Public electric-vehicle chargers are expensive to install, and the people who pay for them rarely capture all the value they create. One of the strongest arguments for private hosts to absorb that upfront cost is a spillover: drivers who stop to charge also spend money at nearby shops. Keith et al. measured this using card-spending data across California. Spending at a nearby business rose 1.4% ($1,478) per year in 2019 and 0.8% ($404) in 2021–2023. They estimated that one station's first-year spillover recovers roughly 8% of a fast charger's installation cost. The authors say plainly that their window cannot tell whether this boost lasts, fades as a novelty, or shrinks as chargers become common. Whether the boost lasts decides whether the capital is ever paid back.
This note proposes a retrospective cohort study of chargers. It borrows the long-horizon methods clinical epidemiology uses for treatments whose short-term signals mislead. The central idea is simple. The drop from 1.4% to 0.8% mixes three explanations that call for different policies. The first is that a station's effect decays as the station ages (a novelty effect). The second is that the whole economy changed after 2020 (a calendar-period effect). The third is that each new charger matters less where chargers are already dense (saturation). Because California stations opened in different years, we can compare stations of the same age observed in different years, and stations of different ages observed in the same year. That comparison pulls the three explanations apart. We then go beyond spending, which is a proxy, to the outcome that matters: whether nearby businesses survive.
Core Claim
A station's local economic effect is a function of three quantities: its age $a$ in years since opening, the calendar period $p$, and the local charger density $s$ around it at time $p$. Call this function $\theta(a, p, s)$. The claim is that $\theta(a,p,s)$ can be estimated from staggered station openings in the Alternative Fuels Data Center records, linked to SafeGraph/Advan spending, visits, and dwell time. The decomposition answers three questions that the two-slice design of Keith et al. cannot.
The first question is whether spillovers decay with station age. The second is whether that decay, if any, shows up in business survival and not only in spending. The third is how many years of realized spillover it takes to cover installation cost under the estimated decay curve, as opposed to the flat curve that a one-year snapshot implicitly assumes.
Keith et al. also report a puzzling pattern. The effect within 100 meters rose from 2.7% to 3.2% while the average effect fell, and median dwell time dropped. That pattern is already hard to explain with pure novelty decay. It is more consistent with saturation or with a change in who stops to charge. Our design can tell these apart.
How This Relates to Prior Work
Keith et al. supply the data sources, the matching approach (difference-in-differences combined with propensity score matching), and the motivating anomaly. We differ in three ways. We follow each station along its own time since opening rather than pooling stations within two calendar slices. We model saturation explicitly. We add a hard endpoint.
The planning literature constrains the problem rather than solving it. Luo et al. optimize shared-EV station deployment with reinforcement learning but leave installation cost and multi-year durability out of the objective. The Frederiksberg agent-based study (Bayesian optimization of EV charging infrastructure location planning) shows that at low EV penetration, installation cost can make total welfare negative. Shen et al. plan phased rollouts using assumed Gaussian demand growth. None of these models has an empirical estimate of how site value changes as a station ages. Our estimated curve is exactly the input they lack.
Clinical retrospective cohorts supply the method and the warnings. Tewari et al. use propensity scores to correct the fact that healthier men were steered to surgery. Charger siting has the same structure, because operators place stations where commerce is already strong. Tewari et al. also show that cohorts spanning decades drift in what they record and in how practice is done. That is our calendar-period problem. Chen et al. show that a 46-month median follow-up can hide divergence in a disease known for late recurrence. Work on cardiac resynchronization (Hu et al.) shows that gains in an intermediate imaging proxy did not translate into fewer deaths or hospitalizations. Together these motivate treating spending as a proxy that must be checked against business survival. Wen et al. supply the multilevel structure we need, since businesses sit inside neighborhoods and counties with shared shocks.
Research Program
The unit of analysis is a business–station pair. A business is "treated" when a station opens within a set distance. Distance bands are 100 m, 250 m, and 500 m, following Keith et al.'s distance gradient. Each opening year forms a cohort. Each cohort is compared with businesses whose nearest station opens later ("not-yet-treated"). Those comparison businesses are matched on pre-opening spending trends, business category, and neighborhood income and density. Because comparisons are made only within cohorts and against not-yet-treated units, early-treated businesses never serve as controls for later ones. That avoids a known distortion of pooled fixed-effects regressions when effects change over time.
For each cohort and each calendar year we obtain an effect estimate. We then fit $\theta(a,p,s)$ across cohorts. Age, period, and cohort are linearly dependent, since cohort equals period minus age, so one restriction is required. We state ours openly. Cohorts are allowed to differ only through observable traits at opening: port type, which is Level 2 versus direct-current (DC) fast charging, and density at opening. Any remaining cohort effect is assumed to be zero, and we test this restriction in the held-out check below.
