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  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.

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  2. Removed: Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems - Part II

    This e-letter was removed because it significantly exceeded the maximum word count permitted.

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  3. Removed: Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems - Part I

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    Sosa and Bhatti (1) show that death rates arising from political violence exceed death rates from road crashes in some localities of Afghanistan. In contrast, data from OECD countries indicate that the former are far less common than the latter (2). An implication is that Afghanistan is justified in devoting heavy resources to terrorism. In contrast, OECD countries should be more relaxed regarding the terrorist threat and avoid being unduly swayed by public perception.

    Here, I consider data from another troubled region - Northern Ireland. These data have been extracted from yearly reports issued by Northern Ireland's Chief Constables (3); note that there have been minor changes in procedures for data collection over the years, which however do not alter fundamental conclusions.

    Differences regarding the backgrounds to the Northern Irish and Afghan data should be noted. First, Northern Ireland is part of the UK, so is relatively affluent and more able to devote resources than relatively- impoverished Afghanistan. Second, Northern Ireland's terrorism deaths have been recorded over a considerable period of time from the late 1960s. They had fitfully reduced by the late 1990s - but not disappeared - around the time of a non-belligerence pact in 1998. In contrast, Sosa and Bhatti restrict themselves to a short period of time (2008 to 2010).

    Means per year (SEs in brackets) for road-deaths in Northern Ireland were 309.8 (7.3) for the 1970s, 198.7 (7.4) for the 1980s and 155.6 (5.0) for the 1990s.

    Means and SEs per year for terrorist deaths in Northern Ireland were 192.0 (39.7) for the 1970s, 79.3 (4.9) for the 1980s and 51.5 (9.9) for the 1990s.

    These figures indicate that the numbers for both modes of death have steadily reduced. The road data broadly shadow what has been happening in transport statistics in Great Britain (4). Subjecting the data to two-way analysis-of variance reveals that cause of death and year-range are both significant (respectively, F(1,27) = 71.76; p < 0.0005 and F (2,27) = 29.88; p < 0.0005). The interaction between the two variables is not significant (F(1,27) = 0.89; p = 0.88).

    1972 was the only year in which road-deaths (372) were less than terrorist deaths (467). Indeed, this latter is the highest of any individual year-total. This reflects the unpredictable nature of terrorist incidents in both timing and resources, a point also apparent in the predominantly higher SEs for terrorist deaths. Terrorist incidents are more likely to be newsworthy - often overwhelmingly so - but this should not discourage initiatives to reduce road-deaths.


    1. Sosa LMR, Bhatti JA. Inj Prev. Published Online First: [24.1.2013] doi:10.1136/injuryprev-2012-040716.

    2. Wilson N, Thomson G. Deaths from international terrorism compared with road crash deaths in OECD countries. Inj Prev 2005, 11, 332-3.

    3. Chief Constable's Annual Reports 1970-1999. Belfast: Royal Ulster Constabulary.

    4. Reinhardt-Rutland AH. Has safety engineering worked? Comparing mortality on road and rail. In PT McCabe (Ed.). Contemporary Ergonomics 2003. London: Taylor and Francis. Pp. 341-346.

    Conflict of Interest:

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  5. Potential value of East York dataset

    I would like to add to the Editor's argument [1] by emphasising the uniqueness, and the potential value, of the East York ridership dataset.

    Over the past 23 years, laws prohibiting children (or everyone) from riding bicycles, unless they wear helmets, have been enacted in hundreds of American municipalities, the large majority of American states, seven out of ten Canadian provinces, all of Australia and New Zealand, and numerous other jurisdictions around the world. In how many of these jurisdictions was child ridership objectively documented, to see whether the helmet requirement had any adverse effect upon it?

    Irresponsibly, in almost none. So far, only in Melbourne (Victoria law, implemented in 1990) and New South Wales (law implemented in 1991); in Calgary, Edmonton, and surrounding communities (Alberta law, implemented in 2002); and in East York (Ontario law, implemented in 1995). The Australian data were published in a scientific journal in 1996 [2], while the Alberta data, collected in 2000 and 2006, still languish in a PhD thesis [3]-- perhaps because they are so unfavourable to helmet legislation. (There are other examples of relevant ridership data that have been collected, but not disseminated, such as for British Columbia [4], and Duval County, Florida [5, 6, 7].) Only in East York were the surveys carried out annually or biennially over a relatively long time span, 1990 to 2001.

