Provisional COVID-19 infrastructure induces large, rapid increases in cycling [original]

SUSTAINABILITY

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Provisional COVID-19 infrastructure induces large,

rapid increases in cycling

Sebastian Krausa,b,1 and Nicolas Kocha,c

aMercator Research Institute on Global Commons and Climate Change, 10829 Berlin, Germany; bDepartment Economics of Climate Change, Technical

University of Berlin, 10623 Berlin, Germany; and cPotsdam Institute for Climate Impact Research, 14473 Potsdam, Germany

Edited by Susan Hanson, Clark University, Worcester, MA, and approved February 18, 2021 (received for review November 26, 2020)

The bicycle is a low-cost means of transport linked to low risk

of transmission of infectious disease. During the COVID-19 crisis,

governments have therefore incentivized cycling by provision-

ally redistributing street space. We evaluate the impact of this

new bicycle infrastructure on cycling traffic using a generalized

difference in differences design. We scrape daily bicycle counts

from 736 bicycle counters in 106 European cities. We combine

these with data on announced and completed pop-up bike lane

road work projects. Within 4 mo, an average of 11.5 km of

provisional pop-up bike lanes have been built per city and the

policy has increased cycling between 11 and 48% on average.

We calculate that the new infrastructure will generate between

$1 and $7 billion in health benefits per year if cycling habits

are sticky.

urban planning |active travel |generalized difference in differences

The COVID-19 crisis has led to important changes in trans-

port behavior in 2020 (1). Early evidence points to shifts from

public transport to car use as users have reacted to the pandemic

(2). Governments have incentivized cycling as a low-cost, sustain-

able, equitable, and space-saving mode of transport that reduces

the risk of COVID-19 transmission. A key measure has been

the redistribution of street space in cities to create provisional

bike infrastructure typically marked and protected by materi-

als readily available from road construction companies. As of

July 8, 2020, 2,000 km of these infrastructure changes had been

announced in European cities (3).

Transport mode choices are influenced by a variety of behav-

ioral effects that make people stick to their habits, such as status

quo bias, default effects, and time-inconsistent preferences (4).

This complicates the task of policymakers to encourage people to

cycle, particularly in the short run. However, major disruptions

to public transport, such as strikes, cause people to reconsider

their habits (5) and the provision of dedicated infrastructure

has been identified as an important means to increase cycling

(6). Thus, the fast provision of new bike infrastructure dur-

ing the COVID-19 pandemic is a suitable policy experiment

to investigate the responsiveness of cycling under conducive

conditions.

Here, we estimate the causal effect of the post-COVID-19

lockdown rollout of provisional (“pop-up”) bike lanes in Euro-

pean cities. We compile new data on daily bike counts in 106

cities. We connect to the open data application programming

interfaces (APIs) of these cities to download bike counts from

a total of 736 counters. We combine these data with information

on day-to-day kilometer changes in pop-up cycling infrastructure

(Fig. 1).

The spatial placement of pop-up bike lanes has mainly been

driven by the availability of street space that could be redis-

tributed without restricting car traffic to one direction and

the existence of “shovel-ready” construction plans. The exact

timing of pop-up bike lane construction is driven by admin-

istrative idiosyncrasies and the availability and schedules of

construction firms. Therefore, the timing of the pop-up bike lane

rollout has been as good as random. This quasi-experimental

setting allows us to address the important concerns that bike

lanes could be built as a reaction to increased cycling traffic

(reverse causality) or that both the implementation of bike lanes

and bicycle counts could be driven by a third factor, such as

local “green” preferences, that cannot be measured (omitted

variable bias).

Results

We use panel regressions to compare bike traffic in treated cities

before and after they get treated with control cities. We find that

pop-up bike lanes have led to substantial increases in cycling.

This effect is robustly visible in comparisons over both a longer

and a shorter time span. First, in Fig. 2 we show the effect

comparing treated and control cities over several months before

and after treatment. Second, in Fig. 3 we provide estimates

from a range of more conservative specifications identifying the

effect based on daily variation within a narrow time window in

the same city.

The outcome in all our regressions is modeled as the natu-

ral logarithm of the cycling count. We use daily variation in this

variable either at the counter or at the city level. Our coefficients

can be interpreted as the average change in cycling caused by the

pop-up bike lane program.

