Addressing Bias in Causal Effects Estimated Under Mis Specified Interference Sets, with Application to HIV Prevention Trials

April 19, 2024

Information

The identification and estimation of causal effects in the presence of interference relies on assumptions about, and correct measurement of, interference sets within which one individual's exposure may influence another one’s outcome. It can be challenging to properly specify interference sets, and when misspecified or mismeasured, intervention effects estimated by usual approaches will typically be biased. To address this bias, we propose several bias-correction methods developed under various study designs and estimators. We illustrate our methods in the analysis of HIV prevention trials, where social and sexual networks play a critical role in disease transmission.

Speaker: Ariel Chao, MPH

March 15th, 2024

ID11595

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00:01<v Laura>All right, let's get started.</v>
00:03Thank you, everyone, for coming.
00:05So let me introduce our speaker today.
00:08Ariel Chao is a PhD student in the department
00:11of biostatistics, advised by me and Donna Spiegelman.
00:16So let me say few things about her, about Ariel.
00:21So I've been working with Ariel for three years now
00:24and I have to say it's been a real pleasure.
00:27Ariel is an extraordinary student, very patient,
00:30definitely her characteristic and independent.
00:34I've always been impressed by her creativity
00:37and the way she would always find solutions by herself.
00:41We have been having issues
00:42with getting data from our collaborators
00:45and she never gave up and found ways to keep working
00:48on what she had while waiting.
00:51So she deeply cares about the applications
00:53and she's working on and she has a great intuition.
00:57I also been impressed
00:59on how she can work in several things at the same time.
01:03And as you will see today, she's very talented
01:06and I wish her the best for her future career.
01:10Before that, today, she will present her work
01:13on addressing bias in causal effects,
01:15estimated underspecified interference sets
01:18with application to HIV prevention trials.
01:22So let's give Ariel a more welcome.
01:26Ariel, (crackling drowns out speaker).
01:30<v Speaker>Let me just add,</v>
01:32Ariel has a lot of material to present
01:34so we decided to not take questions while she's talking
01:38or she'll never get through the necessarily.
01:40And then we're gonna allow
01:42for around 10 minutes at the end for questions.
01:44So write down the questions
01:45and then we'll try to give as many people a chance
01:48to ask her questions at the end.
01:51<v Laura>I will keep track of it.</v>
01:53<v Speaker>I'm just monitoring the chat.</v>
01:55<v ->Oh yes, can someone, 'cause I don't think I can see you.</v>
01:58<v Speaker>I can see you.</v>
02:01<v ->All right.</v>
02:02So thank you, Laura, and it's been a real pleasure
02:05working with you as well.
02:06So today, I'll be presenting on my dissertation research,
02:10which is on addressing bias in causal effects
02:14estimated under misspecified interference sets.
02:16And we've applied our methods through the analysis
02:19of HIV prevention trials.
02:23So as an introduction, so interference
02:26or spillover is often present in either randomized
02:29or observational studies.
02:31Whereby interference, we mean
02:32that a participant's outcome can be determined
02:35by not only their own exposure
02:37but also the exposure of others.
02:38So a common example is with vaccines.
02:42So say, my disease status is not only affected
02:44by my own vaccination status,
02:46but also the vaccination status of others around me.
02:49And in the context of HIV prevention trials,
02:52it's been found in several network-based studies
02:54that when only some participants of a network
02:57are trained on say HIV knowledge
03:00or safe practices, that the members
03:03who are weren't trained in the network
03:05also demonstrated increased knowledge
03:07and reduced risk behaviors.
03:09And this is known as disability effect.
03:12So causal inference, that is conducted the presence
03:17of interference is often done under assumptions
03:19on the extent and mechanism of interference.
03:22And typically, this will require a specification
03:25of an interference set for each participant.
03:28Whereby interference sets,
03:29we mean that a group of individuals
03:32who can affect the outcome of that participant.
03:35And then to this interference set,
03:37we also typically apply an exposure mapping function
03:41that will take the exposure vector
03:43observed in this interference set
03:45and map it to some scaler quantity.
03:47And we'll see some examples of this later.
03:51So existing literature interference sets
03:53are typically assumed to be correctly specified
03:56so that the exposures
03:57that are mapped from these interference sets
03:59are also correctly measured.
04:01But often, this correctly specifying
04:04an interference set is challenging.
04:06For example, networks can be mismeasured
04:10and when interference sets are misspecified,
04:12we show under various settings that causal effects estimated
04:15by usual purchase are typically biased.
04:18And there have been several publications
04:20that have addressed this issue.
04:22And the majority of these publications aim
04:25to first estimate the true networks
04:27and then using these estimated networks
04:29to estimate the causal effects.
04:31And there have also been methods proposed
04:32for a sensitivity analysis as well.
