This originally appeared at https://journals.sagepub.com/doi/full/10.1177/20503245211055381
The development of drug driving policies should rest on sound epidemiological evidence as to the crash risks of driving after using psychoactive drugs. The findings from individual studies of the increased risk of crashing from the acute use of cannabis range in size from no increase (and perhaps even a protective effect) to a 10-fold increase. Coherent cannabis-driving policies cannot readily be developed from such an incoherent evidence base. A weighted average measure of risk, as provided by a meta-analysis, might be useful. However, if the range of risks found in the cannabis-crash studies reflects the different ways that a variety of biases are being expressed, then the simple application of a meta-analysis might provide little more than an average measure of bias. In other words, if the biases were predominantly inflationary, the meta-analysis would give an inflated estimate of crash risk; and if the biases were predominantly deflationary, the meta-analysis would give a deflated estimate of risk.
We undertook a systematic search of electronic databases, and identified 13 culpability studies and 4 case–control studies from which cannabis-crash odds ratios could be extracted. Random-effects meta-analyses gave summary odds ratios of 1.37 (1.10–1.69) for the culpability studies and 1.45 (0.94–2.25) for the case–control studies. A tool was designed to identify and score biases arising from: confounding by uncontrolled covariates; inappropriate selection of cases and controls; and the inappropriate measurement of the exposure and outcome variables. Each study was scrutinised for the presence of those biases, and given a total ‘directional bias score’. Most of the biases were inflationary. A meta-regression against the total directional bias scores was performed for the culpability studies, giving a bias-adjusted summary odds ratio of 0.68 (0.45–1.05). The same analysis could not be performed for the case–control studies because there were only four such studies. Nonetheless, a monotonic relationship was found between the total bias scores and the cannabis-crash odds ratios, with Spearman’s rho = 0.95, p = 0.05, indicating that the summary odds ratio of 1.45 is an overestimate. It is evident that the risks from driving after using cannabis are much lower than from other behaviours such as drink-driving, speeding or using mobile phones while driving. With the medical and recreational use of cannabis becoming more prevalent, the removal of cannabis-presence driving offences should be considered (while impairment-based offences would remain).
The purpose of this review is to evaluate the epidemiological evidence for the causal role of the acute use of cannabis on the risk of being involved in a road crash. We excluded studies where the use of cannabis was not measured through the presence of delta-9-tetrahydrocannabinol (THC) in oral fluid, blood or urine. This involved the exclusion of studies that detected only the presence of THC metabolites such as THC acid, which are known to still be detectable long after the effects of intoxication have subsided (if intoxication is experienced at all). However, we need to stress that even the presence of THC in biological specimens does not automatically imply acute intoxication. We include studies that employ one or other of the two most commonly used ways of studying the role of drugs in crash causation: culpability studies and case–control studies. In a culpability study (also known as a responsibility study), the prevalence of a drug in drivers who were culpable for the crashes they were involved in is compared with its prevalence in drivers who were not culpable for their crashes. If a drug plays a causal role in the crashes, its prevalence will be greater in the culpable drivers than in the not culpable drivers. In a case–control study, the prevalence of a drug in ‘cases’ (crashed drivers) is compared with its prevalence in ‘controls’ (such as drivers who are randomly interviewed and tested for drugs at petrol stations). If a drug plays a causal role in the crashes, its prevalence will be greater in the cases than in the controls. The outcome measures are odds ratios (ORs), which, for most purposes, can be considered equivalent to relative risks (RRs). The only drug of interest in this review is cannabis. We use the general term ‘cannabis-crash OR’ to include the outcomes from both culpability and case–control studies. But, when referring specifically to culpability studies, the term ‘cannabis-culpability OR’ is sometimes used.
Wide range of estimated cannabis-crash risks from single studies
Published cannabis-crash ORs range in size from 0.46 (0.2–1.3) (Williams et al., 1985) to 10.88 (6.4–18.4) (Del Balzo et al., 2018). Based on the findings of very low cannabis-crash risks by Williams from the US and other early US and Australian researchers, Drummer (1995: 13) advised the Road Safety Committee of the Parliament of Victoria that ‘Cannabis showed a negative effect on relative risk suggesting that cannabis use actually reduced the culpability rate. This may suggest either that cannabis is protective and actually increases driving ability, or, more likely, that drivers taking cannabis over-compensate for any loss of driving skills’. In contrast, Del Balzo et al. (p. 71) advised that their own finding of a very high cannabis-crash risk ‘supports the use of urine testing for cannabis in the procedures for issuing a driving licence’. In the face of an incoherent evidence base, a road safety policy advisor might be at a loss as to how to assess the size of the threat posed by cannabis-driving. However, it is obvious that to focus on only a single study or a small number of studies could be misleading. It might therefore be assumed that a weighted average measure of risk, as provided by a meta-analysis, would be useful. That assumption is discussed in the following two sections, where some problems with the uncritical use of meta-analytical results are considered.
Quality assessment (QA) in published meta-analyses of the cannabis-crash relationship
Four systematic reviews with meta-analyses have been conducted by research groups from different countries on the relationship between the recent use of cannabis and the risk of crashing (Asbridge et al., 2012, from Canada; Li et al., 2012, from the US; Rogeberg and Elvik, 2016a, from Norway; and Hostiuc et al., 2018a, from Romania). All four reviews considered the quality of the included studies.
From their meta-analysis, Asbridge et al. (2012) obtained a summary unadjusted cannabis-crash OR of 1.92 (1.4–2.7). They assessed the quality of their nine included studies using the Newcastle–Ottawa Scale (NOS; Wells et al., 2020), which comprises items that assess three quality domains: the selection criteria for cases and controls; the comparability of the case and control groups; and the appropriateness of the means of measuring the exposure (e.g. cannabis use) and outcome (e.g. crash involvement) variables. These three domains are all relevant to the methodological rigour of the studies. The reviewers identified four studies as high quality, and five as medium quality, but none as low quality. They reported that the high-quality studies had a slightly higher summary cannabis-crash OR than the medium quality studies, although the difference was not statistically significant.
From their meta-analysis, Li et al. (2012) obtained a summary unadjusted cannabis-crash OR of 2.66 (2.1–3.4). They assessed the quality of their nine included studies using the Public Health Critical Appraisal Checklist (PHCAC; Heller et al., 2008). The PHCAC comprises some items that cover the same ground as the NOS, but also includes items to measure the usefulness of the findings in the context of public health. Some of the additional items measure: whether or not the research question is stated clearly; whether or not the results are presented clearly; and whether or not the public health implications of the study have been adequately discussed. The reviewers reported that all of the included studies were of ‘high quality and credibility’ (p. 67), so they could not provide separate summary cannabis-crash ORs for different levels of quality. Their assessment of quality failed to acknowledge that five of the nine studies involved self-reported drug use, and were therefore likely to have been seriously compromised by under-reporting (see Eichelberger and Kelley-Baker, 2020).
Rogeberg and Elvik (2016a) ‘revisited’ the meta-analyses conducted by Asbridge et al. (2012) and by Li et al. (2012) and found them to be defective in a number of respects. In particular, they criticised both research groups for including unadjusted cannabis-crash ORs in preference to adjusted ORs, and thereby inflating their summary cannabis-crash ORs. Most egregiously, both meta-analyses included the unadjusted cannabis-crash OR of 7.16 (2.8–18.5) for Blows et al. (2005) instead of the much smaller adjusted value of 0.80 (0.2–3.3).
From their own meta-analysis, Rogeberg and Elvik (2016a) obtained a summary adjusted cannabis-crash OR of 1.36 (1.2–1.6). They conducted QA of the included studies using a four-item measure of quality that had been developed by Elvik (2013) specifically for application to drug-crash studies. Only two of the four items, the adequacy of the measure of drug use and the adequacy of the controls for confounding factors, were straightforward measures of methodological rigour. The other two items concerned the authors’ desiderata for a thorough study: the coverage of different crash severities, and whether or not supplementary evidence was provided concerning a possible dose–response relationship between drug concentration and crash risk. Some errors in Rogeberg and Elvik’s quality scores were identified and corrected by Rogeberg et al. (2018), who reported that the 8 high-quality studies had the highest summary cannabis-crash OR, while the 14 medium and 4 low quality studies had similar, but lower, ORs. However, the three 95% confidence intervals (CIs) overlapped considerably, so the quality-based differences failed to achieve statistical significance.
