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DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR?

CHENG CHENG∗

In response to concerns that distracted driving due to cell phone use has become a threat to roadway safety, many states have passed laws that prohibit drivers from texting and talking on handheld cell phones. In light of recent evidence that these bans do not reduce traffic accidents, this article asks whether this is because the laws are ineffective in reducing usage. Using data on observed driver cell phone usage combined with a difference-in-differences approach that exploits the within-state variation in the adoption of bans, I find that prohibiting drivers from texting and talking on handheld cell phones reduces each by 60% and 50%, respectively. This suggests the policy is effective at reducing the targeted behavior, which leads me to discuss other factors and behavioral responses that may counteract the reduction in observed usage (JEL K32, D04, R41).

I. INTRODUCTION

In recent years, there has been increasing con- cern over distracted driving due to cell phone use. This stems from the substantial recent increase in cell phone usage while driving, as well as a body of research and official statistics suggesting that this behavior may lead to distraction and traffic accidents. One survey reports that over 60% of drivers regularly send text messages while driv- ing, and that 66% of drivers report answering calls while driving (Tison, Chaudhary, and Cos- grove 2011). A growing body of research includ- ing naturalistic studies and studies of simulated driving tasks provides evidence that cell phone usage does affect driver behavior by, for example, slowing drivers’ reaction time or taking drivers’ eyes away from the roadway more often (Hosk- ing, Young, and Regan 2009; Just, Keller, and Cynkar 2008; Olson et al. 2009). While it is dif- ficult to know for sure whether and how much driver cell phone use increases accidents and casualties, official estimates from the National

∗I thank Mark Hoekstra, Jason Lindo, Christopher Car- penter, Wesley Wilson, Scott Adams, Daniel Hamermesh, Jonathan Meer, Jeremy West, seminar participants at Texas A&M University, University of Mississippi, University of North Carolina at Charlotte, the 2013 Annual Meeting of the Southern Economic Association, and two anonymous referees for helpful comments and suggestions. I also thank Timothy Pickrell of the National Highway Traffic Safety Administra- tion for providing data of the National Occupant Protection Use Survey. Any errors are my own. Cheng: Department of Economics, The University of

Mississippi, University, MS 38677. E-mail cheng@ olemiss.edu.

Highway Traffic Safety Administration (2009) are that 995 people lost their lives in motor vehi- cle crashes in the United States in 2009 due to the use of cell phones while driving.

In response, states have started to pass cell phone bans — texting bans and handheld bans — that prohibit drivers from using cell phones behind the wheel. Texting bans prohibit drivers from sending or reading text messages on cell phones; handheld bans prohibit all drivers from engaging in phone calls, either talking or listening, on handheld cell phones when operating motor vehicles. These bans impose significant penalties for violations, including fines (ranging from $20 to $500 in adopting states), license suspension, and even jail time. Therefore, by raising the expected cost of using cell phones while driving, one might expect the bans to reduce traffic accidents by reducing drivers’ cell phone use.

Most of the existing literature consists of single-state studies that examine the impact

ABBREVIATIONS

DD: Difference-in-Differences FARS: Fatality Analysis Reporting System IIHS: Insurance Institute for Highway Safety NHTSA: National Highway Traffic Safety Administra- tion NOPUS: National Occupant Protection Use Survey UCR: Federal Bureau of Investigation’s Uniform Crime Reports VMT: Vehicle Miles Travelled WLS: Weighted Least Squares

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Economic Inquiry (ISSN 0095-2583) Vol. 53, No. 3, July 2015, 1420 – 1436

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1421

of cell phone bans in early adopting states. Handheld bans have been shown to induce drivers to use cell phones less often in Connecti- cut (Cosgrove, Chaudhary, and Roberts 2010), New York (McCartt, Braver, and Geary 2003; McCartt and Geary 2004), and Washington, DC (McCartt and Hellinga 2007; McCartt, Hellinga, and Geary 2006). In addition, several studies find evidence that cell phone bans reduce accidents in New York ( Jacobson et al. 2012; Nikolaev et al. 2010; Sampaio 2010). Two studies from the Highway Loss Data Institute (2009, 2010) evaluate the ban effects on collision claim fre- quencies: the 2009 study finds handheld bans increase collision claim frequencies in Connecti- cut and New York but not in California and the District of Columbia; the 2010 report finds that texting bans increase collision claim frequencies in California, Louisiana, and Minnesota, but not in Washington.

However, a lingering concern with single-state studies is the reliability of statistical inference. First, while cluster-robust standard errors are reliable when the number of clusters is large, they are not when there are only a few clusters (Cameron, Gelbach, and Miller 2008), which applies to single-state studies that typically use a few neighboring states as control groups.1 Sec- ondly, some single-state studies do not cluster standard errors at the recommended (higher) state level to account for possible within-state cross-county correlation when using county- level data, as suggested by Cameron and Miller (forthcoming). Moreover, some other studies do not cluster to account for within-state correla- tion at all (Bertrand, Duflo, and Mullainathan 2004), which has been pointed out by Abouk and Adams (2013).

By adopting a multistate design and address- ing the inference concerns that single-state stud- ies have, recent studies published in economic journals show that cell phone bans have no meaningful effect on traffic accidents.2 Abouk and Adams (2013) focus on the effect of tex- ting bans on single-vehicle-single-occupant acci- dents. They use monthly data from 2007 to

1. This issue does not apply to Burger, Kaffine, and Yu (2013), who use a regression discontinuity design and find California’s handheld ban does not reduce accidents.

2. In contrast, a recent working paper by Rocco and Sam- paio (2012) finds that cell phone bans do reduce fatalities. That study focuses on the 1991 – 2009 period and uses a dif- ferent set of control states by excluding 18 states where local jurisdictions have enacted bans regarding cell phone use while driving. Kolko (2009) finds evidence that hands-free laws reduce traffic fatalities in bad weather or wet road conditions.

