contacted, and 32% do not have a villagenumber recorded. The survey design elicited at-home contacts differently than thosethat occurred outside the home: the numbers contacted at home in the morning andin the afternoon/evening were recorded, so village and time point were not collected asseparate variables. Furthermore, in 60% of analyzed surveys, the number contacted athome in the morning was missing.We used multiple imputation, expanding on the procedure used in another analysisof this data set (Potter et al., 2019) to adjust for missing contact data. For outside-home locations, up to four variables may be missing: the response to “Was this locationvisited?”, the time of day (AM or PM) the location was visited, the number of peoplecontacted at that location, and the village where the location is located. The responsesto whether the location was visited were imputed based on a log binomial regressionmodel with location type, symptom status, and age category as predictors, stratifiedon day relative to the survey day. Missing times were imputed by sampling from thedistribution of non-missing times for that location type. To impute missing numbers ofcontacts for non-home locations, we fit a negative binomial distribution to the reportedcontact numbers, predicting the number contacted by the location, symptom status,time of day, and age category. For at-home contacts, we predicted number contactedbased on symptom status, time of day, day relative to survey day, age category, andgender. Missing villages for out-of-home contacts were sampled from the observed dis-tribution of visited villages for the respondent’s village of residence, combining data fromboth survey days. As such we are assuming the data are missing at random; in otherwords, the predictors in our imputation model are sufficient to explain the distributionof unobserved values (Rubin, 1976). 8 able 1.
Percentages of contacts with residents of treated clusters based on (1)contacts reported while located in treated clusters, (2) contacts in the respondent’sown compound to visitors from clusters of the opposite treatment assignment,and (3) total percentages of contacts to residents of treated clusters (treatmentexposure).
Treatment Percent reported Percent TreatmentVillage Assignment in treated clusters from visitors exposureKalome Ndofane Vaccine 100 0 100Ngayokheme Vaccine 99 0 99Ndokh Vaccine 99 1 99Ngangarlame Vaccine 99 0 99Diohine Vaccine 99 0 98Mokane Ngouye Vaccine 99 1 98Nghonine Vaccine 98 2 96Logdir Vaccine 95 2 93Darou Vaccine 96 5 90Poudaye Vaccine 93 2 90Ngalagne Kop Control 0 0 0Mboyene Control 0 0 0Poultok Diohine Control 0 0 0Bary Ndondol Control 0 1 1Toucar Control 1 0 1Gadiak Control 2 0 2Godel Control 2 0 2Khassous Control 3 0 3Kothioh Control 3 0 3Meme Control 14 0 14
We created twenty imputed data sets, calculated percentages of contacts to treatedclusters for each village in each of these imputed data sets, and combined the percentagesusing standard rules for combining multiply imputed data (Rubin, 1987).
4. Results
Table 1 displays the treatment exposure estimates for each village enrolled in the trialbased on the multiply imputed data. For each village, we display the percentage ofcontacts reported when the respondent visited treated villages, the estimated percentagesof contacts from visitors from villages of the opposite treatment assignment, as well asthe overall percent of contacts to treated villages, which was used as a covariate in thecontamination-adjusted model. The overall percentages are generally close to zero forcontrol villages and close to 100 for treated villages, with a few exceptions.Our estimated time-varying treatment effects (both unadjusted and contamination-adjusted) are displayed in Figure 1 for Year 1 of the study. Since the graph displaysthe integral of the time-varying coefficients, the slopes of the curves represent the coeffi-cients themselves - the estimated difference in hazard rates between vaccine and controlvillages at each point in time. Both models indicate that the influenza vaccination pro-gram reduces influenza through September. Then it is estimated to be ineffective until9 ig. 1.
Estimated effects of the influenza vaccination program for Year 1 (July 2009 - May 2010)of the study. The time-varying effects are the difference in cumulative incidence of lab-confirmedsymptomatic influenza infection between groups, measured in percentage points. −3−2−101 Date (cid:243)ı T b ( t ) d t Aug 1 Sep 1 Oct 1 Nov 1 Dec 1 Jan 1 Feb 1 Mar 1 Apr 1 May 1 Jun 1No−contamination estimatorContamination−adjusted estimator
February (since no influenza was circulating), after which the program is associated withan increase in the hazard of influenza for a month. This latter time period coincides withthe appearance of the A (H1N1) (2009) pandemic strain of influenza (A/H1N1pdm09)in the community, which first appeared in late January 2010. See Figure 2 for a graphof numbers of infections by influenza type and week.Figure 3 presents the two estimators excluding cases of A/H1N1pdm09 influenza fromthe analysis. Its slope represents the instantaneous effect of the influenza vaccinationprogram on the hazard of infection for non-pandemic strains only.Figure 4 presents results for the second year of the study. This is the first publicationof Year 2 estimates for this trial, as the primary analysis only analyzed Year 1 (Dialloet al., 2019). As mentioned previously, the formulation of the vaccine provided duringthis year included the A/H1N1pdm09 strain, unlike the formulation provided in Year 1.Figure 5 shows that substantially fewer infections were detected this year. We expectreports to be lower during the strike (Jan. 1 - Feb. 18, 2011) since household surveillancewas not conducted during that time, but frequencies prior to the strike were also muchlower than in Year 1. Figure 4 shows that after a delay of approximately two monthswith little effect, the two estimators both indicate that influenza vaccination reducedincidence in Year 2. The delay is likely due to the relative sparsity of cases in the firstweeks of the year. The start of the strike mentioned in Section 3 is shown as a vertical10 ig. 2.
