Congestion Pricing: When the Causal Design Fails the Test
In brief
An event-study audit of NYC bridge and tunnel traffic that shows why a plausible policy story is not enough for a causal business decision.
Business question
Congestion pricing began in New York on 5 January 2025. A mobility business may want to change rider pricing, driver incentives, or its city strategy after the policy.
The question is not simply whether traffic was different afterward. It is whether the policy changed traffic more than it would have changed without the policy.
Why it matters
Traffic changes naturally. Weather, holidays, construction, commuting patterns, and facility problems can all move the numbers. If we compare only before and after, we may blame the policy for a change it did not cause.
Decision brief
- Recommendation: do not use this comparison group to claim a congestion-pricing effect or change rider pricing.
- Evidence: affected crossings were already 8.0%–10.2% above comparison crossings in placebo event weeks.
- Potential value: none estimated; this study is a decision-quality audit.
- Evidence strength: High for rejecting this comparator; insufficient for estimating the policy effect.
- Cost / resource requirement: A credible estimate requires a new comparator, route-exposure data, and internal ride outcomes; cost cannot be estimated from this study.
- Main risk: pre-existing trends, spillovers, facility shocks, and the gap between traffic counts and ride-hailing outcomes.
- Cost of inaction: Cannot be estimated from this dataset; acting on a false causal claim could misprice rides or misallocate supply.
- Success / stop rule: Proceed only if pre-trends and placebo checks pass; stop the causal claim if the replacement comparator fails them.
- Next action: rebuild the comparator and validate it with pre-trends, placebos, route exposure, and internal ride outcomes.
My role
I owned the event-study specification, comparator audit, placebo interpretation, and recommendation to pause the causal claim. I did not control the policy, facility operations, or ride-hailing data. I would hand the decision owner a rejected comparator, a pre-registered replacement rule, and the evidence required before pricing action. Reproducible analysis and validation notes show the design and limits.
Data used
I used the official MTA Bridges and Tunnels Hourly Crossings dataset. It provides traffic counts by facility and vehicle class. I selected car counts and built 27,080 facility-day observations across 10 facilities from 2019 to May 2026.
Three facilities provide access toward the central business district: RFK Bridge Manhattan, Queens-Midtown Tunnel, and Hugh L. Carey Tunnel. Seven other facilities act as comparison crossings. This is a traffic study, not a ride-hailing study. It does not measure platform requests, driver supply, or revenue.
Approach
- Compare affected and comparison facilities before the policy.
- Check whether they were moving in a similar way.
- Compare their changes around the policy date.
- Run placebo dates to see whether the same pattern appears before the policy.
- Stop the causal conclusion if the comparison group is not credible.
The method is an event study. In plain language, it compares the gap between the two groups week by week around the policy instead of relying on one before-and-after average.
Key findings
The comparison group was already moving differently
Before congestion pricing began, the affected crossings were already above the comparison crossings by about 10.2% in one earlier event week and 8.0% in another.
Chart takeaway: MTA bridge and tunnel event study: affected crossings were already moving differently before congestion pricing, so the comparison is not reliable
Business meaning: the chosen comparison group does not show what would have happened to the affected crossings without the policy. The later differences cannot be assigned to congestion pricing with confidence.
The most useful result is a decision to pause the claim
The model can still show a post-policy difference, but that difference may reflect the pre-existing gap or another shock. A precise number is not useful if the comparison is biased.
Business meaning: a Country Manager should not change rider prices or driver incentives based on this result. The better next step is to build a comparison that matches the affected facilities before the policy.
Recommendation
What: Do not make a causal claim from this control group.
Where / who: Rebuild the comparison using facilities with similar pre-policy traffic patterns. Treat nearby crossings as possible spillover areas, not automatically as clean controls.
Why: The pre-policy trends fail the basic test required for this type of comparison.
Risk: A new control may also be affected by the policy or by a facility-specific event.
Next test: Pre-register the control-selection rule, add weather, construction, transit, and facility-disruption data, and require acceptable pre-policy trends and placebo results before estimating a policy effect.
What internal data would improve the decision
For a ride-hailing business, I would add requests, completed and cancelled rides, pickup delay, driver online time, passenger price, driver pay, and routes. I would then estimate effects separately for affected trips, border areas, peak periods, and airport flows. The public MTA study is useful external context, not a substitute for platform data.
Key takeaway
The strongest analysis is sometimes the one that refuses a weak answer. This study found that the affected and comparison crossings were already on different paths, so the business should improve the comparison before changing pricing or supply policy.
Technical appendix
Validation record
| Check | Current evidence | Decision |
|---|---|---|
| Control selection | 3 affected facilities versus 7 comparison facilities; selected before interpreting post-policy movement | Keep as an audit, not a final estimate |
| Panel and model | 3,880 facility-week rows across 388 weeks and 10 facilities; log(1 + weekly car crossings), time index, event-week indicators, HAC max lags 4 | Reproducible but only 10 facility clusters |
| Pre-trends | Several pre-policy leads differ from zero, including event week −4 (effect 0.102; p < 0.001) | Fails the required parallel-trends check |
| Placebo dates | Placebo interventions on 10 Nov, 8 Dec, and 22 Dec 2024 also produce significant movements | Comparator is not credible for causal attribution |
| Formal pre-trend test | HAC test of the pre-policy linear slope: p = 0.011 | The treated-control gap was already changing before policy; the comparator is not clean |
The event-study script estimates the difference between affected and comparison facilities by week around 5 January 2025. It uses HAC uncertainty on the weekly group difference. The pre-policy coefficients are the reason the causal claim is blocked. Reproducible code, validation output, and zone-exposure notes are available for review.