2010 and find that accidents are reduced only within a few months after the adoption of tex- ting bans and then return to former levels. Bhar- gava and Pathania (2013) examine handheld bans instead. By analyzing data from 1989 to 2007, they show that banning drivers from talking on cell phones while driving has no effect on fatal crashes.3

These studies raise a question as to why cell phone bans do not reduce traffic acci- dents in general. Is it because cell phone bans are not effective at reducing driver cell phone usage? If so, it suggests that better policies or enforcement could still affect driver behavior in a meaningful way and thus subsequently reduce traffic accidents. However, if the bans do reduce observed driver cell phone usage significantly — which is the best outcome one could hope for given these bans — it suggests that other factors or driver responses may be respon- sible for the overall ineffectiveness of the bans in reducing accidents.

To my knowledge, this study is the first multi- state study that addresses the question of whether cell phone bans affect driver behavior.4 To do so, I apply a difference-in-differences (DD) strategy to two panel datasets from 2004 to 2010: individual- level observational survey data on drivers’ vis- ible cell phone usage from the National Occu- pant Protection Use Survey (NOPUS), and state- level data on fatal traffic accidents and casual- ties from the Fatality Analysis Reporting System (FARS). Specifically, I exploit the within-state variation in the adoption of texting and handheld bans among the 23 adopting states; effective dates of these bans can be found in Table 1. Intuitively, I compare the relative changes in outcome mea- sures, including drivers’ visible cell phone usage (handheld device manipulation and handheld cell phone usage), traffic accidents, and traffic casu- alties, between states that passed cell phone bans (treatment states) and states that did not (con- trol states), from before and after the adoption of cell phone bans. The identifying assumption is that states where drivers are prohibited from

3. In their main analysis, Bhargava and Pathania (2013) cleverly exploit the discontinuity in cellular plans that transit from “peak” to “off-peak” pricing at 9 p.m. on weekdays from 2002 to 2005 in California. They find that although the call likelihood increases by 7.2% during 9 – 10 p.m. from Mondays to Thursdays, this sharp local rise in call likelihood does not lead to more crashes.

4. Broadly, there is also a larger literature focused on evaluating the impact of mandatory state laws on improving roadway safety (e.g., Carpenter and Stehr 2011; Cohen and Einav 2003).

1422 ECONOMIC INQUIRY

TABLE 1 State Texting and Handheld Bans with Primary

Enforcement as of 2010

Effective Date

State Texting

Ban Handheld

Ban

Arkansas 10/01/2009 California 01/01/2009 07/01/2008 Colorado 12/01/2009 Connecticut 10/01/2010 10/01/2005 Georgia 07/01/2010 Illinois 01/01/2010 Louisiana 07/01/2008 Maryland 10/01/2009 Massachusetts 09/30/2010 Michigan 07/01/2010 Minnesota 08/01/2008 New Hampshire 01/01/2010 New Jersey 03/01/2008 03/01/2008* New York 11/01/2001 North Carolina 12/01/2009 Oregon 01/01/2010 01/01/2010 Rhode Island 11/10/2009 Tennessee 07/01/2009 Utah 05/12/2009 Vermont 06/01/2010 Washington 06/10/2010* 07/01/2008 Wisconsin 12/01/2010 Wyoming 07/01/2010

Note: *States that have upgraded the enforcement type from secondary to primary.

using cell phones would have followed simi- lar trajectories in cell phone usage, accidents, and casualties to other nonadopting states, in the absence of the adoption of cell phone bans. To assess the validity of this assumption, I show that outcomes do not diverge between adopting and nonadopting states prior to the adoption of cell phone bans using graphical and regression anal- ysis. In addition, I also find evidence that the adoption of cell phone bans is as-good-as-random by showing that DD estimates are robust to the inclusion of time-varying covariates that are used in previous studies, such as unemployment rate, median income, violent and property crime rates, and demographics (Abouk and Adams 2013; Carpenter and Stehr 2011; Cohen and Einav 2003).

Results provide strong evidence that drivers reduce visible cell phone use when cell phone bans increase the expected cost of doing so. Specifically, cell phone bans significantly lower a driver’s probability of talking and texting on a handheld cell phone while driving by 50% and 60%, respectively. These results are robust to

various robustness checks such as allowing for region-year or region-year-quarter fixed effects to account for common regional shocks, including state-specific linear time trends to impose more flexible assumptions on unobservables, and using different definitions of cell phone bans. In addi- tion, the results are robust to including controls for characteristics of individual drivers and sur- vey observational sites. There is also no evi- dence that the bans affect seat belt usage, which suggests it is unlikely the results are driven by other concurrent policies aimed at improving driver safety.

While I find cell phone bans significantly reduce drivers’ cell phone use, results show these bans do not reduce traffic accidents and casual- ties, which is consistent with Abouk and Adams (2013) and Bhargava and Pathania (2013). In addition, I am able to show that there is no reduction in traffic accidents even among the groups of drivers who reduce their cell phone use the most in response to the laws. One poten- tial explanation for this seemingly contradictory finding is that the bans may cause more hidden cell phone use, which is likely more dangerous and could lead to an increase in accidents and casualties that offsets any reductions elsewhere. It is also possible that the use of cell phones does not necessarily result in more accidents and casualties because drivers compensate for this distracted driving behavior by simply driving more carefully.5

These findings have significant welfare and policy implications. While current bans do alter driver behavior as intended — indeed, as police cannot observe hidden usage, the best the law can do is to reduce observed usage — they do not have the intended effect on accidents and casu- alties. This suggests that these cell phone bans impose significant costs on drivers by distorting driver behavior, without generating measurable safety benefits to either those drivers or other drivers on the road. More importantly, the find- ings provide evidence that the ineffectiveness of the bans in reducing accidents is not merely a matter of enforcement. Rather, it suggests that a more complex set of factors is at play and needs to be sorted out if policymakers are to suc- ceed in reducing accidents and fatalities due to distracted driving.

5. It is also possible that drivers switch to hands-free use as a result of the bans, which may be similarly distracting. I find little evidence of this, though I note that it is more difficult for the surveyors to observe hands-free usage.