Standard Difference in Differences. Fig. 2 shows the dynamic treat-

ment effect of the pop-up bike lane program. For the analysis

shown here, we define March 2020 as the time of treatment and

plot the estimated differences between treated and control cities

over time. Since we expect cycling to increase in both treated and

Significance

Active travel makes people healthier and creates a wide

range of additional social and environmental benefits. The

provision of dedicated infrastructure is considered a crucial

policy to increase cycling. However, evaluating the impact

of this type of intervention is difficult because infrastructure

changes are typically slow. The rollout of so-called pop-up

bike lanes during the COVID-19 pandemic is a unique empirical

context to estimate the pull effect of new cycling infrastruc-

ture. We show that the policy has worked. We find large

increases in cycling. This result is robust for a variety of

empirical counterfactuals. Further research is needed to inves-

tigate whether this change is persistent and whether similar

results can be achieved in situations outside the context

of a pandemic.

Author contributions: S.K. and N.K. designed research; S.K. analyzed data; and S.K. and

N.K. wrote the paper.y

The authors declare no competing interest.y

This article is a PNAS Direct Submission.y

This open access article is distributed under Creative Commons Attribution-NonCommercial-

NoDerivatives License 4.0 (CC BY-NC-ND).y

1To whom correspondence may be addressed. Email: [email protected].y

This article contains supporting information online at https://www.pnas.org/lookup/suppl/

doi:10.1073/pnas.2024399118/-/DCSupplemental.y

Published March 29, 2021.

PNAS 2021 Vol. 118 No. 15 e2024399118 https://doi.org/10.1073/pnas.2024399118 |1 of 6

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FRHU

Apr

May

Jun

Jul

Wien

Stuttgart

Köln

Düsseldorf

Berlin

Lahti

Tours

Strasbourg

Rouen

Rennes

Paris

Nantes

Lyon

Grenoble

Chambéry

Caen

Avignon

Budapest

Dublin

Gdańsk

Fig. 1. Treated cities and their treatment intensities in terms of imple-

mented kilometers of public bike lanes in service (cumulative) on a given

day between March and July 2020. Cities used in the estimation sample for

Fig. 3 are marked in boldface type. Control cities are plotted in SI Appendix,

Fig. S2. London, Milan, Rome, and Lisbon are missing from the sample due

to a lack of daily bicycle counter data. Data are from the European Cyclists’

Federation (3).

control cities as a reaction to COVID-19, we take the difference

between the cycling increase in treated and in control cities as

our estimate of the average effect of the program. This differ-

ence in differences approach suggests an increase in cycling of

41.6% induced on average by the policy. A crucial assumption

for this research design is that cycling would have evolved on a

parallel trend in the treatment and control group in the absence

of treatment. This is called the common trends assumption. Since

we model the outcome as the natural logarithm of cycling counts,

we make the assumption that cycling would have grown at the

same rate in the treatment and in the control group.

Fig. 2 allows us to verify this assumption. The treatment effect

becomes apparent after the treatment sets in. Before, treat-

ment and control groups have been on the same trend. There

is a slight, albeit statistically insignificant downward trend before

treatment, hinting at the possibility of stronger mobility reduc-

tions due to COVID-19 in cities that have decided to build

pop-up bike lanes. This could for instance be the case because

local and national governments are more likely to take wide-

ranging action if their country is hit by a more intense outbreak.

It could also be due to governments acting upon stronger risk

aversion of their local populations toward cycling in the context

of emptier roads and increased speeding during the lockdown.

We mitigate some of these potential selection into treatment

effects by controlling for COVID-19–related dynamics with fixed

effects at the country–day level. This removes the effect of daily

national-level policy changes, such as lockdowns.

A remaining concern is that bike lanes could have been built

as a reaction to locally increased cycling traffic (reverse causality)

or that both the implementation of bike lanes and bicycle counts

could be driven by an unaccounted third factor (omitted variable

bias). We address these potential biases with regressions focus-

ing on changes over a shorter time span as discussed in the next

section.

