General comments:

This study uses CESM1-WACCM4 for an idealized experiment with six-months volcanic aerosol injection in the Northern Hemisphere high latitude stratosphere. The authors emphasizes that potential increased sudden stratosphere warming events are found in response to the eruption. If the results are solid, then it can add valuable new insight to the research field. However, current experiment design, results and discussions in the paper are not convincing enough to make solid conclusions as stated in the paper.

Below are some major questions that need to be clarified/addressed:

• The study uses CESM1-WACCM4 with specified chemistry, which is already an old version of the model, how this old version is suitable for this study is not convincingly stated in the manuscript.
• The experiment design, why the injection mass maintains over 6 months without any change and over wide vertical range (10-27 km), is it possible for a volcanic eruption? This looks more like a stratospheric aerosol modification case instead of a volcanic eruption case.
• How is the aerosol distribution? What changes do aerosol zonal mean have along the time? How are the shortwave and longwave radiation and stratospheric temperature changes related to the aerosol distributions? These are all unclear questions, which make it hard to understand the mechanism explanation in the following parts.
• The manuscript emphasizes two competing mechanisms for explaining the results, one is the local stratospheric aerosol induced warming mechanism, the other one is the local surface cooling induced wave activity change mechanism, however, no results or supplement figures prove if the warming is at the same location as the aerosol loading area, or the increased wave propagation originates from the cooling areas.

Besides, why there is a cooling in the first winter in both the cpl and atm-only runs are not well explained. In the winter, there is no shortwave radiation, then the aerosol induced stratospheric warming due to longwave radiation absorption should be a dominating effect compared to the first summer, but why it’s the opposite? Connection to strengthened polar vortex in the winter needs to be explained better.

Moreover, the aerosol induced stratospheric warming should be weakened in the second and third winter due to decreased aerosol, thus the strengthened polar vortex in the first winter can also be weakened due to less aerosol in the second and third winter, how can you rule this out from your second mechanism?

• There are 27 sudden stratospheric warming events counted in the third winter, but there are only 20 ensemble members, so there is more than one SSW event in one member. What is the definition of the SSW event used here? Is it only based on the U50? Is it reasonable to count like this? More clarifications are needed. A figure showing the wind changes and marked SSW events in each member would make it clearer.
• Discussions needs to be largely improved. Comparison with other related studies and limitations of this study are limited.
• The structure and English writing of the manuscript can be improved. The discussion and summary can be separated with improved discussions and clear conclusions in the summary.

Specific comments

L37-46: Too long for an introduction on this well-known statement.

L51: “the aerosols tend to stay longer in the polar stratosphere (Graf et al., 1994, 2007)” Correct? This study (“Initial atmospheric conditions control transport of volcanic volatiles, forcing and impacts” https://acp.copernicus.org/articles/24/6233/2024/) shows longer lifetime of volcanic aerosol in the NHET after tropical eruptions compared to extratropical eruptions.

L57-61: Are Tropical or NH extratropical eruptions described here? Any difference will it have after tropical and NH extratropical eruptions?

L111-112: “that is comparable to the interactive chemistry model version”

Not convincing with this simple statement.

What is the aerosol module used in this model? How is the model’s ability on simulating volcanic aerosol evolutions and NH high latitude dynamics like polar vortex, SSW etc.? These are important aspects that needs to be evaluated for this study.

L126-127: Better moving this sentence to the previous paragraph where describing the coupled ocean and related runs.

L132: EVA is not height dependent in Toohey 2016.

L137-138: a midlatitude location at which latitude?

Figure 1 and L136-142: Not clear how this scaled is performed based on extinction and aerosol mass from the figure and the text description. What is the original EVA forcing?

Figure 1 and L147-148: The months in Figure 1 and decline on Oct 1 is confusing, if the decreasing starts on Oct. 1 as written in the text, then Nov., Dec., Jan next year is used for the first winter calculation?

L154: It can be quite different for a 45° N injection compared to a 65° N injection, how this assumption affect your results needs to be discussed.