    The East York dataset should be a particularly useful complement to the others for additional reasons. For one, unlike in Australia, and several other major and minor jurisdictions, there has never been any police enforcement of the law. From the beginning, police forces said they would not, or could not, enforce it [8]. For another, bicycle helmet laws do not spring up overnight: they are preceded by campaigns to increase the perceived dangerousness of bicycle riding. In both Australia and Ontario as elsewhere, these campaigns long preceded the actual introduction of the legislation [9, 10, 11]. Yet in Australia, the single early survey was done after the campaigns were already well underway; and not done during the same season of the year as the later ones-- November to January for 1987/88, but May and June of 1990, 1991, and 1992 [10]. Only in East York was there a survey done (1990) before much, though by no means all [9, 11], of the early campaigning; and only in East York was there also rough seasonal consistency, the observation periods being August and September of 1990, June through October of 1991 and 1992, and what has been described as either May to September [12] or April to October [13, 14, 15] of 1993-2001.

    And therein lies a rub, or at least a first hint of one. Unlike for Australia and Alberta, the East York surveys have been described neither consistently nor completely, and this not just for the dates but crucially, for the sampling strategies, efforts, and site selections as well [16]. Worse, the actual numbers of cyclists counted have been reported with not just small discrepancies, but huge and incomprehensible ones [Table 1]. Even the notice of correction [17] appended to the original study is itself in need of a correction notice, for-- as we can now determine, the actual corrections at last having been published-- every statement in it is false. As summarised by the Editor [1], "the inconsistency without explanation diminishes the credibility of the results and diverts attention from the central research question."

    Table 1.

    Counts of Children Riding Bicycles, East York, Ontario,
    1990-1997, 1999, 2001

    One study, same events, as differently reported by:


    Parkin et al. 1993, 1995 [18, 19]

    Parkin et al. 2003 [13]

    Macpherson et al. 2001 [20]; Macpherson 2003 [12] (Table 6)

    Macpherson 2003 [12] (Table 7)































    Table 1, continued:


    Report of pers. comm. 2003 [21]

    Macpherson 2005 [22]

    Khambalia et al. 2005 [14]

    Macpherson et al., 2006/2012 [17]























    All Years

    At least one year's count is 550 and at least one is 1795; total for all years is 10,935

    What then are we to make of the East York data? With such inconsistencies, and no help from the authors forthcoming, the natural conclusion is: little or nothing of scientific value.

    I have come to believe that, with some clarification, this conclusion-- and the shameful waste it would imply, of over a decade of research effort on an unrepeatable historical circumstance-- is not inevitable, and this was one of the motivations for my complaint to Injury Prevention. Regardless of any data destruction, the authors should be able to tell the research community whether there was a survey in 1989, or not; and if not, on what basis they were able to say that the helmet use rate in that year was 0% [11]. The authors should be able to tell us whether the sites sampled, or their number, were the same for every year from 1990 to 2001 [15]; or not the same [14]. The authors should be able to tell us whether, as seems the only logistical possibility, the 1990 survey was a minimal one, and therefore had all sites or areas sampled to the same extent. They should be able to tell us if, as seems implied by the statistical goals (to roughly double the 1990 sample size) and the time budget (again roughly double), the 1991 survey also had double the number of survey hours, and whether these were again uniformly distributed amongst the sites or areas; or if not, then according to what strategy. The authors should be able to tell us what the situation was for 1992, and then again with regard to the overall sampling strategy for 1993-2001. And the authors should be able to tell us by what method they aggregated the site-level cyclist counts and numbers of survey hours into overall rates, something they have yet to clearly explain.

    I think these are the minimal explanations that the authors owe the research community, whose members have endeavoured to understand, or wrongly used [23], their work; the bicycling community, whose members had to defend their way of life against the premise of it [24, 25]; and the Canadian taxpayer, who paid for it.


