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and the growing field of forensic economics (Zitzewitz 2012). Using data from private emissions facilities in New York State, we examine the impact of the.
Discretion and Manipulation by Experts: Evidence from a Vehicle Emissions Policy Change Lamar Pierce and Jason Snyder1 Abstract: Environmental regulation seeks to limit pollution through strict emissions thresholds for existing cars, yet it remains unclear how frequently inspectors enforce these and what impact test manipulation has on policy efficacy. We demonstrate (1) a strong discontinuity in the emissions results distribution, with vehicles expected to barely fail missing from the data; and (2) When the state tightens emissions standards, over 50% of vehicles newly at risk show instantaneous test improvements. These improvements cannot be explained by legitimate repairs and are consistent with facilities exploiting procedural discretion in order to help consumers evade strengthened regulations. Keywords: Fraud, Corruption, Forensic Economics, Environmental Policy, Moral Hazard, Regulation

                                                                                                                        1 Thanks to seminar participants at Washington University St. Louis, University of California Los Angeles, and the Southern California Conference in Applied Microeconomics. Volodymyr Bilotkach and Matt Kahn provided us with thoughtful comments. All mistakes are ours alone. Lamar Pierce is an associate professor at the Olin Business School, Washington University in St. Louis. He is the corresponding author and can be reached at [email protected] or at One Brookings Drive Box 1133, St. Louis, MO 63130. Jason Snyder is an assistant professor at the Anderson School of Management, UCLA.

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Electronic copy available at: http://ssrn.com/abstract=1831494

I. Introduction

Vehicle emissions are one of the most important determinants of environmental quality worldwide, accounting for over half of carbon monoxide, 29 percent of hydrocarbon emissions, and 10 percent of total suspended particulate emissions in the United States (Ernst et al. 2003; Currie and Walker 2011). The severity of these externalities makes government regulation necessary for optimally limiting mobile source emissions, and while one effective regulation is to control emissions levels in newly-produced cars, governments must also inspect older cars to ensure that deterioration does not generate excessive pollution.2 This regulatory testing of used cars typically employs strict emissions thresholds to assign a passing or failing status to a vehicle. Under strict application of the regulation, all vehicles emitting particulate levels above the threshold would be repaired or decommissioned. When the government desired a lower level of pollution, it could simply increase the stringency of the emissions threshold. Marginal vehicles that barely passed prior to the threshold increase would then fail the emissions inspection, be repaired, or be replaced by cleaner vehicles. This marginal change in emissions thresholds would thereby improve air quality. In a world with precise regulatory enforcement, the relationship between increasing the stringency of an emission threshold and reducing pollution would be mechanical, with the marginal benefit of such a policy change easily predictable. Yet agency concerns pervasive in the regulatory apparatus suggest otherwise. In the United States, most states delegate emissions inspections to private sector facilities.3 The historical debate on privatization has largely revolved around tradeoffs between the operational efficiency of the private sector vs. reduced incentives for fraud in the public sector (Lazare 1980; Voas and Shelley 1995). Private inspection facilities are responsible for testing vehicles to ensure they are below the emissions threshold and for reporting those vehicles that are excessive polluters. Inspectors at these facilities have considerable discretion in what constitutes a fair test. The state allows them to stop or repeat any test they feel does not accurately represent the true emissions of the vehicle in order to avoid the reporting of inaccurate results. While this discretion may eliminate some false positive results from the testing procedure, it also provides considerable opportunity for moral hazard on the part of the expert agent. This moral hazard could produce                                                                                                                         2 Davis (2008) and Currie and Walker (2011) show that other policies, namely driving restrictions and E-ZPass, can also reduce total emissions and improve health. 3 A survey of state websites identified that 27 states outsource to multiple licensed private inspection firms, 11 use staterun facilities, one uses both state-run and private facilities, and one uses a licensed private monopoly.

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Electronic copy available at: http://ssrn.com/abstract=1831494

behavior with questionable legality, such as when an inspector repeatedly tests a marginal vehicle until it finally appears to be passing. But it may also produce outright fraud, where the inspector substitutes a cleaner vehicle in the test, or diverts exhaust from the testing equipment. There is ample anecdotal (Lambert 2000; States News Service 2010) and academic (Hubbard 1998; 2002; Pierce and Snyder 2008; Oliva 2012) evidence suggesting that private sector inspectors fraudulently pass vehicles that should fail in exchange for bribes or implicit promises of future business. While existing studies estimate average levels of emissions testing fraud, we take a marginal approach by examining only those vehicles made newly at risk by tightened emissions standards. More specifically, our paper examines how severely these agency concerns undermine the ability of a state government to curtail pollution through increasing the marginal stringency of emissions thresholds. Unlike prior work, we demonstrate that the discretion of private emissions inspectors may limit the State’s ability to reduce mobile emissions by simply increasing the stringency of the regulation. Understanding this impact is critical for policy because it helps predict the marginal effect of discretion on future policy changes in mobile emissions standards, rather than estimating the average effects as seen in previous work. Our work further contributes to research on the gaming and efficiency of “notched” policies (Blinder and Rosen 1985; Sallee and Slemrod 2010), and the growing field of forensic economics (Zitzewitz 2012). Using data from private emissions facilities in New York State, we examine the impact of the agency problem on the state’s implementation of stricter emission standards in 2003.

A key

dilemma in uncovering the extent of this manipulation is that it is intentionally performed under a veil of secrecy. Although it is difficult to determine if any individual test is fraudulent, the distribution of all testing data can leave systematic evidence of manipulation. We focus on each vehicle’s first test of each year, since these first tests are when the inspector first observes the failing condition of the vehicle prior to diagnosis and repair. Absent manipulation, one would expect the distribution of these initial emissions test scores to be continuous throughout the domain of possible scores. When we examine the distribution of emissions results we find sharp discontinuities at the regulatory thresholds in Figures 2-5.4 Many of the vehicles to the right of the line, which must be repaired before legal operation, appear to be missing.                                                                                                                         4 For other uses of regression discontinuity in forensic economics, see (Duggan and Levitt 2002; Wolfers 2006; Snyder 2010 & 2012; Forbes et al. 2011). Levitt and Porter (1999) posit a structural approach to specifying a counterfactual distribution akin to the regression discontinuity design.

