Displaying 1-10 letters out of 157 published
Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems - Part I
- 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 [4-10]-- some of which require translation to the new context-- this application brings new problems of its own. Overlayed on top of these is the general unsuitability of the epidemiological approach to transportation injuries and traffic engineering problems.
- These issues occur in abundance and deserve illumination, while replies are required to be brief. Consequently this is not a balanced assessment of strengths and weaknesses, but a spotlight on a selection of the latter. Even so this will have to be done over a series of eventual responses. I thank the authors for kindly providing extra information about their study as necessary for the following analysis.
- The case-crossover method is particularly vulnerable to recruitment and severity bias, information and recall bias, bias in the selection of control sites, temporal confounding of various sorts, and other problems [4-10]. It is also as subject as any other method to confounding by unmeasured, uncontrolled factors, and model dependence of adjustments for measured confounders. I focus on a few of these that take unusual forms in this study, even though there is reason to suspect that the others are at least as important. Examined in this first response are vulnerabilities to control site selection bias.
- For each site where an injury event occurred, the authors find control sites by randomly selecting another location along the route the rider took, from start to termination at the injury event. This is supposed to adjust for exposure to infrastructure types, the probabilities of their selection, and thus hopefully the resulting overall relative frequencies, being proportional to their relative lengths along the routes.
- To compare by facility types, intersections must be paired with other intersections, and likewise non-intersections with non-intersections. For injuries occurring at intersections, usually the location randomly chosen for use as a control will not land on another intersection, so the authors randomly adjust that location forward or back until it does. The authors have informed me that this was necessary about 70% of the time.
- In these instances, the selection of control intersections of various sizes (i.e., traversed widths) is dependent on their spatial distribution along the route, but indifferent to their widths. This allows their selection to be disproportionately biased in favour of smaller intersections associated to longer non-intersection segments. 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 in fact 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  has discussed the potentially large biases in relative risk estimates that can result from not taking intersection widths into account.
- Likewise, sometimes the random location selected to control for a non-intersection injury event site lands on an intersection, so the authors randomly adjust that location forward or back until it doesn't. In these instances (about 30%), this allows the selection of non-intersection control sites to be disproportionately biased in favour of whatever are adjacent larger intersections. This might very well have included cycle tracks, considering the ones in existence at the time of the study.
- There is though already a potential selection bias before this stage. Injuries almost always occur some distance before the very end of a planned trip. The authors restrict their selection of control sites to the route traversed before the injury event, thus systematically excluding the tails of the planned trips from selection. Bicycle facilities have particular distributions within cities and along routes (and over all routes in the sample considered as a whole), and consequently, excluding the tails of the planned trips may disproportionately bias the selection of control sites. For example, consider a route with no intersections, having a bicycle facility in the first and last thirds only. Suppose injury events occur completely at random along this route, so that they have no association with infrastructure type (or any other factor). The injury events therefore occur in bicycle facilities and non-facilities in proportions of 2:1, and likewise so should the selection of control sites. But an elementary calculation shows that, 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 control sites occur in facilities and non-facilities in proportions of about 3.21:1.
- Some of the above vulnerabilities to bias are analogous to those familiar from meteorological case-crossover studies, where selection bias may occur if there are long-scale temporal waves of exposure, or serial autocorrelation. In the present context these correspond to spatial waves or autocorrelation of exposure, which occur both within routes and across subjects, the latter if only because the constraints of urban geography mean their routes may overlap. There can also be temporal waves or autocorrelations in the present study, e.g. for injuries occurring to different people during the same rush hour, in response to e.g. large scale spatio-temporal patterns of traffic congestion.
- Other studies have addressed such issues with more or less success by using bidirectional sampling. This and the resulting matter of selecting control sites post-terminating event has been discussed extensively in the meteorological literature on case-crossover studies [7-9], and by Maclure in the epidemiological literature .
- 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.)
- This ends a first instalment, devoted only to control site selection bias. The next eventual instalment shall cover various other vulnerabilities to bias in this study, including the fundamental one introduced by considering only distance at risk, instead of or without the addition of time at risk .
- 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. Maclure M. The case-crossover design: a method for studying transient effects on the risk of acute events. Am J Epid 1991;133:144-153.
- 11. Chipman ML, MacGregor CG, Smiley AM, Lee-Gosselin M. Time vs. distance as measures of exposure in driving surveys. Acciden Analysis & Prevention 1992;24:679-684.