From one of their meta-analyses, Hostiuc et al. (2018a) (as corrected by Hostiuc et al., 2018b) reported a summary adjusted cannabis-crash OR of 1.42 (1.2–1.7). They assessed the quality of the 12 included studies using a multi-item scale they had developed. The scale comprised two types of quality items. The first measured a study’s ‘risk of bias’ (the extent to which the reported cannabis-crash OR was likely to be deflated or inflated), and included items relating to the study’s methodological rigour (similar to the NOS items). The second type measured aspects of quality that the authors considered to be irrelevant to the risk of bias. Those items measured study features such as the number of cases included; the ‘recruitment strategy’; and whether or not the authors had made a proper assessment of the limits of the study. Hostiuc et al., used their scale to classify the quality of each study as either high, medium or low. However, they failed to provide separate summary cannabis-crash ORs for the different levels of quality, so it is not known how the studies’ quality scores relate to their cannabis-crash ORs.
It should be noted that the two meta-analyses that used adjusted cannabis-crash ORs (Hostiuc et al., 2018b; Rogeberg et al., 2018) produced smaller summary cannabis-crash ORs (1.36 and 1.42) than the two that used unadjusted cannabis-crash ORs (Asbridge et al., 2012; Li et al., 2012) (1.92 and 2.66). Admittedly, some different studies were included in the different meta-analyses. Nevertheless, it seems reasonable to conclude that uncontrolled confounding can inflate the size of a cannabis-crash OR, and that the use of statistical controls for confounding can reduce the inflationary bias.
Beyond QA to the directional risk of bias
As discussed above, each of the four systematic reviews used a different QA tool. Asbridge et al. (2012) and Li et al. (2012) used readily available QA tools that were broad in scope, while Rogeberg and Elvik (2016a) and Hostiuc et al. (2018a) tailored their own QA tools for use in drug-crash studies. However, the usefulness of QA tools in relation to systematic reviews is limited. While QA scores can be useful in determining which studies are of sufficient merit to be included in a systematic review, they are of little value when used to account for the biases inherent in the included studies (as was attempted in three of the four meta-analyses). The irrelevance of QA scores to the conduct of meta-analyses was recognised in 1994 by the respected epidemiologist Sander Greenland who observed that ‘most quality scoring schemes ignore direction of bias’ (p. 300), and concluded therefore that ‘quality scores are useless and potentially misleading’ (p. 300).
QA tools have undergone two evolutionary steps to make them relevant to the conduct of meta-analyses. The first is to measure only the ‘risk of bias’ to which the study is exposed. Accordingly, QA items that assess methodological rigour are retained, but items that are irrelevant to rigour, such as the usefulness of the study in the context of clinical practice, are not included. However, a further step is required. A non-directional risk-of-bias score is of little value, because it is not just the risk of bias that is relevant, it is also the direction of bias (inflationary vs. deflationary). The desirability of a directional (or ‘quantitative’) risk of bias measure is now widely recognised in the research evaluation literature (see, e.g. Sterne et al., 2016: 4; Lash et al., 2014: 1969).
As will be shown in this review, many of the included studies suffer from one or more biases, most of which tend to inflate their cannabis-crash ORs. A simple meta-analysis would therefore be misleading, as it could not compensate for the inflated values of the ORs. The ultimate aim of this review is to provide an accurate summary cannabis-crash OR for use in guiding the development of drug driving policy and practice. This review therefore includes analyses that compensate for directional study biases. In the words of Lash et al. (2014: 1971), ‘Bias analysis becomes necessary if a reader attempts to draw substantive conclusions beyond those of the original study report, such as in public health policy’. We identified the main categories of bias as (1) uncontrolled confounding, (2) selection bias and (3) measurement error (as discussed in some detail in our Methods and results section and in our two appendices).
Methods and results: Inclusion and exclusion criteria
Inclusion and exclusion criteria for the study design
There are four main types of potentially relevant epidemiological study designs: culpability, case–control, case crossover and cross-sectional. Our literature search discovered many instances of potentially relevant case–crossover and cross-sectional studies. However, none complied with our full set of inclusion and exclusion criteria. So, our review includes only culpability and case–control studies. Studies are not excluded for having only small numbers of cannabis-positive drivers.
Inclusion and exclusion criteria for the exposure variable
The purpose of the exposure variable is to indicate the recent use of cannabis: it is defined as toxicological evidence for the presence of delta-9-THC in oral fluid, blood or urine. This definition excludes: self-reported (acute) use of cannabis within a few hours of the crash; self-reported (chronic) regular use of cannabis; involvement in a rehabilitation program for cannabis abusers; or information on the therapeutic use of cannabis from pharmaceutical dispensaries or health service providers. The definition of the exposure variable excludes studies where the recent use of cannabis is not based solely on testing positive to THC, but instead includes testing positive for other cannabinoids, such as THC-COOH. Case–control studies would not have been excluded for having different THC cut-offs for the cases and controls: the use of different cut-offs would have been taken into account in evaluating the study’s directional risk of bias. However, as it eventuated, all of the potentially included case–control studies had either the same cut-off for cases and controls where the same matrix was involved or equivalent cut-offs where different matrices were involved (Gjerde and Morland, 2016).
As noted above, we excluded studies where the cannabinoid toxicology did not necessarily identify the presence of THC. As a consequence, we excluded a number of otherwise relevant studies that were based on information from the US Fatality Analysis Reporting System (FARS). The FARS database, which is maintained by the US National Highway Traffic Safety Administration (NHTSA), contains the data from a regular annual nationwide census of fatal crashes. FARS has been operational since 1975 and has collected information on more than 1 million fatal crashes. It has information on over 100 variables that characterises the crash, the vehicle and the people involved. However, a major limitation, from the perspective of the current review, is that the FARS variable that codes for the detection of cannabis fails to distinguish between THC and non-THC cannabinoids (e.g. Hartman and Huestis, 2014). The NHTSA have advised that the FARS information on drugs is so patchy and inadequate that it cannot legitimately be used to ‘make inferences about impairment, crash causation, or comparisons with alcohol‘ (Berning and Smither, 2014: 3). And in further NHTSA advice, Compton and Berning (2015: 1) observed that ‘Current limitations in the FARS dataset do not allow the calculation of unbiased, reliable and valid estimates of the risk of crash involvement that result from drug use’. That advice has recently been endorsed by Gjerde and Morland (2016: 1494). The studies that were excluded from our review because they were based on FARS data are identified in Reference List 2 in Appendix B (see Supplemental material).
Inclusion and exclusion criteria for the outcome variable
For culpability studies, the outcome variable is a dichotomous indicator of whether or not the subject was culpable for the crash that he or she was involved in. For case–control studies, the outcome variable is a dichotomous indicator of whether the subject was involved in a crash or was selected from a non-crashed control group. Evidence for crash culpability or involvement must come from official sources such as police traffic accident report forms. Studies are excluded if the evidence for crash culpability or involvement was only through self-report. Culpability studies are excluded if the outcome variable was not a direct measure of culpability for the crash, but instead identified the causal role in the crash of one or more unsafe driving actions (UDAs), such as excessive speeding.
Inclusion and exclusion criteria where there are multiple cannabis-crash ORs from a single research program
In the case of multi-jurisdictional studies where jurisdictional results were reported separately as well as being summarised in an overall report, we use the overall cannabis-crash OR, rather than the full set of jurisdictional ORs. Where the findings from a single study were reported in a number of different publications, only the results from the most recent publication are normally included, because the earlier publications may be based on less than the full set of subjects. For any study that provided both an unadjusted (i.e. based on raw counts data) cannabis-crash OR and an adjusted (i.e. based on a multiple logistic regression) OR, only the adjusted OR is included. Where the only available cannabis-crash OR was unadjusted, it is included. If a study provided separate cannabis-crash ORs for different THC concentration ranges, as well as an overall OR, only the overall OR is included. Further details on these particular inclusion and exclusion criteria are provided in Appendix B (see Supplemental material).