Weekly observed incidence of lab-confirmed symptomatic influenza infections by typeduring Year 1 (July 2009 - May 2010) of the study.
Date N u m be r o f i n f e c t i on s Influenza Type
Seasonal (A/H3N2 or B) A/H1N1pdm09 line.Table 3 displays the estimated difference in cumulative hazard of lab-confirmed symp-tomatic influenza infection due to the influenza vaccination program. These are simplythe values of the curves in Figures 1, 3, and 4 for the last day of follow-up, and theconfidence intervals correspond to those in the figures. Because the cumulative hazardis low, the difference in cumulative hazard is approximately equal to the difference incumulative incidence due to treatment.The overall incidence rates are displayed in Table 2 for comparison purposes. Sincethe overall incidence in the control group was 6.13%, our estimated additive effect of-0.68% indicates the vaccination program prevented about 11% of influenza infections.Our two estimators and confidence intervals are similar, but the no-contaminationestimators are slightly attenuated because they assume no mixing between clusters ofopposite treatment assignments. The confidence intervals for the contamination-adjustedestimator are slightly wider, reflecting the loss of information caused by contamination,but again, are similar. For Year 1 both effects are not statistically significant when allinfections are included but achieve significance (barely) when A/H1N1pdm09 infectionsare excluded. The Year 2 estimates are statistically significant. The Year 2 estimatesare interpreted differently as they cover different time intervals; a higher difference incumulative incidence is expected for the longer interval if vaccine performance stays11 ig. 3.
Estimated effects of the influenza vaccination program for Year 1 (July 2009 - May2010) of the study, excluding H1N1 2009 pandemic influenza infections. The time-varying ef-fects are the change in the cumulative hazard of lab-confirmed symptomatic influenza infection,measured in percentage points. −3−2−101 Date (cid:243)ı T b ( t ) d t Aug 1 Sep 1 Oct 1 Nov 1 Dec 1 Jan 1 Feb 1 Mar 1 Apr 1 May 1 Jun 1No−contamination estimatorContamination−adjusted estimator ig. 4. Estimated effects of the influenza vaccination program for Year 2 (July 2010 - May 2011)of the study. The time-varying effects are the change in the cumulative hazard of lab-confirmedsymptomatic influenza infection, measured in percentage points. −3−2−101 Date (cid:243)ı T b ( t ) d t Aug 1 Sep 1 Oct 1 Nov 1 Dec 1 Jan 1 Feb 1 Mar 1 Apr 1No−contamination estimatorContamination−adjusted estimator Beginning of strike ig. 5. Weekly observed incidence of lab-confirmed symptomatic influenza infections by typeduring Year 2 (July 2010 - May 2011) of the study.
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of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strikeEnd of strike050100150200 Aug 1 Sep 1 Oct 1 Nov 1 Dec 1 Jan 1 Feb 1 Mar 1 Apr 1
Date N u m be r o f i n f e c t i on s Influenza Type
Seasonal (A/H3N2 or B) A/H1N1pdm09
Table 2.
Incidence of influenza by treatment group and study year.
Study Year Treated Control AllYear 1, all infections 999/18200 (5.49%) 1076/17550 (6.13%) 2075/35750 (5.8%)Year 1, excluding A/H1N1pdm09 630/18200 (3.46%) 833/17550 (4.75%) 1463/35750 (4.09%)Year 2, all infections 224/18547 (1.21%) 341/17815 (1.91%) 565/36362 (1.55%) the same. While bias from the strike starting Jan 1, 2011 does not impact the Year2 estimate censored at that date, the uncensored one could be biased. The rates ofreporting infections during health post visits (as opposed to household visits) were 12.5%in treated villages and 17% in control villages, so the vaccine effect could be overestimatedby including a time interval with only health post visits. Because the rates are similar,and because the strike lasted 49 days of a 320-day follow-up period, the bias is likelylow.
5. Discussion
We have applied state-of-the art statistical methodology to estimate the overall effectof a trivalent influenza vaccine program in Niakhar, Senegal. This method incorporatessocial contact data together with treatment and infection data to reduce the bias in thisestimate caused by interference between clusters. Ours is the first study we know ofapplying this novel method to contact and infection data collected jointly in a clinical14 able 3.
Estimated difference in cumulative incidence of influenza (measured in percent-age points) due to the influenza vaccination program.
