1. Vulnerabilities of the case-crossover method as applied to transportation injuries and traffic engineering problems

    The case-crossover method in its familiar application is to look for factors that recur when cases occur, for individuals crossing exposure to them as examined over a time interval. This study [1-3] applies the method in a different way, the exposures being examined over a spatial route, with neither the identified factors nor the various routes being independent of the highly constrained urban geographies of the settings. Thus in addition to all the familiar vulnerabilities of the case-crossover method [4-9]-- some of which require translation to the new context-- this application brings new problems of its own. It is not possible to note even most of just the major ones in this correspondence, and further criticism may be found elsewhere [10-12]. I thank the authors for kindly providing extra information as necessary for the following analyses.

    1. Control site selection bias.

    The authors find control sites by random selection along the route the injured rider took. Contrary to [2], such comparisons only make sense if the control locations match the case locations by intersection status, which often they do not. To make them match, in [3] the authors randomly adjust selections forward or back until they do. This was necessary for about 70% of the cases at intersections, and 30% at non-intersections.

    In these instances, selection of control intersections is dependent on their spatial distribution along the route, but indifferent to their widths. This biases their selection in favour of smaller intersections associated to longer non-intersection segments. Likewise, the selection of non-intersection control sites is disproportionately biased in favour of whatever are adjacent larger intersections.

    For example, over a route whose length is 30% intersections, 70% non- intersections, beginning at 0 and having terminated at 1, with intersections between 0 and 0.05, 0.5 and 0.6, and 0.85 to 1, the probabilities of choosing the three intersections as control sites should occur in ratios of 1:2:3. But by the authors' adjustment method, in those instances where adjustment is needed, they are respectively 0.5 x 0.45/0.7, [(0.5 x 0.45)+ (0.5 x 0.25)]/0.7, 0.5 x 0.25/0.7, thus occurring in ratios of approximately 1:1.56:0.56. Maclure [4] has discussed the potentially large biases in relative risk estimates that can result from not taking intersection widths into account.

    There is already selection bias before this stage. For example, consider a route with no intersections, having a bicycle-specific facility in the first and last thirds only. Suppose injury events occur at random along this route. They should therefore occur in facilities and non-facilities in proportions of 2:1, and likewise so should the selection of control sites. But under the authors' method of selection, the probability of the control being in a facility is [2+ln(4/3)]/3, so that instead the proportions are about 3.21:1.

    Such problems have been discussed extensively in the meteorological literature on case-crossover studies [7-9], and by Maclure in the epidemiological literature [4].

    There is still another potential randomisation failure at this level of selection to consider. The standard deviation of the uniform distribution on [0, 1] is almost one-third (1/[2*SQRT(3)]). For individual runs of only 801 in length (for non-intersections), or 272 (for intersections), this can easily result in quintiles being out of balance by plus or minus 10 to 25%, which can again skew the estimates. (Thus the reader wishing to closely check by simulation the probability calculations given above should use a much larger n, such as on the order of 10^5.)

    2. Anomalous or internally inconsistent results.

    (1) The authors note that contrary to previous studies, they found surplus injuries at intersections with the greatest bicycle traffic. They suggest their finding may not be generalisable. But they do not explain why their method should have led to a non-generalisable result.

    The authors' method does not track the effect of an independent variable-- in this case, cyclist traffic-- as it varies at a fixed location. Instead it ranges over entirely different locations, which coincidentally may have different values of the independent variable. Yet cyclists do not choose their routes at random, and many routes may share intersections and links.

    In most cities there are inherently hazardous locations that attract bicycle traffic because they are in some way inevitable, such as for being the only way to access a bridge. Thus even if control site selection within routes had been correctly randomised, this would not balance the bias across routes.

    Nor is bicycle infrastructure installed at random. Instead, the locations for it are typically chosen either to take advantage of already safe circumstances, or to address special hazards, via multiple special measures. Thus another set of anomalous results, this time put forth as addressing the cycle track controversy:

    (2) The authors find bicycle-only paths in parks to be 17.6 times as dangerous as bicycle-only paths in streets. They find multi-use paths in parks to be 22.8 times as dangerous as bicycle-only paths in streets.

