ACP review:

This work by Bednarz et al. studies the climate impacts of the dramatic and strong Hunga eruption, where large quantities (150Tg) of H2O was injected into the stratosphere using CESM2 (WACCM6) ensemble (30 members). Much less SO2 was in the eruptive material, 0,5-1,0Tg, so this case study is relevant when it comes to understand how the optical properties of water can affect various atmospheric thermal gradients and thus climate, compared to SO2 that is usually in the focus. Their findings include a sigificant La Nina response in the first two years following the eruption that in turn trigger changes in the NAO via changes in tropospheric wave flux up into the stratosphere. SH was also explored where changes in the SAM was also identified. In general the results are quite convincing and where the possible mechanistic pathways are detailed. This is a well written manuscript and I do recommend it‘s publication in ACP after addressing a few comments that I have.

First, I wonder if adding a figure showing the temperature response with time from the surface and up (like Figure 5/Hovmoller plot), for say 0-20°and 65-90°. That could show more clearly how strongly the eruption impacts the stratosphere and the associated climate impacts.

L40-41: Here more explanation would be good, since the high AOD is basically due to the large stratospheric water content that enhances the reaction of SO2 into sulfate aerosols in addition to supporting the growth of the sulfate particles themselfs.

L56: It would be good to mention the water vapor lifetime in the models vs observations/measurements, how realistic is it to expect such a delayed response due to water vapor only? Not in the study of Jucker et al but more in general.

L121: „Some significant, largely negative...“ sounds confusing, so these significant anomalies are they largely negative?

L124: this is section 4, right?

L126: Section 5 perhaps?

Figure 1: So even where the anomalies are zero (white), the response is significant? Please explain.

L210-211: I think it needs mentioning that  such a mechanism has been proposed with respect to sulfate-rich stratospheric eruptions – but here the focus is mainly on a water vapor-rich eruption. I think that the small amount of SO2 causes a negligible impact on the PV here, despite the amplification/growth of SO2 due to water vapor.

Review of “Indirect climate impacts of the Hunga eruption” by E.M. Bednarz et al.

The authors use single model large ensemble simulations to assess the potential impacts of the 2022 Hunga Tonga volcanic eruption. The manuscript is generally well written and presents interesting results well worthy of publication.

My main comment is that there is a certain lack of acknowledgment that many of the described results have been reported earlier. There is ample referencing in the introduction, but the results are mostly presented as new findings, while to me they are mostly confirmations of previous findings, or more detailed but similar results. In particular, the cited Jucker et al (2024) study is very similar in several points: It uses WACCM, has 30 ensemble members , discusses longer-term surface impacts, shows a figure very similar to Fig 1c,d, and discusses a similar global wave train and a potential role of changes in ENSO.

Of course, that study only adds water vapor and does not start from the observed state of the atmosphere. So the current simulations are certainly different, but not to a point to be entirely new.

In addition, this manuscript seems to be a spin-off from the APARC Hunga Tonga impact comparison effort, from which there will probably be more publications forthcoming. How is this study then different to others? For instance, I noticed another submitted manuscript, the cited Zhuo et al (2025) has some common authors and shows an almost identical Figure 1. So similar to my comment above, I believe this should be acknowledged more openly in the manuscript, and more context given.

To be clear, I wouldn’t want this manuscript to become a constant comparison to other papers. Just giving more of an idea of where these results lie with respect to published literature would be good.

More specific comments:

L 28: “demonstrates”: I am not sure one should be that definite. There are still open questions and as noted above, others have reported similar results.

L34: “eruption erupted” - not wrong, but maybe one can find a more elegant expression?

L81: “Meinshausen”, not “Meineshausen”

L82-83: I think the way the ocean is initialized is rather important. So even if it is described in Richter et al (2022), I think it would be good to describe this in more detail. In particular, how do the authors deal with model drift which is often the problem in coupled simulations initialized close to observation?

L83-84: “first 1-2 months”: I understand this depends on ensemble member as the nudging is how the ensemble is created. But this is not clear at this point at all. Consider adding just a little but more information, as my immediate reaction was “so what is it, 1 or 2 months?”

L116, Figures 2,3: Why did the authors decide to focus on annual means versus seasonal impacts? Warm versus cold season impacts could be rather different.

L127: This already is section 4. Maybe this should be “Section 5"?

L139-146: Why did the authors decide to focus on the early La Nina response and largely discard the later El Nino response? Could it be that La Nina is forced by aerosols and El Nino by water vapor in the long term given its longer residence time? Or could it be that the coupled model shifts into an El Nino as a response to the La Nina, regardless of longer-term forcing? Related to this, why did the authors decide to stop the analysis after 5 years even though their simulations were run for 10 years and the signals are still pretty strong in year 5?

L160-161: I agree, but the fixed SST simulation still has wave-like signals in the extratropics. Where do those come from?

L166: this should probably be “(section 5)” and “(section 6)”

L233-234: I agree, but one could also invert the argument that if there are surface signatures found even in the fixed SST simulations, it is likely that the real impact (where the ocean is coupled) should be expected to be larger.

Figure 5: Again, there are still significant signals at the end of 2026, so why stop here? How does this look for 2027 and later?

L381: Domeisen, not Domaisen

L389-391: This is a very long parenthesis. If there’s so much to say, it’s probably better to say it in a separate sentence.

L416: Again, I am not sure this study “demonstrates”.

