General comments:

The authors present results from a novel set of climate change simulations with a very high resolution coupled ocean-atmosphere model. They compare these results to simulations using a version of that coupled model with a somewhat coarser atmospheric resolution. 

I am confident that readers will be interested in the results of this work - the construction of a very high resolution coupled climate model, its computational characteristics, and its simulations. I also am confident that scientists will be interested is using the model output that has been made available. The team of researchers is to be congratulated for this significant computational achievement. 

Having said that, I do have significant concerns. A primary goal in such a study is to evaluate what impact the very high resolution grid has on a model's ability to simulate the current climate and to simulate the response of the climate system to radiative forcing changes. Due in part to the short length of the simulations, single realization, and initialization shocks from the land and atmosphere, it is difficult to pinpoint changes in the model behaviour that come about from the use of very high resolution (with the notable exception of tropical cyclones).  Therefore, the scientific results of the study (especially their robustness) are rather limited.

The repeated initialization shocks, especially from the land conditions, contribute to drift and uncertainty in the simulations. It is possible that a simpler experimental design could have been more useful. For example, some sort of idealized CO2 increase experiment (gradual, or switch on) might have offered the possibility of more statistical significance in the results. A notable issue in the manuscript is the lack of assessment of statistical significance - understandable due to the short length of the records, but this makes it very difficult to assess robustness. What is noise and what is a signal of climate change that is different in the HR model than in the MR model?

The focus on regional changes is somewhat problematic, given the short length of the simulations and the considerable climate noise on such small scales. Oftentimes the results are presented without statistical significance or dynamical assessments in a very descriptive, qualitative style. It is difficult to know what to make of such findings. As one example: page 13, lines 04-06 ... the regionally enhanced drying is called out without an assessment of significance or quantification of the role of the high resolution model in simulating this impact. What should the reader conclude from that, given the short simulations? There are many similar examples of qualitative discussion of regional changes without a quantification of the extent to which these changes are related to the high resolution of the model.

Specific comments:

1. p. 2, line 37 What is meant by "... increase in regional information"?

2. I do not find Fig 1 especially illuminating

3. Fig 2: There are multiple acronyms that are not explained in the caption. I do not understand what this Figure is trying to convey.

4. p. 4, line 99 The text is discussing the sequence of runs (2000s, etc) but the referenced figure shows the spatial grid. I am not clear why Fig 3 is referenced for that discussion.

5. p. 5 Lines 18-24 There are lots of acronyms used here that do not convey much information to those unfamiliar with those terms.

6. p. 5, line 4 Is there any parameterization of ocean mesoscale eddies used? If not, is the model able to adequately represent ocean mesoscale eddies at mid to higher latitudes? 

7. p. 6, lines 45-46 Does the model simulate sudden stratospheric warming events realistically? If such a statement is included in the text it would be warranted to have a figure, perhaps in the supplementary section, documenting that.

8. Fig 4a: The MR model warms quite rapidly over the observational record. This seems inconsistent with the observational record. How does that impact the overall results presented in the manuscript?

9. p. 7, line 56 Why not just state what the radiative imbalance is?

10. p. 8, bottom I am very surprised at the decision to use 1990 land initial conditions for all of the runs, even those starting at 2090. There is tremendous inertia in the soil which can take up to a decade or longer to adjust. It seems to me that the entire duration of these transient simulations would be during a period of strong land adjustment. Wasn't there some way to use the land conditions from the MR run and perhaps regrid to the HR run? That would also have issues, but might have less drift.

11. p. 10, Line 11 The bias reduction here may not be due to changes in physics, but to the cold drift of the HR coupled model relative to the MR model; starting from the very warm state of the MR model, the HR model drifts cooler and therefore appears to have a lower error, but it is certainly not clear that this is attributable to any improved physical representations. Further, what is the reason for this cold drift?

   The short durations of all of these simulations really preclude a robust assessment of changes to resolution and physics.