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We investigate what happens to these missing vehicles by studying how the distribution of initial test scores changes when the regulation becomes more stringent (the line moves to the left). We find that when the stringency of the regulation is tightened for two of the pollutants (hydrocarbons and nitrogen oxide), approximately 50% of the vehicles only at risk of failing in the new regime have shifted to the passing range, which we represent in Figures 3-5. The observed distribution is consistent with inspectors observing the vehicle’s emissions and assisting the vehicle in passing the official test result. When the threshold becomes stricter, inspectors respond by manipulating the results for vehicles that are newly at risk of failing. An alternative explanation to our interpretation of inspector manipulation is that in response to the new regulation, vehicles newly at risk are preemptively repaired prior to their first test. Our results cast doubt on this hypothesis by demonstrating a dramatic shift of vehicles from above to below the new threshold immediately after the policy change. We observe this large shift in tests occurring within a day (Figure 6) and several hours (Figure 7) of the policy shift. If these vehicles were preemptively repaired we would expect a more gradual increase in the rate of change due to the necessary time lapse for repair. Furthermore, there is little incentive for the owner to request legitimate preemptive repairs, since a second test following the repair of an initially failing car is free. This evidence casts considerable doubt on the alternative hypothesis of preemptive repair, and suggests that a substantial number of vehicles pass as a result of inspectors abusing their discretion in direct response to the increase in regulatory stringency. Finally we find no evidence that owners of automobiles newly at-risk under the strengthened regulation game the policy changes through earlier inspections. Figures 8 and 9 show that that the older vehicles exposed to a more stringent threshold were no more likely to be inspected in the days leading up to the policy change than newer cars not impacted by the new regulations. This paper proceeds as follows: Section 2 describes the market for emissions testing; Section 3 describes the data; Section 4 provides the methodology and results; Section 5 concludes.

II: The Market for Emissions Testing

The Federal Environmental Protection Agency (EPA) mandates which states must institute vehicle emissions programs, yet leaves the implementation of these programs to state governments. Some states directly test vehicles at state-owned facilities, but many outsource some or all testing to 4

licensed privately-owned firms. Emissions inspectors working at these private facilities are legally required to follow strict testing procedures, yet have discretion to diverge from these policies. With dynamometer-based tailpipe testing common in many regions, skilled mechanics can make temporary adjustments that allow almost any vehicle to pass emissions tests without addressing the underlying causes of the excess pollution. Even the most polluting cars can be certified clean when inspectors substitute other cars during testing procedures. Evidence from Hubbard’s (1998) study of California inspections suggests such fraud is quite common, similar to a 2001 covert audit program in Salt Lake City, Utah that found nearly 10% of facilities overtly testing one car in place of another (Groark 2002). Massachusetts found that vehicles retested by the state had substantially higher levels of emissions.5 In our focal state, a driver registering a vehicle weighing less than 8500 lbs. and newer than 1981 must have it tested for hydrocarbons (HC), carbon monoxide (CO), and nitrogen oxide (NOx), choosing any licensed facility to conduct the test. In order to pass, the vehicle’s emission score for hydrocarbons, carbon monoxide, and nitrogen oxide all must fall below a given threshold. Two measurements of each pollutant are taken: one that covers the full cycle of the four-minute dynamometer test and one that covers only the last ninety seconds of the test. As long as the vehicle passes one of these measures, it passes that part of the test. If a vehicle were to fail the four-minute hydrocarbons test, for example, but passed the last ninety-second test, it would be given a passing score on hydrocarbons. The only way to fail is to fail both of these tests.6 While many areas in the United States now test post-1996 model cars using OBDII, an onboard diagnostic system, a large portion of areas around the world still conduct emissions tests by analyzing the exhaust released from the vehicle’s tailpipe.7 Since vehicles made prior to 1996 still generate considerable mobile source pollution, dynamometer testing is still a critical means for providing environmental regulation even in states with OBDII testing. While in some states prices for emissions tests may vary, our focal state mandates a price of approximate $20 per test. When a licensed inspector conducts a dynamometer test, he follows a state-prescribed sequence of engine RPM (revolutions per minute) that measures emissions output at different engine loads. The inspector is allowed two tests to pass a vehicle, with the second chance designed to                                                                                                                         5 This report, published by the Massachusetts Office of the Inspector General, can be found at http://www.mass.gov/ig/publ/emissrpt.pdf. 6 These two measures are highly correlated. 7 Thirty-four states still use tailpipe testing, although most tailpipe tests are now restricted to pre-1996 vehicles, many of which are the worst polluters in operation.

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account for margin of error in test results and the possibility that the engine was not properly warmed up prior to testing.8 Inspectors strictly following protocol would conduct the first test, whose results would be provided to the state via electronic transmission. If the result is a pass, the vehicle is issued an inspection sticker and is then legal for registration. If the result of this first test is a fail, the inspector can then choose to run a second test. Cars passing the second test are issued stickers and can legally register. Cars failing the second test must be repaired, with repairs reported to the state prior to retesting the vehicle at the facility of the customer’s choosing. These repairs may involve simple (but time-intensive) replacements of engine seals or more expensive catalytic converter replacements. These repairs often result in a vehicle passing its retest, as the repairs correct the fundamental mechanical problem causing excessive exhaust. In some cases, however, the car will continue to fail, as the mechanical problems are either too extensive to be fixed or too expensive for the customer to afford. In this case, if the vehicle has received over $450 in repairs, the consumer can receive a oneyear exemption from the DMV. The facility must keep receipts of these repairs on-site in case of a DMV audit. While the facility could write fraudulent repair receipts for customers, this would increase the cost to the station of getting caught by involving much more serious tax fraud implications. If the vehicle has already received its one-year exemption, the customer can either junk the car, or resell it to a region with less stringent emissions requirements.9 The sequence above represents how inspectors strictly following government regulations would conduct testing. Yet inspectors gain information during the testing procedure that allows them to use their discretion to illicitly help high-polluting vehicles pass. This opportunity comes from the inspector’s discretion to stop the first test in process without reporting results to the state. During the course of the first test, the inspector is allowed to legally abort the test up to two times, just in case the inspector fails to follow the designated RPM trace or the testing machine is not working correctly, both of which are unusual events. While this discretion may provide for fewer cars failing due to test malfunction, it also provides an easy opportunity for inspectors to avoid failing a vehicle by providing them with information about likely test outcomes prior to officially reporting results. Since stopped tests are not reported to the state, the facility can use the stopped test                                                                                                                         8

Catalytic converters are ineffective at low temperatures. This option has interesting implications for the market for heavy-emitting vehicles. Davis and Kahn (2008), for instance, show that NAFTA caused many high emissions vehicles to move to Mexico, where they replaced even worse polluting cars. 9

