Interference and Sensitivity Analysis
Causal inference with interference is a rapidly growing area. The literature has begun to relax the “no-interference” assumption that the treatment received by one individual does not affect the outcomes of other individuals. In this paper we briefly review the literature on causal inference in the presence of interference when treatments have been randomized. We then consider settings in which causal effects in the presence of interference are not identified, either because randomization alone does not suffice for identification or because treatment is not randomized and there may be unmeasured confounders of the treatment–outcome relationship. We develop sensitivity analysis techniques for these settings. We describe several sensitivity analysis techniques for the infectiousness effect which, in a vaccine trial, captures the effect of the vaccine of one person on protecting a second person from infection even if the first is infected. We also develop two sensitivity analysis techniques for causal effects under interference in the presence of unmeasured confounding which generalize analogous techniques when interference is absent. These two techniques for unmeasured confounding are compared and contrasted.
29 \issue4 2014 \firstpage687 \lastpage706 \doi10.1214/14-STS479 \newproclaimassumptionAssumption
Interference and Sensitivity Analysis
A]\fnmsTyler J. \snmVanderWeele\correflabel=e1]firstname.lastname@example.org, A]\fnmsEric J. \snmTchetgen Tchetgen and B]\fnmsM. Elizabeth \snmHalloran
Causal inference \kwdinfectiousness effect \kwdinterference \kwdsensitivity analysis \kwdspillover effect \kwdstable unit treatment value assumption \kwdvaccine trial
Cox [(1958), page 19] wrote that there is no interference between different units if the observation on one unit is unaffected by the particular assignment of treatment to the other units. The assumption of no interference is a key component of Rubin’s “stable unit treatment value assumption,” called SUTVA (Rubin (1986)), that is often required for potential outcomes to be well-defined. However, in many settings, the assumption of no interference obviously does not hold. Consider an individual who, if not vaccinated, would have infected another person, but who, if vaccinated, would not infect that other person. In this case, the infection outcome of the second person depends on the treatment of the first individual, and there is thus interference. Under the assumption of no interference, the effect of a treatment compares two potential outcomes the individual would exhibit under treatment and control. With interference, an individual could have many potential outcomes depending on the treatments assigned to the other individuals (Rubin, 1978, 1990).
In some settings interference is a nuisance, while in other settings it creates effects of scientific, public health or social science interest. An example of the former includes agricultural experiments where treatments in neighboring plots can interfere with one another (Kempton (1997)). Fallow rows between treatment plots can sometimes eliminate interference between plots, but more often the interference must be taken into account. In infectious diseases, interference is inherent in the biology of transmission, it cannot be eliminated, and it produces intrinsically interesting effects. Social interaction is a primary source of interference in studies with humans subjects and often cannot be eliminated.
Progress in causal inference with interference has been made recently in different contexts, including those in the social sciences, econometrics and infectious diseases. Several causal effects can be defined in the presence of interference, and sometimes similar effects have different names in different contexts. Social scientists have long been interested in the effects of neighborhoods on the economic, sociological and psychological well-being of their inhabitants, resulting in the term neighborhood effects (Sobel (2006)). The consequences of interference between individuals in this context are also known as spillover effects. In infectious diseases, these effects were generally called indirect effects of interventions (Halloran and Struchiner (1991)).
In Section 1.1 we present informally some examples of studies on causal inference with interference in different contexts. In Section 2 we present formal definitions of direct, indirect, total and overall effects as well as infectiousness effects in the presence of interference. In Section 3 we develop a number of new sensitivity analysis techniques in settings in which causal effects are not identified, either because the effect estimand itself relies on assumptions beyond randomization or because treatment is not randomized and there may be unmeasured confounding. The sensitivity analysis techniques help address these issues of identification in these settings. Section 3 contains the new results of the paper and, as will be seen below, many of these new results in the context of interference build on foundational work on sensitivity analysis by Robins, Rotnitzky and Scharfstein (2000) outside the context of interference. Section 4 offers some concluding remarks on directions for future research on interference. A reader who is primarily interested in the technical development can skip Section 1.1 and move on directly to Section 2.
1.1 Motivating Examples
1.1.1 Interference and housing mobility
Sobel(2006) considered interference in the Moving to Opportunity (MTO) demonstration sponsored by the U.S. Department of Housing and Urban Development. In this housing mobility experiment in poor neighborhoods in five cities, eligible ghetto residents were randomly assigned to receive one of two forms of relocation assistance or no assistance (control). Sobel argued that the no interference assumption is not plausible for the MTO demonstration because many of the participants likely knew other participants at each of the five sites. Thus, the participants could have influenced each other through social interaction. For example, a family that decided to move to a new neighborhood could give rise to worse outcomes for a family that stayed in the original neighborhood because of the decline in social support for the family that stayed.
Sobel (2006) defined causal estimands and estimators for indirect/spillover effects for the MTO randomized trial of housing vouchers, taking compliance into account. He assumed that interference could occur within the sites, but not across sites, which he called partial interference. He made a key contribution in proposing causal estimands for assessing effects in the presence of interference by averaging causal effects over all possible treatment assignments for a particular allocation strategy compared to a benchmark strategy wherein no units received the treatment assignment. Although his language is different, he essentially defined causal estimands analogous to the direct, indirect, total and overall effects defined in the next section.