The hard endpoint is business closure, taken from the place records' open/closed status. We will first validate that status against long runs of zero visits. Closure is analyzed with a Cox proportional-hazards model, a standard survival regression that estimates how a factor changes the instantaneous risk of an event. Station presence enters as a time-varying exposure, and its effect is allowed to vary with station age.
Finally, we convert the estimated curve into a payback horizon. This is the number of years until discounted cumulative spillover across nearby businesses equals installation cost. We report it under the fitted curve, under a flat curve, and stratified by neighborhood income. The income stratification follows the equity tension raised in the Wuhan siting study.
Baselines
The naive reference point is a simple before–after comparison of spending at businesses near new stations, with no control group. It shows how much of any apparent effect comes from siting stations in places that were already growing. We expect it to overstate the effect substantially. Any credible design must at least remove that inflation.
The strongest existing method is the difference-in-differences with propensity matching of Keith et al.. Their reported result is a 1.4% ($1,478) annual spending effect in 2019 and 0.8% ($404) in 2021–2023, rising to 2.7% and 3.2% within 100 m. We will reimplement it on our panel with their covariates and two-slice structure. This lets us confirm we can reproduce their numbers before extending them. Their design implicitly assumes the effect is constant within a slice, which makes it the right competitor for a paper about time-varying effects.
A third baseline is a standard two-way fixed-effects event study run on the longer panel. This is the simplest extension of Keith et al.'s approach and the method a referee would reach for first.
All methods use the same matched sample, the same covariates, and the same distance bands. They also get the same tuning budget for matching calipers, chosen by pre-trend balance rather than by outcome.
Our measure of "beating" a baseline is forecasting rather than fit. Each method is estimated on openings and outcomes through 2021. Each then predicts the 2023–2024 effects for stations that by then are three or more years old. The decomposition must cut forecast error relative to Keith et al.'s design, which predicts a flat effect. It must also cut error relative to a pure age-decay model.
Two ablations isolate the key ingredient. One removes the saturation term. The other pools all periods, which collapses the decomposition back to age alone. If neither ablation degrades the held-out forecast, the three-way decomposition is not earning its complexity, and we will report that.
Why not just…?
Why not just extend Keith et al.'s difference-in-differences with more years of data? This is the real competitor, and it is included as a baseline. More years alone do not separate age from period. In any one later calendar year, older stations also carry pandemic-era shocks. Pooled fixed-effects regressions additionally borrow early-treated units as controls, which biases estimates when effects drift. If the longer-panel event study forecasts the held-out years as well as the decomposition does, the simpler method wins, and the contribution shrinks to the closure endpoint and the payback curve.
Why not just simulate ten years of operation with an agent-based or reinforcement-learning model? Simulators such as MATSim in the Frederiksberg study or the environment in Luo et al. contain no model of host-business spending or closure. Any decay they produced would come from assumed behavior. Luo et al. also note that historical demand is observed only where stations already exist. Our estimates are meant to calibrate such simulators, not to compete with them.
Why not just run a six-month prospective pilot at new stations? A pilot measures the early part of the curve, which is precisely where novelty effects live. The digital-health trials of Chew et al. and Kwan et al. show short gains whose persistence could not be established. Our year-one estimate will tell us directly how much a pilot would overstate long-run value.
Why not just use charger utilization records instead of business outcomes? Utilization measures the operator's revenue, not the spillover that justifies a host's capital outlay. Utilization data are also mostly proprietary. Where public utilization proxies exist, we will use them as a covariate to separate "fewer drivers" from "drivers spending less per stop."
Decisive Checks
The design fails if effects already appear before a station opens. We test this with pre-trends over the six quarters before opening, and with placebo opening dates shifted two years earlier. We also use a negative-control outcome: businesses 1–2 km away, which should show no effect. If they show one, local commercial shocks are driving the results.
To gauge how much hidden siting bias it would take to erase the age-decay estimate, we report sensitivity bounds on unmeasured confounding. Following Tewari et al.'s experience with drift in what gets recorded, we rerun everything restricted to cohorts from 2016 onward, when the place records are most complete.
The headline result we commit to reporting has two parts. The first is whether the within-500 m spending effect at age four or more is distinguishable from its year-one value after period and saturation are held fixed. The second is whether closure hazards move in the same direction. If spending decays but survival does not, or the reverse, that discordance is itself the finding. It would be the infrastructure counterpart of the proxy-versus-outcome gaps documented in clinical follow-up.
References
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