This manuscript examines the indirect surface climate effects of the January 2022 Hunga volcanic eruption using a large-ensemble simulation approach. The authors employ the state-of-the-art CESM2(WACCM6) Earth system model with interactive chemistry and aerosols in both atmosphere-only and coupled ocean–atmosphere configurations. The 30 ensemble members are used for each configuration, a large sample that improves eruption signal detection relative to previous studies (e.g., 10-member ensembles in the HTHH-MOC project). The study shows that, despite the eruption’s weak direct radiative forcing, indirect mechanisms produce statistically significant regional surface climate effects. Model results indicate a La Nina-like cooling of the equatorial Pacific during the first 1–2 years post-eruption, followed by an El Nino-like state around year 4. These ENSO phase shifts subsequently influence extratropical circulation: the North Atlantic Oscillation is altered during boreal winters, and the Southern Annular Mode is modified in austral spring, through a combination of ENSO teleconnections and stratospheric polar-vortex disturbances.

Overall, the manuscript is well-written, and the analysis is comprehensive. The authors effectively use the two model configurations to distinguish the role of ocean coupling, showing that the coupled runs exhibit more pronounced surface impacts (due to ENSO responses) than the atmosphere-only runs. The inclusion of interactive chemistry/aerosols and the consideration of both Northern and Southern Hemisphere effects (including stratospheric ozone changes) are strengths of the study. The manuscript also acknowledges the modest magnitude of the signals relative to internal variability, and it employs statistical significance tests and ensemble subsampling to assess result robustness.

I recommend publication after the following major points and minor fixes are addressed.

Major comments:

1. The study relies on a single climate model (CESM2(WACCM6)). While this model is sophisticated and the large ensemble lends confidence to internal consistency, it is important to situate the findings in the context of other models and studies. The authors are encouraged to expand the discussion of how their results compare to previous Hunga-Tonga modeling efforts. For example, Jucker et al. (2024) used chemistry–climate model simulations with water-vapor-only forcing and also found multi-year surface responses; the authors might comment on similarities or differences in timing (Jucker et al. saw responses 3–8 years post-eruption) or in mechanisms.  A brief comparison would also acknowledge the multi-model context and underscore which findings are novel versus confirmations of prior work.
2. The coupled-ocean simulations show significant cooling in Northern Hemisphere extratropical surface temperatures during the first 1–3 years, which the authors attribute to circulation changes rather than direct radiative forcing (since most aerosols remained in the Southern Hemisphere). To strengthen this attribution, it'd be very helpful to analyze and/or clarify the TOA radiative flux changes due to the eruption. For example, the authors could include a decomposition of the TOA radiative perturbation by component (shortwave vs longwave, or aerosol vs water vapor vs ozone contributions) to confirm that direct radiative forcing in the NH is minimal, and thus the NH cooling must stem from indirect effects. It would strengthen the case that circulation, not local direct radiative forcing, drives the NH response.
3. Given the central role of the ENSO response in this study, the manuscript should more directly compare the simulated ENSO behavior to observations. The model predicts a La Nina–like state in 2022–2023 followed by an El Nino–like phase by 2025. In reality, a protracted La Nina persisted from 2021 through late 2022, and an El Nino event emerged by mid-2023 (much of the world experienced a transition to El Nino conditions by late 2023). The manuscript already notes that the eruption may have reinforced the prolonged La Niña episode, but the model–observation comparison could be improved. Explicitly point out that the simulated La Nina-like cooling in 2022–2023 coincides with the observed La Nina, whereas the model’s El Nino-like warming appears in year 4, about a year later than the real‐world phase shift in 2023–2024. Discuss whether this lag is simply internal variability or whether it indicates that the volcanic perturbation prolonged La Nina conditions.
4. The simulation setup injects 0.5 Tg SO₂ and 150 Tg H₂O between 25–30 km altitude on 15 January 2022. The authors should justify the assumed injection altitude profile, and discuss how it might affect the results. For instance, was 25–30 km chosen based on the bulk of the eruption mass being in the lower stratosphere, or to align with the HTHH-MOC protocol? Showing a modelled time-height cross-section for Figure 1 would clarify how the stratospheric aerosol/water vapor spreads vertically in your simulations. Ideally, a sensitivity test could show that slightly different injection height assumptions would not qualitatively change the outcomes. 
5. The manuscript employs statistical analysis to identify significant responses (e.g., stippling where the forced-minus-control difference exceeds ±2 standard errors of the mean, roughly corresponding to a 95% confidence level). Please state the significance threshold consistently (e.g., forced minus control exceeds ±2 SEM ≈ 95 % confidence). Also, please add a brief rationale for choosing N = 30 and comment on statistical power relative to the weak signals.
6. The study outlines a multi-step causal chain: asymmetric volcanic aerosol forcing displaces the ITCZ, initiating La Nina-like cooling; this cooling then reshapes planetary-wave activity and perturbs the polar vortices, ultimately producing regional surface-climate anomalies, including shifts in the NAO. In addition, stratospheric aerosol vs. water vapor effects have opposing influences on the polar vortex (strengthening vs. weakening), and there are hemispheric differences with ozone-related effects in the south. This multifaceted chain of causality from 2022 Hunga eruption can be challenging to grasp from text alone. While this is not mandatory, a schematic, summarizing the indirect pathways by which the Hunga eruption influences surface climate, would enhance the presentation and could be included in the conclusions for clarity.

Minor suggestions

Line 110 (Figure 1): the ΔsAOD (× 10³) appears too large compared with observations (OMPS; SAGE-III, etc); please double-check.

Line 14 “The 2022 Hunga eruption erupted …” → “The 2022 Hunga volcano erupted.”

Line 45 “Stocker, et al., 2024” → “Stocker et al. (2024)”.

Line 55 “Jucker at al.” → “Jucker et al.”

Lines 80 & 380 “Meineshausen” → “Meinshausen”; “Domaisen” → “Domeisen”.

Line 118 Use “damps” instead of “dampens”.

Line 360 “Quagia, et al. in prep” → “Quaglia et al., in preparation”.