On the importance to consider the cloud dependence in parameterizing the albedo of snow on sea ice
Abstract. The impact of a revised snow surface albedo parameterization, which explicitly considers the cloud dependence of the snow albedo, is evaluated in simulations of a coupled regional climate model of the Arctic. The revised snow surface albedo parameterization leads to a more realistic simulation of the variability of the surface albedo during the snow melt period in late May and June. In particular, the reproduction of lower albedo values under cloud-free/broken-cloud conditions during the snow melt period represents a major improvement and results in an earlier disappearance of the snow cover and an earlier onset of sea-ice melt. In this way, the consideration of the cloud dependence of the snow albedo results in an amplification of the two-stage snow-albedo/ice-albedo feedback in the model. This finds expression in additional loss of sea-ice volume of more than 1000 km3 and additional reduction of summer sea-ice extent of around 250,000 km2 during one melting period, with accumulating magnitude of the overall changes in subsequent years.
Lara Foth et al.
Status: open (until 13 Jul 2023)
- RC1: 'Comment on egusphere-2023-634', Anonymous Referee #1, 09 May 2023 reply
Lara Foth et al.
Lara Foth et al.
Viewed (geographical distribution)
The authors implement a previously suggested snow albedo parameterization in a regional climate model - this is done as a function of cloud-cover and temperature. They first statistically compare the modelled results against MOSAiC data, and find a fairly convincing improvement in the agreement. However, it is unclear how much of these improvements are due to the temperature parameterization, and how much is due to the cloud cover sensitivity - this must be clarified before publication.
They then investigate the impact of their parameterization on a pan-Arctic scale, and generate some interesting results regarding the difference in sea ice extent & volume. However, the results are not interpreted with respect to the model’s sensitivities to initial conditions, boundary forcing, and the choice of study period. If the method is sensitive to these factors, this will seriously limit the impact of the results.
Before publication the authors must first discuss the degree to which their study period (2019/20) is actually representative of the typical situation - the simplest way to do this would be to just extend the study period to more seasons. I believe the authors should also justify why their results are not sensitive to changes in the initial & boundary conditions that are within the uncertainty of those conditions - this may end up being quite brief, but it is important. Finally, the use of the model itself to investigate this question needs to be justified a bit further; it was unclear to me whether this new parameterization improved or worsened the skill of the model on a pan-Arctic scale.
Based on the above, I believe this manuscript needs some major additions before it can be published. If the authors can address my concerns, I would be happy to re-review.
1. Interannual Variability of the Pan-Arctic Findings
My largest concern is that the model-based results regarding sea ice extent and volume are derived from only one melt season (2019/20). Without presenting evidence that this season is somehow representative of the others, the model-based results represent a single number drawn from an unknown probability distribution. It is therefore unclear to me how to interpret the results with respect to the underlying feedback mechanisms. Without investigating other years, results concerning the role of the albedo parameterization cannot safely be interpreted outside of the specific study period.
2. Separability of Cloud and Temperature Dependence
My secondary concern is that the authors have implemented both a cloud dependence and a temperature dependence in their albedo parameterisation, but often report results (such as in the abstract, and title) as if they are simply evaluating the new cloud dependence. It is important and currently unclear to me how much of the results are due to the temperature dependence, and how much is due to the cloud-dependence. Regarding the title, we will only actually know the importance of the cloud dependence in this study’s albedo parametrization once the temperature effect that the authors have included has been established and controlled for.
3. How skillful is this model in the study period?
The impact of this study is tightly linked to the skill of the model in the study period, so it is striking that this is not discussed. I can only assume (see my minor comments below) that the model run began with the sea ice in the right place and with roughly the right thickness and overlying snow depth based on satellite observations. But after initialisation does the sea ice move, grow and melt in a realistic way? If the sea ice doesn’t behave correctly in the model, then the real-world impact of getting the albedo right will not be available through the model study. The authors should present their findings in the context of the model’s underlying ability to investigate these questions.
On this note, I was surprised that the authors didn’t contextualise the additional loss of sea ice volume and extent with regard to the “truth” of the model. i.e. do these extra reductions move the modelled sea ice extent/volume closer or further away from the truth per satellites? That is to say, was it over or underestimating these variables before?
Manuscript structure: There are some peculiarities with the manuscript structure: the paper as a whole would definitely benefit from deeper analysis and a dedicated discussion section. To illustrate the need for a discussion section, the first paragraph of Conclusions (~L140) is a really nice piece of analysis, but cannot reasonably be described as a conclusion. I think the lack of dedicated discussion has also led to the omission of the key methodological details and considerations that I’ve outlined above and below.
Open data: It was unclear to me how I could reproduce or replicate this analysis, and I was frustrated to see a “data available on request” statement when this sort of statement violates the Copernicus data policy. While I appreciate the data is available on a tape drive somewhere in DKRZ, no instructions are given as to where to find it, and no DOI or similar is given. The authors should upload the model output to a public and persistent repository such as Zenodo, where it can be reversioned as the review process progresses. If a request is indeed necessary to publish this data on Swift, this is that request! I also note that no code was presented for review, which further hinders my ability to replicate and validate the analysis.
Ice types: the MOSAiC floe was located on second-year ice, and this should be mentioned since it results in a considerably less saline snowpack which will affect the temperature dependence of the albedo parameterization. I could not see in the manuscript what the ice type was for the Svalbard flights which led to the development of the new parameterization, but this should be stated and compared to the MOSAiC floe. If all of this takes place of second year ice, how relevant is it to first-year ice which is increasingly dominant in the Arctic?
Figure 3: it seems like, if this pattern continues, the difference in SIV might continue to increase? Hopefully it will level off to some stable difference value, which will more realistically represent the impact of this parameterization. By simulating such a short period, it seems like you’re simulating what might be referred to as a “transient response” of the system to your changes, rather than an “equilibrium response”. And I think it’s the equilibrium response that we should be really interested in? This should be discussed.
Internal variability: I’m not an expert on regional climate models, but my understanding is that they do show some internal variability. I.e. if you ran the model with slightly different initial conditions or boundary forcing, you would get a different figure for the impact of this albedo parameterization that is larger than the scale of the perturbation to the conditions/forcings? Reading Rinke et al. (2004 Clim Res; and noting that Dr. Rinke is on this paper) it seems like this sensitivity of the findings to small differences and uncertainty in the initial/boundary conditions should at least be mentioned.
This is of course clearly related to my previous concern about interannual variability (which could be viewed as an expression of internal variability). But I think it’s worth me explicitly asking this question: for the year 2019/20, how sensitive are your SIE/SIV findings to small changes to the initial or boundary conditions? If they are significantly sensitive, then that would limit the power of this study.
Sea ice initialisation: I couldn’t find any information on how the sea ice was initialised in this experiment. Given this study is about the timing and nature of snowmelt onset, it seems obvious that the initial state of the sea ice in terms of its extent/thickness distribution and snow depth are relevant. The authors should specify how they initialised the sea ice cover, and what biases may be contained in this initialisation. Along these lines, the general evolution of the sea ice both in the model and reality for the study period should be briefly described.
I found the comparison of the model parametrization with MOSAiC data slightly odd. I agree with what you’ve written about the fact that the model timing won’t agree with the MOSAiC data so a statistical comparison is necessary. But why didn’t you just evaluate the quality of the albedo parameterization based on the observed variables in Table 1? Seems to me that would be the first step - test the parametrization by calculating the albedo with the in-situ observed snow temperature and cloud covers, then see if the model also gets it with its own modelled snow temp and cloud cover.