12. p. 10, line 29 I am not sure what is meant by "relatively weak" here. Is there some metric of the double ITCZ that is used?

13. p. 17, lines 40-52 Is there anything about the behaviour of the hi res model that differs from most CMIP6 class models? If so it would be useful to focus on those differences and assess whether the differences are robust, and explain those differences that may be the resolution of improved dynamics and resolution.

14. Fig. 15 How confident are the authors that the differences between Fig, 15b and 15c are robust given the very short length of the simulations?

15. p. 35, lines 88-90 This is a rather qualitative assessment that I am not sure is supported by the results of the manuscript. For example, the pattern and amplitude of tropical ENSO SST variability in HR is noticeably worse than in MR.

The authors conducted a set of transient present-day and future climate simulations with a high-resolution Earth System Model and explore the benefit of global, storm-resolving modeling in comparison to conventional CMIP-style high-resolution modeling as well as regional downscaling.  

The simulations are certainty impressive (also due to the computational resources used to conduct such simulations) and could increase our physical understanding of climate interactions on regional scales. However, there is a range of open questions that are important to be considered for the credibility of the conclusions drawn (e.g. in regards to the drift in the high resolution simulations). Also, the analysis would benefit from a more in-depth analysis of the physical processes behind the observed changes in the transient model climate (potentially on the cost of reducing the number of analyzed climate features and modes of variability).

Major comments:

The 9-km simulations all show a large initialization shock and drift towards colder conditions. Even in the CTL experiment, a substantial drift is evident up to about 10 years into the simulation. This indicates that the spin-up of the 10-year time slice future projections, which is considered as the first 2-years of each simulation, is likely substantially underestimated. A more thorough discussion on these drifts and their impact on the presented result is necessary. Figure 4 only shows the global mean of the model drift, but how does it manifest regionally? The main argument of the authors for conducting the HR simulations is that it enables an investigation of regional features. So are the regional patterns robust or an artifact of the model drift initiated by the model initialization? I would suggest to investigate the regional patterns of the model drift for the pre-industrial simulation – where is it strongest (e.g. are there major drifts in the SSTs over the North Atlantic, Southern Ocean, Arctic)? How long does the (regional) system need to reach an equilibrium? It would be helpful to show 2-D patterns of the trends in the PI simulation for the first 10 years of the simulation. This could also hint at the actual trends in the HR time-slice simulations, which seem be underestimated due to the initialization shock that leads to an overall decrease in temperatures throughout the entire length of the simulations.

Besides exploring the robustness of the results in terms of their spin-up, I feel that the overall evaluation of the PI climate could be more thorough. Given the about 1.5 K colder global temperatures of the HR setup in comparison the MR setup, it would be useful to see how the model performs in comparison to other CMIP models (e.g. some scatter plot of global values of the main variables in comparison to CMIP models and MR). Also why do we see the largest differences over the equatorial Pacific, Arctic Ocean, Antarctica. Here, surface processes play a significant role – could this still be an artifact of the model system drifting? Is in the sea-ice areas e.g. the sea-ice cover the major driver for the differences (given that the HR and MR models show temperature differences much larger than 2 K in the Arctic (e.g. Fig. 5)). Here, a more thorough physical investigation of the differences is essential to understand the differences.

In general, the overall analysis is very descriptive and lacks physical explanations. For example, Section 4 Line 85: “Warming hotspots occur over… “. Some of them are high-mountain terrains, so I assume that large changes in the annual snow cover are evident, but this is not discussed in the manuscript. However, mountains are also usually higher in a HR setup due to the spatial resolution. How do these differences come into play? Another example, Section 5, Line 55: “Comparisons with…” Do the authors have a hypothesis why extreme precipitation is underestimated in both setups? Or in Section 6.2, Line 01: “It should be further noted…”. What are the possible explanations for the differences in HR and MR? These are just three examples of many. Overall, it would be useful to quantify the advances of the HR model in comparison to the MR model and how does this manifest in the modeled climate? This is of specific interest, given that the authors claim that the HR setup is superior to the MR setup.

