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HMG-CoA reductase inhibitors and COVID-19 mortality in Stockholm, Sweden: A registry-based cohort study

['Rita Bergqvist', 'Department Of Global Public Health', 'Karolinska Institutet', 'Stockholm', 'Viktor H. Ahlqvist', 'Michael Lundberg', 'Centre For Epidemiology', 'Community Medicine', 'Region Stockholm', 'Maria-Pia Hergens']

Date: 2021-10

Existing studies have been limited in their appreciation of the complexity of causal inference when using observational data and may thus be prone to the critical pitfalls of observational studies of clinical interventions. Such pitfalls have, for example, been clearly demonstrated in works on statins and cancer [ 28 ] and, indeed, in studies of COVID-19 [ 50 ]. These include failure to differentiate between new and prevalent users (leading to survival bias), using post-baseline information to establish exposure (leading to immortal time bias), introducing collider bias by sampling only hospitalized patients and/or conditioning on positive PCR test results or adjusting for potential mediators (such as disease severity).

Several cohort studies of hospitalized COVID-19 patients have reported negative associations between statin use and mortality [ 20 – 27 ], in line with our findings. These studies have been summarized in meta-analyses indicating an overall reduction of unfavorable COVID-19 outcomes (including death, intensive care unit (ICU) admission, and mechanical ventilation) of about 30% in statin users [ 48 , 49 ]. The meta-analyses also demonstrate substantial heterogeneity between studies (i 2 90%) [ 29 ], and a recent large-scale study on severe COVID-19 and all-cause mortality in COVID-19–positive Danish citizens showed no association between statin use and either outcome [ 19 ].

In this register-based cohort study of 963,876 Stockholm residents aged 45 or older, statin treatment was associated with a moderately lower risk of COVID-19 mortality. Adjusted HRs were largely consistent across age groups, sexes, as well as across different COVID-19 risk groups and indications for statin treatment. This result was corroborated by our sensitivity analysis explicitly emulating a target trial among initiators of statin treatment.

Strengths and limitations

Our study has several strengths. Most importantly, we applied a rigorous methodological approach to avoid the potential biases mentioned above, resulting in a study with high internal validity. To avoid conditioning on PCR testing, which may introduce collider bias (as previously observed in connection with COVID-19 research [50]), the outcome measure was based on data from The Swedish Cause of Death Register. This register contains all deaths determined by physicians to be caused (in full or in part) by COVID-19, based on testing or other diagnostics. Moreover, mortality carries a smaller risk of selection bias than outcome measures such as ICU admission or severity of disease.

Furthermore, we were able to control for a large set of important confounders using data collected in a standardized manner. We also avoid confounding that may arise from altered behavior during the COVID-19 pandemic. Specifically, the end of the period of exposure was set to 1 March 2020—the start of the pandemic in Stockholm—since the collection of prescriptions during a pandemic could be a proxy for certain behaviors affecting the risk of exposure to the virus (for example, the frequenting of public spaces). While we believe that this is a major strength of our study, such time restrictions imply that we include statin dispensations, which, in theory, could have been collected long before a COVID-19 infection. Indeed, individuals who collect a sole prescription in early 2019 will be classified as exposed. However, this is in line with the intention-to-treat principle. As such, our estimate may represent a conservative estimate of the causal effect of statins on COVID-19 mortality; our estimate can be interpreted as that obtained from an observational intention-to-treat analysis in the presence of noncompliance, which we believe is the clinically relevant causal contrast. Another important aspect is the differentiation in recommendations for different age groups during spring and summer; people aged 70 or older were recommended to isolate, which could render analyses based on dispensation during the spring and summer unrecoverable from such selection mechanisms.

Lastly, in context of other evidence on COVID-19, the duration of follow-up is long and the number of exposed cases high. Our study includes the total population of Stockholm County, whereas most previous studies were hospital-based. Hence, the results are likely to have higher external validity.

However, the study also has several important limitations. Firstly, as in any observational study, residual confounding cannot be ruled out. For example, we have not adjusted for smoking or body mass index (BMI), but only diagnosed obesity. Both smoking and high BMI are strongly linked to statin use [51], and high BMI has been identified as a risk factor for COVID-19 death [52]. Although we would expect this to result in an underestimation of a potential protective effect, we cannot dismiss the possibility that our findings may be explained by confounding.

Secondly, as in most pharmacoepidemiological studies, we have assumed that drug dispensation captures drug use correctly. This assumption is easily challenged since not all patients filling prescriptions adhere to treatment. This misclassification is, however, unlikely to explain our findings. Any nondifferential misclassification will generally dilute associations, and we judge a possible differential misclassification to bias our findings toward a positive association if adherence is particularly low in severely ill patients (including in COVID-19) or patients that have low health literacy and fewer means of avoiding the infection.

Lastly, we have not been able to study possible effects of dosage, type, or brand of statins. Specifically, despite our study being, the hereby largest study of statins and COVID-19 mortality, we had an insufficient sample size to perform such granular analysis. As such, our estimate should be interpreted as the mean of possibly heterogeneous effects.

Further aspects should be considered when interpreting our findings. This study does not concern the possible effect of statin treatment for treatment of severe COVID-19, but its possible preventive effect. Furthermore, although our duration of follow-up is longer than comparable studies, future studies could shed light on the long-term effects of statins on COVID-19 mortality and possible heterogeneity in effects over subsequent COVID-19 waves. Although we emulated a target trial with an intention-to-treat analysis, the study does not provide an analysis of the risk of adverse events in potential target groups. Safety evaluations are outside the scope of the current study as they require extensive clinical and qualitative safety data, and such evaluations should address several aspects of the overall concept of statin safety. Nonetheless, this has been addressed in previous clinical trials, but not in connection with this new potential indication (COVID-19 prevention). Although statins are considered to have a favorable safety profile [53] compared to many other drug classes discussed in connection with COVID-19, a clinical risk assessment must always be made. Finally, although our study has greater generalizability due to the general population design (as compared to hospital-based studies), its results should be interpreted in light of the Swedish COVID-19 strategy, which may have implications for the generalizability of our findings.

[END]

[1] Url: https://journals.plos.org/plosmedicine/article?id=10.1371/journal.pmed.1003820

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