the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 27 Feb 2026
The SOLCHECK Project: A State-of-the-Art Investigation into the Imprints of Solar Variability Across Multiple Timescales
Abstract. The project Solar Contribution to Climate Change on Decadal to Centennial Timescales (SOLCHECK) investigated the influence of solar variability on the atmosphere from the pre-industrial era to the present and future. Variations in the Sun’s output, ranging from weeks to millennia, leave distinct imprints on the climate system. Assessing these imprints is challenging due to limited observations, incomplete representation of feedbacks in climate models, and computational constraints. By exploiting a large ensemble of simulations with advanced chemistry–climate models incorporating realistic solar forcing, SOLCHECK particularly aimed at reducing prevailing uncertainties of the atmospheric solar imprints, and to assess the sensitivity of the atmospheric response to solar forcing on different time scales and in different climate states. One key result of SOLCHECK is that although the initial radiative and chemical response to the 11-year solar cycle is consistent across models in the upper tropical stratosphere, the tropospheric climate response in northern winter is highly sensitive to the dynamical state of the stratosphere, thus impeding a robust assessment of surface solar signatures and decadal climate prediction skill. Another important finding suggests that the climate system reacts differently to solar forcing under past, present, and future conditions, showing a stronger response to external solar variations in the tropical upper troposphere and the Arctic as anthropogenic warming progresses. SOLCHECK further highlighted potential impacts of extreme solar storms in a future climate, as such events, although occurring extremely seldom, may have substantial effects on surface UV with potential consequences for ecosystems and human health.
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RC1: 'Comment on egusphere-2026-126', Anonymous Referee #1, 08 Apr 2026
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AC1: 'Reply on RC1', Ulrike Langematz, 02 Jun 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2026-126/egusphere-2026-126-AC1-supplement.pdf
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AC1: 'Reply on RC1', Ulrike Langematz, 02 Jun 2026
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RC2: 'Comment on egusphere-2026-126', Anonymous Referee #2, 06 May 2026
OVERALL COMMENT:
This paper presents a summary of the SOLCHECK project, highlighting the modeled atmospheric and surface climate impacts of solar forcing (encompassing both irradiance and solar energetic particles). First, using three different models and an extensive number of experiments, they conclude that the 11-year solar cycle robustly impacts the upper tropical stratosphere, but this signal does not robustly propagate to the lower atmosphere, due to a (claimed) dependence on the dynamical state of the stratosphere. Second, the authors suggest that the climate system shows increased sensitivity to solar forcing under future conditions, compared to pre-industrial state. Third, they suggest that extreme solar storms in the future could have substantial effects on surface UV. The subject of the paper is relevant for the journal's readership and wider climate community, as it concerns the long-standing problem of our limited understanding of the effects of solar variability on climate. Also, there is clearly some merit in presenting results from three very different models.
While some of the conclusions of the paper are indeed supported by the evidence provided by the authors (e.g. the robustness of the tropical stratospheric response in temperature and ozone to the sunspot solar cycle - Fig. 2 - as well as the chemical impacts of SPE events - Fig. 1), some are not supported at all (e.g. there is no demonstration of the claimed "sensitivity of the 11-year solar signal to the dynamical state of the stratosphere", nor the "potential impacts of extreme solar storms in a future climate"...!). This makes parts of the paper weak and quite speculative. I would strongly suggest addressing the (major) shortcomings detailed below, and either (1) rephrase things to make results more in line with the evidence provided so far or (2) tone done statements in case additional evidence cannot be provided. I also have reservations about the setup of the GSM experiments, and therefore, I am not convinced about the claimed "increased sensitivity" under future conditions (see specific comments below).
Last but not least, I strongly urge the authors to take care of essential aspects, such as the quality and labeling of Figures (many are quite blurry and/or have wrong labels!), and also including a Table of the experiments. Only if these shortcomings are addressed, this paper could be reconsidered for publication.SPECIFIC COMMENTS:
L19: actually, models have made great strides in representing all the essential processes involved in the atmospheric and chemical response to the solar cycle. Some of the latest generation of CCMs include, for example, particles forcing, spectral solar irradiance, interactive chemistry. The problem may not only lie in models deficiencies (although models are by far not perfect... but some are useful!) but rather in the very small magnitude of the solar signal, relative to the internal variability. This could/should be acknowledged here.