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1423

II. DATA

A. Texting and Handheld Bans

In this study, cell phone bans refer to texting and handheld bans that apply to all drivers in all locations.6,7 Also, I focus on texting and hand- held bans with primary enforcement and do not consider cell phone bans with secondary enforce- ment in the main analysis.8 Primary enforcement in the context of cell phone bans means that law enforcement officials can stop drivers who are observed violating cell phone bans by either making phone calls or texting while driving, without having other primary reasons such as running a red light or speeding. In contrast, under secondary enforcement drivers can only be pulled over for a primary offense first.9 Therefore, ex ante it makes sense to focus on the primary cell phone bans that substantially increase the cost of using cell phones while driving due to the strong enforcement. In fact, most adopting states adopted primary cell phone bans. Up to 2010, only Nebraska, New York, and Virginia adopted secondary texting bans; Maryland is the only state that has a secondary handheld ban. During the examination period, two states also updated the enforcement level of their cell phone bans from secondary to primary: New Jersey upgraded its secondary handheld ban in 2008 and Washing- ton upgraded its secondary texting ban in 2010.

To determine if and when a state passed either a texting ban or a handheld ban between 2004

6. Due to their limited coverage, other cell phone bans that are only applicable to specific drivers and locations are not considered to be handheld or texting bans discussed in this study. Some state bans only target inexperienced drivers who are either below the statutory age (usually 18 years old) or provisional license holders. For example, Missouri has a texting ban that only applies to drivers who are 21 years old and younger; Kansas’s handheld ban is only applicable to learner’s permit and intermediate license holders. In some other states, the bans are only effective in specific areas. Illinois, for instance, restricts all drivers from talking on handheld devices in construction and school speed zones. Also, several states prohibit bus drivers from texting when a passenger of 17 years old or younger is present, such as Texas.

7. Both bans do allow for the possibility of using cell phones for interactive communications in emergencies. Also, persons who perform their official duties such as certified law enforcement officers, firefighters, and ambulance drivers are exempt from the requirement of the cell phone bans.

8. I also look at the effect when including secondary cell phone bans. Results are not statistically different from those reported in Section IV.

9. For example, in a state where the cell phone ban has secondary enforcement and seat belt law has primary enforcement, a driver could be pulled over for not wearing a seat belt and then get citations for not wearing a seat belt and using a cell phone. But the driver cannot be stopped for just using a cell phone without any other primary offense.

and 2010, I found the text of the actual laws or bills and then cross-checked with other sources such as Abouk and Adams (2013), Bhargava and Pathania (2013), National Conference of State Legislatures (NCSL), the Insurance Insti- tute for Highway Safety (IIHS), and Ibrahim et al. (2011).10 Table 1 lists the 23 states that have passed primary cell phone bans as of 2010 along with the corresponding effective dates.11

New York was the first state to pass a hand- held ban in 2001 and New Jersey became the first to pass a texting ban in 2008.12 For the five states that passed both cell phone bans, all of them adopted handheld bans no later than they adopted texting bans. Therefore, it is difficult to distinguish between the effect of handheld bans on their own and the effect of handheld bans when texting bans are already in effect, which is important when interpreting the estimated effect of handheld bans.

Figure 1 shows the geographic distribution of texting bans and handheld bans as of 2010: the 22 states with texting bans appear to be equally distributed across the United States, and the six states with handheld bans are only located in the northeastern and western regions.

B. Outcome Measures

Empirical analysis in this article relies on the outcome measures of state cell phone bans. To construct these variables, I use data from two dis- tinct datasets; descriptive statistics can be found in Table 2.

The first set of outcome measures is the observed cell phone usage while driving by individual drivers, which essentially provides the first-stage evidence on the mechanism through which cell phone bans may affect accidents and casualties. The observed handheld cell phone

10. I thank Abouk and Adams (2013) for helpful conver- sations that corrected the coding of cell phone bans in some states in the earlier version of this article.

11. The effective dates are the dates when the full enforcement begins rather than the initial announcement dates. The reason to choose the effective dates based on whether the enforcement starts is consistent with the purpose of this paper: to evaluate if drivers respond to the incentive change in using cell phones while driving, which only makes sense when there is full enforcement of cell phone bans. For example, Georgia’s texting ban was supposed to become effective on July 1, 2010, but due to the ticketing issue the full enforcement began one month later.

12. The District of Columbia passed both its texting ban and handheld ban on July 1, 2004. However, it is excluded from this analysis due to missing data. Also, Washington was the first state to pass a texting ban with secondary enforcement on January 1, 2008.

1424 ECONOMIC INQUIRY

FIGURE 1 State Texting and Handheld Bans with Primary Enforcement as of 2010

usage contains two main categories. The first category is “handheld cell phone usage,” which refers to the situation in which drivers hold cell phones to their ears while driving. The sec- ond is “visible handheld device manipulation.” In this scenario, drivers are observed visibly text-messaging or manipulating other hand-held device while driving. The raw data come from the 2004 – 2010 National Occupant Protection Use Survey (NOPUS) and are kindly provided by the National Highway Traffic Safety Administration (NHTSA) for this project.13 NOPUS is the only nationwide probability-based observational sur- vey of driver electronic device use in the United States. Unlike usual surveys that are performed through interviews or questionnaires, NOPUS is based on the observations of data collectors and is conducted at intersections controlled by stop signs or stoplights between 7 a.m. and 6 p.m. at different state observational sites each June.14

13. NHTSA publishes the national estimates of drivers’ electronic device use annually.

14. One concern about NOPUS is that driver behav- ior is only observed at traffic-controlled intersections and could be different at other locations. I address this concern in Section IV.C by looking at whether cell phone bans have dif- ferential effects on accidents in different locations, including at intersections.

Observers collect information on multiple char- acteristics of drivers and observational sites, such as age range and weather condition. The survey covers around 30 states each year, although the composition of states covered varies slightly over time.15 This dataset also includes data on individual use of headsets and seat belts, which can be used as further tests.