Contamination-Adjusted No-ContaminationStudy Year Estimate 95% C.I. Estimate 95% C.I.Year 1, all infections -0.68 [-2.53, 1.18] -0.65 [-2.40, 1.09]Year 1, excluding A/H1N1pdm09 -1.45 [-2.81, -0.08] -1.35 [-2.64, -0.06]Year 2 (July - Dec 2010) -0.59 [-1.01, -0.17] -0.59 [-0.99, -0.19]Year 2 (July 2010 - May 2011) -0.73 [-1.16, -0.31] -0.73 [-1.14, -0.32] trial setting. We produce the first estimates of contact rates between clusters of op-posite treatment assignments for this trial and the first, to our knowledge, in Senegal.Our results provide insight into the extent to which the standard assumption of partialinterference is violated in a trial of this structure and of the impact of this violation onestimates.Our time-varying effect estimates show that in Year 1 of the study, the treatmentprogram – vaccination of children – reduced lab-confirmed symptomatic infection withseasonal influenza in the community. Our estimates found the treatment program tobe associated with a small (though statistically insignificant) increase in infections withA/H1N1pdm09 influenza. While other studies have found evidence for this relation-ship (Cowling et al., 2010; Skowronski et al., 2010), others have found evidence that triva-lent influenza vaccination protects against A/H1N1pdm09 infection. A meta-analysis of17 studies, including the two just mentioned, found that the overall evidence points to aprotective effect, but the authors cautioned against drawing a solid conclusion becausemost of the studies reviewed were observational (Yin et al., 2012). Two subsequent ran-domized trials also found evidence for a protective effect (Cowling et al., 2012; Mcbrideet al., 2016).The extent of contamination measured in our data resulted in little difference be-tween the cumulative incidence for the estimator adjusting for contamination and theone assuming no contamination. The latter was smaller because, as has been foundin other studies, contacts to members of clusters of the opposite assignment attenuatethe estimate of the overall effect from what it would have been with no contamina-tion (Carnegie et al., 2016; Tiono et al., 2013; Wang et al., 2014). The model we imple-ment explicitly adjusts for contamination, correcting this under-estimation. In addition,the standard errors associated with this adjusted estimator were larger than those for theno-contamination estimator because information available to estimate the effect of thetreatment program decreases as mixing increases – so these intervals accurately reflectthe decrease in information from zero mixing to the small level of mixing we observed.As noted in Carnegie et al. (2016) the approach we have used to estimate the overalleffect fails when 50% of contacts occur to clusters of the opposite treatment assignment.This is because our method uses the contact rates between clusters to differentiate treat-ment status, so no information distinguishing clusters is available for our approach whenmixing is at 50%.The level of contamination in the data was fairly small: the percent of contacts toclusters of the opposite treatment was between 0% and 3% for most villages, althoughthere were some outliers, with 14% being the largest observed value. To our knowledge,15hese are the first data-based contamination estimates of this type for Senegal. Our find-ing that this amount of contamination has a negligible impact on the effect estimate maybe encouraging for researchers who carefully define cluster selection to minimize contam-ination, as was done in this study. The villages in this trial were separated by physicalboundaries such as bodies of water and roads, and their definition as cultural/politicalentities also has an impact on social contact behavior.Our study has several limitations. First, the extent of missing data in the contactsurvey is substantial. As noted previously, for locations visited outside the home two daysbefore the survey, 24% are missing time of day, 59% are missing the number of peoplecontacted, and 32% do not have a village number recorded. We used multiple imputationto adjust for missing data, but bias is still a risk. For example, if numbers of peoplecontacted in villages of the opposite assignment were higher for participants who didnot respond to this question than for those who responded (and who have similar valuesfor covariates included the multiple imputation model), then the true contaminationvalues may be higher than our predicted values. This would mean that the magnitudeof the true overall effect is larger than our estimate. If, on the other hand, we haveoverestimated contamination, then the true effect may be closer to our no-contaminationestimate (closer to -0.65 than -0.68). Implementation of similar surveys in the futuremay be improved by a diary-based approach, in which participants fill out a paperdiary as they go about their day (Mossong et al., 2008; B´eraud et al., 2015; Melegaroet al., 2017; Johnstone-Robertson et al., 2011; Horby et al., 2011; Fu et al., 2012; Readet al., 2014). In addition we would recommend consideration of procedures employedby Kiti et al. (2014), including conducting a pilot study, providing wristwatches withpre-programmed alarms to remind participants to fill out their diary, and by assigning“shadow” respondents to fill out the diary for illiterate participants. Alternately andpotentially more accurate would be an approach using remote wireless sensors to detectwhen two participants are located within 1.5 meters of each other - a distance at whichinfection may be transmitted (Kiti et al., 2016; Stehl´e et al., 2011; Fournet and Barrat,2014; Barclay et al., 2014; G´enois et al., 2015).A second limitation of the contact survey is that contacts were reported separately formorning and afternoon time intervals without recording the extent of overlap. Becausemorning and afternoon contamination estimates were similar, either is likely a reasonableapproximation to the percent of contacts to clusters of the opposite assignment duringa full day. However, it would be preferable to record numbers of contacts throughoutthe entire day in future studies. We also note that contacts recorded on the day ofthe survey did not contribute to analysis since truncation bias arose from the fact thatmost surveys were conducted in the