Displaying 1-9 letters out of 166 published
Recompression in water with air supply at shallow depth cannot be superior to breathing pure oxygen on surface
We read with interest the article named 'Prevention and treatment of decompression sickness using training and in-water recompression among fisherman divers in Vietnam' that was published in Injury Prevention 2016 February issue. We want to share our opinion about some parts of the article, especially in three subjects.
It was mentioned that, the aim of the study was to investigate the impact of training programmes run over a period of 3 years, focusing on preventing DCS by reducing unsafe diving practices and treating DCS by means of IWR, in the last sentence of introduction. So we understood that the main subject of the study is forcing fisherman divers to make safe dives resulting in decrease in DCS and also to treat urgently with IWR if disease occurs. Therefore this education only involves lowering DCS and treating with IWR. But it is remarked as "Since implementing IWR training, annual mortality and morbidity incidence rates due to neurological DCS were reduced in our pilot sample" in second sentence of discussion. It was understood from the article, prior to 2009, annual mortality due to diving was estimated 4?1 cases per 1000 fisherman divers and annual incidence of DCS was 8?2 cases. Between 2009 and 2012 fatality rate dropped 1 per 1000 divers and annual incidence of DCS dropped 2?1 per 1000 divers. However we know it is unlikely to have a mortality rate of four cases in every eight DCS cases before 2009 and also one fatal case within two cases of DCS between 2009 and 2012. Many studies was reported before about this issue, in one of them Xu et al. showed nine deaths of 5278 consecutive DCS cases with a incidence of 0.17% in a decade (1). It seems suspicious that one in a two cases DCS mortality rate as mentioned in the article. Probably the mortality reasons must be other than DCS, e.g. drowning, nitrogen narcosis and diving related accidents, before 2009 and also between 2009 and 2012 in these dive sites. We found it very challenging; two days 10 subjects IWR training courses reduced annual mortality rates due to the DCS.
On the other hand, in the treatment of DCS, there appears three main goals;  immediate reduction in bubble size,  to increase the washout of inert gas and  to provide oxygen delivery to the tissues to restore normal functions (2). If we put an order in terms of treatment efficacy; standart recompression treatment in chamber (oxygen, 45-60 feet), IWR with oxygen, breathing oxygen at surface, IWR with air at working depth (fisherman divers' traditional IWR), IWR with air (Clipperton Protocol, 9 m.) had superiority each other, respectively in the treatment of DCS. It is well known that, in the absence of a hyperbaric chamber treatment, IWR with oxygen of course superior to breathing oxygen at surface in DCS. Known risks of IWR are drowning, applying difficulties, hypothermia and disability to transfer patient to chamber because of being underwater. It has been shown that IWR with air at 9 meters has no significant benefit in DCS; also authors mentioned in the article IWR with air is useless which the fisherman divers used to do traditionally. Nevertheless authors advised to divers apply IWR with air at nine meters, which is the last choice in treatment of DCS but they did not mention exactly why divers should follow this protocol. If it is done with oxygen it should be helpful but not with air. According to our knowledge IWR with air should not be performed, if it is to be done deep treatment protocols must be chosen, not at shallow depth like nine meters (3).
The last point we want to take attention is that only eight of 24 DCS patients have been treated with oxygen, the rest were treated with air. Unfortunately the number of divers, which were treated with oxygen, is very low. However, two of eight of these patients (%25) started with oxygen but continued with air, because the cases were not able to breathe from a second stage regulator. In our opinion, if the rate (%25) is really in high ranges like this, there could be given educations about using hoses without second stage regulator.
Declaration of conflicting interests: The authors declared no conflicts of interest with respect to the authorship and/or publication of this letter. Funding: No author or related institution has received any financial benefit for this letter.