L24-25: while I agree on the first part of this sentence, I strongly disagree with the latter one ("the tropospheric... stratosphere"); this has not really been shown in the paper. Fig. 3 does not really support this, as wind changes there are not really in phase with the solar cycle and there is no robust evidence that the downward propagation depends on the "background state of the stratosphere". More targeted experiments (e.g. testing the impact of the 11 year solar cycle under different initializations resembling different vortex states, for example....) with MANY more ensembles would be needed to demonstrate this point.
L27-28: I am not sure the method employed in the GSM experiments is correct. Are the authors really imposing the same exact TSI perturbation under 1850 and 2100 conditions, or are they employing a scaling of TSI/SSI background conditions (see my specific comments below on this)? It may well be that a different (absolute) TSI reduction is being employed under both conditions (being larger under 2100!), which would invalidate the conclusion about the "enhanced sensitivity" of future climate to solar variations.
L30: this point is only really shown briefly for KASIMA, but not for the other 2 models and it's unclear how sizable the UV perturbation is, compared to UV perturbations due to e.g. cloud and surface albedo changes are. That is: would this UV change be detectable in the real world?
L70: again, I am not convinced about this point, as the evidence provided by the authors is lacking in this respect.
L75: please also add Sukhodolov et al., 2017 here: https://www.nature.com/articles/srep45257
L89: why 19 members, and not... for example... 30 or 40? Deser et al., has shown in many papers that one needs really large ensemble sizes to study circulation metrics
Fig. 1: I think there are several major issues with this Figure, starting with the labels being wrong, the colorscale of panels b-e-h being not optimal, and ending with a wrong description in the caption (where are the UVI panels for EMAC...? what is the difference between the late October 2003 event and the Halloween storm of October 2003 described near L95...? I guess you rather mean the "extreme" SPE for the middle row...? I also believe many, if not all, the panel labels are wrong!)
L115: I totally agree with this conclusion, and I think it should be highlighted in the conclusions' and abstract!
Figs.2 and 3 are VERY blurry. Please improve the quality of these Figures
L149: can you please clarify what you mean with "internal model dynamics"?
L151/L160: I would recommend to analyze and consistently show that this downward progression of the signal is robust in observations, before blaming the models for not "capturing" / "reproducing" it
L153-155: this is not really convincing - as there is no robust evidence of any "phase locking". To support this, the authors would need to analyze the signal in detail and use advanced techniques such as wavelets or similar...
L190: can the authors explain why the inclusion of the solar forcing would worsen the skill in certain regions of the SH hemisphere? Also, why is the CSS so patchy? Could it be that this metric underestimates the amplitude of "unforced" variability?
L207-223: I am a bit worried about the set-up of the GSM experiments. Can the authors verify that the absolute TSI variation they are employing in 1850 and 2100 conditions is the same? If not, part of the basic-state dependence would not really be such, but rather, it would be a dependence on the TSI forcing being employed
L218-223: this would need to be analyzed and shown quantitatively. In the present form, all this discussion feels quite speculative
Fig 5 - again, all panel labels seem to be wrongly references in the Figure caption.
Citation: https://doi.org/10.5194/egusphere-2026-126-RC2 -
AC2: 'Reply on RC2', Ulrike Langematz, 02 Jun 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2026-126/egusphere-2026-126-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Ulrike Langematz, 02 Jun 2026
Status: closed
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RC1: 'Comment on egusphere-2026-126', Anonymous Referee #1, 08 Apr 2026
As summarised in the abstract, this manuscript reports climate model simulations designed to assess the “influence of solar variability on the atmosphere from the pre-industrial era to the present and future.” This is a very well-written article reporting a well-intentioned study by the authors, many of whom have a solid history in studies of this type. However, as explained further below, whether intentional or not, a somewhat unfair advantage is given to the effect of particle precipitation through emphasis on a “worst-case” SEP event occurring only once every few millennia. In contrast, the 11-yr solar UV forcing adopted for the simulations is severely diluted and underestimated, leading to no modeled top-down influence on tropospheric climate at all! Prior work on the latter mechanism is also not adequately reviewed or taken into consideration. Major revisions are needed prior to publication.
