Do shared e-scooter services cause traffic accidents? Evidence from six European countries

refsection\begin{abstract} We estimate the causal effect of shared e-scooter services on traffic accidents by exploiting variation in availability of e-scooter services, induced by the staggered rollout across 93 cities in six countries. Police-reported accidents in the average month increased by around 8.2% after shared e-scooters were introduced. For cities with limited cycling infrastructure and where mobility relies heavily on cars, estimated effects are largest. In contrast, no effects are detectable in cities with high bike-lane density. This heterogeneity suggests that public policy can play a crucial role in mitigating accidents related to e-scooters and, more generally, to changes in urban mobility. \end{abstract} \section{Introduction} In the EU alone, over 150,000 people are killed or seriously injured in traffic accidents every year. The oecd2018 estimates that social costs of traffic accidents exceed 3% of the EU's GDP. In recent years, e-scooters emerged as a prominent mode of transportation in cities worldwide. Between 2018 and mid-2022, more than \$5bn was invested in companies providing shared e-scooter services McKinsey2022. Despite their increased availability, the role of shared e-scooters in future urban mobility ecosystems remains a highly divisive discussion topic. Proponents argue that shared e-scooters can ease issues related to motorized traffic, such as air pollution, noise, and congestion shaheen2019shared, gossling2020integrating, abduljabbar2021role. Opponents raise concerns about sustainability, safety, and crowded sidewalks hollingsworth2019scooters, james2019pedestrians, sanders2020scoot. One central point of contention is the social cost induced by shared e-scooter services through traffic accidents. Thus far, the public and academic discussion has mostly focused on the large relative change in injuries from e-scooter-related accidents over time choron2019integration. This increases occurs by design because e-scooters were virtually non-existent before 2018. Additionally, this approach is lacking because substitution between modes of traffic and other indirect effects are not accounted in by these raw numbers, as detailed below. To address this scarcity of evidence, this article studies medium-run effects of the introduction of shared e-scooters on road safety in six European countries. We identify the effect on urban accidents using quasi-experimental variation in the availability of shared e-scooters across cities and time. In our analyses, treatment start is defined as the city-specific launch date of the first shared e-scooter service. Once the technology and capital for dockless e-scooters became widely available and national regulation allowed their use, e-scooter firms rapidly expanded into large cities across our sample countries, Austria, Finland, Germany, Norway, Sweden, and Switzerland. We assume that the city-specific treatment timing is exogenous to accidents conditional on city fixed effects and time fixed effects since the rollout of e-scooter services is mainly determined by national regulation and business constraints, time-invariant city characteristics, as well as seasonal variation. In more technical terms, ghanem2022selection show that a sufficient condition for the parallel trends assumption to hold are that the selection mechanism is independent from city-time-varying unobservables and that city-time-varying unobservables that affect accidents have a constant mean over time conditional on city-level time-invariant unobservables. This allows us to estimate effects in a difference-in-differences model, using the monthly data on traffic accidents in cities before and after the arrival of e-scooter providers. We use the estimator proposed in borusyak2021revisiting, which also straightforwardly allows us to conduct heterogeneity tests for subgroups and to obtain estimates with and without using never-treated cities in our control group. All our estimates account for period and city fixed effects, and heterogeneous treatment effects under staggered rollout. Our data combine administrative traffic accident data from 2016 to mid-2021 at the city-month level with extensive data on the timing of the rollout of e-scooter services by over 30 providers in 93 major European cities. Our estimation sample consists of all cities with a population of at least 100,000 that are not suburbs of larger metropolitan areas, and where a shared e-scooter service was introduced or announced by the end of 2021. The six countries are selected based on publishing accident data in the required detail and on having launched e-scooter services early enough, to be able to observe medium-run effects. The launch dates of shared e-scooters are manually collected from public sources and contain data on all firms offering e-scooter services in the six countries (details in (ref)). We find that police-reported accidents in cities with shared e-scooter services increased significantly by \(8.2\pm2.9\%\) (mean estimate \(\pm\) std. error) relative to a counterfactual, estimated from cities where e-scooters launched later. Treatment effect estimates are larger (\(11.5\pm3.5\%\)) for summer months when e-scooters are used and deployed more intensively, while estimates for winter months are statistically insignificant. The estimate for the average effect is smaller but still economically and statistically significant (\(4.7\pm2.3\%\)) if the control observations are expanded to include, possibly less comparable, cities that never received e-scooters. Our results are robust to different specifications that address potential concerns related to endogenous treatment timing, or confounding effects of COVID-19 countermeasures and seasonality. To explore the underlying mechanisms, we study treatment effect heterogeneity between cities with different traffic and road characteristics. Following the literature on cycling safety---a closely related mode of transportation---we analyze accidents along the dimensions of separated micromobility-suitable infrastructure (henceforth bike lanes), registered cars per capita, and modal splits. In cities with a low density of bike lanes or relatively many registered private cars per capita, the effects are substantial (\(11.5\pm3.9\%\) and \(10.1\pm4.1\%\)). In contrast, we find no significant effect in cities with comparably extensive bicycle infrastructure and smaller effects in cities with a low number of cars per capita. Thus, our heterogeneity results point towards a central role of separated cycling infrastructure and public policy in mitigating accidents. This has important policy implications since many cities, regions, and countries have made political commitments to increasing their micro-mobility modal share (including the use of bicycles, e-scooters, and similar modes of transportation) in the face of climate change.