Dear Editor and Authors,

I found this manuscript exploring the association between DPP4i treatments and COVID-19 severity in hospitalized patients with type 2 diabetes extremely interesting and timely.

The authors performed a secondary analysis of the CORONADO study on 2462 patients and after applying propensity score (PS) based analyses found that pre-hospitalization used of DPP4i was not associated with the primary outcome (i.e mechanical ventilation or mortality within 7 days of hospitalization).

The manuscript is well written and well described, however, there are some issues that need to address:

1) The Authors stratified the population on pre-admission treatments, while no information is described regarding in-hospital treatments. This is somehow specified in the discussion but it’s not clear from methods.

Moreover, in the flow-chart it seems that patients were evaluated on day 7 for the concomitant treatments. Please clarify whether stratification was based only on pre-hospitalization treatments. This should be clarified also in the abstract.

1A) This aspect is relevant to put the results in the context of a recent published paper showing potential benefit from in-hospital use of sitagliptin on COVID mortality (PMID: 32994187).

Although that study is likely biased by several confounding factors not properly addressed (PMID:33033068), it is appropriate to compare the results of that paper with the results obtained by the Authors in this substudy of the CORONADO study.

2) Missingness and complete case analyses:

2A) In the manuscript is unclear how missing data were considered, specifically for those variables that are included in the PS model (e.g. BMI and that seems to have around 20% of missingness).

From the STROBE checklist it’s stated that the authors performed a Complete-cases analyses: “For multivariable analyses, the same population with no missing data on the different covariates considered was presented in full and adjusted models.” This should be specified in the text.

2B) Moreover, the complete-case analyses (that from table 3 seems to be on 1884 subjects instead of the 2449 described in tab1 and 2) should be considered and mention as a limitation and I would encourage the Authors to use multiple imputation approaches to overcome it.

2C) Anyway, I recommend to show the table with all the subjects included in the analyses to compute the PS. Current tables 1 and 2 (with the overall cohort) can be moved to the supplementary material, while the tables with the 1884 subjects included in the analyses should be described in the main text.

2D) Please add also a table (might goes in suppl materials) to describe the same data currently shown in Suppl table 1 but describing the population of subjects included in the propensity score-based analyses.

3) From the description it seems that the PS was evaluated for subjects included in model 0 (total n=1884). Is it unclear whether the same PS was used in model M1 (n=1344) and model M2 (n=778). Given the different populations, different PS should be estimated and used to estimate average treatment effect.

Minor comments:

• Given the high occurrence of the primary outcome, I would encourage the Authors to report the estimated treatment effect as relative risks that is more relevant from a clinical point of view.

• Figure 2: SMD scale should be clarified, is it 0 to 40 SMD or 0 to 0.4 or 0 to 4 … ?

• In the discussion, when citing the lack of association between the use of DPP-4 inhibitors
  and the occurrence of community-acquired pneumonia from any cause, please include also more recent analyses including results from observational data and meta-analyses of RCTs (PMID: 32691492) that confirms it.

I thank the Authors for their replies to my previous comments, however, the problem of missing data and of complete case scenario analyses remains a major issue in this paper.

While I agree in part with the authors on the limits of multiple imputations given the non-random pattern of missingness, these limits are less relevant than the limits of conducting a complete-case analysis, in this case, were the patients excluded from the analyses are those with the worst outcomes (see below).

Indeed, this is a clear example that complete case only analyses hides important possible perturbation of results, that might be caused by important selection bias:

1) First of all in the current presentation of clinical characteristics is misleading, indeed table 1 and 2 are not describing the population in which the main analyses is conducted that is almost 30% less as sample size. It is therefore necessary to show the population of interest in the main text.

2) The missingness in this type of data observational study conducted in an emergency situation is far from random indeed. In fact, it is possible that patients with missing data are those with worst conditions.

Excluding these patients therefore can lead to important biases. This aspect should be evaluated showing the association between completeness and outcome (i.e. Given the variable complete-case yes or not (0/1) test if this is associated with primary outcome or death)

a. This can be seen from supplemental table 5, where if you test the this association it appears clear that subjects excluded from the analyses are those with the highest mortality.

Indeed subjects excluded had almost a 50% higher probability of dying comapre to those included in the analyses. (Odds ratio OR 1.5 (1.2-2.0) p = 0.002)

3) This bring to the issue also of table 3
- table 3 must include the sample size included in each model, otherwise one could have the wrong impression that the sample size is the same. Moreover please include P values, since one needs to interpret these data in the context of the multiple tested hypotheses.

• One question remains, and should be clarified. Why the effects of DPP4 on death is almost 3 times-higher from model 1 to model 2 ? is it because the diabetes duration and hba1c are such strong negative confounding factors?

This seems unlikely. This can be related to the different populations, is that a selection bias (e.g. patients with worst outcome on DPP4 have been excluded in this analyses) or it is because of a true effect of DPP4 in this population?

One way to initially look at that is to check the model 0 and 1 in the same population where model 2 has been tested. If the effects are similar in all models then the nominal association is likely linked to selection bias and not on true effect of DPP4i.

Therefore it is likely that the reported lower mortality associated with use of DPP-4 at 28 days is a chance findings.

I recommend clarifying this aspect in the discussion and remove the following sentence from the abstract (“A significant reduction of mortality on day 28 after admission was observed in DPP-4 inhibitor users (OR: 0.53 [0.31-0.89]))

Altogether I recommend two options: perform multiple imputations or keep the current analyses with additional ones clarifying the presence of a bias linked to the selection of patients only with complete data (i.e. higher mortality in excluded patients), modify the reported data, and remove all comments on the nominal association between DPP4i and lower mortality that seems unreliable.