To the best of our knowledge, this is one of the few studies that evaluated and highlighted the possible impact of different epidemiologic study designs (i.e., case–control, case–crossover, and case–time–control) on the association between MVA risks and psychotropic medication exposure in the same study population.
The results of our case–crossover study did not show any significant increase in MVA risk associated with the exposure to the selected psychotropic medicine groups [e.g., Regular user stratification: Anxiolytics: Adj. OR = 0.95 (95 % CI: 0.68–1.31); SSRIs: Adj. OR = 1.00 (95 % CI: 0.69–1.46)]. Stratifications according to the number of days and DDDs used in the previous year were consistent with the above-mentioned findings, and, in particular, did not show any effects of exposure frequency on the risk of experiencing an MVA [e.g., 1–15 day stratification: Anxiolytics: Adj. OR = 1.45 (95 % CI: 0.52–4.09); SSRIs: Adj. OR = 0.65 (95 % CI: 0.11–3.87)]. Therefore, if compared to our recent pharmacoepidemiological study [9
], it can be observed that the current case–crossover analysis produced different results than those of the case–control analysis, which actually found a statistically significant association between traffic accident risk and exposure to anxiolytics and SSRIs [Anxiolytics: Adj. OR = 1.54 (95 % CI: 1.11–2.15); SSRIs: Adj. OR = 2.03 (95 % CI: 1.31–3.14)—all exposed individuals].
Lastly, the outcomes of the case–time–control analysis showed a borderline statistically significant increased risk only in SSRI users, in the stratification referred to regular users [Adj. OR = 1.16 (95 % CI: 1.01–1.34)], whereas the acute user stratification only showed a statistically significant association between MVA risk and other antidepressant users [Adj. OR = 1.76 (95 % CI: 1.11–3.01)]. Therefore, it can be speculated that, in this case, the findings of the case–time–control analysis only partially supported the outcomes of the case–control one.
The discrepancies between the outcomes of the case–control and case–crossover studies could be attributed to the choice of study design. The case–crossover design is a commonly used scientific method to investigate whether a certain event was triggered by something unusual that happened just before the event itself [14
]. The case–crossover is a matched case–control study, but it only involves cases and each case serves as its own control [14
]. Because of this peculiarity, the case–crossover design controls for stable subject-specific covariates and it overcomes control selection bias [13
]. However, this type of design requires that the exposures are brief and their effects transient [10
]. Considering that psychotropic medications are often used on a regular and chronic basis [8
], it can be speculated that, in the present study, one of the most important assumptions of the case–crossover design was not met, and, therefore, the choice of this study design was probably not appropriate. To be more precise, it is relevant to point out that the case–crossover odds ratio is estimated by the ratio of the number of cases exposed only during the case window to the number of cases exposed only during the control window (i.e., ratio of discordant pairs). Given that only discordant pairs contribute to the estimation of the odds ratio in matched analyses, if the exposure does not change in a systematic way over time, it is likely to face a loss of precision because there is a lack of discordant pairs as exposure becomes more homogeneous, and eventually reduces the power of the study [13
]. Therefore, based on the above-mentioned considerations, it can be conceivably hypothesised that the case–crossover analysis should be limited to intermittent users of the selected medication groups. However, it is important to note that, in the current study, this restriction led to a consistent loss of cases and, even if the ORs calculated for this specific group of users were more similar to the ORs obtained by applying the case–control technique, it can be speculated that, as stated before, our study did not have adequate statistical power to detect reliably the association between incidental psychotropic medication users and MVA risks [10
Stratifying the data according to the number of DDDs and days of use in the previous year did not support the associations that were shown in the case–control study either. With respect to the DDD, a possible explanation for this might be that, since the defined daily dose is a unit of measurement and does not necessarily reflect the recommended or prescribed daily dose [28
], the actual doses used by our study population could have been considerably different from the recommended DDD; therefore, perhaps this stratification was not appropriate and led to a misclassification of our medication users.
With respect to the days of use, it is difficult to explain the study outcomes, but, as stated above, they could be related to the low sample size in the infrequent user groups which might have resulted in a lack of statistical power to address the issue of the association between the risk of experiencing an MVA while incidentally exposed to psychoactive medications [10
Besides the points reported above, there could also be other possible explanations for the discrepancies among the findings of the two designs that were used. As some authors have also pointed out [8
], possible reasons for different results between case–crossover and case–control studies may be related to selection bias of the control–person–time (i.e., our selected control–person–time did not properly represent the population-time that generated the cases due to, for example, possible divergences in the driving patterns between the case and control times), confounding by indication (no information was available on what medical condition the psychotropic medications were prescribed for, and, consequently, we could not account for the confounding effect of the disease) different effects of the medication at different points in time (e.g., different estimates in relation to therapy duration and/or prior exposures [31
]), time-varying within-subject confounding factors (e.g., fluctuations in disease severity, co-morbidities, etc.), and time trend bias (i.e., changes in the prescribing patterns of the medications of interest).