- In section 3, possible impacts of the 11-yr solar cycle on stratospheric and tropospheric dynamics are investigated. As shown in Figure 2, a clear, but rather weak, 11-yr solar signal in ozone and temperature in the tropical middle and upper stratosphere is obtained in the three considered models. In section A2.2 (lines 377-378), it is noted that the assumed solar spectral irradiance forcing is “based on the CMIP6 solar forcing dataset (Matthes et al., 2017)”, which is an average of the NRLSSI2 and SATIRE spectral irradiance models. The resulting effect of 11-year solar forcing on the stratosphere using this SSI dataset was investigated by Matthes et al. using two “state-of-the-art” chemistry-climate models, CESM1-WACCM and the ECHAM/MESSy atmospheric chemistry model (EMAC). One of these models, EMAC, appears to be nearly the same as that used in the present study. As shown in their Figure 8, to assess the impact of the 11-year solar cycle, differences between perpetual solar maximum and minimum experiments on annual mean profiles of shortwave heating rates, temperature, and ozone concentrations averaged over the tropics (25S to 25N) were calculated. The modeled solar flux during cycle 22 for November 1989 was used for solar maximum and that for November 1994 was used for solar minimum. This was representative of cycles occurring during the last half of the 20th century and corresponds to a difference of about 150 units of F10.7 solar flux. As seen in their figure, the shortwave heating rate change for ECHAM peaks at about 0.20 K/day at 1.5 hPa while that for WACCM peaks at about 0.22 K/day at 2 hPa. Their temperature change peaks at about 1 K for both models at 2 and 1 hPa. Their ozone change peaks at about 2.5% for both models at 35-40 km altitude. For comparison, the ensemble mean EMAC shortwave heating change between solar maxima and minima estimated in the present manuscript (Figure 2a) is only 0.1 K/day and the temperature change in the upper stratosphere is only 0.3 K. The EMAC ozone change shown in Figure 2c is given in ppmV and peaks at about 0.12 ppmV at 10 hPa. At 3 hPa (~ 40 km), the change is about 0.06 ppmV, which is less than 1% (for a climatological mean of ~ 7 ppmV). So, overall, the minimum to maximum changes shown in Figure 2 are much smaller (by factors of 2 to 3) than those estimated by Matthes et al. (2017) using a comparable climate model but applying larger UV forcing typical of recent strong solar cycles.
- Part of the reduced UV forcing assumed in the present study is due to fact that the results in Figure 2 are composite averages for time-progressive simulations extending from 1850 to 2014. Also, rather than taking an absolute difference between monthly means at solar maximum and minimum to define the spectral irradiance change, 3-year smoothed DJF means of F10.7 were used (section A2.2, lines 391-393). A plot of the assumed F10.7 variation is shown in Figure 3a of the manuscript. During the early part of the record, the highly smoothed solar cycle variations were much weaker than during the latter half of the 20th century, which effectively dilutes the solar UV forcing. According to this plot, the average change in smoothed F10.7 from solar minimum to maximum appears to be no more than 70 or 80 flux units, i.e., about half of what was assumed in the time-slice simulations of Matthes et al. (2017). Consequently, the simulated stratospheric impacts of 11-yr solar forcing shown in Figure 2 are much weaker than is appropriate for most solar cycles occurring during the last 70 years, greatly reducing the ability of these simulations to capture the top-down mechanism.
- Prior work on the top-down UV forcing problem (other than that of Matthes et al. (2017)) is also not adequately reviewed and taken into consideration in the manuscript. The comprehensive review of Gray et al. (2010; https://doi.org/10.1029/2009RG000282) is only mentioned in passing in line 52 in the context of TSI variations but is misspelled and is not in the reference list. The SPARC-sponsored project SolarMIP from a decade ago is not mentioned and the three primary publications of that project (Mitchell et al., 2015, https://doi.org/10.1002/qj.2530; Hood et al., 2015, https://doi.org/10.1002/qj.2553; Misios et al., 2016, https://doi.org/10.1002/qj2695) are not referenced or discussed in the manuscript, a major omission. For example, adopting a solar minimum to maximum change in F10.7 of ~130 flux units, it was found using multiple linear regression that three high-top CMIP-5 models with interactive ozone chemistry simulated an ozone change in the middle to upper stratosphere of up to 3% , a temperature change near the tropical stratopause of ~ 1 K, and November – December zonal wind changes of up to 6 m/s near 50oN, in approximate agreement with the results of Matthes et al. (2017).