04:36However, we pursue a different approach where we assume
04:39that we have a validation study
04:41in which the true interference sets are measured alongside
04:44the observed or surrogate ones for a subset
04:46of the study sample.
04:48And this will allow us
04:49to empirically estimate the measurement error process
04:52and use the estimated measurement error parameters
04:55to bias correct causal effects.
04:58So again, this dissertation is a collection of three papers
05:01where we first consider the setting
05:03of an egocentric network randomized trial
05:06where at most one person per network
05:08can receive the intervention.
05:10Then we extend our methods
05:12to consider cluster randomized trials
05:13where multiple participants per cluster
05:15can receive the intervention.
05:17And we also consider general settings
05:19where interference sets can be mismeasured
05:22and the exposure is not necessarily randomized.
05:27So I'll begin with the first paper
05:29on egocentric network randomized trials.
05:32So under this design, we have index participants
05:34who are recruited into this study
05:36and they're each asked to nominate a set of network members,
05:40which can be their drug injection partners or sex partners,
05:44and they form egocentric networks.
05:46And the index participants are the ones in the study
05:49who are randomized to receive their intervention.
05:52And examples of this are typically
05:57be peer education or behavioral-based.
05:59And the index participants are asked to encourage
06:03behavioral change to their network members.
06:07So for some notation,
06:08we have participant ik being the i participant
06:11in the k network.
06:13And we'll let i equal one denote the index participant
06:16in each network and I incur then one
06:18denote the network members.
06:20We'll also define a network neighborhood for participant ik,
06:24which comprises of participants
06:26who share a network link with ik.
06:30And then we also have a true membership matrix
06:33which essentially represents whether a participant
06:37is a network member of a certain index.
06:39And we also have an intervention assignment indicator,
06:45which again the intervention is randomized
06:46and only received by the index member.
06:51So we'll let, throughout this dissertation,
06:54represent an individual exposure to the intervention.
06:57So because in here in NNRT, only index participants
07:01who are randomized to treatment can receive the treatment
07:05and therefore, A is only equal to one for a treated index
07:09and A is equal to zero for everyone else.
07:13And so to define potential outcomes under interference,
07:16we need to make assumptions on the interference structure.
07:18So here, we assume neighborhood interference
07:22with an exposure mapping function, which essentially says
07:26that I case potential outcome is determined
07:28by their own individual exposure
07:31and the exposures of those in I case network neighborhood
07:34and not anyone outside of it,
07:36including participants from other networks
07:39and out of study individuals.
07:42So we further apply an exposure mapping function
07:46to this network neighborhood
07:48and in this paper, we consider an exposure mapping function
07:51defined by the number of treated neighbors.
07:54So under this assumption,
07:58ik's potential outcome is given by y indexed by A and G,
08:01which is their individual exposure
08:02and the spillover exposure given by the number
08:06of treated neighbors in their neighbor neighborhood.
08:11So this figure is a representation
08:14of two networks where in order
08:16to define the spillover exposure,
08:19we further make the assumption
08:21that the networks are not overlapping.
08:23And so this means that index participants
08:25cannot be connected amongst themselves
08:28and network members can only be connected
08:30to one index participant.
08:32And by making this assumption we can obtain G
08:36by multiplying M and R, which is the membership matrix
08:39and intervention assignment.
08:41And so the spillover exposure
08:42for each participant is only determined
08:44by whether they are connected to a treated index member,
08:47which is shown in this figure.
08:53So the causal estimate of interest in this paper,
08:56the average spillover effect which is the impact
08:58of the intervention on the network members.
09:01And we here, we define the spillover effect
09:03as a risk difference and as a risk ratio.
09:06And under assumptions of positivity
09:08and unconfoundedness which is guaranteed in the ENRG design
09:13under perfect treatment compliance,
09:20we can identify the spillover effects
09:22using observed outcomes and estimate them
09:25using observed outcomes as well.
09:29So under the unconfoundedness assumption,
09:33if we had data on the true exposures, we would estimate
09:36the spillover effect using sample average estimators
09:40using the two by two table at the top.
09:43The issue with this is that in ENRTs, the networks
09:46that are observed, which are the ones
09:47that are collected at study baseline,
09:49they may not represent the true connections that take place
09:52during the study period.
09:54So for example, a network member can fall out of touch
09:56with the index participant that they enrolled with
09:59and they can also befriend another index of another network.
10:04And so under these observed networks,
10:06there's spillover exposure may also be misclassified.
10:10And using these misclassified spillover exposures,
10:14we will instead estimate the spillover effect
10:16using the two by two table at the bottom of this slide.
10:20And we show that the estimated spillover effects
10:23under this table would be biased.
10:27And here's a representation of the types
10:29of network misclassification that can occur in ENRT.
10:34So here, the black links represent
10:36the correctly measured network ties.
10:39The blue links represent network links that are observed
10:42but are in fact not true.
10:44And the red links represent the ones that are not observed
10:47but in fact occur during the study period.