The second set of outcomes is the number of roadway accidents and casualties. They are aggregated to the state and quarterly levels using data from the FARS. FARS is a nationwide cen- sus provided by NHTSA, containing information on fatal accidents and casualties at the individual, vehicle, and the crash levels. Formally, accidents are measured as the number of motor vehicles involved in fatal crashes; casualties are defined to be the sum of corresponding “incapacitating injuries” and “fatalities.”16 In addition, accidents and casualties are normalized using vehicle miles travelled (VMT); VMT data are from the Federal Highway Administration (1975 – 2010).

15. On average, 80% of the treatment states with hand- held bans and 60% of the treatment states with texting bans are included each year.

16. I exclude other unknown or minor injuries such as “possible injuries” and “nonincapacitating evident injuries.”

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1425

TABLE 2 Descriptive Statistics

Variable Mean Observations

Panel A Accident rate (per 100 million VMT) 2.01 (0.60) 1400 Casualty rate (per 100 million VMT) 1.81 (0.64) 1400 Fatality rate (per 100 million VMT) 1.39 (0.44) 1400 Injury rate (per 100 million VMT) 0.42 (0.25) 1400 Accidents 294 (313) 1400 Casualties 252 (255) 1400 Accident rate by drivers with at least one passenger 0.81 (0.28) 1400 Accident rate by drivers without any passenger 1.21 (0.36) 1400 Accident rate by young drivers 0.42 (0.15) 1400 Accident rate by adult drivers 1.41 (0.44) 1400 Handheld device manipulation 0.0062 (0.08) 331,883 Handheld cell phone usage 0.0541 (0.23) 331,883 Headset usage 0.0066 (0.08) 331,883 Seat belt usage 0.84 (0.37) 331,883 VMT (millions) 14,741 (15,136) 1400

Panel B Texting ban 0.08 (0.26) 1400 Handheld ban 0.06 (0.24) 1400 Unemployment rate (%) 5.88 (2.28) 1400 Median income ($) 228,613 (268,641) 1400 Primary seat belt law 0.50 (0.50) 1400 Population 6,013,147 (6,608,285) 350 Police 19,916 (23,805) 350 Government spending on highway 2,332,007 (2,309,445) 350 Government spending on public welfare 8,428,193 (10,800,000) 350 Male aged 15 – 24 (%) 7.23 (0.54) 350 Male aged 25 – 44 (%) 13.66 (0.79) 350 Violent crime rate 400 (169) 350 Property crime rate 3164 (745) 350 Age 45 (12) 331,883 White 0.79 (0.41) 331,883 Black 0.11 (0.31) 331,883 Male 0.58 (0.49) 331,883 Weekend 0.23 (0.42) 331,883 Weekday nonrush hour 0.43 (0.49) 331,883 Urban area 0.20 (0.40) 331,883 Rural area 0.21 (0.41) 331,883 Clear weather 0.90 (0.31) 331,883

Notes: Each cell contains the mean with the standard deviation in parentheses. Quarterly state-level variables have 1400 observations and annual state-level variables have 350 observations. Variables from the individual observational survey have 331,883 observations.

It is important to note that over the time period beginning around 2000 during which cell phones became more popular, traffic accidents and casualties declined steeply. I show this decline in Figure S1 (Supporting Information), which shows that the casualty rate fell by around 25% between 2004 and 2010, while handheld device manipulation increased from nearly 0% to around 1%. While this provides some evidence against the idea that increased driver cell phone usage results in more accidents and casualties, it also highlights the importance of using a research design that can disentangle the impact of the driver bans from other determinants of accidents and casualties that were clearly changing over

this time period. That research design is described in Section III.

C. Time-Varying Control Variables

I have also obtained data on determinants of the outcome measures to serve as controls. To estimate the effect of cell phone bans on cell phone usage, I utilize the NOPUS data which contain characteristics of individual drivers (median age group, race, and gender) and obser- vational sites (whether the observation time is weekend or weekday rush hour, whether the site is urban or rural, and whether the weather is clear or not). To gauge the effect of cell phone

1426 ECONOMIC INQUIRY

bans on accidents and casualties, I have also collected quarterly and annual data on a set of control variables. Quarterly variables include unemployment rate, median income, and primary seat belt law, with data collected from the Bureau of Labor Statistics, the U.S. Census Bureau, and the IIHS, respectively. Annual population and demographic (proportion of male in the 15 – 24 and 25 – 44 age groups) data are also obtained from the U.S. Census Bureau; annual violent crime and property crime data are from the Fed- eral Bureau of Investigation’s Uniform Crime Reports (UCR). Importantly, I also include the number of full-time equivalent police from UCR to capture the effect of the enforcement of cell phone bans. In addition, I obtain data on government spending on highway infrastructure and public welfare (the U.S. Census Bureau) to distinguish the effect of cell phone bans from the effect of other policies that could have been implemented simultaneously.

D. Sample Period

The sample period used in this study is the 2004 – 2010 period. I choose the year 2004 as the starting point because the quarterly state- level VMT data are only available starting from 2004, which are used to normalize the count of accidents and casualties.17

III. IDENTIFICATION STRATEGY

I apply the DD strategy to estimate the effect of state cell phone bans enacted between 2004 and 2010. Intuitively, I ask whether drivers in states that enact cell phone bans use cell phones less frequently and are involved in fewer acci- dents over time, relative to drivers in other states.

The annual state-level panel data model based on the individual observational survey of driver behavior is:

Outcomeisy = β0 + β1Texting Bansy(1)

+ β2Handheld Bansy + Xisyγ

+ cs + uy + εisy,

where i indexes individuals, s indexes states, and y indexes years. The dependent variable Outcomeisy is the dummy variable that equals 1 if the individual driver is observed using or

17. The 2004 data on “visible handheld device manipu- lation” are not available.

manipulating a cell phone and otherwise equals 0. Texting Bansy is an indicator variable that equals one if the texting ban is effective in state s in year y.18 Handheld Bansy is similarly defined. Individual-level control variables in Xisy include observed race and median age, as well as a set of indicators that correspond to weekday non- rush hour, weekend, rural and urban areas, and weather condition. cs and uy are state- and year- fixed effects, respectively. εisy is the idiosyn- cratic term. The parameters of interest are β1 and β2, which measure the average effect of texting and handheld bans, respectively. Due to potential error correlations within states, standard errors are clustered at the state level.