Generalized Difference in Differences. In our second set of specifi-

cations (Fig. 3) we investigate more focused comparisons using

both variation in the timing of treatment between cities and vari-

ation in the treatment dose, i.e., the number of kilometers of

pop-up bike lane in service on a given day. With these specifi-

cations we robustify the more simple difference in differences

design by using additional fixed effects and by including con-

trol variables for the weather, for changes in overall mobility

and public transport, and for the number of active bike counters

in a city. Crucially, we look at the effects of pop-up bike lanes

in a shorter time span to investigate potential reverse causality

between cycling and the implementation of pop-up bike lanes.

Although pop-up bike lanes tend to be based on preexisting plans

by city planners or civil society organizations and could therefore

be implemented comparatively quickly, the erection of a bike

lane needs at least a few days’ notice and the exact timing of

these road works depends on the availability and the schedule of

construction firms. This has been confirmed in our conversations

with local policymakers in Berlin and Paris. Our preferred spec-

ifications (Eq. 1) are therefore based on comparisons of cycling

counts on the days before and after a change in the treatment

intensity (marked in blue). These comparisons are created by the

Fig. 2. Treatment effect (difference between treated and control cities) in months before and after the beginning of the pop-up bike lane policy. Obser-

vations are binned into months. Treatment for this plot is hard coded to March 2020 and the baseline category and the beginning of the sample are set to

February 2019. Estimates are from Poisson regressions that include city and country–day fixed effects (SI Appendix, Eq. S1). The shaded area shows the 95%

confidence interval. Data for the outcome variable are from the European Cyclists’ Federation (3) and data for the treatment variable are from municipal

bike counters (Materials and Methods).

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SUSTAINABILITY

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Model:

Treatment definition:

Control group:

Controls:

Poisson

OLS

Binary

KM per sqkm

KM per capita

City level

Treated only

To be treated

Counter FE

City FE

City−week FE

City−calendar week FE

Day FE

Country−day FE

Transit control

% change in cycling

Fig. 3. Estimates of the average effect of pop-up bike lanes on cycling.

Dose–response regressions (in kilometers, kilometers per capita, or kilome-

ters per square kilometer in service on a given day) are multiplied by the

average treatment dose. The 90 and 95% confidence intervals are shown in

darker and lighter color. The unit of observation is the bike counter except

for regressions at the city level. Preferred specifications are marked in blue

(Eq. 1) and are reported in more detail in SI Appendix, Table S5. Gray (and

blue) indicators (Bottom) indicate the type of specification. Three estimates

are from OLS specifications and therefore use the natural logarithm of the

bicycle count as the outcome. All other specifications are Poisson regressions

using the level of the count. Data for the outcome are from the European

Cyclists’ Federation (3) and data for the treatment are from municipal bike

counters (Materials and Methods). All regressions include controls for the

number of active counters in a city on a given day and for the weather (tem-

perature, sunshine, wind, precipitation) (7). All regressions, except those

that rely on observations before 2020, include a control for overall mobility

(8). The transit control is from Apple routing requests (2020 only) (1). Code

is from ref. 9.

inclusion of city–week fixed effect. This fixed effect ensures that

our estimates are based on variation within the same city within

the same week. If the exact (i.e., day-level) timing of the rollout

of pop-up bike lanes has been as good as random, estimates from

these specification are not driven by reverse causality.

Our unit of observation in most regressions is the cycling

counter. This allows us to control for within-city differences

despite doing a cross-city study. We do this by including a counter

fixed effect that flexibly controls for any local confounders that

are time invariant within the time frame of the variation used

in the analysis. We thereby control for the density of public

transport stops, population density, and topography, but also for

additional, unobservable dimensions, such as social capital and

local preferences for green lifestyles, at a high spatial resolution

within the city. With the counter fixed effect we also rule out

that our result is driven by new counters that get placed next to

pop-up bike lanes. We assign treatment to each counter based on

its city, since we measure daily changes in the pop-up bike lane

network at that level. We investigate the effect of this source of

measurement error by defining the treatment dose either as a

binary variable or in terms of kilometers, kilometers per capita,

and kilometers per square kilometer of city area. We find that

measuring the dose–response in terms of kilometers attenuates

the effect (7.6%). This indicates that the effect is not exclusively

driven by the announcement effect of new infrastructure in a city,

but by the de facto availability of new infrastructure in the neigh-

borhood surrounding a counter, which is better approximated by

a measure in per capita or per area terms (estimates of 23.3 and

30.2%, respectively). Remaining measurement error due to some

counters being closer to or farther from new infrastructure than

the rest of the sample is unlikely to be systematic conditional on

fixed effects and control variables (detailed discussion of mea-

surement error in SI Appendix). We also run specifications for

which we take the mean of all counters in a city (marked as city

level in Fig. 3) to show that the effect is not driven by our use of

the counter as the unit of observation.