L162-167 Better to start description of cpl and then atm-only to keep it consistent across the whole paper.

Figure 2 and L194-206: Better to adjust the order of fig 2(a) and 2(b) and related descriptions, same consistency reason. The time axes Jan, May, Sep. is confusing, better to use Jan. Jul. instead? Any significance test results?

L196-199: Needs to be rephrased. The seasonal variation of the solar radiation is not the reason of different anomalies in the first and second winter.

Figure 2c: why is there a break in the tropics (around 0 degree) in the aerosol mass distribution?

L210-211: “at 65°N” is confusing.

L212-213: Better to convert unit to avoid this exponential value expression.

L218-223: Unclear explanation. More analysis are needed to differentiate the shortwave and longwave radiation effect and the direct radiation effect and dynamical effect to understand the different stratospheric temperature responses in the summer and winter.

Figure 3 and L233-234: Is this the 2 STD of experiment or control ensemble runs? How different are they compared to the control runs? Figure 3a and 3b show different length, better to use Jan and July?

L237-240: “high latitude into midlatitudes” and “subtropics into midlatitudes”, one is equatorward, oppositely, the other one is poleward, confusing.

Figure 4: better to make it larger, it’s not easy to see the details.

L246-248: where shows the local heating? Figure 3a and 4a only shows the temperature difference to the control run, but what is the temperature gradients of experiment and control runs?

L255-259: “locate sources of wave activity”? But the cooling and the upward wave activity locates at different areas, then how can this explain the bottom-up mechanism? 

L275-277: what is the direct thermal forcing?

L277-279: Do you mean the inconsistent results are due to the U50 definition, then why use this index? what if other indices are used, can they show consistent results?

L280-282: North Pacific … North Atlantic and Siberia, they are all ocean, how to understand the reasoning “pointing to a possible influence of the change in land-sea thermal contrast”?

Figure 5: as written in the general comments, clarification on the definition/counting/presenting of SSW events are needed.

L329-330: why is it a stratospheric cooling? If thermal response to aerosol injection, then it’s stratospheric warming.

Section 3.3: Does it contribute a lot to the main purpose of the paper by just describing the detailed spatial patterns. What connections do they have with previous results? How aerosol distribution lead to the temperature responses? How do they relate to the different cpl and atm-only configurations? Addressing these questions are helpful to improve the quality of the study.

Summarizing discussions: The first three paragraphs just repeat most of descriptions in the results section. Discussions are needed to compare with other related studies. Like how’s SSW response to volcanic eruption in the observations and studies using other models? What different reasons do they have if showing different results? How the specified chemistry model configuration affects the result? What kind of impact will it have on the results if including aerosol microphysics and stratospheric chemistry in the model? This study (“Volcanic forcing of high-latitude Northern Hemisphere eruptions” https://www.nature.com/articles/s41612-023-00539-4#:~:text=High%2Dlatitude%20explosive%20volcanic%20eruptions,Pinatubo%20eruption. ) shows initial polar vortex stability affects the aerosol distribution, but the forcing is produced with EVA, how will these affect the results. These needs to be discussed.

L416-422: How this relates to equatorial eruptions? “WACCM4 is insensitive to the injection latitude”, is the volcanic forcing produced by EVA? How can this conclusion be made here?

L427: what is “dynamic surface response”?

L430-432: Is this too arbitrary? No model-observation comparisons were made, and the aerosol forcing is much stronger than any volcanic forcing used in previous CMIP5/CMIP6 simulations.

L434-435: Don’t understand this conclusion. Figure 3 shows stronger stratospheric warming in cpl than atm-only in the second and third winter.

L439: what is “an intrinsic reason originating in the model”?

Technical corrections

L43-44: surface and stratospheric meridional temperature gradients?

L62: effect -> affect; as the positive phase of … -> Leading to a positive phase of…?

L81: Icelandic volcanism?

L90-91: history and current activity makes these types of eruption?