\footnote{E.g., in the Pan-European Master Plan for Cycling, signed by 54 European nations, 16 nations have approved national cycling strategies stating an increased cycling modal share as explicit measurable objectives ecf.} The lessons from the changes in modal shares induced by the staggered rollout of shared e-scooter services can serve as a precedent for how to safely increase micro-mobility in cities. Our results naturally account for substitution between modes of transportation. Raw numbers of e-scooter accidents, even if they were recorded consistently and published for many cities, would be ill-suited to inform policy, because they cannot account for substitution and indirect effects. If, e.g., e-scooters substitute for cars, then cities may see an increase in e-scooter accidents but a reduction in accidents involving cars. The resulting overall effect could be a reduction in accidents, in spite of an increase in e-scooter accidents. Therefore we study accidents involving personal injury, irrespective of the involved vehicles. The fact that we find large significant treatment effects, suggests that substitution effects must be negligible. Another reason to focus on overall accidents is that not all accidents caused by e-scooters must necessarily involve an injured e-scooter user. For example, the analysis of two Swedish data sets of injuries associated with e-scooters stigson2021electric showed that 8% of such injuries were sustained by other road users. An additional 5% were pedestrians or cyclists injured by parked e-scooters. If shared e-scooters indirectly affect accidents among other modes of transportation, studying overall accidents can reveal those effects regardless of whether detailed classifications of all indirectly involved parties are available. The existing evidence on injuries caused by e-scooter accidents is of limited generalizability and not suited to inform public policy for two more reasons. First, previous studies are mostly descriptive and based on hospital data in single cities or countries. These analyses usually characterize accident risk factors and types of injuries badeau2019emergency, sikka2019sharing, trivedi2019injuries, blomberg2019injury, yang2020safety, namiri2020electric, stigson2021electric, but do not quantify the effects of e-scooter services on overall accidents resulting in injuries. Second, existing literature does not study the role of different city characteristics in mitigating accidents. We add to the literature on factors affecting and mitigating traffic accidents, such as traffic regulations peltzman1975effects, abouk2013texting, van2015optimal, bauernschuster2022speed or road characteristics wang2013effect. \section{Data and empirical strategy} \subsection{Data sources and sample} We limit our study to cities of at least 100,000 inhabitants that are not suburbs of larger cities and the period between January 2016 and June 2021.\footnote{The panel horizon of 6/2021 addresses a trade-off: Shorter horizons reduce the available post-treatment periods to estimate effects. Longer horizons include periods for which few yet-to-be-treated cities remain to estimate the period fixed effects. Using 6/2021 ensures enough yet-to-be-treated cities remain (see (ref)) without omitting the whole summer of 2021. Estimates are comparable when using different cut-offs, e.g., 12/2020 or 9/2021.} (ref) describes all data sources in detail. \subsubsection{E-scooter service rollout} The data on the launch dates of e-scooter services in different cities have been collected from official press releases, social media channels, and websites of e-scooter providers, local newspapers, or cities. We corroborate our data with dates provided directly by two large e-scooter firms. In total, we have data on rollouts for 38 different providers. (ref) illustrates the recorded launch dates of providers in all included cities until December 2021. \subsubsection{Traffic accidents} We have monthly administrative data on traffic accidents involving personal injury for January 2016 to June 2021. Data from Sweden is not available for 2016 and 2017. Austria, Germany, and Switzerland report traffic accidents by city, however the Scandinavian countries report accidents by municipalities. For large cities, as in our sample, municipalities and cities are well-aligned: the population of the average Scandinavian sample city, makes up 88% of corresponding municipality's population (details in (ref)). For the cities of Stockholm, Oslo and Helsinki, which span multiple municipalities, we use data from the homonymous municipality, covering the majority of the respective city's population. \subsubsection{Heterogeneity variables} To investigate treatment effect heterogeneity along different city characteristics, we use three different variables: share of separated bike lanes in the road network, registered cars per capita, and cycling modal share. The length of separated cycling infrastructure and total road network length are collected from OpenStreetMap. Data on cars per capita and on cycling modal shares by city are primarily obtained from eurostat, and supplemented with local administrative sources or academic papers. \subsection{Empirical strategy} The analysis of treatment effects under staggered rollout requires special care. Standard multi-period DD estimators---commonly referred to as two-way fixed-effects (TWFE) estimators---can be biased when treatment effects vary over time (e.g., decrease with exposure duration) and when estimation uses data spanning periods in which (i) earlier-treated units remain treated across periods while (ii) later-treated units start being treated. This bias arises because in standard TWFE models the change in outcomes of earlier-treated