I struggled with this paper.  The analysis is done quite well, and I couldn’t really find any technical errors.  But my problem is the motivation for the study and the framing.  This is just a weird idea.

More specifically, the authors conclude that to scrub SAI, you would need to do an SAI-level effort.  So who, exactly, is doing this?  Someone who is opposed to SAI and wants to stop SAI is…going to do SAI?  I don’t get it.

Related to that, the authors assert that this method is “effective”.  That may be true from a purely chemical standpoint (more on that shortly), but that’s a really narrow perspective.  If your countermeasure takes as much or more effort than the original activity, I wouldn’t really call that effective.  And again, it requires building a huge amount of infrastructure that is, until deployment, indistinguishable from SAI.  So it’s hard to justify effectiveness in many senses beyond chemical.

Getting into the chemistry, the choice of calcite is poorly justified.  There are also really important processes missing, including aerosol mixing state (it looks like you use a simple assumption for this), chemical interaction (offline oxidants), and aerosol aging.  There is strong evidence to suggest that after a while the calcite aerosols just get covered in sulfate and look a lot like sulfate aerosols.  And in terms of particle growth, using a modal double-moment scheme probably has some issues.  The point being, while this is an interesting idea, you’ve made enough assumptions in your model that your results could be totally wrong.

And finally, I don’t understand the call to include this in GeoMIP.  Getting the microphysics and chemistry right for this idea is highly important.  Only a small handful of GeoMIP models can do this.  If you had proposed it to CCMI I might agree.

Overall, I have trouble with what the authors did, including the justification for doing the study in the first place, how the modeling was done, and the interpretation of the results.  I think these issues could ultimately be addressed by reframing the paper, as there’s some good technical work in here.  But considering the headlines this idea might generate, overclaiming what you’ve done and the results you’ve found is irresponsible.

This manuscript presents findings from general circulation model simulations with interactive stratospheric aerosol and chemistry, to assess aerosol scavenging effect from calcite particles,  within a future scenario of an elevated sulphate aerosol loading in the stratosphere following a large-scale deployment of Stratospheric Aerosol Injection (SAI) geoengineering.

The model simulations are designed to quantify the efficacy of a notional “counter climate intervention” situation, where the calcite particles have been emitted to an already developed SAI-enhanced stratospheric aerosol layer in the years after a large-scale SAI geoengineering deployment.

These are interactive stratospheric aerosol simulations where both types are transported independently in the model, the calcite emission handled as essentially a high-altitude size-resolved dust emission, but with modified aerosol properties.  

The notion of the “counter climate intervention” is introduced, with this action of a separate additional injection of calcite particles designed to change/reduce/neutralise the initial surface cooling effects from the spun-up “SAI geoengineered” elevated stratospheric sulphate aerosol.

The simulations apply the latest version of the UK Met Office model (UM-GAL9) and explore the extent to which such a targeted anthropogenic emission of calcite particles could “scrub” such a global geoengineered sulphate aerosol haze, and how the SAI radiative forcing would be affected (to what extent the intended surface cooling effect from the sulphate SAI geoengineering would be reduced).

The authors have run quite a large number of simulations to explore this scenario (Table 1), and the science topic aligns with SAI predictions, the interaction of the calcite with the sulphate aerosol a novel aspect, and then certainly scientifically relevant to the Atmospheric Chemistry and Physics journal.

However, I have to say I agree with most of the comments made by the other reviewer, in relation to this scenario being somewhat far-fetched, or too secondary to an already uncertain main SAI simulation.  The main effect explored is the scavenging/scrubbing effect, which is implicitly strongly dependent on the model's simulated SAI enhancement, and then it is unclear what the reader can conclude meaningfully from these secondary integrations.



I also tend to agree with the other reviewer’s questioning of the motivation and framing for this study. And having thought carefully about this decision, I feel this study is too exploratory for publication within a specialist journal such as ACP.   Other journals (e.g. Earth’s Future or Geoscientific Model Development) would be more suitable for these  simulations, towards then publishing what is currently a highly exploratory study, geared to a somewhat secondary counter-intervention scenario that seems poorly motivated, at least within this initial manuscript (see specific comments below).

I realise the authors have put a considerable effort into running and analysing the model simulations, and do share also the other reviewer’s positive comments that the results within the manuscript are well explained, and presented well.  However the manuscript is in my opinion out of scope for ACP.

One specific point the other reviewer makes, is to question whether this scenario be included within the next phase of GeoMIP.   And whilst I do not respond with my own views on that, I do see why the reviewer asks the questions there. It relates to the central question of the study exploring model responses from a control run which is itself very highly uncertain.

And then these secondary experiments, to assess a “counter climate intervention” effect seem premature, when there is such a large uncertainty around the main question of efficacy and risks from SAI geoengineering.

Whilst for the Pinatubo observed case, the different interactive models agree quite well (Quaglia et al., 2023), Clyne et al. (2021) have shown how differing treatment of chemistry and physics within the interactive models lead to markedly different results for cases where there are fewer observations to constrain/calibrate model predictions, e.g. early historical major eruptions.

It is certainly relevant for ACP to explore what the models predict for SAI geoengineering, and whilst I have considered whether this exploratory simulation could potentially be caveated sufficiently to be publishable in ACP, I just don’t see how that can be the case for these simulations, not for ACP.

The results from the counter climate intervention scenario must be extremely dependent on the SAI-enhanced state predicted there, and specifically for this case of the main effect being a scavenging or scrubbing of the existing aerosol predicted by the model.