Methods and results: Literature search
A formal search strategy for the peer-reviewed journal literature was developed by NB in consultation with a Research Librarian from the University of Adelaide. The search was restricted to papers written in the English language, and published up to 27 February 2020. Key search terms included, for example, ‘traffic accidents’ OR ‘motor vehicles’ OR ‘cars’ OR ‘automobile’ OR ‘road’ AND ‘accident’ OR ‘crash’ OR ‘collision’ OR ‘injuries’ OR ‘fatal’ AND ‘Cannabis’ OR ‘Cannabinoids’ OR ‘Marijuana’ OR ‘tetrahydrocannabinol’. The search terms were optimised for each of the four databases searched: PubMed, PsycInfo, Embase and Scopus. The complete search terms for each database are provided in Appendix B (see Supplemental material). The formal search strategy was supplemented with hand searching by MW for publications that met the inclusion and exclusion criteria except that they were not restricted to journal articles. The literature search is summarised in Figure 1.
Hand searching within the non-journal literature can provide a valuable contribution to an overall search strategy. A study by Lacey et al. (2016) that was commissioned by the US NHTSA is one of the most rigorously conducted and influential studies in this field (see, e.g. Rosekind et al., 2020), but it has not been published as a journal article. Hostiuc et al. (2018a) failed to include it in their meta-analysis because their search strategy did not incorporate hand-searching.
There were 1967 journal article records identified in the formal journal search, and 986 duplicates removed, leaving 981 records to be screened for eligibility (Figure 1). In the first stage of screening, based on titles, keywords and abstracts, 807 records were excluded because they were easily recognised as being outside the scope of our review. Some were animal studies; some were drug prevalence studies; and some were studies of cannabinoid pharmacology. Full-text copies of the journal articles were obtained for the remaining 174 records. They were assessed for eligibility in the second stage of screening, in terms of the criteria described above for the exposure and outcome variables. We excluded 138 of the articles because they clearly either failed to meet any of the inclusion criteria or they met at least one of the exclusion criteria, leaving 37 to be included in the review. These 37 articles from the formal journal search were supplemented by 17 articles from hand-searching, only 2 of which were journal articles, with the others comprising 8 technical reports, 6 conference papers and 1 book chapter. At that stage of the literature search, 54 articles had been identified that explored a relationship between the recent use of cannabis, as determined toxicologically, and involvement in a road crash. References for the 54 articles are provided in Appendix B (see Supplemental material). For some of the articles, the toxicological identification of the recent use of cannabis involved testing positive to cannabinoids other than THC. And for some others, more than one article was published from a single study. When those and other exclusion criteria were taken into account, 13 articles remained that described the results of culpability studies, and 4 that described the results of case–control studies. The reasons for excluding all but 17 articles from the list of 54 are provided in Appendix B (see Supplemental material). All of these processes were conducted independently by MW and NB, but with collaboration and agreement at each stage, before progressing to the next stage.
Methods and results: Assessment of the directional risk of bias
Appendix A (see Supplemental material) provides our attempt to identify the main biases that could distort the cannabis-crash ORs reported in the epidemiological literature. Most of the identified biases could be classified as being due to: (1) uncontrolled confounding, (2) the inappropriate selection of subjects or (3) errors in the measurement (or definition) of the cannabis exposure variable or the crash outcome variable. Individual biases within those three types were investigated only where the expected direction of the bias (inflational or deflational) was evident from the published literature. This point needs to be emphasised. For example, in the case of uncontrolled confounding, many more than the four identified confounders (see below) have been discussed in the literature. But to be included in our bias analyses there had to be sufficient published evidence to estimate the strength of the bias as well as its direction.
Four major sources of confounding were identified: age, sex, co-use of alcohol and time of day. All are inflational. Modelling summarised in Appendix A (see Supplemental material) indicates that the biasing effects of unadjusted confounding are not as potentially strong as for the other types of bias, and even the strongest confounder is unlikely to increase a cannabis-crash OR of 1.00 to more than about 1.30.
Alcohol and other psychoactive drugs are the potential confounders that are of most concern to researchers. But because they are of such concern, they are usually adequately controlled for, either by the conduct of subgroup analyses (where co-users are excluded) or through multiple logistic regression analyses (where the presence of alcohol and other drugs is controlled for statistically). As it eventuated, only 1 of the 17 studies (Mura et al., 2003) failed to control for alcohol. That failure contributed to Mura et al.’s total bias score (see Table 1, and Appendix B, Supplemental material, Table B8). Similarly, only 2 of the 17 studies (Gadegbeku et al., 2011; Mura et al., 2003) failed to control for other major types of drugs. However, those failures did not contribute to those studies’ total bias scores, because not enough is known about the circumstances of the co-use of cannabis and other drugs to enable the quantitative calculation of directional bias scores. It could be assumed that any such other drug biases would be inflationary. Consequently, the total bias scores for those two studies (Table 1) could be underestimates.Table 1. Details of the studies included in the meta-analyses.
|Study (date)||Country||Culpability or Case–control||N (THC + ve)a||OR (95% CI)||OR type||Total bas score|
|Terhune (1982)||US||Culp||17||2.14 (0.8−5.7)||Unadj.||2|
|Williams et al. (1985)||US||Culp||19||0.46 (0.2−1.3)||Unadj.||1|
|Terhune et al. (1992)||US||Culp||19||0.66 (0.3−1.6)||Unadj.||3|
|Longo et al. (2000)||Australia||Culp||44||0.82 (0.5−1.5)||Unadj.||3|
|Lowenstein and Koziol-McLain (2001)||US||Culp||<11c||0.70 (0.1−3.3)||Adj.||0|
|Mura et al. (2003)||France||CC||137||1.91 (1.3−2.7)||Unadj.||8|
|Drummer et al. (2004)||Australia||Culp||56||2.70 (1.0−7.0)||Adj.||7|
|Gadegbeku et al. (2011)||France||Culp||650b||1.43 (1.2−1.7)||Adj.||4|
|Ogden et al. (2011)||Australia||Culp||35||1.76 (0.9−3.6)||Unadj.||8|
|Bernhoft et al. (2012)||Four EU countries||CC||91||1.25 (0.5−3.5)||Adj.||5|
|Hels et al. (2013)||Four EU countries||CC||162||1.91 (1.2−3.2)||Adj.||7|
|Poulsen et al. (2014)||New Zealand||Culp||314||1.29 (0.8−2.3)||Adj.||2|
|Drummer and Yap (2016)||Australia||Culp||102||2.97 (1.5−6.0)||Unadj.||5|
|Lacey et al. (2016)||US||CC||613||1.00 (0.8−1.2)||Adj.||−1|
|Martin et al. (2017)||France||Culp||325||1.65 (1.2−2.3)||Adj.||4|
|Brubacher et al. (2019)||Canada||Culp||165||1.07 (1.0−1.2)||Adj.||3|
|Drummer et al. (2020)||Australia||Culp||90||1.90 (1.2−3.1)||Adj.||5|
OR: odds ratio; THC: tetrahydrocannabinol.
For case–control studies, this is the total number of THC-only cases and THC-only controls (see Appendix B, Supplemental material, for details).
The exact number of THC-positive subjects is not known, but from information provided by Laumon et al. (2005), in a table on p. 2, it seems likely that the number is about 650 (for a THC cut-off level of 1 ng/ml).
N = 34 drivers were initially identified through the presence of non-psychoactive cannabinoids in urine. In follow-up toxicological analyses, an undisclosed number (10 or fewer) tested positive for THC.
