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Category: Effects
Type: Offsetting behavior that shrinks the safety gain from a protection, because the person who is protected takes more risk
Origin: Sam Peltzman, Journal of Political Economy 83(4), August 1975, pages 677–725. The two-word name is the one used in his September 2004 AEI-Brookings lecture
Also known as: Offsetting behavior. Risk compensation is the broader label
Quick Answer — The Peltzman Effect is offsetting behavior that shrinks the safety gain from a protection, because the protected person takes more risk. Sam Peltzman argued this in 1975 for devices that cars were required to carry. His abstract says the offset was virtually complete. A later study of laws that require people to wear belts is a different rule. In that state panel, higher belt use still cut occupant deaths per mile. The instrumented estimate for people outside the car was not a significant rise.

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What is the Peltzman Effect?

The Peltzman Effect is offsetting behavior that shrinks the safety gain from a protection, because the person who is protected takes more risk.
This article indicates that these offsets are virtually complete, so that regulation has not decreased highway deaths.
That sentence is the abstract of Peltzman’s 1975 paper. The protection in that paper is a device the car must carry. A later law that tells a person to wear a belt is a different rule, and it has its own numbers. A life jacket lowers the cost of a rough trip for the person who wears it. It does not lower the cost for a swimmer the boat may hit. That picture is an illustration. It is not one of the studies on this page. The pages next door measure other misses. Zero-Risk Bias is a preference for driving one risk all the way to zero. Illusion of Control is a personal expectancy above the chance on a task, once a skill cue is present. A belt changes the expected harm of a crash. It is not those two results.

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The Peltzman Effect in 3 Depths

  • Beginner: A belt can soften a crash for the person wearing it. The same driver can still choose a faster trip. Write both facts before you judge the belt.
  • Practitioner: Keep two counts, people inside the car and people outside it. The 1975 abstract says the second count rose. In the later belt-use panel, the instrumented estimate for that count is -0.042, and it is not marked significant.
  • Advanced: A laboratory range of 40 to 50 percent, an elasticity of -0.133, and a law’s 5.43 percent are three different objects. Peltzman’s 2004 lecture says the economic logic does not tell you how large the offset will be.

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Origin

The 1975 paper is Sam Peltzman, “The Effects of Automobile Safety Regulation,” Journal of Political Economy, volume 83, number 4 (August 1975), pages 677–725. The journal PDF was not re-read. The sentences below from that paper are the abstract, as printed by the journal. Peltzman is at the University of Chicago in the September 2004 lecture used here. The abstract says technological studies imply that annual highway deaths would be 20 percent greater without legally mandated safety devices on automobiles. It says those studies ignore offsetting effects of nonregulatory demand for safety and of driver response to the devices. It then says the offsets are virtually complete, so regulation has not decreased highway deaths. Time-series data, and not the cross-section, imply some saving of auto occupants’ lives at the expense of more pedestrian deaths and more nonfatal accidents. The 20 percent is the engineering claim he says was offset. It is not a death toll he measured on a road. In September 2004 he gave the AEI-Brookings Joint Center Distinguished Lecture, “Regulation and the Natural Progress of Opulence,” Related Publication 04-21. The lecture’s summary uses the name Peltzman Effect for offsetting behavior of this kind. He dates the regulatory break to the National Traffic and Motor Vehicle Safety Act of 1966. The first standards he names required installation of seat belts, collapsible steering columns, and pop-out windshields, among others. Installation is not the same as a later fine for leaving a belt unbuckled. He says the economic logic is that the devices lower the price of risky driving, because a crash is less severe for the occupant. The logic does not say whether the offset is partial, complete, or more than complete. His account of the mid-1970s facts is that occupant deaths per accident fell substantially, and that this was entirely offset by more accidents and by more deaths among pedestrians, bicyclists, and motorcyclists. That is the 2004 lecture’s recollection. It is not a table cell copied from the 1975 PDF. He also says the finding met considerable skepticism. The same lecture gives a long decline that predates the agency. From 1925 to 1960, deaths per mile driven fell at 3.5 percent a year. From 1965 to 2002, highway fatalities per vehicle mile fell at 3.5 percent a year. He treats the match as a reason for skepticism about the regulation. In the next paragraph he says the natural progress of opulence is probably more important here than offsetting behavior, and that safety would likely have kept improving had the agency not been created. Those are two sentences. This page does not fold them into one.

