The manuscript examines how mixed-phase cloud microphysical parameters influence macrophysical cloud properties during a marine cold-air outbreak over the Labrador Sea. Using two nested domains to represent upwind stratiform and downwind cumuliform cloud regimes, the authors conduct an extensive ensemble of simulations that systematically co-vary six microphysical input parameters. They employ Gaussian Process emulation to quantify relationships between input parameters and cloud-scale responses. The analysis identifies regime-dependent dominant parameters and demonstrates strong nonlinear interactions among them, underscoring the limitations of single-parameter sensitivity studies. The manuscript is clearly written, methodologically rigorous, and the analysis is comprehensive. I recommend publication following minor revisions.

Minor concerns

l. 21 – I wonder if there are any other studies that could be cited here?

ll. 54-59 Please also include Elsaesser et al. (2025) here.

Sec. 2.1 I wonder if the author could list cloud-top temperature (CTT) here (e.g., from a typical configuration). Assuming that CTT varies across configurations (e.g., I would expect stronger ice processes to produce lower/warmer cloud-tops, thereby preventing themselves) and if not too much work, perhaps CTT could even be added to Fig. 6?

Sec. 2.2.2 If aerosol was considered here, it would affect both N_d and N_inp; it is unclear if the chosen dynamic ranges for N_d and N_inp correspond well? I wonder if the authors could briefly quantify and explain.

Fig. 6 I’m surprised by the large cloud cover in the Cu regime. How do the authors define cloud cover?

Fig. 7/8 Is the small sensitivity of mprof in Sc-dominated regimes connected to the large cloud fraction (as well as small IWP) ?

Fig. 9 How should the reader interpret a greater TWP in the Cu-dominated regime under increased E_HM? While a LWP reduction make sense to me, I’m surprised to see an even stronger IWP increase.

Typos/Language

l. 342 “shown … show “

References

Elsaesser, G., M. van Lier-Walqui, Q. Yang, M. Kelley, A.S. Ackerman, A. Fridlind, G. Cesana, G.A. Schmidt, J. Wu, A. Behrangi, S.J. Camargo, B. De, K. Inoue, N. Leitmann-Niimi, and J.D.O. Strong, 2025: Using machine learning to generate a GISS ModelE calibrated physics ensemble (CPE). J. Adv. Model. Earth Syst., 17, no. 4, e2024MS004713, doi:10.1029/2024MS004713.

This paper develops a cloud emulator based on perturbed parameter ensembles of a regional model to investigate how six cloud microphysical parameters affect mixed phase CAO clouds over the Labrador Sea. The results show that the sensitivity of cloud properties to any single microphysical parameter are highly dependent on, and interconnected with, the values of the other parameters. Overall, the manuscript is generally well written and clearly structured. However, I have several major concerns regarding the construction of the emulator and the selection of the sensitivity parameters, particularly the omission of CCN-related processes. I therefore believe that major revisions are required to clarify several key methodological and physical aspects prior to publication.

Major comments:

One of my main concerns is the author’s selection of cloud droplet number concentration (Nd) and ice-nucleating particles (INPs) as the perturbed parameters. The selection of Nd instead of CCN, while simultaneously selecting INP concentrations, is physically difficult to justify. INPs are a subset of aerosols with strong ice-nucleating ability and are generally associated with way larger uncertainties than CCN. The authors state that aerosol-derived Nd is not used to avoid additional uncertainties, but this reasoning appears inconsistent given that the study includes the much more uncertain INP parameter. If INP variability is considered acceptable within the emulator framework, then CCN should be also included rather than fixed-Nd profile.  The omission of CCN effects through a prescribed Nd should be more carefully justified. I am particularly concerned because, in real CAO environments, Nd is strongly controlled by aerosol aging processes and activation to CCNs. Also, CCN will have competition of water vapors with INPs in mixed-phase cloud, hence affects INPs response as well. Treating Nd as an independent tunable parameter, rather than linking it to aerosol activation, may bias the INP response and the interpretation of the relative importance of microphysical sensitivities.

My second concern comes from the sparsity of the sampling in the 6-D parameter space. The PPE uses 66 ensemble members, which is reasonable, but 66 samples in a six-dimensional nonlinear parameter space may still be sparse, especially given the strong parameter interactions and equifinality demonstrated in the manuscript. This raises questions about the robustness of the emulator, particularly near the boundaries of the parameter space where extrapolation risks may be larger. I therefore suggest that the authors conduct a convergence test to evaluate the stability of the emulator results. In addition, a more explicit discussion of emulator uncertainty quantification and potential extrapolation errors in the manuscript would be helpful.

Finally, while the authors acknowledge case specificity, many conclusions are framed in broader terms regarding mixed-phase CAO clouds and aerosol–cloud interactions. Given the strong dependence of mixed-phase cloud processes on thermodynamic structure, aerosol regime, and synoptic conditions, I suggest that the authors more explicitly frame their conclusions as case-specific and discuss how different aerosol forcing and environmental conditions (such as continental versus marine environments), could alter the inferred parameter sensitivities.

Minor comments:

Page4 L109: in the manuscript, the author only considered dust as INPs. However, rmore and more studies have reported that sea-salt aerosols can also act as effective INPs, particularly in marine environments (e.g. Wagner et al., 2021; JV Trueblood et al., 2021). Given that this case is over the Labrador Sea, it would be helpful to discuss the potential contribution of marine (sea-salt) INPs and how excluding them might affect the inferred INP sensitivity. If feasible, I encourage the authors to include an additional sensitivity test (or at least an order-of-magnitude estimate) representing sea-salt INPs, or to justify why dust-only INPs are appropriate for this case.

Page5 Figure1: change the color blue for C323. The current lines are nearly invisible on printed paper

Page6 L134: please explicitly write the global mode name you used for dust concentration simulation

Page7 L165: please define the variable Niics,xy when first introduced

Page25 L483-484: It seems to me that you did not demonstrate where the dust source originates in your nested region. Therefore, I am not fully convinced that "purposefully omitting measurements from desert soil sources" is an appropriate choice. I would also suggest presenting the desert dust ns–T relationship in Figure A1 to show how those dust properties would differ from those examined here.

Page 27 L515: Page 27, L515: Why are only these three levels (surface, 1 km, and 2 km) selected? It would be helpful to clarify the typical upper bound of the cloud top height, how many model levels are located beneath it, and whether these selected levels adequately capture the vertical structure of the INP concentration variation.