The quarterly state-level panel data model of accidents and casualties is:

Outcomesyq = β0 + β1Texting Bansyq(2)

+ β2 Handheld Bansyq + Xsyqγ

+ Πsyλ + cs + uyq + εsyq,

where q indexes quarters. Outcomesyq is the nat- ural log of accident/casualty rate (count per 100 million VMT). Formally, accident is defined as the number of vehicles involved in collisions, and casualty is defined as the sum of incapac- itating injuries and fatalities in accidents. Tex- ting Bansyq is an indicator variable that equals one if the texting ban is effective in state s in quarter q of year y. Handheld Bansyq is simi- larly defined. Xsyq is a vector of quarterly time- varying covariates, including unemployment rate and median income. Πsy is a vector of annual time-varying covariates, containing demograph- ics, primary seat belt law dummy, violent and property crime rates, government spending on highway and public welfare, police and popula- tion. uyq is year-quarter fixed effects. εsyq is the idiosyncratic term. Similar to Model (1), β1 and β2 capture the average effects of cell phone bans on accidents and casualties.

The crucial identifying assumption for the DD strategy used here is that states that adopt cell phone bans and other nonadopting states would have trended similarly in outcomes, including cell phone usage, accidents, and casualties, in the absence of the adoption of cell phone bans. Therefore, if this assumption holds, differences in things like the rate of accidents between adopting and nonadopting states do not pose a threat

18. As the survey is conducted in June each year, in the year when the texting ban is adopted, Texting Ban equals 1 if the texting ban is adopted before June and equals 0 otherwise.

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1427

to identification.19 To provide evidence of the validity of this identifying assumption, I per- form several tests. The first is to examine if there is any graphical evidence of divergence in out- comes before the adoption of cell phone bans, as well as formally test for divergence in the regression analysis by including leading indi- cators of both cell phone ban indicators. The second is to compare estimates of Texting Ban and Handheld Ban with and without control- ling for time-varying covariates. If these two sets of estimates differ significantly, it provides evidence that the time-varying determinants of outcomes varied systematically over time across treatment and control groups, which casts doubt on the identifying assumption. More specifically, this would cause me to worry that unobserved time-varying determinants, variables that I can- not directly control for, could vary in a similar way and potentially bias the DD estimates. In addition, to ensure that regional common shocks do not drive the results, I include region-year or region-year-quarter fixed effects, and there- fore identify effects by comparing changes in out- comes between states that adopt cell phone bans and other nonadopting states within the same Census region of the country.

Finally, I perform two more tests to provide more evidence that the estimated effects of cell phone bans are not confounded with other fac- tors. First, I show that VMT is not affected by cell phone bans, providing evidence that cell phone bans indeed do not affect the overall level of driv- ing. This suggests that any change in accidents and casualties will not be caused by changes in traffic congestion. Second, I show that cell phone bans have no effect on drivers’ safe-driving behavior, measured by use of safety seat belts, which suggests that the estimated effects of cell phone bans are not likely to be confounded by the effects of other concurrent policies that aimed at improving driving safety.

IV. RESULTS

A. Do Cell Phone Bans Reduce Drivers’ Cell Phone Usage?

In this section, I examine whether cell phone bans make drivers use cell phones less often.

19. In addition, the policy evaluation literature (e.g., Friedberg, 1998) has argued that even though initial levels of outcomes of interest might be correlated with whether a state adopts a law, they are not correlated with when the law is adopted.

Regression results using the NOPUS data from Model (1) are reported in Table 3. Panel A presents the effects of cell phone bans on the behavior of handheld cell phone usage while driv- ing. In column 1, in which state- and year-fixed effects are controlled for, estimates of Texting Ban are insignificant and close to 0, providing evidence that texting bans have no effect. In con- trast, handheld bans reduce the drivers’ proba- bility of talking on handheld cell phones by 2.8 percentage points, which is significant at the 1% level. This represents a 50% drop from the rate of 5.6% in states adopting handheld bans before these bans are enacted. Column 2 is the preferred specification, in which I additionally control for time-varying covariates, including driver charac- teristics (e.g., gender, age, and race), observa- tional site features (e.g., rural or urban areas), and weather condition. Estimates of Texting Ban and Handheld Ban remain almost unaffected after controlling for time-varying controls compared to estimates in column 1. This provides evidence that the within-state variation in cell phone bans is orthogonal to known determinants of handheld device manipulation, which is consistent with the idea that the within-state variation in bans is as- good-as-random. It also gives me some reason to believe that the within-state variation would also be orthogonal to unobserved determinants (Altonji, Elder, and Taber 2005).

In column 3, I include leading indicators of Texting Ban and Handheld Ban to directly test if cell phone usage trends diverge 1 year before bans are enacted. The two insignificant leading indicator estimates show no evidence of such divergence. In Figure 2A, I also show the esti- mated difference in handheld cell phone usage while driving between adopting and nonadopting states over time from before and after the adop- tion of handheld bans. Specifically, this figure plots coefficients from a DD model in which I control for state- and year-fixed effects, time- varying covariates, existence of texting bans, and then allow for divergence each year starting from the fourth year prior to the adoption of handheld bans. Estimates are therefore relative to the aver- age difference in the average use of handheld cell phones 5 or more years prior to the adoption of handheld bans. The figure suggests that (1) there is no evidence of divergence prior to adoption and that (2) the difference in handheld cell phone use experiences a structural drop right after the adoption of cell phone bans. As the difference decreases from the average of 0.009 before ban adoption to the average of −0.021 after adoption,

1428 ECONOMIC INQUIRY

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CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1429

FIGURE 2 Estimated Difference in Driver Cell Phone Use before and after the Adoption of Cell Phone Bans

between Adopting and Nonadopting States, Relative to the Difference 5 or More Years before Adoption

–.02

–.01

.01

.02A

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re n c e

–4 –3 –2 –1 0 1 2+

Year since the Adoption of Handheld Bans

–.02

–.01

.01

.02

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re n c e

–4 –3 –2 –1 0 1 2+

Year since the Adoption of Texting Bans

the change in the difference is −0.029 which corresponds to the estimate of Handheld Ban (−0.0284) in column 2.