    1. Johnston BD. Living in the grey area: a case for data sharing in observational epidemiology. Injury Prevention 2012;0:1–2. doi:10.1136/injuryprev-2012-040671.

    2. Robinson DL. Head injuries and bicycle helmet laws. Accid Anal Prev 1996;28:463-475.

    3. Karkhaneh M. Bicycle helmet use and bicyclists head injuries before and after helmet legislation in Alberta Canada. PhD thesis, University of Alberta, 2011.

    4. Foss RD, Beirness DJ. Bicycle helmet use in British Columbia: effects of the helmet use law. Pre-and post-law bicycle helmet use in British Columbia. April 2000. University of North Carolina Highway Safety Research Center; Traffic Injury Research Foundation. (accessed Feb 24 2009).

    5. Bicycle helmet use laws: lessons learned from selected sites. National Highway Transportation Safety Authority. (accessed Nov 18 2012).

    6. Conserve by Bicycle Phase 1 Study: Report. Florida Department of Transportation. Nov 18 2012).

    7. Florida Traffic and Bicycle Safety Education Program. (accessed Nov 18 2012).

    8. Wright L, MacKinnon DJ. Province eyes tougher law on helmets . The Toronto Star (metro edition). 1996;Oct 17:A2.

    9. Legislative Assembly of Ontario, committee transcripts: Standing Committee on Resources Development, November 20, 1991 - Bill 124, Highway Traffic Amendment Act, 1991. <> (accessed Nov 18 2012).

    10. Finch CF, Heiman L, Neiger D. Bicycle use and helmet wearing rates in Melbourne, 1987 to 1992: the influence of the helmet wearing law. Monash University Accident Research Centre 1993;Report No. 45. (accessed Jul 25 2009).

    11. Wesson D, Spence L, Hu X, et al. Trends in bicycling-related head injuries in children after implementation of a community-based bike helmet campaign. J Ped Surg 2000;35:688-689.

    12. Macpherson AK. An Evaluation of the Effectiveness of Bicycle Helmet Legislation. PhD Thesis, Institute of Medical Sciences, University of Toronto 2003.

    13. Parkin PC, Khambalia A, Kmet L, Macarthur C. Influence of socioeconomic status on the effectiveness of bicycle helmet legislation for children: a prospective observational study. Pediatrics 2003;112:e192-e196.

    14. Khambalia A, MacArthur C, Parkin PC. Peer and adult companion helmet use is associated with bicycle helmet use by children. Pediatrics 2005;116:939-942.

    15. Macpherson AK, Macarthur C, To TM, Chipman ML, Wright JG, Parkin PC. Economic disparity in bicycle helmet use by children six years after the introduction of legislation. Inj Prev 2006;12:231-235.

    16. Kary M. Compendium of errors and omissions in Canadian research group's bicycle helmet publications. (accessed Dec 1 2011).

    17. Update to Macpherson et al. 7 (3): 228. Correction. Inj Prev 2006;12:432. (accessed Nov 18 2012).

    18. Parkin PC, Spence LJ, Hu X, Kranz KE, Shortt LG, Wesson DE. Evaluation of a promotional strategy to increase bicycle helmet use by children. Pediatrics 1993;91:772-777.

    19. Parkin PC, Hu X, Spence LJ, Kranz KE, Shortt LG, Wesson DE. Evaluation of a subsidy program to increase bicycle helmet use by children of low-income families. Pediatrics 1995;96:283-287.

    20. Macpherson AK, Parkin PC, To TM. Mandatory helmet legislation and children’s exposure to cycling. Inj Prev 2001;7:228–230.

    21. Robinson DL. Helmet laws and cycle use. Inj Prev 2003;9:380–383.

    22. Macpherson AK. An Evaluation of the Effectiveness of Bicycle Helmet Legislation. (accessed Dec 15 2008).

    23. Legislation for the compulsory wearing of cycle helmets. British Medical Association Board of Science and Education, November 2004. (accessed Nov 18 2012).

