After its first round of revisions, this manuscript is improved relative to the first version. There are fewer speculative statements, and some details have been described better. When pushed by both reviewers to add depth via additional simulations and analyses, the authors have instead argued for why these are not necessary. Fair enough; the authors can ultimately determine the scope of their study. At the same time, its impact on the community will be similarly scaled. The topic of ice processes and SIP in Arctic clouds is important, and the community does need more studies of this nature to help make the needed advances in understanding and modeling. Thus, perhaps this study is a baseline for very warm Arctic mixed phase and multi-layered clouds that can motivate the modeling community to dive further into the relevant processes. In this regard, it is useful to eventually see this manuscript published. There are, however, still some important details for the authors to address before the paper is ready for publication. All of the comments below can be addressed via text modifications, thus I would characterize these as minor revisions.
The Main Challenge
The main persisting challenge I have with this paper is encapsulated in the first paragraph of the discussion/conclusion section. The text outlines the two foci of the paper: 1) “to show that multilayer clouds can be accurately modelled….” and 2) “to evaluate the microphysical sensitivities…..while constraining the parameterisations to the observed ground-based measurements to better represent cloud phase.” The first of these statements suggests that in this manuscript the multilayer clouds have been accurately modelled. This depends strongly on the definition of accurate. If it is defined as simulating clouds at approximately the right times and heights, then perhaps it can be argued that these simulations were indeed accurate. But I argue that this type of accuracy is simply due to the advective forcing of the model (i.e., where and when is moisture advected at the large-scale). In my mind the main point of the paper, as conveyed in the title, is rather about microphysics, and if we refer to Figure 10 we see that the clouds are not accurately simulated. Arguably the most important aspect of these clouds is the super-cooled liquid water, which ultimately determines the impact of these clouds on the environment and defines the cloud life cycle. The broader Arctic mixed-phase modeling community also appears to agree that the liquid component is the most important, based on the existing modeling studies in the literature. These simulations do not get the liquid component of the clouds correct and do not show any simulations that significantly impact the liquid component, on average (e.g., Fig. 10). Thus, in my mind, these simulations cannot be considered “accurate.” The second focus is on sensitivities in the microphysics. The paper has indeed examined sensitivities for the ice component, but interestingly, the simulations show no corresponding sensitivities for the liquid component. Thus, while in the most extreme sensitivity tests the observed ice component is indeed approximately reproduced by the model, there is no change in the poor representation of the liquid. So technically the cloud phase is “better represented,” going from very bad to not quite as bad, but it is not well represented. Moreover, it is worth pondering if the sensitivity to ice processes would be different if there were less liquid water (like in the observations) or if there were more sensitivity of the liquid water to the ice (as is seen in many other model studies). So are these sensitivities to ice parameterizations representative?
I still believe this paper has interesting results that contribute to the field, but it is important that the authors present the paper in the proper context. First, there needs to be some discussion of the liquid component of these clouds. Why does the liquid component show such little sensitivity to the perturbations in the ice? Why does the model produce too much liquid to start with? And why is the model seemingly unable to produced sustained liquid water clouds that have much lower (more realistic) liquid water paths? One main goal for why we care about the ice is to properly simulate the phase partitioning in these clouds, so this topic must be discussed more. Second, the authors need to provide the justification for why it is still relevant to examine the sensitivity to various ice processes in these cases where the liquid water is so far from accurate. Are these sensitivities generally representative and therefore relevant for thinner (more accurate) liquid water clouds? i.e., is it OK that the liquid component is not well simulated? I think the authors can make these points, and they need to make these points.
Specific Comments:
Line 0: The title is much improved.
Line 94: “ice floe” not “ice shelf”
Line 96: “….taken from level 3 files produced from Vaisala….”
Line 102-103: Thanks for mentioning the cloud classification is challenging. However, the newly included statement is misleading. Yes, having radar and lidar helps with cloud classification. Yet, in multilayered clouds (the focus of this study), the lidar signal is often attenuated by the lower cloud, rendering the phase classification in the upper clouds very unreliable. This is a distinct weakness of the CloudNet approach and adds significant uncertainty.
Line 103-104, 162: CCN and INP acronyms have already been introduced in the first section.
Line 106: “…..and from the US Atmospheric Radiation Measurement (ARM) facility….”
Line 108: Introduce the CSU acronym.
Line 153-155: I understand the computational cost of high resolution. The manuscript mentions that a simulation was done at higher resolution, but with the baseline (default) approach to ice processes. According to the statement given here, this higher resolution did not have as big of an effect on the ice as the liquid. However, many of the other sensitivity simulations employ different details about the ice that might be sensitive to resolution. If the authors simply do not want to do further high-resolution simulations, that is acceptable, but a general statement like provided here that cloud ice is less effected by resolution seems to be inappropriate. It is possibly true for the one tested model set up, which itself already has many other problems, but unless the simulations are run, we do not know if it is true for some of the other ice processes that are tested and might produce more ice. Moreover, the fact that the high-resolution simulation gets some change in the liquid, when the other simulations conducted in this paper apparently do not, is very useful for addressing a major deficiency of the current paper – the fact that there is little impact on the poorly represented liquid phase by changing the ice processes.