References 1. Xu W1, Liu W, Huang G, Zou Z, Cai Z, Xu W. Decompression illness: clinical aspects of 5278 consecutive cases treated in a single hyperbaric unit. PLoS One. 2012;7(11):e50079. 2. Diving and Subaquatic Medicine, Fifth Edition. Carl Edmonds, Michael Bennett, John Lippmann, Simon Mitchell. 2015. p. 167 3. 6th ed. USA: U.S. Navy Diving Manual, 2008
Conflict of Interest:
A Comment on May et al. (2002)
A survey of jail inmates done by J P May, D Hemenway, and A Hall indicated that, among those who admitted to having been shot, 91% reported having gone to the hospital for treatment. This comment explains why this finding cannot be taken seriously.
Put yourself in the position of a jail inmate who was part of this survey. Most jail inmates are awaiting trial. They are the most legally vulnerable of all criminals - unlike uncaught criminals they are subject to legal punishment, yet unlike prison inmates, the punishment they will receive is still to be determined - the hammer has not yet come down. This is a set of criminals who are understandably obsessed with not looking any more criminal to the authorities than they already appear. How is this relevant to the jail survey conducted by May et al.? Suppose you were a jail inmate who had been shot, but did not seek medical treatment because you were shot while committing a crime, and knew that if did go to the hospital, police would interrogate you as to how you got shot and possibly connect you to the crime.
When such a jail inmate was asked whether they had ever been shot, either of 2 things would happen. The inmate would either accurately answer "yes" or would falsely deny having been shot, for the same reason that they did not seek hospital treatment - they did not want to be connected to the crime they were committing when they were shot. These inmates would not be asked the follow-up question "Did you go to the hospital for treatment of that wound?" They would simply be excluded from further analysis, and therefore would not go into the computation of the percent of the 307 gunshot-wounded inmates who had sought hospital care. Instead, they would erroneously be placed in the set of 1,816 inmates who did not report being shot. This is what is known to researchers as a "censored sample" - the inmates who had been shot while committing a crime and who did not seek hospital treatment would largely be "censored out" of the sample, leaving mostly inmates who been shot in less incriminating circumstances. It is scarcely surprising that many of these 307 inmates had sought medical treatment - those who were relatively "innocent victims" had no reason not to go to the hospital. This sample, however, can tell us nothing about the share of all criminals who are shot who received hospital treatment, and certainly can tell us nothing about the share of those shot by their victims while attempting a crime who received hospital treatment.
Now consider those who accurately reported having been shot, among those who had been shot by their victim while attempting to victimize them, and who consequently did not go to the hospital. These inmates may have been willing to report that they had been shot because they did not anticipate the surveyors asking any follow-up questions, such as the one concerning medical treatment. They were then asked the question as to whether they went to the hospital to get treated. At that point, an inmate of this sort could either accurately answer "no" or lie and answer "yes." How is such an inmate likely to perceive a truthful "no" answer? There is no sensible legitimate reason why an innocent victim of a gunshot wound would not seek professional medical treatment - being shot is a very serious injury, and the medically sensible step is to seek professional treatment of the injury. Only a person with something to hide from the police in connection with that wounding would avoid going to the hospital. The inmate knows this, and knows that the surveyors know it as well. So how likely is it that this inmate, in these legally vulnerable circumstances, would honestly answer "no"? Doing so would be tantamount to confessing to yet another crime that the authorities did not yet know about. Thus, there would be a powerful motivation to falsely answer "Yes," and no strong motivation to accurately answer "No," beyond the inmate's commitment to the general moral norm that one should not lie - a commitment that is likely to be lower in a sample of jail inmates than in the population as a whole.
In sum, (1) the subsample of jail inmates who had admitted having been shot is likely to have excluded most of those who had avoided hospital treatment because they were committing a crime when they were shot, and (2) among those who admitted being shot, few inmates were foolish enough to admit they had not sought medical treatment. Consequently, the claim that 90% of the inmates who had been shot had gone to the hospital cannot be given much credence.
The implicit underlying assumption of the researchers was that one could expect truthful answers from jail inmates who had powerful reasons to not be truthful. To be sure, those who had been shot as innocent victims could afford to seek hospital treatment and could be truthful about doing so when surveyed. These inmates probably account for most of the 316 inmates who reported seeking treatment. In contrast, it is extremely unrealistic to expect truthful answer from those who were shot by their victims while committing crimes that the authorities either did not know about, or did not know the inmate had committed. Inmates have no reason to conceal crimes that the authorities already know about, and prior research shows that they are indeed willing to self-report these offenses in surveys. Crimes for which the offender was never arrested are another matter entirely.