    24. Testimonies of Neil Farrow and of the Windsor Bicycling Committee. Legislative Assembly of Ontario, committee transcripts: Standing Committee on Resources Development, December 02, 1991 - Bill 124, Highway Traffic Amendment Act, 1991. <> (accessed Nov 18 2012).

    25. Testimony of Marcia Ryan. Legislative Assembly of Ontario, committee transcripts: Standing Committee on Resources Development, November 25, 1991 - Bill 124, Highway Traffic Amendment Act, 1991. <> (accessed Nov 18 2012).

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    Schwebel (1) raises the issue of how auditory processing might contribute to safe negotiation of the roads by pedestrians. In particular, does the masking of relevant auditory information entail unnecessary danger? Almost coincidentally, a recent review (2) has considered possible technological developments that might provide useful supplementary information to aid drivers in avoiding collisions: potential sources might be auditory in nature.

    The purpose of this note is to draw attention to psychophysical evidence for the potential of auditory information in such contexts. For those with normal or corrected-to-normal eyesight, visual information is almost certainly of primary importance in conveying potential collision - specifically, visual expansion of the viewed object, or "looming". The object - say, an automobile - may be moving towards the static observer; alternatively, the observer may be moving towards a static object. Also, both observer and object could be moving towards each other. In contrast, an unthreatening receding object undergoes visual contraction.

    There is strong evidence of hard-wired sensory processing of visual motion: motion aftereffects are well-known illusions in the visual modality, whereby the observer perceives illusory motion of a static stimulus after viewing steady motion of that stimulus for a minute of so. The aftereffect of visual approach is substantially stronger than the aftereffect of visual recession: the sensory-systems of humans (and many other species) are much more sensitive to approach, almost certainly reflecting the survival value in avoiding damaging collisions (3,4).

    An analogous asymmetry applies to the auditory modality: in this case, approach is conveyed predominantly by increasing sound-level, while the less critical recession is conveyed by decreasing sound-level. Growing -louder aftereffects are stronger than growing-softer aftereffects (5). However, there is a limitation to the effectiveness of audition in determining collision. In vision, most objects are rigid or near-rigid: objects varying in size - for example, inflating or deflating balloons - are unusual, so an assumption of rigidity with regard to vision is extremely plausible. However, in audition, analogous assumptions are weaker and more ambiguous. For example, many sounds are percussive: after a short rise-time, their sound-levels steadily reduce. Indeed, evidence suggests that compensation for this characteristic is necessary in measuring auditory aftereffects (5).

    The clear inference to be drawn is that vision provides better evidence for collision than does audition. No doubt the latter is useful for the visually-impaired - and might be quite well-developed for this group. However, for the normal-sighted the ambiguity of auditory stimuli may be such that vision inevitably predominates in responding to motion-in -depth. Instead, the real issue of much auditory stimulation on the road - such as music presented over earphones, or via an automobile's sound- system - may be one of distracted attention.


    (1) Schebel DC. Do our ears help us cross streets safely? Inj Prev 2012 10.1136/injuryprev-2012-040682.

    (2) Spence C. Drive safely with neuroergonomics. Psychologist 2012; 18: 664-667.

    (3) Scott TR. Lavender AD, McWhirt RA, Powell DA. Directional asymmetry of motion aftereffect. J Exp Psychol 1966; 72: 806-815.

    (4) Reinhardt-Rutland AH. Perception of motion-in-depth from luminous rotating spirals: direction asymmetries during and after rotation. Perception 1994; 23: 763-769.

    (5) Reinhardt-Rutland AH. Perceptual asymmetries associated with changing-loudness aftereffects. Percept Psychophys 2004; 66: 963-969.

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  7. Furthering the interests of every apple: The need for reliable injury data collection in Queensland.

