I read a couple of very interesting blog posts regarding randomised control trials (#RCTs in Twitter), here I reproduce one from the very influential “EGAP: Experiments in Governance and Politics” blog with a nice overview of RCTs and the “spillover effect”.

I think it makes for a very interesting discussion on methodology, and even philosophy of science–a topic I am particularly fond of. I hope you enjoy reading it; as always, please leave your messages and comments below.

I hope you are having a nice summer vacation as it begins to come to an end.

Kind regards,

Me.

10 THINGS YOU NEED TO KNOW ABOUT SPILLOVERS

This guide helps you think through how to design and analyze experiments when there is a risk of “interference” between units. This has been an important area of research in recent years and there have been real gains in our understanding of how to estimate spillovers in a defensible way.

Spillover problems arise whenever one unit is affected by the treatment status of another unit. Spillovers make it difficult to work out causal effects (we say why below) . Experimentalists worry a lot about them, but the problem is not unique to randomized experiments. It is a universal problem for assessing causal effects. However, spillover analysis is difficult enough when the design is in the direct control of the researcher; it is orders of magnitude more difficult when units are assigned to treatment by some unknown process.

1. What they are

Spillovers are the effects of a treatment assigned to one unit on outcomes for another unit.

Here are some examples of how spillovers (or  “interference”) might occur in an experiment.

• Public Health: Providing an infectious disease vaccine to some individuals may decrease the probability that nearby individuals become ill.
• Criminology: Increased enforcement may displace crime to nearby areas.
• Education: Students may share newly acquired knowledge with friends.
• Marketing: Advertisements displayed to one person may increase product recognition among her work colleagues.
• Politics: Election monitoring at some polling stations may displace fraud to neighboring polling stations.
• Economics: Lowering the cost of production for one firm may change the market price faced by other firms.
• Within-subjects experiments across many domains: the possibility that treatment effects persist or that treatments are anticipated can be modeled as a kind of spillover.

These examples share some features:

• An intervention: the vaccine, increased enforcement, election monitoring;
• An outcome: incidence of disease, crime rates, electoral fraud; and
• A “network” that links units together: face-to-face social interaction, geographic proximity within a city, road distance between polling stations.

The network is a crucial feature of any spillover analysis. For each unit, it describes the set of other units whose treatment assignments “matter.” To take the education example: it may matter to me if you treat another student in my classroom, but it probably doesn’t matter if you treat a student in a different city. I’m connected to the other students in my classroom, but not to students in other cities.

2. If ignored, spillovers “bias” treatment effect estimates

If unaddressed, spillovers “bias” standard estimates of treatment effects (e.g. differences-in-means or OLS regression). “Bias” is in scare quotes because those estimators will return unbiased estimates of causal effects, just not the causal effects that most researchers are interested in.

Imagine an experiment in which there are 50 villages. A treatment is randomly administered to some villages but not others. Let’s assume that a village receives spillovers if there is another village within a 5km radius that receives treatment. If we naively compare treated villages to untreated villages, we will not recover an unbiased estimate of the true treatment effect. Instead, we’ll recover an unbiased estimate of the average difference between treated and untreated villages, when some number are treated. As it turns out how many villages are treated can make a big difference.

In this case, positive spillovers cause a negative bias and vice-versa. This is because when spillovers are positive, the control group mean is inflated, so the difference-in-means is smaller than it otherwise would have been. The extent of the bias, however, depends on the number of units treated as well as the magnitude of the spillover effect. In this example, the more units are treated, the smaller the bias resulting from spillovers. This is because when more units are treated, both the treatment and control group means are similarly inflated by positive spillovers and deflated by negative spillovers.

Often, evaluators are trying to estimate what would happen if a program were rolled out to everyone. Evidence from an RCT that ignores spillover could greatly over or underestimate the total effects of the intervention.

3. Most experimental analyses implicitly or explicitly assume that there are no spillovers.

The assumption that there are no spillovers is known as the non-interference assumption; it is part of a somewhat more elaborate assumption sometimes referred to as the Stable Unit Treatment Value Assumption (or SUTVA) that is generally invoked in the analysis of experimental data.

What does the non-interference assumption mean? Subjects can only reveal one of two “potential outcomes”: either their treated outcome or their untreated outcome. Which of these they reveal depends on their own treatment status only. The treatment status of all the other subjects in the experiment doesn’t matter at all.