He then compared his causal estimands to what is usually estimated in studies of housing mobility not taking interference into account. He showed that what is usually estimated actually gives the difference between (i) the average effect of the voucher on those who received them and (ii) the average effect on those not receiving vouchers of having people leave the neighborhood. Both effects could be negative (detrimental) with the difference positive, thus making it important to take potential interference into account.
1.1.2 Interference in vaccination programs
Motivated by an interest in the effects of vaccination and vaccination programs, Struchiner et al. (1990) and Halloran and Struchiner (1991, 1995) conceptually defined direct, indirect, total and overall effects in the presence of interference. The direct effect of a treatment on an individual was defined as the difference between the potential outcome for that individual given treatment compared to the potential outcome for that individual without treatment if the treatment assignment in the others in the population was held fixed. In contrast to direct effects, an indirect effect describes the effect on an individual of the treatment received by others in the group when that individual’s treatment was held fixed. In particular, the indirect effect of a treatment on an individual was defined as the difference between the potential outcomes for that individual without treatment when the group (i) receives an intervention program and (ii) receives a benchmark program of no intervention. Total effects describe the combination of direct and indirect effects of a particular treatment assignment on an individual. The total effect of a treatment on an individual is the difference between the potential outcomes for that individual (i) with treatment when the group receives an intervention program and (ii) without treatment when the group receives no intervention. Overall effects describe the average effect of an intervention relative to no intervention.
Halloran and Struchiner (1995) proposed individual-level causal estimands of direct, indirect, total and overall in the presence of interference by letting the potential outcomes for any individual depend on the vector of treatment assignments to other individuals in the group (Rubin, 1978, 1990). However, they did not propose population level causal estimands.
A number of studies have been conducted to estimate indirect, total or overall effects of vaccination programs outside of the causal inference framework. In the United Kingdom, the indirect effect of a new program of meningococcal C vaccination was estimated by comparing the attack rates in unvaccinated children and adolescents before and after introduction of the program (Ramsay et al. (2003)). The United Kingdom introduced routine meningococcal serogroup C vaccination for infants in November 1999. The vaccine was also offered to all children and adolescents aged 18 years in a phased catch-up program. Adolescents were vaccinated first and the program was completed by the end of 2000. About 75% of the children and adolescents were vaccinated. The attack rate in unvaccinated infants through adolescents per 100,000 unvaccinated population in July 1998–June 1999 was 4.08 (95% CI: 3.7, 4.5) and in July 2001–June 2002 was 1.36 (95% CI: 0.86, 1.85). Vaccinating about 75% of the children and adolescents thus seemed to produce an indirect effect, with a relative reduction in the number of confirmed meningococcal C cases in the unvaccinated children and adolescents, of 67% (95% CI: 52, 77).
To obtain group- and population-level causal estimands for direct, indirect, total and overall causal effects of treatment, Hudgens and Halloran (2008) proposed a two-stage randomization scheme, the first stage at the group level, the second at the individual level within groups based on Sobel’s approach of averaging over all possible treatment assignments. As did Sobel (2006), they assumed interference can occur within groups but not across groups. The causal estimands defined by Hudgens and Halloran (2008) are applicable to other situations with interference in fixed groups of individuals where treatment can be assigned to individuals within groups. A brief formal development is given in Section 2.
As an example, Hudgens and Halloran (2008) presented a hypothetical two-stage randomized placebo-controlled trial of cholera vaccines (Table 1). Suppose in the first stage five geographically separate groups were randomized so two were assigned to vaccinate 50% and three were assigned to vaccinate 30% of individuals, then individuals were randomly assigned to be vaccinated or not. Causal effect estimates (and estimated variance) are given in the change in number of cases per 1000 individuals per year. The estimated indirect effect of vaccinating 50% versus 30% in the unvaccinated individuals is 2.81 (3.079). This suggests that vaccinating 50% of the population would result in 2.8 fewer cases per 1000 unvaccinated people per year compared with vaccinating only 30%. Similarly, the estimated total effect is 4.11 (0.672). This suggests that vaccinating 50% of the population would result in about 4.1 fewer cases per 1000 vaccinated people per year compared with unvaccinated persons vaccinating only 30%. The estimated overall effect is 2.37 (1.430). The estimated overall effect is a summary comparison of the two strategies, suggesting that, on average, 50% vaccine coverage results in 2.4 fewer cases of cholera per 1000 individuals per year compared to 30% vaccine coverage. A public health professional could use these estimates in evaluating the cost-benefit of vaccinating more people and preventing more cases versus vaccinating fewer people. The direct effect under 30% coverage is 3.64 (0.178), nearly three times greater than the direct effect under 50% coverage, which is 1.30 (0.856). The difference shows that even the direct effects can depend on the level of coverage due to interference between individuals. Note that the direct effect under 50% coverage of 1.30 and the indirect effect of 2.81 sum to the total effect of 4.11.