    Re: Comparing apples with apples? Abusive Head Trauma, Drowning and LSVROs (response to Kaltner, Kenardy, Le Brocque & Page, 2012), by Watt, Franklin, Wallis, Griffin, Leggat and Kimble (2012)

    Developing the epidemiological literature base on the occurrence of all forms of childhood injury is essential to the development and promotion of injury prevention efforts. As is rightfully highlighted by Watt, Franklin, Wallis, Griffin, Leggat and Kimble (2012), limitations in the availability of easily accessible child injury data exist in Queensland. Within Kaltner, Kenardy, Le Brocque & Page's (2012) paper, published figures on rates of alternate forms of childhood injury were utilised to contextualise the occurrence of Abusive Head Trauma (AHT). Their selection was based on the most recent figures available to the authors following extensive literature searches; as is discussed by Watt et al., more comparable and recent figures are not accessible in the public sphere.

    With the cessation of funding to the Queensland Trauma Registry, the availability of up-to-date, reliable injury data within Queensland is limited. This presents a further challenge to all injury researchers in the state, alongside the hurdle of approvals necessary to access Queensland Health data as overviewed by Watt et al. (2012). In undertaking the important work of research and prevention for all forms of childhood injury, high level support-including financial commitment- for the development and maintenance of reliable and accessible injury databases is necessary.

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    Hemenway (1) describes three beliefs which may jeopardize injury- avoidance: optimistic ("it will never happen to me"), fatalistic ("accidents happen") and materialistic ("you probably deserved it"). Such a scheme parallels well-known trait theories regarding the individual's general personality (2); given the value of those endeavours,Hemenway's scheme deserves serious consideration.

    Nonetheless, it may be incomplete. In this note, I argue for the inclusion of values that I label as societal - that is, they are best understood in terms of major societal groups. Evidence supporting this proposal resides in a comparison of road-travel and rail-travel; this suggests that society expects higher standards of safety for rail than for road. Two examples follow:

    A. SAFETY AND VEHICLE DESIGN: Traditionally, Britain's railway carriages were equipped with slam-doors, which could be opened by passengers even when the train was moving. During the mid-2000s, such stock - even if relatively new - was mostly replaced by carriages using less reliable sliding-doors under electronic control of guard and driver. The saving in injuries and deaths has almost certainly been miniscule: I see no evidence against this assertion in Britain's transport data (3). Society deemed that the relevant legislation should be enacted, despite the heavy costs involved.

    Cost can have different implications on the road: SUVs - large and powerful four-wheel-drive automobiles - are more dangerous than smaller, cheaper-to-buy and cheaper-to-run automobiles (4). One might suppose that governments would seek to reduce the prevalence of SUVs, since the choice of SUV ownership appears to be little more than an issue of perceived prestige.

    B. ATTENTION TO THE TASK: Society has long expected that train drivers pay undivided attention to their job. Indeed, the use of a "dead- man's-handle" or its modern developments entails the train automatically coming to a stand if the driver diverts attention (5).

    In contrast, values concerning the road imply that drivers can safely carry out other tasks during driving. A notably transparent example concerns the common media device of televising an inverview while the interviewee is driving. This presents an extraordinarily inept message to the motoring community. Inattention on the road is supposedly discouraged, although specific legislation is limited. The banning of mobile-phone use is a rare case, but its effectiveness must be seriously doubted (6).

    CONCLUSION: Hemenway offers a useful scheme for investigating injury prevention. I argue here that - at least regarding travel - the problems are not simply to be understood by reference to the individual's beliefs. The problems are also societal. The two examples above indicate greater threat on road than on rail. There are other examples that can be developed: the use of psychoactive drugs (7,8) and failure to observe speed-limits (9). Paradoxically, the latter may have been exacerbated by the legally-required use of seatbelts (10).

    The imbalance in societal values is consistent with casualty statistics (3). Until society is prepared to recognise and implement the lessons from rail-travel, an important conduit for injury prevention in road-travel will remain under-exploited.


    1. Hemenway D. Three common beliefs that are impdiments to injury prevention. Inj Prev 2012; 00:1-4. doi:10.1136/injuryprev-2012-040507

    2. Hewstone M, Fincham F, Foster J. Psychology. 2005. Leicester UK: BPS.

    3. Department for Transport 2011. Transport statistics GB: 2010 Annual report. London: TSO.

    4. Simms S, O'Neill D. Sports utility vehicles and older pedestrians. BMJ 2005;331:787-8.

    5. Harris M. Dead man's handle. In Simmons J, Biddle G (eds). The Oxford campanion to British railway history. 2002. Oxford:OUP (p 125).