groups is used to estimate the counterfactual change over time, in spite of the fact that the outcome of these observations comprises the evolving treatment effect. Detailed discussions of these issues is found in goodman2021difference, callaway2021difference, sun2021estimating,borusyak2021revisiting. In our setting the conditions that give rise to the bias of the TWFE estimator fully apply. Treatment timing varies considerably and treatment effects are likely to vary over time for a number of reasons: Fleet sizes grow over time and vary seasonally, urban traffic can adapts to the services, and e-scooter technology improves. For this reason, we base our analyses on two sets of methods that address this issue: i) an event-study estimator based on monthly data borusyak2021revisiting and ii) a simple DD estimator based on annual data that uses two groups of cities (early-treated cities and late-treated cities) and compares differences in accidents in 2018 to differences in accidents in 2020. All specifications account for city and period fixed effects to capture effects of confounders that are either relatively stable across time (e.g., population, city-specific traffic characteristics, coding or reporting standards) or space (e.g., seasonality in traffic, technological development, climate change). Our results are also robust to allowing for city-specific time trends ((ref)). \subsubsection{Event-study estimates} For our data, assume outcomes in each city-period are described by \begin{equation} \log accidents_{it} = \alpha_i + \beta_t + \tau_{it}d_{it} + \varepsilon_{it}, \end{equation} where \(\alpha_i\) is a city-level fixed effect, \(\beta_t\) is a month-level fixed effect, \(d_{it}\) is a city-month-level indicator for treatment and \(\tau_{it}\) is the city-month-specific treatment effect. The error term, \(\varepsilon_{it}\), captures random variation in the number of reported accidents that is unrelated to treatment but varies over time and space, e.g., measurement error due to reporting or coding of accidents. The individual city-month-specific treatment effect cannot be identified (separately from the error \(\varepsilon_{it}\)). But we are interested in (conditional) expectations of these effects \(\tau_{it}\), e.g., the average treatment effect across all post-treatment months \(\mathop{\mathbb{E}}[\tau_{it}]\) or the average treatment effect within 12 months of a city's launch date, \(l_i\), \(\mathop{\mathbb{E}}[\tau_{it}|t\leq l_i+12]\). These can be estimated. Estimation follows three steps. First, only untreated observations (pre-treatment city-months) are used to estimate \(\alpha_i\) and \(\beta_t\). Second, these estimated city fixed effects and month fixed effects are used to estimate treatment effects for each treated city-month, \(\widehat{\tau_{it}} = \log \textrm{accidents}_{it} - \hat{\alpha}_i - \hat{\beta}_t\). Third, these city-month estimates are averaged. This average is weighted with weights to match the respective estimand of interest, e.g., the average effect across all post periods ((ref), col. 1) applies an equal weight to all treated periods and the average effect within 12 months of treatment ((ref), col. 3) applies an equal weight to the first 12 treatment months by each city and a weight of zero to other observations. The average effects by season ((ref), col. 4--5) or month since introduction are estimated analogously by applying weights of zero to the respective other months. Heterogeneity tests ((ref)) assume accidents are: \begin{equation} \log accidents_{it} = \alpha_i + \beta^h_t + \beta^h-l_t\mathbbm{1}_{(x_i>\overline{x}_i)} + \tau_{it}d_{it} + \varepsilon_{it}, \end{equation} where \(\mathbbm{1}_{(x>\overline{x}_i)}\) indicates if a city is above the country median of the specific heterogeneity variable, so \(\beta^\text{h-l}_t\) allows for different month fixed effects depending on the heterogeneity variable. Estimation proceeds as before, estimating city fixed effects and both sets of month fixed effects on control observations only. Effect estimates are again obtained as a weighted average of month-city level estimates. Tests for equality between effects are conducted by using weights that sum up to 1 for cities above the median and to -1 for cities below the median of the variable of interest, thus estimating \(\mathop{\mathbb{E}}[\tau_{it}|\textrm{above median}] - \mathop{\mathbb{E}}[\tau_{it}|\textrm{below median}]\). This estimate and the corresponding standard error can then be used to test the hypothesis that \(\mathop{\mathbb{E}}[\tau_{it}|\textrm{above median}] = \mathop{\mathbb{E}}[\tau_{it}|\textrm{below median}]\). We estimate all models using the natural logarithm of the number of accidents as the dependent variable. Effects sizes are likely not constant in absolute terms, but only relative to the baseline number of accidents, e.g., because the number of deployed e-scooters tends to be roughly proportional to city size. Also, the number of accidents exhibits seasonal swings, with absolute magnitudes roughly proportional to levels. After applying the logarithm, the seasonal swings run parallel across cities, as visualized in (ref). This effect of the logarithmic transformation is expected if, relative to levels, seasonal swings are parallel across cities. Having parallel seasonality across cities is essential to maintain the parallel trends assumption. Using logarithmized dependent variables is unproblematic in our case as observations with zero accidents are rare. Only a single city has zero accidents for only a single month (Oulu, Finland, Feb 2019, two years before e-scooters were introduced). For the estimation, we impute one accident for this observation, but our estimates are qualitatively robust to dropping this observation. The log-linear specification has the benefit of providing estimates that can be approximately interpreted as semi-elasticities, i.e., the percentage increase in accidents due to the rollout of e-scooter services. Tables show transformed estimates expressing non-approximate semi-elasticities \(100\cdot(\exp(\hat{\tau})-1)\%\). Standard errors allow for the clustering of the model error at the city level. Standard errors are computed from residuals based on (ref). To obtain residuals it is necessary to assume a model that is parsimonious enough so that it can separate \(\tau_{it}\) from \(\varepsilon_{it}\). Hence we cannot (as in estimation) allow for arbitrary treatment effect heterogeneity. Instead, we assume that treatment effects are constant within cohorts and use the quarter of scooter introduction to define cohorts, with two exceptions. Zurich, which is the first city that received e-scooters and the only city in Q2 of 2018, is added to the cohort of Q3 2018, and cities that launched scooters in Q1 2021 and Q2 2021 are considered as one cohort. For the heterogeneity analysis in (ref), where the samples are split, several quarters contain too few cities and we thus rely on half-years to define cohorts. To have sufficiently many observations per cohort all cities that launched until June 2019 are considered one cohort and all that launched since December 2021 are considered as one. The assumption of constant treatment effects within cohorts bears the risk of being incorrect. However, it was shown that this possible misspecification yields conservative inference borusyak2021revisiting. Throughout the paper, unless indicated differently, standard errors are computed through a leave-out procedure, that computes the cohort-level treatment effect to obtain the residual, under omission of the focal unit borusyak2021revisiting. \subsubsection{Annual difference-in-differences} As additional corroboration, we use an annual DD framework comparing changes in accidents from 2018 to 2020 between cities that introduced scooters during 2019 and cities that introduced scooters in or after July 2020. In this panel, there are only two periods and two groups of cities (those that are treated in 2019 and those that are treated later). This model is thus a standard 2-period DD setup, which sidesteps the above-mentioned issues with heterogeneous treatment timing and time-varying treatment effects. We use 2018, the last year before companies started introducing e-scooter services in most cities as the pre-treatment period, and 2020 as the post-treatment period. Choosing a later post-treatment year would destroy the ability to maintain a comparable set of control cities that are yet-to-be-treated. Choosing an earlier post-treatment year would be disadvantageous because in most sample cities scooters were only introduced during 2019. The regression equation is \[\log \textrm{accidents}_{it} = \alpha_i + \delta_t + \beta \textrm{treatment}_{it} + \varepsilon_{it},\] where \(\textrm{treatment}_{it}\) measures if city \(i\) launched shared e-scooters before period \(t\). \(\alpha_i\) and \(\delta_t\) are city and year fixed effects. \section{Results} (ref), column 1 reports the average treatment effect across all treated city-months. Accidents involving personal injuries increased on average by \(8.2\pm2.9\%\) (mean estimate \(\pm\) std. error). To put the estimated effect into perspective: the median sample city in terms of accidents (Potsdam, Germany, population of 180,334) reports 54 accidents in the average pre-treatment month. An increase of 8.2% thus implies an additional 4.4 monthly accidents. \begin{table*}[htbp] \caption{Estimated treatment effects on police-reported accidents involving personal injury} \adjustbox{max width=\textwidth}{{ \def\sym#1{\ifmmode^{#1}\else\(^{#1}\)\fi} \begin{tabular}{l*{8}{c}} \toprule &\multicolumn{6}{c}{\begin{tabular}{c}Monthly event-study estimate\\ \end{tabular}} &\multicolumn{2}{c}{\begin{tabular}{c}2018 vs 2020\\difference-in-differences\end{tabular}}\\\cmidrule(lr){2-7}\cmidrule(lr){8-9} &\multicolumn{1}{c}{(1)} &\multicolumn{1}{c}{(2)} &\multicolumn{1}{c}{(3)} &\multicolumn{1}{c}{(4)} &\multicolumn{1}{c}{(5)} &\multicolumn{1}{c}{(6)} &\multicolumn{1}{c}{(7)} &\multicolumn{1}{c}{(8)} \\ & &\begin{tabular}{c}Incl. never-\\treated cities\end{tabular} &\begin{tabular}{c}First 12\\months\end{tabular} &\begin{tabular}{c}Non-winter\end{tabular} &\begin{tabular}{c}Winter\end{tabular} &\begin{tabular}{c}Excluding\\COVID\end{tabular} & &\begin{tabular}{c}Incl. never-\\treated cities\end{tabular} \\ \midrule %-increase in accidents& 8.2***& 4.7** & 5.3** & 11.5***& 1.9 & 5.7***& 9.2***& 6.0** \\ & (2.9) & (2.3) & (2.1) & (3.5) & (3.3) & (2.1) & (2.8) & (2.6) \\ \midrule Mean pre-treatment accidents&\phantom{space}\clap{93.2}\phantom{space} &\phantom{space}\clap{83.0}\phantom{space} &\phantom{space}\clap{93.2}\phantom{space} &\phantom{space}\clap{100.6}\phantom{space} &\phantom{space}\clap{78.5}\phantom{space} &\phantom{space}\clap{95.8}\phantom{space} &\phantom{space}\clap{1292.1}\phantom{space} &\phantom{space}\clap{1154.0}\phantom{space} \\ Treated observations&\phantom{space}\clap{1704}\phantom{space} &\phantom{space}\clap{1704}\phantom{space} &\phantom{space}\clap{956}\phantom{space} &\phantom{space}\clap{1140}\phantom{space} &\phantom{space}\clap{564}\phantom{space} &\phantom{space}\clap{948}\phantom{space} &\phantom{space}\clap{48}\phantom{space} &\phantom{space}\clap{48}\phantom{space} \\ Total observations &\phantom{space}\clap{5880}\phantom{space} &\phantom{space}\clap{7134}\phantom{space} &\phantom{space}\clap{5880}\phantom{space} &\phantom{space}\clap{5880}\phantom{space} &\phantom{space}\clap{5880}\phantom{space} &\phantom{space}\clap{5880}\phantom{space} &\phantom{space}\clap{150}\phantom{space} &\phantom{space}\clap{188}\phantom{space} \\ Cities &\phantom{space}\clap{93}\phantom{space} &\phantom{space}\clap{112}\phantom{space} &\phantom{space}\clap{93}\phantom{space} &\phantom{space}\clap{93}\phantom{space} &\phantom{space}\clap{93}\phantom{space} &\phantom{space}\clap{93}\phantom{space} &\phantom{space}\clap{75}\phantom{space} &\phantom{space}\clap{94}\phantom{space} \\ \bottomrule \end{tabular} } } \begin{tablenotes}[flushleft] • \emph{Notes:} * p<0.1, ** p<0.05, *** p<0.01. The table shows estimated treatment effects from log-linear specifications (see (ref)). Raw estimates are transformed to semi-elasticities: \(100\cdot(\exp(\hat{\tau})-1)\%\). Standard errors are transformed correspondingly. Col. 1 and 3--7 rely on yet-to-be-treated observations as controls. Col. 2 and 8 additionally use never-treated cities. Standard errors are in parentheses. For event-study estimates in col. 1--6, standard errors allow for clustering of the model error at the city level and are computed using the leave-out procedure recommended in borusyak2021revisiting, defining cohorts as the quarter in which scooters were