1.1.3 Interference in the context of kindergarten retention
Hong and Raudenbush (2006) considered interference in the context of the effect on reading scores of children of being retained in kindergarten versus being promoted to the first grade. Interference was assumed possible through the dependence of the potential outcomes of reading test scores of one child on whether other children were retained or not. Hong and Raudenbush were principally interested in the effect of a child’s being retained and how this varied with being in schools with low retention and versus those with high retention. They used a sample of data from 1080 schools with 471 kindergarten retainees and 10,255 promoted students. In their application, students are clustered in schools. Individual treatment assignment was whether a student is retained. They used a school-level scalar function based on the proportion of the students that were retained to determine whether a school was a “high-retention” or “low-retention” school. The study was observational at two levels: schools were not randomized to have high or low retention, and students were not randomized to be retained. However, they framed their analysis within a two-stage randomization procedure similar to that described in Hudgens and Halloran (2008) in which both stages would have been randomized. They also assumed interference was possible within schools but not across schools.
Using a propensity score-based approach, accounting for interference, and assuming that assignment at both the school and the individual level was ignorable given a number of observed individual-level, school-level, and school-aggregated-individual-level characteristics, Hong and Raudenbush (2006) obtained estimates of the effect on reading scores of retention in high-retention and low-retention schools. Specifically, in low-retention schools, they estimated the effect on reading scores of a student being retained versus being promoted, was 8.18 (95% CI: 10.02, 6.34), and in high-retention schools the effect estimate was 8.86 (95% CI: 11.56, 6.16). A standard deviation in reading test scores in this sample is 13.48 points. We will return to this example below to demonstrate sensitivity analysis in the context of interference.
1.1.4 Interference between two sides of the face
Rosenbaum (2007) took a different approach to causal inference with interference when analyzing randomized experiments than those in previous sections. He pointed out that if Fisher’s null hypothesis of no effect for any individual in the population is true, then there is no effect and consequently no interference. Thus, Fisher’s permutation test of no effect will have the correct level, even if, under the alternative hypothesis, there would be interference. He presented several examples, including data from a randomized, double-blind experiment in which 15 people received different preparations of botulinum A exotoxin on each side of their face to treat wrinkles to test which was less painful.
Rosenbaum presented exact nonparametric methods for inverting randomization tests to obtain confidence intervals for assessing treatment effect assuming nothing about the structure of the interference between units. He assumed that there were a number of blocks (groups) with a number of individuals within each group, some of which, but not all, were randomized to a treatment, the others to control. He developed a general notation that allowed interference across blocks and did not assume a two-stage randomization. Rosenbaum (2007) differentiated two null hypotheses. The first null hypothesis is that treatment has no primary effect, that is, the response of each unit does not vary under different randomization assignments in the collection of the possible assignment matrices with fixed number randomized in each block. Analogous to the benchmark allocation of Sobel (2006) and the two-stage randomized trials described above where possibly some communities receive only the control intervention, Rosenbaum (2007) invoked uniformity trials in which individuals within treatment groups would be randomly assigned to treatment and control, but everyone in control groups would receive just control. The second null hypothesis is that treatment has no effect, that is, under different randomization assignments in the collection of the possible assignment matrices with fixed number randomized in each block, each individual’s response equals his response in a uniformity trial. If there is no effect, then no benefit is gained from receiving the treatment. If there is no primary effect, there is no advantage to being one of the treated individuals, but the benefits could be shared by all of the individuals.
Rosenbaum gave conditions using distribution-free tests in which without performing the uniformity trials, he was able to get confidence statements about the magnitude of the effect and/or primary effect, though not able to distinguish between them. In the botox example, the 15 people are the blocks, the two sides of the face the individuals. All 15 people reported less pain from the treatment containing alcohol. Using his method, the hypotheses of no effect and no primary effect were rejected with a one-sided significance level 0.000031.
Luo et al. (2012) extended this approach in the context of a cognitive neuroscience experiment in which the brains of a moderate number of subjects are studied using functional magnetic resonance imaging while challenged with a rapid fire sequence of randomized stimuli. Interference was assumed to occur between units of time in the same individual.
1.1.5 Interference and infectiousness effects
In vaccine contexts, a vaccinated person who becomes infected might have a lower probability of transmitting to a susceptible person during a contact than an unvaccinated person who becomes infected. This is called the effect of the vaccine on infectiousness. In a study in Niakhar, Senegal, for example, Préziosi and Halloran (2003) estimated the relative reduction in infectiousness to household contacts of a vaccinated case of pertussis compared to an unvaccinated case to be 67% (95% CI: 29, 86). Estimating reduction in infectiousness can be of considerable public health interest, particularly with vaccines that do not protect well against infection.
Developing general methods for causal inference for infectiousness effects poses complicated challenges. Even if the vaccine is randomized, the infectiousness effect is measured only in people who become infected, a post-randomization variable, so the estimate would in general be subject to selection bias. VanderWeele and Tchetgen Tchetgen (2011b) and Halloran and Hudgens (2012a, 2012b) proposed causal quantities corresponding to the infectiousness effect in the simple situation of households of size two. The general approach combines causal inference with interference with principal stratification (Frangakis and Rubin (2002)). The latter accounts for the fact that the comparison in the groups who become infected may be subject to selection bias. The causal infectiousness effect is not identifiable without further assumptions. In Section 2.6 we present the bounds that were developed previously. In Section 3.2 we present new results for sensitivity analyses for causal infectiousness effects.
1.1.6 Other approaches
Manski (2013) studied identification of potential outcome distributions when treatment response may have social interactions. He called the no interference assumption the individualistic treatment response to differentiate it from other forms of treatment response that depend on social interaction. VanderWeele et al. (2012) discussed the relation between causal interactions and interference and how under randomization it is possible to test for specific forms of interference. They show that the theory for causal interactions provides a conceptual apparatus for assessing interference as well.