morning. A diary-based approach would avoid thisproblem, or if interviews are conducted, they should focus on days before the surveyday. The literacy level of the population of interest should be considered in choosing theoptimal approach to collect contact data.Finally, the type of contacts recorded in our study emphasize transmission via largedroplets (in close proximity) rather than by aerosol droplets which have a longer range.While many studies have investigated the importance of fomite transmission, physicalcontacts, small droplets, and aerosol droplets for transmission, their relative importanceis not well understood (Weber and Stilianakis, 2008; Cowling et al., 2013; Teunis et al.,16010; Wei and Li, 2016; Kutter et al., 2018). Although the contact survey had lim-itations, it seems unlikely that the true contamination levels are higher enough thanour estimated ones to substantially impact the efficacy estimates. Therefore we believethat our conclusion that contamination was low and had only a small impact on efficacyestimates is valid. However, careful design of the contact survey would improve dataprecision if a similar approach is applied when clusters are smaller and closer. We wouldrecommend such studies as future research. For example, a compound-based random-ization scheme had been considered for this trial design instead of village-based, andin fact, the protocol allowed for both possibilities. The level of contamination for sucha design, which would likely be higher than that for villages, could be estimated withour social network data in order to understand its potential impact on estimation. Al-though our method adjusts for the contamination, higher contamination decreases theinformation available to detect an effect. Since our approach removes the dilution fromthe effect estimate while simultaneously increasing standard errors, the lost power fromcontamination is not regained via our adjustment. Rather, the estimate and standarderror estimates are both more accurate than unadjusted estimates. We expect this rela-tionship to hold for other adjustment approaches which have been proposed but, to ourknowledge, not yet applied or tested (e.g., Reiner Jr. et al. (2016)).We also recommend collection and estimation of cross-cluster contamination for dif-ferent types of contacts (e.g., physical contacts, sexual contacts), for various definitionsof clusters in various settings. These estimates can be used to inform future trial designs,choose whether the method we have applied would be better than one which does notadjust for contamination, and ultimately improve the accuracy of vaccine effectivenessand standard error estimates.
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C on t ac t s u r vey f o r m a n t i g r i pp a l t r i va l e n t sa i s onn i e r c h e z l es e n f a n t s sé n é g a l a i s C o mm un i t y C on t a c t F o r m T he l o c a t i on o f c a s e s du r i ng t he i r i n f e c t i ou s pe r i od F o r m J v . : | __ | __ | __ | __ | __ | __ | __ | I n t e r v i e w T i m e : A M P M O n se t d a t e o f t h e | __ | __ | / | __ | __ | / | __ | __ | f i r s t i n f l u e n z a sy m p t o m : D D / M M / Y Y Tod ay Y es t e r d ay D ay b e f o r e yes t e r d ay N o . o f i nd i v i du a l s t h e s ub j ec t s po ke w i t h i n h i s / h e r c o m pound A M : | __ | __ | P M : | __ | __ | N o . o f i nd i v i du a l s t h e s ub j ec t s po ke w i t h i n h i s / h e r c o m pound A M : | __ | __ | P M : | __ | __ | N o . o f i nd i v i du a l s t h e s ub j ec t s po ke w i t h i n h i s / h e r c o m pound A M : | __ | __ | P M : | __ | __ | Lo ca t i on D i d t h e s ub j ec t v i s i t a n y o f t h ese l o ca t i on s ? W h e n d i d t h e s ub j ec t v i s i t ? N o . o f i nd i v i d - u a l s t h e s ub j ec t s po ke w i t h N o . V ill a g e N o . C o m pound Lo ca t i on D i d t h e s ub j ec t v i s i t a n y o f t h ese l o ca t i on s ? W h e n d i d t h e s ub j ec t v i s i t ? N o . o f i nd i v i d - u a l s t h e s ub j ec t s po ke w i t h N o . V ill a g e N o . C o m pound Lo ca t i on D i d t h e s ub j ec t v i s i t a n y o f t h ese l o ca t i on s ? W h e n d i d t h e s ub j ec t v i s i t ? N o . o f i nd i v i d - u a l s t h e s ub j ec t s po ke w i t h N o . V ill a g e N o . C o m pound Y es N o A M P M Y es N o A M P M Y es N o A M P M A no t h e r C o m pound A no t h e r C o m pound A no t h e r C o m pound | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | | __ | __ | | __ | __ | | __ | __ | __ | M a r ke t | __ | __ | | __ | __ | M a r ke t | __ | __ | | __ | __ | M a r ke t | __ | __ | | __ | __ | M o s qu e / C hu r c h | __ | __ | | __ | __ | M o s qu e / C hu r c h | __ | __ | | __ | __ | M o s qu e / C hu r c h | __ | __ | | __ | __ | F i e l d | __ | __ | | __ | __ | F i e l d | __ | __ | | __ | __ | F i e l d | __ | __ | | __ | __ | S c hoo l | __ | __ | | __ | __ | S c hoo l | __ | __ | | __ | __ | S c hoo l | __ | __ | | __ | __ | S po r t s f i e l d / P ub li c p l ace | __ | __ | | __ | __ | S po r t s f i e l d / P ub li c p l ace | __ | __ | | __ | __ | S po r t s f i e l d / P ub li c p l ace | __ | __ | | __ | __ | O u t s i d e o f t h e s t ud y z on e | __ | __ | S pe c i f y : ________________ O u t s i d e o f t h e s t ud y z on e | __ | __ | S pe c i f y : ________________ O u t s i d e o f t h e s t ud y z on e | __ | __ | S pe c i f y : ________________ A no t h e r p l ace : | __ | __ | | __ | __ | A no t h e r p l ace : | __ | __ | | __ | __ | A no t h e r p l ace : | __ | __ | | __ | __ | S pe c i f y : __________________________________ S pe c i f y : __________________________________ S pe c i f y : __________________________________ D i d t h e s ub j ec t v i s i t a no t h e r l o ca t i on , no t s p ec i f i e d a bo ve , du r i ng t h e l as t d ays ? Y es : -- > S p ec i f y : N o : N o . V ill a g e : | __ | __ | D e t a il s : __________________________________________________________ S i gn a t u r e o f t h e i n t e r v i e w e r : _____________________________________ I n t e r v i e w e r N o . : T I V | __ | __ | __ || __ | __ | __ | able 4. Fraction and percent of contacts reported by respondents while located in treatedvillages by village of residence and time of day.