launched. For the estimates in col. 7--8 standard errors are clustered at the city level. All estimates account for period fixed effects and city fixed effects. \end{tablenotes} \end{table*} Unless stated otherwise, the set of control observations consists of all pre-treatment months for cities where, as of 2021, e-scooters services were announced or introduced. We view these yet-to-be-treated cities as the most comparable counterfactual. However, the low number of yet-to-be-treated cities towards the end of the sample may be a concern that we address. Column 2 presents estimates using an extended set of control cities that includes never-treated cities where no e-scooter firm launches occurred until 2021. In this sample, the estimated treatment effect is an average increase in total accidents of \(4.7\pm2.3\%\). Since this sample is larger, it may allow for a more precise estimation of the counterfactual. However, never-treated cities may be less comparable to (eventually) treated cities. Indeed, never-treated cities in our data are regionally clustered: 15 out of the 17 never-treated cities are German cities, 9 of which are from one state (North Rhine-Westphalia). Including these cities skews the counterfactual towards North Rhine-Westphalia. In addition, most of the never-treated cities are part of a larger metropolitan areas, straddling the line between urban and suburban areas, which are less comparable to the other cities in the sample. We thus consider the estimates in column 1 more reliable. An alternative way to address the low number of control cities towards the end of the panel is to rely on yet-to-be-treated cities and shorten the time frame of the analysis by ending earlier. Re-estimating the specification from column 1 on a sample ending in 2020 yields an estimate of \(5.8\pm2.3\%\) ((ref), col. 4). (ref) provides an overview of treatment dates, which shows the remaining yet-to-be-treated cities in each period. The estimates in the first two columns can be interpreted as the average effects across all post-treatment periods. For the average treated city, the data span 18 post-treatment months. Since all city-months are weighted equally, early-launch cities (spanning up to a maximum of 38 treatment months) have a larger overall weight in the estimate in columns 1--2 than late-launch cities. This is addressed in column 3. Column 3 reports a short-run effect estimate for the first twelve months after rollout in each city. The average estimated increase in accidents within the first twelve months is smaller than the estimate in column 1, but still statistically and economically significant. On the one hand, this difference could be explained by early-adopting cities having larger effects. On the other hand, it could be that effect sizes increase with exposure. While a conclusive statement is not possible, (ref) shows that effect estimates for the second twelve-month period tend to be larger than for the first twelve-months period. First-year effect estimates for early-adopting cities are, however, marginally smaller than estimates for late-adopting cities. This may indicate that effect sizes are increasing in the medium term. But since cities with multiple years of exposure are few, this finding is only suggestive. Columns 4 and 5 of (ref) show average effects during non-winter months (March--October) and during winter months (November--February), respectively. We expect the treatment effect to be concentrated in the non-winter months, since providers tend to reduce the number of deployed e-scooters and e-scooters utilization drop considerably during winter, according to descriptive analyses and news reports mathew2019impact, obrien_2021. The estimates indicate that e-scooter services significantly increase the total number of accidents by \(11.5\pm3.5\%\) in the non-winter months (col. 4) and only by \(1.9\pm3.3\%\) in the winter months (col. 5), which is statistically indistinguishable from 0. A related pattern is observed when we look at average treatment effects by month since the city-specific e-scooter introduction. (ref) shows these estimates, for the first 18 months after the introduction and pre-treatment estimates for the 12 months before. Post-introduction months consistently indicate increased accident numbers with some apparent heterogeneity in the treatment effect over time. The fact that the effect of e-scooters on accidents temporarily drops after five months can be explained by a majority of launches occurring in spring and summer. Accordingly, for many cities, the fifth month coincides with the beginning of winter, when we expect less strong effects. Similarly, the drop around month 17 may be related to the second winter a year later. In line with this conjecture, treatment effect estimates are more stable over time if we exclude winter months from the month-level analysis ((ref)). \begin{figure}[htbp] \begin{center} \caption{Monthly treatment effects and pre-trends} \end{center} \begin{tablenotes}[flushleft] • \emph{Notes:} The figure shows average treatment effects relative to treatment introduction. In the line plot, filled dots indicate treatment effect estimates for the first 18 months relative to the introduction of e-scooter services. Circles indicate estimates for pre-treatment months. Effects after month 18 are combined into a single coefficient, because month-level estimates for long-term effects are estimated on small subsamples (few cities had e-scooters early enough for long-term effects to materialize). So, monthly estimates for later months cannot be estimated with comparable precision as for earlier months. In the right part, the average treatment effect estimate and corresponding 95%-confidence interval, across all available post-treatment city-months is shown ((ref), col. 1). Shaded areas/bars indicate the 95%-confidence interval around the estimates, based on standard errors that allow for the clustering of the model error at the city level, computed via the leave-out procedure using half-year of scooter launch as cohorts (see (ref)). All estimates account for city fixed effects and month fixed effects. \end{tablenotes} \end{figure} Estimated pre-treatment coefficients are statistically insignificant, suggesting that there was no anticipation effect and no pre-existing differential trends. Additional balance tests