Comment on acp-2021-438

difficult time understanding what the results were from this study. While I understand that overall the liquid water path increased and ice water path decreased over the Southern Ocean region in the modified model compared to the control simulation, the overall bias was not assessed. I also do not understand the additional simulations used to assess changes in cloud cover and the convective scheme. There is an overall lack of explanation regarding why specific things were tested and what these could tell us. Additionally, there are many details missing that would limit the study from being reproducible, including how cloud level types are defined, what parameters in the convective scheme are changed and to what values.

Varma propose and implement a heterogenous ice nucleation parameterization approach that scales the primary ice nucleation temperature based on dust number concentrations. In comparing a 20-year simulation with the default physics (control) to 20-year simulation with the updated ice nucleation scheme, they report an overall decrease in ice water and increase in liquid water. Their results indicate simulated outgoing SW radiation decreased and cloud fraction also decreased with the proposed ice nucleation scheme. Varma et al. attribute these findings to additional feedbacks associated with convective cloud physics scheme, including a parameter that defines cloud fractions associated with a given amount of detrained condensation that differs between liquid and frozen clouds. The authors report that this approach 1) "improves the physics of the model" (line 234) and 2) "is one of the first global atmospheric models to implement such an approach to simulated the roles of INPs with minimum complexity in the micro-physics scheme to improve the SW radiation biases over the SO region".
While the topics of southern ocean ice nucleation, cloud phase, and SW radiation are very important, I have major concerns with this study. If my comments were to be adequately addressed, I think the study would change entirely and need to be resubmitted as a separate publication. Therefore, I recommend this manuscript to be rejected.

General Comments:
Major Comment 1 -A major concern of this study is the approach for representing heterogeneous ice nucleation. The proposed parametrization essentially scales the heterogeneous ice nucleation temperature (thetr) based on dust number concentrations relative to an arbitrary reference dust concentration (refdust), such that thetr is lower (higher) for mixed phase clouds in regions with dust concentrations lower (higher) than refdust. refdust is completely arbitrary, referred to as a "tuning parameter", and is mentioned (line 121) to be a heuristic parametrization. A first major question is why was an existing dust ice nucleating particle parameterization not considered for this study? Neimand et al., 2012 andDeMott et al., 2015 are well-vetted dust-specific INP parameterizations that have been tested against laboratory and field measurements and have also been implemented into global models (Zhao et al., 2020). While the authors appear optimistic that observations could help constrain parameters in their thetr paramterization, it is not obvious how one would constrain non-physical parameters like thetr and refdust. This approach is likely highly sensitive to refdust, though the sensitivity of the study results to refdust is not tested here. Another major question is, given the number of challenges involved in simulating aerosol and ice nucleating particles, the parameterization needs to be assessed for accuracy and skill. There are observations of ice nucleating particles over the Southern Ocean that not included in this study, and I do not see a path in which this parameterization could be evaluated. It is also not clear how accurate simulated dust concentrations are in the Unified Model.
Major Comment 2 -I also have a major concern regarding the authors arguing that adding this new approach improves the model physics. First, I do not think the parameterization is in any way based on our understanding of the physical process of ice nucleation (i.e., for a given temperature, the available number of ice nucleating particles depends on the aerosol population including the abundance and composition). I also do not see how the parameterization can be physically constrained. Regardless, I also do not see an assessment of the model performance with the "improved" physics. I only see analyses on changes in simulated clouds from the control simulation. Without an assessment of simulated clouds or TOA SW radiation, it is not clear that the model has actually been improved.
Major Comment 3 -I had a difficult time understanding what the results were from this study. While I understand that overall the liquid water path increased and ice water path decreased over the Southern Ocean region in the modified model compared to the control simulation, the overall bias was not assessed. I also do not understand the additional simulations used to assess changes in cloud cover and the convective scheme. There is an overall lack of explanation regarding why specific things were tested and what these could tell us. Additionally, there are many details missing that would limit the study from being reproducible, including how cloud level types are defined, what parameters in the convective scheme are changed and to what values.

Specific Comments:
Introduction: L44 -"Our focus will be on the immersion freezing process as it is the most commonly implemented heterogeneous ice nucleation process in global climate models (GCMs)." It is unclear to me what is meant by this. Do you mean that the immersion freezing process is most active in GCMs? Is it the case that immersion freezing is expected to be a common ice nucleation pathway in these low-level stratocumulus clouds? Do you have a reference for this? L53 -"Among these, mineral dust is… " I agree that mineral dust is a strong source of ice nucleating particles near land sources, but many studies have highlighted the role of marine ice nucleating particle sin remote regions, especially the Southern Ocean (Burrows et al., 2013, Wilson et al., 2015, McCluskey et al., 2019. Why are marine sources ignored in this study? L54 -"in the generally low INP environment over the SO region" -how low? Please provide a reference (e.g., McCluskey et al., 2018;McFarquhar et al., 2020;Schmale. Et al., 2021) L55 -"… INP dependency on immersion freezing is not included in most of the GCMs" -I believe the authors mean "immersion freezing dependency on INPs". Note that this is not necessarily the case anymore. See CESM2 ice nucleation scheme (e.g., Gettelman et al., 2019) which is based on the classical nucleation theory approach for estimating ice nucleation rates based on dust aerosol abundance from Hoose et al., 2010 and implemented into CESM by Wang et al., 2014. (note this CNT parametrization is referred to later, Line 65) L67 -Just because mineral dust is a globally dominate in immersion freezing does not mean mineral dust dominates over the Southern Ocean region. Please include a discussion on the marine source of INPs.

Methods:
L87 -"paucity in INPs in clean environments…" -How low? Please include references. L92 -While the number density of dust is low over the SO region, studies have determined it possible for even small amounts of dust to have a strong influence on INP estimates (E.g., Zhao et al., 2020). How accurate is the simulated dust aerosol in regions far-removed from dust sources? Are there previous papers that have asses the dust concentrations from this model, or possible observational datasets that could be used to make sure the dust concentrations are reasonable? Couldn't this can be particularly

Results
L150 -it is extremely difficult to interpret figure 5 due to their small size and font size. L172 -I think the discussion regarding the reduction in TOA outgoing SW radiation & cloud fraction needs to be expanded. The authors state "This is probably because, previously, the large amounts of ice clouds were introducing compensating errors, which the new scheme now removes" -what compensating errors? Can the authors expand on this? Discussion: L183 -What is the reason for comparing to the exp_cap study? Did I miss that? Because this is not clear, I do not really follow most of this discussion. L184 -How were the model data segregated identified the cloud level types used in Figures  7, 8, and 9? Are these statistically significant differences between the exp simulations and control simulations? L192 -this paragraph regarding "potential feedback processes from the convections scheme" is confusing without the support analysis? I think there would be room for more discussion on this. L203 -The authors introduce two more simulations, but it is not clear to me what is being changed. Perhaps adding the simulation details to the table would help. What is the difference between exp_eff and control_eff? How would one constrain the parameters that control cloud fraction (a non-physical quanity) and detrained condensate (perhaps physical, but difficult to isolate). What values were used in the exp_eff and control_eff experiments?