We found evidence of an association between prescription of anxiolytic and hypnotic drugs and mortality over an average follow-up period of 7.6 years among more than 100 000 age and general practice matched adults. In patients who were prescribed these drugs, there was an estimated overall statistically significant doubling of the hazard of death (hazard ratio 2.08), after adjusting for a wide range of potential confounders, including physical and psychiatric comorbidities, sleep disorders, and other drugs. This association remained significant and followed a dose-response pattern after restricting analyses to those with at least 12 months of follow-up and to those who were only prescribed the study drugs in the first year after recruitment (hazard ratio 1.75). Crude cumulative mortality in those given drugs was 26.46 per 100 people over the full follow-up period compared with 16.82 per 100 controls. After excluding deaths in the first year, there were approximately four excess deaths linked to drug use per 100 people followed for an average of 7.6 years after their first prescription.

While overall effect sizes were broadly in keeping with most previous findings, our estimates of association were lower than that reported by one study,23 which reported an adjusted hazard ratio of 4.56 over 2.5 years. This may reflect differences in the length of follow-up, as both studies reported declining associations with mortality over time.

Strengths and limitations of this study

Use of data from the UK General Practice Research Database was an obvious strength, given the size and representativeness of the sample, and the quality, completeness, and duration of the follow-up data. Data on drug use were based on documented prescriptions rather than self reported receipt or use of drugs. We had detailed information on a wide range of potential confounders, going back several years. In particular, we were able to control for a large number of physical and psychiatric morbidities as well as prescriptions of other drugs. This is especially important given the possibility of confounding by indication (that is, study drugs may be given more often to those who are seriously ill and who may not be able to sleep because of pain or other consequences of long term or life threatening illnesses). In contrast with a recent report,23 we were able to adjust for anxiety disorders as well as all other psychiatric disorders. We were also able to identify and control for recorded instances of sleep problems (including those secondary to physical and psychiatric disorders).

Our recruitment strategy and ascertainment of drug use were further strengths. We minimised misclassification by excluding people who had received only one prescription, since some people never fill prescriptions or take the drugs. Using defined daily doses to quantify cumulative use of study drugs allowed us to combine the effects of different drugs in a way that is not possible by counting prescriptions or pills.23 In further contrast with previous research,23 we chose to classify study drugs by class rather than by indication for the purposes of recruitment; for example, we included all benzodiazepines, not just those recorded as having been prescribed for insomnia. We would argue that this resulted in a more accurate estimation of use of these drugs, as well as ensuring that our results are generalisable to all of those who receive anxiolytic and hypnotic drugs in primary care. Our models were adjusted for all main indications for these drugs. Although pooling of study drugs may have overlooked variation in associations with mortality across classes, subgroup analyses indicated statistically significant associations (and dose-response effects) between mortality and all three classes of study drug. The largest hazard ratios were found for benzodiazepines.

Despite using prescribing records, we may have underestimated use of study drugs. Patients with more serious psychiatric disorders may be cared for by secondary care services rather than solely in primary care. Although in most cases responsibility for longer term (repeat) prescribing is usually delegated to general practice, it is possible that prescribing for these patients may be under-recorded in the General Practice Research Database. Likewise, we had no information on the use of study drugs that were obtained illicitly, although this was likely to have been modest compared with use of prescribed drugs. It is highly unlikely that study drugs were used before recruitment among the patients eventually prescribed the drugs or controls, given that the patients were registered with the study practices for 15 years on average. This was not so in a previous study,23 in which around one fifth of the exposed group had received a prescription for a study drug before recruitment.