L96: the response within of NH stratospheric polar vortex?

L194: short-wave -> shortwave

L199: substantially

L272: N America -> North America

L462: smaller size -> smaller magnitude?

This study assesses how high-latitude eruptions affect stratospheric circulation and more specifically the occurrence of sudden stratospheric warming (SSW) events. There are few studies on the influence of high-latitude eruptions on stratospheric circulation, which makes this a welcome contribution to the field. However, there are issues with the methodology that make me skeptical of the conclusion of an extremely significant impact in the third post-eruption year. I’m requesting this be better explained, kept from being the only focus of the title, and that a small amount of additional simulation output be presented to give a clearer sense of this conclusion’s veracity. There are also issues with the structure of the paper and a number of instances where the results are insufficiently explained, which I would like to see the authors rectify, and so I am requesting major revisions. There are a number of positive aspects of this study, particularly the combined use of atmosphere-only and coupled simulations and the in depth presentation of wave activity anomalies, so I hope the authors will modify this manuscript to realize the potential of these inclusions. 

Major comments

1) I’m skeptical of the author’s claim of a very substantial increase in SSWs specifically in the *third* post-eruption winter. The authors do present this result as “surprising” but since readers will assume what they will I want to be careful this isn’t a methodological artifact. I hence request the authors give a clear explanation of why the effect is substantial only in the 3rd year and show a time series of the stratospheric wind from which it can be seen how distributed the SSWs are among ensemble members (in order to see how susceptible this result is to noise). There are a few issues here so I’d like to see more material:

    a) It is hard to believe this would be so strong *after* most aerosols have left the stratosphere, so this should be thoroughly explained, along with potential caveats.

    b) The large difference in SSW number across seasons in the control experiments suggests the 20 ensemble members used are not enough to make firm conclusions on post-eruption SSWs, which is potentially a major issue here.

    c) As explained more below, the volcanic influence may be substantially weaker in the third year than the prescribed forcing used here represents.

   d) The number of SSWs in year 3 cpl are *more* than 1-per-year on average, which seems strange. Could the authors please add a time series of the stratospheric wind in each ensemble member either to the manuscript or supplement, showing where these transitions occur? I want to at least know this isn’t heavily affected by a handful of simulations that cross the SSW threshold several times, which would mean potentially far more than 20 simulations are needed. Likewise, perhaps another statistic (e.g. “percent of ensemble members containing at least one SSW” in each winter) would be less susceptible to noise, so I would encourage the authors to attempt this if it helps establish the claim.

2) I feel the structure of the paper is currently inhibiting its potential, and that this would be a much nicer paper to read if the structure were changed. Currently the Results section is very dry, simply stating what is in the figure, year-by-year from one experiment to the other. Nearly all explanations of the results are instead in the Summarizing Discussions section. I strongly recommend merging much of the explanations into the Results, so that the reader immediately knows why the Results are important. The discussion section could then become less technical and more focused on the big picture concepts of high-latitude eruptions, resulting climate damages, predictability, etc, for which the results have relevance. And about the Results again, I quite like the combined use of atmosphere-only and coupled simulations but find the structure of the Results limits their effective use. I feel this would be better if instead of the atmosphere-only experiment having its own Results section after most results have been described, the atm-only and cpl experiments were described together, perhaps with one section on the surface cooling pathway and another on the stratospheric warming pathway. Currently there is no clear sense in Results how the atm-only experiments relate to the cpl (more realistic) case.

3) The prescribed aerosol forcing doesn’t account for high-latitude eruptions leading to aerosols in the stratosphere for less time than tropical eruptions, due to entering the stratosphere far closer to descending stratospheric circulation. This is not necessarily huge but could nullify much of the 3rd winter effect by positioning this stage at the 2nd winter. Fig. 2g of Toohey et al (2019) shows with interactive aerosol modeling that eruptions at 56N have a 12% to 44% lower e-folding lifetime than similar eruptions in the tropics, depending on eruption season. I don’t believe this lifetime difference is covered in EVA, and is stated to not have been factored into the conversion from 45N EVA data to a 65N eruption. I request the authors check how their volcanic forcing compares to high-latitude eruptions with interactive aerosol studies and at least explain this as a caveat.