In column 4, I also include region-year fixed effects. The estimates are unchanged, which sug- gests that the effects are not confounded by regional common shocks. Finally, in column 5, I include state-specific linear time trends to relax the assumption that state-level unobserv- able covariates are constant from 2004 to 2010 and find that results stay robust (Friedberg 1998).

From columns 6 to 10, I re-estimate the effects of cell phone bans using weighted least squares (WLS) in which state population is used to adjust

the sampling weight because the chosen sam- ple depends on observational sites that are not necessarily representative. Results are not sta- tistically different from estimates in the first six columns.

In panel B, I examine if cell phone bans have any effect on handheld device manipulation while driving, such as sending text messages. Results provide evidence that texting bans significantly reduce the probability of such behavior by about 0.6 – 1.9 percentage points, which is about 40% – 70% drop compared to the manipulation rate before adopting states passed texting bans. These findings are also confirmed

1430 ECONOMIC INQUIRY

by Figure 2B. Meanwhile, there appears to be a substitution from manipulating handheld devices toward using handheld cell phones caused by handheld bans as almost all the estimates of Handheld Ban are positive and significant at the 1% level.

Thus, both graphical and regression evidence suggest that texting bans and handheld bans are quite effective in reducing visible handheld device manipulation and handheld cell phone use, respectively, by increasing the expected cost of using a cell phone while driving. Moreover, handheld bans appear to induce drivers to fur- ther shift toward more texting. One interpreta- tion consistent with this finding is that it is much easier to avoid detection by police while tex- ting than to avoid detection when talking on a handheld phone, as one can always text by hold- ing the cell phone in a concealed way. But a caveat in interpreting the effect of handheld bans is that, as discussed in Section II.A, it is dif- ficult to distinguish between whether handheld bans matter on their own and whether banning both texting and talking while driving is what really works. In addition, given the way in which NOPUS data are collected, there is always the open question as to whether the relative declines in usage measured here extend to other locations and times.

B. Do Cell Phone Bans Reduce Accidents and Casualties?

After establishing the mechanism through which cell phone bans could matter, I now turn to the quarterly state-level panel data to investi- gate the effect of cell phone bans on accidents and casualties. Estimates in Table 4 provide evidence that neither of the bans appears to have meaningful effects on traffic accidents and casualties, as the majority of the estimates are statistically insignificant and close to zero.20

These findings are largely consistent with Abouk and Adams (2013) and Bhargava and Pathania (2013).21 However, a potential concern is that in Table 4 Handheld Ban estimates become

20. In Table S1, I also look at incapacitating injuries and fatalities separately and find similar results.

21. In addition, permutation tests in the spirit of Bertrand, Duflo, and Mullainathan (2004), Chetty, Looney, and Kroft (2009), Abadie, Diamond, and Hainmueller (2010), and Nunn and Qian (2011) further confirm the results of the null effect of cell phone bans on traffic accidents and casu- alties. Such tests are also called “refutability” tests in the study by Angrist and Krueger (1999). Results are available upon request.

economically and statistically significant when linear trends are included. This is worrisome because it suggests perhaps states were on diverging trends before handheld bans were adopted and including these linear trends con- trols for that. However, I find no evidence of diverging trends.22

Combined with the evidence from how drivers respond to texting bans and handheld bans, it seems quite interesting that cell phone bans have no effect on traffic accidents and casualties even though they reduce cell phone use while driving. There are two possible interpretations for this. One is that cell phone bans could reduce acci- dents and casualties by reducing some drivers’ use of cell phones. But meanwhile they could also make drivers more likely to text or make phone calls in a concealed way. This type of behavior is likely more dangerous and would thus lead to more accidents and casualties, offsetting any reduction due to less overall cell phone use while driving. The other interpretation is that drivers compensate for distracted cell phone-related driv- ing behavior by driving more cautiously in other ways, similar to the “Peltzman Effect” (Peltzman 1975) in the setting of safety-belt use. Therefore, texting or talking on handheld cell phones does not necessarily lead to more accidents and casu- alties, because rational drivers simply drive more cautiously when doing so. Both of these interpre- tations are consistent with the finding that cell phone bans do not reduce accidents and casual- ties, even though they do reduce overall usage of cell phones by drivers.23

C. Differential Effects

To this point, I have shown the average effect of cell phone bans on drivers’ cell phone usage, and subsequently on accidents and casualties. Here, I investigate the differential effects of cell

22. I provide graphical evidence in Figure S2. Similar to what I did in Figure 2, I calculate and plot the estimated dif- ference in accident and casualty rates by year relative to the adoption of handheld bans between adopting and nonadopt- ing states, only controlling for state- and year-quarter fixed effects. In particular, the graphical evidence suggests that the DD strategy would difference out the common declining trend in accidents and casualties. As a result, it probably makes lit- tle sense to include linear trends, as there is little evidence of diverging accident and casualty trends before handheld bans were passed.

23. Substituting other distracted driving behavior (e.g., talking to passengers or fiddling with radios) with the use of cell phones could also explain why cell phone bans do not affect accidents and casualties for risk-loving drivers (Bhargava and Pathania 2013; Hahn and Tetlock 1999).

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1431

T A

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1432 ECONOMIC INQUIRY

phone bans on different types of drivers and in different locations.

