This paper has multiple issues.  I recommend major revisions.

The paper is not well-written and there are multiple grammatical and spelling errors, including the wrong tense.  It would have been more considerate for the reviewers if you had used AI to fix these or if all the co-authors had proofread the paper.  There are multiple acronyms that are not defined, and there are acronyms that are define and never used again.  I have made more corrections in this paper than ever before in a paper I have reviewed.  That work should be done by the authors or the Editor and not the reviewers.  I gave up on p. 12 with detailed corrections, as it was too much work.

This paper is too long and it has a simple message:  specified emissions from SSP2-4.5 and ARISE latitudinally-dependent emissions control particle and ozone impacts on human health.  This message could have been conveyed with a much shorter paper and fewer details.  The title says that the impacts are caused by climate changes, but rather should make clear that the climate changes are changed by climate forcing.

This paper claims that it is better than previous work because it includes a more comprehensive treatment of the climate system.  But it needs to make clear right at the beginning what it does not include.  There is no treatment of UV changes (now possible with TUV incorporated in WACCM) and tropospheric chemistry does not include changes in photolysis.  So all the conclusions have to be tempered by these omissions, and this has to be made clear in the abstract.

The abstract focuses on SAI impacts, but that is not correct.  This specific SAI scenario, with more forcing in the SH, produces direct effects there.  So the results here are not general results for SAI, and that also needs to be made clear in the title and the abstract.

It is certainly not correct to present results in the abstract to three significant figures with no error bars, particularly since there were 10-member ensembles used here.

Equation 2 has multiple variables that are not explained.  What do each of them mean?  What are the units.  And what is the science behind this equation?  Furthermore, where does the equation come from?  What is the reference?

How can OSMDA8 (the highest daily 8-hour average ozone concentration during the ozone season) be important for mortality?  Shouldn’t the impact of ozone on mortality be the amount of ozone times the exposure?  What if there are many days in a season with a little less ozone, and hence a lower OSMDA8 and in a different season only one day with a high OSMDA8 value and all the other days very low?  Wouldn’t the first case be worse for health?  Please explain why the metric you are using makes sense.  

Also, how much would ozone exposure affect mortality as a function of time over a person’s lifetime?  Does it matter at what age they are exposed? 

Lines 148-150.  You can’t just choose to ignore uncertainty that you know about.  This will give you the wrong answers.  This just reinforces that the numbers in the abstract to 3 significant figures and no error bars can’t possibly be correct.

Fig. 3 has multiple issues:  

- You have to use the same scales for all the panels in each row, like you did for Fig. 1, so that they can be compared.  Otherwise the same color means different things in each panel.

- Needs stippling like in Fig. 1 to indicate which results are significant.

- Is it height above sea level?  How can you have values under the ice in Antarctica?

- Mark the latitude in more increments, and use natural ones, every 15 or 30 degrees.

- The font in the figures is too small to see.

- You plot water concentration, but is it water vapor or total water, including liquid and solid?  If water vapor, you have to use normal meteorological units of mixing ratio or absolute humidity.  And you show large changes in the Tropics, but the ITCZ has a large seasonal cycle and spatial variations.  Showing zonal-mean annual-mean values obscures much of the signal.

The shading in Figs. 2-3 is hard to make out, as only two colors are used, and the boundaries between the different values are not clear.  Use distinct different colors.

Figure A4:  Text is much too tiny to read.  Make the panels much bigger and use fewer per row.  Since the color bar is the same for all the panels, get rid of the small ones and just use one large one.  And what are the ////?

It looks like Fig. A4 was done with GrADS, and it looks much better than the others, with better labeling of the axes and distinct colors for the shading.  But why is there no white box behind each number in the contour labels, so they can be more easily read?

Figure 4:  It is really hard to compare the two columns, as they need to be plotted with the same color scale.  But it looks like the values in the left column for some countries like India and larger than the standard deviation.  So why are they indicated as being significantly different from zero?

The paper uses “notably” randomly.  These should all be deleted.  Every sentence should be noted or it should not be in the paper.

The paper references Fig. 7 before Figs. 5 and 6.  This is confusing.  Figures have to appear in numerical order in a paper.

There are 95 additional comments in the attached annotated manuscript.