Toohey, M., Krüger, K., Schmidt, H., Timmreck, C., Sigl, M., Stoffel, M., & Wilson, R. (2019). Disproportionately strong climate forcing from extratropical explosive volcanic eruptions. Nature Geoscience, 12(2), 100-107.

4) Post-eruption Eliassen-Palm and Plumb flux anomalies are shown and described, and I think their inclusion is one of the main things that makes this study original for a high-latitude eruption case. However, these are barely put into the context of a) the volcanic forcing that causes the anomalies or 2) the net impacts of wave-eddy interactions on stratospheric circulation. I feel these results need to be physically explained within the Results and put into a context someone in the volcano-climate community without a geophysical fluid dynamics background can appreciate. Perhaps the authors can deduce how the studied volcanic circulation impacts are modulated by eddies/waves from the already cited Bittner et al (2016) as well as DallaSanta et al (2019), then considering how those results might vary for a high-latitude case. The Bittner study includes EP fluxes that look especially appropriate for a comparison to the present study’s results.

DallaSanta, K., Gerber, E. P., & Toohey, M. (2019). The circulation response to volcanic eruptions: The key roles of stratospheric warming and eddy interactions. Journal of Climate, 32(4), 1101-1120.

5) I do not find the title suitable for this study, so hope the authors will alter it. There are three things about the current title I find problematic:

     a) Only a minority of the paper is really about SSWs and this is the most uncertain part of the results. I feel the paper doesn’t concretely enough settle the SSW question to warrant this as a title. But the study would be more defensible if it generalized this part of the title to impacts on “stratospheric circulation and sudden stratospheric warmings” or just “stratospheric circulation”, or similar, maybe a Part 1 style title given the mention of an upcoming study also on high-latitude eruptions and circulation.

    b) I would take out “long-lasting”, as it’s just confusing in that it sounds like this is a constant-aerosol-presence geoengineering experiment. I don’t believe distributing the explosive eruptions over 6 months is a major factor for the results, compared to a one-off eruption of the same mass, and there isn’t a one-off experiment here to compare with anyhow. I would omit this and let readers simply read the methods for an explanation that this is designed to closely resemble eruptions like Laki.

   c) I also feel “an idealized modeling study” is confusing. I get that this is not an actual eruption case, but this level of being idealized is not particularly high. This subtitle makes it sound like the study uses an energy balance or intermediate-complexity model, rather than a full GCM. I would omit or reword, as the idealized nature is explained in the abstract anyhow.

Specific comments:

Line 29: For multiple reasons it seems doubtful the studied impacts are an “important source of interannual variability and a possible source of increased seasonal predictability of northern hemisphere regional climates”: 1) eruptions of this type and magnitude only occur 2-3 times per millennium, 2) adding similar magnitude eruptions to forecast systems has small influence on prediction skill (Aquila et al, 2021), and 3) as this study mentions, simulated volcanic impacts tend to be overestimates, and still the results aren’t incredibly confident. I expect there are more realistic reasons to study this, e.g. to understand impacts on people and ecosystems on the rare occasions when these events do happen (both historical, e.g. after Laki, and future).

Aquila, V., Baldwin, C., Mukherjee, N., Hackert, E., Li, F., Marshak, J., ... & Pawson, S. (2021). Impacts of the eruption of Mount Pinatubo on surface temperatures and precipitation forecasts with the NASA GEOS subseasonal‐to‐seasonal system. Journal of Geophysical Research: Atmospheres, 126(16), e2021JD034830.

Lines 51-2: The line “aerosols tend to stay longer in the polar stratosphere” appears incompatible with the aerosols entering the stratosphere far closer to the downwelling polar circulation, and the shorter lifetime found in studies using models with interactive aerosol microphysics and chemistry (e.g. Toohey et al., 2019 cited above). Please rectify or explain this.