We can state the non-interference assumption more formally using potential outcomes notation: $y_i(z_i, \mathbf{Z}) = y_i(z_i', \mathbf{Z'}) \text{, if } z_i = z_i'$, where $\mathbf{Z}$ and $\mathbf{Z'}$ represent any two possible random assignment vectors. In words, this expression states that the other units’ treatment assignments do not affect $Y_i$.

How reasonable is the non-interference assumption? The answer depends on the domain. Every study that finds a statistically significant impact of spillovers is providing evidence that the assumption is incorrect in that particular application. Most papers discussing spillovers tend to focus on examples in which the non-interference assumption is false. But other studies suggest that spillovers are sometimes surprisingly weak. Sinclair, McConnell, and Green (2012) for example find no evidence of within-zip code spillovers of experimental encouragements to vote, bolstering the non-interference claims made by the dozens of previous turnout experiments.

4. You need some kind of non-interference assumption whenever you try to estimate spillover effects

The usual non-interference assumption is very strong: it says that there are no spillover effects. When you try to estimate spillovers, you are replacing this strong assumption with a (slightly) weaker one. Perhaps you think that spillovers take place in geographic space — the treatment status of one location may influence the outcomes of nearby units. Allowing spillovers to take place in geographic space requires the assumption that they do not also occur in, for example, social space. This assumption would be violated if the treatment status of, say, Facebook friends in faraway places affects which potential outcome is revealed. To restate this point more generally: When you relax the non-interference assumption, you replace it with a new assumption: no unmodeled spillovers. The modeling of spillovers itself requires strong, often untestable assumptions about how spillovers can and cannot occur.

Suppose we were to model spillovers in the following way. Every unit has four potential outcomes, which we’ll write as $Y(Z_{i}, Z_{j})$, where $Z_i$ refers to a units own treatment assignment, and $Z_j$ refers to the treatment assignment of neighboring units within a specified radius. $Z_j = 1$when any of the units within the radius are treated and zero otherwise.

• $Y(Z_i = 0, Z_j = 0)$— Pure Control, abbreviated $Y_{00}$
• $Y(Z_i = 1, Z_j = 0)$— Directly treated, no spillover, abbreviated $Y_{10}$
• $Y(Z_i = 0, Z_j = 1)$— Untreated, with spillover, abbreviated $Y_{01}$
• $Y(Z_i = 1, Z_j = 1)$— Directly treated, with spillover, abbreviated $Y_{11}$

What assumptions are we invoking here? First, we are stipulating that the treatment assignment of units outside the radius do not alter a unit’s potential outcomes. Second, we are modeling spillovers as a binary event: either some unit within the radius is treated, or not — we are ignoring the number of treated units, and indeed, their relative proximity.

This potential outcome space is already twice as complex as the one allowed by the conventional non-interference assumption. However, it is important to bear in mind that this potential outcome space can be incorrect in the sense that it does not accurately reflect the underlying social process at work in the experiment.

5. Spillovers are only indirectly “randomly assigned”

The beauty of randomized experiments is that treatment assignments are directly under the control of the researcher. Interestingly in an experiment, spillovers are also randomly determined by the treatment assignment – after all, you’re assigning some unit’s neighbor to treatment or control on a random basis. The trouble is that the probability that a unit is in a spillover condition is no longer directly under the control of the experimenter. Units that are close to many other units, for example, might be more likely to be in the spillover condition than units that are off on their own.

Take a look at the graph below of 50 units arrayed in geographic space. The 10 red units (both filled and unfilled) were randomly selected for direct treatment and yellow units for control. A filled point represents a unit in a spillover condition, whereas an unfilled point represent a unit that has no treated neighbors within the 5km radius. Notice that the units closer to the center of the graph have a much higher chance of being in a spillover condition than do units towards the edges.

6. To estimate spillovers you need to account for differential probabilities of assignment to the spillover

When we estimate causal effects, we have to take account of the probability with which units are assigned to a given treatment condition. Sometimes this is done through matching; sometimes it is done using inverse probability weighting (IPW).