Village Treatment AM Fraction AM Percent PM Fraction PM PercentDarou Vaccine 149/149 100 123/123 100Kalome Ndofane Vaccine 1221/1244 98 959/959 100Poudaye Vaccine 53/65 82 47/47 100Mokane Ngouye Vaccine 1478/1513 98 1307/1312 100Ngayokheme Vaccine 6414/6489 99 5638/5682 99Ndokh Vaccine 135/137 99 101/103 98Nghonine Vaccine 303/306 99 222/231 96Ngangarlame Vaccine 859/953 90 533/586 91Diohine Vaccine 1195/1377 87 1104/1230 90Logdir Vaccine 158/185 85 53/80 66Ngalagne Kop Control 0/1052 0 0/873 0Bary Ndondol Control 0/545 0 0/512 0Mboyene Control 1/634 0 1/522 0Toucar Control 6/2870 0 0/2006 0Godel Control 0/456 0 0/449 0Khassous Control 0/151 0 0/96 0Kothioh Control 3/643 0 0/440 0Meme Control 0/78 0 0/97 0Poultok Diohine Control 0/1717 0 0/1240 0Gadiak Control 10/466 2 10/310 3
B. Cross-village exposure summaries
This section displays analyses that informed our calculation of cross-village exposurerates. The cross-village exposure rate for a village is defined to be the percentage ofcontacts to people in clusters of the opposite treatment assignment. The tables in thissection summarize these rates based on contacts made while the respondent was visitingother villages and do not incorporate contacts made to visitors from other villages inthe respondent’s own home. The tables summarize rates of contacts to treated villagesby village of residence; these represent the cross-village exposure rate for control villagesand one minus the cross-village exposure rate for treated villages.Table 4 compares fractions and percentages of contacts to treated villages betweenmorning and afternoon/evening time intervals. Cross-cluster exposure rates are sim-ilar for the two time intervals, with the main differences being Poudaye and Logdir,whose higher variability than others is likely due to the small number of overall contactsreported in those villages.Table 5 compares fractions and percentages of contacts reported by respondents dur-ing visits to treated villages during the morning by village number and symptom sta-tus. Since numbers of asymptomatic reports are low and cross-village exposure is low,cross-village exposure is lower for asymptomatic than symptomatic participants in mostvillages. Table 6 shows the analogous percentages calculated based on the imputed dataand shows higher levels of cross-cluster exposure for symptomatic than asymptomaticpeople. 23 able 5.
Fraction and percent of contacts reported by respondents while locatedin treated villages by village of residence and symptom status.
Treatment Asymptomatic SymptomaticVillage Assignment Fraction Percent Fraction PercentDarou Vaccine 61/61 100 88/88 100Ndokh Vaccine 28/30 93 107/107 100Ngayokheme Vaccine 1468/1490 99 4946/4999 99Nghonine Vaccine 32/32 100 271/274 99Kalome Ndofane Vaccine 352/359 98 869/885 98Mokane Ngouye Vaccine 178/183 97 1300/1330 98Ngangarlame Vaccine 171/174 98 688/779 88Diohine Vaccine 555/610 91 640/767 83Poudaye Vaccine 6/6 100 47/59 80Logdir Vaccine 58/58 100 100/127 79Ngalagne Kop Control 0/258 0 0/794 0Bary Ndondol Control 0/4 0 0/541 0Mboyene Control 0/86 0 1/548 0Toucar Control 0/839 0 6/2031 0Godel Control 0/316 0 0/140 0Khassous Control 0/19 0 0/132 0Meme Control 0/30 0 0/48 0Poultok Diohine Control 0/559 0 0/1158 0Kothioh Control 0/157 0 3/486 1Gadiak Control 0/137 0 10/329 3 able 6. Percent of contacts reported by respondents while locatedin treated villages by village of residence and symptom status based onmultiply imputed data.
