General Comments

This study presents a comprehensive look at the performance of the Model for Prediction Across Scales (MPAS-atmosphere) across both hydrostatic and non-hydrostatic scales (e.g., 60km to 3km), uniform and variable-resolution grid-spacing, and two sets of built-in physical parameterization schemes (mesoscale suite and convection-permitting suite). The authors assess MPAS skill compared with CMA observations and ERA5 reanalysis in Henan province and tersely compare results to GFS forecasts over a single-member, sub-weekly simulation period.

Overall, I think the paper is well written and fits within the scope of GMD and could be, given a bit more work, a valuable contribution to the scientific community, particularly due to its emphasis on evaluating the use of new variable-resolution global climate models for extreme event recreation and sub-weekly weather forecasting. However, I think there are still several major revisions that need to happen prior to this paper being accepted. I would suggest that the editor assign major revisions to this manuscript.

Major Comments

1. Given that this paper centers around the recreation of one weather event, why did the authors not perform an ensemble of simulations with slightly perturbed initial conditions to highlight internal variability impacts on precipitation intensity and spatial distribution? Was the computational demand too high to do so? If so, as mentioned below, it would benefit the reader to know this type of information explicitly. If not, why not perform, at least, a small ensemble of simulations. Related to this, it does concern me that all of the conclusions in this manuscript are based on single-member ensembles of a single event. Would these results hold if the authors simulated another event, perhaps in another season? The authors should at least acknowledge this limitation of their study, and at best run a few additional simulations to explore whether new simulations qualitatively alter their conclusions.
2. Lack of discussion of physical meaning of results: Overall, the manuscript reads more like a technical report than a scientific manuscript; it focuses much more on questions of 'what' than questions of 'why'. In my opinion, this severely limits the usefulness of the paper. In its current form, I suspect that the only readers who might find the manuscript interesting would be users of the MPAS-Atmosphere model, since it essentially only focuses on describing how precipitation depend on resolution and parameterization schemes suite. Instead, if the manuscript had a stronger emphasis on why, the manuscript might be of interest to other model users facing similar questions about the effects of resolution and parameterization. For example, all of the figures basically focus on the precipitation itself, and while there are some references to the effects of large-scale circulation, but their analysis of this is somewhat superficial. Adding more analysis of how resolution or parameterization schemes lead to differences in large-scale circulation and precipitation will improve the paper.
3. What is the basis for dividing the extreme precipitation event into two separate periods and analyzing them separately?
4. Lines 166-172: the authors emphasize the relationship between the precipitation and atmospheric wind field. In Figure 3c, the wind filed predicted by GFS is very close to the ERA5 reanalysis, but the location and intensity of precipitation is still poorly forecasted. In addition to the wind field, other factors affecting precipitation can be discussed.
5. Lines 258-267: Although the V3km.CP reproduced the third precipitation peak compared to 15km.CP, the authors should be note that the magnitude of the third precipitation peak simulated by V3km.CP is much smaller than the observation, rather than just praising the V3km.CP simulation.
6. Some conclusion statements are “common sense”. For example, “This implies that, when the resolution of the refined region is coarser than the cloud-resolving scale, the convection-permitting parameterization scheme suite does not necessarily work better than the default mesoscale suite, but once the refined mesh is close to the cloud-resolving scale, the convection-permitting suite becomes scale aware such that it can intelligently distinguish the convective precipitation and grid-scale precipitation, respectively.” This kind of statements should be deleted. This is the purpose of designing these suites in this model, and cannot be the findings of this study.
7. In addition, some conclusions are not supported by the analysis. For example, line 295, “Consequently, the latent heat release from the simulated peak precipitation would further feed back to the large-scale wind field such that the impact of the wind field upon the simulated peak precipitation is amplified.” I cannot find the results to support this conclusion. So is the line 302, “This implies that the seamless mesh transition of the global variable-resolution model is superior in simulating the extreme precipitation event.” Please add more analysis and discussion before drawing these conclusions.

Minor Comments

1. Line 21: “(Jinfang et al., 2021)” maybe “(Yin et al. 2021)”.
2. The nine-dash line is missing from all the maps.
3. Line 213: “westerly wind” maybe “easterly wind”.
4. The authors mention in Lines 259-260 and Lines 271-272 that “the forecast performance of the CP suite and MS suite at 15km is comparable”, but in fact all the CP simulations clearly miss the third precipitation peak, the differences are significant. I suggest rewording this statement.
5. In addition to the correlation coefficients, I suggest that the authors add root-mean-square error or mean deviation characterizing the forecasted precipitation intensity.