We use a variable capturing transit routing searches on Apple

maps (1) to control for omitted variable bias that could be

present if changes in public transport affect both pop-up bike

lane construction and cycling. In our preferred specification this

could still be the case, if daily changes in the provision or in the

use of public transport in a city led to new pop-up infrastruc-

ture within the same week. Public officials may for instance have

tried to schedule the erection of pop-up bike lanes for the same

day as planned public transport disruptions. The transit control

removes this potential remaining bias. Since the Apple data are

available only for a subset of larger cities in our sample (marked

in boldface type in Fig. 1), we run our main regressions (Fig. 3)

on this smaller sample. SI Appendix, Table S4 shows robustness

to lifting this sample restriction and to excluding Paris, which has

had the strongest treatment, from the analysis.

We control for subnational changes in policies and behaviors

related to COVID-19 with a variable that captures overall human

mobility based on Facebook user movements. We control for the

number of counters active in a city on a given day to account

for unusual traffic situations, for instance when a counter gets

shut down because of road works. We also include control vari-

ables for daily total precipitation and mean wind, temperature,

and sunshine to address the concern that both the scheduling of

pop-up bike lane construction work and daily variation in cycling

could have been driven by weather conditions.

We check the sensitivity of our results to changing the time

span of our identifying variation and to reshaping our treatment

and control group definitions (additional specifications in Fig.

3). The effect is robust to including days from the same calen-

dar week in previous years in these comparisons rather than days

from 2020 only. We also provide estimates for the effects of the

policy based on comparisons between 1) treated and untreated

cities, 2) treated cities using only their variation in treatment

timing, 3) cities that are already treated and those that have

announced only pop-up bike lanes, and 4) treated cities only

using their variation in treatment dose and treatment timing.

Heterogeneity Analysis. We investigate how the treatment effect

of pop-up bike lanes varies depending on relevant features of

the cities in our sample (Table 1). These heterogeneous effects

should not be interpreted causally, since we cannot control

for additional omitted variable bias or reverse causality cre-

ated by the inclusion of these variables in our model. We find

that the effect of pop-up bike lanes is stronger in cities with a

higher population density [1] and a higher modal share of public

transport in commutes [2], which are correlates of a built envi-

ronment favoring active travel. The treatment effect is lower

for cities with faster average speeds of car commutes [6] and

for cities with more road death per capita [7]. It is also lower

for cities with more cars per capita [5]. However, this estimate

is imprecise. These heterogeneities confirm research that found

that US cities with better safety, low car ownership, and more

density have more cycling (10, 11).

Our analysis also shows that the baseline length of the bike

lane network per capita [3] is correlated with a lower treatment

effect. We interpret this as an indication that the pop-up bike

lane effect is a phenomenon of catch-up growth in cities with

a high cycling potential that was previously impeded by missing

infrastructure. The effect of baseline cycling modal shares [4] is,

however, statistically unclear.

Further research could also look at the effect of pop-up bike

lanes in terms of improvements in bike lane network connectivity

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Table 1. Heterogeneous treatment effects of the pop-up bike lane rollout

×baseline (natural log) of

[1] [2] [3] [4] [5] [6] [7]

Population PT modal Bike lanes Cycling modal Cars Car commute Road deaths

density share per capita share per capita speeds per capita

Pop-up treatment 0.221* 0.258*** −0.194* 0.093 −0.592 −0.509** −0.351***

(0.121) (0.100) (0.115) (0.082) (0.485) (0.233) (0.058)