and a discussion of (the lack of) pre-treatment differences are in (ref), (ref), and (ref). To address possible concerns that the treatment effect estimates may be driven by developments related to the COVID-19 pandemic, (ref), column 6, shows the average effect across all months except the months with the most relevant COVID-19 countermeasures in the sample countries (March to May 2020 and November 2020 to May 2021). The average treatment effect estimate for the remaining months is \(5.7\pm2.1\%\). Column 7 and 8 use annually aggregated data and show estimates for the annual DD specification (see (ref)). This estimation sample has two groups of cities. The treatment group consists of all cities where e-scooters were launched in 2019. For column 7, the control group consists of all yet-to-be-treated cities that were not treated by July 2020. For column 8, the control group additionally includes never-treated cities, analogous to column 2. The sample of cities used for in these annual DD estimates is smaller than our main sample but allows for simpler analyses and is thus shown as a corroboration. The estimates are comparable in magnitude to the event-study estimates in columns 1-2. \subsection{Mechanisms} To investigate mechanisms, we study treatment effect heterogeneity along different traffic and road characteristics of cities. Regulations for e-scooters differ slightly across countries (e.g., Scandinavian countries legally treat the e-scooters in questions as bicycles, while Austria, Germany, and Switzerland, consider e-scooters a separate vehicle category). However, the rules regulating cycle path use are the same for e-scooters as for bicycles fersi2020. Because e-scooters share several characteristics with bicycles, including applicable traffic rules and travel speed, city characteristics associated with cyclist safety are also likely relevant to the effect of shared e-scooters on traffic accidents. There is also a `safety in numbers'-theory that could extend to e-scooter users, implying that e-scooters could be safer in cities with larger numbers of cyclists Jacobsen205. We thus use three heterogeneity variables related to cyclist safety, which were previously used in related work kraus2021provisional: (i) share of bike lanes in the total road network, (ii) the number of registered cars per capita, and (iii) the cycling modal share. The three measures provide complementary evidence as they are collected from different sources and capture constraints faced and choices made by people when choosing their mode of transportation. Infrastructure data is collected from \emph{OpenStreetMaps} OpenStreetMap, while data on registered cars comes from national administrative bodies. Modal share estimates are collected from different municipal or independent academic surveys, so they have a higher risk of being measured inconsistently.(ref) describes the data sources in detail. For each of the three dimensions, we classify cities into two groups depending on whether they fall above or below the country-specific median. We use country-specific median splits to address concerns about differential reporting standards (e.g., where cars are typically registered) and structural or cultural differences across countries (e.g., what types of cycling infrastructure are typically built). \begin{table}[htbp] \caption{Treatment effects are heterogeneous} \begin{center} { \def\sym#1{\ifmmode^{#1}\else\(^{#1}\)\fi} \begin{tabular}{l*{3}{c}} \toprule &\multicolumn{1}{c}{\begin{tabular}{c}Share of\\bike lanes\end{tabular}}&\multicolumn{1}{c}{\begin{tabular}{c}Cars per\\capita\end{tabular}}&\multicolumn{1}{c}{\begin{tabular}{c}Cycling\\modal share\end{tabular}}\\\cmidrule(lr){2-2}\cmidrule(lr){3-3}\cmidrule(lr){4-4} &\multicolumn{1}{c}{(1)} &\multicolumn{1}{c}{(2)} &\multicolumn{1}{c}{(3)} \\ \midrule %-increase for above-median cities& 0.2 & 10.1***& 9.6** \\ & (2.7) & (4.1) & (4.7) \\ \addlinespace %-increase for below-median cities& 11.5***& 4.7* & 7.3***\\ & (3.9) & (2.6) & (2.6) \\ \midrule \(p\)-value \(H_o\): coefficients identical& 0.018 & 0.256 & 0.658 \\ Cities & 93 & 93 & 93 \\ Observations & 5880 & 5880 & 5880 \\ \bottomrule \end{tabular} } \end{center} \begin{tablenotes}[flushleft] • \emph{Notes:} * p<0.1, ** p<0.05, *** p<0.01. (ref) shows estimated treatment effects from log-linear specifications (see (ref)). Standard errors in parentheses. In addition to city fixed effects and month fixed effects, regressions control for interaction fixed effects between month and the median-split indicator. Raw estimates are transformed to semi-elasticities: \(100\cdot(\exp(\hat{\tau})-1)\%\). The table illustrates the average effect estimates for different subsamples, defined by sample splits using the country-level medians of different city characteristics shown in the table header. Standard errors allow for clustering of the model error at the city level and are computed using the leave-out procedure recommended in borusyak2021revisiting, defining cohorts as the half-year in which scooters were launched. Tests for coefficients differences are described in (ref). \end{tablenotes} \end{table} (ref) shows separate treatment effect estimates for the groups defined by each variable's country-specific median split. These estimates should not be interpreted as causal effects of the heterogeneity variables themselves, but rather as estimates of the group-specific treatment effect of introducing e-scooters. While the effect of shared e-scooters on accidents in each subsample is identified under the same assumptions as our main effect, the differences in effects between subsamples are not necessarily caused by these heterogeneity variables. Other variables that are correlated with the heterogeneity variables, such as cities' road conditions, average vehicle speeds, speed limits, or income levels, could drive the observed heterogeneity in treatment effects. Estimates in column 1 imply that e-scooters only had a small and statistically insignificant effect on total accidents in cities with an above-median density of bike lanes. In contrast, the implied effect for cities with a below-median density of bike lanes is large and highly significant, \(11.5\pm3.9\%\). The difference between the coefficients is highly significant (\(p\)-value=0.018). These results are in line with findings summarized in a