In the current manuscript, Roy et al. have used MERR2 reanalysis data set to look at the inter annual variaility in the Antarctic stratosphere for 2013-2020. They have also used the MLS O3 measurement combined with a chemical transport model REPROBUS to derive the ozone loss inside the Antarctic region for the past 8 years. The authors have investigated the causes of Antarcitc polar ozone loss mainly focus on different stratosphere and Chlorine activation by looking at the observed ClO evolution from MLS.  The current study and methods used here are not NEW and most of the results from the current manuscript are understandable, i.e., most conclusions are consistent with previous studies. There is no exciting result or some interesting sciences to be addressed from this work. However, the paper is well written and organised. The message in the current version is clear. The quantification of chemical ozone loss for the Antarctic polar region under different meteorological conditions is still useful for the atmospheric community.  The paper is still publishable at ACP after major revision. Detailed comments are seen below:

1) In the abastract/introudction, the authors have mentioned that "ozone depletion episodes can change precipitation". How siginficant causes the precipitation changes due to ozone depletion? Is there any strong eveidence to support it?

2) Line 18 in the first page, it is not correct to say "quantifies the ozone loss.. using satellite measurements" because the authors also use the passive ozone from REPORUBUS model.

3) Following on 2), there are some inconsistecies in the current version. Line 88 says  ozone loss is from MLS satellites, Line  has caused some confusion about the "ozone loss".  Then Line 87 in Page 3 says "we calculate the ozone loss using the REPROBUS model simulations". Then the authors mentioned they have calculated the ozone loss in Line 94 Page 4  "the loss is comupted by subtracting the measured ozone from the modelled passive tracer....".

Line 92 in Page 4 mentioned that the "passive tracer identical to the ozone was initialized on July 1 of each year and contined until the end of November", but there are weird large ozone loss in early July in Figure 4. This looks to me that the REPROBUS has not simulated ozone well compared with MLS data most of the years from 2013-2020. The model simulations are even worse for 2018 and 2022 when looking at the first July ozone loss figures. Can you explain why? Is tracer transport/chemistry or other processes causing these discrepancies for 1 July 2018 and 2020.?

4) Most of the main paper, the authors claimed that "observe" ozone loss. This is only true if REPROBUS can reproduce the observed MLS ozone during the period, but this is not the case (please see 3)).

5) The caulcation of PSC areas. There is nowhere to mention what the values of HNO3, H2O etc (and where they are from) used for the PSC   diagnostics based on thermodynamic equilibrium. 

6) Line 46 in Page 2, it would be better to specific the region either altitude/regions more specifically for "significant recovery trends in the ozone"

7) Line 49 in page 2, what is the  value of "the positive ozone trends"? Based on the current version, have authors also compared the ozone loss over the period of 2013-2020 the peroid 2001-2017? This would be interesting to know if they have also seen something "A reduction in the saturation of ozone loss" over the period 2013-2017, may be similar or even sigifnicant smaller ozone loss rate over 2013-2020 compared to 2001-2017, this will make it robust to say "confirming the positive ozone trends".

8)Line 60 in Page 60, why only choose these three years? Better to add other examples here..

9) Lines 89-90. It looks that REPROBUS  is forced by ECMWF operational analyses, which has not nudged the satellite/in-situe observations. Please note that ECMWF operational anaysis has changed resolution to 137 vertical levels from 2013 , not sure why the paper cites Dee etal. (2011) which is mainly for the description of ERA-Interim reanalysis. Of course, this will have some changes in the model simulations if the authors using the simulation forced by ERA5 (as an example). 

10) Methods. Since the loss calcuation is based on the equivlanet latitude (Line 95 in papge 4), the authors still use the geographic averaged latitude to do other calcuations (for example, temperature, PSC etc..). I would suggest the authors use the same criteria to re-make the figures. 

11) some results should be careful made, there seems some results mentioned by the authors are not consistent with what it has been shown in Figures. For example Line 108 in Page 4, but I can still see the lowest temperature for 2015 occurrs in the early September, not in August in the top panel of Figure 1 .

12) Why use "growth of temperature", then "descend", "descent". They are improper used for the temperature.

13) Line 153, "the vortex lasted the longest in 2015", but looking at Figure1, it seems to me "2020" has the long-lasting cold polar vortex.

14) sometimes there is no explaination for the results shown. For example, Line  171 in Page 6, what causes the still large ozone loss in the upper stratosphere? The authors claimed "The loss is less than 1.4 ppmv in the upper stratosphere in all years".

15) For the ozone loss, the authors only look the ozone loss in different way (sometimes, they gave largest ozone loss values using different altitude or averaged different regions or periods). I would suggest the authors add the partical column ozone loss, then make one table to list the partical column ozone loss, peak ozone loss, averaged ozone loss etc, which should make the readers usier to understand the key ozone loss results from 2013-2020.

16) Again, there is inconsistent in the text and the caption of Figures. For example, Line 206 (mean of the ClO values...." and Figure 5 "peak ClO measurements". For Figure 5, there is no explaniation why 2015 has the larges PSC areas than other years, which is very hard to see from all the figures inclduing Figures 1 and 2.

This paper gives an overview of Antarctic polar vortex ozone loss and meteorological characteristics for a recent eight year period.  Most of these Antarctic winters have been analyzed in previous papers but the period as a whole and the use of model output to diagnose chemical ozone loss is unique.  This work doesn’t necessarily advance our knowledge of Antarctic ozone hole chemistry or evolution but rather gives an update on the status in recent years.  The most interesting result is the model derived ozone loss in Figures 4 and 5, especially in 2020.  It would be nice to see how the recent ozone loss compares to earlier years but that may be beyond the scope of the paper.

Although the paper doesn’t break new ground, I would recommend publication with consideration of the few comments below.  There are a number of grammatical errors that should be addressed and I don’t have time to list them all.

Specific comments:

Should include reference to Manney et al., 2020 paper that looked in detail at the 2020 winter compared to several previous winters in the time period shown in this paper.

Also, Ansmann et al., 2022 discuss the 2020 and 2021 Antarctic ozone holes and how they were affected by forest fire smoke.

Why not use the same reanalysis product for the meteorology analysis as was used to drive the REPROBUS model?  Or just use the model meteorology.  I’m sure there are differences in the meteorology of MERRA-2 and ECMWF during these years.

Line 21:  should be 2020, not 2000

Line 70: Need to include the Klekociuk et al., 2021 paper in your list of references

Line 167:  I would remove ‘in 2013-2019’ from this header.  Or at least change 2019 to 2020 since that is the correct end year of the analysis.