N 59,521 27,486 24,611 27,486 34,408 26,886 34,922

Estimates are based on the interaction term of the treatment variable (in kilometers per city area) and the natural logarithm of the heterogeneity

variables (column names). Coefficients are scaled to the average treatment dose in our sample. They can be interpreted as the unit change in cycling if a

heterogeneity variable is one unit higher (when assuming treatment with an average pop-up bike lane program). All regressions include counter, city–week,

and country–day fixed effects. They also include weather controls (7), a control for overall mobility (8), and a control for the number of counters active in a

city on a given day. Data for the outcome variable are from the European Cyclists’ Federation (3) and data for the treatment variable are from municipal bike

counters (Materials and Methods). All heterogeneity variables except for bike lanes per capita (17) are from the European Urban Audit (18, 19). Standard

errors clustered at the city level are reported in parentheses. Significance levels are *P<0.1, **P<0.05, ***P<0.01.

and directness as proposed by ref. 12 and other more complex

measures of a bike lane network, such as the level of protec-

tion of a bike lane and the treatment of intersections (13). In

this context it is important to investigate how underserved com-

munities can be provided with a pop-up bike lane network that

is complete and inclusive and how additional political, cultural,

and economic barriers to cycling for low-income and minority

groups can be removed (14). Bike sharing can support changes

in modal choice (15), but important barriers to adoption remain

for underrepresented groups (16). We therefore think it would

be valuable to investigate interactions between the pop-up bike

lane policy and time series data on bike sharing policies including

changes in pricing and the availability of bikes and stations.

Discussion

We find robust evidence for substantial short-run increases

in cycling in European cities due to new provisional cycling

infrastructure. Independent of its potential impacts in reducing

COVID-19 transmission, the net benefits of the intervention are

likely to be large. The direct cost of cycling infrastructure is low.

At the higher end, 1 km of bike lane in Sevilla has previously

cost e250,000 (20). However, Berlin’s approach of iterative plan-

ning with provisional infrastructure during the pandemic has for

instance reduced costs to e9,500/km as of July 2020 (21). These

costs are small compared to the substantial health benefits from

the new infrastructure. Previous research has found that every

kilometer of cycling generates health benefits of $0.45 (22). As

a complementary and more stylized analysis, we combine this

estimate from the literature with our econometric estimates of

policy-induced cycling increases to provide a projection of health

benefits generated by pop-up bike lane programs. We calcu-

late baseline values for total cycling in a city based on data on

daily kilometers cycled in German cities in 2018 and extrapo-

late these numbers to the other European cities in our sample

based on city-level data on transport and population (Materials

and Methods). This extrapolation is approximate but sufficient

to calculate a range of potential health benefits. Based on our

regression-based estimate for the 95% confidence interval of

the “treatment dose” in terms of kilometers per square kilo-

meter, we project that the additional cycling induced by the

pop-up bike lane treatment during its first months of operation

has generated between $0.5 and $1.7 billion in health benefits.

Thus, the new infrastructure may generate between $2.2 and $6.9

billion/y in health benefits if the new bike lanes become perma-

nent and make cycling habits stick. We project this range to be

between $1.2 and $3.5 in annual health benefits if we use our

alternative estimate for the 95% confidence interval of the pol-

icy effect based on the “treatment dose” in terms of kilometers

per capita.

The magnitude of our estimate is large compared to previous

evaluations of new cycling infrastructure improvements that have

found statistically unclear or modest effects, typically because

of the limited scale of the interventions (23–25). Our estimate

implies a higher responsiveness of cycling to new infrastructure

than the associations found in cross-sections of US cities (10, 26).

However, in cities in Europe (17) and the United Kingdom (27)

additional infrastructure is associated with more cycling than in

the United States. The case of Sevilla has shown that in a dense

city with a high share of narrow, cycling-friendly roads the con-

struction of bike lanes on major roads can create substantial

cycling growth: 120 km of new bike lanes have led there to a

fivefold increase of cycling between 2006 and 2011 (20). Simi-

larly, pop-up bike lanes have often been placed on main roads.

Thereby they have removed important bottlenecks for cyclists

and generated important improvements for the overall cycling

network. Many of the cities in our sample are fundamentally well

suited for cycling. For instance, they are often dense and have a

high share of side roads with slow car speeds. Therefore, they

can be assumed to have a high potential for catch-up growth,

which is one explanation for our larger effect estimate. In addi-

tion, the pandemic has led to a reshuffling of otherwise rather

inelastic mobility choices and thus created the conditions for new

infrastructure to induce shifts to active travel. However, this also

means that our results cannot be directly generalized to other

settings. Given this limitation in terms of external validity, we

caution against an overinterpretation of our estimates as pro-

viding a benchmark value for increases in cycling that planners

should expect from an additional kilometer of bike infrastruc-

ture. It remains to be evaluated whether the new bicycle use is

sticky and how similar treatments influence behavior outside of

the context of a pandemic.