- To correct these issues, there are several alternatives. The best solution would be to simply remove section 3 from the manuscript, including the study of impacts on prediction skill, which are unlikely to be accurate given the lack of a top-down dynamical response. The remainder of the manuscript, including the SEP simulations (section 2) and the effect of greenhouse gas increases on climate impacts of an hypothesized GSM (section 4), could be retained to make a viable paper. Otherwise, one would need to begin by comprehensively reviewing prior work on the top-down solar UV forcing problem, including at least the publications noted above as well as others. These results would need to be considered throughout the manuscript, including in the conclusions section and in the abstract. In addition, more simulations would need to be performed using a more realistic solar flux variation. One should start with time-slice experiments using EMAC with a 10.7 cm solar flux change of 150 units to reproduce the results of Matthes et al. (2017). Then, time-progressive simulations using the same model should be performed with results analysed using multiple linear regression. Monthly or weekly mean solar fluxes should be used rather than 3-month smoothed averages. Daily solar fluxes would be a further improvement since daily fluctuations can be quite large. Analyses of zonal winds during austral winter as well as boreal winter would be needed as noted in comment 9 below.
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Regarding section 2, the abstract and the description in section 2 do not make it clear whether UV dose effects on human health of “worst-case” events such as that believed to have occurred in 774-775 would be limited mainly to high polar latitudes (> 70o where the ozone loss occurs) or whether effects would be substantial at middle and lower latitudes where most of the population resides. For example, the description of Figure 1 in section 2 and the figure caption do not mention that the NOy and ozone calculations are averaged over latitudes > 70oN. One has to look at the labels on the figure to find this. According to lines 109 – 110, “The long-lasting ozone reduction increases UV erythema dose by <5% at mid and low latitudes (Fig. 1c) …” However, according to the green shading in Figure 1c, the KASIMA change in UV exceeds 30% at 20o – 40oN. So this implies substantial effects outside of the polar regions. Similarly, in the Conclusions (lines 240-241), “Ozone loss exceeded 40% around 40 km, with effects on UV radiation and mid-stratospheric temperatures …” But the latitudes where this occurs are not specified (see comment 7 below). Please revise the abstract and the conclusions section to make these descriptions clearer.
Other Comments:
6. The sentence in lines 74 to 76 should be separated into two sentences.
7. In Figure 1, all parts except part (c) are for latitudes > 70N. But part (c) shows the largest increase in UVI at middle and low latitudes. Presumably, this is because the ozone loss in the upper stratosphere also affects the ozone concentration at lower altitudes where dynamical transport can transfer it to lower latitudes. If this is the case, please add text to describe this. Also, a plot of the total ozone change similar to that of Figure 9 of Reddman et al. (2023) would help the reader to understand this better.
8. Figure 2c is a plot of the ozone change in ppmV. However, most previous studies (e.g., Matthes et al., 2017) have shown the change as a percentage of the climatological mean. Please replace this figure with one showing percent change. This would produce a peak at a somewhat higher altitude.
9. Ability to detect an 11-year zonal wind signal could be enhanced in several ways. Doubling the solar cycle UV forcing amplitude in the FOCI experiment was a reasonable attempt but 11-yr zonal wind responses have been detected in other model simulations without resorting to this (e.g., Matthes et al., 2017, their Figure 10 using EMAC and WACCM; Hood et al., 2015, their Figures 10 and 11). Note that a modeled zonal wind signal may be more easily detectable in austral winter due to a more stable polar vortex in that hemisphere.
10. In Figure 3, it is very difficult to distinguish the FOCI lines from the F10.7 lines (both gray).
11. In Figure 3a, there is a strong stratopause temperature dip in ~ 1993. Could this be related to dynamical effects of the Pinatubo eruption? Were volcanic aerosol injections included in the model setup?