Two kinds of differential effects related to driver types are of particular interest. The first is that cell phone bans could affect a driver’s behavior differentially depending on whether the driver is accompanied by passengers or not. For example, a driver may be able to substitute pas- sengers’ cell phone use for her own, thereby mak- ing it easier for her to comply with the ban. In short, raising the cost of using a cell phone while driving is likely to change behavior the most when there are good substitutes available, and drivers with passengers have more substitutes available. Similarly, risk-averse passengers who are aware of the cell phone bans are more likely to remind the drivers to comply with the bans. Thus, it is reasonable to expect that cell phone bans would have the biggest effect on drivers accom- panied by passengers.

In Panel A of Table 5, results show that drivers who are driving with passengers do respond more to cell phone bans than those who are driv- ing alone. As the estimates in columns 1 and 3 based on Model (1) only represent absolute changes in probabilities of handheld cell phone use and handheld device manipulation, respec- tively, in columns 2 and 4, I convert them to proportional changes relative to the correspond- ing probabilities prior to cell phone bans being adopted in order to better compare these esti- mates. The results imply that texting bans reduce manipulation of handheld devices about 1.5 times as much for drivers with passengers as for sin- gle drivers. There is a similarly disproportionate effect for handheld bans. One somewhat pecu- liar finding is that texting bans appear to induce drivers with passengers to be much less likely to talk on handheld cell phones. This could be because passengers text or talk on their phones in lieu of the driver doing so when a ban is in effect.

Along similar lines, it is interesting to know if cell phone bans also have differential effects on young and adult drivers as well as these two types of drivers generally have different driving behav- ior. Results from Panel B suggest that cell phone bans only differentially alter the way young and adult drivers send text messages, not whether or not they make phone calls while driving. In particular, texting bans significantly reduce the probability of manipulating handheld devices among adult drivers by 68% but have no signifi- cant effect on young drivers. Also, handheld bans induce more adult drivers to shift from talking to texting while driving than young drivers.

Results in Panel C further show that there are no differential effects on accidents with respect to the presence of passengers and drivers’ age, as in each column estimates are insignificant and are not significantly different from each other. This is striking, and suggests that even for those subgroups whose behavior is most affected by the ban, there is no evidence of a reduction in accidents or casualties. Again, this could be explained by more hidden use of cell phones or by compensating driving behavior, as discussed in Section IV.B.

Finally, one might be concerned that drivers only change their behavior in locations observed by NOPUS such as traffic-controlled intersec- tions, but not in other locations. As a result, one might not expect to see reductions in overall accidents and casualties. It is also possible that drivers substitute usage away from intersections and toward freeways, which could also explain why accidents do not decline overall. Therefore, in Table S2, I examine the differential effects of cell phone bans on accidents in different loca- tions. Results in columns 1 and 2 show that cell phone bans have no significant effect on acci- dents in intersection areas. Thus, even in loca- tions where driver cell phone usage is reduced, there is still no evidence of a decline in accidents. In addition, columns 1 – 6 show no evidence of displacement from traffic-controlled intersection areas to nonintersection areas, intersections with- out traffic controls, or arterial and local roads.24

D. Additional Tests and Robustness Checks

In this section, I perform different kinds of tests and robustness checks. First, to understand whether cell phone bans could affect traffic acci- dents and casualties through channels other than reducing drivers’ cell phone usage, I look at if the general driving behavior is affected. To do so, I focus on the effect of cell phone bans on VMT, which is a measure of the total vehicle mileage. Estimates in the first five columns of Table S3 are all insignificant and close to zero, which sug- gests that it is unlikely that the effect of cell phone bans on accidents and casualties could be

24. FARS data imply that 28% of the accidents happen near intersections, and 63% of these accidents are in traffic- controlled intersections. In particular, traffic controls include highway traffic signals (e.g., flashing traffic control signal), regulatory signs (e.g., stop signs), school zone signs (e.g., school speed limit sign), warning signs, and others (e.g., crossing guard).

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1433

TABLE 5 Differential Effects of Cell Phone Bans by Driver Type

1 2 3 4

Handheld Cell Phone Usage

(Talking on Handheld

Cell Phones)

% Change Compared to Rate

of Handheld Cell Phone Use

Prior to Adoption of Cell Phone Bans

Handheld Device Manipulation (Sending Text

Messages, etc.)

% Change Compared to Rate

of Handheld Device

Manipulation Prior to Adoption

of Cell Phone Bans

Panel A. Differential Effects by the Presence of Passengers on Cell Phone Use Texting ban × Driver

with at least one passenger

−0.0205*** (0.0070)

−50 −0.0171*** (0.0040)

−77

Texting ban × Driver without passenger

−0.0013 (0.0099)

−2 −0.0129*** (0.0036)

−52

Handheld ban × Driver with at least one passenger

−0.0329*** (0.0066)

−70 0.0104** (0.0043)

347

Handheld ban × Driver without passenger

−0.0256*** (0.0084)

−42 0.0133*** (0.0037)

190

Observations 331,883 — 2,935,666 —

Panel B. Differential Effects by Driver Age on Cell Phone Use Texting ban × Young

driver (16 < driver age < 24)

−0.0034 (0.0100)

−5 −0.0066 (0.0050)

−23

Texting ban × Adult driver (driver age > 25)

−0.0073 (0.0078)

−16 −0.0152*** (0.0036)

−68

Handheld ban × Young driver (16 < driver age < 24)

−0.0463*** (0.0083)

−52 0.0119*** (0.0037)

108

Handheld ban × Adult driver (driver age > 25)

−0.0254*** (0.0074)

−50 0.0120*** (0.0038)

240

Observations 331,883 — 2,935,666 —

log(Accident Rate) (Drivers with at least

One Passenger)

log(Accident Rate) (Drivers

without Passenger)

log(Accident Rate) (16 < Driver

Age < 24)

log(Accident Rate) (Driver

Age > 25)

Panel C. Differential Effects on Accidents Texting ban 0.0150

(0.0288) −0.0223 (0.0296)

−0.0198 (0.0393)

−0.0041 (0.0268)

Handheld ban −0.0012 (0.0326)

−0.0028 (0.0311)

0.0032 (0.0288)

−0.0272 (0.0326)

Observations 1400 1400 1400 1400 State and

year/year-quarter fixed effects

Yes Yes Yes Yes

Time-varying controls Yes Yes Yes Yes

Notes: The table reports panel data OLS estimates. Standard errors are clustered at the state level. Time-varying controls for Panels A and B include indicators for gender, age group, race, rural and urban areas, weekday nonrush hour, weekend, and clear weather. Time-varying controls for Panel C include unemployment rate, demographics, seat belt law dummy, state median income, violent and property crime rates, government spending on highway and public welfare, police, and population.