Line 352-353: I believe this is an incorrect assumption. In the observations there is at least a 1-2 km gap between the upper and lower clouds. It takes time for ice to fall across this depth. The lower cloud layer is less than 1 km thick. Thus, the timing for seeding vs fallout from the lower cloud layer does not work out for this hypothesized mechanism for forming ice in the observed lower cloud. Moreover, why would there have been seeding ONLY upstream for this whole time period? There is no clear reason why that would happen upstream consistently over time but not at the observation site. Typically, if there were seeding upstream the whole system would advect in time and eventually be observed at the Eulerian observation point. It is much more likely that either: 1) The “observations,” which are really retrievals, are wrong about the presence of ice in the lower cloud, or 2) there is a mechanism for forming ice in the lower cloud that does not involve seeding.
Line 354: “redundant” seems like the wrong word here.
Line 425-437: This paragraph talks about impacts on frozen hydrometeors in a couple of ways. While there are some sensitivities, I would argue that these are rather inconsequential. First, in Fig. 10 the logarithmic Y axis means that much of the range and apparent changes are so small as to not even be detectable from the observational perspective. For the most extreme case of INPx1E6 the FWP only gets up to 1 g/m2! And the differences among the other cases are all very small and well below 1 g/m2. Thus, while indeed the model suggests that there is SOME ice present, it is inconsequential in most cases. Similarly, towards the end of the paragraph there is discussion of ice particle collisions. However, at the highest concentration there is 1 particle per 50 L, and for the 1E4 simulation it is 1 particle per 500L! Again, the number of collisions resulting from these low concentrations is vanishingly small and inconsequential for the cloud processes. It seems to me that this paragraph could be summarized by the statement that while some of these model changes have slight impacts, ice processes are not significant in any of them.
Line 457-458: As noted in the text, the key transition in the lower cloud occurs just after 12, but the process rates are given for 6-12 UTC. Thus, do the processes described in the figure actually represent the apparently abrupt shift that occurs just after 12?
Line 459-461: Perhaps I am missing a key detail here, but how do these SIP mechanisms impact the ice mass? These processes are ones in which individual ice crystals turn into multiple ice crystals, such that there would be an impact on ice number but not on mass (other than the conversion of liquid droplets to ice in some of the processes). Ice-ice collisions, for example, should have no mass change, just a number change. Thus, I’m confused by how these are put in terms of mass rates. I believe they should instead be number rates. If not, please provide a clear explanation for the reader.
Line 468: Again, ice-ice breakup does not directly impact mass. The subsequent vapor growth of the new, higher number of ice crystals could impact mass growth, but that is no longer breakup but rather depositional growth.
Line 471-473: How much of a drop in temperature? This would be useful to know. Presumably this drop in temperature is due to advective tendencies because radiative cooling in the cloud layer should be minimal.
Line 490: This is a nearly identical sentence to one that was included a couple of paragraphs prior.
Line 491: Why is this not already “realistic”? What is the basis for thinking that breakup needs to be reduced?
Line 495-500: I do not understand the SIP scaling. Is this simply an implementation of a different parameterization for collision breakup? If so, just be clear that it is a different parameterization that is not modified here but simply tested (and found to render collision breakup ineffective). My problem is that the word “scaling” makes it sound like there is some parameter that is being adjusted (“scaled”) to modify the effectiveness of the collision process. If you believe the default collisional breakup is too aggressive (first that should be clarified and justified), it should certainly be possible to “scale” the collision process by adjusting one of multiple components of the collisional breakup parameterization. But I get the sense that the authors do not want to explore such details. In any case, the language used here is unclear. If I understand what is being said, perhaps it is most clear to just state that the so-called scaling adjustment to the collision parameterization effectively nullifies the process altogether.
Line 534-536: Yes, I agree that the assimilation and/or advective tendencies for key parameters are likely problematic here. These may be why the liquid water is not well represented and not very responsive to the ice microphysics. It is worth noting this point explicitly here, unless there are other explanations for why the liquid is represented so poorly.
Line 559-563: These statements are speculative and not supported by any evidence presented in this paper. i.e., I do not see any ICON-ART results that are shown to be more realistic for this type of case. Moreover, it has not been shown that better representation of updrafts, which might impact droplet activation, enhances the predictability of cloud properties. These statements should be removed. All that can really be said is that in future studies it might make sense to explore if ICON-ART and/or better resolved vertical motions can help to improve the representation of this type of cloud.
Line 585-586: This statement is not true. According to Fig. 10 the 1E6 simulation produces a reasonable amount of ice in both the upper and lower cloud layers, better than any of the SIP simulations. Thus, according to these simulations, SIP (at least the added SIP parameterizations) are not required to reach observed levels of ice.
Line 606: The number of grid levels is increased, while the grid spacing is thus decreased.
Appendix B: This appendix has no text, only figures. Does this conform to ACP style? |