    6. McEvoy SP, Stevenson MR, McCartt AT, Woodward M, Haworth C, Palmara P, Cercarelli R. Role of mobile phones in motor vehicle crashes resulting in hospital attendance: a case-crossover study. BMJ 2005;331:428 -430.

    7. Perkins A. Red Queen: the authorized biography of Barbara Castle. 2003. London: Macmillan.

    8. Hall W. Driving while under the influence of cannabis. BMJ 2012;344:e595 doi: 10.1136/bmj.e595.

    9.Reinhardt-Rutland AH, Roadside speed-cameras: arguments for covert siting. Police J 2001;74:312-315.

    10. Reinhardt-Rutland AH, Seat-belts and behavioural adaptation: the loss of looming as a negative reinforcer. Safety Sci 2001;39:145-155.

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  9. Old hypothesis that roads are safer than cycle tracks unsupported by data

    We acknowledge that we did not control for all of the differences in road geometry and building typologies because there are no ideal matched streets (Re: Cooper). However, alternative research designs also have limitation and feasibility issues. For before and after study designs, some of the Montreal cycle tracks are 20 years old, before injury surveillance and traffic counting data systems were available. Limiting to cycle tracks that were developed after these data were available would limit us to a much smaller number of cycle tracks, thus reducing the statistical power. Utilizing a multivariate analysis to account for other factors such as road geometry, buildings types, pedestrians, trees, etc. would answer a different research question - about the possible independent effect of each factor - and would require many more cycle tracks or another unit of analysis (ex. intersections). Therefore, bicycling on cycle tracks was compared to bicycling on streets without cycle tracks. To select the alternative reference streets without cycle tracks, a few parallel reference streets were considered for each street with a cycle track, The parallel street was then selected because it had, as much as possible, the same cross streets. Recognizing no perfect reference street existed, we also compared relative danger from vehicular traffic by obtaining the injuries to motor vehicle occupants (EMR data). Given these limitations, none of the 6 pairs were found to have a statistically significant higher risk of injury on the cycle tracks. Thus, not one of the comparisons in this research conducted in Montreal supported the old hypothesis that bicycling on cycle tracks posed greater risk than bicycling in the road. In fact the opposite was true as bicycling on the cycle tracks posed less risk.

    Conflict of Interest:

    None declared

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  10. Effectiveness of breed-specific legislation in decreasing dog-bite injury hospitalizations in Manitoba--what it means to researchers, policy-makers and the public

    Our population-based study (1) on the effectiveness of breed-specific legislation (BSL) targeting pit-bull (terrier) type dogs in the Canadian province of Manitoba generated some interest in the media and among policy -makers and the public in Canada and the United States (2-10). With this experience of listening to different stakeholders and communicating with some, we hope to elaborate on our findings in language that is accessible to all. The objective of the study was to determine trends in the frequency of dog-bite injury hospitalizations (DBIH) over time for jurisdictions with and without a ban on pit bull (terrier)-type dogs in Manitoba (1).

    We reported that at the provincial level in Manitoba, there was a decrease in incidence of DBIH from 3.47 to 2.84 per 100,000 person-years associated with implementation of a ban on pit-bull terrier type dogs. That is, there was a decrease by 0.63 per 100,000 persons per year (an 18.1% decrease in DBIH rate) in 16 self-selected urban and rural jurisdictions. Correspondingly, in people aged 0 to < 20 years, there were 1.76 fewer DBIH per 100,000 person-years (a 25.5% decrease in DBIH rate) in Manitoba. This decrease in rates of DBIH may be a conservative finding because enforcement of legislation, which was not measured and is known to have varied across the jurisdictions and over the years, is assumed to be minimal, if at all. While the type of legislation studied was specifically a ban, no jurisdictions were known to have outlawed pit bulls overnight. As existing individual dogs were allowed to live out their lifetimes, no drastic reduction in numbers of pit bulls, and by extension, in numbers of DBIH, was expected in jurisdictions that implemented bans only gradually since 1990.