*Significant at the 10% level; **significant at the 5% level; ***significant at the 1% level.

1434 ECONOMIC INQUIRY

due to differences in traffic congestion during the examination period.25

Second, the NOPUS data allow me to examine the effect of cell phone bans on drivers’ seat belt usage, which I use as a proxy for general safe-driving behavior. If the estimated effects of cell phone bans also pick up effects of other concurrent policies that improve driving safety, then I expect to see cell phone bans significantly increase the use of seat belts. However, I find zero effect as shown in columns 6 – 10, which suggests this confounding story is not likely to be true.

Third, results in columns 11 – 15 provide evidence that cell phone bans do not induce drivers to increase their use of hands-free technologies. While observing hands-free tech- nologies is perhaps somewhat difficult, this result does suggest that substitution over this time period is only between talking and texting on handheld phones.

Moreover, cell phone bans could also lead to more pedestrian deaths if drivers choose to drive more aggressively (e.g., speeding) when using cell phones while driving is prohibited, similar to what Peltzman (1975) argues regarding mandatory safety devices on automobiles. My data allow me to further investigate if cell phone bans lead to more nonoccupant casualties, but I find no conclusive evidence of that.26

Finally, I check if different definitions of cell phone bans change the results in Table S5. In Panel A, I drop two states (New Jersey and Wash- ington) where cell phone bans were upgraded to the primary enforcement. In Panel B, to single out the effect of texting bans, I exclude the six states that passed handheld bans. In Panel C, I keep the same state and year combinations used in NOPUS since NOPUS data are not balanced. In Panel D, I redefine Texting Ban and Handheld Ban to be fractions of days during a quarter rather than binary variables in order to better capture the effects of cell phone bans in the quarter when they are enacted.27 Results provide evidence that

25. Carpenter and Stehr (2011) find that state youth bicycle helmet laws have the unintended consequence of reducing youth bicycling.

26. Estimated effects of cell phone bans on nonoccu- pants casualties are reported in Panel B of Table S4. Texting Ban estimates are all close to zero and insignificant. Hand- held Ban estimates are in general large, although most are imprecisely estimated.

27. For example, California adopted handheld ban on July 1, 2008. Therefore, in terms of fractions of days with tex- ting ban in 2008, the value of Handheld Ban for California in 2008 should be 0.5, compared to 1 using the binary definition.

the estimated effects are robust to these changes in definition.28

V. CONCLUSION

Texting and handheld bans are the major response from state legislatures to the widely perceived increase in distracted driving. How- ever, recent studies show that these bans do not reduce traffic accidents over the medium or long term. This study asks if this is because the laws fail to change driver behavior, which might be the case if the bans were not enforced. In contrast, results provide evidence that driver behavior is very responsive: texting bans reduce visible texting while driving by around 60% and handheld bans reduce the probability of talking on handheld cell phones while driving by around 50%. In addition, cell phone bans appear to have a larger effect on adult drivers and drivers accompanied by passengers. However, these apparent changes in behavior do not lead to meaningful reductions in accidents or casualties, which is consistent with existing literature. This is true even for subgroups who reduce cell phone usage while driving the most.

This apparent puzzle can be resolved by sev- eral different explanations. One is that hand- held cell phone use while driving is less dan- gerous than commonly believed. Similarly, it is possible that the risk of handheld use is offset by driving more carefully while using handheld phones. Alternatively, the bans may induce more hidden and likely dangerous use of cell phones while driving. While it is difficult for me to shed light on which of these potential interpretations is driving the results, it is clear that while cur- rent bans are effective in changing drivers’ behav- ior, they do not achieve the ultimate policy goal. This suggests that improving the effectiveness of the laws in reducing accidents is considerably more complex than merely improving enforce- ment. Perhaps more importantly, the results also have important social welfare implications in

28. The 2004 – 2010 sample period only leaves out New York’s handheld ban, which was passed in 2001. As a check, I include New York’s 2001 handheld ban by using the 2000 – 2010 sample and estimate the count model (accidents and casualties are not normalized). I find that this does not meaningfully affect the estimated effects of cell phone bans on accidents and casualties. For example, when including New York, the estimates of Texting Ban and Handheld Ban for acci- dents are −0.0256 (SE = 0.0230) and −0.012 (SE = 0.0257), respectively, which are similar to the corresponding count data model estimates of −0.0148 (SE = 0.0221) and −0.0249 (SE = 0.0340) reported in column 1 of Panel A in Table S6.

CHENG: DO CELL PHONE BANS CHANGE DRIVER BEHAVIOR? 1435

that cell phone bans impose significant social costs on drivers, without yielding the intended social benefits.

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SUPPORTING INFORMATION

Additional Supporting Information may be found in the online version of this article:

Figure S1. Cell Phone Use while Driving, Accident Rate, and Casualty Rate by Year

Figure S2. Estimated Difference in Accident/Casualty Rate Before and After the Adoption of Handheld Bans between Adopting and Non-adopting States, Relative to the Difference 5 or More Years before Adoption

Table S1. Effects of Cell Phone Bans on Fatalities and Injuries

Table S2. Differential Effects of Cell Phone Bans by Location

Table S3. Additional Tests: The Effect of Cell Phone Bans on VMT, Seat Belt Usage and Headset Usage

Table S4. Effects of Cell Phone Bans on Casualties of Occupants and Nonoccupants

Table S5. Additional Robustness Checks Table S6. The Effect of Cell Phone Bans on Traffic

Accidents and Casualties (Count Data Model)