Conflict of Interest:
The author replies
I welcome Stevenson's participation and thank him for providing the counterpoint to my commentary.[1, 2] Naturally I object to much of it, starting with the title. We are not discussing the importance of good science, rather what makes for it.
Stevenson begins by taking us on a philosophical excursion: "The underlying philosophy of science is that of [causal] determinism". Determinism, causal or otherwise, is but one item in an ontology, and ontology is but one component of-- let us acknowledge that there is still no unanimity[4, 5]-- a philosophy of science. Yet apart from noting that transportation systems are systems, in terms of philosophy my commentary concerned exclusively epistemological, methodological and ethical matters. Thus the topic of determinism, and Stevenson's entire introduction, is out of place. I don't know how I could "totally dismis[s] the value of" something I never touched upon.
Instead of facing contemporary problems, Stevenson wishes I had used my limited space to consider epidemiology's history, extolling in particular much cited but nowadays little heeded works of Haddon and Gordon (the bibliographic entry given here for the latter being the correct one). Very well: Gordon emphasised the importance of the accident-prone individual, and that injury could not be effectively prevented without knowing the conditions under which cases occur. To this end "causes are sought through direct investigation of the site of the accident, of the associated circumstances, and of the person who was injured", and further that "The start is through field investigation, individual case study of the patient, the family group, and the immediate surroundings".
Does this sound like the epidemiology of bicycling as we have known it-- or as countenanced by "evidence based medicine"? Or did the authors of highly consequential studies[9, 10, 11] use improvised, never-tested proxies? Upon finding that none of their supposed indicators of crash severity or street dangerousness accounted for the outcomes of interest, did they get the idea that they had missed the real factors; or did they conclude to the contrary that helmets were a virtual panacea and cycle tracks were safe without qualification?
Elsewhere Haddon, citing the work of De Haven, himself famously a crash survivor, emphasised that it was not impact velocity per se, but impact conditions that determined injury outcome, and accordingly placed emphasis on vehicle design. I discussed at relative length the failure of epidemiologists to consider this. Haddon further propounded that "measures which do not require the continued, active cooperation of the public are much more efficacious than those which do", and that operating to the contrary constitutes victim blaming. For the past three decades in the field of bicycling safety, the public health community, with its all-helmets, all the time approach, has devoted effectively all its efforts to violating Haddon's prescriptions.
Stevenson might consider that I am not the first to object to the epidemiological approach to transportation safety. For one, the eminent engineer Hauer already did so, for complementary reasons. Hauer was not unfair: he also skewered his own profession.[13, 14] I recommend the public health community follow his example, and engage in more profound self-criticism, and less profound self-congratulation.
Rather than continue with any of many further objections to Stevenson's counterpoint, let me highlight a hidden agreement. Just as there is no objection to harm reduction in drug policy, there is no objection to evidence-based medicine, each being too vague a platitude. But there is plenty of objection to Harm Reduction, and likewise to Evidence Based Medicine: they are specific, institutionalised implementations of contentious philosophies, albeit wrapped in the corresponding platitudes. Stevenson says I suggest "that epidemiology dismisses mechanism-based reasoning"; I do not. I, and others, observe to the contrary that EBM dismisses mechanism-based reasoning.[8, 15] In concert with other objections, I therefore conclude that, in mistaking the wrapping for the content, epidemiology has institutionalised an unrealistic philosophy (this description was in response to reviewer objection: the original was "primitive"). With his emphasis on causality and mechanism-- each famously trans-empirical, not empirical (the work cited being Stevenson's choice, not mine)-- I am pleased to see that Stevenson agrees.