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Key Points

Four readings keep each number on the rule that produced it. A device a car must carry is not a fine for an unbuckled belt. A crash-test percent is not a state’s death rate.
1

Separate the device from the trip

Holding the number of crashes fixed, a belt protects the person who wears it. Cohen and Einav report a government survey of laboratory evidence, Department of Transportation 1984: belt use by front-seat passengers could prevent 40 percent to 50 percent of fatalities, compared with unrestrained people. That range sits inside a crash. It is not the change in a state’s deaths when a law raises belt use. This page did not re-read the 1984 survey.
2

Let the logic stop before the size

Peltzman’s 2004 lecture says a mandated device reduces the price of driving faster or more aggressively, because the expected harm of a crash is smaller. Simple economics then says the devices encourage more risky driving, and that this offsets the promised gain to some degree. He says the reasoning stops there. Partial, complete, and more than complete are all open until someone counts. Cobra Effect is a reward that brings more of the thing it was meant to cut. A belt is not a bounty.
3

Count the people the belt cannot cover

Pedestrians and bicyclists do not wear the car’s belt. Cohen and Einav treat their deaths as a cleaner test of offsetting behavior than occupant deaths, because occupants face both the protection and any change in driving. In their instrumented column, the elasticity of non-occupant deaths per vehicle mile with respect to belt use is -0.042, with a standard error of 0.121, and no significance star. The standard error is wide. The estimate is not a precise zero, and it is not a rise.
4

Keep a smaller gain

The same column for occupants is -0.133, standard error 0.047, marked at their 1 percent confidence level. A 10 percent higher belt-use rate, in their words, reduces occupant fatalities by about 1.35 percent. Their conclusion rounds the elasticity to about -0.135. The positive column, estimated without state fixed effects, is +0.114. They treat that positive sign as the result of belt use being chosen, not as the effect of the laws. A gain that is smaller than a crash dummy promised can still be a gain.

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Applications

Write the person the protection covers, the person it does not cover, and the column that holds the place fixed. Then read the percent again.

Split the death rate before you judge the device

Before you say a safety rule failed, write deaths inside the car per vehicle mile and deaths outside it. The 1975 abstract says time-series data show a saving of occupants at the expense of pedestrians, with a virtually complete offset of total deaths. That sentence is the abstract. The 1975 tables were not re-read, so no coefficient from them is on this page.

Park the crash-test percent beside the state percent

The 40 to 50 percent figure is a laboratory comparison of a belted front-seat passenger with an unrestrained one, holding crashes fixed. The state elasticity of occupant deaths per mile is about -0.13. The two numbers answer different questions. A training slide that prints only the laboratory range has not reported what the state panel found.

Write who a workplace guard covers

When a guard, a harness, or an alarm is added, write injuries to the person it protects and injuries to the person it does not. Peltzman’s lecture uses the pedestrian, the bicyclist, and the motorcyclist as the second group for car devices. A shop that copies the belt elasticity has not copied the 556 state-years. The -0.133 stays on that panel.

Read the column that holds the state fixed

The same belt-use file gives +0.114 for occupant deaths when states are not held fixed, and -0.133 when belt use is instrumented by the laws. The first column is the one they say is biased by the choice to wear a belt. A memo that quotes only +0.114 has quoted the column they set aside.