Specific comments:

Page 7, Line 62: “This is somewhat outside the likely range of CMIP6 models” – please add the range that CMIP6 models show. What implication does the climate sensitivity value have on the presented results and the future climate response discussed in Section 4?

Figure 4: I am wondering why the authors chose to use the ERA5 initial conditions over the MR initial conditions for the atmosphere and land? What is the benefit of using 1990 conditions, as it probably induces a larger shock than e.g. using the conditions from the respective MR time slices. Could the MR initial condition reduce the initialization shock? While the atmospheric processes are relatively fast, some memory might be stored in the land. Did the authors test other initialization strategies.

Section 3: Why is the HR setup so much colder than the MR setup – did both model versions have different tuning targets? Which role do the different parameterizations play (or in case of HR, resolving the small scales)? What are the physical processes and/or model specifics that cause the differences between HR and MR? All of these points should be discussed in more depth. As is, this section seems very descriptive.

Section 4: Again, very descriptive. How much are the results biased by the initialization shock. Further investigations are needed (see general comments).

Fig. 7: Color scale of panel f) is hard to distinguish for very low and medium high values.

Section 4, Line 31: High and low clouds in high latitudes have quite different effects on the surface depending on the season, specifically in terms of their greenhouse effect. This should at least be mentioned.

Figure 12: Are atmospheric or oceanic biases responsible for the extended sea-ice cover towards the Latev Sea? Why not comparing to the entire historical period for satellite data? Why was this specific year picked?

Section 5: I wonder how significant these values are given the drift of the model system. The significance should be discussed.

Figure 13: Red and pink are very hard to distinguish, consider a different color scale.

Page 26, Line 25: It would be good to see a discussion on how the shift in the peak activity months may influence the underestimation of the strength of the cyclones discussed earlier. It also makes me wonder how well the seasonal cycle, e.g. in temperature, is represented in the simulations, given these shifts.

Page 27, Line 67: The results are discussed in relation to CMIP and it is stated “the MJO is fairly realistic compared to the majority of the CMIP5 and CMIP6 models.” This statement lacks references and should also be discussed in more depth. What are the differences? Do the CMIP models also show the double peak? I would suggest to include a CMIP ensemble plot to Figure 15.

Page 28, Line 78: Are there hypotheses that would explain such a frequency split in the MJO from other studies? Do CMIP model show a similar behavior? More in-depth analysis is needed either here or in the Discussion section.  

Page 29, Line 97: “This illustrates…”. Do regional modeling studies support this finding? If so, they need to be referenced. In general, there is very little discussion on previous results that are obtained from regional modeling. To convince the reader that global high-resolution modeling is superior to regional high resolution modeling these discussions are important to add!

Page 31, Line 29: I would like to see the GPCC results, or at least add a reference where these results can be seen.

Section 7: In general, the discussion is very short given the many features presented in the manuscript. Few references are cited, which makes it difficult to really grasp whether the global high-resolution model is superior to regional high-resolution models, as implied several times throughout the manuscript.

Page 35, Line 83: ‘is still affected by the atmospheric resolution’ – or the initial shock due to the initialization routine (see general comment above).

Page 84-85: ‘however, the drift in …’ – This claim is not correct. The external forcing is quite dominant for the SSP8-8.5 scenario, so the drift due to the initialization shock might simply be overcompensated for by the dominant external forcing. To really understand how much in the model response is due to the initial shock and how much due to the external forcing, the authors need to make a more thorough analysis of the trends in the PI simulation induced by the shock. Thereby, they might get a better sense of the climate changes driven by the external forcing or initial shock. This is essential also in terms of a quantification of the significance of the results.

Page 35, Line 12: What would we gain from an even higher resolution? Are there any specific hypotheses in regards to the findings the authors have presented in this paper?