2. Kary M. Unsuitability of the epidemiological approach to bicycle transportation injuries and traffic engineering problems. Inj Prev (Published Online First 14 Aug 2014). doi:10.1136/injuryprev-2013-041130
6. Haddon W. On the escape of tigers: an ecologic note. Am J Pub Health 1970;60:2239-2234.
7. Gordon JE. The epidemiology of accidents. Am J Pub Health 1949;39:504-515.
8. OCEBM Levels of Evidence Working Group. The Oxford Levels of Evidence 2. Oxford Centre for Evidence-Based Medicine. http://www.cebm.net/index.aspx?o=5653(accessed Dec 2013).
9. Thompson RS, Rivara FP, Thompson DC. A case-control study of the effectiveness of bicycle safety helmets. N Eng J Med 1989;320:1361-1367.
10. Thompson DC, Rivara FP, Thompson RS. Effectiveness of bicycle safety helmets in preventing head injuries: a case-control study. JAMA 1996;276:1968-1973.
11. Lusk AC, Furth PG, Morency P, et al. Risk of injury for bicycling on cycle tracks versus in the street. Inj Prev 2011;17:131-135. doi:10.1136/ip.2010.028696
12. Haddon W. Advances in the epidemiology of injuries as a basis for public policy. Pub Health Rep 1980;95:411-421.
13. Hauer E. On exposure and accident rate. Traf Eng Cont 1995;March:134-138.
14. Hauer E. A case for evidence-based road safety delivery. In: Improving Traffic Safety Culture in the United States - The Journey Forward, pp. 329-343. AAA Foundation for Traffic Safety: Washington, DC, 2007. http://www.aaafoundation.org/pdf/Hauer.pdf(accessed Dec 2013).
15. Clarke B, Gillies D, Illari P, et al. The evidence that evidence-based medicine omits. Prev Med 2013;57:745-747. doi:10.1016/j.ypmed.2012.10.020
16. Rosenberg A. Philosophy of Science: A Contemporary Introduction (2nd ed.), 2005, pp. 35-37, 116-117. Routledge: New York.
Conflict of Interest:
False and Just As False
The question before the reader is this: is Olivier and Walter's reanalysis of Walker's data constructed around the false claim that increasing the sample size increases the risk of Type I errors; or around "increasing power when computing sample size leads to an increase in the probability of a type I error"-- and is the latter claim true or false anyway, if it means anything at all?
There is no space here to properly dispense with this matter, or the many other faults of Olivier and Walter's reanalysis. This is done elsewhere.[5, 6] Instead I confine myself to three observations.
1. "Increasing power when computing sample size" means sample size is a varying output (result), while power is a variable input. Since the probability of Type I errors is claimed to thereby increase, it too is an output. But then no result is forthcoming, because Olivier and Walter are positing one equation in the two unknowns. Thus their counter-assertion here is also false: the Type I error level is left undetermined, free to be chosen as seen fit. And indeed Olivier and Walter saw fit to choose exactly the same criterion for statistical significance as Walker: alpha = 0.05.[1, 2]
How then did Olivier and Walter seemingly give an example where the Type I error rate thereby increased? While purporting to increase power "when computing sample size", in fact they held sample size fixed.
2. Here Olivier and Walter claim an effect size of d = 0.12, and elsewhere d < 0.2, "is trivial by Cohen's definition". That too is false: Cohen never defined any effect size as trivial. He proposed only that d = 0.2 was "small" but not trivial. The numerical example Cohen gave to introduce his concept of d was in fact d = 0.1, without any disparaging remark-- but with the corresponding sample sizes extensively tabulated.
3. Seven millimetres is approximately one-third the diameter of handlebar tubing, and seven centimetres is a vital fraction of the diameter of a human limb, skull, or torso. If after an initial set-up of whatever passing distance, an unexpected excursion of driver or rider changes the gap to 0, and helmet wearing to one either of those distances closer, the contact goes from none to brushing to one with sufficient mechanical purchase to be disastrous. In other words, finding out what effect size is clinically significant or not is the business of the scientist, not the statistician.
I imagine the reader may not yet have enough information to decide which false claim Olivier and Walter's reanalysis is based upon. I also imagine that for most readers, that it is one or another or all of them, is enough.
