Findings · Toronto's Speed Cameras

What five years of Toronto's rotating speed cameras, and the first seven months after every one was switched off, show in the collision record.

The kind of evidence this is. These are observational data from a programme that launched into a pandemic-era traffic collapse. We report associations, carefully tested, and state the uncertainty plainly. The camera-free-year readings are preliminary and sealed before the data existed; a confirmatory re-pull is due October 2026.

−4 to −7%

Crash change while a camera operated

most defensible range across designs

0.92

Odds ratio for injury collisions near cameras

p < 0.001, about 8% lower

62%

Of 383 sites saw crashes rise after the camera left

p = 2.58 × 10⁻¹⁰

−28.6 pp

Injury gap at former sites, Jan–Jun 2026

vs control areas, calibrated p < 0.0001

400–1,700

Collisions avoided over 5.4 years

incl. 60–260 injury collisions

4–15

Killed or seriously injured outcomes prevented

imputed, not directly measured

The programme

Toronto ran the only large North American speed camera programme that rotated its cameras. From July 2020 to November 2025, roughly 50 units rotated across 520 sites in all 25 wards over 627 enforcement periods, typically three to six months at a time, with 96 sites cycled more than once. Each site therefore has its own before, during and after, and can be compared with itself rather than with a different street across town. That matters because cameras were placed deliberately at the city's worst locations, so any comparison against other places measures where cameras went as much as what they did.

We matched 790,725 Toronto Police collision records from 2014 through 2025 to all 520 sites. As far as we know, no previous Canadian evaluation has matched individual collision records to individual camera locations; earlier studies used aggregate crash counts or speed compliance data. Ontario's Bill 56 received Royal Assent on 3 November 2025 and every camera came down on 13 November.

Crashes

Crash rates ran lower at a site while its camera operated, and how much lower depends on the design. Within-site designs cluster between −5 and −10 percent; designs that also net out the calendar sit lower. We read −4 to −7 percent as defensible and decline to publish a single number.

Design	Estimate	p
Within-site, raw (each site vs itself)	−10.2%	2.2 × 10⁻⁶
Within-site, 2017-truncated baseline (RTM guard)	−6.9%	n/a
Within-site, cohort-weighted decomposition	−5.5%	n/a
Calendar-matched control cells	−3.9%	0.006
Callaway–Sant'Anna (assumption questioned)	+1% to +3%	n.s.

The average conceals real unevenness. 304 of 520 sites recorded fewer crashes during enforcement and 216 recorded more, so about four in ten showed no improvement. Three of our eleven formal tests came out significant in the wrong direction, which we read as the signature of placement at the worst locations rather than of cameras causing harm.

The effect holds at every buffer distance

Buffer	Crashes near camera	Median change	Sites improved	p
100 m	43,795	−22.9%	63.6%	2.6 × 10⁻⁶
150 m	64,113	−15.6%	61.3%	8.3 × 10⁻⁶
200 m	89,413	−9.3%	58.7%	8.7 × 10⁻⁶
250 m (primary)	126,644	−10.2%	58.5%	1.0 × 10⁻⁵
400 m	250,354	−4.8%	56.0%	3.0 × 10⁻⁴
500 m	337,219	−6.1%	58.1%	1.2 × 10⁻⁵

**Effect by distance, out to one kilometre.** The reduction is largest at the tightest radius and attenuates with distance, which is the gradient a spatial deterrence account predicts. It persists to one kilometre (median −4.5%, p < 10⁻⁹).

Injuries

The clearer association is with fewer people hurt. In a staggered comparison with year controls, the odds that a collision near a camera involved injury declined about 8 percent more than in the rest of the city.