The three types of agents responsible for selection biases were identified as: (1) government authorities (such as the police) or hospital administrators; (2) the subjects themselves (self-selection); and (3) the researchers – through the way that the cases and controls (or culpable and not-culpable drivers) had been defined. Evidence is provided in Appendix A (see Supplemental material) that selection biases can be much stronger than confounding biases. A cannabis-crash OR of 1.00 could easily be increased to 1.50 or more by a selection bias. As it eventuated, all of the selection biases were inflationary, except for a self-selection bias in the case–control study by Lacey et al. (2016), where the crashed (case) drivers were allowed to refuse a drug test, and did so more frequently than the control drivers.
Measurement biases arise from the inappropriate definition or measurement of either the cannabis-exposure variable or the crash-outcome variable. A number of such biases are discussed in Appendix A (see Supplemental material), where all but one was deemed not to be relevant to the studies under consideration here. The exception is an inflationary bias where the assessments of the drivers’ culpability were not made independently of knowledge about the drivers’ toxicological results.
One potential type of measurement bias that has received considerable attention in the cannabis-crash literature (e.g. Gjerde and Morland, 2016) is the deflationary bias from the use of a low THC cut-off threshold in the definition of a cannabis-positive subject. The concentrations of THC in blood and oral fluid are at their peak soon after using cannabis. They then fall rapidly for two or three hours, but may not reach a zero baseline until many hours later, or perhaps even days later for heavy users (Odell et al., 2015; Spindle et al., 2019). If there is a positive relationship between the use of cannabis and the risk of crashing, then the risk will presumably be greatest very soon after using cannabis and then fall to a baseline level over the following few hours. If the toxicological testing for THC involves a high cut-off threshold, and therefore a short detection window of only three or four hours, then only the recent users will be detected, and the size of the cannabis-crash OR will be maximal. But if the testing involves a low THC cut-off threshold, and therefore a long detection window of many hours, then many non-recent users will be detected, and the size of the cannabis-crash OR will be smaller. This deflationary bias can be called the ‘low-threshold bias’. At this point, it is necessary to distinguish between two possible alternative definitions of the cannabis-exposure variable. The first is the definition as used in this review: testing positive to THC in a body fluid, as an indicator of the previous use of cannabis. This is the ‘conventional’ definition, as used in practice in the studies under review here and in previously published systematic reviews of similar studies. The cannabis-crash OR for such drivers can be called the ‘conventional’ OR. The alternative definition of the cannabis-exposure variable identifies only those drivers who have used cannabis so recently (within, say, the previous 4 h) that they are likely to be impaired. The cannabis-crash OR for such drivers can be called the ‘intoxication’ OR. Both the conventional OR and the intoxication OR are theoretically legitimate measures of the risk of crashing. However, the intoxication OR is obviously impossible to obtain using available toxicological techniques. The two measures should not be confused. In that context, we believe that it was appropriate for Gjerde and Morland (2016) to criticise Rogeberg and Elvik (2016a) for claiming that their conventional review of the cannabis-crash literature was an investigation of ‘The effects of cannabis intoxication on motor vehicle collision’. They were obviously wrong in making that claim, as they later acknowledged (Rogeberg and Elvik, 2016b). In the first sentence of this paragraph, we describe the deflationary bias from the use of a low THC threshold as a ‘potential type of measurement bias’. In doing so, we are not so much questioning the bias’s existence as questioning its relevance to the nature of our review. The low-threshold bias is simply not relevant to a review that employs the conventional definition of the cannabis-exposure variable. While results for the intoxication definition of the cannabis-exposure variable would obviously comprise the best measure of the maximum crash-inducing effect of impairment by cannabis, results for the conventional definition are also very informative, as they are directly relevant to the context of drug driving enforcement as implemented in Australia and in a number of other jurisdictions. Australia, for example, has implemented ‘zero tolerance’ cannabis-presence driving offences whereby it is a punishable offence for a driver to have any trace of THC in their oral fluid or blood, along with widescale roadside drug testing (RDT) regimes. The question naturally arises as to the crash risk that pertains to such offences and regimes. And that is the question that this review is attempting to answer.
One further type of bias that should be considered is a publication bias, which can occur when the formal publication of studies depends on the nature of the findings (Song et al., 2013). As a general rule, studies with statistically significant findings are more likely to be published that those that favour the null hypothesis. The results of meta-analyses can thereby be distorted in the direction of stronger effect sizes. However, all of the studies of interest in this review and most of the studies in the four other reviews considered here (Asbridge et al., 2012; Hostiuc et al., 2018a, 2018b; Li et al., 2012; Rogeberg and Elvik, 2016a) used toxicological evidence to explore the roles of alcohol and other drugs in road crashes – such that strong drug effects will always be found, if only for alcohol. It therefore seems unlikely that publication bias could play a role in these studies. All four of the other systematic reviews included analyses to detect the possible role of publication bias. As we assumed, none found any evidence of such a bias (at least, with respect to those in studies that involved toxicological evidence of cannabis use). However, there is another reason for our lack of interest in publication bias. The types of biases of concern in this review are those that pertain to individual studies, and which can therefore possibly be compensated for in a meta-regression. Publication bias is not of that ilk.
Bias detection and scoring
The seventeen included studies were scrutinised by MW for the presence of directional biases (as identified in Appendix A, Supplemental material), and a draft ‘bias report’ was prepared for each. Where contactable, the corresponding author was sent his or her bias report to check for accuracy. Only one of the authors, Kenneth Terhune, was unable to be contacted (in relation to Terhune, 1982 and Terhune et al., 1992). Feedback was provided by the authors of six of the remaining fifteen studies (Bernhoft et al., 2012; Hels et al., 2013; Lacey et al., 2016; Longo et al., 2000; Martin et al., 2017; Poulsen et al., 2014), and the bias reports were revised accordingly, with minor changes required to three. No response was received in relation to nine of the studies. The final bias report for each study is provided in Appendix B (see Supplemental material), along with any author feedback.
Some aspects of bias scoring are now briefly considered. The four uncontrolled confounding biases were all inflationary, but relatively weak, and were assigned scores of either + 1 or + 2, depending on the type of bias and the circumstances of the study. Because all three types of selection bias were potentially stronger than the confounding biases, and potentially either deflationary or inflationary, they were all assigned a potential score range of −3 to + 3, with the actual scores depending on the type of bias and the circumstances of the study. Only one relevant type of measurement bias was identified. It was the ‘culpability assessment bias’, whereby the culpability assessors, who were inappropriately aware of the drug status of the drivers, could have been influenced by that information. As this type of bias was inflationary and potentially strong, it was assigned a potential score range of + 1 to + 3. Each included study was scored for the presence of every relevant bias– as recorded for the culpability studies in Table B5 from Appendix B (see Supplemental material), and for the case–control studies in Table B8. A total bias score was calculated for each included study, as also recorded in Tables B5 and B8, and as provided here under the heading ‘Total Bias Score’ in Table 1.
Methods and results: Statistical analyses
For each of the seventeen included studies, both authors extracted the relevant study details: the study authors, the year of publication, the location of study, the type of study (culpability or case–control), the severity of the crashes involved (fatal, injury or property-damage-only), the body fluid (matrix) used for toxicological analysis (blood, oral fluid or urine), THC-positive sample size, the OR and 95% CI (extracted or calculated by us), and the OR type (unadjusted/adjusted). Any discrepancies were resolved by discussion. Table 1 provides most of that information, while Table 2 provides the crash severity and the matrix (blood, oral fluid or urine) used for toxicological analysis. Additional details about each study can be found in Appendix B (see Supplemental material).Table 2. Evidence for threshold or dose–response THC effects.