2. Walker I. Drivers overtaking bicyclists: Objective data on the effects of riding position, helmet use, vehicle type and apparent gender. Accident Analysis and Prevention 2007;39:417-425. doi:10.1016/j.aap.2006.08.010
4. Olivier J, Walter SR. Too much statistical power can lead to false conclusions: a response to 'Unsuitability of the epidemiological approach to bicycle transportation injuries and traffic engineering problems' by Kary. Inj Prev Published Online First: doi:10.1136/ injuryprev-2014-041452
Conflict of Interest:
Children left in vehicles: How unsafe !!
This article brings into prospective a dangerous and habitual practice of leaving infants and children unattended in vehicles and its serious ill effects on health most notably being death. Although the article describes scenario in a developed western setup such incidents are increasingly becoming common in developing Asian countries like India and require immediate attention.
The study addresses an important and often ignored issue of occurrence of hyperthermia in children left unattended in vehicles. There is a strong need that print and social media should bring such shocking occurrences into public domain more piercingly so that people specially parents together with caretakers would become aware of such problems leading to them being more careful and attentive. The community as a whole should bring about basic necessary changes in attitude and perception of individuals to prevent such dreadful events.
We agree with the authors that policy makers and law makers need to take a serious and stringent look into such issues so that timely interventions and strict regulations can be put into place. The community and government should work interactively towards developing guidelines, safety norms and mostly create awareness amongst ignorant parents.
Lastly we would like to state that in a country like India with warm winters and ambient temperatures being high normal in most part of country throughout the year along with little awareness about such a catastrophic phenomenon, a study in Indian context is urgently required.
Conflict of Interest:
"Question about survey data-Table 2"
In Table 2 on page 2 of the manuscript "Seatbelt and child-restraint use in Kazakhstan: attitudes and behaviours of medical university students," the last two questions focus on how often the respondent fastened children appropriately. However, there is no choice for if the respondent never rode with children in the past year. If that was the case the respondents may choose the response "never"-not because they did not fasten the seatbelt or appropriate restraint but did not travel with children. This would lead to false negative findings. In addition, the total N for respondents looks the same as the other questions so it does not appear that filtering took place. Since the sample was young and mostly single it may be they were never in a vehicle with young children.
I am hoping the authors can provide some clarity about this issue
Conflict of Interest:
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 , 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  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  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 .
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 . 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 .
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.
References1. 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.
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- 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. http://john-s-allen.com/blog/?page_id=5705 (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. http://john-s-allen.com/blog/?page_id=5702 (accessed Dec 2013).
- 12. Allen JS. Safe bicycle routes: engineering versus epidemiology. 2013. http://john-s-allen.com/blog/?p=5522 (accessed Dec 2013).
- 13. Bicycle infrastructure and safety. Transport Canada, Urban Environmental Programs: Case Studies in Sustainable Transportation, Issue Paper 90. March 2012. http://publications.gc.ca/collections/collection_2012/tc/T41-1-90-eng.pdf (accessed Dec 2013).
- 14. City of Vancouver. Downtown Separated Bicycle Lanes Status Report, Spring 2012. June 5 2012. http://bikeroute.files.wordpress.com/2012/06/downtown_lanes_report.pdf (accessed Dec 2013).
- 15. Aultman-Hall L, Kaltenecker MG. Toronto bicycle commuter safety rates. Accident Analysis & Prevention 1999;31(6):675-86.
- 16. Boufous S, de Rome L, Senserrick T, Ivers RQ. Single- versus multi- vehicle bicycle road crashes in Victoria, Australia. Inj Prev doi: 10.1136/injuryprev-2012-040630.
- 17. Chipman ML, MacGregor CG, Smiley AM, Lee-Gosselin M. Time vs. distance as measures of exposure in driving surveys. Accident Analysis & Prevention 1992;24:679-684.
Conflict of Interest:
Removed: Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems - Part IIThis e-letter was removed because it significantly exceeded the maximum word count permitted.
Removed: Vulnerabilities of the case-crossover method as applied, and unsuitability of the epidemiological approach, to transportation injuries and traffic engineering problems - Part IThis e-letter was removed because it significantly exceeded the maximum word count permitted.
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