In this section we present previously developed formalizations of the direct, indirect, total and overall effects as well as the infectiousness effects as background for the development of the new sensitivity analyses under interference in Section 3.
Suppose there are groups of individuals or blocks of units. For , let denote the number of individuals in group and let denote the treatments those individuals receive. Assume is a dichotomous random variable having values 0 or 1 such that can take on possible values. Let denote the subvector of with the th entry deleted. The vector is referred to as an intervention or treatment program, to distinguish it from the individual treatment . Let and denote possible values of and . Define to be the set of vectors of possible treatment programs of length , for . For example, .
Denote the potential outcome of individual in group under treatment as . Denote as the vector of such outcomes under treatment for group . The notation allows for the possibility that the potential outcome for the individual may depend on another individual’s treatment assignment in group , that is, it allows for interference between individuals within a group. The potential responses can be assumed fixed, since they do not depend on the realized random assignment of treatments , whereas the observed responses do depend on and thus are random variables. We also consider potential outcomes that are independent and identically distributed across blocks. Partial interference is assumed to hold, that is, the outcome of one individual can depend on treatment of other individuals in the same block, but not those in different blocks. The form of the interference within groups is assumed unknown and can be of arbitrary form.
2.2 Treatment Assignment Mechanisms
Following Hudgens and Halloran (2008), consider a two-stage randomization scheme, the first stage at the group level, the second at the individual level within groups. Let and denote parameterizations that govern the distribution of for . Corresponding to the first stage of randomization, let denote the group assignments with if the group is assigned to and 0 if assigned to . Let denote the parameterization that governs the distribution of and let denote the number of groups assigned . Following Sobel (2006), Hudgens and Halloran (2008) focused on a mixed group and mixed individual assignment strategy, whereby a fixed number of groups were allocated to , and within each group, a fixed number of individuals were allocated to treatment versus control. VanderWeele and Tchetgen Tchetgen (2011a) and Tchetgen Tchetgen and VanderWeele (2012) considered what we call a simple randomization scheme whereby treatment is randomly assigned to different individuals within group according to a Bernoulli probability mass function. The causal estimands defined below have the same form under either randomization scheme, though the different randomization schemes result in subtle differences of interpretation.
2.3 Average Potential Outcomes
Causal estimands are typically defined in terms of averages of potential outcomes which are identifiable from observable random variables. Following this approach, the potential outcomes for individual in group under can be written
In other words, the individual average potential outcome is the conditional expectation of given under assignment strategy . In contrast, under the simple allocation strategy of VanderWeele and Tchetgen Tchetgen (2011a), the potential outcomes are averaged over the unconditional distribution of . Averaging over individuals, define the group average potential outcome under treatment assignment as . Finally, averaging over groups, define the population average potential outcome under treatment assignment as . The causal estimands in the next section are defined in terms of the individual, group and population average potential outcomes. The individual estimands were defined in Halloran and Struchiner (1995), the individual average, group average and population average estimands in Hudgens and Halloran (2008).
2.4 Direct, Indirect, Total and Overall Causal Effects
The individual direct causal effects of treatment 0 compared to treatment 1 for the individual in group were defined by
The individual average direct causal effect for the th individual in the th group was defined by
that is, the difference in individual average potential outcomes when and when under . The group average direct causal effect as defined by , and the population average direct causal effect by .
The individual indirect causal effects of treatment program compared with on individual in group were defined by
where is another dimensional vector of treatment random variables. (Note does not denote the transpose of .) Similar to direct effects, the individual average indirect causal effect were defined by . Clearly, if , then , that is, there will be no individual average indirect causal effects. Finally, the group average indirect causal effect was defined as and the population average indirect causal effect as .
The individual total causal effects for individual in group were defined as
The individual average total causal effect was defined by , the group average total causal effect was defined by , and the population average total causal effect was defined by . It follows by simple addition and subtraction that a total effect is the sum of the direct and indirect effects at the individual, individual average, group average and population average levels. For example, .
The overall causal effect was defined to be the average effect of an intervention program relative to no intervention. The individual overall causal effect of treatment compared to treatment for individual in group was defined by . Similarly, for the comparison of to , the individual average overall causal effect was defined by , the group overall causal effect by , and the population overall causal effect by where and and . VanderWeele and Tchetgen Tchetgen (2011a) showed that the overall effect decomposes into the sum of an indirect effect and a contrast of two direct effects on the individual average, group average and population average levels. For example, .
The quantities defined above under interference have two important distinctions from those used in causal inference without interference. First, they quantify causal effects only for participants in the randomized study. Second, they depend on the randomization probabilities [through ]. Although the causal estimands here depend on the assignment mechanism (e.g., comparing two different proportions vaccinated), we could alternatively compare allocation strategies of always vaccinate versus never vaccinate to recover traditional causal estimands that do not depend on the assignment mechanism.
The estimands defined above simplify under the assumption of no interference between individuals within a group since the potential outcomes of the th individual in group can be written as and . In turn, the individual direct causal effect is no longer dependent on the treatment assignment vector and simply equals . The corresponding group average direct causal effect becomes , that is, the usual average causal effect estimand. By (2.4), the individual indirect causal effect equals zero for all individuals assuming no interference. That is, assuming no interference implies the treatment has no indirect effects. Similarly, by (2.4) the individual total causal effect equals the individual direct causal effect. Likewise, at the group average level, under the no interference assumption the indirect causal effect is zero and the direct causal effect equals the total causal effect.