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as a pretest providing information about the likely outcome of a test carried out to fruition. Thus, before the reported emissions test begins, the facility and customer know whether or not the car will pass, and approximately how near it is to the pass threshold. Except in rare cases of machine failure or error, the inspector strictly following regulatory procedures will conduct the first test to fruition. But for those inspectors willing to fraudulently pass vehicles, the results observed during the first test will likely determine how an inspector approaches the official test.10 If the car is passing the test, the inspector will likely let the test continue to completion, with the passing results sent to the state system. But if the car is failing, the inspector can stop the test and make several temporary adjustments to change the results. The inspector may use fuel additives, adjust the tailpipe probe, or divert exhaust before it reaches the tailpipe. Even more nefariously, the inspector may use a technique called “clean-piping”, substituting a car known to be clean for the failing vehicle in the official test.11 Since the inspector is required to check for customer tampering, it is difficult for customers to cheat on the emissions tests without the complicity of the mechanic. The inspector intending to help pass gross-polluters could let the vehicle fail the first test and then rerun the test after making illegal adjustments. Yet this presents a risk for the facility that the state will observe very different test results without reported repairs. It is much easier and less dangerous for the inspector to simply stop the first test during operation and send the fraudulently passing results as the first recorded data to the state. Inspectors have strong incentives to manipulate the test in order to pass vehicles. Hubbard (2002) identified that customers are more likely to return to inspection stations that have previously passed them for future. Firms in the emissions-testing market tend to profit from passing older cars, as this ensures that these cars will remain on the road and in need of future mechanical repairs. By contrast, customers who fail emissions tests are likely to either retest the vehicle at another facility,12 or buy new or newer cars that need little if any repair work. The incentives to pass vehicles are strong enough that they may lead to explicitly illegal behavior. The California Bureau of Automotive Repair noted that “it appears, based on BAR enforcement cases, that some stations improperly pass vehicles to garner more consumer loyalty for                                                                                                                         10

Inspectors may not need pretesting to predict failure, and may illegally alter the car prior to beginning. The use of clean-piping is further discussed in Hubbard (1998) and Oliva (2012) and has been confirmed anecdotally. 12 This is similar to the “audit shopping” studied in the accounting literature (e.g, Davidson et al. 2006). Bennett et al. (2012) find that higher numbers of proximate emissions facilities increase both pass rates and the switching behaviors of car owners 11

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delivering to consumers what they want: a passing Smog Check result” (California Bureau of Automotive Repair 2011, p. 22). In contrast, the incentives to fail a vehicle are weak, even for facilities that might retain the customer for immediate repair work. Emissions repair bills are limited to the $450 necessary to receive a one-year waiver, an amount worth much less than the annual service and repair bill the facility could charge in subsequent years. Edmunds.com, for example, estimates the annual service and repair costs of a 5-year-old Chevrolet TrailBlazer at $2,089, with older vehicles having even higher annual revenue potential. Allowing polluting cars to pass emissions has clear costs for society, increasing air pollution in urban areas.

The three tested pollutants, CO, HC, and NOx, all have proven health

consequences. Carbon monoxide, an odorless, poisonous gas, inhibits the transport of oxygen from blood into tissues, and can cause general difficulties in the cardiovascular and neural systems (Utell et al. 1994). When combined in the presence of sunlight, HC and NOx form ground-level ozone that can aggravate respiratory problems, especially in children, and may cause permanent damage to lung tissue (Utell et al. 1994). The health cost of vehicle emissions has been estimated as between $29 billion and $530 billion in 2001 (U.S. EPA 2001). A ten-year study of children conducted by the University of Southern California found evidence linking air pollution to reduced lung function growth, higher absenteeism from respiratory problems, and asthma exacerbation and development (Gauderman et. al 2002).

III: Data

Our dataset comes from the New York Department of Environmental Conservation, where emissions testing is conducted by licensed private firms. We use vehicle inspections conducted on gasoline-powered vehicles under 8,500 pounds just before and after the state implemented a policy change on April 1, 2003 that lowered the threshold for two of the measured pollutants (see Figures 2 & 3). We segment our sample by vehicle model years, because the policy decreased the threshold most severely for vehicles with model years between 1983 and 1990.

Vehicles manufactured

between 1991 and 1995 saw a smaller decrease in the passing threshold, while those manufactured in 1996 or afterward saw no change in the pass threshold.

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Furthermore we limit our sample to vehicles tested three months before and after the policy shift.13 These data include vehicles owned by individuals, corporations, fleets, and government agencies, although we are unable to directly observe vehicle ownership. Only those vehicles in downstate New York are included, as upstate vehicle face different sets of regulations. The data collected during inspections include inspection date, inspection time, vehicle identification number (VIN), facility identifiers, inspector identifiers, and inspection results. These data allowed us to uniquely identify vehicles, including characteristics such as make, model, year, and odometer reading. The detailed information on time and location of inspection as well as vehicle characteristics allow us to control for most predictors of vehicle deterioration and likely emissions.

IV: Empirical Methods and Results

To establish evidence of the presence of discretionary passing by repair stations, we first examine the entire distribution of vehicles emissions results for vehicles tested by the state in 2003. The inspection generates six unique measures: the amount of HC, NOx, and CO pollutants for both the idle and transient components of the test. A bright line rule assigns whether the vehicle has passed or failed that component of the test. If a measure is below a discrete threshold designated by the state, it passes that component of the test. If it is above the threshold it fails. We exploit a policy change in April 2003, however, that lowered the threshold such that many cars that passed in the previous year would not pass in late 2003. This policy change represented an attempt by the state to reduce overall vehicle emissions and airborne particulates by requiring vehicles that had barely passed emissions tests in the previous years to be repaired or replaced. We provide summary statistics on all tests within three months before and after the policy shift in Table 1, separating the tests into our three model-year samples (1982-1990, 1991-1995, 1996-2002). Based on observable vehicle characteristics, there appears to be little difference in the vehicles brought it during the two periods, a point we will focus on later in our identification.