With regard to the case–time–control analysis, our study only showed a positive association between MVA risk and SSRI users [Adj. OR = 1.16 (95 % CI: 1.01–1.34)], in the regular user group, and other antidepressant users [Adj. OR = 1.76 (95 % CI: 1.11–3.01)], in the acute user stratification, but, in contrast to our earlier findings, no evidence of an increased traffic accident risk associated with anxiolytics was detected [Adj. OR = 1.10 (0.94–1.27)]. The reason for the discrepant outcomes of this analysis is not clear, but it might also be related to the choice of the study design. The current case–time–control study was performed to remove bias due to time trends from the case–crossover estimate [22
], and, as suggested by Suissa [18
], to possibly control for confounding by indication. However, since the case–time–control design can be seen as an elaboration of the case–crossover design [30
] (i.e., it corresponds to the division of the case–crossover matched-pair odds ratio by a “control–crossover” (time–control) matched-pair odds ratio [32
]), our findings could have been limited by the same shortcomings as those of the case–crossover approach (e.g., selection bias in the control–time window, within-person confounding, time-varying within-subject confounding factors, etc.). Additionally, our case–time–control design might have had the same difficulty addressing chronic exposures and chronic effects as our case–crossover analysis. In particular, if the exposure was chronic, few controls were available with discordant exposures in different time periods, and, as well as the case–crossover design, our resultant case–time–control analysis could have been hampered by a poor statistical power compared to a conventional study [32
]. Moreover, since the case–time–control design requires a traditional control group, our study, and, consequently, its results could have been hampered by the same limitations as the case–control design, as well (e.g., selection bias in the collection process of the control group, between-person confounding, higher complexity due to the necessity of a control group, etc.) [18
]. Lastly, as Greenland argued [32
], on the one hand, our case–time–control design could have been a helpful tool to adjust for time trends in measured exposures, but, on the other hand, if unmeasured confounders and/or carryover effects were present, new biases could have been introduced. As a consequence, the problem of confounding by indication would not have been solved and our final results could have been either more or less confounded than those obtained by the case–control and case–crossover analyses [32
Our study supports the observations of Hebert et al. [8
], who also compared the results of a case–control study to those of a case–crossover study using the same database to determine the association between BZDs and the risk of MVAs. In that study, the case–control approach demonstrated an increased MVA risk associated with the use of long-acting BZDs whereas the case–crossover approach applied to all cases did not show any association. The authors concluded that the differences among the findings of these studies could have derived from intrinsic differences between the two designs, and that, in particular, a lack of intermittency of exposure could have altered the point estimates of their case–crossover analysis [8
Although the differences between the study populations should be considered as a possible cause of divergent findings, the previously mentioned assumption could also clarify the discrepancies between the outcomes of Hemmelgarn et al.’s case–control study [6
] and those of Barbone et al.’s case–crossover study [7
] which, respectively, showed a statistically significant association between BZD exposure and traffic accident in older adults and no evidence that BZDs increased traffic accident risks in elderly patients.
Lastly, this hypothesis could also explain the contradictory findings between our case–control study on SSRIs and increased MVA risk [9
] and Barbone’s case–crossover outcomes which, in contrast to our research, found no increased risk of road-traffic accidents in users of SSRIs [7
In conclusion, our investigation has shown that different study designs seemed to give different answers to the same research hypothesis, in the same population (i.e., the outcomes of the case–crossover and case–time–control analyses were not in line with the outcomes of the case–control analysis, which showed an increased traffic accident risk in anxiolytic and SSRI users). Considering that every study design has different design-specific assumptions, and strengths and limitations, it could be assumed that our analyses actually tested distinctive causal hypotheses and focused on different aspects of psychoactive medication use and MVA risk [8
]. As a consequence, it seems reasonable to conclude that each pharmacoepidemiological design may be appropriate only in certain settings and under specific assumptions [22
], and, therefore, if possible, multiple designs and analyses should be used to investigate the different aspects of factors that can play a role in traffic safety while driving under the influence of psychotropic medications.