10:50And because of these types of misclassification
10:55person's truth, spillover exposure
10:56can be different from their observed one.
11:02In this paper, we further assume
11:04non-differential misclassification,
11:07which is that the misclassification process
11:09doesn't depend on potential outcomes.
11:12So under this assumption we derive an expression
11:15for the bias using four parameters,
11:17which are the baseline Malcolm rate,
11:20the true spillover risk ratio, PM, which is the probability
11:25of being classified into the correct network as well as PR,
11:28which is the intervention allocation probability.
11:32And using these expressions we can show
11:34that there's no bias when PM is one,
11:36which is when everyone is correctly classified
11:38due to the correct network.
11:41We can also show that the bias is always towards the null
11:44under the non differential misclassification assumption.
11:47So the ASP would always be underestimated
11:50under this assumption
11:51if spillover exposures were misclassified.
11:57So in order to correct for this bias,
11:59we use a validation study.
12:01So again, this is where the true network
12:03or spillover exposure is measured
12:05alongside the mismeasured ones
12:07for a subsample of the main study.
12:09And then in this paper, we estimate the sensitivity
12:12and specificity of spillover exposure classification
12:15among network members and we assume that the parameters
12:18that are estimated in the validation study
12:20is generalizable to the main study.
12:24We can show that the sensitivity
12:26and specificity can be expressed as functions of PM and PR
12:32where the intuition is that if a participant
12:35or if a network member is observed to be connected
12:38to a treated index, given that there really are connected
12:43to a treated index,
12:44this can be because they are correctly classified
12:47or it could be because they were misclassified
12:49but still connected
12:50to a treated index just from another network.
12:54We can also estimate the sensitivity
12:55and specificity using the two by two table.
12:58Here, when we assume that the misclassification process
13:02doesn't depend on covariate.
13:07So we propose three estimators in this paper.
13:10The first is called the matrix method estimator.
13:13And here, this estimator takes the estimated sensitivity
13:17and specificity from the validation study
13:20to bias correct accounts observed
13:22from the two by two table in the main study.
13:25And this would be the form of the bias corrected estimators
13:27for this spillover effect.
13:29And we can obtain its variance
13:31by the multivariate delta method.
13:33And if we believe that there is clustering in the study,
13:36we can also adjust for this by a design effect inflation
13:40or we can perform network bootstrapping
13:43where we re-sample networks as whole.
13:46And we know that to use this method
13:49and for this method to perform well,
13:52there needs to be constraints on the value of sensitivity
13:55and specificity for the estimator to be stable
13:58and to avoid estimating negative cell counts.
14:02So when these constraints are not met,
14:05we can instead consider an inverse matrix method estimator
14:10which corrects the cell counts in the two at two table
14:13in the main study using the positive
14:15and negative predictive values
14:16instead of the sensitivity and specificity.
14:19And this method uses the PPV and MPV
14:22estimated separately for those with and without the outcome.
14:26And therefore the matrix method estimated
14:28may be more efficient relative to this estimator
14:31if the outcome is rare
14:32and the validation study is small
14:37and the last estimator we considered
14:39was a likelihood-based estimator
14:42because while the matrix
14:43and inverse matrix estimators are easily implemented,
14:47there's no clear way of directly incorporating the effect
14:49of clustering into the entrance.
14:52And therefore, we can specify an outcome model
14:55including a network random effect
15:00to account for clustering by networks
15:02and using the likelihood specified here,
15:06we can obtain the MLE of the ASP
15:10and its variance by the inverse
15:13of the observation information matrix.
15:19Right, so I'll go over our application
15:23of our methods using the HPTN 037 study,
15:26which was an ENRT that was conducted in Philadelphia
15:30and Chiang Mai Thailand
15:31where in the study indexes were randomized
15:34to receive an intervention that consisted
15:36of a peer education training where they were encouraged
15:42to disseminate HIV knowledge
15:44and injection sexual risk reduction behaviors
15:47with their network members.
15:49In the study, we were interested in looking at the effect
15:53of the intervention on any self-reported HIV risk behaviors
15:57at one year after study enrollment.
16:01Here, we define G star,
16:03which is they observed spillover exposure
16:05based on the intervention assigned to the networks
16:07and receive by their index members.
16:09And we define G the true spillover exposure
16:17based on an exposure contamination survey
16:19that was taken at six months post baseline.
16:22So in the survey, participants were asked
16:24to recall five specific terminologies associated
16:28with the intervention training.
16:31So we suppose that if a network member were able
16:33to recall any of these five terms, that they were exposed
16:36to the intervention through a treated index
16:38and if they weren't able to recall
16:40any of the terms, then they weren't exposed.