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Our results do not change if we alter the window size. 9

In Figure 2 we plot the distribution of hydrocarbon test results three months prior to the strengthening of the regulatory threshold.14 In this graphic there clear evidence of a discontinuity in the distribution test results precisely at the old regulatory threshold. If the inspector were not reacting to the regulatory threshold on the first test result, one would expect to see a continuous density function.15 In Figures 3a and 3b, we show what happens to the distribution of hydrocarbons results when the threshold is moved inward for model-year 1982-1990 vehicles. The dots represent the distribution of test results within three months before the policy shifted inward (between January 1 and March 31 of 2003) and the x’s represents the distribution of test results within three months afterwards (between April 1 and June 30 of 2003). Vehicles that have an emissions reading just below the higher pre-April threshold would have passed the hydrocarbon test prior to the policy shift but would have failed the post-April test. Similarly, Figures 4a and 4b present the policy change and distributions for nitrogen oxide, which also received more stringent thresholds on April 1. Figures 5a and 5b represent the results for the two carbon monoxide tests surrounding the April 1 policy change, which did not impact carbon monoxide. The figures clearly show that discontinuities at the new regulatory thresholds for hydrocarbons and NOx only appeared after the regulation went into effect. Since our data represent the first tests conducted to completion by the inspectors, these shifts in the discontinuity cannot result from repairs conducted in response to failed tests, but instead likely represent inspector manipulation. One can further observe from the distributions that the magnitude of the manipulation has not been small, since the increased mass in the distribution is at very low emissions levels. This suggests that inspectors are unlikely to be simply warming up vehicles or adjusting the tailpipe probe in order to nudge them to the passing side of the threshold, instead likely employing more severe manipulations such as the clean-piping discussed in Oliva (2012). We estimate and present in Table 2 the significance of these discontinuities for all six emissions measurements both before and after the threshold changes using the following specification: 1  𝐷𝑒𝑛𝑠𝑖𝑡𝑦 = 𝛼 + 𝛽! ∗ 𝑇ℎ𝑟𝑒𝑠ℎ𝑜𝑙𝑑 + 𝜷 ∗ 𝑁 !! 𝐷𝑒𝑔𝑟𝑒𝑒  𝑃𝑜𝑙𝑦𝑛𝑜𝑚𝑖𝑎𝑙  𝑜𝑓  𝑡ℎ𝑒  𝑀𝑒𝑎𝑠𝑢𝑟𝑒 + 𝜀                                                                                                                         14

We show hydrocarbon results because this pollutant had the most substantial change in threshold. While some of this discontinuity could stem from polluting vehicles leaving the state in prior years, the starkness of the discontinuity is striking. A selection argument is extremely doubtful due to the imprecise correlation in tests across years for any given vehicle. Furthermore, we do not observe such a discontinuity at the old threshold persisting after the policy change. This explanation will become even less plausible following our policy change analysis. 15

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For each measurement we construct the probability density function (pdf) for each measurement. Each pdf aggregates all observations into bins of a magnitude described in Table 2. We create a 7th degree polynomial based on the measure being tested. For example, in Figure 2 this would be the four-minute hydrocarbon result. Finally we construct a dummy variable Threshold equal to 1 if the vehicle fails the given measurement and 0 if the vehicle passes. This parameter estimates the size of the magnitude and significance of the discontinuity across all measures for each time period. Our results show that the discontinuity is significant for all the pre-April 1 tests using the old thresholds. More importantly, the discontinuity is significant for the In order to identify this manipulation by emissions inspectors, we implement a research design that exploits the sharp policy shift in the regulatory threshold. Using only those emissions tests within three months of the policy change, we define vehicles according to the six tests dimensions presented in Figures 3-5. The first group is those cars whose emissions results always exceed both the old and new thresholds on either the four-minute or 90-second measurement, for each of the three dimensions.16 These vehicles, which we refer to as never pass, had emissions results great enough to fail the test both before and after the policy shift increased environmental standards. The second group includes those vehicles whose emissions scores were between the old and new pass thresholds. These cars, which we refer to as pre-pass, would pass if tested prior to April 1, but would fail in the period afterward. The third group is composed of those cars whose emissions results were below the newer threshold. These vehicles, which we refer to as always pass, had emissions scores low enough to pass in either regulatory period. Figure 2 presents these three categories for the fourminute hydrocarbon test. The key to our analysis is to identify the probability that a vehicle falls into each of the three categories, or ranges of emissions. If inspectors are not manipulating emissions tests, we would expect the probability for each category to be approximately equal across short periods of time for the first emissions test observed. The number of cars in the always pass category, or below the new threshold, should be approximately equal on any two consecutive days. While the emissions of tested vehicles may gradually decrease across time as vehicles are repaired and replaced, this change should be relatively continuous.

                                                                                                                        16 As we explain earlier, a vehicle passes an emissions test so long as it passes either the four-minute or the 90-second test for each of the three emissions dimensions (HC, NOx, and CO).

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If alternatively, customers or inspectors are manipulating tests in response to the policy change, there should exist a discontinuity between the day before and the day of the policy switch. Inspectors who observe a vehicle falling into the pre-pass range on March 31 will allow the test to run to completion, and legitimately pass the car. Inspectors observing a likely pre-pass result on April 1, however, would stop the test, manipulate the vehicle, and then rerun the test, with the car appearing clean on the official results. In the case of strategic manipulation, we should therefore observe that the number of pre-pass vehicles discretely drops on April 1, while the number of always pass vehicles discontinuously increases. Such a discontinuous change is important for identification due to the possibility of preemptive repair. Since legitimately and permanently repairing vehicles takes time to schedule and complete, particularly when parts need to be ordered, it is an unlikely alternative explanation for such a discrete shock. Problems discovered prior to April 1 that place a car in the pre-pass range would not be repaired, since those cars could simply conduct the test using the old threshold and legitimately pass without repairs. We would likely observe no change, however, to the group of vehicles that never pass, as inspectors would manipulate the tests for these vehicles at similar rates both prior to and after the policy change. We present in Figure 6 the daily frequencies of model-year 1982-1990 vehicles falling within each of the three categories between January 1 and March 31, 2003. The discontinuity in the always pass category is immediately evident. On April 1, 2003, the frequency of vehicles below the new threshold discretely increases. The frequency of vehicles in the pre-pass drops dramatically on April 1, while the frequency for the never pass appears unchanged. In Figure 7 we repeat our frequency plot for each of the three categories, this time using only those tests conducted before 10AM for two weeks before and after the policy change. Vehicles tested in this period on April 1 are unlikely to have been identified as failing and then legitimately repaired in the early morning. In contrast, these vehicles could easily have been manipulated in this time period, using clean-piping or another common technique. Since these cars would have passed on March 31, they are also unlikely to have been tested and pre-emptively repaired in prior days. The discontinuities for always pass and pre-pass are still obvious for these morning tests. The visual results for always pass and pre-pass vehicles in Figures 6 and 7 are consistent with inspectors beginning to manipulate tests for pre-pass vehicles exactly when these cars fall below the regulatory threshold: the first hour of business on April 1, 2003.