Review by Alan Robock 

The authors quantify, using the Earth system model CESM2-WACCM, the potential effects that stratospheric aerosol injection (SAI) might have on surface air quality. They specifically assess a scenario in which an SSP2-4.5 trajectory is simulated with and without SAI sufficient to limit surface temperature increase to no more than 1.5 K. Consistent with prior research they find that surface air quality changes specifically due to SAI are small in magnitude, and dwarfed by interannual variability.

The central question of the paper is interesting and important. The use of an ESM is encouraging, although I have concerns about the specific ESM chosen due to the lack of interactive tropospheric photolysis as well as the simplified representation of some key processes relevant to fine particulate matter. These caveats are substantial, and should have been directly evaluated as well as more openly discussed in both the abstract and the main text. Nonetheless, the manuscript potentially offers a useful incremental advance in our understanding of the broader effects of SAI. With major revisions, I believe that this work could warrant publication. I have elaborated on these concerns below.

Major comments

The two most significant concerns are related, and boil down to the question of whether the model being used is appropriate for the task at hand. On the one hand, the authors make a good case that the fully interactive nature of the CESM2-WACCM6 simulation means that it can capture key meteorological responses to SAI which are likely to be significant to the air quality response. Since these responses were often either neglected entirely or crudely parameterized in previous studies, directly simulating the interactions of changing meteorology with air quality is a valuable advance. However, the first question is whether the chosen model is appropriate for simulations of air quality. I am aware of almost no studies which have used WACCM for air quality modelling, beyond one study which is cited by the authors and which was itself an intercomparison of CMIP6 models. There seem to be several modelling choices in WACCM which, while sensible for a model of whole-atmosphere climate responses, might compromise its representation of air quality responses. For example Hancock et al. (2023) indicate that WACCM does not include any representation of ammonium or nitrate aerosols, but these are standard in models such as CMAQ which are dedicated to air quality – and such aerosols can be dominant in understanding air quality responses to climate change (see e.g. Nolte et al. (2018)). Indeed it appears that a recent paper in ACP which used WACCM for the boundary conditions in an air quality simulation specifically chose to use WRF for the regional analysis, in part because it includes air quality-relevant aerosol chemistry lacking in WACCM (Clayton et al., 2024). I would strongly recommend that the authors perform a detailed evaluation of a) WACCM’s ability to represent baseline air quality in the present day, b) WACCM’s ability to reproduce already-understood effects of climate change on air quality, and c) the likely gaps in WACCM’s representation of processes and species which are important to air quality, beyond the question of tropospheric photolysis below.

The second concern is related. Specifically, the fact that WACCM uses fixed tropospheric photolysis rates is a significant shortcoming in a study which seeks to understand the atmospheric composition implications of stratospheric aerosol injection. This is a difficult issue to rectify, and I am glad to see that the authors have at least acknowledged this challenge. However, previous studies (e.g. Xia et al., 2017) did include this response and discussed at length the potential for tropospheric UV changes to be significant in understanding the tropospheric ozone response – and thus the air quality response. The authors themselves argue that tropospheric photochemistry is the dominant factor in NH surface ozone change (line 219).  Ideally, an analysis such as that by Clayton et al. (2024) in which WACCM outputs are used as boundary conditions to a more air quality-focused model may be a way to resolve these issues, and I would recommend that the authors seriously consider if there is a way that they could perform a more comprehensive simulation of tropospheric chemistry using their existing data - recognizing that this would require a great deal of additional work but would also resolve what I perceive as being a major gap in the work.

Notwithstanding such an expansion, these are sufficiently significant deficiencies that I believe they need to be much more strongly highlighted. I would recommend that the abstract explicitly state that changes in tropospheric photolysis are not considered, and that statements that this is the first study to use “comprehensive” stratospheric and tropospheric chemistry (e.g. line 29 and 58) be removed. While I absolutely believe that this study can provide a valuable contribution to our understanding of the impacts of SAI on the environment, I would argue that it needs to be placed in the correct context (and thus allow subsequent studies to fill the remaining knowledge gaps).