2.5 Inference and Challenges
Assuming the two-stage randomization and mixed allocation strategy, Hudgens and Halloran (2008) proposed unbiased estimators for the various population average effects. They provided variance estimates under the assumption of stratified inference, that is, if it matters only how many people are allocated to treatment, not exactly which ones. Tchetgen Tchetgen and VanderWeele (2012) provided conservative variance estimators (i.e., guaranteed to be no smaller than the true variance in expectation), under more general assumptions and provided finite sample confidence intervals for the various effects without the assumption of stratified interference. Liu and Hudgens (2014) further developed large sample randomization inference for the direct, indirect, total and overall causal effects in the presence of interference when either the number of groups or the number of individuals within groups grows large, but not necessarily both.
2.6 Interference and Infectiousness Effects
To develop causal estimands for the infectiousness effects presented in Section 1.1.5, we follow the development of VanderWeele and Tchetgen Tchetgen (2011b) and Halloran and Hudgens (2012a). Consider a setting with households (groups) indexed by . Each household consists of two persons indexed by . We let denote the vaccine status for individual in household , where if the individual received vaccine and if the individual did not. For each household, denotes the vaccine status of the two individuals in the household. We let denote the infection status of individual in household after some suitable follow-up in the study. We let denote the potential outcome for individual in household if the two individuals in that household had vaccine status of ; we treat the potential outcome vector as a random variable that is independent and identically distributed across households.
We assume partial interference, that is, the exposure status of persons in one household in the study do not affect the outcomes of individuals in other study households. The assumption that clusters constitute isolated pairs would be reasonable in a vaccine trial conducted with a relatively small number of households in a very large city so that it is unlikely that the various households in the study would interact with one another. We will assume that the two individuals in each household are distinguishable (e.g., a husband and wife pair) and we will consider a simple randomized experiment in which only one of the two individuals (e.g., the wife) is predetermined to be randomized to receive a vaccine or control and the second person (e.g., the husband) is predetermined to be always unvaccinated. We let denote the individual who may or may not be vaccinated (e.g., the wife) and the individual who is always unvaccinated (e.g., the husband). In other settings in which the individual (husband or wife) who is subject to vaccination is itself randomized (i.e., two-stage randomization), the analysis below could be done separately in those households in which the wife was selected for vaccine randomization versus those in which the husband was selected.
The crude (or net) estimator for the infectiousness effect on the risk difference scale was defined as
where the expectation is taken over all households. This is a comparison of the infection rates for individual in the subgroup in which individual was vaccinated and infected versus in the subgroup in which individual was unvaccinated and infected. Even though the vaccine status for individual is randomized, conditioning on a variable that occurs after treatment, for example, the infection status of individual , in effect breaks randomization. The net estimator for the infectiousness effect could be subject to selection bias. We are computing infection rates for individual for subpopulations that may be quite different with respect to individual .
This contrast compares the infection status for individual if individual was vaccinated, , versus unvaccinated, , but only among the subset of households for whom individual would have been infected irrespective of whether individual was vaccinated, that is, . Such a subgroup is sometimes called a principal stratum (Frangakis and Rubin (2002)). The contrast in (2.6) is not subject to selection bias, so it can be considered a formal causal contrast for the infectiousness effect.
Unfortunately, we do not know which households fall into the subpopulation in which individual would have been infected irrespective of whether individual was vaccinated. The contrast (2.6) is, in general, unidentified, even when treatment is randomized, though the observable data do provide some information about (2.6). Bounds and sensitivity analysis are further facilitated by other assumptions.
For all , .
Assumption 2.6, usually called a monotonicity assumption, states there is no one who would be infected if vaccinated but uninfected if unvaccinated. Under Assumption 2.6, there are three principal strata or subgroups of households defined by the joint potential infection outcomes of individual under vaccine and control. They are (i) the doomed principal stratum in which individual is infected whether vaccinated or not, (ii) the protected stratum in which individual is infected if unvaccinated and uninfected if vaccinated, and (iii) the immune stratum, in which individual does not become infected whether vaccinated or not. The causal contrast (2.6) is defined in the doomed principal stratum.
To simplify notation, let , , and . The crude (net) infectiousness effect (2.6) is then just , and the causal infectiousness effect (2.6) is . Under randomization and monotonicity, any household where individual 1 is infected if vaccinated must be in the doomed stratum, so . Thus, one component of the causal infectiousness effect (2.6) is identified.
However, any household where individual 1 becomes infected if unvaccinated could be in the doomed or protected stratum. Thus, is not identified without further assumptions. However, under monotonicity, the ratio of the proportion in the protected stratum to the sum of the proportions in the protected and doomed strata is identified by the observed data. Thus, we know what proportion of the households in which individual 1 received control and was infected is in the doomed stratum, just not which ones, so we do not know what proportion of secondary transmissions occurred in the doomed strata. Under Assumption 2.6, Halloran and Hudgens (2012a, 2012b) derived upper and lower bounds for causal effects on infectiousness that are constrained by the relation in the data between and .