Conflict of Interest:
COMPARING DEATHS DUE TO POLITICAL VIOLENCE AND ROAD CRASHES IN NOTHERN IRELAND
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:
Potential value of East York dataset
- I would like to add to the Editor's argument  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 , while the Alberta data, collected in 2000 and 2006, still languish in a PhD thesis -- 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 , 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 . 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 . 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  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 . 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 
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 , "the inconsistency without
explanation diminishes the credibility of the results and diverts
attention from the central research question."
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 
Macpherson et al. 2001 ; Macpherson 2003  (Table 6)
Macpherson 2003  (Table 7)
Table 1, continued:
Report of pers. comm. 2003 
Macpherson 2005 
Khambalia et al. 2005 
Macpherson et al., 2006/2012 
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% . 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 ; or not the same . 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 , 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. http://www.hsrc.unc.edu/safety_info/bicycle/helmet_use_bc.pdf (accessed Feb 24 2009).
5. Bicycle helmet use laws: lessons learned from selected sites. National Highway Transportation Safety Authority. http://www.nhtsa.gov/people/injury/pedbimot/bike/bikehelmetuselawsweb/pages/7ProfileBJacksonvill.htm (accessed Nov 18 2012).
6. Conserve by Bicycle Phase 1 Study: Report. Florida Department of Transportation. http://www.dot.state.fl.us/safety/ped_bike/brochures/pdf/CBBphase1%20Report062907.pdf(accessed Nov 18 2012).
7. Florida Traffic and Bicycle Safety Education Program. www.saferoutesinfo.org/sites/default/files/page/Pieratte.pdf (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. <http://www.ontla.on.ca/web/committee-proceedings/committee_transcripts_details.do?locale=en&Date=1991-11-20&ParlCommID=105&BillID=&Business=Bill+124%2C+Highway+Traffic+Amendment+Act%2C+1991&DocumentID=17013> (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. http://monash.edu.au/muarc/reports/muarc093.html (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. http://www.cyclehelmets.org/papers/c2031.pdf (accessed Dec 1 2011).
17. Update to Macpherson et al. 7 (3): 228. Correction. Inj Prev 2006;12:432. http://injuryprevention.bmj.com/content/12/6/432.full (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. http://www.neurosurgery.pitt.edu/circl/webinars/archive/2005/documents/macpherson_101105.pdf (accessed Dec 15 2008).
23. Legislation for the compulsory wearing of cycle helmets. British Medical Association Board of Science and Education, November 2004. http://www.helmets.org/bmareport.htm (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. <http://www.ontla.on.ca/web/committee-proceedings/committee_transcripts_details.do?locale=en&Date=1991-12-02&ParlCommID=105&BillID=&Business=Bill+124%2C+Highway+Traffic+Amendment+Act%2C+1991&DocumentID=16994> (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. <http://www.ontla.on.ca/web/committee-proceedings/committee_transcripts_details.do?locale=en&Date=1991-11-25&ParlCommID=105&BillID=&Business=Bill+124%2C+Highway+Traffic+Amendment+Act%2C+1991&DocumentID=16980#P181_55605> (accessed Nov 18 2012).
Conflict of Interest:
AUDITORY CONTRIBUTIONS TO ROAD-SAFETY: IMPLICATIONS FROM AFTEREFFECTS OF AUDITORY MOTION AND VISUAL MOTION
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.
Conflict of Interest:
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.
Conflict of Interest:
IMPEDIMENTS TO THE PREVENTION OF TRAVEL-RELATED INJURY: SOCIETAL AS WELL AS INDIVIDUALISTIC
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.
Conflict of Interest:
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:
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. http://news.nationalpost.com/2012/07/05/controversial-pit-bull-bans-result -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. http://www.calgarysun.com/2012/07/06/calgary- 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. http://fullcomment.nationalpost.com/2012/07/06/barbara-kay- study-proves-pitbull-ban-is-justified/ (accessed 9 September, 2012).
5. DogsBite Blog. New Canadian study shows pit bull bans result in fewer hospitalizations. Dogsbite.org, Austin, Texas. July 9, 2012. http://blog.dogsbite.org/2012/07/new-canadian-study-shows-pit-bull- 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. http://www.nationalcanineresearchcouncil.com/blog/winnipeg-manitoba -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. http://metronews.ca/news/winnipeg/291327/severe-dog-bites- 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. http://fullcomment.nationalpost.com/2012/07/11/george-jonas-the-state-has- 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. http://www.attorneygeneral.jus.gov.on.ca/english/about/pubs/dola- pubsfty/dola-pubsfty.asp#TOC_03 (accessed 9 September, 2012).