    What does the change in incidence of DBIH at the provincial level mean? The Canadian province of Ontario, with a population about 11 times larger than Manitoba, has a province-wide ban on pit-bull terrier type dogs since 2005 (11). Assuming that Ontario's DBIH rate, rate of penetration of dog population (i.e., dogs per capita of human population) and dog-breed distributions are similar to those in Manitoba, we applied the decrease of 0.63 DBIH per 100,000 people per year to Ontario's population of 12.8 million in 2011 (12,13). (While Manitoba's rural population is considered to be 28%, Ontario's rural population is reported to be 15%.) We estimate that there may have been 81 fewer DBIH in 2011 alone in Ontario on account of the province-wide ban. As Ontario's population of those aged < 20 years was 3 million (13), 54 (66.7%) of the estimated decrease by 81 DBIH among all ages in 2011 would have been in people aged < 20 years.

    When considering rate differences in post-legislation period compared with pre-legislation period in Winnipeg alone, our data do not indicate a change in DBIH rate. Therefore, it is natural to assume that BSL does not work. However, our study does not account for changes in overall number of dogs over the long period under study. Based on growth in number of pet dog populations in the United States over the last two decades (14,15), we propose that any hypothesized decrease in the number of DBIHs due to pit-bull attacks is likely masked, and the effect of legislation diluted, by a simultaneous increase in DBIHs due to attacks by dogs from other breeds or breed groups. Again, this explanation is quickly assumed to be evidence that breed bans do not work. After all, an argument against BSL is that breed composition in dog populations can change such that other dangerous dogs replace dogs from banned breeds. A limitation of the study was our inability to separate the proportion of DBIHs caused by dogs of banned breeds from the proportion caused by dogs of other breeds or breed groups. However, with the assumption that replacement is necessarily different from addition of more dangerous dogs to the existing numbers, we compared DBIH rates in jurisdictions with pit bull-specific ban (e.g., Winnipeg) to DBIH rates in jurisdictions without such bans (e.g., Brandon). The idea behind this analysis is that, unlike pit-bull specific bans, voluntary changes in breed popularity have no boundaries, and jurisdictions with bans are assumed to be similar to jurisdictions without bans in every respect other than the existence of the ban. Such an analytic approach is also an improvement over a pre/post analysis of data from a single jurisdiction adopting the ban.

    We adopted a generalized estimating equations (GEE) model for this comparative analysis. This multivariate model allowed us to isolate the effect of legislation while modeling annual DBIH counts adjusted for human population counts, calendar year of DBIHs and baseline differences in underlying DBIH rates across jurisdictions with and without legislation. The model yielded an incidence rate ratio--i.e., the rate of DBIHs in jurisdictions with a ban relative to the rate in jurisdictions without a ban.

    The results from the GEE model were not remarkable when data from all Manitoba jurisdictions were analyzed, but as control jurisdictions were more likely to be rural jurisdictions, there was a high inter-correlation among variables. One way of controlling for the confounding effects of rurality of jurisdictions is to stratify the dataset into rural and urban. Therefore, we restricted analyses to urban jurisdictions alone. The results indicated that for every one DBIH in Brandon, there were 1.29 DBIHs in Winnipeg before the pit-bull ban and 1.10 DBIHs after the ban. This is a 14.7% reduction in rate of DBIH in people of all ages. In people younger than 20 years old, for every one DBIH in Brandon, there were 1.28 DBIHs in Winnipeg before the ban and 0.92 DBIHs after the ban. This amounts to a 28.1% reduction in rate of DBIH. These findings were statistically significant. Other reasons for this decrease cannot be ruled out in this real-world, observational study which can be thought of as a non-randomized, self-selected community trial. However as far as we can ascertain, no other dog-control legislation is different between the two jurisdictions.

