This study focuses on the global and regional (tropical, subtropical, and springtime polar) impacts of a new SAI experiment on stratospheric ozone changes and potential drivers. This experiment mainly differs from previous GeoMIP experiments by injecting SO₂ at symmetric subtropical latitudes instead of equatorial bands, and using a pathway of lower GHGs, namely SSP2-4.5 compared to SSP5-8.5, and reducing the warming to roughly present-day temperatures. It applies a multi-model approach to differentiate between inter-model and SAI experiment differences. Chemical and dynamical effects are separated using additional model runs that exclude heterogeneous chemistry on SAI aerosols. The simulated SAI experiments exhibits smaller lower stratospheric warming compared to equatorial injection scenarios, which translates into smaller stratospheric circulation changes.

The studies' main findings include the need for more accurate modelling of stratospheric transport, as inter-model differences appear to be driven by these. Generally, inter-model differences dominate over differences within injection scenarios in the one tested model. There seems to be an asymmetry between the polar responses. The authors attribute the decrease in column ozone to halogen catalysed chemical loss, and transport changes induced by SAI. As process importance differs between different latitudinal regions, the authors separate different contributions and attribute dynamical response differences to process level uncertainty in stratospheric transport.

The below-mentioned comments are not critical, but require some changes that go beyond simple re-wording. Thus, I suggest moderate revisions of the manuscript as outlined below.

Since heterogeneous halogen activation on sulfate aerosols is put forward as one of the major factors in decreasing ozone columns, a brief introduction of the mechanism, corresponding studies, and model differences would be helpful.

At multiple instances in the manuscript, the authors refer to either "heterogenous" or "heterogeneous" chemistry. Please check for consistency.

At multiple instances, the authors write TO3 or O3, please correct this to O₃.

Please check for consistency when referring to sulfate and sulfate aerosols.

l.26: Instead of, or additionally to, "more plausible middle-of-the-road", please mention the SSP.

l.29: "compared to [a] no-SAI"

l.35: While agree with the strategy dimension, I don't recall analysis of the scenario dimension. At least in case the latter refers to different SSPs. To keep this argument, some further analysis to isolate its influence should be included, which may already be present in previous G6-1.5K-SAI publications.

l.38: A reference for ozone's shielding role, and effects on life and ecosystems should be included here.

l.43: Since the impacts of climate intervention methods are highly uncertain, a more careful formulation, such as "to [potentially] temporarily offset", should be considered here.

l.52: This full sentence lacks a reference to acknowledge previous work.

ll.53-55: This statement also lacks at least one, or several references.

ll.64-66: This statement lacks a reference to heterogeneous chemistry of aerosols. At this stage, more details on halogen chemistry, and results from other models (e.g., SOCOL, MPI-ESM) with aerosol chemistry could be added.

l.68: Please reference the GeoMIP project properly here.

l.77: Consider hyphenating "middle-of-the-road".

l.79: Consider hyphenating "business-as-usual".

l.100: "each of the model[s']"

Figure 1 (a): This figure would benefit from a shading or similar representation of errors to better estimate model differences. This is especially the case for the runs with SAI. The authors may also consider a visualisation and brief discussion of the inter-model differences in the chosen base-line states, and their impacts on their findings.

l.115: Please clearly state the CESM version.

l.121: "including [the] most"

Table S1: Please write "2 Cl", "2 Br", ...; please also restructure the table's title, for instance moving "in each model" to the end of the title. 

ll.160-162: This statement regarding the coarse mode may also deserve a citation.

ll.162-164: This statement regarding the SAD would pose as significantly increased uncertainty of chemical responses and would deem SAD as a much weaker constraint for this response. It would potentially also limit the extent to which chemical responses in UKESM imply responses in MIROC. This aspect deserves some further discussion in the corresponding section (section 7 or 8).

Figure 2: A visualisation of the uncertainties would be useful. Subfigure (c) uses a different period (2050-2069) on the right side compared to the left side. These differences should be discussed and evaluated. In the same subfigure, the relation of ozone and surface temperature change seems to be ambiguous and without clear physical connection. In case the authors want to use this metric, it should be more thoroughly introduced before.

l.180: lacks a reference to BDC changes following GHG emissions.

ll.184-186: The statement on dynamical effects on ozone lacks references, being itself not straightforward, nor directly related to the results of this study.

ll.186-188: The connection between global-mean total column ozone and surface temperature is ambiguous, and neglects the complex relationship between the two. It appears that the authors aim to connect the ozone column changes directly to potentially policy-relevant changes in surface temperature. By doing so, the underlying processes are blurred and physical understanding is lost. To my knowledge, no direct connection between these two quantities exists that would allow to link them in this way. I recommend to either exclude this metric (ozone column change per degree of warming), or justify its use and physical foundation more clearly. This oversimplification must be removed in the final version of the manuscript. This holds for all plots using this metric.

l.192: "larger earlier in the century than later" --> This doesn't really hold for CESM, except from the mid-2070s.

l.194: "progressively higher" --> the aerosol burden curve seems to flatten, whereas temperature difference increases roughly linearly. This may be discussed in the context of separating the earlier to later parts of the century, instead of mainly focussing on decreasing halogen concentration.

ll.224-226: I don't agree with this statement for the earlier period from 2045-2064. Please clarify this confusion, and also rather refer to the figure than, or in addition to, the original paper to clarify the comparison here.

l.229: Please reference the G6sulfur experiment.

ll.229-230: "and thus potentially less favourable outcome" --> I suggest to omit this part, being speculative and not adding information.