16:43And because there was a possibility
16:45that network members may be exposed to the training
16:48but just didn't remember any of the terms
16:51or that there may be network members
16:53who were not exposed to the training
16:56but just said that they remember terms
16:57because of social desirability,
16:59we only included network members
17:01who recalled the positive control term which was exposed
17:04to everybody regardless of their randomization arm
17:08and none of the negative control terms,
17:09which none of the participants were supposed to know
17:14that only these participants
17:15were included in the validation study
17:16so we can more accurately estimate
17:19the sensitivity and specificity.
17:23So here are the effects of the intervention
17:27or the spillover effects of the intervention
17:29on risk behaviors were from the validation study we see
17:34that there was indeed some degree
17:36of network misclassification where the sensitivity was 60%
17:41and specificity was 79%.
17:44So then intent-to-treat estimator uses G star,
17:47which is the intervention assigned to the networks.
17:50And we do see already
17:51that there was significant spillover effect
17:54of the intervention on reducing risk behaviors.
17:57And this effect was amplified
17:59after applying our bias correction method.
18:03So we applied the matrix method estimator as well as the MLE
18:07and the inverse matrix method
18:11was not an ideal choice in this study
18:14because of our small validation study
18:15and the number of participants
18:18who had the outcome within the study.
18:21Here, we also compared several standard errors were first,
18:26we consider standard standards obtained
18:27from the delta method and those inflated
18:30by the design effect.
18:32And we see that the confidence intervals here
18:34were pretty wide, which is due
18:36to the small validation study sample size.
18:40However, when we consider network bootstrapping
18:42or the likelihood base method,
18:44we see that the confidence interval significantly narrowed
18:47and we were able to see a significant spillover effect.
18:54So as a summary of this first paper,
18:56we proposed several bias correction estimators
18:58for this spillover effect
19:00to address network misclassification and NRTs.
19:04So our methods here assume that both the exposure
19:07and outcome are binary measures
19:09and we did not consider covariate adjustment
19:12because the intervention is randomized.
19:15And so as a segue to the second paper,
19:18we will be developing methods
19:20for non-binary exposures outcomes
19:23as well as allowing for covariate adjustment.
19:26And we develop these methods in the setting
19:27of cluster randomized trials.
19:35So causal inference in cluster randomized trials
19:38in CRTs often rely on the assumption
19:41of partial interference,
19:43which is that participants are separated
19:46into non-overlapping clusters
19:47and interference is assumed
19:50to be only contained within these clusters
19:52and not across clusters.
19:54And this assumption is typically made
19:56because there is an absence of social network data and CRTs.
20:02So interference sets define other departure
20:06interference assumptions are usually given
20:07by the randomization clusters in the trial.
20:10So this can be villages or communities
20:16and the interference says they're given
20:17by the randomization clusters can be measured with there
20:20because they might be a lot larger than the true networks
20:24if they were considered to be whole communities.
20:26And also interactions can exist
20:28across these communities as well.
20:31So this figure was taken from a file genetic analysis
20:35from BCPP where BCPP was in HIV prevention CRT
20:40that was conducted in 30 communities in Botswana.
20:44And so the randomization clusters were communities
20:48but from the phylogenetic analysis where they sequenced
20:52HIV genes viral sequences
20:58that they saw that the viral transmission chains obtained
21:00from the sequences, the majority of them
21:04actually crossed two or more communities,
21:06which was an indication
21:07of high-end cluster mixing in this study.
21:10And interference says that are defined
21:11just by communities would be misspecified in this case.
21:18So here we again have participant ik
21:20as the i participant indicate cluster.
21:24We have script one and to denote the study sample.
21:28In this study, we first consider a two-stage CRT
21:33where clusters are first randomized
21:36to an intervention allocation strategy.
21:38Here, we consider strategies alpha one and alpha two
21:42and alpha one and alpha two are probabilities.
21:44And under a balanced design,
21:46half of the clusters would be assigned to alpha one
21:48and half would be assigned to alpha alpha two.
21:51Then after the first stage randomization,
21:55participants within these clusters
21:57would be randomized to receive the intervention
21:59with the probability equal to the one
22:01that was assigned to their cluster.
22:04And we'll extend our methods to consider general CRTs,
22:07which can be considered as a special case
22:10of a two-stage design where alpha one
22:12and alpha two are one and zero, which means
22:15that clusters are randomized to intervention or control
22:18and there isn't a second stage randomization
22:20at the participant level.
22:25So we again have to denote the individual exposure.
22:29And to define potential outcomes in the setting,
22:32we first define a subset of the study sample
22:35for participant ik and we denote this by script I.
22:40So here, we make the partial interference assumption
22:45where ik's potential outcome is influenced
22:48by their own exposure as well as the exposures
22:52of the participants within this subset
22:55and not anyone outside of this subset.
22:57So because only the exposures of the participants
23:00will affect the outcome of ik, we call this subset
23:05for ik's interference set.
23:08And we can further apply an exposure mapping function
23:11to this interference set
23:14to obtain a scaler quantity of a spillover exposure.
