The authors aim to explore how NOD.Q-derived haplotype encoding also the low affinity FcgR locus (referred to here as Cia9) contributes to arthritis development in B10 mice. Specifically, they attempt to disentangle the role of haplotype-encoded FcgRIIb and FcgRIII compared to global deficiency of these receptors and with minimised impact of the NOD.Q flanking region. They use 4 congenic mouse strains with varying coverage of the Cia9 region that allow them to study ‘natural polymorphism’ of the FcgR genes on mouse chromosome 1, indeed they convincingly demonstrate that the NOD.Q-derived FcR genes are implicated in exacerbating CIA and CAIA. The manuscript will of interest to immunologists working on elucidating factors that contribute to autoimmunity, but some important experiments and controls are currently missing, similarly the authors should address discrepancies with published data better.

Major concerns:
1. Lack of phenotyping of these 4 congenic strains with respect to how NOD.Q haplotype affects the expression of the various FcgRs. Some of these are shown in later figures (Figures 5-8), but not across cell types, especially of interest are the Cia9k and Cia9i compared to WT mice. Are defects specific to cell types examined? This needs to be demonstrated. In addition, the authors should explain, if FcR expression defects only arise following disease onset or with inflammatory stimuli (not always present in naïve mice) – how can these be ‘disease causative’?
2. The authors should show at which point global FcgRIIb-deficiency results in increased anti-CII antibody level, this is an important control – currently missing from Figure 3 (as the mice need to be sacrificed earlier could use this timepoint)? This is important as the authors’ interpretation is that unlike global FcgRIIbKO mice, the Cia9i and Cia9k mice do not have increased 'autoantibody' production – yet the authors have not shown the increased antibody production in FcgRIIbKO; previous observations by others may be due to now much better appreciated impact of microbiome on immunity and 'cleaner' animal facilities.
3. It is not clear how the authors have excluded an effect for FcgRIV? This should be addressed as both Cia9k and Cia9i strains contain the FcgRIV gene, that presumably could play a role, but is ignored by the authors; and it has been previously implicated in inflammatory diseases. The only figures where it features is Supplementary figure 4 and Figure 6 some (few panels), which does not justify conclusions that are exclusively based on expression of FcgRIIb and FcgRIII.
4. The rationale for using the CIA and CAIA should be explained a lot better. At the moment not clear what the advantage of using the two models is.
5. Figure 5 shows reduced expression of FcgRIIb in B cells activated with LPS in vitro, the relevance of this is unclear, B cells should be isolated from CIA mice for the assessment of FcgRIIb expression. The same is true for myeloid cells and NK cells.
6. The switch from spleen to peritoneum to investigate myeloid population is not clear – how is this relevant, when previously only investigated the splenic populations? Should certainly also show data from the spleen.
7. The authors have on a number of occasions referred to discrepancies between their observations and those made by Luan JJ, Monteiro RC, Sautes C, Fluteau G, Eloy L, Fridman WH, et al. Defective Fc gamma RII gene expression in macrophages of NOD mice: genetic linkage with up-regulation of IgG1 and IgG2b in serum. J Immunol. 1996;157(10):4707-16. Since three of the discrepant findings are also most relevant to understanding the impact of the haplotype, the authors should explain this
8. Albeit there seems to be an effect of FcgRIIb exerted by the haplotype – it is not clear what the authors propose the mechanism is – altered macrophage function? This should be substantiated by experiments in the CIA model. If peritoneal macrophages are the important subset in this disease, they should demonstrate their depletion negates the disease exacerbating phenotype in Cia9k and Cia9i, compared to WT?
9. A control is missing for experiments in Figure 8, namely blocking of FcgRIII, to demonstrate direct effect of increased receptor on depletion of these cells, rather than enhanced Treg depletion via another mechanism.