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To statistically test for the presence of a jump on April 1, we run linear probability models measuring the likelihood of vehicles appearing in each of the three categories. 2  𝑅𝑒𝑠𝑢𝑙𝑡  𝐶𝑎𝑡𝑒𝑔𝑜𝑟𝑦 = 𝛼 + 𝛽! ∗ 𝐴𝑓𝑡𝑒𝑟  𝐴𝑝𝑟𝑖𝑙  1!"      𝜷 ∗ 𝑁 !! 𝐷𝑒𝑔𝑟𝑒𝑒  𝑃𝑜𝑙𝑦𝑛𝑜𝑚𝑖𝑎𝑙  𝑜𝑓  𝐷𝑎𝑦𝑠  𝑆𝑖𝑛𝑐𝑒  𝐴𝑝𝑟𝑖𝑙  1!" + 𝜷 ∗ 𝐶𝑜𝑛𝑡𝑟𝑜𝑙𝑠 + 𝜀 We use a standard approach, regressing a dummy variable indicating whether the vehicle fell into one the possible results categories on a dummy variable indicating if the test was done after the policy change, and relevant control variables. Our specification includes vehicle odometer cubic, vehicle weight quadratic, and vehicle age quadratic variables as controls, while using either a linear or seventh-degree time function for polynomial smoothing.17 The identification strategy involves demonstrating that the treatment variable causes a discrete increase in the probability of falling into the always pass category and a discrete decrease in the pre-pass category, while controlling for time trends and other potential predictors. We use the sample of model-year 1982-1990 vehicles for this model, since these cars had the largest increase in stringency. We present our results in Table 3. Columns 1 and 2 represent linear probability models predicting the likelihood of falling in the always pass category, with column 2 including seventhdegree polynomial smoothing and control variables. Standard errors are clustered at the facility level. Our results suggest an 8% increase in the likelihood of falling into the always pass category starting April 1, and are robust to the inclusion of control variables. This suggests that vehicles are immediately shifted to below the new regulatory threshold on the day of the policy change. Columns 3 and 4 represent similar linear probability models predicting the likelihood of a vehicle falling into the pre-pass category between the two regulatory thresholds. In each model we observe an 8% drop in the likelihood on the day of the regulatory change. Columns 5 and 6 repeat the linear probability model for the never pass category. These results show no change in this category after the policy change. The results from these regression discontinuity models strongly support the visual evidence in Figures 6 and 7, and are consistent with inspectors manipulating emissions tests on prepass vehicles the moment the new threshold takes effect. Table 4 supplements this analysis by estimating the model using only tests from before 10AM for two weeks days before and after the policy change. Again we find similar results, which effectively rules out preemptive repair. Across all of the results, we find that changes in the specification of the polynomial or other control variables

                                                                                                                        17

We repeat the regressions using polynomial smoothing functions of various degrees with no impact to our results. 13

have little impact on the parameter of interest. This suggests, though not conclusively, that omitted variables bias is not driving these results. One could worry that self-selection might be biasing the magnitude of our results. If drivers who are at risk of failing attempt to take the test before the policy change, our parameter might be incorrectly estimated. Intuitively the amount of information and sophistication the average driver would have to posses to engage in this strategy would be significant. Nevertheless we present evidence that suggests individuals do not rush to get their vehicles tested before the policy changed. If this were the case, we would expect to observe a significant bump in the volume of cars impacted by the new regulations (1982-1990) just prior to April 1 and a significant drop afterwards as cars that were at risk went in for their scheduled inspections earlier. In Figure 8 we present the daily volume of inspections three months prior to and after the April 1 policy change. The figure shows no considerable difference to the left or right of the policy change. The vehicles most affected by the policy change, with model years 1982-1990, show no difference before or after the policy change in volume, relative to newer vehicles. The pattern of inspections for the vehicles made between 1991 and 1995, which had smaller threshold changes, is also similar to the pattern of inspections for the vehicles made after 1995 that were not subject to any change in regulation. Figure 9 uses only vehicles tested before 10AM, and similarly finds no discontinuities in inspection volume. Table 5 presents regression discontinuity models similar to equation 2, only with dummy variables for the three model-year categories as dependent variables. Models with polynomial smoothing in Table 5 show no identifiable discontinuity following the policy change, consistent with our argument that customers are not preemptively testing at risk cars prior to the policy change. We also test for this volume discontinuity using only the early morning test examined in Table 6. Again, we see no large discontinuities at the policy change for any category of model-year. We see smaller, weakly-identified discontinuities for the newer models that received little or no threshold change, but no change in the most strongly impacted older vehicles. Finally, in unreported results we find no economically significant differences in the odometer readings, testing weight, or age of the vehicles being inspected before and after the policy change, consistent with the implication from Table 1.

14

V: Conclusions

In this paper we use a regression discontinuity design to identify the strategic manipulation of emissions tests by licensed private inspectors. Inspectors, as state-licensed experts charged with enforcing environmental regulations, are given discretion to gather and use information in the process of testing for the purpose of ensuring fairness and accuracy of results. Yet this discretion and information allows these experts to manipulate the test by aborting it in process and thereafter making temporary adjustments or substitutions that allow the vehicle to fraudulently pass. This manipulation is motivated by the moral hazard of attracting and retaining repeat repair and service business (Hubbard 2002). The many older cars in our sample provide consistent business for mechanics, who are likely to suffer financially from customers who take there business to more lenient facilities or who choose to replace the vehicle with a newer, more reliable car. We exploit a policy change that lowered the pass threshold based on the vehicle model-year, thereby immediately putting hundreds of thousands of vehicles newly at risk for failure on April 1, 2003. Given the considerable welfare implications of increased mobile emissions (Ashenfelter and Greenstone 2004; Currie and Niedell 2005; Currie et al. 2009a; 2009b; Agarwal et al. 2010; Currie and Walker 2011; Fowlie et al. 2012), the argument for allowing inspectors the discretion to stop tests in process seems tenuous. Although eliminating this discretion seems an obvious remedy to the problem, inspectors motivated by financial gains will likely find other ways to manipulate the system, albeit less precisely as they try to predict which vehicles require pre-test manipulation. And given the low number of facilities detected and penalized by the State (States News Service, 2010), current levels of enforcement seem insufficient to deter manipulation. Our results therefore seem to justify increased investment in the monitoring of private inspection facilities, particularly when the State is implementing increased thresholds that immediately put new cars at risk for failure. Privatizing government regulatory enforcement may yield efficiency gains from competition and customer choice, yet it brings considerable social cost through moral hazard for leniency. The State must give experts discretion in order to exploit their knowledge and expertise, but in doing so must acknowledge the potential for this discretion to be abused toward profit-improving behaviors. This discretion has strong implications for the ability of the State to achieve regulatory goals through strengthening environmental standards, because the private market experts charged with enforcing