Measure	Value	p
Injury odds near cameras, staggered DiD with year controls	OR 0.920 (≈ −8%)	2.3 × 10⁻⁵
Same, simpler specification	OR 0.951	0.005
Sites with injury-rate rise after camera departure	46% (no rebound)	0.94
Median monthly injury rate, during → after	0.164 → 0.124	n/a
Injury share of crashes, before → during → after	15.1% → 14.4% → 14.0%	n/a

Two things distinguish the injury result. It did not reverse when cameras left, and it reaches farther than the crash benefit: at the 76 isolated cameras a trend-adjusted injury reduction near 24 percent appears out to 250 to 500 metres, where the crash reduction has already faded. An independent SickKids and Toronto Metropolitan University team measuring speeds rather than crashes found the share of vehicles speeding at camera sites down 45 percent, and the share travelling 20 km/h or more over the limit down 88 percent.

**The benefit did not stop at the camera pole.** Difference-in-differences adjusted change by distance band. Crash reductions fade beyond 250 metres; injury reductions carry farther.

Deaths and serious injuries

We estimate rather than measure this. The programme's 5.4 years work out at roughly 4 to 15 killed-or-seriously-injured outcomes prevented, and its removal at about 1 to 3 a year. Fewer than 20 such events occurred near camera sites in that period, in a file that ends in 2023, so no direct test is available to us. The figure scales the measured injury effect by an observed rate of 0.06 KSI persons per injury collision.

Estimate	Prevented KSI persons, 5.4 years	Per year
Lower bound (RTM-adjusted −4% effect)	~4	~1
Central (within-site Poisson −9.6%)	~9	~2
Upper (central + halo zone)	~15	~3

Our direct evidence on severe injury comes from London, where the KSI ratio near 304 cameras narrowed from 1.09 to 1.02 after installation.

What happened when cameras left

Among the 383 sites with a non-zero rate in both periods and at least three months of data afterwards, crash rates rose at 62 percent once the camera was removed. This is the evidence the rotational design exists to produce, since a downward trend or regression to the mean gives crashes no reason to climb when the camera goes.

**Crashes rose when cameras left.** Mean monthly crash rates at the 383 testable sites, with the site-by-site change alongside. We read this as direction rather than magnitude: once Toronto's post-COVID recovery is netted out, the excess specific to former camera sites cannot be distinguished from zero (−5.7 pp, interquartile range −34 to +38, p = 0.60).

Drivers appear to remember a camera, and that memory decays as the gap lengthens. At the 96 sites where a camera later returned, it issued about a third fewer tickets than on its first deployment, 14.6 a day falling to 10.5, with 72 percent of sites lower. The reduction is deepest, near two-thirds, when the camera returned within a year, and thins to about a fifth after gaps beyond two years.

How we know this is not simply the pandemic

The programme launched in July 2020, mid-collapse in traffic volumes, so any before-and-after comparison risks reading the recovery as a camera effect. Waterloo Region shares Ontario driving law, the pandemic timeline and similar urban form, and deployed no automated enforcement until February 2025.

**Waterloo had the same pandemic without the cameras.** Through 2023, the last clean vintage and the one our primary estimate uses, Waterloo reached 94 against Toronto's 82. The 2024 pair is hatched because Waterloo's publication format changed that year, lifting records 38 percent while halving the injury rate, so its 129 should not be read as roads getting worse.

Specification	DiD estimate (index pts)	95% CI	p
All collisions, 2019–2023 (primary)	−19.2	[−38.5, 0.1]	0.051
All collisions, 2019–2024	−25.2	[−46.9, −3.5]	0.023
Injury collisions, 2019–2023 (upper bound)	−55.1	[−74.9, −35.2]	<0.0001
All collisions excl. hit-and-run, 2019–2023	−22.3	[−41.7, −2.9]	0.024

Parallel pre-trends hold for total collisions (p = 0.24) and fail for injury collisions (p = 0.04), so the injury figures are labelled an upper bound and borrow none of this design's authority. With two cities no standard error is fully valid, a serial-correlation correction widens the interval past zero, and one control city cannot rule out a Toronto-specific shock arriving with the cameras.

**A synthetic Toronto points the same way.** A weighted blend of eleven camera-free Ontario municipalities, matched to Toronto's pre-camera trajectory. Real Toronto runs roughly 5 to 6 index points below its synthetic twin for collisions and about 16 for injury collisions. The placebo test sits at p = 0.250 and cannot clear conventional thresholds with so few donor cities, so we read this as directionally consistent and exploratory.