Independent of these concerns, I was struck by one of the conclusions drawn (and which is highlighted in the abstract). The authors argue that internal variability is key, on the basis that they find significant differences across ensemble members.  This aligns climate intervention effects on air quality with the well established effects of climate change on air quality (e.g. Fiore et al., 2015) where noise in the meteorological response can be greater than the change in exposure to pollutants resulting from SAI. It would have been useful to discuss how the projected effects of SAI on air quality compare to the air quality "penalty" projected for climate change, given that there is a robust literature discussing not only this question but also specifically the problem of how to deal with internal variability in such projections. The lack of such a discussion is a notable absence, and leaves the paper somewhat unmoored.

The use of large ensembles is a good (if expensive) solution to this problem, but analysis of air quality interventions may also rely on representative meteorological years if it can be shown that the outcome would be the same as when using a large ensemble average (see e.g. Stewart et al. (2017) and Abel et al. (2018) for examples looking at air quality change in future conditions). Here it seems that internal variability is used to draw some conclusions which seem hard to justify; for example, on lines 291-293 it is claimed that "health impacts under SAI are not governed mainly by the magnitude of SO2 injected". Certainly it is true that SAI alone is not going to become the dominant cause of air pollution under almost any scenario, and the comparison of ARISE-SAI-1.0 and 1.5 shows how important these other factors are - an important contribution. However the paper simultaneously argues that there is a robust surface ozone response relative to a scenario where the amount of SO2 injected is zero (SSP2-4.5), so presumably the magnitude of the injection is not entirely irrelevant. Is there evidence that a robust (if complex) difference in the effects of larger injection quantities would not emerge if using a larger ensemble, longer averaging period, and/or if other factors (eg surface-level emissions of air quality precursors) were held constant? I would suggest that the authors explore in more detail the degree to which their results might be improved by such approaches, not least because the data to do so appears to already exist (e.g. it should be straightforward to evaluate the degree to which a smaller ensemble would or would not have allowed the same conclusions to be drawn - which would be valuable information for those interested in performing future studies of atmospheric composition change under SAI).

Minor comments

Some aspects of the air quality response which I had expected might be significant were seemingly not discussed. I would recommend discussing whether elements of the air quality response to SAI which have been significant for studies of the climate penalty – for example, changes in planetary boundary layer height, and the (highly model-dependent) lightning response – are playing a significant role in the calculated response. These factors are well described in the literature already cited and would be expected to be represented in an ESM (ostensibly one of the key novelties of this work), so providing a careful evaluation of how these factors translate to an SAI study would be valuable.

While I understand why the authors have chosen not to estimate the health impacts of UV changes associated with SAI, I was surprised that no formal analysis was done at all of surface UV changes. The statement on line 372 – that a preliminary analysis indicated “very modest changes” – is unfortunately not much help, as the authors do not provide any metric of what they consider to be “modest” (or why). Quantifying (say) relative changes in projected population exposure to UV would help us to understand whether such changes need further study. Quantitative analysis of UV changes may also be useful in understanding the degree to which neglecting changes in tropospheric photolysis change may or may not be a minor oversight.

Hancock et al. (2023) indicated that WACCM-based estimates of exposure to PM2.5 may overestimate the role of dust, due to inclusion of too-large particles in the PM2.5 metric. Given that dust is the predominant factor in exposure under ARISE-SAI-1.5 for a significant fraction of the world (Figure 2), it would be useful to have more information on how the PM2.5 calculation was performed and whether the issue identified by Hancock et al. was addressed.

There are numerous grammatical errors (e.g. lines 221-222: “many of this conditions”, “we deem important”; line 228: “These estimates and Fig. 4 show that the standard deviation of mortality estimates highlights the large spread in project PM2.5-related deaths”; Eq. 2 says the PM2.5 threshold is 2.4 (no units given), but Table 1 says 2.5 ppm - and Burnett et al (2018) say 2.4 ug/m3). I would recommend the authors take some time to go through the paper in depth and fix such errors before resubmitting.