|Study (date)||Crash severity||Body fluid analysed (OF = oral fluid)||Significant main effect of THC?||Dose relationship examined?||N THC concentration categories||THC ranges (ng/ml)||Dose relationship claimed?|
|Terhune (1982)||Injury||Blood||No||Yes||2||<3; >3||No|
|Williams et al. (1985)||Fatal||Blood||No||Yes||4||< 1; 1–2; 2–5; >5||No|
|Terhune et al. (1992)||Fatal||Blood||No||No||3||<3; 3–20; >20||No|
|Longo et al. (2000)||Injury||Blood||No||Yes||3||<1; 1–2; >2||No|
|Lowenstein and Koziol-McLain (2001)||Injury||Urine||No||No||1||n/a||No|
|Mura et al. (2003)||Injury||Blood||Yes||Yes||2||<2; >2||No|
|Drummer et al. (2004)||Fatal||Blood||Yes||Yes||2||<5; >5||Yes|
|Gadegbeku et al. (2011)a||Fatal||Blood||Yes||Yes||4||< 1; 1–3; 3–5; >5||Yes|
|Ogden et al. (2011)||Injury||Blood||No||No||1||n/a||No|
|Bernhoft et al. (2012)||Fatal||Blood||No||No||1||n/a||No|
|Hels et al. (2013)||Injury||Blood/OF||Yes||No||1||n/a||No|
|Poulsen et al. (2014)||Fatal||Blood||No||Yes||3||<2; 2–5; >5||No|
|Drummer and Yap (2016)||Fatal||Blood||Yes||No||1||n/a||No|
|Lacey et al. (2016)||Range||Blood||No||No||1||n/a||No|
|Martin et al. (2017)||Fatal||Blood||Yes||Yes||4||<1; 1–3; 3–5; >5||No|
|Brubacher et al. (2019)||Injury||Blood||No||Yes||4||0; 0–2; 2–5; >5||No|
|Drummer et al. (2020)||Injury||Blood||Yes||Yes||3||<1; 1–5; >5||Yes|
These results are not actually from Gadegbeku et al. (2011), but are from the same study, as reported by Laumon et al. (2005).
The cannabis-crash ORs obtained from culpability and case–control studies are considered to provide measures of fundamentally different outcomes. No attempt is therefore made to mathematically convert a cannabis-crash OR from one type of study to its apparent equivalent in the other – as was done by Rogeberg and Elvik (2016a) and Rogeberg (2019). In other words, the thirteen culpability studies and four case-control studies are treated separately in this review (except when exploring the possibility of dose effects – see later).
The main statistical goal of our review was to provide two summary cannabis-crash ORs: one for the thirteen culpability studies and one for the four case–control studies. The conventional means of doing so is to use a meta-analysis, whereby a weighted summary (meta-analytic) OR is calculated from the individual study ORs. In a meta-analysis, the weighting for each study’s OR is proportional to the number of observations that contribute to it, and is therefore proportional to its precision as indicated by the narrowness of its 95% CI. The meta-analytic results for the 13 culpability studies are shown in Figure 2, and for the 4 case–control studies in Figure 4. In these figures, the weighting of each cannabis-crash OR is indicated by the size of the black square that represents it. For example, from Table 1, it can be seen that Brubacher et al.’s (2019) cannabis-crash OR (1.07) has by far the narrowest 95% CI (0.2) amongst the 13 culpability studies. It therefore has the strongest weighting, which is reflected in its relatively large black square as shown in Figure 2. Similarly, Lacey et al.’s (2016) cannabis-crash OR (1.00) has by far the narrowest 95% CI (0.4) amongst the four case–control studies, which is reflected in its relatively large black square as shown in Figure 4.
We chose to use random-effects rather than fixed-effect meta-analyses (see, e.g. Borenstein et al., 2009, Chapter 13). In a fixed-effect analysis it is assumed that the true effect size is the same for all studies, such that a summary cannabis-crash OR from a meta-analysis is an estimate of this common effect size. We could not make that assumption, as we hypothesised that the cannabis-crash ORs from many of the studies were seriously affected by various biases. So, we used random-effects analyses where it is assumed that the true effect size varies from one study to the next, and that the studies represent a random sample of the biasing effects that could have been observed.
We acknowledge that two recent reviews (Hostiuc et al., 2018a, 2018b; Rogeberg, 2019) have adopted different approaches to obtaining summary cannabis-crash risk effect sizes. Hostiuc et al., used the inverse variance heterogeneity model (Doi et al., 2015) instead of a random effects model. Their model is proposed to overcome some known shortcomings of random effects models with respect to weighting of larger versus smaller studies and the precision of model estimated CIs. Rogeberg used a Bayesian model to estimate total crash risk from culpability studies. These two approaches represent a potential advance over standard approaches but for our purposes we wished our analyses to be comparable with those of previous studies of cannabis-, alcohol- and other crash risks.
A secondary statistical goal of our review was to provide two bias-adjusted summary cannabis-crash ORs: one for the thirteen culpability studies and one for the four case–control studies. The conventional means of making such adjustments is through a meta-regression, where the influence of each study’s OR on the shape of the modelled regression equation is proportional to its precision as indicated by the narrowness of its 95% CI. In our culpability meta-regression, the relationship between the extent to which a study suffered from inflational biases and the study’s cannabis-culpability OR was modelled by a regression equation from which a prediction was made as to the value of the OR in the absence of any bias (i.e. the modelled OR value corresponding to a total bias score of zero). The results of our meta-regression for the 13 culpability studies are shown in Figure 3. Unfortunately, as described below, a meta-regression could not be conducted for the four case–control studies, so an alternative analysis was conducted, as depicted in Figure 5.
We do not report p-values for our ORs. Instead, we use the conventional rule of thumb that an OR is statistically significant if its 95% CI does not include the value 1.00.
Culpability studies: Forest plot for studies of cannabis-culpability risk
The cannabis-culpability ORs, with their 95% CIs, from the 13 culpability studies are shown in Figure 2. The ORs ranged from 0.46 to 2.97. Eight studies reported ORs that were not statistically significant (where the 95% CI included an OR of 1.00). In six of the studies the ORs were unadjusted. The meta-analytic summary OR from the model was 1.37 (1.10–1.69). The 13 effect sizes were heterogeneous Q (12) = 34.0, p < 0.001 and I2 = 64.7% indicating moderate-to-high heterogeneity, as would be expected if the studies were affected to different extents by different biases.
A meta-regression assessed our directional total bias score as a moderator of the reported cannabis-culpability ORs. For this meta-regression model, the directional total bias score was significantly associated with the cannabis-culpability ORs (Q(1) = 10.3, p = 0.001) and explained 77.9% of heterogeneity. The intercept of the model (i.e. directional total bias score of zero) expressed as an OR was 0.68 (0.45–1.05) (Figure 3).
While we could interpret this result to mean that the best bias-free estimate of the cannabis-culpability OR is 0.68, such that the recent use of cannabis is protective against the risk of being culpable for a crash, we consider that that would be an over-interpretation. Instead, we interpret this result to mean that the null hypothesis cannot be rejected for the effect of the recent use of cannabis on the risk of being culpable for a crash.
Case–control studies: Forest plot for studies of cannabis-crash risk
The cannabis-crash ORs, with their 95% CIs, from the four case–control studies are shown in Figure 4. The ORs ranged from 1.00 to 1.91. Two studies reported ORs that were not statistically significant (95% CI included an OR of 1.0). One OR was unadjusted. The meta-analytic summary OR from the model was 1.45 (0.94–2.25). The four effect sizes were heterogeneous Q (3) = 13.0, p = 0.005 and I2 = 76.9% indicating moderate-to-high heterogeneity.
The small number of included case–control studies precludes meta-regression to assess our directional total bias score as a moderator. Nonetheless, Figure 5 shows a monotonic relationship between the total bias scores and the cannabis-crash ORs, with Spearman’s rho = 0.95, p = 0.05.
The lack of a regression equation makes it difficult to interpet these results. Clearly, the most strongly biased studies have the highest cannabis-crash ORs. Lacey et al. (2016), with a cannabis-crash OR of 1.0, was the only study where an attempt was made to carefully match the individual case and control drivers. We interpret the results in Figure 5 to mean that the null hypothesis cannot be rejected for the effect of the prior use of cannabis on the risk of being involved in a road crash.