Police enforcement

Cameras and officers operated independently, and we found no evidence of substitution in either direction. Both tests run at neighbourhood level, which limits their power.

Measure	Value	p
Speeding tickets, cameras vs police radar	2,150,715 vs 436,307 (≈ 4.9 : 1)	n/a
Police ticketing change after 2020, camera vs non-camera areas	+124% vs +122%	n/a
Camera effectiveness by police-activity tercile	no gradient	0.41
Same, controlling for baseline crash rate	no gradient	0.34
Crash rise after removal, by police response	≈ +28% either way	0.62
Police backfill of camera gaps, per active camera-month	−0.4%	0.65
Tickets per month, median camera vs officer	280 vs 76	n/a
Replacing 50 cameras' output	≈ 185 officers; $25.8M vs $2.5M	n/a

Covering all 520 sites around the clock would take an estimated 5,756 officers, more than the entire Service. Ticket volume is not the right metric, though, and the substitution tests suggest even volume-matched officer enforcement would not have prevented the post-removal rise.

The camera-free year

We committed our predictions in writing on 18 July 2026, before any 2026 collision record was pulled, and ran them with frozen, checksummed code. Through June 2026 crashes at former sites rose no faster than the rest of the city. Injuries ran the other way.

Window (2026)	Former-site crash excess	Share above control	p	Injury excess	p
Jan–Apr (sealed primary)	−6.9 pp	47.6%	0.998	−33.6 pp	<0.001
Jan–May (sensitivity)	−3.8 pp	45.5%	0.971	−33.6 pp	<0.001
Jan–Jun (sensitivity)	−3.4 pp	45.7%	0.811	−28.6 pp	<0.001

**Crashes straddle zero; injuries sit left of it.** Each dot is one former camera site over January to June 2026, with the control area's own change subtracted. Because small counts skew, we calibrated against 4,000 simulated runs in which former sites follow the control exactly; the observed injury median fell outside the null in every run (p < 0.0001).

**The gap is not fading month to month.** Monthly injury gaps run −5.1, −12.5, +7.8, −12.6, −8.9, +3.9 points with no trend (ρ = +0.09, p = 0.87). A balanced early-late split puts it at 27 points early and 30 late. Camera-era placebo years run the opposite way.

Two accounts of the suppression, both still open

Drivers trained by five years of enforcement may have kept the habit, or the standing school-zone features that remain at nearly every former site may carry it: signage, markings, zone speed limits. The channels we can measure do not explain it. The suppression is at least as deep at sites that never had a co-deployed radar sign, physical co-treatment exposure does not track it (p = 0.85), and camera tenure shows no dose relationship (ρ = −0.08, p = 0.36).

**The 2026 window sits inside the flat part of the decay curve.** Retained deterrence at returning cameras runs −64 percent under 12 months of absence, −34 percent at 12 to 24, and −21 percent beyond (p = 0.005). Months two through seven sit where an imprint should still be near maximum, so a flat gap is consistent with both accounts. The window that separates them runs November 2026 to November 2027.

Equity, and how many cameras a network needs

Among the 228 sites we could match to Census neighbourhoods, 43 percent sat in Neighbourhood Improvement Areas or Emerging Neighbourhoods against 27 percent of neighbourhoods citywide. That placement is a fact. Whether cameras worked differently there is an estimate, and within our power the answer is no: we detected no difference in benefit by income, poverty rate, visible-minority share or the City's composite wellbeing index, with p-values from 0.15 to 0.63. We report it as a null with limited power.

**Concentration of benefit is a poor argument for a smaller network.** About half the avoided crashes came from roughly 40 of the 520 sites and 90 percent from 168. The concentration mostly reflects the skew of busy intersections; reshuffling site performance at random produces more concentration, not less. We cannot predict which sites will respond, since a site's first-deployment performance does not predict its second (ρ = 0.13, p = 0.22), so 168 randomly chosen sites would be expected to capture about a third of the benefit.