A further possible assumption is the following:
Assumption 2.6 states that the average infection rate for individual if both individuals and were unvaccinated would be lower in the subgroup of households for which individual would be infected and unvaccinated than in the subgroup of households for which individual would be infected and vaccinated. The assumption might be thought plausible insofar as the subgroup for which individual was vaccinated and infected might be less healthy than the subgroup for which individual was unvaccinated and infected; thus, if both people are unvaccinated, individual is more likely to be infected in the first subgroup than in the second.
Under Assumptions 2.6 and 2.6, VanderWeele and Tchetgen Tchetgen (2011b) showed the crude contrast in (2.6) is conservative for the causal contrast in (2.6) in that , that is, . Analogous results in fact also hold for the risk ratio, odds ratio and vaccine efficacy scales (VanderWeele and Tchetgen Tchetgen (2011b)).
The approach may be employed outside of the vaccine context. For example, in an observational study in which the treatment is a smoking cessation program in which one of two persons in a household participated. The participation of the first person might affect the smoking behavior of the second. This might occur either (i) because smoking cessation for the first person encourages the second to stop smoking or because (ii) even if the first person does not stop smoking, the second person might nevertheless be exposed to some of the smoking cessation program materials. One could evaluate this second type of effect (the analogue of the infectiousness effect) by applying the approach described above.
3 Interference and Sensitivity Analysis
In this section we develop sensitivity analysis techniques that can help assess the presence of causal effects in two settings where these effects in the presence of interference are not identified. These causal effects may not be identified either because the treatments are not randomized or because, even if the treatments are randomized, the spillover effects of interest involve conditioning on a post-treatment variable thereby breaking randomization. Building on the previous sections, we first consider the setting of a randomized trial where the spillover effect of interest is not identified by randomization alone because of conditioning on a post-randomization variable as in the infectiousness effect described in Section 2.6. We present sensitivity analysis methods for assessing this infectiousness effect in part by adapting research in Robins, Rotnitzky and Scharfstein (2000). We then consider the setting of observational data such as in Hong and Raudenbush (2006) in which causal effects and spillover effects may not be identified due to one or more unmeasured confounding variables. We present two sensitivity analysis techniques for causal effects in the presence of interference that extend analogous results for causal effects under no-interference (*24; VanderWeele and Arah (2011)) to the setting of causal effects and spillover effects in the presence of interference.
3.2 Sensitivity Analysis for the Infectiousness Effect
In Section 2.6 we described two previously developed approaches to bounds on the infectiousness effects. Here we develop methods for sensitivity analysis for the infectiousness effect. We follow the development first in VanderWeele and Tchetgen Tchetgen (2011b) and Halloran and Hudgens (2012a) and then in Hudgens and Halloran (2006); further technical development is given in the Appendix. See also VanderWeele and Tchetgen Tchetgen (2011b) and Hudgens and Halloran (2006) for concrete applications. A simple sensitivity analysis approach also follows from the development of VanderWeele and Tchetgen Tchetgen (2011b). We use the same notation as in Section 2.6. As noted in Section 2.6, under monotonicity Assumption 2.6, we have that and, thus, to obtain the causal infectiousness effect, we need to express in terms of the observed data and sensitivity analysis parameters. We will describe three different parameterizations.
First, let denote the sensitivity parameter which contrasts the average counterfactual infection rates for individual if both individuals and were unvaccinated in the subgroup of households for which individual is vaccinated and infected versus the subgroup of households for which individual is unvaccinated and infected. It follows from the development in VanderWeele and Tchetgen Tchetgen that, under monotonicity, and, thus,
In other words, to obtain the infectiousness effect under monotonicity, we can calculate the crude infectiousness effect in (2.6), specify the sensitivity parameter and subtract the sensitivity parameter from the crude estimate to obtain the infectiousness effect. We can vary over a range of plausible values in a sensitivity analysis to produce a range of plausible values for the infectiousness effect. The sensitivity analysis parameter is subject to certain empirical constraints as described below. However, because of the simple relationship above, a corrected confidence interval under sensitivity parameter can be obtained simply by subtracting from both limits of the confidence interval for the crude estimate in (2.6).
We can also use a similar approach but with a different parameterization of the sensitivity analysis parameters. Following Hudgens and Halloran (2006), we can vary , the probability of secondary transmission in the protected stratum when individual 1 receives control with bounds set by constraints of the data (Halloran and Hudgens, 2012a, 2012b). The quantity is not identifiable from the observed data without further assumptions, but once a value of is assumed, then the probability of secondary transmission in the doomed stratum is fixed and, thus, is identified. Varying , the infectiousness effect (2.6) on the risk difference scale can be obtained as , where is given by
and where can vary between
with the left side giving rise to the upper bound for the causal infectiousness effect and the right side giving rise to the lower bound on the risk difference scale. Note that a drawback of this approach is that the parameter is constrained by the observed data and similar restrictions are imposed on above by virtue of the identity .