TreatmentVillage Assignment All Asymptomatic SymptomaticKalome Ndofane Vaccine 100 100 100Ngangarlame Vaccine 99 100 99Diohine Vaccine 99 100 98Mokane Ngouye Vaccine 99 100 99Ngayokheme Vaccine 99 99 99Ndokh Vaccine 99 99 99Nghonine Vaccine 98 99 98Logdir Vaccine 95 94 96Darou Vaccine 96 90 100Poudaye Vaccine 93 84 95Ngalagne Kop Control 0 0 0Bary Ndondol Control 0 0 0Mboyene Control 0 0 0Poultok Diohine Control 0 1 0Toucar Control 1 1 0Gadiak Control 2 3 2Godel Control 2 1 3Khassous Control 3 0 3Kothioh Control 3 2 4Meme Control 14 0 20 . Calculation of time-to-event We restrict our analysis to the twenty villages enrolled in the cluster-randomized trial asthese villages received both active and passive surveillance while the other ten receivedonly passive surveillance. The surveillance period for Year 1 was July 15, 2009 to May31, 2010. These dates determined the start and end of follow-up participants with thefollowing exceptions: • Start of follow-up was the date participants moved to the study area if the movetook place after surveillance began. • If participants moved out of the study area or to a cluster of the opposite treatmentassignment during surveillance, their end of follow-up was the move date.Time-to-infection was calculated by subtracting the start of follow-up from the samplecollection date for infected people; censoring times were calculated based on start andend of follow-up for uninfected people.Thirteen participants were excluded from analysis because of inconsistencies in theirrecorded residence data. In addition, those who moved to the study area after theend of Year 1, and those who were infected before moving to the study area or beforefollow-up began were excluded. Because the primary analysis did not censor or excludeparticipants based on their residence data, our counts of participants and cases differslightly from that paper (Diallo et al., 2019).Time to event for Year 2 (for which surveillance covered July 15, 2010 to May 31,2011) was calculated analogously. However, during Year 2 of the study, household-basedsurveillance did not occur from January 1, 2011 to February 18, 2011 due to a strikeof employees performing this surveillance, so only infections reported in health postswere recorded during that time period. This could cause bias if the proportions ofinfections observed at home compared to in health posts different between treatmentarms. During the non-strike period of Year 2, proportions of lab-confirmed symptomaticinfluenza infections reported during household visits were 83 .
07% in the control groupand 87 .
50% in the vaccine group, respectively (Table 7). Since infections for control armparticipants were reported more frequently in health posts than those for vaccine armparticipants, the differential reporting could create bias in the efficacy estimate, makingthe vaccine appear more effective than it actually is. Inverse probability weighting wasconsidered to correct this bias (Seaman and White, 2013). Such an approach would entailup-weighting the observed infections during the strike by . = 5 .
91 in the controlarm and . = 8 .
00 in the vaccine arm, and down-weighting the people classified asuninfected throughout the study period (since some of these would have had infectionsthat would have been detected during household surveillance during the strike). Thisapproach would assume that health post visiting behavior was the same during thestrike and outside of the strike. However, the data indicate that that assumption doesnot hold. Outside of the strike, 66% of infections reported in health posts were in thecontrol group, but during the strike, 78% were. The larger proportion of up-weightedcontrol group infections resulted in a weighted overall effect estimate that was higher,rather than lower, than the unweighted one. As the assumption required by inverse26 able 7.
Reporting rates of lab-confirmed symptomaticinfection by location within each treatment arm duringYear 2, excluding the strike period
Control VaccinePercent reported in compounds 83.07 87.50Percent reported in health posts 16.93 12.50 probability weighting did not hold, we instead censored the Year 2 data at the last daybefore the strike. A secondary analysis includes all of the Year 2 data.