23:17Here, we consider stratify interference,
23:22which essentially assumes that spillover occurs
23:25through the proportion of treated participants
23:27in the interference set regardless of who they are.
23:30So the spillover exposure would be given by disproportion
23:34and as in the first paper,
23:35we can index potential outcomes by A and G.
23:41Here, we consider four causal effects
23:45which the individual effect, spillover effect,
23:48total effect and overall effect.
23:50The individual effect is the effect
23:53of the individual exposure under a fixed spillover exposure.
23:57And on the other hand, the spillover effect is the effect
24:01of the spillover exposure under a fixed individual exposure.
24:05And then the total effect is the effect
24:07of having both an individual exposure to the intervention
24:10and some degree of spillover exposure
24:12versus neither type of exposure.
24:15And then the overall effect compares the effect
24:17of being assigned to a cluster randomized
24:21to treatment allocation strategy alpha versus alpha.
24:27So these causal effects can again be identified
24:32under the assumption the identifying assumptions
24:35we made in the paper earlier
24:37or as in the first paper,
24:38which were the unconfounded assumption
24:42which would hold under a two-stage design
24:44given perfect treatment compliance.
24:47And we estimate these effects
24:49using a regression-based estimation approach,
24:52which is consistent
24:53and efficient under a correctly specified model
24:56for the potential outcome.
24:59So here, we consider an outcome model in this form
25:06where we include a cluster random effect to account
25:10for the effect of clustering and the inference
25:12and we also have an interaction between A and G
25:15so that we can allow the individual effect to vary
25:18with G and the spillover effect to vary with A.
25:23So once we have the estimated coefficients from this model,
25:27we can estimate causal effects
25:30using these estimated coefficients.
25:36So again, in CRTs,
25:38because we don't have data on social connections
25:41and when we consider interference to be given
25:43by randomization clusters, they can be measured with error.
25:47And as a consequence, this spillover exposure
25:49can also be measured with error.
25:51So we have shown in this paper
25:53that when the outcome model is fit with G star instead of G,
25:57the estimated model coefficient will be biased
26:00and the causal effects estimated
26:01with these bias coefficients were therefore also be biased.
26:08And to correct for the bias
26:10in these regression coefficients,
26:12we apply a regression calibration approach
26:15which is developed under the assumption
26:17that the measurement error is additive
26:20and also the non differential measurement error
26:22as in the previous paper.
26:25So to apply this method,
26:27we will first regress the outcome
26:30on the mismeasured exposure
26:31in the main study as we would
26:34under the intent-to-treat analysis.
26:36In the validation study
26:37because we assumed that the measurement error is additive,
26:41we fit a linear measurement error model of the true exposure
26:45given the mismeasured spillover exposure.
26:49And then we can obtain bias corrected regression
26:51coefficients using the coefficients
26:53obtained from these two models.
26:56And we can obtain the variance
26:59of these corrected coefficients using the delta.
27:06We can also extend this approach to account
27:09for covariate adjustment
27:11and there may be several reasons why we need
27:13to adjust for covariates.
27:15First, if we step out of the two stage CRT setting
27:18and we consider a general CRT where intervention is work,
27:22clusters are assigned to either intervention or control.
27:25And a lot of public health studies that the interventions
27:29that are given to these clusters may be prone
27:31to non-compliance.
27:33And intervention uptake will depend
27:36on individual characteristics
27:38that may need to be accounted for.
27:41So in the when there are confounders between the outcome
27:46and the individual exposure, A or G,
27:50we would need to assume conditional unconfoundedness
27:55of the individual exposure exposures.
27:57So when there are covariates or confounders between Y and A,
28:02we would adjust them in the outcome model.
28:05And if they were confounders between Y and G,
28:09we would adjust for them in the outcome model
28:11as well as in the measurement error model.
28:15We might need to also make the non-differential
28:20measurement error assumption conditional on covariates.
28:25And in this case, because these covariates are related
28:27to the measurement error as well as the outcome.
28:30They would need to be adjusted in both models as well.
28:34And lastly, we may only be able
28:36to generalize the measurement error parameters estimated
28:40in the validation study to the main study
28:43conditional on covariates.
28:44And in this case, we would adjust
28:46for these covariates as well.
28:50But regardless of the types of covariates that are adjusted
28:53for the regression calibration estimators
28:56and variance estimators
29:01for the coefficients that are of interest that are used
29:04to estimate the causal effects, they would not be changed
29:08as in the case without the variates.
29:14We've applied our methods to the BCPP study,
29:19which is, which was a HIV prevention CRT
29:22and 30 Botswana communities that was conducted
29:26between 2013 and 2018.
29:28And this trial was to assess whether an intervention package
29:33will reduce HIV incidents.