12. Statistics Canada. Population, urban and rural, by province and territory. http://www.statcan.gc.ca/tables-tableaux/sum- som/l01/cst01/demo62a-eng.htm (accessed 9 September, 2012).
13. Statistics Canada. Focus on geography series, 2011 census-- province of Ontario. http://www12.statcan.gc.ca/census-recensement/2011/as -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. http://www.prweb.com/releases/2011/4/prweb8252684.htm (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:
Comparing apples with apples? Abusive Head Trauma, Drowning and LSVROs
Kerrianne Watt1, Richard C Franklin1, Belinda Wallis2, 3, Bronwyn Griffin2, 3, Peter Leggat1; Roy Kimble2,3
1School of Public Health, Tropical Medicine and Rehabilitation Sciences, James Cook University
2Queensland Children's Medical Research Institute
3Royal Children's Hospital, Centre for Burns and Trauma Research, School of Medicine, University of Queensland
Re Infant Abusive Head Trauma incidence in Queensland, Australia Kaltner et al doi:10.1136/injuryprev-2012-040331
Head trauma in children, particularly as a consequence of abuse, is an important issue and we support the need for interventions in this area. We would however like to clarify some potentially misleading information published in the article by Kaltner et al, regarding the incidence of abusive head trauma (AHT) in Queensland in relation to other serious childhood trauma such as drowning and low speed vehicle run-overs (LSVROs).
Kaltner et al estimated that the incidence rate for AHT (as defined by death or admission to hospital for greater than 24 hours) among children aged 0-2 yrs in Queensland during 2005-2008 was 6.7 per 100 000 per annum. Kaltner argued that the incidence rate for AHT was higher than that for drowning and LSVROs. However, the references used for incidence rates related to drowning and LSVROs are not comparable in several respects. Firstly, there is a 10 year gap between the incidence rates for LSVROs and drowning referenced by Kaltner et al, and the calculated AHT incidence rates. The Mackie1 data on drowning are derived from 1992-1997, and the data on LSVROs from the Queensland Council on Paediatric Morbidity and Mortality2 relate to 1994-1996. Secondly, the incidence rates for drowning and LSVROs referred to by Kaltner relate to fatalities, whereas the incidence rates calculated for AHT relate to hospital admissions and fatalities. Thirdly, Kaltner et al used data relating to 0-4 yr old children in their incidence rate calculations, whereas the referenced incidence rates for drowning and LSVRO relate to 0-5 yr olds (drowning) and 0-4yr olds (LSVRO), respectively. We suggest that for these three reasons, it is not appropriate to compare incidence rates calculated for AHT and drowning / LSVROs.
We present for alternative consideration incidence rates calculated from two recently completed studies on drowning and LSVROs funded by the Queensland Injury Prevention Council. In these studies, data from multiple sources (death, hospital admission, Emergency Department presentation, ambulance) were linked to calculate incidence rates for fatal and nonfatal drowning (2002-2008) and LSVRO incidents (1999-2009)3-4. From data collected for these two studies, we have calculated incidence rates for drowning and LSVROs using the same definitions employed by Kaltner et al for AHT (i.e., fatalities and admission to hospital for 24hrs or more), for 0-2 yr old children in Queensland, for the same time period (2005-2008). The comparable incidence rates (IR) are as follows: drowning IR = 65.27 per 100 000 per annum; LSVRO IR = 42.06 per 100 000 per annum. These incidence rates are much higher than those referenced by Kaltner et al (drowning – 4.6; LSVRO 2.4).
This information is yet to be publicly released, and highlights the value of linked data when exploring injury issues. The difficulties associated with obtaining these data may explain why Kaltner et al reported incidence rates that were not directly comparable. This also reinforces the importance of defining serious injury to allow comparison of like with like5.
There is currently no linked health dataset in Queensland. Linked data to obtain accurate, contemporary and crucial information regarding injury are only available on a project by project basis, when specific funding, ethical approval, and access approval (via the Director General of Queensland Health), are obtained. In addition, funding for the Queensland Trauma Registry was terminated, thus losing another vital source of information about injury in Queensland. As highlighted earlier this year in this journal, reliable information about injuries fundamentally underpins good injury prevention6
There is no doubt that AHT among young children is an important issue and one that deserves increased attention and focus on prevention. However this does not diminish the importance of other causes of serious and fatal injury among young children, such as drowning and LSVROs. We advocate for urgent attention on better data collection regarding serious injury in Queensland to facilitate prevention strategies for all injury among children.
