key: cord-0745199-btyx39ca
authors: Cozzi-Lepri, Alessandro; Guaraldi, Giovanni; Meschiari, Marianna; Mussini, Cristina
title: Re: ‘methodological evaluation of bias in observational COVID-19 studies on drug effectiveness' by Wolkewitz et al
date: 2021-05-06
journal: Clin Microbiol Infect
DOI: 10.1016/j.cmi.2021.04.026
sha: b797e26e0d45311174e495e9213f781b8f68b085
doc_id: 745199
cord_uid: btyx39ca

nan

We read with interest the paper by Martinuka et al published on CMI (1) . Although we agree with the general issue that making valid causal inferences from real-world observational data is a demanding task that requires high-quality data and adequate statistical methods as well as clinical knowledge and statistical expertise, a few points regarding specific criticisms to our TESEO study need to be pointed out (2) . Indeed, the authors seemed to have misread both the design and statistical methods used in our study.

First, the study population was people with COVID-19 pneumonia admitted to a tertiary hospital, not people entering ICU as incorrectly reported in Table 1 .

Immortal bias seems to be a non-issue in the setting of people hospitalised with COVID-19 pneumonia. Indeed, the probability of dying before starting any treatment in such target population is close to zero so immortal bias is unlikely to occur.

The second common misconception regards the presence of competing risks and how to control for these. Although we agree that people who are discharged before day 28 are no longer at risk of undergoing mechanical ventilation or dying and this was a competing risk in our analysis, our aim was to give an estimate of the average treatment effect equivalent to what could be estimated in the emulated randomised trial (3). Thus, the aim was to quantify the survival time distribution for the situation without the competing risk. Specifically, for unbiased estimation of the effect of the intervention, we had to assume that participants whose follow-up was censored due to the competing risk could be represented by the ones who remained in follow-up. This was achieved in the secondary analysis which correctly adjusted for informative censoring using inverse probability of censoring weights (not reported in Table 3 ). A competing risk analysis would have been appropriate if the aim was to quantify the risks after taking into account that participants could also experience an early discharge, not causal inference using a marginal model. The two paradigms are often confused (4).

We also agree that to treat the intervention as time-fixed and to control only for time-fixed confounding factors was a simplification. Nevertheless, again the amount of potential bias introduced by this simplification depends on specific settings. In our setting, treatment was initiated almost immediately after hospital admission (typically within 48h) and although some time-varying variables could change very rapidly (e.g. the PaO2/FiO2 ratio) the introduction of large bias by using J o u r n a l P r e -p r o o f a time-fixed approach is likely to be negligible. In addition, to report that we ignored time-varying confounding is simply inaccurate (Table 2) . Indeed, in our secondary analysis we did control for postbaseline varying confounding of starting other pharmaceutical interventions such as steroids.

Moreover, as an example, we report the results of another recent analysis of ours aiming to emulate the RECOVERY trial (comparing the risk of death in people who were randomised to remain on steroids alone or to add tocilizumab to steroids). We performed this analysis using a time-fixed intervention variable with time fixed confounding or, alternatively as recommended by Martinuka et al., using all time-varying factors. As shown in the Table, 

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