29:35So in this trial, 15 communities were randomized
29:39to receive intervention package
29:41that included HIV testing, linkage to care,
29:45and early ART initiation for those who are HIV positive
29:49as well as increased access
29:50to voluntary medical male circumcision.
29:53And the other 15 communities
29:55were randomized to a standard of care.
29:58So in the primary analysis they found
30:00that there were decreased incident rates
30:03and increased file suppression rates
30:05in the intervention communities
30:06compared to control communities.
30:08And in our application, we are accounting for non-compliance
30:12to the components where we analyzed the individual's
30:15spillover, total, and over effects
30:17of the package intervention
30:18that was received on behavioral and clinical outcomes.
30:23And here, we consider the communities
30:26to be the misspecified interference sets
30:29and we determined the true exposures
30:33using phylogenetics data, which we consider
30:36as our validation data.
30:41So the phylogenetic data was obtained from the study shown
30:45in the beginning of this section
30:46where they found viral transmission chains
30:49that crossed multiple clusters.
30:53So here, they approached HIV positive individuals
30:56in the study and obtained blood samples from them
30:59and they were able to sequence their viral genomes
31:03and construct HIV clusters
31:06where a participants group in the same viral cluster
31:09were implied to be from the same viral transmission chain.
31:14So here, each viral cluster they found to be composed
31:18of two to 27 participants who were
31:19from one to 16 communities.
31:23And there were several considerations that we had to make
31:27by using the phylogenetic data as our validation data
31:32because the viral clusters only captured participants
31:35were infected by the same HIV strain.
31:38And would not necessarily represent a participant's
31:42entire true interference set.
31:45So we had to make some assumptions
31:47to obtain the true spillover exposure
31:50using this phylogenetic data where the first,
31:53we consider the connections observed
31:56within the viral cluster were representative
32:01of the participants
32:03who were HIV positive in ik's true interference set.
32:08And then we also assume transportability
32:12of the measurement error process where we assume
32:15that the inter-cluster interactions
32:17that we observed from the viral clusters
32:19would've been the same among those who were HIV negative.
32:23And lastly, we considered
32:25that because those who are HIV positive
32:26might not have the same characteristics
32:28for intervention uptake as those who are HIV negative.
32:32We derived the true spillover exposure
32:35based on a weighted average of cluster intervention uptake.
32:40So for example, if there were five participants observed
32:44in the viral cluster
32:46from two different randomization communities,
32:49then we take the intervention uptake
32:52of these two communities
32:53and waited by the portion of participants
32:56from each community that were observed in the viral cluster.
33:04And so here are some details on the intervention components
33:09for the study.
33:11I don't know, do I have enough to?
33:13Okay, so basically,
33:16there are four components to this intervention package
33:19and these four components were eligible
33:22to different study populations.
33:24So here are the eligibility criteria that we had considered
33:28for our application where for testing, we considered
33:33that they were eligible for testing if they did not have
33:35documented HIV positive status prior to baseline
33:38and participants were eligible for HIV care
33:41and ART initiation if they were HIV positive at baseline.
33:47And for circumcision, we considered someone
33:51to be eligible for this treatment
33:54if they were an HIV negative male at baseline
33:56who had not been circumcised.
33:59And we also considered several definitions
34:02of the individual exposure which were receiving
34:05at least one of these intervention components
34:08or receiving all eligible components
34:10versus some or none of them.
34:13In this paper, we also considered three outcomes.
34:17First was a behavioral outcome that we defined
34:20as a sexual risk behavior score
34:22and these is defined as the number
34:26of self-reported behaviors that they had reported
34:30at their survey interview at one year post baseline.
34:35And then we also looked at two clinical outcomes,
34:37which were viral load at one year post baseline
34:40and HIV incidents by the end of the study.
34:46Before we looked at the effect
34:48of receiving the individual components,
34:50we first assessed the overall effect of being assigned
34:54to an intervention cluster versus control
34:57on these three outcomes where the ITT estimates
35:01were conducted assuming that the interference sets
35:06were communities.
35:08And we see that there was a minimal overall effect
35:15of cluster assignment on decreasing sexual risk behaviors.
35:20But there was significant effect on viral load
35:23and incidents where our findings echoed the ones
35:28from the primary analysis where they found
35:30increased viral suppression
35:32and decreased incidents for clusters assigned
35:34to intervention and versus control.
35:37And after bias correction we see
35:39that these effects are again amplified,
35:43which was expected due to the high levels
35:45of inter-cluster mixing where say,
35:48some preventative measures from intervention communities
35:52may have gone into the control communities
35:54and some incidents observed in intervention communities
35:57may have been attributable to control communities.
36:03And we also looked at the effect
36:05of receiving at least one component
36:08on essential risk behavior score where we see
36:12that after applying our bias correction method,
36:15that there was a significant total
36:17and overall effect of receiving at least one component
36:21on decreased sexual risk behaviors.
36:27And there was also a significant individual effect
36:30of receiving both HIV care
36:33and ART on decreased viral load which was expected.