Figure 3: (a) is very busy, and may justify only showing the running mean (with uncertainty); (b) shows a jump (with change in sign) for CESM which may be discussed in more detail to ensure it being physical. 

Figure 3 (c) uses 'DU' as the y-axis as physical quantity, whereas it should be 'TO₃' in [DU]. Similarly, Figure 6 confuses physical quantities and units. Please check all Figures regarding these.

Figure 4 lacks indications of the physical quantity (pressure) and its units (hPa) on the y-axis; please also add the diagnosed tropopause, since it is referred to at several instances in the text, but seems to be defined inconsistently.

ll.250-251: I only agree with the decrease in tropical ozone column from around 2050 in CESM and MIROC, and from around 2070 in UKESM. 

l.252: Please reference the figure showing the change in the BDC here.

ll.252-254: The connection between lower stratospheric decrease in ozone and upper stratospheric ozone is not clear. Please reformulate (and split) this sentence to clarify the argument. 

l.256: The difference in sign of the ozone response appears like an offset. A discussion of this effect between the models would be useful here. For instance, adding a factor to the UKESM response could shift it towards the observed CESM values. Within this framework, a brief discussion on the influence of the early phases of SAI on the following trajectory or sensitivity tests could be insightful, and further make the results more robust.

ll.257-258: MIROC seems to drift more significantly towards more negative values in Figure 3 (a). A short discussion of possible reasons and corresponding uncertainty would be useful.

l.267, l.276, l.280: The mentioning of the lower stratosphere and tropopause seems to use different definitions of these regions. Please ensure to consistently refer to the same regions, and annotate them within the corresponding figures.

ll.272-274: This statement requires a reference, or more elaborate evaluation.

l. 283: Please be more concrete in linking stratospheric warming to circulation changes. For instance, one may rather refer to "stratospheric circulation" and its specific features (e.g., BDC) rather than circulation in general.

ll.283-285: This statement is not new, and deserves acknowledgement of previous work.

ll.304-307: "The much lower climatological stratospheric water vapor in MIROC (Fig. 7h) might reduce aerosol water uptake and hence partially contribute to the model showing comparable amount of heterogenous halogen activation and halogen-catalyzed ozone depletion than the other two models (Section 3, also Sections 5-6), despite much larger aerosol SAD (Section 2, Fig. 1d)." --> Aerosol water uptake, or hygroscopic growth, mainly depends on Relative Humidity (RH) and not stratospheric water vapour. The former determines the thermodynamic equilibrium vapour pressure over binary solutions such as H₂SO₄-H₂O droplets. RH is generally very low in the stratosphere, resulting in large decrease in uptake sensitivity with height. The climatological absolute humidity in MIROC may be significantly lower than in the other two models, but so may saturation vapour pressure, resulting in relatively constant RH, and thus aerosol water uptake. I suggest to check RH for differences between MIROC and the other two models to constrain this statement.

Figure 5: In case no AoA figure is added for CESM, please change the naming of the subfigures to (a)-(e). This figure also deserves an annotated diagnosed tropopause.

Figure 6: Please write (a) and (b) in the caption, not (A) and (B). Write-out the abbreviation "TEM" in full please.

ll. 342-344: Increased transport by the BDC resulting in increased ozone lacks a reference.

Figure 8 would perhaps benefit from using relative instead of absolute units for ozone columns. Such a visualisation may also limit the model dependence on inter-model differences in climatology.

l. 350: I would agree with this statement for CESM and MIROC, but not for CESM.

ll. 352-354: Please provide some reference or figure for this statement. In this context, some justification for the presence (and absence) of these difference may be added.

ll.363-364: "higher climatological" than what?

ll.382-384: I agree that figures 9 and 8c illustrate the change in TO3, but don't see how they allow to attribute these to transport changes.

ll.384-385: Please show, or reference, the difference in the importance of chemistry vs. transport in a figure or similar to support this statement.

l.394: Figure 5d is non-existent.

ll.410-411: The projected increase in ozone is still debated and not as clear as stated here.

l.413: Just write CESM and MIROC here, without the later negation.

ll.416-419: This statement blurs climate sensitivity and ozone columns, and deserves justification or correction.

l.442: "Domaisen" -> "Domeisen"

ll.453-454: Please reference the corresponding figure here (10b).

ll.473-475: This statement deserves a reference.

ll.478-480: Neglecting differences in surface cooling and injection rate and deeming them less relevant deserves further justification.

ll.486-488: This statement lacks justification on why it has to be halogen catalyzed loss, and not other chemical processes, or chemistry-dynamics interactions.

l.487: "pearly" -> "clearly"?

ll.545-548: The direct comparison to Tilmes+2022 seems difficult since it uses a different "strategy" and scenario. I agree that mentioning these differences is relevant, but directly inferring conclusions from them obscures the differences and complexity.

l.579: I agree with the importance of mentioning the comparison alongside SSP2-4.5. However, its implications for the analysis should be further elaborated to justify its mentioning.

l.581: The "lagging" of the ozone response is not strictly shown here. Especially from 2060, the ozone responses rather seem to converge. This statement requires further justification.

ll.583-584: Please provide reference(s) for this "common assumption".

ll.584-586: I don't see the relevance or direct connection to the results and objectives of this study.