12. On p. 9, the last sentence (lines 190-191) is very difficult to understand. Please re-phrase.
13. Discussion of Figure 5 in lines 209-223 on p. 11: Presumably these effects are all a consequence of TSI variability and are not affected by the stratospheric effects of UV forcing. If so, please state that this is the case.
14. In Figure 5, the labels (a, b, etc.) are inconsistent with what is stated in the caption and in the text.
15. Section 5 (Conclusions). The short paragraph on solar signals of the 11-yr solar cycle (lines 245-249) is not very informative. As requested in comment 4 above, this component of the paper (section 3) either needs to be removed or augmented by carrying out new simulations of the type described there. A detailed comparison with previous results of SolarMIP and Matthes et al. (2017) should be provided.
16. In section A2.2, the method of determining solar maximum and solar minimum years is described in lines 390-395. Please state what the mean difference is in F10.7 flux units when averaged over all of the cycles considered here. It appears to be ~ 70 or 80 but whatever it is should be stated and the value should be compared to the effective values considered in previous studies (e.g., Matthes et al., 2017).
17. F10.7 is measured only back to about 1947. How was F10.7 determined for years back to 1850? Please explain. Is it possible that the early cycles are being underestimated?
18. In the title, “State-of-the-Art” should be replaced with “Chemistry-Climate Model” or just “Modeling”. “State-of-the-art” should only be used to describe the models that are being used. It should be left to others to decide if the modeling study itself is state-of-the-art.
Citation: https://doi.org/10.5194/egusphere-2026-126-RC1 -
AC1: 'Reply on RC1', Ulrike Langematz, 02 Jun 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2026-126/egusphere-2026-126-AC1-supplement.pdf
-
RC2: 'Comment on egusphere-2026-126', Anonymous Referee #2, 06 May 2026
OVERALL COMMENT:
This paper presents a summary of the SOLCHECK project, highlighting the modeled atmospheric and surface climate impacts of solar forcing (encompassing both irradiance and solar energetic particles). First, using three different models and an extensive number of experiments, they conclude that the 11-year solar cycle robustly impacts the upper tropical stratosphere, but this signal does not robustly propagate to the lower atmosphere, due to a (claimed) dependence on the dynamical state of the stratosphere. Second, the authors suggest that the climate system shows increased sensitivity to solar forcing under future conditions, compared to pre-industrial state. Third, they suggest that extreme solar storms in the future could have substantial effects on surface UV. The subject of the paper is relevant for the journal's readership and wider climate community, as it concerns the long-standing problem of our limited understanding of the effects of solar variability on climate. Also, there is clearly some merit in presenting results from three very different models.
While some of the conclusions of the paper are indeed supported by the evidence provided by the authors (e.g. the robustness of the tropical stratospheric response in temperature and ozone to the sunspot solar cycle - Fig. 2 - as well as the chemical impacts of SPE events - Fig. 1), some are not supported at all (e.g. there is no demonstration of the claimed "sensitivity of the 11-year solar signal to the dynamical state of the stratosphere", nor the "potential impacts of extreme solar storms in a future climate"...!). This makes parts of the paper weak and quite speculative. I would strongly suggest addressing the (major) shortcomings detailed below, and either (1) rephrase things to make results more in line with the evidence provided so far or (2) tone done statements in case additional evidence cannot be provided. I also have reservations about the setup of the GSM experiments, and therefore, I am not convinced about the claimed "increased sensitivity" under future conditions (see specific comments below).
Last but not least, I strongly urge the authors to take care of essential aspects, such as the quality and labeling of Figures (many are quite blurry and/or have wrong labels!), and also including a Table of the experiments. Only if these shortcomings are addressed, this paper could be reconsidered for publication.SPECIFIC COMMENTS:
L19: actually, models have made great strides in representing all the essential processes involved in the atmospheric and chemical response to the solar cycle. Some of the latest generation of CCMs include, for example, particles forcing, spectral solar irradiance, interactive chemistry. The problem may not only lie in models deficiencies (although models are by far not perfect... but some are useful!) but rather in the very small magnitude of the solar signal, relative to the internal variability. This could/should be acknowledged here.