1. Mackie IJ. Patterns of Drowning in Australia, 1992-1997. Medical Journal of Australia; 1999; 171:587-90.
2. Queensland Council on Obstetric and Paediatric Morbidity and Mortality. Maternal, Perinatal and Paediatric Morbidity and Mortality 1994-1996. Brisbane: Queensland Council on Obstetric and Paediatric Morbidity and Mortality. Brisbane, 1998.
3. Kimble R, Wallis B, Nixon J, Watt K, Cass D, Gillen T & Griffin B. 10 Year Review of Low Speed Vehicle Run-Overs in 0-15 years across Queensland. Injury Prevention; 2010; 16 (Suppl 1): A1-289.
4. Wallis B, Watt K, Franklin R, Nixon JA, Kimble R. Nonfatal drowning in children and young people in Queensland (Australia) 2002-2008. Injury Prevention; 2010; 16 (Suppl 1): A138
5. Langley J, Cryer C. A consideration of severity is sufficient to focus our prevention efforts. Injury Prevention; 2012; 18(2) 73-74.
6. Langley JD, Davie GS, Simpson JC. Quality of hospital discharge data for injury prevention. Injury Prevention; 2007; 13: 42-44.
Still more errors and omissions
When Lusk et al. submit to the editor a formal list of errata to be attached to their article, I expect they will duly correct all the errors, omissions, and false statements that have been brought to their attention, and not just the three they chose to mention here. This would include amongst other items providing a correct explanation for their choices of particular termination points (rather than the nonsensical one found in footnote 2 to their Table 1), and retracting their false statement that the path and comparison streets have similar cross traffic and numbers of intersections. And as I also already objected, the authors need to explain how they got the usage data for the year 2000 they claim to have for the de Maisonneuve path segment. Considering that no municipality maintains automatic counters there, and that the authors' study was not underway in 2000, contrary to their claim it would seem they do not have data as they describe for that year.
Since I expect the authors will do their duty and correct these faults, I use the space remaining to correct two new errors they have introduced, and to object further.
(1) The path segment they claimed to have studied from 1999 to 2008 but that did not exist for almost the entirety of that period was created in 2007, not 1997.
(2) The corresponding length correction would have been approximately 180 metres, if they had gotten the extra length right to begin with. They did not, and so the correction should be instead approximately 350 metres. The authors are yet to explain how they got their lengths.
(3) The authors tell us not to worry about their selections of comparison streets: these were done "a priori, without knowledge of their safety record, in consultation with local cycling advocates". In fact the biases are so extreme that they are obvious without any measurement. Who were these sight, smell, and hearing impaired local advocates? Their contribution is not identified in either the contributorship statement or the acknowledgements, and the genesis of the study's path and comparison samples remains as mysterious as ever.
(4) The authors say their failures to describe the radical divergences between their path and comparison streets "do not affect the study results." They need to be reminded that without appropriate comparisons, their study lacks validity. Indeed, showing that a comparison is preposterous does not change the results so calculated: instead, it discredits them.
(5) I object to the authors' claim that "not even one comparison pair showed significantly greater risk" for the path. Let us be clear: even with the biased nature of the comparisons, over the near decade of the study period, according to their methods the actual injury rates on the paths were in three cases respectively 21%, 18%, and 1% worse than on the comparison streets. That none of these were found statistically significant is an indictment of the imprecision of the authors' methods, not an endorsement of the paths. I particularly object to this exploitation of the confusion between statistical and public health significance because I already called the authors on it in my previous criticism.
The authors bemoan the fact that on-street path construction has been "hampered" by the AASHTO guidelines, and present their own results as enough against them that it should no longer be discouraged. This summer a cyclist riding on the Christophe Colomb path segment studied by the authors-- a cyclist who did everything right by the rules of the path, and therefore much wrong by the ordinary rules of the road-- was killed by a truck  in circumstances exactly as warned about on page 34 of the AASHTO guidelines .
1. http://www.cbc.ca/news/canada/montreal/story/2012/07/24/montreal-cyclist-hit-24-07-2012.html?cmp=rss, accessed Aug 26 2012.
2. AASHTO Task Force on Geometric Design (1999). Guide for the development of bicycle facilities. Washington, DC: American Association of State Highway and Transportation Officials.
Conflict of Interest:
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