Sometimes, the only practical way to calculate assignment probabilities is through computer simulation (though analytic probabilities can be calculated for some designs). For example you could conduct 10,000 simulated random assignments and count up how often each unit is in each of the four conditions described in the previous section. In R:

 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25 26 27 28 29 30 31 32 33 34 complete_ra <- function(N,m){   assign <- ifelse(1:N %in% sample(1:N,m),1,0)   return(assign) } get_condition <- function(assign, adjmat){   exposure <-  adjmat %*% assign   condition <- rep("00", length(assign))   condition[assign==1 & exposure==0] <- "10"   condition[assign==0 & exposure>0] <- "01"   condition[assign==1 & exposure>0] <- "11"   return(condition) } N <- 50   m <- 20   set.seed(343) coords <- matrix(rnorm(N*2)*10, ncol = 2) distmat <- as.matrix(dist(coords)) true_adjmat <- 1 * (distmat<=5)  diag(true_adjmat) <-0 Z_mat <- replicate(10000, complete_ra(N = N, m = m)) cond_mat <- apply(Z_mat, 2, get_condition, adjmat=true_adjmat) prob00 <- rowMeans(cond_mat=="00") prob01 <- rowMeans(cond_mat=="01") prob10 <- rowMeans(cond_mat=="10") prob11 <- rowMeans(cond_mat=="11")

We can display the resulting probabilities plotted below against the number of units within the 5km radius. The further from the center a unit is, the higher the probability of not being in the spillover condition.

We must account for these differential probabilities of assignment using IPW. Below is a block of R code that shows how to include IPWs in a regression context.

 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36 37 38 39 40 41 42 43 44 45 46 47 get_prob <- function(cond,prob00,prob01,prob10, prob11){   prob <- prob00   prob[cond=="10"] <- prob10[cond=="10"]   prob[cond=="01"] <- prob01[cond=="01"]   prob[cond=="11"] <- prob11[cond=="11"]   return(prob) } get_Y <- function(cond, Y00, Y01, Y10, Y11){   Y <- Y00   Y[cond=="10"] <- Y10[cond=="10"]   Y[cond=="01"] <- Y01[cond=="01"]   Y[cond=="11"] <- Y11[cond=="11"]   return(Y) } Y00 <- rnorm(N) t10 <- 10    t01 <- -3    t11 <- 5     Y01 <- Y00 + t01 Y10 <- Y00 + t10 Y11 <- Y00 + t11 assign <- complete_ra(N, m) cond <- get_condition(assign = assign, adjmat = true_adjmat) Y <- get_Y(cond = cond, Y00 = Y00, Y01=Y01, Y10=Y10, Y11=Y11) weights <- 1/get_prob(cond=cond, prob00=prob00,prob01=prob01,prob10=prob10,prob11=prob11) df <- data.frame(Y, cond, weights, prob00, prob01, prob10, prob11) fit <- lm(Y ~ cond=="01", weights=weights,           data = subset(df, prob00 >0 & prob00 <1 & prob01 >0 & prob01 < 1 & cond %in% c("00", "01")))

There are two very important things to remember when using IPW:

• Only include units that have a non-zero and non-one probability of being in allconditions being compared. The code above only compares the pure control condition to the untreated spillover condition (see the subsetting in the lm call).
• Remember the IPW mantra: units are weighted by the inverse of the probability of being in the condition that they are in.

7. Choosing the wrong interference assumption will yield incorrect estimates

You might be tempted to simply construct a model for a particular type of spillover and estimate it. But unfortunately, just as spillovers can produce biased estimates of treatment effects, incorrectly modeled spillovers can create biased estimates of spillover effects (as well as treatment effects).

To get some intuition for the problem, the simulator below lets you pick an interference assumption: the radius beyond which spillovers cannot occur. As in point (4) we are assuming that there are only 4 potential outcomes – the three causal effects we are interested are the average differences as compared with $Y_{00}$. The tension in the simulator is between the true (in principle, unknown) spillover network that generates outcomes and the assumed spillover network used for estimation.

The causal effect estimates are only correct when the spillover assumption is correct. The potential outcomes were generated under a true radius of 5km. When any radius other than 5km is selected, some if not all of the estimates are biased. This simulator underlines a discouraging point about spillover analysis: it is generally not possible to know if you’ve got the “correct” model of spillovers. Short of doing so, the answers yielded by the model will be incorrect.

Download R code for the above Shiny App in this .txt file

Most applied researchers have settled on two responses to the “unknowability” of the spillover network. First, they specify “theoretically-driven” models of spillover. Usually, this involves the careful application of qualitative information from the experimental context. Second, researchers tend to present estimates under a series of spillover assumptions, for example the estimates under increasing radii.

8. Sometimes you can avoid spillovers with “buffer rows”

One approach to addressing the problem of spillovers is to ensure that other units’ treatment assignments cannot interfere with potential outcomes by including “buffer rows” between experimental units. The buffer row analogy comes from agricultural studies in which experimental crop rows were physically separated by non-experimental rows that presumably prevented interference due to local changes in soil nitrogen content, insect behavior, or water usage.