The possibility of dose effects
It is possible that one or both of two types of dose effect were present in a study’s cannabis-crash results. The first is a two-phased threshold effect, which involves the absence of any effect of cannabis below a low threshold concentration of THC. The disputed existence of a threshold effect was discussed previously, where it was noted that some published cannabis-crash ORs would be underestimates if sub-threshold drivers had incorrectly been defined as positive for THC. The second type of dose effect was originally described by Hill (1965) as a ‘biological gradient’, but is now better known as a ‘dose-response effect’. Hill proposed ten criteria for inferring that a relationship between two variables is causal rather than accidental. His criteria are still widely cited in epidemiological papers, despite the fact that none of them provides conclusive proof of causality (Rothman and Greenland, 2005). One of the criteria that are very indicative of causality is a dose–response relationship between the exposure and outcome variables. A large volume of research, starting with Borkenstein’s Grand Rapids case–control study in 1964, has clearly demonstrated a dose–response relationship between driver blood alcohol concentration (BAC) and the risk of crashing. Any such relationship for the effect of cannabis on the risk of crashing could be linear or curvilinear, but should at least be positively monotonic. In the context of looking for threshold and/or dose–response effects, it is considered unnecessary to distinguish between culpability and case–control studies. The cut-off levels of THC that are used to define the category boundaries of the cannabis variable are in terms of nanograms of THC per milliliter of body fluid (ng/ml).
The main THC dose results for the seventeen studies are summarised in Table 2. Further details can be found in Appendix B (see Supplementl material). The researchers involved in seven of the studies did not test for either type of dose effect. Given the scientific and applied importance of such effects it is likely that at least some of those studies provided no indicative evidence of the effects, and the researchers decided not to investigate further. Dose effects were explored in 10 studies, but were not found in 7 of them. Three studies provided some evidence for dose effects. Drummer et al. (2004) claimed to have found a THC threshold effect at 5 ng/ml. Their threshold OR of 6.6 had a wide 95% CI of 1.5–28.0. Poulsen et al. (2014) designed their responsibility study as a replication of Drummer et al.’s study. They used more THC-positive drivers than Drummer et al., but failed to replicate the threshold effect. This failure casts doubt about the reliability Drummer et al.’s evidence. The second study, by Gadegbeku et al. (2011), did not report any results that were relevant to possible dose effects. However, Laumon et al. (2005) had previously investigated a major subset of the same crashes that were analysed by Gadegbeku et al., and they calculated cannabis-culpability ORs for four THC concentration subgroups. In their abstract, Laumon et al., claimed that ‘A significant dose effect was identified’ (p. 1). That misleading claim was inappropriately based on the four unadjusted cannabis-culpability ORs (from their Table 3). The four corresponding adjusted cannabis-culpability ORs (also from their Table 3) provide no evidence of a dose effect. The third study is Drummer et al. (2020). In describing their reported dose effect Drummer et al., said ‘The increase in [cannabis-culpability] odds was most apparent at higher blood THC concentrations. At 5 ng/ml and above the OR was 3.2 (p = 0.01), and at THC concentrations of 10 ng/ml and above the OR was 10 (p = 0.03) [not shown in Table 2] indicating that the odds of culpability increase with rising concentrations’ (p. 3). Those findings are rendered dubious by the highly selective nature of the data used in this study (as discussed in Appendix B, Supplemental material).
In summary, dose effects of THC were explored in only ten of the seventeen epidemiological studies. In seven of the ten, the researchers made no claim to have identified a dose effect. In the other three, the researchers did claim to have found dose effects. However, one of the claims was unable to be reproduced in a more powerful replication study, one was not supported by the best available evidence from the study itself, and the third was from a study that investigated a highly selected set of injury crashes. Overall, the evidence for THC dose effects from the 17 studies is unconvincing.
Types of evidence for the risks of drug driving
In 2004, the Australian state of Victoria was the first jurisdiction in the world to introduce stand-alone per se zero-tolerance drug driving offences for illegal psychoactive drugs, including cannabis, along with a large-scale program of random RDT (Boorman and Owens, 2009; Moxham-Hall and Hughes, 2020; O’Halloran, 2010). The introduction of RDT was contrary to the advice from a national Austroads Working Group on Drugs and Driving that there was not a sufficient evidence-base to support it (Potter, 2000). And the sufficiency of the evidence base has continued to be questioned, especially in relation to cannabis (Hall, 2012; Hall and Homel, 2007; McDonald, 2009; Prichard et al., 2010; Quilter and McNamara, 2017; Roth, 2015). One purpose of this review is to establish if there is yet a sufficient evidence base to support the continued inclusion of cannabis as a proscribed drug in Australia’s RDT programs.
For the purpose of this discussion the distinction between ORs and relative risks (RRs) is overlooked, except to note that, where they differ, a positive OR will be larger than the corresponding RR. Illustrations of some of the points made below were taken from the Australian experience. Policymakers who justify the introduction or revision of a drug driving policy in relation to illegal drugs may do so as a means of prosecuting the War on Drugs. If so, the information provided in scientific papers such as this will not be relevant. The fact that Australia’s RDT programs target only illegal drugs is of some concern in that regard.
A five-level hierarchy can be used to describe the scientific merit of the main types of scientific evidence that might be relied upon in the development of drug driving policy, with the more rigorous evidence coming from the higher levels:
The findings from human performance studies.
Drug-crash risks from single epidemiological studies.
Average drug-crash risks from reviews and/or meta-analyses.
Average drug-crash risks from reviews and/or meta-analyses after correction for biases.
Information about drug prevalence lies at the bottom of the hierarchy (level 1). Nevertheless, media releases from Australian ministers with responsibility for drug driving countermeasures frequently refer to drug prevalences amongst driver casualties in support of their policies. For example, when signalling the toughening of some Victorian drug driving laws, the Police Minister said ‘We know that more than half of our deaths on the road at the moment are because of drug-driving. … This is a growing issue; alcohol is a small part now of what we see of deaths’ (Willingham, 2020). In this hyperbolic media statement, the minister was presenting information about drug prevalence (including medical drugs) in a way that could easily be misinterpreted as pertaining to causality. Injured drivers would presumably be found to have high prevalences of caffeine if tested for it. Prevalences are meaningless when presented out of the context of background usage rates.
The relevance of evidence from studies of human performance, at the second level of the hierarchy, is difficult to assess. The use of sensitive laboratory/simulator apparatus and within-subject statistical analyses makes it relatively easy to demonstrate the detrimental effects of a variety of environmental and personal variables on a range of human skills. The common assumption that the statistical significance of a performance decrement implies some level of real-world impairment has been seriously challenged in a book by Macdonald (2019). For example, ‘weaving’, or more precisely the standard deviation of lateral position (SDLP), is considered by many researchers to be a sensitive test of cannabis-related impairment (Bondallaz et al., 2016; Ramaekers et al., 2011; Veldstra et al., 2015). However, the relevance of SDLP performance to crash causation has been seriously questioned by Ginsburg (2019: 611) who pointed out that the use of cannabis increases a baseline SDLP by up to only about 8 cm, which is roughly about 2% of a typical lane width in the US. (In Australia and New Zealand, the recommended lane width for both urban and rural roads is 3.5 m (Fanning et al., 2016), so the use of cannabis would be increasing SDLP by 2.3% of the recommended lane width.) The clear implication of Ginsburg’s calculation is that decrements in SDLP performance are trivial from a road safety perspective. It seems obvious that a distinction needs to be drawn between performance decrements and real-world impairments of safety-relevant skills. The second example is provided. Choice reaction time (CRT) is a frequently studied index of human performance. Der and Deary (2006) have shown that CRTs are highly statistically significantly longer for every 10 years of aging during adulthood. In other words, the CRT performance of 60-year olds is significantly worse than that of 50-year olds, and the CRT performance of 50-year olds is significantly worse than that of 40-year olds, etc… Obviously, these differences are of no relevance to road safety: it has never been proposed that 50-year olds should be barred from driving because of their statistically-significant age-related performance decrements when compared with 40-year-olds. Humans are over-engineered when it comes to most driving-related tasks, such that laboratory demonstrations of statistically-significant performance decrements may be of no real-world significance. Given the dubious relevance of performance studies to an understanding of the risk of driving after using cannabis, the alternative is to use the more directly relevant evidence from epidemiological studies of cannabis-crash risks.