Line 52: I’m not convinced the tropopause being lower near the poles would enhance the dynamical effects of aerosols there compared to lower-latitude eruptions, since the circulation structure tends to follow relative heights in the troposphere rather than actual geometric heights. Could the authors at least please explain this in their answer to the review?

Lines 54-5: “not analogs” is a bit extreme, as certainly tropical and high-latitude eruptions are related. How about “not close analogs”?

Line 64: Somewhere in the intro the manuscript should make clear what’s original in this study. The focus on high-latitude eruption impacts on SSWs seems to be new to the best of my knowledge, and same for the focus on eddies (EP-flux analysis) after a high-latitude eruption. Studies on related SSW impacts should be cited, for instance the impact of reduced sunlight studied by Muthers et al., 2016 is relevant here. Also, for high-latitude eruptions and stratospheric circulation (but not SSWs), The ‘Part 1’ Zambri et al (2019) and Oman et al (2005) are relevant. I’m also a bit surprised the results of Sjolte et al (2019) aren’t discussed more specifically, as would seem appropriate.

Muthers, S., Raible, C. C., Rozanov, E., & Stocker, T. F. (2016). Response of the AMOC to reduced solar radiation–the modulating role of atmospheric chemistry. Earth System Dynamics, 7(4), 877-892.

Oman, L., Robock, A., Stenchikov, G., Schmidt, G. A., & Ruedy, R. (2005). Climatic response to high‐latitude volcanic eruptions. Journal of Geophysical Research: Atmospheres, 110(D13).

Zambri, B., Robock, A., Mills, M. J., & Schmidt, A. (2019). Modeling the 1783–1784 Laki eruption in Iceland: 1. Aerosol evolution and global stratospheric circulation impacts. Journal of Geophysical Research: Atmospheres, 124(13), 6750-6769.

Lines 75-8: Could the authors please explain the bottom-up method as clearly in the text as they do the top-down method? Is this also a thermal wind, but in the opposite direction due to lower tropospheric cooling, compared to stratospheric warming? These “bottom-up” and “top-down” terms aren’t used again, despite their relevance to the cpl and atm-only experiments that I think should be related to these terms (or at least the language made consistent).

Lines 85-9: Explosive vs effusive. Since this paper is about stratospheric aerosols it is about explosive eruptions. Laki was a relatively long-lasting eruption event in the 1780s, but what’s important here is several explosive eruptions that emitted material into the stratosphere over a period of 5 months in the 1780s, not effusive emission into the troposphere. This should be explained if the long-lasting element is a focus, and if not should the discussion here should at least be clearer. The ‘Part 2’ Zambri et al (2019) study includes a table of these eruptions from an earlier source

Zambri, B., Robock, A., Mills, M. J., & Schmidt, A. (2019). Modeling the 1783–1784 Laki eruption in Iceland: 2. Climate impacts. Journal of Geophysical Research: Atmospheres, 124(13), 6770-6790.

Fig. 1: I cannot understand the “normalized” units. Can the authors please switch this to something that clearly indicates how far the state is from peak and zero response? Preferably this would simply be the actual units, and the right side of the plot can be used as a secondary axis, allowing the same figure to show both kg/kg and 1/km.

Line 153: Is the “red curve” actually the orange one?

Fig. 2a,b: Can the x-axis please be edited to prominently show every January?

Line 236: Since there’s a lot going on here, could the authors please introduce this subsection with a brief explanation of how this will fit together, e.g. this is a time where stratospheric warming (rather than tropospheric cooling) is a prominent factor, and presumably is responsible for altered wave activity and through this circulation changes.

Line 243: Could the authors please explain physically the significance of “strong upward EP flux” (i.e. in terms of meridional buoyancy flux and wave-mean circulation interactions). Not many researchers in the volcano-climate community have extensive geophysical fluid dynamics training. Please generally walk the audience through.

