Review of Yuwen Li et al., 2025, The Impact of Rocket-Emitted Chlorine on Stratospheric Ozone 

This is an interesting, timely and well written article. As rocket launch rates increase, understanding the role of rocket exhaust on stratospheric composition is crucial, since the stratospheric ozone layer is a vulnerable, recovering part of the planet. You report on stratospheric ozone changes under different chlorine emission scenarios from rocket launches. The conclusions drawn are supported by the simulations they present, but much more context and confidence could be provided by model evaluation. I also think the methods section requires clarification. I have compiled my thoughts below, comprising major revisions I think should be addressed before publication. 

Major queries: 

1. Why did you not include other pollutants? This is an especially important question for NOx, which Ryan et al. (2022) found to be a more important factor in stratospheric ozone depletion than SRM-derived Clx and alunima. 
2. Your choice of time period needs further justification and explanation. Why did you choose to simulate 1990-2012? During the early 1990s, the Montreal protocol was just gaining momentum and stratoshperic ozone holes were still frequently very large. In addition, the relevant rapid space industry expansion is a modern post-2012 phenomenon. I understand that you wanted to use reanalysis meteorology, which necessitates going back into the past, but it would be great to elaborate on the justification of your time period choice, and why you didn’t choose to go from 2025 or 2024 back.  
3. Moreover, it is unclear to me whether your simulations for 1990-2012, with 2019 rocket emissions, have underlying changes in anthropogenic emissions - especially ozone depleting substances  - that were occurring during 1990-2012. You mention that greenhouse gas levels are constrained to 2020 levels, but the inclusion of other anthropogenic emissions needs clarification. ODS emissions have changed significantly between 1990 and 2012 following the Montreal Protocol. 
4. You say that you “focus solely” on the Clx emisions but can you please clarify whether that means you include only Clx emissions from rockets, or include all emissions but only vary Clx/only focus on changes caused by varying Clx. 
5. To build confidence in your choice of model and reanalysis data, validation plots of stratospheric ozone are needed. This would provide strong context especially to your discussion of interannual variability. How well does your model do at capturing observed total column ozone and vertical profiles in the Arctic and Antarctic? Without this, there is no way to assess the significance or uncertainty in the results you present. So, I think an extra “control” simulation is needed with realistic emissions for 1990-2012 to allow for model evaluation. 

Minor queries and suggestions: 

Line 38: “the hydrocarbon” probably should be “hydrocarbons” 

Line 46 onwards: The discussion of Ryan et al (2022) needs some refinement: that paper examined all rocket pollutants, not just NOx, and in addition, it would be fair to say they found launch NOx “relatively less important”, but not “not important” as you state. It is worth pointing out here that the ozone impacts in that paper were most significant in the upper stratosphere. 

Line 81: It is worth putting the longitude of Korou too. 

Line 81: Link to table 1 here as this is where you outline the emission inventory scaling year on year. 

Table 1: if you’re keeping the focus as Clx emissions only, it would be helpful to add a column to the table detailing the magnitude of the Clx emissions (i.e. Tg Clx). This would help the reader understand quickly the extra Clx in each simulation. 

Section 3.1: You show Cly increases. Could you elaborate briefly (in the text is fine) on which species dominate the Cly changes in your rocket scenarios? 

Line 137: “These are the regions where chlorine chemistry is expected to have an impact on ozone” - this sentence (and possibly  the one after it too) sounds like it needs a reference. 

Section 3.2: in your discussion of ozone decreases (e.g. of a certain amount of ppb, or DU), it would provide great context to readers slightly less familiar with stratospheric ozone if you included what these changes amounted to as a percentage. (You do this at some points but it could be more widespread.) 

Figure 8: one advantage of your simulation period is that there were some significant ozone holes in there. When you talk about interannual variability, you have the opportunity to contextualize the significance of the ozone depletion due to rockets (and each year’s meteorology) against the size of the each year’s actual ozone hole. This could either be as a percentage in the text, or incorporated as a timeseries into Figure 8. 

Line 250 onwards: could you hypothesize further on why you think you model a smaller Cly concentration change than Revell et al (2025)? What differences in deposition, chemical scheme or other model factors might give rise to this? This seems like a pretty significant difference in conversion to reactive chlorine, which it would be good to understand (and again make me wonder how well your model performs relative to observations at converting other ODS to reactive chlorine and simulating past ozone holes). 

