Spatial Jumps

Evaluating Infrastructure Development
Investment in infrastructure is a key lever for economic growth in developing countries; to this end, World Bank financing for infrastructure is roughly 40% of its total commitments. Knowing the impact of these investments is therefore crucial for policy, but estimating the impact of these investments is difficult: Infrastructure is frequently targeted towards regions where growth is anticipated and coupled with complementary investments. Therefore, separating the impacts of any one investment from others or even from pre-existing growth trends is hard. This explains why development economists are pretty obsessed with finding ways to estimate the causal impact of infrastructure projects, which has led to many creative solutions. One possible option is to use spatial jumps.

What is Spatial Regression Discontinuity?
For reasons frequently discussed on this blog, simply comparing outcomes before and after the construction of infrastructure (which could be correlated with pre-existing trends), or comparing outcomes in communities receiving the new infrastructure to those not (which could be correlated with productivity, or other targeting criteria) is not going to convincingly capture the causal impact of these investments. Further complicating this, the infrastructure development is often coupled with other government interventions to protect and enhance the returns to these investments.
An alternative is to use a spatial discontinuity in the coverage of an infrastructure, or a sharp change in access to a policy across a border. In an application we discuss at the end of the post, hillside irrigation schemes in Rwanda are gravity-fed, meaning canals carry water through these schemes. For two reasons, this allows us to identify the causal impact of irrigation access. First, this creates a discontinuity in access to irrigation: plots just below the canal receive access to irrigation, while plots just above the canal do not. Second, this requires the canals follow a constant gradient (not too steep, not too shallow); within the irrigation site, relative elevation can’t be manipulated, so we can consider whether plots lie just above the canal or just below the canal “as good as random”.



The essence of this research design is captured in the image above. The canal cuts through the hillside, dividing plots into two sets: the pink and the purple. The pink plots are below the canal, and they receive access to irrigation from the system. The purple plots are above the canal, and they do not receive any access. In practice, we focus our analysis on plots just above and just below (within 50m of) the boundary created by the canal: these plots are shaded darker pink and darker purple in the figure. The close proximity of these plots, but difference in access to irrigation, allows us to assume that any differences in agricultural outcomes and investment on these plots are caused by access to irrigation.
 
How does SRD compare to RDD?
So yes, this is similar to a regression discontinuity design (RDD; see a great curated list of posts on the technical details on this, and other research designs, here). When using a RDD, researchers seek to estimate the effects of a policy with a sharp eligibility threshold by comparing individuals who are just barely eligible for a policy to individuals who are just barely ineligible. Although RDD and spatial regression discontinuity (SRD) are similar in spirit, here are a number of crucial differences in implementing SRD vs. standard RDD (these differences are reviewed at length by Keele and Titiunik and Cattaneo et al., and our discussion follows theirs closely):

• Differences between RDD and SRD that affect estimation
  • Multidimensional cutoff: Unlike a normal RDD, where a single score determines whether an individual is eligible, in an SRD latitude and longitude determine whether a unit is eligible.
  • Discrete units: Data may only be available at a sufficiently coarse level where the standard RDD assumption (with a sufficiently large number of observations, many individuals would be very close to the cutoff) may not hold. This is common, for example, when county level data in the United States is used to study impacts of policies that vary across state borders.
• Differences that affect interpretation of estimates
  • Bundled policies: For normal RDD, it’s often the case that only a single policy changes at the eligibility threshold. This is rarely the case in SRD, where multiple policies frequently change across geographic boundaries.
    • This is often addressed by careful understanding of the context, or looking at changes in trends across the discontinuity around a change in a particular policy on one side.
  • Geographic spillovers: In RDD, relatively few individuals (compared to the population) may be near a threshold, so the impact of moving a few individuals across the threshold may be very small on other individuals near the threshold. The same may not be true in SRD, where a policy that targets geographically proximate units may have important spillover effects—this complicates interpretation.
    • Important to note is that, while spillovers often change the interpretation of what’s being estimated, they do not change the fact that estimates are a relative effect of the policy (potentially relative to a positive or negative spillover onto ineligibles).
  • “Manipulation”: In RDD, we are often worried that individuals may choose their score to select themselves into being eligible for the policy; this “manipulation” creates bias, since it means individuals just barely eligible may now be very different from individuals who are just barely ineligible.
    • In SRD, while geographic units may not move, other forms of selection (such as by individuals, or of the boundary itself) may be possible.
• Differences that affect inference
  • Standard errors: In SRD, both outcomes and eligibility typically exhibit spatial correlation.
    • Conley standard errors or appropriately clustered robust standard errors (see one discussion here) may be used to correct for this.

