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

Transcript

• 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.