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Case Study

Alma Cohen and Liran Einav studied mandatory seat-belt laws in the United States. The text read here is Harvard Law School John M. Olin Center Discussion Paper No. 341, last revision October 2001. Both authors are listed then in the Department of Economics at Harvard. The paper later appeared as “The Effects of Mandatory Seat Belt Laws on Driving Behavior and Traffic Fatalities,” The Review of Economics and Statistics 85(4), November 2003, pages 828–843. The journal typeset was not re-read. Every coefficient below is the discussion paper. The file is the 50 states and the District of Columbia, from 1983 through 1997. During that window every jurisdiction except New Hampshire adopted some belt law. New York’s law began on 1 December 1984. Primary enforcement means an officer may stop a car for the belt alone. Secondary enforcement means the belt can be cited only when the car was already stopped for something else. Belt use is the observed share of front-seat occupants wearing a belt. Early years are missing for many states, so the regressions have 556 rows. A complete grid would have been 51 jurisdictions times 15 years, which is 765. The mean observed use in those 556 rows is 52.89 percent. They regress the log of fatalities divided by vehicle miles traveled on the log of belt use. Year effects are in every column. The instruments are three law indicators: secondary enforcement, primary enforcement that did not follow a secondary law, and a switch from secondary to primary. Their note marks three stars at the 1 percent confidence level, two stars at 5 percent, and one star at 10 percent. Standard errors are robust. For occupants, ordinary least squares without state effects gives 0.114 (standard error 0.029). With state effects the coefficient is -0.053 (0.022). Instrumented, it is -0.133 (0.047). Using the other use series, from the Centers for Disease Control, as an instrument for measurement error alone gives -0.097. They read that split as about half measurement error and half the choice to wear a belt, inside the gap between the state-effects column and the law-instrument column. For non-occupants the same three columns are 0.158 (0.056), -0.119 (0.058), and -0.042 (0.121). The last cell has no star. They say the positive first column could be read as a Peltzman effect, and that it lines up with earlier papers that did not treat belt use as chosen. Once the laws instrument use, they find no significant support for compensating behavior. A regression on pedestrians alone, leaving bicyclists out, also leaves the use coefficient insignificant. They do not print that coefficient. A count of police-reported crashes, 17 states from 1989 through 1994, likewise leaves the use coefficient insignificant. They call crash counts poorly defined, because many minor crashes never produce a report. On the first stage, with state effects, a secondary law raises belt use by 0.112 (standard error 0.012). A primary law that did not follow a secondary law raises it by 0.219 (0.024). A switch from secondary to primary raises it by 0.135 (0.017). Their prose reads the primary coefficient as about 22 percentage points, the secondary coefficient as about half of that, and the switch as about 13 percentage points. They then turn the occupant elasticity into lives. A 10 percent higher use rate cuts occupant fatalities by about 1.35 percent and has no significant effect on non-occupant fatalities, which they say is about 500 lives a year at the national level. Moving national use from 68 percent to the unmet year-2000 target of 85 percent is about 1,000 to 1,500 lives a year. Moving every secondary state to primary enforcement, from 68 percent use to about 77 percent, is about 500 lives a year. The 68 percent in the introduction is the 1996 national level. Do not add 500 to 1,000. They also say their elasticity is less than half the figure used by the National Highway Traffic Safety Administration, which they describe as a 45 percent elasticity based on belt use among drivers in fatal crashes. That 45 percent is not the laboratory range of 40 to 50 percent. The lesson is a use law, a state panel, and an occupant elasticity of -0.133 beside a non-occupant elasticity of -0.042 that is too noisy to call a rise. The -0.133 is 556 state-years of belt use. It is not the 1966 installation standards, and it is not one driver’s afternoon.

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Boundaries and Failure Modes