    The fundamental (not the only) hazard of cycle tracks is that they force cyclists to be in the path of turning and crossing vehicles at junctions. The protection they can offer is only between junctions, where the absolute risks are lower, while they force cyclists into danger at junctions, where the absolute risks are higher [13]. Attempts to mitigate the hazards at junctions generate inconvenience and frustration for all users, such that their benefits may not be durable, as was the case for the Burrard Bridge in Vancouver subsequent to the authors' short study period [14].

    The authors' work estimates only relative risks of cycle tracks, and only between intersections. By missing both absolute risks and the action at intersections, it does not do anything to address the cycle track controversy, and it is wrong to use its results to promote cycle tracks.

    The only novel cycle track result from this study is the anomalously large relative benefit it ascribes to cycle tracks between intersections. This limited result suffers from the following weaknesses:

    (i) As found by the authors and others, the majority of cyclist injury events, including hospitalisations, result from bicycle-only crashes [2, 15, 16]. As noted by others, if cycle tracks work by protecting cyclists from motor vehicles, how can they reduce injuries by 95%, if the majority of such injuries have nothing to do with motor vehicles?

    (ii) If cycle tracks work by protecting cyclists, then the authors' results that introduced this section indicate cyclists need protection most of all not from motor vehicles, but from pedestrians and squirrels.


    1. Harris MA, Reynolds CCO, Winters M, Chipman M, Cripton PA, Cusimano MD, Teschke K. The Bicyclists' Injuries and the Cycling Environment study: a protocol to tackle methodological issues facing studies of bicycling safety. Inj Prev 2011;17:e6. doi:10.1136/ injuryprev-2011-040071.
    2. Teschke K, Harris MA, Reynolds CCO, Winters M, Babul S, Chipman M, et al. Route Infrastructure and the risk of injuries to bicyclists: a case-crossover study. Am J Pub Health 2012;Oct 18:e1-e8. doi:10.2105/AJPH.2012.300762.
    3. Harris MA, Reynolds CCO, Winters M, Cripton PA, Shen H, Chipman ML, et al. Comparing the effects of infrastructure on bicycling injury at intersections and non-intersections using a casecrossover design. Inj Prev 2013;0:18. doi:10.1136/injuryprev-2012-040561.
    4. Maclure M, Mittleman MA. Should we use a case-crossover design? Ann Rev Public Health 2000;21:193221.
    5. Redelmeier DA, Tibshirani RJ. Interpretation and bias in case-crossover studies. J Clin Epidemiol 1997;50;1281-1287.
    6. Sorock GS, Lombardi DA, Gabel CL, Smith GS, Mittleman MA. Case-crossover studies of occupational trauma: methodological caveats. Inj Prev 2001;7(Suppl I):i3842.
    7. Lee J-T, Kim H, Schwartz J. Bidirectional casecrossover studies of air pollution: bias from skewed and incomplete waves. Env Health Perspectives 2000;108:1107-1111.
    8. Bateson TF, Schwartz J. Selection bias and confounding in case-crossover analyses of environmental time-series data. Epidemiology 2001;12:654-661.
    9. Lumley T, Levy D. Bias in the case-crossover design: implications for studies of air pollution. NRCSE Technical Report Series NRCSE-TRS No. 031, 1999.
    10. Kary M. Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems-- Part I. (accessed Dec 2013).
    11. Kary M. Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems-- Part II. (accessed Dec 2013).
    12. Allen JS. Safe bicycle routes: engineering versus epidemiology. 2013. (accessed Dec 2013).
    13. Bicycle infrastructure and safety. Transport Canada, Urban Environmental Programs: Case Studies in Sustainable Transportation, Issue Paper 90. March 2012. (accessed Dec 2013).
    14. City of Vancouver. Downtown Separated Bicycle Lanes Status Report, Spring 2012. June 5 2012. (accessed Dec 2013).
    15. Aultman-Hall L, Kaltenecker MG. Toronto bicycle commuter safety rates. Accident Analysis & Prevention 1999;31(6):675-86.
    16. Boufous S, de Rome L, Senserrick T, Ivers RQ. Single- versus multi- vehicle bicycle road crashes in Victoria, Australia. Inj Prev doi: 10.1136/injuryprev-2012-040630.
    17. Chipman ML, MacGregor CG, Smiley AM, Lee-Gosselin M. Time vs. distance as measures of exposure in driving surveys. Accident Analysis & Prevention 1992;24:679-684.

    Conflict of Interest:

    None declared

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