L24-25: while I agree on the first part of this sentence, I strongly disagree with the latter one ("the tropospheric... stratosphere"); this has not really been shown in the paper. Fig. 3 does not really support this, as wind changes there are not really in phase with the solar cycle and there is no robust evidence that the downward propagation depends on the "background state of the stratosphere". More targeted experiments (e.g. testing the impact of the 11 year solar cycle under different initializations resembling different vortex states, for example....) with MANY more ensembles would be needed to demonstrate this point.
L27-28: I am not sure the method employed in the GSM experiments is correct. Are the authors really imposing the same exact TSI perturbation under 1850 and 2100 conditions, or are they employing a scaling of TSI/SSI background conditions (see my specific comments below on this)? It may well be that a different (absolute) TSI reduction is being employed under both conditions (being larger under 2100!), which would invalidate the conclusion about the "enhanced sensitivity" of future climate to solar variations.
L30: this point is only really shown briefly for KASIMA, but not for the other 2 models and it's unclear how sizable the UV perturbation is, compared to UV perturbations due to e.g. cloud and surface albedo changes are. That is: would this UV change be detectable in the real world?
L70: again, I am not convinced about this point, as the evidence provided by the authors is lacking in this respect.
L75: please also add Sukhodolov et al., 2017 here: https://www.nature.com/articles/srep45257
L89: why 19 members, and not... for example... 30 or 40? Deser et al., has shown in many papers that one needs really large ensemble sizes to study circulation metrics
Fig. 1: I think there are several major issues with this Figure, starting with the labels being wrong, the colorscale of panels b-e-h being not optimal, and ending with a wrong description in the caption (where are the UVI panels for EMAC...? what is the difference between the late October 2003 event and the Halloween storm of October 2003 described near L95...? I guess you rather mean the "extreme" SPE for the middle row...? I also believe many, if not all, the panel labels are wrong!)
L115: I totally agree with this conclusion, and I think it should be highlighted in the conclusions' and abstract!
Figs.2 and 3 are VERY blurry. Please improve the quality of these Figures
L149: can you please clarify what you mean with "internal model dynamics"?
L151/L160: I would recommend to analyze and consistently show that this downward progression of the signal is robust in observations, before blaming the models for not "capturing" / "reproducing" it
L153-155: this is not really convincing - as there is no robust evidence of any "phase locking". To support this, the authors would need to analyze the signal in detail and use advanced techniques such as wavelets or similar...
L190: can the authors explain why the inclusion of the solar forcing would worsen the skill in certain regions of the SH hemisphere? Also, why is the CSS so patchy? Could it be that this metric underestimates the amplitude of "unforced" variability?
L207-223: I am a bit worried about the set-up of the GSM experiments. Can the authors verify that the absolute TSI variation they are employing in 1850 and 2100 conditions is the same? If not, part of the basic-state dependence would not really be such, but rather, it would be a dependence on the TSI forcing being employed
L218-223: this would need to be analyzed and shown quantitatively. In the present form, all this discussion feels quite speculative
Fig 5 - again, all panel labels seem to be wrongly references in the Figure caption.
Citation: https://doi.org/10.5194/egusphere-2026-126-RC2 -
AC2: 'Reply on RC2', Ulrike Langematz, 02 Jun 2026
The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2026/egusphere-2026-126/egusphere-2026-126-AC2-supplement.pdf
-
AC2: 'Reply on RC2', Ulrike Langematz, 02 Jun 2026
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- 1
As summarised in the abstract, this manuscript reports climate model simulations designed to assess the “influence of solar variability on the atmosphere from the pre-industrial era to the present and future.” This is a very well-written article reporting a well-intentioned study by the authors, many of whom have a solid history in studies of this type. However, as explained further below, whether intentional or not, a somewhat unfair advantage is given to the effect of particle precipitation through emphasis on a “worst-case” SEP event occurring only once every few millennia. In contrast, the 11-yr solar UV forcing adopted for the simulations is severely diluted and underestimated, leading to no modeled top-down influence on tropospheric climate at all! Prior work on the latter mechanism is also not adequately reviewed or taken into consideration. Major revisions are needed prior to publication.