The analogous design choice in our villages experiment would be to sample a set of 50 experimental villages from a larger set of villages, such that all 50 experimental villages were a healthy distance away from each other – say, separated by a minimum of 75km. Of course, we still must make a non-interference assumption along the lines of: “No spillovers between villages that are 75km or more apart.” This assumption also rules out spillovers that might take place over non-geographic networks, such as an information network via radio, telephone, or internet.

The main advantage of buffer-row-inspired design is the massive reduction in complexity. You can get a clean estimate of a direct treatment effect using standard analytic techniques, without needing to posit complicated assumptions about the possible avenues for spillover.

The main disadvantage of this design, however, is that by design you cannot estimate natural spillover patterns — which could be critical in understanding normal social processes. (Note: if you do do a buffer design, don’t ignore the buffers themselves — data on these can give you a better handle on spillover effects even though they are never going to receive treatment directly.)

9 There are other design-based approaches for detecting spillover effects.

Some researchers employ a “multilevel” design for exploring spillover effects. The “levels” of the experiment correspond to the spillover network. For example, Sinclair, McConnell, and Green (2012) employ a multilevel design to investigate the possible spillover effects of an encouragement to vote. The levels in their experiment are the neighborhood (nine-digit ZIP code), the household, and the individual. The authors’ non-interference assumption is that the treatment assignments of units in other neighborhoods do not matter. What determines which potential outcome is revealed is a combination of three things:

• An individual’s own treatment assignment
• The treatment assignment of his or her housemate
• The treatment assignment of others in the neighborhood

Following a relatively complex randomization scheme, the authors assigned treatments so as to create variation in all three levels.

What are the advantages of this design? First, it requires the researcher to stipulate a non-interference assumption ex ante, so there can be no question of fiddling around with interference assumptions until a statistically significant result pops up. Second, it assigns individuals to treatment (including spillover) conditions with known probabilities, so IPW can proceed without having to resort to the simulation method discussed above.

What are the disadvantages? As ever, the difficulty is that the non-interference assumption used in the design stage could be wrong. Perhaps there are significant spillovers across neighborhoods – after all, neighborhood boundaries as described by nine-digit ZIP codes are arbitrary; it could be that the best of friends happen to straddle these boundaries. Or it could be that the spillover network is only indirectly governed by geography. Workplace social ties may be the true means by which the treatment assignment of one unit influences the outcome expressed by others. Of course, nothing about a multilevel randomization scheme prevents the exploration of such alternative spillover structures.

10. Even if a treatment is binary, spillovers might not be. The right model might require dealing with “dosage”

We’ve explored a non-parametric approach to estimating spillover effects (see Aronow and Samii 2014 for a fuller treatment of this method as well as a conservative variance estimator in the presence of spillovers.). Units were randomly assigned to one of four conditions with a complex (but knowable) probability. Our estimates of causal effects were calculated as the average differences between the treatment conditions. This approach has the advantage of making IPW quite easy to perform – simply weight each observation by the inverse of the probability of it being in the condition that it’s in.

But what about “dosage”? Perhaps in fact spillovers work as a decreasing function of the distance to every other treated unit or in some other more complex way. The spillover is then a continuous variable that describes the “dosage” of exposure to spillovers. The non-parametric IPW approach would require us to chop up the continuous variable in to bins and then calculate average outcomes according to the bin. The IPW estimator quickly becomes quite noisy, as fewer and fewer units occupy each bin.

Bowers, Frederickson, and Panagopoulos (2013) propose a framework that can accommodate any causal model that maps treatment assignments into potential outcomes. The potential outcomes can be in discrete categories (like we’ve been assuming for most of this guide) or a continuous function of the dosage of spillovers.

A schematic sketch of their method is as follows. Suppose the causal model has two parameters: $\beta_1$, the direct treatment effect and $\beta_2$, the indirect effect of a single unit of spillover dosage. A joint test of the hypothesis that $\beta_1 = \beta_2 = 0$is equivalent to a test of the sharp null hypothesis of no effect. Such a test yields a p-value — the probability that the observed data were generated according to the causal model in which $\beta_1 = \beta_2 = 0$.

But we aren’t restricted to only obtaining p-values for the hypothesis that $\beta_1 = \beta_2 = 0$. Those parameters could take on any value, and we could associate a p-value with any pair of parameters. The essence of the Bowers, Frederickson, and Panagopoulos method is to pick the set of parameters that generates the highest p-value by searching through the set of plausible combinations of parameters.