As described in the European Road Safety Decision Support System on Risks and Measures, the first stage in developing an evidence-based road-crash countermeasure program should be to identify risky exposures (e.g. Martensen et al., 2019). That approach is reflected in the third, fourth and fifth levels of the hierarchy. Unfortunately, Australian policy developers rarely make any reference to the epidemiological findings on drug-crash risks. For example, the Victorian Transport Minister’s second-reading speech on the introduction of RDT referred to the facts that illegal drugs were prevalent among fatally injured drivers, and that drugs could cause impairments, without making any reference to the crash risks (Batchelor, 2003). But even a reference to a drug-crash risk can be inappropriate when it is to the cherry-picked results from a single epidemiological study (at the third level in the hierarchy). For example, the Victorian Minister for Roads, in his second reading speech on the introduction of ‘cocktail’ penalties for driving after the combined use of alcohol and illegal drugs, said ‘Research indicates that when drivers combine alcohol with illicit drugs, they are on average 23 times more likely to be killed in a crash compared with drivers who are drug and alcohol free’ (Mulder, 2014). One point to note in passing is that the reported high risk is not pertinent, as it could have been entirely due to the effect of alcohol. More relevantly, the finding was from a single study by Li et al. (2013) that used the US FARS database, which, as discussed above, is considered unfit for the purpose of drug-crash analyses. Furthermore, a broad review of the evidence from a number of studies of the exacerbating effect of cannabis on the effect of alcohol on the risk of crashing showed that the evidence is inconclusive (White, 2017, Part 7 & Attachment E: 135–142).
The development of drug driving policies should be guided by summary drug-crash risks from all of the relevant individual studies, as provided in epidemiological reviews (at the fourth and fifth levels of the hierarchy). But even then, some reviews are better than others at taking study biases into account. The two most frequently cited reviews are by Li et al. (2012) and Asbridge et al. (2012). Li et al., based their summary-cannabis-crash OR of 2.66 (2.1–3.4) on raw counts data in such a way that no biases were corrected for. Asbridge et al., also based their slightly lower summary cannabis-crash OR of 1.92 (1.4–2.7) on raw counts data, but they did at least control for the confounding effect of alcohol by restricting their analysis to drivers who tested negative for alcohol and drugs other than cannabis. The two meta-analyses that used adjusted cannabis-crash ORs (Hostiuc et al., 2018b; Rogeberg et al., 2018) included cannabis-crash ORs from studies that had statistically controlled for the effects of alcohol and drugs, as well as for the main demographic variables, and for various other confounders that were identified by the research teams. However, the current review is the first to provide evidence at the fifth level of the hierarchy, by attempting to adjust for the effects of biases from factors other than just uncontrolled confounders.
Summary of the main findings
Ours is the first review of the cannabis-crash literature to take into account a wide range of potential study biases. The three main types of directional bias involve confounding by uncontrolled covariates; subject selection; and errors in the measurement of the exposure and outcome variables. From some modelling work and other considerations, we conclude that the selection and measurement biases have the potential to be considerably stronger than the confounding biases (for reasons that are explored more fully in Appendix A, Supplemental material). We do not see our approach to bias assessment as being definitive. Rather, we see it as a first step towards the development of a more rigorous methodology for assessing the extent to which directional biases can distort the reported size of a drug-crash OR. Nevertheless, we believe that our tentative exploration of the biases in each of the included studies (see Appendix B, Supplemental material) has produced some clear findings:
Most of the studies are affected by one or more directional biases.
The biases are predominantly inflationary.
The studies with the highest cannabis-crash ORs tend to have the highest total bias scores (Table 1).
Using strict selection criteria, which included good toxicological evidence for the recent use of cannabis, we find little difference between the summary cannabis-crash ORs for the 13 culpability (1.37; 1.1–1.7) and four case–control (1.45; 0.9–2.3) studies. Using less strict inclusion criteria, which included self-reported evidence of recent cannabis use, and employing some different analytical techniques, Rogeberg, Elvik and White (2018, Table 1) reported a summary cannabis-crash OR that was considerably larger for the 15 case–control studies (1.82; 1.2–2.8) than for the 11 culpability studies (1.12; 1.1–1.2). Rogeberg (2019: 78) advised that ‘Understanding this discrepancy should be a priority for future research’. Given that selection and measurement biases have the potential to be expressed more easily in case–control studies than in culpability studies (where the culpable ‘cases’ and non-culpable ‘controls’ are drawn from much the same population of drivers), we consider that the discrepancy reported by Rogeberg, Elvik and White is most probably an expression of the high susceptibility of most case–control studies to the effects of selection and measurement biases.
The two most recently published meta-analyses of cannabis-crash risks from epidemiological studies (Hostiuc et al., 2018a, 2018b; Rogeberg, 2019) concluded that the null hypothesis of no overall effect of the recent use of cannabis on the risk of crashing cannot be rejected. In the words of Hostiuc et al. (p. 1) ‘Our analysis suggests that the overall effect size for driving under the influence of cannabis on unfavorable traffic events is not statistically significant …’ And according to Rogeberg (p. 75) ‘The magnitude of the estimated risk increase [using raw counts data from culpability studies] is sufficiently small that we cannot rule out residual confounding’. Neither of those meta-analyses involved the close scrutiny of the included studies for the presence of all three main types of directional bias. When taking such biases into account, we fully endorse the conclusion that the null hypothesis (that the recent use of cannabis does not increase the risk of crashing) cannot be rejected.
Both Hostiuc et al. (2018a, 2018b) and Rogeberg (2019) left open the possibility that the very recent use of cannabis (as possibly signalled by high levels of THC) increases the risk of crashing. They point out that any evidence for a moderately strong very-recent-use THC effect would be washed out in analyses where the prior use of cannabis is defined by any detectable level of THC. However, given that we fail to find any satisfactory evidence of dose effects in the seventeen studies (as discussed in relation to results provided here in Table 2), we are sceptical of the possibility that even the very recent use of cannabis could increase the risk of crashing. Nevertheless, we acknowledge that no published epidemiological study has been able to capture the crash risk for drivers within only the first 2 or 3 h after using cannabis, when they are most likely to be impaired, so we acknowledge the possibility that there is an elevated crash risk pertaining to very recent use. That possibility was explored theoretically by Rogeberg and Elvik (2016b), who concluded that, if there were an elevated crash risk from very recent use, it would probably not be more than doubled (i.e. the cannabis-crash OR would not be greater than 2.0).
Summary of conclusions concerning cannabis-crash ORs
Taking the role of study biases into account, we have shown that the best epidemiological evidence concerning the risk of crashing after using cannabis (as indicated by testing positive to THC) is compatible with the null hypothesis that the recent use of cannabis has no effect at all (such that the cannabis-crash OR = 1.0). We will refer to that value as the ‘bias-adjusted cannabis-crash OR’.
It is possible that some researchers and policymakers might not agree with our bias adjustments. They would presumably therefore rely on the results of conventional cannabis-crash meta-analyses. The findings from our meta-analyses roughly agree with those of other recently published reviews: that the recent use of cannabis increases the risk of crashing by 50% or less (such that the cannabis-crash OR is not greater than 1.5). We will refer to that value as the ‘meta-analytic cannabis-crash OR’.
Given that we found no convincing evidence for a dose–response relationship between the concentration of THC and the risk of crashing, we consider that our first two conclusions apply equally to all cannabis-crash risks irrespective of the THC cut-off thresholds.
We commented above that those drivers who had very recently consumed cannabis (within 2 or 3 h of crashing) might comprise a higher risk subset, who cannot necessarily be identified through high concentrations of THC. And we noted that Rogeberg and Elvik (2016b) had estimated that their crash risk could be doubled (such that the cannabis-crash OR = 2.0). We will refer to that value as the ‘immediate cannabis-crash OR’.
