This is an important study.  It is the first to perform a multi-model comparison of the ozone change differences between insolation reduction and stratospheric aerosol injection, which is much needed.  The analyses are clear and well described.  I’m overall quite pleased with this study.  Nevertheless, I am recommending some revisions.

My biggest concern is that there are some overstatements and loose claims, especially regarding mechanisms.  The advantage of a multi-model intercomparison is to learn things you cannot learn from single model studies.  If the models are showing vastly different things, you can tie that to individual processes that may or may not be present, albeit doing so can be difficult.  If the models are showing similar things (which is often the case here), then you can identify robust mechanisms.  My impression of this paper is that sometimes you do this, and sometimes you simply report results and speculate on the mechanisms or reasons for model differences.  In the latter case, there is little value added beyond single model studies.  I would like to see some more in-depth investigation into why you are getting the results that you are.  (See some specific examples below.)  I acknowledge that not all models have all of the output you would need to do this.  But if the models are showing similar results, you can at least investigate mechanisms in one of the models or cite someone who has already done this.

It’s interesting that the main result you found is an increase in TCO, whereas many previous studies found a decrease.  I would like to see you talk more about this.  What’s different between your study and the previous ones?

You may want to consider moving the appendix to supplemental online material.  Appendices count in your page charges, but supplements do not (unless I’m operating under some old assumptions about fee structures).

Specific comments:

Line 8:  solar insolation is redundant

Line 16:  Do you mean 2/3 of the models?  There are more than 3.

Line 47:  denoted

Lines 171-176:  I had a lot of trouble with this paragraph.  G6sulfur and G6solar contain changes in greenhouse gases.  Also, the point of these experiments was not to reverse stratospheric temperature changes in SSP5-8.5, nor would a reversal of those changes be expected.

Line 178:  I was expecting you to talk about the specific differences between the models.

Line 189:  I’d like to see more discussion here.  The range of uncertainty for models that actually inject SO2 is much smaller than the total range.  Can you explain/show why?

Figure 2c:  I know this panel is called correlation, but did you compute a correlation or best fit line?

Figure 3:  Why does panel (d) have a different way of denoting statistical significance?

Line 204:  Why?  I don’t think you’ve convincingly showed this.

Lines 215-216:  I’m puzzled by this sentence.  If it’s not related to geoengineering then that feature would show up in the baseline simulation.  Or it’s due to natural variability.  Either way, you can’t make a claim like this without backing it up.

Lines 231-234:  Possible reason?  Did you investigate this or do you have a citation to back this up?

Line 235:  2015

Lines 240ff:  Could be?  It seems like you could (should) figure this out.

Lines 301-302:  Can you verify this?

Line 304:  SSP5-8.5

Lines 311-315:  It would be nice if you could say more about this.  Why are you getting differences?

The paper by Tilmes et al. considers the stratospheric ozone response to sulphate and solar geoengineering across a set of models participating in GeoMIP. As such, the paper investigates an important potential environmental side effect of solar radiation management geoengineering. The study is well-written and quite comprehensive already in terms of the various impacts and points discussed. I would thus recommend publication subject to a few minor comments listed below.

Minor comments:

• l. 12 on p.1 to l. 26 on p.2: in the abstract are quite complex and contain a lot of highly specific details. Maybe this could be summarised more briefly/in a simpler fashion, especially for the general reader. I think the complexity arises from discussing different regions, simulations, baselines, solar, sulphate and GHG effects, plus multiple variables. I recommend just summarising the overarching messages.
• p. 2 l. 43: maybe the effect of changing TTL temperatures on stratospheric water vapour / composition is also worth mentioning?
• p. 6 l. 168: the effect on the BDC requires a reference
• Figure 1: is the temperature (T) response (stratospheric warming) due to the aerosols mainly determined by how much warming has to be offset in each model (e.g. how much aerosol has to be injected), or is it a real mixture of factors, or other aspects are more relevant (e.g. radiative heating intensity for a given aerosol increase)? I see you comment on this in the main text, i.e. there are substantial differences. Interesting to see that the interactive chemistry models appear to show smaller T-responses. Coincidence or possibly effects of ozone loss (cooling) and increasing in stratospheric water vapour (cooling, too)? Could you comment on this?
• l. 204: “largely driven by tropospheric temperatures”. Maybe dangerous to express this way as it ignores the actual mechanism? (lifting of the tropopause under tropospheric warming and changes in the jet stream affecting wave propagation) I know there are uncertainties in the mechanism but best to rephrase. We certaintly wouldn't want new students for example to misunderstand this.
• l.212-216: could this simply be internal variability? 20 years are fairly short for polar vortex coupled atmosphere-ocean simulations. Statistical significance can give strange results in such cases, especially if p-values are not adjusted for multiple hypothesis testing.
• Caption Figure 6: maybe clarify: “for the three INTERACTIVE stratospheric chemistry models” and that this is “Aerosol surface area density”.
• l. 268: do you mean STRATOSPHERIC humidity changes (across all models considered)? Better to clarify.
• Figure 8: could you increase the resolution slightly? It looks quite coarse.
• Figure 9: maybe worth highlighting how significant those changes are relative to historical observed variability (e.g. by a grey shading for one observed sigma around zero)? For example, in the top right subfigure models show vastly different variability characteristics, which leaves the reader to wonder which model is too variable or shows too little variability.
• l. 404 don’t -> do not
• l. 413: can you say though which model(s) probably performed best / are best suited for the task? The CNRM model seemed strangely unresponsive? Is this a feature also found in Keeble et al. (2021), ACP? There, results were extremely dependent on the model and showed quite clearly that certain chemistry responses could be discounted.
• l. 425 -430: this is a central result it seems, and probably worth highlighting even more in the abstract instead of the detailed discussion of certain results? Your final sentence in the abstract already covers this point, but it be clearer/more explicit about the implications and why this questions state-of-the-art thinking in our discipline.