This study investigates the functional consequences of a selection of autoantibodies that have been previously described in the sera of COVID-19 patients. In particular, the authors focused on anti-ACE2 autoantibodies and anti-IFN autoantibodies. They found that a large percentage of COVID-19 patients had autoantibodies against these ‘self’ antigens, but suggest that for most of these patients the autoantibodies are polyreactive and unable to functionally inhibit either ACE2 or IFN. They provide evidence that a smaller fraction of COVID-19 patients have target-specific autoantibodies (e.g. against IFN), and that these target-specific autoantibodies are more functionally relevant.

This is a manuscript that will be of interest to immunologists studying the autoreactivity noted to develop in COVID-19. The manuscript is clearly written, and the data mostly support the key messages. The overall concept presented is also important. However, there are several areas where experimental data might be needed to clarify findings and support the concept, or where clearer explanations are necessary:

Experimental clarifications:

1. Fig 1I – To make these observations compelling, the authors need to control that they have successfully enriched all the IgG from the sera in the pull-down assays. If only a fraction of total IgG is purified, could this account for the observed lack of effect? This could be assessed by reanalysing the eluted IgG with their ELISA assay to determine if binding to ACE2 is the same as the whole serum and would provide an important control. Analysing total IgG before/after pull-down would also be an indicator of successful enrichment. I note that the methods state they validated pull-down by checking absorbance at 280nm, but this would just pick up any sticking protein, and would not be specific to IgG or give an indication of enrichment. It could also be tested if the sera with IgG depleted (and validated to have no IgG) still inhibit ACE2. Related to this, can the authors speculate on what the inhibitor of ACE2 function is in patient sera if not the ACE2-binding IgG?

2. Fig 2H-J – the authors only use a single amount of IFN in their assays. However, it is possible that polyreactive antibodies might still inhibit IFN function, albeit they are not able to counteract the amount used in this study. Assays performed with smaller amounts of IFN would uncover this and might change the conclusions of the authors.

3. Related to line 141 - The authors note that some target-specific anti-ACE2 sera (n=12) do exist. It would make the authors’ results more generalisable if they were to test these sera in the ACE2 function assay of Fig. 1I. As the manuscript stands, it reads that all the ACE2-binding antibodies do not inhibit function, while only some of the anti-IFN autoantibodies are specific. It would be valuable for the audience if the target-specific autoantibodies observed have relevance not only to IFN, but also to ACE2.

Other clarifications:

Line 86 – How were the reference parameters determined to make the statement that IgG titers were low?

Fig 1B – Please add a legend for this panel and define ‘rec’.

Line 99 - It is not clear how correlating serum sACE2 with anti-ACE2 IgG addresses anything about sACE2:spike complexes contributing to ACE2 reactivity. Please clarify.

Line 103 - If there is a weak correlation between sACE2 levels and anti-ACE2 IgG (Fig 1G), how can the authors be so definitive about ACE2 reactivity not resulting from sACE2 as a target-specific response?

Line 107 – Please add a reference to the previous work looking at inhibition of recombinant ACE2.

Fig S2C/D - The authors observe quite a continuum of anti-IFN autoantibodies in their assays, with a very high proportion of apparent positives (compared to healthy donors), whereas other investigators have reported more discrete positive/negatives for anti-IFN autoantibodies with only about 10% of severe COVID individuals being positive (original study and a number of follow-ups from different labs). Why do the authors think they detect such high positivity rate for these autoantibodies in their cohort? Is it something to do with their assay versus others? When they assess target-specific anti-IFN IgG, they say this is 2.2% of total samples (line 141). What % is this from severe COVID samples? Does this now match with the observations of others that it is about 10% of severe COVID patients that have these anti-IFN autoantibodies?

Line 146 - It would be useful if the authors described in a bit more detail how they defined these groupings of promiscuous versus target-reactive. If they are based on specificity of reaction (ie binding IgG to ACE2 and IFNa = polyreactive, whereas binding IgG solely to IFNa = target-specific), this would be useful to highlight in the graphs so it is visually obvious.

Fig 2H-J - Because of the color scheme in Fig 2G, H and I, it is not clear if the ‘target-specific’ anti-IFN sera are actually from the SLE patients (many of whom have anti-IFNa antibodies) - can the authors clarify for the reader that this is not the case and that H-I refer to the COVID cohort? In this regard, the title to figure 2 suggests that all severe COVID-19 sera don’t block IFN function, while IFN-specific sera do. Perhaps consider re-wording for clarity?

Fig 2H-I - It would be useful to the reader if the samples/donors noted in Figs 2H and I could be matched up so that cross-comparisons between the figure panels were easier

The authors have very nicely addressed all of the points raised regarding their original submission and clarified their findings with new experimental data or discussion. The manuscript will be of interest and relevant to a wide audience interested in, and studying, autoantibodies in infectious diseases.