15

increased standards may have little incentive to increase stringency, and significant discretion to circumvent the stricter regulations. Privatization in enforcement may therefore yield an additional cost not normally considered in outsourcing decisions---losing the option value of ratcheting up regulatory standards in the future. It is important to note that the test manipulation that we observe could be welfare improving if the threshold were excessively high, such that the welfare benefits of repairing the marginal pre-pass vehicles were less than the costs. We find this to be unlikely in our setting given the welfare calculation from Currie et al. (2009). Their estimates that increased standards in New Jersey saved 449 infant lives worth $2.2 billion annually suggest that the benefits to New York far outweigh the foregone costs of legitimate repairs. Given that our model parameters suggest 8% of the total fleet vehicles are illegitimately passed after the policy change, this welfare benefit could fund a considerable level of repairs for these polluting vehicles. For example, it would fund $1,100 in repairs for two million cars, which would represent 8% of a total fleet of 25 million vehicles (far more than in New Jersey or downstate New York). Given these numbers, it is difficult to believe that manipulating these marginal vehicles could bring a net welfare gain.

16

References Agarwal, Nikhil, Banternghansa, Chanont, and Linda Bui. 2010. “Toxic Exposure in America: Estimating Fetal and Infant Health Outcomes from 14 Years of TRI Reporting.” Journal of Health Economics Vol. 29: pp. 557-574. Ashenfelter, Orley and Michael Greenstone. 2004. “Using Mandated Speed Limits to Measure the Value of a Statistical Life.” Journal of Political Economy Vol. 112: pp. 226-67. Bennett, Victor, Pierce, Lamar, Snyder, Jason, and Michael Toffel. 2012. “Competition and Illicit Quality.” Harvard Business School Working Paper 12-071. Blinder, Alan S. and Harvey S. Rosen. 1985. “Notches.” American Economic Review Vol. 75 (4): pp. 736-747. California Bureau of Automotive Repair. 2011. Final statement of reasons for Article 5.5 of Chapter 1 of Division 33 of Title 16 of the California Code of Regulations. June 10. Chay Ken Y. and Michael Greenstone. 2003. The Impact of Air Pollution on Infant Mortality: Evidence from Geographic Variation in Pollution Shocks Induced by a Recession. Quarterly Journal of Economics Vol. 118: pp. 1121-1167 Collins, Glenn. 2003. “A Week into April, and Wondering Where that Snow Shovel is Stored.” New York Times, April 8: D1. Currie, Janet, Eric A. Hanushek, Megan E. Kahn, Matthew Neidell and Steve G. Rivkin. 2009a. “Does Pollution Increase School Absences?” The Review of Economics and Statistics, Vol. 91: pp. 682–694 Currie, Janet and Matthew Neidell. 2005. “Air Pollution and Infant Health: What Can We Learn from California’s Recent Experience?” Quarterly Journal of Economics Vol. 120: pp. 1003-30. Currie, Janet, Matthew Neidell, and Johannes F. Schmieder. 2009b. ”Air Pollution and Infant Health: Lessons from New Jersey,” Journal of Health Economics, Vol. 28: pp. 688-703 Currie, Janet, and Reed Walker. 2011. “Traffic Congestion and Infant Health: Evidence from EZPass.” American Economic Journal: Applied Economics 3: pp. 65-90. Davidson, Wallace. III, Jiraporn, Pornsit, and Peter DaDalt. 2006. “Causes and Consequences of Audit Shopping: An Analysis of Auditor Opinion, Earnings Management, and Auditor Changes.” Quarterly Journal of Business and Economics 45(1): 69-87. Davis, Lucas W. 2008. “The Effect of Driving Restrictions on Air Quality in Mexico City.” Journal of Political Economy 116: 38-81. Davis, Lucas W. and Matthew E. Kahn. 2010. “International Trade in Used Vehicles: The Environmental Consequences of NAFTA.” American Economic Journal: Economic Policy 2: 58-82. Duggan, Mark and Steven Levitt. 2002. “Winning Isn’t Everything: Corruption in Sumo Wrestling.” American Economic Review 92(5): 1594-1605.

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Ernst, Michelle, James Corless, and Ryan Greene-Roesel. 2003. “Clearing the Air: Public Health Threats from Cars and Heavy Duty Vehicles---Why We Need to Protect Federal Clean Air Laws.” (). Surface Transportation Policy Partnership. Washington, DC. http://www.transact.org/report.asp?id=227. Fowlie, Meredith, Christopher Knittel, and Catherine Wolfram. 2012. “Sacred Cars? Cost-Effective Regulation of Stationary and Non-stationary Pollution Sources.” American Economic Journal: Economic Policy 4: 98-126. Gauderman W, Gilliland, F., Vora, H., Avol, E., Stram, D., McConnell, R. Thomas, D., Lurmann, F., Margolis, H., Rappaport, E., Berhane, K., and Peters, J. 2002. “Association Between Air Pollution and Lung Function Growth in Southern California Children: Results from a Second Cohort.” American Journal of Respiratory and Critical Care Medicine 165. Groark, Virginia. 2002. “An Overhaul for Emissions Testing.” The New York Times, June 9: 4. Hubbard, Thomas N. 1998. “An Empirical Examination of Moral Hazard in the Vehicle Inspection Market.” RAND Journal of Economics 29: 406-426. Hubbard, Thomas N. 2002. “How Do Consumers Motivate Experts? Reputational Incentives in an Auto Repair Market.” Journal of Law and Economics 45: 437-468. Lambert, C. 2000. “Payoffs Alleged as Emissions Tests End.” Palm Beach Post, June 30. Lazare, D. 1980. “Jersey Weighs Its Shift to Private Inspections.” New York Times (October 26) S21. Levitt, Steven and Jack Porter 1999 “How Dangerous Are Drinking Drivers?” Journal of Political Economy 109: 1198-1237 Forbes, Silke, Lederman, Mara, and Trevor Tombe. 2011. “Do Firms Game Quality Ratings? Evidence from Mandatory Disclosure of Airline On-Time Performance.” Unpublished Working Paper. McFadden, Robert D. 2003. “Blizzard Buries Northeastern U.S., Disrupting Travel.” New York Times, Feb. 18: pp. B4. Oliva, Paulina. 2012. “Environmental Regulations and Corruption: Automobile Emissions in Mexico City.” http://www.econ.ucsb.edu/~oliva/Docs/Smog_Checks_Jan2012.pdf Pierce, Lamar, and Jason A. Snyder. 2008. “Ethical Spillovers in Firms: Evidence from Vehicle Emissions Testing.” Management Science 54: 1891-1903. Sallee, James M. and Joel Slemrod. 2010. “Car Notches: Strategic Automaker Responses to Fuel Economy Policy.” NBER Working Paper No. 16604. Snyder, Jason A. 2010. “Gaming the Liver Transplant Market.” Journal of Law, Economics, & Organization 26(3): 546-568. Snyder, Jason A. 2012. “Discontinuous Electoral Distributions” Working Paper.