    Going forward, researchers should compare DBIH rates temporally as well as geographically. Future (controlled) studies in other places where pit-bull specific bans have been in effect long-term are still necessary to conclusively understand if rates of DBIHs generally and gradually decline when pit-bulls are removed from the population. This is because effectiveness (or magnitude of rate decrease) may be variable depending on local conditions, even if everyone agreed that pit-bulls caused a disproportionate number of DBIHs. For example, if rate of pit-bull penetration is high, then magnitude of effectiveness of a pit-bull ban would likely be higher than observed in our study, if a cause-effect relationship truly exists. However, if rate of pit-bull penetration is zero (i.e., no pit bulls), then a ban that was proven to be 100% effective elsewhere (hypothetically speaking) would bring about little change to DBIH rate as, technically, there are no dogs to be banned. Furthermore, pit bulls in one region of the world may be less aggressive than pit bulls in another region owing to potentially different lineages and differences in dog-owning cultures. While the value inherent in local data should not be underestimated for the purposes of local policies, data from larger jurisdictions with bigger populations of dogs, including those from the banned breeds, and higher rates of DBIHs will further shed light on this public health topic that appears to attract a lot of public and stakeholder interest.


    1. Raghavan M, Martens P, Chateau D, Burchill C. Effectiveness of breed-specific legislation in decreasing the incidence of dog-bite injury hospitalizations in people in the Canadian province of Manitoba. Injury Prevention doi:10.1136/injuryprev-2012-040389. E-pub ahead of print.

    2. Blackwell T. Controversial pit bull bans result in fewer dog bites: study. National Post, July 5, 2012. -in-fewer-dog-bites-study/ (accessed 9 September, 2012).

    3. Kaufman B. Calgary bylaw boss dismisses pit bull breed ban study. Calgary Sun. July 6, 2012. bylaw-boss-dismisses-pit-bull-breed-ban-study (accessed 9 September, 2012).

    4. Kay B. Study proves pit bull ban is justified. National Post, July 6, 2012. study-proves-pitbull-ban-is-justified/ (accessed 9 September, 2012).

    5. DogsBite Blog. New Canadian study shows pit bull bans result in fewer hospitalizations., Austin, Texas. July 9, 2012. bans.html (accessed 9 September, 2012).

    6. Anonymous. Winnipeg, Manitoba far behind Calgary in community safety. National Canine Research Council, LLC , Amenia, New York. July 9, 2012. -far-behind-calgary-in-community-safety/ (accessed 9 September, 2012).

    7. Parsons L. Severe bites down after pit bull ban. Winnipeg Metro, July 10, 2012. down-in-winnipeg-since-pit-bull-ban-study/ (accessed 9 September, 2012).

    8. Jonas G. The state has no business in the dog houses of the nation. National Post, July 11, 2012. no-business-in-the-doghouses-of-the-nation/ (accessed 9 September, 2012).

    9. Editorial: Pit bull bans may actually be working. The Hamilton Spectator, July 11, 2012. Excerpt reprinted from The St. John's Telegram.

    10. Raghavan M. Invited presentation: Study on the effectiveness of breed-specific legislation in decreasing dog-bite injury hospitalizations in Manitoba--what it means to researchers, policy-makers and the public. Manitoba Agriculture, Food and Rural Initiatives (MAFRI) Lunch & Learn Session. August 13, 2012, Winnipeg, Manitoba.

    11. Ontario Ministry of the Attorney General. Information on the dog owners' liability act and public safety related to dogs statute law amendment act, 2005. pubsfty/dola-pubsfty.asp#TOC_03 (accessed 9 September, 2012).

    12. Statistics Canada. Population, urban and rural, by province and territory. som/l01/cst01/demo62a-eng.htm (accessed 9 September, 2012).

    13. Statistics Canada. Focus on geography series, 2011 census-- province of Ontario. -sa/fogs-spg/Facts-pr-eng.cfm?Lang=Eng&GK=PR&GC=35 (accessed 9 September, 2012).

    14. PRWeb. New survey reveals pet ownership at its highest level in two decades and pet owners are willing to pay when it comes to pet's health. American Pet Products Association Press Release, Greenwich, CT (Vocus/PRWEb) April 04, 2011. (accessed 2Feb 2012).

    15. Shepherd AJ. Results of the 2006 AVMA survey of companion animal ownership in US pet-owning households. J Am Vet Med Assoc 2008;232:695-6.

    Conflict of Interest:

    None declared

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