Minor concerns:
1. The NOD.Q-derivation of haplotype should be mentioned in the abstract.
2. Suggest that it is more appropriate to refer to mouse ‘strains’ rather than ‘lines’.
3. The authors have not sufficiently explained how the NOD.Q haplotype/FcgR locus, if at all, relates to any observations in humans. Relevance should be established.
4. Results section relating to Figure 2 describes CIA only, while B and D are presumably CAIA.
5. Reference 11 does not refer to the SLAM locus, should be better explained.
6. Occasionally the ‘gamma’ in FcgR is a ‘y’.
7. CAIA only explained in results section for Figure 3, but already used in Figure 1. Should be introduced, when first used.
8. Lines 170-172 – not clear what data the authors are referring to as they do NOT show any differences between FcRIIb and FcRIII in Figure 3C-E.
9. Lines 172-174 also do not appear to be describing the data – perhaps if disease incidence is taken into account?
10. Abstract refers to the genes as ‘disease causative’, however, that is an overstatement of the findings, suggest ‘exacerbate’. Unless the authors are referring to increased disease incidence, albeit this is not explicitly discussed in results.
11. I am somewhat confused by the title – do the authors mean that the alleles are linked to inflammation or to each other?
12. End of line 20 – ‘been’ missing in the sentence.
14. In figure 1, it would be helpful if the authors showed location of SLAM within the Cia9.
15. The specific epithet of species name should not be capitalised – relating to results description of figure 4.
16. Currently the authors have no explanation for testing FcgR-independent and ROS-mediated effects of the congenic fragment (Supplementary figure 1); whether the data are meaningful cannot be assessed.
17. Text refers to Supplementary figure 2, but the data it refers to are in fact in Supplementary figure 3 and vice versa.
18. How do the authors explain reduced FcgrIIb expression on macrophages, but not on B cells in the naïve state?
19. Rewrite the sentence relating to Supplementary figure 5 – lines 342-343.
20. Bars for significance are not consistent in style between figures.
21. Suggest that two-way ANOVA is more appropriate than Mann-Whitney U for comparison of disease severity between groups of mice.

Overall the manuscript text is now difficult to follow (while my comments have been to a large extent addressed, it is a different manuscript now), I believe because of the substantial changes since the original – it lacks cohesiveness, flow; there is also not sufficient explanation for the assays used. Comments 1 and 2 have been addressed however by reducing the size of manuscript which has removed the ambiguous language/overstating findings. The abstract currently is not very informative and neither is the title.
Comment 5 has not been addressed – it is not clear why LPS was chosen to activate B cells, is this what authors envisage driving B cell differential expression in CIA/is it CIA mimetic somehow? Is FcgRIIb upregulated by TLR-signalling? The authors’ reasons for choice of stimulant may be entirely relevant, but are not clearly explained. Similarly for macrophages? I am still somewhat confused as to why the authors have not even attempted to compare naïve and CAIA B cells, macrophages, NK cells. Particularly as within Cia9i and Cia9k there are both mice that develop and do not develop disease? Comment 6 – I believe that it is legitimate to state that the cells are more difficult to isolate for functional studies, but at least the expression of FcgRs can be done on splenic cells rather easily?

To the Authors,
The authors have not addressed comments 5 and 6 –if they are attempting to explain the impact of FcgammaRs in arthritis, and they have chosen to show both CIA and CAIA – then the mechanism is the same in both disease models? If not (the mechanism is not the same) – then authors should not show both disease models. If the mechanism is the same, then the stimulus driving FcgammaR differential expression should be shared? I can accept that it could be an inflammatory and mimicked by LPS, but it is very much a leap, when the authors have not showed that diseased animals share the defect as observed with LPS stimulation of cells derived from naïve mice in vitro.

The response about space restrictions to asking to see ex vivo data for myeloid cell is not sufficient.

The below relates to my first comment about the overall impression of the manuscript.
The authors should not overstate results, use language clearly and precisely. The two below are statements that are not interpretable and there are a number of similar claims throughout the manuscript:
“To study a possible FcγR3 independent effect of the congenic fragment, we first investigated reactive oxygen species (ROS) induced phagocytosis of Daudi cells, showing a difference by the Cia9i but not the Cia9k fragment. ” – between what and what? Compared to WT?
“The serum levels of anti-CII Ig, IgG1 and IgG2b were elevated in FcγR2b KO mice, which was related to arthritis severity rather than a direct effect on B cell response.” - as far as I can tell, only IgG2b are significantly elevated?