recent literature survey reynolds2009impact, suggesting that purpose-built bicycle-specific infrastructure can reduce traffic accidents. The results in column 2 indicate that cities with an above-median density of registered cars experienced a comparatively large treatment effect of \(10.1\pm4.1\%\), while cities with a below-median density of registered cars experienced an estimated increase of \(4.7\pm2.6\%\). When splitting the sample of cities by their cycling modal share, the two groups have numerically similar and statistically indistinguishable (\(p\)-value=0.658) estimated effects. So we find no evidence for the `safety in numbers'-theory for shared e-scooters. The heterogeneity results are similar in the annual DD specification, where we find a similarly large but insignificant difference based on bike lanes and a large and significant difference for cars per capita ((ref)). \subsection{Endogeneity, robustness checks, and placebo tests} The rollout of scooter services is not random. There are a number of factors that are predictive of market entry. These factors can be relatively time-invariant city characteristics, such as population size, and infrastructure or they can be time-varying, such as season, regulatory constraints, and economic or technological developments. The factors that we identify as drivers of e-scooter launches are either unlikely to cause changes in accidents themselves or are controlled for through the fixed effects in our specifications. We provide a discussion of these factors in this section and in (ref). A threat to the identification of causal effects would be if the city-level timing of launches was correlated with changing trends in accidents, or the reporting and coding of accidents. Accordingly, a key identifying assumption of our empirical strategy is the parallel trend assumption, i.e., total traffic accidents in treatment and control cities would have followed a common trend in the absence of e-scooter services. While this assumption cannot be directly tested, it is more plausible if trends between treated and control cities are similar before the introduction of shared e-scooter services. The estimated pre-trend coefficients are insignificant and close to zero (see (ref)). As an additional test, we test if past trends in accidents predict the launch of e-scooter services. We regress a city-month level indicator for the launch of e-scooter services on the 12-month difference in log-accidents ((ref)) and find no evidence that e-scooter launches are predicted by increases or decreases in accidents. Lastly, placebo tests (discussed below) further substantiate the point that seasonality in accidents or differential trends are not driving our results. As additional support that endogenous timing of treatment is not driving our findings, we conduct instrumental variable analyses. For this, we use the interactions of four time-invariant city characteristics (population and the three variables used in the heterogeneity analyses above, see (ref)) and the number of e-scooter firms that were active in a given month in other cities of the same country as instruments. This analysis, which is carried out in a standard two-way fixed-effects framework---and is thus subject to the discussed caveats related to staggered rollout designs---is discussed and presented in (ref). Furthermore, we estimate a synthetic DD model arkhangelsky2021synthetic, which slightly relaxes the parallel trends assumption, as an additional robustness check. Our results are qualitatively robust. Details on the synthetic DD are in (ref). More robustness checks and discussions are provided in (ref). In particular, we provide a detailed discussion of issues arising from the heterogeneous treatment timing in our setting and estimation results for a Poisson model and ordinary least squares (OLS) in a standard (likely biased) TWFE estimation ((ref)). The average effects of shared e-scooter introduction estimated in a standard TWFE DD are qualitatively robust but slightly smaller, as expected. \subsubsection*{Placebo tests on winter-time accidents and placebo launch dates} We conduct two types of placebo tests to corroborate our results. First, we use winter-time accidents as a sub-group of accidents that would likely show significant estimates, if our estimates were capturing differential general trends in urban traffic policies or behaviors. E-scooters are a considerably less attractive transportation mode in cold weather and companies tend to reduce the number of deployed scooters mathew2019impact, obrien_2021. Therefore, shared e-scooters likely cause fewer accidents in winter. Consequently, the winter specification in column 5 of (ref) can be interpreted as a placebo test. Treatment effects are large and significant in summer months, but smaller and insignificant in winter months. If our results were driven by differential trends in traffic risks related to non-seasonal factors (e.g., car-specific road infrastructure, general policy changes, or changes in the recording and reporting standards) the estimates would be less likely to exhibit this seasonality. Second, we redo our estimation from (ref) with placebo launch dates, shifted by 12 and 24 months to the past from the actual city-specific launch dates. If results were driven by non-parallel trends or by seasonality that is not fully captured by the fixed effects, these placebo tests could also indicate significant estimates. The results are shown in (ref) and indicate no discernible patterns, which we view as reaffirming evidence that the parallel trend assumption is justified and that our empirical strategy sufficiently accounts for seasonality. \section{Discussion} We provide evidence that the rollout of shared e-scooter services in large cities led to a significant increase in traffic accidents involving personal injuries. In their 2018 road safety report, the oecd2018 reports that the estimated socio-economic costs of road traffic accidents exceed €500bn for EU member states alone, which is equivalent to around 3% of the EU's GDP. In 2019, an average traffic accident involving personal injuries in Germany was associated with economic costs of around €61,000, including costs of €16,301 for damage to property and €44,778 for personal injuries bast2021accident,bast2021cost.