36:42So here, we proposed methods to bias correct
36:47causal effects estimated underspecified interference
36:50sets in a CRT, although our methods are not restricted
36:54to the setting can be applied to broader settings as well.
36:59And to use our regression calibration method,
37:01we had to assume that both the measurement error
37:04and outcome models were correctly specified.
37:08And we also made some assumptions
37:10on the measurement error structure.
37:11So we proposed for a third paper and IPW-based method
37:19where parametric assumptions on the outcome model
37:22were not required and also we didn't need
37:24to make assumptions on the additive
37:26or non-differential nature of the measurement error process.
37:34Okay, so propensity score based methods are widely used
37:39to estimate intervention effects when characteristics
37:43of the exposed and unexposed participants may be unbalanced,
37:47which may be an observational setting
37:50where the exposure is not randomized.
37:55And in particular, we're focused on an IPW estimator
37:58that has been previously extended
38:00to estimate causal effects in the setting of interference.
38:04And this is typically done assuming the interference sets
38:07are known and true.
38:09And in this paper, we show that when interference sets
38:15are mismeasured and spillover exposures are mismeasured
38:18as a consequence, there is an error
38:19in not only the spillover exposure
38:21but also in the propensity score estimates.
38:28So for notations, here, we have,
38:31we're outside of the network and cluster setting
38:34so we have just i from one to end participants.
38:37Here, the individual exposure status may depend
38:40on observed individual covariates.
38:43And also, here, we assume
38:45the pressure interference assumption as in our second paper.
38:48Although this method doesn't require
38:51the pressure interference assumption.
38:53We can also make the neighborhood interference consumption
38:55if we were working in a setting of social networks.
39:01In this paper, we define a binary spillover exposure,
39:05although our methods can be generalized
39:07to categorical measures of the spillover exposures as well.
39:10And here we consider an extension
39:13of the stratify interference
39:14that we made in the previous paper where G,
39:18we define by one if the proportion
39:21of treated participants in interference set exceeds
39:23a certain pre-specified threshold.
39:27And again, credential outcomes are indexed by A and G.
39:31In this paper, we're interested in the individual spillover
39:35and total effects.
39:39So this is the IPW estimator
39:42for the average potential outcome
39:45where in the denominator, we have
39:47an estimated joint propensity score for the individual
39:51and spillover exposures.
39:53And this can be expressed as the product
39:55of the individual exposure propensity score
39:58and the spillover exposure propensity score.
40:00And these can be estimated
40:01using (indistinct) regression models.
40:04And we can obtain the variance of this estimator
40:07by bootstrap resampling where we can resample
40:11at the individual level or at the cluster level
40:15if we were working in a setting with clusters
40:17as in our second paper.
40:20And this estimator is consistent, if the models
40:23for the propensity scores are correctly specified.
40:29So as in the previous cases when interference specified,
40:35we would observe G star instead of G.
40:38And if we were to use G star in the IPW estimator,
40:43we would get a biased estimate
40:45because the expected value of this estimator is given
40:49by the form shown in the bottom here where we see
40:53that this estimator is only unbiased if the probability
40:57observing the true exposure equal to G,
40:59given that the spillover exposure
41:02is also equal to G is equal to one,
41:04which means that there's no measurement error.
41:07And also from the form of this expectation, we can also see
41:12that the bias can be eliminated if we divide both terms
41:17on the right-hand side by this measurement error probability
41:21and then subtracting away the second term.
41:25Which is the approach that we took.
41:29And this was an approach that was first proposed by brown
41:33and colleagues in the setting without interference.
41:36And here, we extended this estimator
41:38to the setting of interference.
41:42So from this bias corrected IPW estimator, we see
41:46that on the right-hand side in the first term,
41:49we have the IPW estimator that is estimated
41:53in the main study.
41:55We also have an IPW estimator
41:57that is estimated in the validation study alone.
42:00And the measurement error probabilities
42:04are also estimated in the validation study.
42:09And because here, we are estimating potential outcomes
42:12in the validation study, we need to assume generalizability
42:17of the potential outcome
42:18and measurement error process in this study
42:21so that the effects that are estimated
42:23in the validation study alone
42:25would be unbiased for the average effect
42:28that would be observed in the main study.
42:33So using these bias corrected IPW estimators,
42:37we can obtain a bias corrected estimator
42:39for the causal effect which is given as contrast
42:42between potential outcomes estimated
42:45using the bias corrected IPW estimators.
42:48And here, we can write this estimator using
42:55with weights, W here.
42:57Where the weights are meant to minimize the variance
43:00of the bias corrected causal effects
43:03and the weights are given at the bottom here
43:07where the variance of variance terms can also be estimated
43:11using bootstrap resampling.
43:17So while this estimator directly eliminates the bias,
43:21it does require the outcome
43:22to be available in the validation study.