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States News Service. 2010. “40 Facilities Cited for Falsifying 20,000+ Vehicle Emissions Inspections.” Feb. 18. U.S. Environmental Protection Agency. 2001. Our Built and Natural Environments: A Technical Review of the Interactions between Land Use, Transportation and Environmental Quality, Development Community and Environmental Division. EPA 231-R-01-002, Washington, DC, January, www.epa.gov/piedpage/pdf/built.pdf Utell, Mark J., Jane Warren, and Robert F. Sawyer. 1994. “Public Health Risks from Motor Vehicle Emissions.” Annual Review of Public Health 15: 157-78. Voas, S. P. Shelly. 1995. “Ridge Kills New Emissions Tests.” Pittsburgh Post-Gazette. Oct. 19. Wolfers, Justin. 2006. “Point Shaving: Corruption in NCAA Basketball.” American Economic Review 96(2): 279-283. Zitzewitz, Eric. 2012. “Forensic Economics.” Forthcoming in Journal of Economic Literature.

19

Table 1: Summary Statistics Model-years 1983-1990 Time period: Three months prior to policy change Variable

Time period: Three months after policy change

Observations

Mean

Observations

Mean

Result

94,945

.853

117,857

.791

Always pass

94,945

.708

117,857

.791

Prior pass

94,945

.145

117,857

.059

Never pass

94,945

.147

117,857

.150

Odometer

94,945

114,393

117,857

111,267

Model-year

94,945

1988.128

117,857

1988.097

Model-years 1991-1995 Time period: Three months prior to policy change Variable

Time period: Three months after policy change

Observations

Mean

Observations

Mean

Result

161,115

.919

200,608

.911

Always pass

161,115

.899

200,608

.911

Prior pass

161,115

.020

200,608

.004

Never pass

161,115

.081

200,608

.085

Odometer

161,115

109,557

200,608

105,334

Model-year

161,115

1993.167

200,608

1993.172

Model-years 1996-2002 Time period: Three months prior to policy change Variable

Time period: Three months after policy change

Observations

Mean

Observations

Mean

Result

238,564

.979

307,599

.979

Always pass

238,564

.979

307,599

.979

Prior pass

238,564

0

307,599

0

Never pass

238,564

.021

307,599

.021

Odometer

238,564

58,151

307,599

55,558

Model-year

238,564

1998.701

307,599

1998.731

20

Table 2: Estimated discontinuities for model-years 1982-1990 Measure

Passing threshold

Bin Size

Time Period

Estimated jump at threshold

Number of observations

Four-minute hydrocarbons

1.2 g/mi

.01 g/mi

January 1st March 30th

-.0008 (.0002)***

150

Four-minute hydrocarbons

.8 g/mi

.01 g/mi

April 1st June 30th

-.0013 (.0001)***

150

Ninety-second hydrocarbons

.75 g/mi

.01 g/mi

January 1st March 30th

-.0001 (.0002)

150

Ninety-second hydrocarbons

.5 g/mi

.01 g/mi

April 1st June 30th

-.0019 (.0002)***

150

Four-minute nitrous oxide

2.5 g/mi

.02 g/mi

January 1st March 30th

-.0006 (.0001)***

147

Four-minute nitrous oxide

2.0 g/mi

.02 g/mi

April 1st June 30th

-.0010 (.0001)***

147

Ninety-second nitrous oxide

2.5 g/mi

.02 g/mi

January 1st March 30th

-.0005 (.0001)***

147

Ninety-second nitrous oxide

2.0 g/mi

.02 g/mi

April 1st June 30th

-.0005 (.0001)***

147

Four-minute carbon monoxide

15 g/mi

.15 g/mi

January 1st March 30th

-.0006 (.0002)***

148

Four-minute carbon monoxide

15 g/mi

.15 g/mi

April 1st June 30th

.0001 (.0002)

148

Ninety-second carbon monoxide

12 g/mi

.15 g/mi

January 1st March 30th

-.0004 (.0001)***

146

Ninety-second carbon monoxide

12 g/mi

.15 g/mi

April 1st June 30th

-.0002 (.0001)

146

Note: *, **, *** indicate significance at the 10%, 5%, and 1% confidence levels, respectively. Parentheses contain standard errors. All discontinuities estimated using a 7th degree confidence interval. Slight differences in observations are a function of different bin sizes which were chosen to make the result approximately comparable. The abbreviation g/mi stands for grams per mile.

21

Table 3: Test results three months before and after the policy change for model-years 1982-1990 Dependent variable: Always pass

Dependent variable: Pre-pass

(1) .084 (.003)***

(2) .086 (.007)***

(3) -.086 (.005)***

(4) -.080 (.005)***

(5) .002 (.002)

(6) -.006 (.006)

7th Degree polynomial for days since policy change

No

Yes

No

Yes

No

Yes

Cubic odometer controls

No

Yes

No

Yes

No

Yes

Cubic vehicle age controls

No

Yes

No

Yes

No

Yes

212,802

212,802

212,802

212,802

212,802

212,802

3,711

3,711

3,711

3,711

3,711

3,711

Independent variables Post policy change

Observations Clusters

Dependent variable: Never pass

Note: *, **, *** indicate significance at the 10%, 5%, and 1% confidence levels, respectively. Parentheses contain standard errors clustered at the facility level. Saturday and Sunday are jointly coded as one business day. The results are robust to this choice.