\footnote{According to the German federal research institute, bast2021cost, 300,143 traffic accidents involving personal injuries were recorded in Germany in 2019. The total personal damage costs amounted to €13.44bn, which implies average personal damage costs of around €44,778 per accident involving personal injuries.} Assuming these costs per accident apply to all six sample countries, the estimated effect in our main specification (\(8.2\pm2.9\%\)) would thus imply additional socio-economic costs of around €466,186 per month and €5.6m per year for the average sample city with 93.2 monthly accidents before treatment (see (ref)).\footnote{The true costs may be higher, as Germany does not account for under-reporting in cost calculations wijnen2017crash, or lower as the cost estimates also include non-urban traffic accidents.} In addition, a recent study conducted at the University Hospital of Essen in Germany meyer2022scooter suggests that a large share of hospital-treated e-scooter injuries are not reported to the police. By focusing on police-reported accidents our data is more likely to record accidents involving automobiles than accidents involving cyclists and includes relatively more accidents with severe injuries and larger costs Langley376. Findings from retrospective studies examining medical records further show that e-scooter-related accidents are often associated with serious injuries to the head and upper extremities with a substantial proportion of major trauma injuries trivedi2019craniofacial, trivedi2019injuries, badeau2019emergency, moftakhar2021incidence, lavoie2021characterization. In sum, these findings imply that our estimated effects are associated with significant socio-economic costs that have to be weighed against potential benefits from adding shared e-scooter services to the urban transportation landscape. Our main results do not differentiate by severity of injuries. Four countries report the number of accidents involving severe or slight personal injuries and death. Austria and Norway instead disaggregate the number of victims by injury severity. We do not suspect that e-scooter-related accidents are considerably less severe than other urban accidents for four reasons. First, the clinical studies discussed above suggest that police-reported accidents directly involving e-scooters often involve severe injuries. Second, police-reported accidents indirectly caused by e-scooters are likely similar to pre-existing urban accidents. Third, in the appendix we report estimates of treatment effects on accident severity. For this we use the percentage of accidents involving only slight injury as an outcome variable. For Austria and Norway we infer the percentage of slight-injury accidents from the percentage of slight-injury victims. We find that 85% of accidents involving personal injuries are classified as involving slight injuries and that there is no significant change after the introduction of e-scooters (95% confidence interval: \(-1.8\) to \(+0.8\)%-points, details in (ref)). Estimated effects are considerably larger in cities that have poor separated cycling infrastructure and rely more on cars. This is important from an urban planning policy perspective, especially given that earlier studies suggest that better bicycle infrastructure may be associated with more frequent and longer e-scooter trips caspi2020spatial, laa2020survey. Paired with our findings this suggest that improving separated infrastructure may curb negative effects, while simultaneously encouraging e-scooter usage. As highlighted in the results section, the effects of infrastructure are not causally identified. Investigating what additional measures those cities that have well-developed infrastructure are taking to prevent accidents is worth additional study. Our analyses focus on the extensive margin of treatment, i.e., whether or not shared e-scooters are available in a city at all. This is the most relevant dimension for two reasons. First, while there are examples of cities that restricted the maximum number of e-scooters (e.g. Bern, Switzerland; Innsbruck, Austria), the public debate usually revolves around the extensive margin, i.e., whether to ban shared e-scooters from a city's transportation mix or not cnn_ban. Second, the extensive margin analysis allows for an easy interpretation as a semi-elasticity and is less likely to be subject to measurement error and endogeneity issues. Even if exact data on the number of deployed e-scooters were available, e-scooter firms may continuously adapt to accidents and changing traffic conditions, raising concerns about reverse causality. Extensive margin estimates, on the other hand, identify a net effect that includes possible endogenous scaling decisions of suppliers. Our findings should not be interpreted as long-run effects. Effects on traffic accidents may decrease in the future due to safer vehicles, greater experience of users of e-scooters, or changes in the behavior of other traffic participants. They may also increase. While our analyses account for substitution effects between modes of transportation, including walking (police are required to report pedestrian-vehicle accidents), we do not observe the total number of trips within a city. If the introduction of shared e-scooters considerably increases the mobility of citizens in treated cities, i.e., people travel more because e-scooters are available, the social costs, implied by documented effects, should be discounted by the higher number of trips in a cost-benefit analysis. A recent survey of e-scooter users in Paris, however, suggests that the vast majority did not increase their total mobility christoforou2021using. Our analysis does not imply a comparative statement of the safety risks between different modes of transport and is agnostic to what kind of road user is responsible for the increased accidents. Consequently, our results cannot be interpreted as recommendations against the inclusion of shared e-scooters in urban transport landscapes, in particular, compared to automobiles that, due to their size and speed, likely pose the relatively largest urban safety risk. For instance, past studies find that cars and other large motorized vehicles contribute to other road users' deaths at rates 3--6 times higher than bicycles per mile driven aldred2021does, scholes2018fatality. \printbibliography