We evaluated the impact of 15 new or improved cycle lanes in Paris and Lyon on cycling using a controlled ITS analysis. Cycle counts increased on both intervention and control streets in Paris and Lyon. Furthermore, there were positive yet non-statistically significant changes on individual streets immediately after (as indicated by the change in level) or six months after the improvements (as indicated by the changes in trend), except on Rue Julia Bartet. As the changes on this street were introduced during the public transport strike, some of the trend changes may be due to more people switching from public transport to cycling as the strike continued. Altogether, however, these findings suggest that improving or constructing new cycle lanes may be necessary but not sufficient to induce significant changes in cycling levels.
We also found that meta-analysis pooled point estimates for changes in cycling counts were larger in Paris than Lyon, which may be attributable to differences in contexts and additional policies introduced in Paris during the study period, such as the introduction of more ‘stick’ interventions (e.g., ban on diesel vehicles). Indeed, some research has suggested that a combination of carrot and stick interventions, which include both positive and negative motivators for active travel, respectively, may be more effective than either alone [41, 42]. Furthermore, the design of the cycle lanes may have been more supportive of increasing cycling levels in Paris than Lyon. Compared to Lyon, there were more cycle lanes separated from motor traffic introduced in Paris, which certain groups of cyclists (e.g., women) have been found to prefer [43, 44]. However, the effects of these differences were not formally assessed, being beyond the scope of the study.
Previous studies using primarily before-and-after study designs have found that increasing the quantity of new or improved cycle infrastructure was associated with increases in cycling behaviour [45,46,47], only one of which has used an ITS analysis, albeit with an uncontrolled study design . Consistent with the findings of our study, other studies that included a comparison group found either no or unclear effects of improved cycling infrastructure [48, 49]. Some systematic reviews have observed that studies with weaker study designs were more likely to report significant changes in active travel outcomes than those with more robust analytical methods . This is in line with the non-significant findings of our study, which uses a controlled study design with adjustment for baseline trends through ITS analysis.
There may be other reasons we did not find this improved cycle infrastructure to have a statistically significant effect. For example, cycle lanes may not immediately affect cycling levels or may take more than six months to be effective. Other studies have reported a significant change in walking and cycling levels in the longer term , including two years after introducing new infrastructure . Furthermore, one systematic review of the effects of cycling infrastructural changes on physical activity found that studies which had an exposure period of fewer than six months were more likely to find that interventions were not effective . The national Covid-19 lockdown in March 2020 greatly affected cycling levels throughout both cities, and this study cannot therefore provide evidence for effects beyond 6 months after infrastructure construction. However, we did test the effect of extending the length of follow-up for as long as possible before the lockdown, and the results of this sensitivity analysis did not differ substantially from those of the main analyses. Future work should explore longer term effects where possible.
Similarly, another possible explanation for our results is that cycling infrastructure, particularly those involving constructing new lanes, may not be introduced all at once. For longer streets, improvements may have been delivered in several stages. We used the date listed in the databases as the final cut-off point for implementation, as further information about the exact date the other stages were delivered was not available. This may also explain why we did not see significant changes in either the level or trend; it may be that the true effect of the intervention accumulates with each successive phase of construction. Further studies assessing cycle lanes may want to take this into account, and if they have the necessary information on when these were implemented, should use the appropriate methods which take into account these additional interventions .
The selection of control streets within the same city may have attenuated any detectable differences since both intervention and control streets are part of the same cycling network. Strengthening a given section of the cycling network may improve the whole network of which the control streets form part, particularly if control streets are within cycling distance of intervention streets (i.e., a contamination or spill-over effect). For instance, increasing the connectivity of the cycling network may encourage cyclists to use control streets to reach the improved intervention streets. Indeed, cycling levels in both Paris and Lyon have been increasing since the early 2000’s [52, 53]. We attempted to reduce the possibility of contamination effects by choosing control streets that were more than 2 km from intervention streets, but this distance may not be sufficient to completely remove such effects. By using control streets in the same city, however, we could account for the many concurrent events or other interventions introduced during the same period that may have affected cycling behaviour while accounting for contextual influences.
Strengths and limitations
Strengths include using a controlled ITS study design, which is among the most robust quasi-experimental study methods because it accounts for secular trends and other co-interventions or events . We were also able to select from a wide range of potential control streets, allowing us to reduce possible confounding by matching similar streets in terms of pre-intervention trends and built environment features. In addition, by selecting other control streets in the sensitivity analysis, we could account for other potential sources of bias, such as whether the controls selected in the main analysis were representative of streets that did not receive interventions overall.
Some limitations include potential confounding by indication, whereby these cities may have chosen to either improve or extensively monitor those cycle lanes believed to have the largest likelihood of increasing cycling levels. Thus, it is unknown whether the cycle lanes we were able to evaluate (i.e., those with cycle counters installed before the intervention) were randomly selected or representative of other cycle lanes in each city. As the intervention allocation process is often opaque, natural experimental research cannot always avoid these problems. However, we took steps such as selecting control groups based on similar pre-intervention trends to reduce the risk of confounding.
There are also limitations to using cycle count data collected using automatic cycle counters, which allowed us to measure infrastructure usage but not necessarily cycling behaviour (e.g., frequency, duration) or whether certain population groups changed their cycling behaviour more than others. This is partly due to difficulties in ascertaining whether displacement occurred or when cyclists divert their route from nearby streets to improved intervention streets. However, collecting objective data to measure cycling behaviour often involves equipping individuals with accelerometer or GPS devices, which may be costly and requires intensive effort and resources. These measures are thus usually assessed in small samples and worn for a short period , the latter of which would preclude us from using ITS analysis. Nonetheless, the count data on infrastructural usage can support findings from other evaluations on cycling behaviour that measure outcomes more closely related to individual health impacts . Moreover, ZELT cycle count technology has been found to undercount cyclists by 3% on separate paths and 4% on shared roadways , and the presence of bicycles with non-metallic (e.g., carbon fibre) wheels or groups of cyclists may also affect count data [32, 55]. However, any such undercounting is likely to have been small and equally applicable to all streets.
There are also challenges when using routinely collected data. For some streets, pre- and post-intervention periods could not be fully evaluated due to data availability. Although the effects of the study period length were examined in the sensitivity analysis for streets with the available data by extending the study period to one year before and after the intervention was implemented, we could not determine the long-term effects of these interventions. However, routinely collected data can offer additional opportunities in terms of what interventions can be evaluated and the methods used (e.g., ITS analysis). We were able to use routinely collected data to evaluate 15 streets, meaning this study is among the largest city-wide controlled natural experimental evaluations of new cycle lane infrastructure. Including interventions from two cities in France can also provide insights into how the effects of introducing new cycle infrastructure on cycling behaviour may differ according to existing relevant policies and local contexts. By taking wider contextual factors into account, we may in time be able to generalise such findings to other similar industrialised, high-density, and car-centric cities.