Manuscript #egusphere-2025-5346 titled “The Impact of Rocket-Emitted Chlorine on Stratospheric Ozone” takes a detailed look at how chlorine emissions from spacecraft using solid rocket motors (SRM) may impact the health of the ozone layer in the stratosphere. The authors ran the WACCM6 model, nudged with MERRA-2 reanalysis data in order to represent realistic stratospheric meteorology. This methodology also allows for one to isolate the chemical impact of chlorine emissions on stratospheric ozone and perform detailed investigations on stratospheric chemical processes. The authors investigated multiple launch scenarios ranging from a modest 10x the 2019 annual launch frequency of SRM vehicles to an extreme 120x annual launch frequency. The authors show that increased chlorine emissions from the simulated scenarios leads to modest losses in stratospheric ozone that scale linearly with increased launch rates and can potentially slow stratospheric ozone recovery.

While SRM vehicles make up a smaller portion of the present-day launch fleet, this work follows the same path as previous studies which isolate and investigate specific rocket fuel types and the potential impact of emissions from these engines on the middle atmosphere. This manuscript is timely, very well written, and it adds a new piece to the evolving puzzle that is understanding the impact of this new age of space travel on the atmosphere. Overall, I believe this to be excellent work that deserves publication, but requires specific revisions prior to publication, mainly in the motivation and discussion sections.

Major comments:

• I don’t see much justification for the 10x/52x/120x launch scenarios. While the 52x and 120x are clearly meant to be more hypothetical, what is the likelihood of the 10x scenario? Can you provide a probability or potential date that this emission frequency could occur? SRM is not the most heavily used fuel type relative to others such as kerosene and liquid natural gas. While there are clear projections that show both kerosene and liquid natural gas fuel usage increasing, there isn’t as much information about the future of SRM. In fact, some believe it will be used less. Therefore, I’d like to see a stronger argument which supports the notion that we might experience an increase in SRM launch rates such as those studied here.
• Could the authors please provide additional reasoning for choosing to run the model only between 1990-2012? Almost all of the increase in launch rates occur after 2015 with the exponential growth starting in 2019. Wouldn’t it have been better to run simulations through more recent years where your stratospheric chlorine and ozone levels, as well as anthropogenic emissions are more up to date? MERRA-2 is generally up to date (at least through 2024), so the data should be available. If authors believe that the simulation time-frame doesn’t in fact matter, then please provide a reason why this time-frame was chosen.
• You might consider including a baseline control case with the default WACCM emissions somewhere within the manuscript, or supplemental information. This can help readers know that WACCM is indeed producing a realistic stratosphere and seasonal ozone. Additionally, this would help show the scale of the ozone depletion caused by the rocket emissions relative to baseline conditions.
• In the latter half of the discussion section (line 239 onward) the authors compare the magnitude of their ozone depletion from SRM chlorine emissions to that found in the Revel et al. 2025 paper. I worry that the authors may be under representing important differences in methodology between these two studies which likely play a role in the final ozone discrepancy. Previous studies have shown a relatively strong ozone response to dynamical and temperature anomalies caused by the presence of other rocket emissions, especially aerosols (i.e. black carbon). While I think the comparison in this manuscript to the Revel et al. 2025 study is interesting and informative, there needs to be stronger mention of the fact that this work does not include the important contributions of aerosol stratospheric heating and dynamical shifts which may be driving most of this discrepancy between the two studies. This may be beyond the scope of this manuscript but quantifying the individual contributions of chlorine chemistry, stratospheric dynamics, and aerosol heating on ozone would be very interesting.

Line by line comments:

Line 40: this sentence reads awkward to me. Please consider rewording

Table 1: is it possible to add an estimate year or future scenario in which these numbers of launches may occur?

Line 100:  Please provide which fields were specifically nudged by the reanalysis data. Were only SST’s, winds, and temperature nudged? Or did you nudge chemically as well? 

Figure 9-10 caption: I would mention that the contour scale changes amongst the panels

Table 2: These are annual averages, correct? If so, please state that in the table or table caption. Could you please include the error range which represents the year-to-year model variability in ozone alongside your ozone depletion values? Or please provide a calculation of statistical significance relative to the model variability. This can help show whether the ozone depletion values are outside model noise or not.