 
Implementation of Spatial RD
So now that we have highlighted the key differences between SRD and RDD (cutoffs are multidimensional, spatial units are frequently discrete), what tools can we use to measure causal impacts through a SRD approach, and how do they actually work?
 

• Matching
  • Match each observation to its nearest (spatially) neighbor, and regress differences in outcomes (between that observation and its neighbor) on differences in eligibility. Note that since eligibility varies only at the threshold, the difference in eligibility will be different from zero only when an observation’s nearest neighbor is on the opposite side of the boundary.
  • This approach is valid under the standard matching assumption (see Jed’s great coverage on this) that outcomes for neighboring observations on either side of the boundary would be the same, were it not for the difference in eligibility at the boundary.
• Normal RD!
  • Use normal RDD! Just make your running variable the distance to the geographic boundary (positive for eligible observations, negative for ineligible observations), and regress the outcome on eligibility, controlling for distance to the boundary and distance to the boundary interacted with eligibility.
  • Intuitively, this is equivalent to taking an average of normal RDD across each segment of the boundary. Therefore, this approach is valid under standard RD assumptions across each segment.
• A hybrid approach! (Spatial Fixed Effects)
  • For each observation, calculate the average outcome, average eligibility, and average of any other controls of its nearest k neighbors (including that observation), or alternatively all observations within some fixed distance (k is of course selected to remain within some reasonable radius of each observation).
  • Then, subtract from each observation’s outcome (and eligibility, and any other controls) this average; this procedure is known as “spatial fixed effects” (also described by Markus here), and yields a spatially demeaned outcome (or eligibility). Finally, regress the spatially demeaned outcomes on spatially demeaned eligibility, controlling for spatially demeaned distance to the boundary and spatially demeaned (distance x eligibility).
  • In this approach, when only 1 neighbor is selected, and distance to the boundary controls are not included, it collapses to pairwise matching. On the other hand, when all neighbors are selected, it is equivalent to a normal RDD. As a result, spatial fixed effects approaches can be valid even when only one set (matching or RDD) of identifying assumptions hold! 

• Important for all approaches
  • Granular data: SRD designs are more compelling when there are many observations close to the boundary. To ensure privacy of administrative data, observations may only be geocoded at coarse units that prevent implementation of SRD designs.
  • Placebo checks: Standard balance checks on covariates or outcomes which should not be affected by the policy are an important validation of the design.
  • Know the context: Interpretation of what’s being estimated can be particularly complicated when policies are bundled, or in the presence of spillovers.

An application of SRD in Rwanda
As mentioned, we use spatial jumps to evaluate recently constructed hillside irrigation schemes in rural Rwanda (with co-authors Maria Jones and Jeremy Magruder).
These irrigation investments are considered an important component of closing agricultural productivity gaps between sub-Saharan Africa and the rest of the world — particularly so since, as of 2015, only 3.3% of arable land in Africa was irrigated, compared to 50.5% and 63.2% in South and East Asia, respectively. It is important for policy is to figure out whether this productivity gap exists because of fundamentally lower returns to irrigation, or whether there are constraints that affect farmers’ decisions to adopt irrigation.
In our paper, we implement both (for robustness) RD and Spatial Fixed Effects approaches. We test the validity of each approach by showing key plot and cultivator characteristics that should not be affected by access to irrigation are balanced across the boundary. For inference, we cluster our standard errors by water user group (the set of plots that use the same pipe for access to water, and their neighbors above the canal).
The figure above shows the implementation of RD: we see that during the dry season, 7% of plots just above the canal are irrigated, while 24% of plots just below the canal are irrigated. That adoption of irrigation jumps 17pp at the boundary is what allows us to estimate the impacts of irrigation. At the same time, the small share of plots with access to irrigation that make use of the irrigation infrastructure is a puzzle, and we spend much of the paper investigating potential constraints to adoption.