Citations

Abel DW, Holloway T, Harkey M, Meier P, Ahl D, Limaye VS, Patz JA. Air-quality-related health impacts from climate change and from adaptation of cooling demand for buildings in the eastern United States: An interdisciplinary modeling study. PLoS Med. 2018

Clayton, Connor J., et al. The co-benefits of a low-carbon future for PM2.5 and O3 air pollution in Europe. Atmospheric Chemistry and Physics. 2024

Fiore AM, Naik V, Leibensperger EM. Air Quality and Climate Connections. Journal of the Air & Waste Management Association. 2015

Nolte, Christopher G., et al. The potential effects of climate change on air quality across the conterminous US at 2030 under three Representative Concentration Pathways. Atmospheric Chemistry and Physics. 2018

Stewart DR, Saunders E, Perea RA, Fitzgerald R, Campbell DE, Stockwell WR. Linking Air Quality and Human Health Effects Models: An Application to the Los Angeles Air Basin. Environ Health Insights. 2017

This paper examines PM2.5 and ozone-related mortality under stratospheric aerosol injection (SAI) using CESM2-WACCM6 simulations. The question is important, but in its current form the manuscript has substantial shortcomings in scope, methodology, and presentation. I recommend major revisions.

The main issues are: (i) the model choice and configuration are not adequate for robust air quality assessment (e.g., the lack of interactive tropospheric photolysis); (ii) the analysis is narrow, excluding key factors affecting public health (e.g., UV-B, temperature extremes); (iii) the results are presented with a precision that vastly overstates certainty; (iv) the manuscript is poorly structured, far too long for the information it tries to convey, with repetitive text, far too many typos and grammatical errors, and figures that are not consistently referenced or interpretable.

At present, the paper claims novelty while underplaying its limitations. The central message (stratospheric aerosol injection has only modest additional impacts on air quality, relative to policy-driven improvements) can and should be conveyed in a more concise manuscript.

Major comments:

A key issue with this paper is the use of CESM2-WACCM6 for the evaluation of health impacts of stratospheric aerosol injection (SAI). Previous studies have relied on models with shortcomings noted in the introduction, but unfortunately the shortcomings of the model used here are downplayed. Main issues are with the fixed photolysis rates and lack of ammonium and nitrate aerosols, essential to air quality assessment. Without these terms, the author’s conclusions are, at best, incomplete.

These are not minor caveats, but fundamentally constrain the reliability of this study, something the authors should be upfront about. Claims of “comprehensive chemistry” should therefore also be removed.

The use and interpretation of the 10-member ensembles in this manuscript raises several problems. The paper stresses variability across ensemble members yet lacks a systemic metric for uncertainty analysis. Without this, the role of ensembles remains descriptive, rather than analytical.

Simultaneously, there is the issue of overprecision. Results are given such as “-149,397 to -177,296” (line 227) which is indefensible when variability and uncertainty are ignored, as the authors admit to in lines 148-150. Results should be rounded and expressed as mean +- standard deviation or 90% confidence interval. Not as exact integers or with unrealistic significance. Unfortunately, variability is highlighted when it dilutes signal but downplayed when the results look robust. Such inconsistency weakens the conclusions.

Furthermore, the statement that “mortality impacts do not scale with SO2 injection” is unsupported. Only two scenarios are compared, over a relatively short time period. A more nuanced treatment would recognize that non-linearity is plausible but cannot be demonstrated here.

The scope of this work is narrow. While the paper claims that “this study focused on the air quality-related health impacts of SAI”, only ozone and PM2.5 are considered. The abstract (and title) should reflect the scope Unfortunately, the paper glosses over the significant regional increases in mortality (Figure 9), these results deserve more emphasis, as focusing on global aggregates risks misinterpretation of the overall findings.

The discussion largely restates results rather than interpreting them. The reader is left with little beyond “impacts are modest”.

Minor comments:

Figures are dense, inconsistently referenced, and hard to interpret. At worst they are misleading (e.g., different scales across panels in Figure 3). Figure 5(b) is never referred to in the text. Remove this from the paper or discuss the meaning in the main body.

Technical:

Check the citations. E.g., line 123: WHO cited as “(Organization et al., 2021).

Stylistic and typographical:

Line 16: I strongly recommend against using uncommon words like “ameliorate”.

Line 47&48: awkward use of “they” to refer to Harding et al., I suggest referring to the studies instead of the authors when critiquing methods used.

Line 54: “the the”

Line 158: “these three-way comparison”.

Line 184: this is phrased rather unprofessionally: I suggest replacing “, as in” with: “i.e.,”.

And many more.

In its current form, the manuscript overstates its novelty while underplaying its limitations. I therefore recommend major revisions, with a particular focus on the appropriateness of the model used, the ensemble interpretation, and the presentation of the results.