Surveys indicate that separated, protected infrastructure is a

key element to incentivize uptake of cycling (28–30). Cities have

experimented with different measures to create new spaces for

cycling, ranging from painted to provisionally protected bike lanes

and from traffic calming with signs to built “modal filters” that

prevent the passage of cars. Our data on pop-up infrastructure do

not allow us to systematically distinguish between these types of

interventions and the quality of their implementation.∗Further

research should investigate which types of infrastructure have

more successfully increased cycling by previously underrepre-

sented groups, such as women, older people, and children.

*In SI Appendix, Table S3 we show that the results are robust to specifying treatment in

terms of 1) the total length of all types of infrastructure, 2) the total length of measures

clearly marked as bike lanes in the data, 3) the number of measures, and 4) a binary

indicator for treatment.

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Materials and Methods

Bicycle Counter Data. We connect to municipal Open Data Portals to obtain

daily bicycle counts from bike counters in large- and medium-sized cities

in 20 European countries. The raw data and code to download counter

data are included in our code package (31). The outcome is modeled as the

natural logarithm of cycling counts. This means that we investigate percent-

age changes rather than absolute increases in the number of cyclists. Our

outcome varies daily at the counter level (summary statistics and cleaning

procedures in SI Appendix).

Bike Lane Data. The data on planned and completed pop-up infrastructure

projects have been collected and crowdsourced by the European Cyclists’

Federation based on technical reports and media announcements. A visual-

ization of the data can be accessed at https://ecf.com/dashboard. We merge

these data with city polygons from the European Urban Audit 2020 (32) to

generate a cumulative measure for the total number of pop-up bike lanes

in service in a city on a given day (summary statistics and cleaning proce-

dures in SI Appendix). We generate a range of treatment variables (binary,

kilometers built, kilometers per capita, kilometers per square kilometer of

city area) and assign this treatment to counters based on their city polygon.

Control Variables. Using fixed effects in our regressions, we remove and

therefore control for time-invariant differences between cities and between

the locations of the individual counters in our data. Therefore, any addi-

tional time-invariant control variables at the city and the counter level

would be redundant in our analysis. We also use fixed effects interacting

different spatial levels with time dimensions, thereby controlling for many

time-varying observable and unobservable factors. We use additional con-

trols to rule out any bias that may be introduced by time-varying factors

below our fixed effect levels.

We control for daily changes in public transport supply and demand with

the transit variable from the Apple COVID-19 Mobility Trends Reports (1).

This variable captures daily variations in the number of requests for pub-

lic transport directions on Apple Maps. We access these data using the

covmobility package (33).

We capture average human mobility throughout the phase of the COVID-

19 pandemic starting in March with a human mobility index based on

Facebook data (8). The index is from a dataset called “movement range

maps” that Facebook shares after aggregating individual user movements

for humanitarian and research purposes with a reference to the principles

outlined by epidemiologists and public health researchers (34). It measures

the number of daily 600-m grid cells visited by Facebook users compared to

a baseline in February. For most of our sample the index is aggregated to

the state level, where we use the data. On average, in our sample period

daily mobility has been below the February baseline.

We use weather data from the ERA5 climate model that generates hourly

measures of surface temperature, ultraviolet (UV) radiation, precipitation,

and wind at a 0.25◦×0.25◦resolution (7). We use the ecwmfr package (35)

to aggregate this to the European Union Urban Audit city polygons (32) at

the daily level.

Heterogeneity Variables. We analyze heterogeneous treatment effects

along seven city-level variables. Bike lanes per capita measures the length

of the bike lane network in a city based on Open Street Map data (17, 36).

Population density is from the European Urban Audit (19). Public transport

(PT) modal share, cycling modal share, cars per capita, car commute speeds,

and road deaths per capita are based on city transport statistics from Euro-

stat (18). We use the natural logarithm of these variables to obtain the unit

change in cycling for a unit change in the respective heterogeneity variable.