As a third parameterization, we could follow an approach to sensitivity analysis developed in Scharfstein, Rotnitzky and Robins (1999) and Robins, Rotnitzky and Scharfstein (2000). This approach performs sensitivity analysis with a bias parameter on the ratio scale. Gilbert, Bosch and Hudgens (2003) and Hudgens and Halloran (2006) adapted this approach for sensitivity analysis for causal effects on post-infection outcomes, the former in the continuous post-infection outcome scenario, the latter for binary post-infection outcomes. Hudgens and Halloran (2006) and Halloran and Hudgens (2012a) suggested that this approach to sensitivity analysis could be used for infectiousness effects taking as the intermediate infection outcome the infection status of individual 1 and as the potential post-infection outcome the infection status of individual 2. Within the context of the infectiousness effect, again under monotonicity Assumption 2.6, the bias parameter can be expressed as
The bias parameter is the log of odds ratio comparing the risk of infection if individual 1 is not vaccinated among (i) the doomed stratum and (ii) the protected. Note this is not simply a different scale than the bias parameter above (odds ratio versus risk difference) but also a comparison of different subpopulations. Once this bias parameter is specified, then it can be shown that is the positive root of , where
In each of the three parameterizations above, once we have obtained , we can obtain the infectiousness effect on the difference, risk ratio, odds ratio or infectiousness effect scales by , , and , respectively.
We have focused here on the setting of a randomized trial, but the approach is potentially applicable to observational studies as well if, conditional on some set of covariates , the treatment was jointly independent of the counterfactual outcomes (i.e., effectively randomized within strata of ). The sensitivity analysis parameters would have to be conditional on .
3.3 Sensitivity Analysis for Spillover Effects Under Unmeasured Confounding: Approach 1
We now consider a setting in which causal effects and spillover effects under interference are not identified due to unmeasured confounding. Adjustment is often made for covariates to attempt to control for such confounding. However, in an observational study we can never be sure that the control is adequate. One or more unmeasured confounders may bias effect estimates. Confounding control becomes even more complex in settings with interference since when one individual’s outcome is under consideration, control will often need to be made for the covariates of other individuals in the same cluster (Tchetgen Tchetgen and VanderWeele (2012); Ogburn and VanderWeele (2012); Perez-Heydrich et al. (2013)). Unmeasured confounding can thus operate either through the unmeasured covariates for the focal individual or for other individuals in the same cluster. In this subsection, we apply and extend the sensitivity analysis approach of VanderWeele and Arah (2011) to allow for settings with interference and spillover effects. In the next subsection we consider an extension of the sensitivity analysis approach of Robins, Rotnitzky and Scharfstein (2000) to allow for interference and spillover effects.
We consider a general observational setting such as that employed by Hong and Raudenbush (2006) wherein individuals are clustered in groups such that individuals within groups may influence one another but there is no interference between groups. We make the stratified interference assumption above and further assume, following Hong and Raudenbush, that the potential outcome of person , , depends on the treatment received by the individuals in cluster other than person , , only through some known many-to-one scalar function so that can be written as . For example, might be the mean of . Let . Suppose that for all , is determined by simple randomization. We then have that
Hong and Raudenbush (2006) considered a variation on this assumption in the context of observational data. Specifically, for some covariate vector , they assumed that
and from this it follows that
where the right-hand side can be estimated with observed data. Hong and Raudenbush (2006) also allowed to contain cluster level covariates along with cluster aggregates of individual level covariates. Note, however, that (3.3) requires that be mean independent of both and conditional on . If, for each individual, is randomized conditional on , although this will imply that is mean independent of conditional on , it does not necessarily guarantee that is mean independent of conditional on . Let denote the vector of all covariates for all individuals in cluster other than individual . We might, instead of (3.3), consider
where is a known function of . However, once again, with (3.3), even if, for each individual, were randomized conditional on , this would not guarantee that is mean independent of conditional on unless . See Ogburn and VanderWeele (2012) for discussion of causal structures for which assumptions (3.3) or (3.3) will hold. Under assumption (3.3), we have
where again the right-hand side can be estimated with observed data. From this one could obtain conditional direct, indirect and total effects, namely,
These contrasts are important insofar as they allow one to assess the relative importance for an individual’s outcome of changing an individual’s own treatment versus the treatment of other individuals. In other words, the effects allow one to assess the relative importance of spillover. Marginal effects, involving counterfactuals of the form , could be obtained by averaging over the distributions of and .
Suppose now that we have unmeasured confounding by one or more unmeasured confounders and let denote the vector of for all individuals in cluster other than individual . Suppose that the analogue of assumption (3.3) holds conditional on observed and unobserved for some scalar function so that
but that (3.3) does not hold when we do not condition on . Without data on causal effects are not identified. Let and .
Following the sensitivity analysis approach of VanderWeele and Arah (2011) for causal effects under no-interference, we express the difference between the causal effect
and the biased estimand
in terms of sensitivity analysis parameters. Let denote this difference. Technical development is given in the Appendix.
Let and denote arbitrary reference values for and , respectively. Under assumption (3.3) we have that
To obtain the bias factor , one could thus specify the effect of the unmeasured confounders and on the outcome, , for and , and also how the distribution of and differs when versus , that is, and . One can use these sensitivity analysis parameters to calculate the bias factor in (3.3) and then subtract the bias factor from the estimate of the causal effect using the observed data to obtain a corrected effect estimate for .
Note that the expression for the bias factor in (3.3) makes no assumption beyond assumption (3.3) that control for observed and unobserved would suffice to control for confounding of the effect of on ; it allows for multiple unmeasured confounders. However, the use of the bias formula in (3.3) requires specifying a large number of parameters: for every value of and the distributions and .
