This study examines the impact of ICNC and CDNC on the properties of mixed-phase clouds using large-eddy simulations. However, I do not see new and exciting findings in this study, and some results are not convincing. Therefore, I recommend rejecting this paper in the current format.

Major comments:

1. The authors seem to be not familiar with the literature in the field. The impact of ICNC and CDNC on the properties of mixed-phase clouds, which arises from the efficiency of INP and CCN, has been explored extensively in the past. Key conclusions of this study are very similar to some previous studies, e.g, by Solomon et al. 2018 (doi: 10.5194/acp-18-17047-2018). I do not see any new or exciting results out of this study.

2. The authors stated “ICNC/CDNC can be a simplified general factor that contributes to a more general understanding of mixed-phase clouds”. If the authors can establish "a general principle" for the mixed-phase cloud, I think it would be very useful and this study would be worth for a publication. However, this argument is not convincing for the following reasons:

2.1. The author conducted nine idealized simulations of the mixed-phase clouds. It is not convincing to me how results from nine idealized simulations can be helpful to establish a general principle or a general parameterization for the mixed-phase cloud.

2.2. Observations are missing to justify the model setup and evaluate simulation results. For example, it said that “a system of mixed-phase stratocumulus clouds was observed to exist over a period between 02:00 local solar time (LST) and 20:00 LST on March 29th, 2017. On average, the bottom and top of these clouds are at ~400 m and ~3 km in altitude, respectively.” Is there any ground-based observations to support this statement? See Fig. 1 in Solomon’s paper as a good example. 

2.3. Model setup for the initial CCN and INP measurements is also not convincing. One weird result is the extremely high IWC for the control run. As far as I know, IWC in the mixed-phase stratocumulus cloud is usually much smaller than LWC. However, in the control run, IWC/LWC is 26.28, which is extremely high. Do you have any observations to support this result? Can you find any literature to support such high ratio exist in the mixed-phase cloud? If you cannot find observations to support such high IWC/LWC value, it means that the control run might not be setup correctly, and the goal to establish “a general principle” from those simulation results is not convincing.

Here is one suggestion to improve the paper quality: whenever you refer to the observation (cloud, CCN, INP, LWP, IWP...), you should either cite a reference if the results are published or add it in the paper to support your statement. If you don't have those observations, you should provide reasonable assumptions. If results are quite different from previous studies (e.g., extremely high IWC/LWC), you should provide strong justifications.

Review of the manuscript “EGUsphere-2023-862” entitled “Examination of varying mixed-phase stratocumulus clouds in terms of their properties, ice processes and aerosol-cloud interactions between polar and midlatitude cases: An attempt to propose a microphysical factor to explain the variation” written by Lee, Jung, Yoon, Um, Zheng, Guo, Manoj, and Song.

This study shows simulation results of idealized clouds that can occur in a polar region using the Weather Research and Forecasting model with a bin cloud microphysics scheme at a spatially fine resolution. The authors endeavor to examine how variations in cloud development are influenced by changes in cloud condensation nuclei (CCN) and ice-nucleating particle (INP) concentrations.

The authors propose that the ratio between the concentrations of ice crystals and cloud droplets may constitute a pivotal factor influencing cloud development. However, substantiating such a claim is challenging due to the scarcity of supporting evidence, and numerical experiments do not appear to be appropriately designed to substantiate this assertion. Furthermore, despite simulations of stratocumuli in a polar region are conducted, there is a notable absence of evidence regarding the adequacy of the model's cloud representation. Additionally, the experimental design lacks sufficient information for simulating stratocumuli adequately. The authors also introduce logical leaps in their arguments at several junctures. Consequently, for these reasons, the reviewer recommends against the publication of this paper. Detailed discussions on specific issues are provided below.

Major:

1. To convincingly demonstrate that the ratio between ICNC and CDNC (ICNC/CDNC) is indeed a critical factor in cloud development, as emphasized by the authors, it is imperative to systematically vary this ratio and conduct numerical experiments. This research, however, has scarcely undertaken such an approach. The ratios presented in Table 1 vary across all experiments, rendering it challenging to discern whether the differences revealed in each experiment stem simply from disparities in CCN and INP or from the ICNC/CDNC. To substantiate the authors' claims, it is essential that similar outcomes emerge in experiments with matched ICNC/CDNC but differing CCN and INP concentrations, thereby providing evidence for the significance of this ratio. Furthermore, as depicted in Figure 7, all four experiments—200_2, 2000_20, 200_20, and 2000_2—exhibit similar profiles for IWC and LWC. However, the ICNC/CDNC ratios vary significantly among these experiments, ranging from 0.108 to 0.512. Therefore, based on these findings, it is challenging to assert that ICNC/CDNC is a critical factor.
2. The authors present cloud development based solely on profiles of horizontally (and temporally) averaged IWC and LWC. However, it should be noted that cloud development is influenced by a multitude of physical quantities beyond these metrics. Offering results exclusively in the form of averaged IWC and LWC profiles is not considered appropriate.
3. The authors numerically simulate clouds in a polar region using the UM data as initial conditions. However, the adequacy of the model's cloud representation cannot be assessed as there is no comparison between the simulated clouds and those that can form under the actual conditions. For instance, in the control run, the averaged total water path of the simulated clouds is approximately 33 g m^–2. Without a comparison to the total water path of clouds formed under the corresponding conditions in the corresponding region, it is impossible to gauge the fidelity of the model's cloud simulation.
4. According to Figure 2, the potential temperature in the near-surface atmosphere is approximately 257 K, which, assuming a pressure of 1000 hPa, corresponds to an extremely low temperature of approximately –16°C. However, the way SST (and/or surface heat fluxes) is prescribed under these atmospheric conditions remains undisclosed. For example, if the SST is assumed to be near 0°C, this would anticipate significant sensible heat flux. In this situation, it becomes vital to provide details on many cloud-related quantities and synoptic conditions, such as SST evolution, surface heat fluxes, large-scale subsidence, and cloud top height development.
5. In some points of the paper, the authors present arguments with substantial logical leaps. For instance, at L351, the authors assert that drop sedimentation “increases” total cloud mass. However, this assertion is neither logical nor supported by simulation results. The experimental findings merely demonstrate that in the comparison between the 200_2 run and the 200_2_noice run, the former exhibits greater total cloud mass and greater drop sedimentation. This can be attributed to the inherent fact that denser clouds yield more precipitation. In addition, at L403, the authors describe that a higher IWC/LWC ratio in the 200_2 run than in the 200_2_noice run results in more water content (WC), but no logical rationale for this claim is provided, and it is evident only that the inclusion of INP leads to an increase in total water mass.

Minor:

1. I strongly recommend refine the writing. The authors excessively use sentences beginning with "There" and passive voice constructions.
2. Although the authors have discussed the strong correlation between IWC and IWP in the early sections of the paper (e.g., Table 2), they consistently describe them as "IWC (IWP)" throughout the manuscript, which diminishes the readability of the paper. If the correlation is indeed evident, it is advisable to mention either IWC or IWP alone for clarity.