Line 255: Could the authors please explain what the significance is of the *near-surface* Plumb flux anomalies? Does this quantity link surface cooling to a stratospheric mean flow response that is modulated by eddies? Given forcing of the mean flow by waves/eddies is the divergence of wave flux activity, how does this relate? This is perhaps tricky, because the temperature responses in a-c don’t overlap well, while there’s evidence that polar circulation responses to temperature changes occur non-linearly and differ strongly depending on the location of the forcing. But I hope the authors can offer a little perspective on this.

De, B., Wu, Y., & Polvani, L. M. (2020). Non‐additivity of the midlatitude circulation response to regional Arctic temperature anomalies: The role of the stratosphere. Geophysical Research Letters, 47(16), e2020GL088057.

Line 259: Could the authors please add a line to explain what the significance is of the anomalies in wave activity source, and why it might be so focused on the North Pacific?

Line 265: The caption should explain what the blue-to-red colored areas are. Presumably from the color bar units and match to the black contour lines this is a zonal wind anomaly.

Line 271: Can this shift be attributed to the gradual development of surface cooling? Would be helpful if the authors can briefly rationalize this change between winters 1 & 2.

Line 280: As with the above, I’d like to see a brief physical explanation of how this information on the near-surface Plumb flux relates to the volcanic forcing and stratospheric circulation.

Line 288: Somewhere in this paragraph should express that the aerosol has mostly left the stratosphere, while ocean cooling (possibly prolonged by interactions with sea ice) is still at play.

Line 290: Please explain (or at least speculate on) why the wave activity flux is now purely upward unlike before.

Fig. 5: Considering the unperturbed case has no eruptions, shouldn’t the first, second, and third winters all have similar numbers of SSWs? Here they are shown to vary from 6 to 15 (a factor of 2.5x), which suggests the 20 ensemble members are not sufficient for an SSW analysis, at least with the used methodology.

Line 302: Considering how noisy the data is I find this tiny p-value entirely misrepresentative.

Line 320: I agree with the statement, but I think it should be clearly stated atm-only has stratospheric warming but with minimal surface and lower-tropospheric cooling. 

Lines 330: I would be a bit more specific on what the “stratospheric thermal response” is here and generally. I think the authors mean the aerosol warming here but heat fluxes are also part of the dynamical response.

Line 333: Is there a specific reason there’s no SSWs shown from the atm-only runs?

Fig. 7: This figure interrupts the flow of the dynamical Results, so I feel it might be better suited in 2.3 Experimental design.

Lines 364-76: I’m not seeing much evidence of cause and effect links from stratospheric changes to tropospheric responses in this section, which I note can occur due to SSWs or otherwise. I wonder if the authors can rework this a bit and perhaps relate it the literature on stratosphere-troposphere coupling.

Lines 443-458: Optional, but since the manuscript does not really focus on the QBO I feel this could be better as a text in the Supplement with just a brief mention here.

Lines 463: As I explained in the comment on Line 29, the probability of better predicting decadal variability through this study’s explorations is quite low for multiple reasons. I recommend at least better contextualizing this prediction aspect. Alternatively and optionally, I would personally find the discussion/conclusion section more interesting if it instead focused on what the results suggest is experienced by people, societies, and ecosystems on the rare occasions when these eruptions do occur, e.g. understanding and remaining knowledge gaps for how stratospheric circulation responds to eruptions and through this affects northern latitude near-surface conditions.

Typographic/wording issues:

Line 38: language is awkward here, would change from “possibly very strong” to “at times strong” or similar.

Lines, 41,42, and 194: “short-wave” and “long-wave” aren’t usually hyphenated. Would cut the hyphens or at least make “longwave” in Line 217 consistent.

Line 62: “affect” rather than “effect”

Fig. 2b: the pressure coordinates are jammed together, so the figure should be altered to fix this.

Line 458: Would be better with a paragraph break after “detected.”