Under some simplifying assumptions, expression (3.3) reduces to a much easier to use formula. In particular, suppose that there is a single unmeasured confounder and that is scalar. Suppose also that the effects of and are additive in the sense that for and . In the Appendix it is shown that under these assumptions
To use this simplified bias formula, one only needs to specify the effect, , for a one unit increase in the unmeasured confounder , the effect of a one unit increase in the scalar functional of the unmeasured confounders of the other members of the group, , and how the means of and differ when versus when . Once these sensitivity analysis parameters are specified the bias factor can be calculated using formula (3.3) above and then could be subtracted from the estimate of the causal effect using the observed data to obtain a corrected effect estimate for . Under this simplified approach because the bias factor involves only the sensitivity analysis parameters and not the observed data, a corrected confidence interval could be obtained by subtracting from both limits of a confidence interval for . A sensitivity analysis consists of reporting the causal contrasts under a range of plausible values of and . The values correspond to the assumption of no unmeasured confounders. Selecting a plausible range of parameters could be done using subject matter expertise, by external data from other studies or by including a very wide range of parameters that are thought to include those that would constitute very extreme values. Alternatively, one could examine the most important measured confounder and assess the magnitude of the corresponding parameters for the most important measured confounder; one could then consider whether an additional unmeasured confounder with parameters set equal to that of the most important measured confounder would substantially alter results. This would allow an investigator to assess whether an unmeasured confounder would have to be stronger than the most important measured confounder to substantially alter the results.
Consider again the substantive example of Hong and Raudenbush (2006) described in Section 1.1.3. As noted above, Hong and Raudenbush (2006) examined the effect of kindergarten retention on reading test scores allowing for interference by allowing the retention of other students at the school to affect a child’s reading test scores. They assumed that treatment assignment at both the school and the individual level was ignorable given a number of observed individual-level, school-level and school-aggregated-individual-level characteristics. Using a propensity score-based approach, they estimated, in the notation above, the contrasts and , where denotes high-retention school and a low-retention school. They found that, in low-retention schools, their estimates indicated that the effect on reading scores of a student being retained versus being promoted was (95% CI: 10.02, 6.34), and in high retention schools the effect estimate was (95% CI: 11.56, 6.16). A standard deviation in reading test scores in this sample is 13.48 points.
Hong and Raudenbush also went through a sensitivity analysis argument for their results. They noted that the strongest predictor of current test scores were lagged test scores, but that it was unlikely that there was any unmeasured covariate that would predict their outcomes so strongly. They considered instead whether unmeasured individual and school covariates that had effects on readings scores that were equal to those of the measured covariates with second strongest association with reading scores would suffice to explain away the effect estimates. Using an argument based on a formula similar to (3.3), they reported that unmeasured individual and school confounders that had an effect as large as the second most important measured individual and school level covariates would shift the estimate in high-retention schools to (95% CI: 6.95, 1.54) and thus not suffice to bring the confidence interval to include . However, in low-retention schools, unmeasured individual and school confounders that had an effect as large as the second most important measured covariates would shift the estimate and confidence interval in low-retention schools to (95% CI: 2.44, 1.24) and thus would suffice to bring their confidence interval for the effect in low-retention schools to include . The effects in high-retention schools seem more robust to the possibility of unmeasured confounding. In their analyses, Hong and Raudenbush (2006) used a similar expression to (3.3), but in their paper they did not provide a derivation of this formula and did not articulate the assumptions needed for the use of the formula. We have provided the derivations and assumptions required here. Moreover, we have also provided a more general expression, that in (3.3), that is applicable under much weaker assumptions.
We have considered here a sensitivity analysis approach for causal effects and spillover effects in the presence of interference. In other contexts, questions concerning whether the effect of a treatment on an outcome is mediated by some intermediate may be of interest. In settings in which mediation is of interest and interference occurs at the level of the mediator so that the mediator for one unit may affect the outcomes for other units (cf. *36; VanderWeele et al., 2013), a similar sensitivity analysis approach for unmeasured confounding of the mediator and the outcome could be developed by applying and extending the results of VanderWeele (2010b) for direct and indirect effects from the no-interference setting to a setting with interference by following an analogous approach to that presented above.
3.4 Sensitivity Analysis for Spillover Effects Under Unmeasured Confounding: Approach 2
In this subsection we consider an alternative sensitivity analysis approach to assess the influence of unobserved confounding for direct and spillover effects in general settings similar to those considered by Hong and Raudenbush (2006) described above. The following developments follow closely from analogous sensitivity analysis techniques recently proposed in the context of mediation analysis (Tchetgen Tchetgen (2011); Tchetgen Tchetgen and Shpitser (2012)). In order to formalize the approach, suppose that we wish to make inferences about the following causal effects:
where, unless stated otherwise, throughout and are left unrestricted, that is, . These effects are versions, allowing for interference, of the so-called effect of treatment on the treated, which have been studied extensively in the absence of interference by econometricians, epidemiologists and social scientists. The first contrast captures the direct effect of on conditional on the person’s observed exposure and the cluster’s observed data . In contrast, is the spillover causal effect of on within levels of . Note that , so that these effects are relative to the reference average potential outcome under .
Consider the pair of no unobserved confounding assumptions:
It is straightforward to show that under these assumptions, and are identified by