D. Correspondence to compartmental model for infectious disease transmis-sion
The additive hazards model applied in this paper has a natural correspondence to anSIR (Susceptible-Infected-Removed) compartmental model for disease transmission. Tosee this, recall that the contamination-adjusted estimator for an individual in cluster j is obtained from the following additive hazards model: λ j ( t | M ) = β ( t ) + β M ( t ) m j , where m j is the total percentage of contacts of susceptibles in cluster j that are withtreated clusters.Next, we define the following notation:(a) Y k ( t ) = the number of infected people in cluster k at time t (b) κ = the overall average contact rate(c) η k = the per-contact transmission probability of infectives in cluster k (d) m jk = the percentage of contacts from people in cluster j with those in cluster k (e) α jk = the rate of new infections among susceptibles in cluster j from infectives incluster k (f) N k = the population size of cluster k . For simplicity, we assume a fixed populationsize in each cluster.The SIR compartmental model assumes that the rate of transmission from infectivesin cluster k to susceptibles in cluster j is the product of the overall contact rate, thepercentage of contacts from cluster j that are to people in cluster k , and the per-contacttransmission probability: α jk = κm jk η k . The hazard function of a susceptible in cluster j is found by summing these cluster-specific transmission rates, weighted by their cluster-specific proportions of infectives, across all clusters: λ j ( t ) = c (cid:88) k =1 α jk Y k ( t ) N k (1)To simplify notation, we define ν j ( t ) = κη j Y j ( t ) N j , so27 j ( t ) = c (cid:88) k =1 α jk Y k ( t ) N k = c (cid:88) k =1 m jk ν k ( t ) (2)The estimand of interest, which we will denote β ( t ), is the population-averaged dif-ference in hazard of infection associated with a change from 0% to 100% exposure totreatment. That is, β ( t ) = ¯ ν trt ( t ) − ¯ ν ctr ( t ), where ¯ ν trt ( t ) is the average of ν ( t ) in treatedclusters and ¯ ν ctr ( t ) is the average of ν ( t ) in control clusters. While ˆ β Z ( t ) is a consistentestimator for β ( t ) in the absence of contamination, Carnegie, Rui, and Wang provedthat ˆ β M ( t ) is a consistent estimator for β ( t ) in the presence of measured contamina-tion. (Carnegie et al., 2016)If we assume that the individual hazards of infection are identical within a cluster,then the instantaneous rate of change of the number of infected individuals in cluster i at time t is found by summing the individual hazards of all susceptibles in cluster i .Letting S i ( t ) denote the number of susceptibles in cluster i at time t and substitutingfrom (2) yields: dY i ( t ) dt = S i c (cid:88) j =1 α ij Y j ( t ) N j = c (cid:88) j =1 α ij Y j ( t ) S i ( t ) N j , which corresponds to an SIR model with no birth and or death. A similar expressionfor the rate of change of susceptibles is analogously derived, and generalizations suchas birth, death, and the addition of an exposed state for an SEIR model are addressedin Carnegie et al. (2016). 28 . Rationale for adjustment in estimated contamination estimates based on re-ports from visitors to the respondent’s compound We define the following notation as described in the main text: • n j = number of people living in cluster j • D i = number of contacts reported by person i • T i = number of contacts person i made in a location in a treated cluster. • p j = the proportion of contacts from cluster j to treated clusters. • V trt,j = the total number of contacts reported by people in any treated clusterduring their visits to compounds in cluster j .We initially estimated p j with ˆ p j = (cid:80) n j i =1 T i (cid:80) n j i =1 D i The numerator does not include contacts occurring within the respondent’s own com-pound to visitors from other clusters, since these occurred within the respondent’s as-signed cluster. We can use estimates reported by visitors from clusters of the oppositeassignment, rather than by respondents in cluster j , to obtain this information. When j is a control cluster, our estimator is appropriately updated by adding the percent ofcontacts from treated clusters to compounds in cluster j to the contamination estimate:ˆ p j = (cid:80) n j i =1 T i + V trt,j (cid:80) n j i =1 D i = (cid:80) n j i =1 T i (cid:80) n j i =1 D i + V trt,j (cid:80) n j i =1 D i To understand this, we will walk the reader through a toy example of a network depictedin Figure 6, a diagram similar to that in (Potter et al., 2019).Here, A is a control village and B is a treated village, and the red arrow indicates thatOumar contacted Amadou while visiting Amadou’s home in village A. For simplicity,assume all network members are surveyed. The true cross-cluster exposure value for A is 1/7 (noting that each within-village contact is reported twice); it is 1 / S to be an adjacencymatrix indicating contacts to members of one’s own village, so S ij = 1 if i and j madecontact and belong to the same village. S is symmetric, since if i contacted j , then j contacted i as well. Let V denote contacts reported while a member of one cluster wasvisiting a member of a cluster in the opposite treatment arm in the latter’s compound. V is asymmetric to distinguish the host from the visitor and to align with the way thesecontacts were reported, and V , = 1 since person 6 visited person 3 in the home ofperson 3. The recorded counts of contacts occurring in the respondent’s own compound29 ig. 6. Toy example of a social network with corresponding adjacency matrices. l l l l l l l l l l l l l ll l l
Adama Mariama Amadou1 2 3 l l ll l l
Ibrahima Aisha Oumar
Village A (Control) Village B (Treated) l l l l l l l l l l l l l l l l l
Village A Village B
S V H o s t Visitor l l l l l l l l l l l l l l l l l
H = S+V