Regarding section 2, the abstract and the description in section 2 do not make it clear whether UV dose effects on human health of “worst-case” events such as that believed to have occurred in 774-775 would be limited mainly to high polar latitudes (> 70o where the ozone loss occurs) or whether effects would be substantial at middle and lower latitudes where most of the population resides. For example, the description of Figure 1 in section 2 and the figure caption do not mention that the NOy and ozone calculations are averaged over latitudes > 70oN. One has to look at the labels on the figure to find this. According to lines 109 – 110, “The long-lasting ozone reduction increases UV erythema dose by <5% at mid and low latitudes (Fig. 1c) …” However, according to the green shading in Figure 1c, the KASIMA change in UV exceeds 30% at 20o – 40oN. So this implies substantial effects outside of the polar regions. Similarly, in the Conclusions (lines 240-241), “Ozone loss exceeded 40% around 40 km, with effects on UV radiation and mid-stratospheric temperatures …” But the latitudes where this occurs are not specified (see comment 7 below). Please revise the abstract and the conclusions section to make these descriptions clearer.
Other Comments:
6. The sentence in lines 74 to 76 should be separated into two sentences.
7. In Figure 1, all parts except part (c) are for latitudes > 70N. But part (c) shows the largest increase in UVI at middle and low latitudes. Presumably, this is because the ozone loss in the upper stratosphere also affects the ozone concentration at lower altitudes where dynamical transport can transfer it to lower latitudes. If this is the case, please add text to describe this. Also, a plot of the total ozone change similar to that of Figure 9 of Reddman et al. (2023) would help the reader to understand this better.
8. Figure 2c is a plot of the ozone change in ppmV. However, most previous studies (e.g., Matthes et al., 2017) have shown the change as a percentage of the climatological mean. Please replace this figure with one showing percent change. This would produce a peak at a somewhat higher altitude.
9. Ability to detect an 11-year zonal wind signal could be enhanced in several ways. Doubling the solar cycle UV forcing amplitude in the FOCI experiment was a reasonable attempt but 11-yr zonal wind responses have been detected in other model simulations without resorting to this (e.g., Matthes et al., 2017, their Figure 10 using EMAC and WACCM; Hood et al., 2015, their Figures 10 and 11). Note that a modeled zonal wind signal may be more easily detectable in austral winter due to a more stable polar vortex in that hemisphere.
10. In Figure 3, it is very difficult to distinguish the FOCI lines from the F10.7 lines (both gray).
11. In Figure 3a, there is a strong stratopause temperature dip in ~ 1993. Could this be related to dynamical effects of the Pinatubo eruption? Were volcanic aerosol injections included in the model setup?
12. On p. 9, the last sentence (lines 190-191) is very difficult to understand. Please re-phrase.
13. Discussion of Figure 5 in lines 209-223 on p. 11: Presumably these effects are all a consequence of TSI variability and are not affected by the stratospheric effects of UV forcing. If so, please state that this is the case.
14. In Figure 5, the labels (a, b, etc.) are inconsistent with what is stated in the caption and in the text.
15. Section 5 (Conclusions). The short paragraph on solar signals of the 11-yr solar cycle (lines 245-249) is not very informative. As requested in comment 4 above, this component of the paper (section 3) either needs to be removed or augmented by carrying out new simulations of the type described there. A detailed comparison with previous results of SolarMIP and Matthes et al. (2017) should be provided.
16. In section A2.2, the method of determining solar maximum and solar minimum years is described in lines 390-395. Please state what the mean difference is in F10.7 flux units when averaged over all of the cycles considered here. It appears to be ~ 70 or 80 but whatever it is should be stated and the value should be compared to the effective values considered in previous studies (e.g., Matthes et al., 2017).
17. F10.7 is measured only back to about 1947. How was F10.7 determined for years back to 1850? Please explain. Is it possible that the early cycles are being underestimated?
18. In the title, “State-of-the-Art” should be replaced with “Chemistry-Climate Model” or just “Modeling”. “State-of-the-art” should only be used to describe the models that are being used. It should be left to others to decide if the modeling study itself is state-of-the-art.