We will now explore the implications of these four conclusions for: (1) the burden of legal proof of causation; (2) tolerable crash risks; and (3) cannabis-presence driving offences. The implication of our third conclusion is that these explorations do not need to separately consider the situation for cannabis-driving enforcement regimes that have adopted a zero-tolerance approach to any presence of any THC and those that have adopted above-zero cut-off thresholds.
The burden of legal proof of causation
When the value for an exposure-outcome OR equals 2.0, the risk of the outcome for subjects who have been exposed is twice as high as for non-exposed subjects. Furthermore, when the value equals 2.0 there is a 50% chance that the exposure is responsible for the outcome for the exposure-positive cases. For example, an adjusted diazepam-crash OR of 2.0 from a rigorous case–control study would mean that the use of diazepam before driving is the cause of 50% of the crash involvements of the diazepam-positive drivers, with the other 50% being caused by factors other than the use of diazepam.
There are circumstances where the value 2.0 for an exposure outcome OR is particularly relevant. The ‘50% rule’ is a legal rule of thumb that is sometimes applied in the US courts. Under the rule, an exposure is considered to have caused a deleterious outcome for an individual if 50% or more of the deleterious outcomes among exposure-positive cases in the population can be attributed to the exposure (Haack, 2014, Ch. 11: 264–293). For example, if a foetus was exposed to an anti-nausea medication, and the baby was born with limb deformities, then the deformities could legally be attributed to the medication if it could be proven by reference to epidemiological studies that 50% or more of the deformities amongst the medication-exposed babies in the population were related to their mothers’ use of the medication. In other words, a birth defect for a particular baby could be legally attributed to the medication if its mother had used the medication during her pregnancy, and the medication-deformity OR was 2.0 or greater. More generally, under the 50% rule, an OR of 2.0 or greater defines the range of ORs at which scientific evidence for general causation has sometimes been used in the US legal system as evidence for specific causation.
We are not aware of any drug driving litigation where the 50% rule has been applied. However, it is conceivable that a THC-positive driver who was involved in a serious crash might want to argue that the crash was not caused by impairment from cannabis. Let us assume that the case is heard before a judge who is unlikely to be convinced that the true bias-adjusted cannabis-crash OR is 1.0. Citing the 50% rule, the driver could argue that the conventionally-accepted meta-analytic cannabis-crash OR of 1.5 was considerably below the value of 2.0 where specific causation can be inferred from general causation. In other words, the driver could argue that there was no adequate scientific evidence that his use of cannabis played a causal role in his crash. And even if there were evidence that the driver had consumed cannabis immediately before driving, the driver could still argue that the immediate cannabis-crash OR of 2.0 was at the borderline of where specific causation can be inferred from general causation.
Tolerable crash risks
It is a commonly accepted rule of thumb in Australia that drivers with a BAC of 0.05 are about twice as likely to crash as drivers with a zero BAC. The second rule of thumb is that drivers who travel at 10% above the mean speed at a road location (e.g. at 55 km/h in a 50 km/h location or at 110 km/h in a 100 km/h location) are about twice as likely to crash as those travelling at the mean location speed (Kloeden et al., 2002). Those rules of thumb have been endorsed by the Australian Transport Council (ATC), which was the body that brought together the Commonwealth, State, Territory and New Zealand Ministers with responsibility for road safety (ATC, 2008: 30).
In the case of drink-driving, it is legal in Australia for most drivers to drive with a BAC of up to 0.05. The ATC (2011: 88) explicitly acknowledges the compromise involved in setting that limit, which ‘strikes the right balance between societal values and public safety in relation to alcohol use’. It is evident that the ATC was prepared to tolerate drink-driving at BACs up to the level where the risk of crashing is doubled. Although the police in Australia are reluctant to discuss speed camera enforcement tolerances, it is likely that they are generally set in line with published UK policing practice, where speeding below 10% over the speed limit is unlikely to be enforced (Association of Chief Police Officers, 2013). That is known to be the practice in South Australia (Nankervis, 2014), and is probably also the practice in some other Australian states. Some Australian police jurisdictions are therefore tolerating levels of speeding where crash risks are commonly understood in Australia to be doubled. So, it seems, at least with respect to drink-driving and speeding in Australia, that exposure-crash risks with values up to 2.0 can be tolerated because they ‘strike the right balance’. It should be noted that these considerations pertain only to personal risks where individualised sanctions are involved, and do not necessarily pertain to environmental risks. For example, traffic engineers should probably not consider installing a roundabout whose less expensive design results in only 30% more serious crashes than the alternative design.
We are not aware of any discussion of ‘striking the right balance’ in relation to cannabis-crash risks. Nevertheless, that is a conversation that should be started, given the widespread legalisation of the recreational use of cannabis and the even wider spread legalisation of its medical use. In that context, it is relevant to note that the conventionally-accepted meta-analytic cannabis-crash OR of 1.5 is well below the tolerated alcohol-crash and speed-crash ORs of 2.0. Even the hypothetical immediate cannabis-crash risk of 2.0 is at the borderline of tolerability.
Cannabis-presence driving offences
The punishment for a traffic offence should be proportionate to the seriousness of the offence as measured in terms of the effect of the offending behaviour on the risk of crashing. Our epidemiological findings relate to the mere presence of THC in a driver’s body fluid. They are therefore directly relevant to stand-alone zero-tolerance cannabis-presence driving offences. On the basis of our first conclusion, that the bias-adjusted cannabis-crash OR equals 1.0, there is, of course, no epidemiological justification for the existence of such offences. And, given our third conclusion, that cannabis-crash risks are independent of THC cut-off thresholds, there is also no epidemiological justification for such offences, but with above-zero threshold cut-offs for THC.
Especially now, with the medical and recreational use of cannabis becoming more accepted, our main conclusion (that the best estimate of the cannabis-crash OR is 1.0) is consistent with the view that stand-alone cannabis-presence driving laws should be repealed (while impairment-based laws would remain). That is especially so given the injustices involved for the majority of the THC-positive drivers who are penalised but unimpaired (Wiggins and Carrick, 2020), the concomitant violation of civil liberties (McDonald, 2009; Prichard et al., 2010) and the the high cost of conducting RDT operations (National Drug Driving Working Group, 2018). Ross Homel, whose early work on deterrence theory (Homel, 1988) was instrumental in the introduction of Random Breath Testing (RBT) for alcohol in Australia, considers that the inclusion of cannabis in the Australian RDT protocols is a disingenuous attempt to prosecute the War on Drugs under the guise of road safety (Hall and Homel, 2007).
While we believe that the cannabis-crash null hypothesis cannot be rejected, we accept that road safety policymakers might not agree with us. Nevertheless, if they support the need for evidenced-based policy, they would presumably accept the truth of our second conclusion, that the meta-analytic cannabis-crash OR is not greater than 1.5 (irrespective of the THC cut-off). The implication for setting cannabis-presence driving penalties is obvious. On the principle of proportionality, the penalties for THC-positive driving (with a cannabis-crash OR of 1.5) should be about half as severe as the penalties for driving at a BAC of 0.05 (with a BAC-crash OR of about 2.0), or speeding at about 5 km/h above the speed limit on an urban road or 10 km/h above the limit on a rural highway (both with a speeding crash OR of about 2.0). However, in Australia, the penalties for cannabis-presence driving offences are considerably higher than that (Moxham-Hall and Hughes, 2020). Three examples are provided. In the state of Victoria, the maximum fine for a third cannabis-presence driving offence is AU$19,826. Given the targeting of known cannabis users, the likelihood of repeat offending is quite high. In the state of Queensland, the maximum prison sentence for a third offence is 9 months. And in the State of South Australia, the maximum licence cancellation period for a third offence is 1 year. These excessively punitive penalty structures can be taken as a reflection of the fact that the underlying legislation has more to do with the War on Drugs than it has to do with road safety.
Ms Maureen Bell, a Research Librarian from the University of Adelaide, provided invaluable advice on validly searching the electronic databases using reproducible methodologies; Dr Matt Welsh of the University of Adelaide for his involvement in discussions about study biases; and the corresponding authors for six of the studies who provided feedback on the draft bias reports.