The Peltzman Effect is the wrong summary in three retellings. The 1975 abstract is treated as the belt-use panel. A noisy zero is treated as proof that offsetting never happens. A state’s percent is carried into a shop or a clinic. The first boundary is the rule. The 1975 abstract is about devices cars had to carry, and it says the offset of total highway deaths was virtually complete. Cohen and Einav are about fines and stops for not wearing a belt, two decades later. Their instrumented occupant elasticity is negative and marked at 1 percent. Peltzman’s 2004 lecture describes their paper as one in which non-occupant deaths are not an important part of the story, and in which the real-world effect still falls short of a world with no behavioral response. His phrase that the laws should have saved over three times as many lives was not in the October 2001 discussion paper. It is not repeated here as their result. Unintended Consequences is a result the rule did not name. The abstract names more pedestrian deaths. The belt panel’s instrumented non-occupant cell does not. The second boundary is the later reading of the same laws. D. Mark Anderson, Yang Liang, and Joseph J. Sabia, NBER Working Paper 30851 (January 2023), replicate the published reduced form and then extend it. The journal version of their paper was not re-read. They report that Cohen and Einav’s 2003 reduced form associated primary laws with a 5.9 percent lower occupant fatality rate and secondary laws with a 4 percent lower rate. Their own 1983–1997 replication, with errors clustered by state, is a decline of 0.0012 in the occupant fatality rate for a primary law that did not follow a secondary law, which is 5.43 percent of a pre-treatment mean of 0.0221. Secondary laws are a decline of 0.0007, or 3.30 percent. The switch from secondary to primary is small and not significant. Non-occupant coefficients in those main columns are small and indistinguishable from zero. Lengthening the file through 2019, a primary law is a decline of 0.0020, or 9.05 percent, and a secondary law is 3.78 percent. The switch stays insignificant, and the main non-occupant columns stay indistinguishable from zero. Their abstract’s “5 to 9 percent” is this primary-law range, not a third estimate. When they weight by population, the switch indicator is positively and significantly tied to the non-occupant rate in three of four specifications. In a log specification, primary laws are tied to a higher non-occupant rate for 1983–1997, and that estimate loses significance through 2019. In one interaction-weighted log specification, secondary laws are tied to a higher non-occupant rate, and they say that is the only specification in which they find it. “Little evidence” in the main columns sits beside those footnotes. It does not erase them. The third boundary is the export. The -0.133, the 5.43 percent, and the 3.5 percent a year are not a helmet program, a factory guard, or a hospital protocol. The 3.5 percent is Peltzman’s long decline in deaths per mile, twice, and he pairs it with a sentence that gradual progress may matter more than the offset. A team that treats every new protection as fully canceled has not read the belt panel. A team that treats every new protection as the full laboratory percent has not read it either.

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Common Misconceptions

Three retellings travel with the name. One says the devices saved nobody. One says the offset is always complete. One treats a crash-test percent as the change in a state’s death rate.
The 1975 abstract says regulation has not decreased highway deaths, and that occupants were saved at the expense of pedestrians. That is his claim about installation standards, from a PDF this page did not re-read. In the belt-use panel, the instrumented occupant elasticity is -0.133. Anderson, Liang, and Sabia report primary-law reductions of 5.43 percent in the original window and 9.05 percent through 2019. A device can fail to cut the total, in the 1975 abstract, and a use law can still cut occupant deaths per mile.
Peltzman’s 2004 lecture says the economic logic does not choose partial, complete, or more than complete. Complete offset is his reading of the mid-1970s installation standards. In the belt-use panel the instrumented non-occupant elasticity is -0.042 with a standard error of 0.121, and no star. Anderson’s main columns also fail to show a rise in non-occupant deaths. Some weighted and logged specifications do show a rise. Complete, everywhere, is not what these files print.
The 40 to 50 percent is Cohen and Einav’s report of a 1984 laboratory survey: front-seat belt use, compared with no restraint, holding the crash fixed. Their state elasticity is about -0.13. The 45 percent they attribute to the highway-safety agency is a third figure, tied to belt use among drivers in fatal crashes. None of the three is the 5.43 percent primary-law reduction. A slide that prints one of them as all of them has changed the question.
The Peltzman Effect sits beside a wish to erase one risk, beside a felt sense of control, beside a bounty that backfires, beside a result a rule did not name, and beside a judgment that inaction is gentler.

Zero-Risk Bias

A preference for driving one stated risk all the way to zero. The question here is whether a protection changes the risks people then take.

Illusion of Control

A personal expectancy above the chance, once a skill cue sits on a chance task. A belt changes the harm of a crash. It is not that card result.

Cobra Effect

A reward that brings more of the thing it was meant to reduce. The offset here is a change in driving after a protection, not a bounty per animal.

Unintended Consequences

A result the rule did not name. The 1975 abstract names more pedestrian deaths. The belt panel’s instrumented cell for people outside the car is not a significant rise.

Omission Bias

A harm from not acting, rated less bad than the same harm from acting. A belt law requires an action. It is not that rating of a written case.

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One-Line Takeaway

Before you credit a protection with the full engineering gain, write the rate for the person it covers and the rate for the person it does not.