That is not to suggest this particular model is any more likely or less likely to yield a realistic SAI enhancement. It’s just to observe that further work needs to be done to understand differences between the base SAI case, and the natural analogue large volcanic cases, before this type of secondary model experiments around counter climate intervention can be presented, at least for this specialist ACP journal.

In summary, whilst I appreciate this study can still be valuable at this exploratory level, my review finds this too exploratory to be publishable within a specialist journal such as ACP. The study should be re-submitted to either a model development journal such as GMD, or a broader-based journal such as Atmospheric Science Letters or Earth’s Future.

Interactive simulations are important, but for SAI these should focus on the main SAI enhanced case, whilst still the response can be (to some extent) testable comparing to atmospheric observations of a similar response. The study here is essentially assessing the combination of two unconstrained aspects at once, and then the predictions can remain only exploratory secondary experiments.

The study of Weisenstein et al. (2022) has shown that the interactive models differ a lot within their predictions of the main SAI forcing effect, for example Figures 6, 7 and 9 in the SAI intercomparison study indicate the two ECHAM-based models predict around a factor of 2 lower SAI forcing than seen in the CESM simulations

I have listed below a set of specific revisions on the framing of the study that would be needed before re-submission, and I recommend the authors consider a different journal such as GMD or Climate Futures, rather than Atmospheric Chemistry and Physics.

As I say, the results and interpretation presented is of good quality, but the scenarios explored are not sufficiently constrained to yield meaningful results for a specialist journal such as ACP.     In fact, it occurred to me rather the interaction between the dust and sulphate is more towards assessing the sensitivity of a particular aspect of the model, and then this study could fit well to a model development journal such as Geoscientific Model Development or JAMES. Or alternatively to broader-scope journal such as Earth’s Future or Atmospheric Science Letters.

Specific revisions, to improve the framing of the study



1.  Introduction, line 31 – This is a key sentence within the framing of the manuscript, introducing for the first time the stated concept of “Counter Climate Intervention” (CCI).



And yet the stated basis “CCI could be attractive to a rival actor who opposes SCI” is not credible.   I mean actually deploying a large-scale injection of calcite would be too prohibitively expensive to have the scenario be something a “rival actor” could then begin, to conteract the SRM forcing.

Within this same sentence there is then a 2^nd stated rationale, that the same actor could have in mind a “contingency measure” in relation to some unexpected outcome from an initial deployment.  That’s potentially more plausible, compared to the 1^st rationale, for example if an unexpected hemispheric imbalance or large magnitude of a polar ozone effect or other stratospheric response occurred. 



And then when re-framing the article for re-submission to GMD or Climate Futures, suggest to re-factor this sentence to omit the “attractive to a rival actor who opposes SCI”.  It’s not really a valid or plausible possibility, in my opinion.     

2. Introduction, line 33 -- The sentence after that in point 1) states that “CCI research to date has focused on the ethics and political will for CCI…”., but does not provide any citation in the sentence.



There is only the citation to Parker et al. (2018) in the follow-on sentence, but the text there indicates more than 1 study on Counter Climate Intervention.  If that is the case these other studies need to be cited here.

3. Introduction, line 37 – The wording here “could be effectively offset by this approach” over-states the findings in the Fuglestedt et al. (2014) paper, and hasn’t sufficiently explained what “this approach” means here. And which criteria determine to be able to say “effectively offset”, or otherwise. Global-mean or regionally balanced?

4. Introduction, line 38 – similarly this study re: fluorinated gases seems add-on, and potentially not relevant or at best under-developed in this version.

5. Introduction line 40 – “with the goal of making SCI technology inert”. What is meant by “inert” here?

This is poor writing here, and somewhat underlines the concept of a “Counter Climate Intervention” just seems hard to reconcile its name with a realistic purpose or achievable goal.

6. Introduction line 41 – “PA18 suggests adding a substance that promotes condensation or coagulation to force the aerosol to grow and sediment faster”. This is too simplified a narrative, and the specifics here need to be clearer. What substance – at emission?  In addition to sulphur or in place of the sulphur?  In what mechanism would this be effective? Need to be as large as the sulphur emission itself?  Not clear at all how this could even be feasible on paper.

7. Introduction line 42 – “This has parallels to flue-gas scrubbing, i.e. generation of particles that are subsequently removed”.

Not really. It’s a completely different effect, the scrubbing is uptake onto the calcite particles, and occurs very quickly, within the plume itself.



The growth processes happen over much longer timescales, for example the peak in aerosol particle size after Pinatubo occurred much later than the peak in optical depth, around a year after the eruption. So the timescales and associated spatial extent of the changes caused by the two mechanisms are completely different.     The sentence should be re-framed to point out the differences in timescales and the corresponding consequences in terms of strategies within model experiments to assess these effects.

References

Clyne et al. (2021)

“Model physics and chemistry causing inter-model disagreement within the VolMIP-Tambora Interactive Stratospheric Aerosol ensemble", Atmos. Chem. Phys., 21, 3317–3343, https://doi.org/10.5194/acp-21-3317-2021 .

Quaglia et al. (2023)

“Interactive stratospheric aerosol models’ response to different amounts and altitudes of SO2 injection during the 1991 Pinatubo eruption”, Atmos. Chem. Phys., 23, 921–948, https://doi.org/10.5194/acp-23-921-2023 .

Weisenstein et al. (2022)

“An interactive stratospheric aerosol model intercomparison of solar geoengineering by stratospheric injection of SO2 or accumulation-mode sulfuric acid aerosols”, Atmos. Chem. Phys., 22, 2955–2973, https://doi.org/10.5194/acp-22-2955-2022 .