Discussion

These data support the conclusion of our previous review,1 that mental illnesses and prescribed psychotropic treatments moderately increase the risks of occupational injury. Risks were elevated 44% overall in relation to mental health problems and 57% overall in relation to psychotropic drug treatments. There was evidence that the effects of having a mental health condition are not solely a consequence of psychotropic medication. For patients taking common classes of antidepressants, we estimate that risks of injury are raised about 35–40%. The data further indicate that approximately 1 in 10 of all workplace injuries may be attributable to mental health conditions or psychotropic medication, the potentially avoidable fraction being higher (about 30–40%) among individuals with such health problems or taking such prescribed treatments.

Our study had several strengths and a few limitations. The database allowed us to identify a large sample of occupational injuries across Britain, together with a selection of age-matched, sex-matched and location-matched controls. Almost everyone in Britain registers with a family doctor for services that can be freely accessed at the point of delivery. Thus, general practice patient lists offer a sampling frame that is generally representative of the total population. Moreover, the CPRD database, which has been shown empirically to have a high degree of completeness (>97%) and validity for many measures,29 ,30 is likely to capture a very high proportion of acute injuries presenting to medical services (hospital attendances, which are logged within the database, are also free at the point of care, while accidents are rarely treated privately). Set against this, we could not investigate injuries that were only self-treated or mishaps resulting only in damage to property or near miss events. The complexity of the coding system was such that we may not have discovered every case of occupational injury or mental illness within the sampling frame. However, errors of omission would be unlikely to cause bias since the process of case ascertainment was independent of the exposures of interest.

A more significant limitation of the CPRD is that it does not maintain a reliable record of patients’ occupations. Thus, while cases would have been selected from those in work, some controls may have been unemployed; cases may also have been drawn more often from manual occupations than controls. Bias might arise if controls over-represented the prevalence of mental illnesses or treatments for disorders that prevent work, or if these were more common in manual jobs. However, as we have demonstrated elsewhere,31 the resultant bias is likely to be small in practice. (This is because the excess prevalence in controls would reflect the weighted average of risks in subgroups, and be diluted, on the one hand, by a low background rate of unemployment and, on the other hand, by the small difference in risk between manual and non-manual occupations. Moreover, potential biases would act in opposite directions.)

The CPRD record tends to lack information on the circumstances of occupational injury and some cases could have been injured through the fault of third parties rather than themselves. Furthermore, some codes were ambiguous as to occupational causation (such that 15% of cases were possibly, but not probably occupational, as judged independently by two of us (KTP and ECH) blinded to exposure status). Such errors would, if anything, bias risk estimates towards the null and cannot explain the elevation in risks that we observed. Risks of workplace injury could also have been reduced by healthy worker selection effects in the study population—for example, subjects with health problems opting for work with less injury potential or being screened out of hazardous work. This well-known effect would not compromise the internal validity of our study (as risks in workplaces would truly be lower), but is a threat to external validity, as simple extrapolation to unselected workforces could lead to an underestimation of risks.

A notable strength of the CPRD is that for each subject we could access a hugely detailed medical record, in which mental health diagnoses and treatments had been contemporaneously logged, independently of the injury consultation, and with full information on dates of events. The relative timing of events was thus established, although, as a further safeguard against the possibility that errors in the coding of dates masked an element of reverse causation, we explored associations with diagnoses made at least 12 months before the injury consultation in a sensitivity analysis: risk estimates were unchanged.

A further sensitivity analysis explored risks by nature and by external cause of injury, and found them to be broadly and generally elevated (see online supplementary table S3). Non-specificity of effect raises a concern that risk estimates may have been inflated by an overall propensity among cases to consult a family doctor (which is a requirement both of case definition and of qualifying exposures), but a similar significant magnitude of effect among severe cases (those seen in hospitals and those with fractures and amputations) tends to argue against important bias arising in this fashion.

The findings from this study are broadly compatible with other published data on mental illness and accident risk. Thus, in our previous review,1 21 of 22 risk estimates across 11 studies were elevated, 60% of them significantly so at the 5% level, and with a median RR of 1.5. The four largest studies (>1400 subjects analysed5 ,7 ,14 ,16), including a large multistage probability sample from the US Health and Retirement Study cohort,16 provided risk estimates ranging from 1.07 to 1.47. However, studies mostly took self-reported low mood on a screening questionnaire as the basis for exposure definition, and only 6 of the 22 effect estimates were based on a physician's diagnosis of mental illness.

Earlier findings on psychotropic drugs and occupational injury risk have been more mixed. In our review,1 13 of 25 risk estimates (from nine studies) were increased, five of them significantly, the median RR being 1.2. However, the spread of risk estimates was wider than for mental illness, and two high-quality case–control studies with date of event information (to limit scope for reverse causation) reached different conclusions. Voaklander et al14 reported that prescription of anxiolytics, sedatives or hypnotics in the preceding 30 days was associated with a threefold increase in odds of hospital attendance with work-related injury, whereas Gilmore et al,20 in a study of similar design, found much lower RRs (0.8 in men and 1.5 in women). Two other studies favoured a more than doubling of risk from medication,17 ,18 although both had the potential for inflationary bias through reverse causation—in Wadsworth et al,18 for example, the taking of sleeping pills related to the 14 days prior to questioning whereas injuries might have occurred up to a year beforehand. Studies mostly evaluated risks from hypnotics, anxiolytics and sedatives (or did not specify the class of agent), there being relatively few investigations of injury risk from antidepressants and antipsychotics, and, in contrast to this report, none that estimated risks by major classes of antidepressant. Hence, our findings, as well as providing estimates of risk based on accurate date of event information, provide a greater depth of information on specific agents.

On balance, we conclude that a range of common mental health illnesses and classes of psychotropic treatment contribute to an important, minority of workplace injury events. Absolute risks do not justify exclusion of individuals from employment, especially as individualised assessment may reveal factors that mitigate the risk of injury or its impact. However, the data suggest a need to exercise caution in the occupational placement of individuals with such problems, especially in relation to work that carries an unusual degree of risk or special responsibility for the safety of others.