Table 4: Test results for inspections before 10:00 am two weeks before and after the policy change for model-years 1982-1990 Dependent variable: Always pass

Dependent variable: Pre-pass

Dependent variable: Never pass

(1) .089 (.009)***

(2) .102 (.034)***

(3) -.075 (.006)***

(4) -.051 (.023)**

(5) -.013 (.007)*

(6) -.051 (.027)*

7th Degree polynomial for days since policy change

No

Yes

No

Yes

No

Yes

Cubic odometer controls

No

Yes

No

Yes

No

Yes

Cubic vehicle age controls

No

Yes

No

Yes

No

Yes

Observations

10,189

10,189

10,189

10,189

10,189

10,189

Clusters

2,799

2,799

2,799

2,799

2,799

2,799

Independent variables Post policy change

Note: *, **, *** indicate significance at the 10%, 5%, and 1% confidence levels, respectively. Parentheses contain standard errors clustered at the facility level. Saturday and Sunday are jointly coded as one business day. The results are robust to this choice.

22

Table 5: Predicting the percentage of cars tested each day based on level of exposure to a more stringent policy Model-year: 1982-1990 Independent variables Post policy change 7th Degree polynomial for days since policy change Observations Clusters

Model-year: 1991-1995

Model-year: 1996-2002

(1) -.004 (.001)***

(2) -.003 (.003)

(3) -.005 (.001)***

(4) -.002 (.003)

(5) .009 (.001)***

(6) .005 (.004)

No

Yes

No

Yes

No

Yes

1,120,688 1,120,688 3,837

3,837

1,120,688 1,120,688 3,837

3,837

1,120,688 1,120,688 3,837

3,837

Note: *, **, *** indicate significance at the 10%, 5%, and 1% confidence levels, respectively. Parentheses contain standard errors clustered at the facility level. Saturday and Sunday are jointly coded as one business day. The results are robust to this choice. Window is three months before and after the policy change.

Table 6: Predicting the percentage of cars tested each day before 10:00 am based on level of exposure to a more stringent policy Model-year: 1982-1990 Independent variables

Model-year: 1991-1995

Model-year: 1996-2002

(1) .003 (.003)

(2) -002 (.012)

(3) .000 (.004)

(4) -.027 (.014)**

(5) -.003 (.004)

(6) .027 (.016)*

No

Yes

No

Yes

No

Yes

Observations

58,774

58,774

58,774

58,774

58,774

58,774

Clusters

3,503

3,503

3,503

3,503

3,503

3,503

Post policy change 7th Degree polynomial for days since policy change

Note: *, **, *** indicate significance at the 10%, 5%, and 1% confidence levels, respectively. Parentheses contain standard errors clustered at the facility level. Saturday and Sunday are jointly coded as one business day. The results are robust to this choice. Window is two weeks before and after the policy change.

23

Figure 1: Passing an emissions inspection

Pass four-minute or ninetysecond hydrocarbons test

and

Pass four-minute or ninetyPass four-minute or ninetyand second nitrous oxide test second carbon monoxide test

Pass Test

.015

Figure 2: The distribution of four-minute hydrocarbons tests for model-years 1982-1990 Pre Pass: Only Pass before policy change

Never Pass: Fail before and after policy change

Percentage of cars .005 .01

Always Pass: Pass before and after policy change

Old threshold

0

New threshold

0

.5 1 Four−minute hydrocarbons test result

1.5

24

.02

Figure 3a: Impact of policy change on distribution of four-minute hydrocarbons tests for model-years 1982-1990

Percentage of cars .01 .015

Distribution after policy change New threshold

Old threshold

0

.005

Distribution prior to policy change

0

.5 1 Four−minute hydrocarbons test result

1.5

.025

Figure 3b: Impact of the policy change on the distribution on the ninty second hydrocarbons tests for model-years 1982-1990

.02

Distribution after policy change

Percentage of cars .01 .015

New threshold

Old threshold

0

.005

Distribution prior to policy change

0

.5 1 Final ninety−second hydrocarbons test result

1.5

25

.015

Figure 4a: Impact of policy change on distribution of four-minute nitrogen oxide tests for model-years 1982-1990

Percentage of cars .005 .01

New threshold

Old threshold

Distribution after policy change

0

Distribution prior to policy change

0

1 2 Four−minute nitrogen oxide test result

3

.025

Figure 4b: Impact of policy change on distribution of ninety-second nitrogen oxide tests for model-years 1982-1990

Old threshold

Distribution after policy change

Distribution prior to policy change

0

.005

Percentage of cars .01 .015

.02

New threshold

0

1 2 Final ninety−second nitrogen oxide test result

3

26

.05

Figure 5a: Impact of policy change on distribution of four-minute carbon monoxide tests for model-years 1982-1990

Percentage of cars .02 .03

.04

New threshold & old threshold

Distribution after policy change

0

.01

Distribution prior to policy change

0

5

10 15 Four−minute carbon monoxide test result

20

25

.08

Figure 5b: Impact of policy change on distribution of ninety-second carbon monoxide tests for model-years 1982-1990

Percentage of cars .04 .06

New threshold & old threshold

Distribution after policy change

0

.02

Distribution prior to policy change

0

5

10 15 20 Final ninety−second carbon monoxide test result

25

27

Percentage of cars in each category .2 .4 .6 .8

Figure 6: Daily distribution of test result groups for model-years 1982-1990

Percentage of vehicles that would always pass inspection Policy change date: April 1, 2003

Percentage of vehicles that would never pass inspection

0

Percentage of vehicles that would only pass before the policy change

−75

−50

−25 0 25 Bussiness days since policy change

50

75

Percentage of cars by model−year group .2 .4 .6 .8

Figure 7: Daily distribution of test result groups for model-years 1982-1990 tested before 10:00 am

Percentage of vehicles that would always pass inspection Policy change date: April 1, 2003 Percentage of vehicles that would never pass inspection

0

Percentage of vehicles that would only pass before the policy change

−12

−10

−8

−6

−4 −2 0 2 4 Business days since policy change

6

8

10

28

Figure 8: Daily percentage of vehicles from each model-year group Percentage of cars by model−year group .2 .3 .4 .5

.6

Model-years 1996-2002 threshold did not change

Model-years 1991-1995 recieved small threshold decrease

Model-years 1982-1990 received large threshold increase

.1

Policy change date: April 1, 2003

−75

−50

−25 0 25 Business days since policy change

50

75

Percentage of cars in each category .3 .4 .5

.6

Figure 9: Daily percentage of vehicles from each model-year group tested before 10:00 am

Model-years 1991-1995 recieved small threshold decrease

.2

Policy change date: April 1, 2003

−12

−10

−8

−6

Model-years 1996-2002 threshold did not change

Model-years 1982-1990 received large threshold increase

−4 −2 0 2 4 Business days since policy change

6

8

10

29