Empirical Strategy. We estimate a panel regression model at the counter

level with daily counts of cyclists as the outcome variable and the number of

kilometers (kilometers, kilometers per capita, or kilometers per square kilo-

meter of city area) of pop-up bike lanes in service in a city on a given day

as the treatment. This regression analysis forms comparisons between treat-

ment and control groups before and after treatment for each cohort of new

bike lanes and for different treatment intensities (generalized difference

in differences). This separates the effect of pop-up bike lanes from over-

all changes in cycling due to COVID-19. We use a set of indicator variables

(fixed effects) that remove remaining variation from our estimation sample

that would otherwise bias our estimates. Our study design thus allows for

systematic differences in the level of bike traffic between treatment and

control groups, but relies on a common trends assumption, that bike traffic

in treated and control cities would have evolved on a parallel trend in the

absence of treatment. We cannot observe treated units in their untreated

state after treatment (potential outcome). However, we can investigate

pretreatment trends between treated and control cities and check the sen-

sitivity of our estimates to changes in the control group definition, i.e., in

the way we construct the empirical counterfactual (Fig. 3).

In our preferred specification we model the relationship between cycling

traffic and the pop-up bike lane treatment as

ln Countid =βBike Lanescd +Xcd +λi+σcw +ϕnd +εid [1]

where iindexes a counter, ca city, na country, da day, and wa week.

λiis a counter fixed effect that controls for time-invariant factors at

a high spatial resolution. σcw is a city–week fixed effect that controls for

week-specific time-varying factors, thereby restricting identifying variation

to days before and after treatment within the same week in the same city.

ϕnd is a country–day fixed effect that captures any daily changes common

to all cities in a country.

We cannot include fixed effects for factors that vary at the city level over

time, such as local mobility or weather, since this is the geographical level

at which our treatment is measured. Xcd is a vector of control variables

that account for these factors. It includes an index for public transport use

from Apple (1), an index for overall mobility based on Facebook data (8),

weather variables (temperature, UV radiation, wind, precipitation) (7), and

the number of counters per city active on a given day.

The coefficient of interest is β. It captures the effect of the pop-up bike

lane treatment on bicycle counts. Our treatment variable is defined either as

a binary indicator for treatment or as the number of kilometers (kilometers,

kilometers per capita, or kilometers per square kilometer of city area) of

pop-up bike lanes in service on a given day.

Figs. 2 and 3 and Table 1 present the transformed estimate 100 ×

(exp β−1).

Since our outcome is a count variable, we use Poisson pseudo–maximum-

likelihood (PPML) regressions to estimate this model (37). As a robustness

check we also use ordinary least squares (OLS) with the natural logarithm of

the bicycle count as the outcome (Fig. 3). We cluster standard errors at the

city level, where treatment is assigned (38).

Calculating the Health Benefits. We calculate the health benefits by com-

bining our regression estimates of cycling increases for each kilometer of

pop-up bike lane with an estimate of the average health benefits of a kilo-

meter cycled ($0.45 converted from 0.62 Australian dollars), which is lower

than typical values from the gray literature (22). Our dose–response regres-

sions give us the percentage increase in cycling per kilometer of bike lane

divided by the city size or city population. For each city in our sample we

multiply this effect by the size of its pop-up bike lane program. We then con-

vert this result into additional kilometers cycled in a city based on baseline

values of kilometers cycled per person from a detailed transport behavior

survey in 135 German cities (39). We impute values of kilometers cycled

for other European cities based on ordinary least-squares regressions using

information on baseline values of a city’s modal split (trips) of commutes,

its population density, the length of its initial bike lane network, the modal

share of public transport, the number of cars per capita, the average speed

of car commuting, and road deaths per capita (more detail in Heterogeneity

Variables).

Data and Code Availability. Raw data and code have been deposited in

Zenodo (DOI: 10.5281/zenodo.3973038) (31).

ACKNOWLEDGMENTS. We thank Ben Thies and Lennard Naumann for their

excellent research assistance.

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Kraus and Koch

Provisional COVID-19 infrastructure induces large, rapid increases in cycling

PNAS |5 of 6

https://doi.org/10.1073/pnas.2024399118

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