The length of follow-up was also a strength, particularly for the generalisability of the findings. However, higher effect estimates obtained when we restricted our sample of exposed patients to those with no further prescriptions for the study drugs after the first 12 months suggests that results from our initial model, which included patients who continued to receive prescriptions for the study drugs throughout the observation period, may have been biased towards the null by the confounding of use and survival. Results of models in which use was restricted to the first year after recruitment and deaths restricted to those occurring after that first year suggest that much of the excess mortality risk arises early in the period of drug use but remains statistically significant even after discontinuing study drugs. We were not, however, able to explore temporal risk trajectories in detail. It was possible that patients who discontinued drugs within the first year did so because they were particularly unwell (and more morbid than those who continued to take these drugs). However, our findings show that the opposite was true, which strengthens the validity of our estimates of excess mortality in this group compared with the control group. Although those for whom prescriptions for study drugs stopped after the first year were more likely to be censored for reasons other than death, there is no reason to believe that this inflated the association between study drugs and mortality.

Non-randomised outcome studies are especially prone to confounding, including confounding by indication. One option for dealing with confounding by indication is using a comparator group more closely aligned with the exposed group—for example, patients who were starting other types of drugs. However, in the absence of previous evidence that comparator drugs were free of other indication effects, this would again have not ruled out this bias, even though it may have accounted for bias related to the comparison with non-users. Instead, we chose to deal with this in four ways: by taking account of a large number of potential confounders, by comparing effects across different groups of study drugs, by conducting subgroup analyses that limited exposure to year 1 and excluded all deaths during that first year in patients who both used and did not use the study drugs (on the grounds that confounding by indication will have the largest effect in year 1), and by adjusting our estimates of association for comorbidities occurring across the entire follow-up period. Nevertheless, although we controlled for many potential factors that were associated with study drug use and mortality and eliminated confounding of use and survival, it is impossible to exclude confounding arising from unmeasured factors or measurement error.33 34 35 While effects on estimates of association can be substantial,33 such bias is greatest for unmeasured confounders and those that are uncorrelated with other confounders but correlated with the study exposure.34 Bias tends to be greatest in studies that control for relatively few measured confounders.34

Although bias due to confounding was likely to have occurred, the impact was offset by the large number of covariates included in our analyses. One important unmeasured confounder is socioeconomic status, since records in the General Practice Research Database do not include detailed information on occupation, education, housing tenure, income, or employment. However, this variable was partially controlled for by matching by practice. Residual confounding, arising from a mixture of misclassification and indication, was also likely to have occurred in the recording of clinical diagnoses, and through our inability to quantify the severity of illness. Again, this is likely to have been offset to an extent by controlling for a wide range of comorbidities. Adjustment for a large number of measured confounders failed to negate our finding of an association between drug use and mortality but has resulted in appropriately more conservative estimates of the size of this association.23

Cohort studies are also prone to immortal time bias, which arises if the period participants are considered at risk differs between comparator groups.36 Although mortality was counted from the time of the first prescription for all patients, the time until second prescription would be “immortal” for patients who used the study drugs and who had to survive to get a second prescription to be in the study. This would not have applied to controls. However, excluding deaths among those who did not survive to receive a second prescription would have underestimated mortality in patients who used the study drugs. Any bias in the mortality comparison would therefore have been towards the null. Furthermore, this would not have biased the subgroup analysis that excluded early deaths, since deaths were ascertained only after the first year of follow-up for patients who both did and did not use the study drugs.

We considered the possibility of collider bias, a form of selection bias that may occur when two variables are not associated but share a common antecedent or outcome. Adjusting for such a factor can result in a spurious association.37 It is possible, for example, that study drug use and mortality are both associated with (for example) physical illness but themselves are not related. Since adjusting for comorbidities reduced estimates of association between study drugs and mortality, we suggest that these variables were likely to have been acting as classic confounders rather than sources of selection bias.

We did not have access to data on cause of death and therefore were unable to explore associations between prescription of study drugs and specific forms of morbidity such as pneumonia. Neither did we explore interactions between individual forms of morbidity and vulnerability to specific drug classes. In the light of consistent evidence of associations with mortality, such investigations are needed and will be the subject of future studies.