43:25So when this is not available,
43:28we propose an alternative estimator
43:30that does not impose this requirement
43:33where we've extended methods proposed by rule
43:36and colleagues to the setting of interference.
43:40And so this is a regression calibration-based approach
43:43where first, we assume that we have a continuous measure
43:47of the spillover exposure.
43:49And we will predict the true continuous spillover exposures
43:53given the observed ones.
43:55And then under the exposure mapping
43:57that we had specified previously with the threshold,
44:00we would dichotomize this proportion.
44:07And the regression calibration based IPW estimator
44:10would use the predicted binary true exposures
44:15as well as the propensity scores estimated
44:17under these predictive values.
44:19And we've shown that as in the previous paper,
44:23that this estimator is only consistent
44:25if a linear measurement error model fits the data
44:32In this paper, we further consider the case
44:35where we might observe multiple surrogate
44:37interference sets in a study.
44:39And this was motivated by our illustrative example of BCPP
44:45where we may consider a surrogate interference set
44:48defined by a randomization cluster.
44:50And we can also consider a second surrogate interference set
44:54that is defined by household GPS data,
44:57which is available in the study.
45:00So when we have multiple surrogate interference sets,
45:04we propose to first apply our bias corrected estimators,
45:08either the first or the regression calibration-based one
45:13to each surrogate interference set individually.
45:16And then we will combine these individual estimates
45:18using a weighted average estimator to reduce the variance
45:21of the final estimate.
45:25So the weights are given by C in the bottom here
45:29where we would estimate the variance variance matrix
45:33of the individual bias corrected causal effects.
45:42Here, similar to the second paper, we've applied our methods
45:45to BCPP where we analyzed the individual's
45:49spillover total effects
45:50of receiving at least one intervention component
45:53on sexual risk behaviors one year after study enrollment.
45:58So as a reminder, the components here are HIV testing,
46:01HIV care, ART and circumcision.
46:06And here, we consider a binary outcome, which we define
46:09by one if a participant had reported having engaged
46:13in at least 30% of the surveyed risk behaviors.
46:18Here, for application,
46:19we consider the randomization clusters
46:22or communities as our first surrogate interference set.
46:26And we also consider a second surrogate interference set
46:30that is defined by smaller geographical plots.
46:33And in these geographical plots, they comprised
46:38of participant two to 18 participants on average,
46:42which were much smaller than randomization clusters,
46:44which were about 400 participants each.
46:49And in both of these interference sets,
46:52we define the spillover exposure to be one if at least 25%
46:57of participants in the inference set received
46:59at least one intervention component.
47:03And as in the second paper,
47:04we determine the true spillover exposures
47:08from the phylogenetic dataset.
47:13So here are the risk differences
47:16of receiving at least one intervention component
47:19on self-reported sexual risk behaviors
47:22where we compare the estimates obtained when we consider
47:25communities at the randomization clusters
47:27or the geographical plot as to the interference sets.
47:32And we compare these to the bias corrected estimates
47:35where here, I'm presenting the estimates
47:38of coming from the weighted average
47:40of the bias corrected estimates applied individually
47:43to the community and to the geographical plots.
47:48Where here, under the circuit interference,
47:52as we see that most effects were null.
47:56However, after bias correction, we see
48:00that there is a beneficial AIE when G is equal to one
48:05and beneficial ASP when A is equal to one.
48:08Which means that for participants
48:11who received at least one component of the intervention,
48:14if there were in the presence of at least 25%
48:17of participants who also received the intervention,
48:20that they had decreased risk behaviors.
48:22And likewise for ASP one,
48:28for participants who did receive the intervention,
48:32if they were exposed to at least 25% of participants
48:37in the interference set who also received the intervention,
48:41then there risk behavior fears were also reduced.
48:45But on the other hand,
48:48if a participant did not receive at least one component
48:51and greater than 75% of those interference
48:56that also did not receive the intervention,
48:59then this had an adverse effect on the risk behaviors.
49:03So overall, we see that a participant's risk behaviors
49:08are influenced by their own treatment
49:10and also in synergy with the treatment received
49:14by those in their interference set.
49:21So to wrap up,
49:24so we proposed several bias corrected estimators,
49:27which serve to decrease the bias in assessment
49:29of causal effects so that future intervention strategies
49:32can be more efficiently designed and interpreted.
49:36And our methods assume
49:38that we have suitable validation study that provides us
49:42with true measures of the interference set.
49:44However, as we see from our application
49:48that an exposure contamination dataset
49:50or a phylogenetic dataset are still imperfect measures
49:53of true social connections,
49:55although we do assume
49:56that these are more accurate than interference sets defined
49:59by general say spatial boundaries
50:02or administrative boundaries.
50:06And we propose for future extensions
50:08that we can perform sensitivity analysis
50:13on departures from the assumptions
50:14that are made in this dissertation.