Reported counts in visited compounds Reported counts in own compound H ≡ S + V . The recorded counts of contacts while the respondentwas visiting compounds in villages of the opposite treatment assignment are the columnsums of V . Our preliminary approach to estimating interference (without the proposedadjustment) would calculate as follows: • For village A, the denominator (total number of contacts) is the sum of the rowsums of rows 1, 2, 3 of H (total number of contacts reported in the respondent’shome) plus the column sums of columns 1, 2, and 3 of V (total number of contactswhile the respondent visited a home in a cluster of the opposite assignment), sothe denominator is 7. The numerator is the sum of column sums of columns 1, 2,3 of V , so the numerator is zero. Our cross-cluster exposure estimate is 0/7. • An analogous approach for village B yields a cross-cluster exposure estimate of 1/3.Our cross-cluster exposure estimate for A is incorrect since it does not account for thecontamination while Oumar was visiting Amadou since it occurred in Amadou’s home.Our proposed adjustment is to subtract from the numerator of A contacts reportedby members of B and occurring in compounds within cluster A. These comprise theupper right quadrant of matrix V, shown in black, whose sum is 1. Thus our adjustedestimate for cross-cluster contamination for cluster A is 1/7, the correct value. A similaradjustment for B involves the lower left quadrant of V; whose sum is zero, so the estimatefor B (which was already accurate) remains the same.We have demonstrated the reasoning for our update to the estimator assuming thatall network members were surveyed. When network members are randomly sampled,the rows of S and columns of V are sampled randomly, and the estimator is unbiased.Our sampling process favored symptomatic people, who could be less likely to travel,but the data show no evidence for difference in travel patterns based on symptom status,as evidenced by Figure 7. This figure displays the location distribution of contacts bysymptom status and time of day based on the multiply imputed data set. Standarderrors were calculated by generating 500 nonparametric bootstrap resamples of eachimputed data set, pooling across the imputed data sets, and then calculating the 2.5%and 97.5% quantiles for each location proportion (Schomaker and Heumann, 2018).31 ig. 7. Location distribution of contacts by symptom status and time interval. Note: This figurehas been published in (Potter et al., 2019) and is reproduced with permission of the authors.
Another placeOutside studyzoneSports field/Public placeSchoolFieldMosque/churchMarketAnother compoundOwn compound 0 25 50 75 100
Percent of contacts Lo c a t i on Morning, symptomatic 63%17%1%1%4%6%6%1%3%
Another placeOutside studyzoneSports field/Public placeSchoolFieldMosque/churchMarketAnother compoundOwn compound 0 25 50 75 100
Percent of contacts Lo c a t i on Morning, asymptomatic75%15%1%1%1%2%4%1%2%
Another placeOutside studyzoneSports field/Public placeSchoolFieldMosque/churchMarketAnother compoundOwn compound 0 25 50 75 100
Percent of contacts Lo c a t i on Afternoon/evening, symptomatic 73%14%1%<1%1%3%6%1%1%
Another placeOutside studyzoneSports field/Public placeSchoolFieldMosque/churchMarketAnother compoundOwn compound 0 25 50 75 100
Percent of contacts Lo c a t i on Afternoon/evening, asymptomatic . R code library(dplyr)library(knitr)library(xtable)library(survival)library(timereg) = NULL, ain = "Contamination-adjusted Estimator")} ens=dat$censored,trt=factor(dat$treatment),X = NULL,mix.pct=dat$pct,clust=dat$village,years=1,plot.trt = TRUE)load(’tte_dat_SEASONAL’)dat=left_join(tte_dat, intdat, by=’village’)dat$censored = 1-dat$infectedmod=fit_addHaz(time=dat$tte,cens=dat$censored,trt=factor(dat$treatment),X = NULL,mix.pct=dat$pct,clust=dat$village,years=1,plot.trt = TRUE)load(’tte_dat_YEAR2’)dat=left_join(tte_dat, intdat, by=’village’)dat$censored = 1-dat$infectedBEGIN = as.Date("7/15/2010", "%m/%d/%Y") = NULL,mix.pct=dat$pct,clust=dat$village,years=1,max.time=plot.trt = TRUE) G. Data Cleaning
Village of residence was recorded during quarterly censuses of the Niakhar populationby the Niahkar Demographic Surveillance System. Delaunay et al. (2002) If participantsmoved during the trial, their departure date, arrival date, and village of their new resi-dence were recorded. Those who moved a second time had their departure date (but notresidence after second move) recorded as well. The cleaning process for inconsistenciesin the recorded movement data is described below:(a) In 8 cases, the departure and arrival dates of the second move were earlier thanthose of the first move. For these cases, the information for second and first moveswas swapped.(b) In 46 cases, the arrival date of the second move was earlier than the arrival anddeparture dates of the first move, and the departure date of the second move wasmissing. For these cases, the information for second and first moves was swapped.After the swap, the (missing) departure date for the first move was imputed to bethe arrival date of the second.(c) In 13 cases where the departure date of the first move was missing, it was imputedto be the arrival date of the second move.(d) In 83 cases where the arrival date of the second move was earlier than the departuredate of the first, the departure date of the first was recoded to equal the arrivaldate of the second.(e) In 13 cases where the departure date of the first move was earlier than the arrivaldate of the first move, and the arrival date of the second move was non-missing, thedeparture date of the first move was recorded to be the arrival date of the second.(f) After these updates were made, there were 13 cases that did not have arrival anddeparture dates in sequential order (i.e., arrival 1 ≤ departure 1 ≤ arrival 2 ≤≤