the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 11 Apr 2023
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.
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Preprint
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The requested preprint has a corresponding peer-reviewed final revised paper. You are encouraged to refer to the final revised version.
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Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2023-634', Anonymous Referee #1, 09 May 2023
Synopsis
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.
Major Concerns
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?
Minor Concerns
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.
Citation: https://doi.org/10.5194/egusphere-2023-634-RC1 -
AC1: 'Reply on RC1', Wolfgang Dorn, 24 Nov 2023
We thank Referee #1 for the time and effort he/she spent reading the manuscript and providing extensive comments. We also appreciate the enormous number of potential suggestions for improvements and further investigations. Since some of these suggestions go far beyond the purpose of what we actually have intended to demonstrate, we realize the need to explain the purpose in more detail.
The main purpose is to demonstrate that the consideration of a simple cloud dependence in the here applied broadband albedo parameterization is able to mimic the cloud effect on snow surface albedo reasonably. This means that it is not absolutely necessary to switch to a physically more consistent, but also computationally more complex waveband-dependent albedo parameterization, which implicitly would include a cloud effect on the albedo. The second and main purpose is to demonstrate that this rather minor modification of the snow albedo parameterization has a significant impact on the sea ice in a coupled model system due to its influence on the positive surface albedo feedback. We will better emphasize these two points in the revised version of the manuscript.
It has never been the purpose to demonstrate that the sea-ice simulation is closer to reality by considering a cloud dependence in the albedo parameterization. Even though this is actually the case in our model simulations, we had decided to exclude praising our own model, since we aware that the grade of sea ice in a coupled model depends on many parameterizations, not only on the albedo parameterization. Some of these parameterizations are usually subject of a kind of tuning to obtain more realistic sea ice in the model as for instance discussed by Mauritsen et al. (2012, https://doi.org/10.1029/2012MS000154). Therefore, it doesn't mean much whether the modeled sea ice is better or worse than before as long as tuning of parameters in other process descriptions, which are not well established by observations, were applied to counteract the biases of a previously more unrealistic albedo parameterization. In particular, it doesn't disqualify the added value of considering the cloud dependence in parameterizing the snow albedo.
Response to the Major Concerns
1. Interannual Variability of the Pan-Arctic Findings
Corresponding long-term sensitivity simulations for the period 1979-2021 have recently been completed and will be discussed in the revised version of the manuscript. These simulations were running without nudging to ERA5 data, meaning that the model is allowed to diverge from the observed atmospheric circulation so that internal variability becomes more relevant.
2. Separability of Cloud and Temperature Dependence
The new snow albedo parameterization basically uses the same temperature dependence as the original snow albedo parameterization, only the values of the parameters are separately defined for overcast and non-overcast conditions. When averaging the albedo for overcast and non-overcast conditions relative to the frequency of the conditions, the albedo values are almost equal in the two parameterizations. This means that changes in the temperature dependence effectively depend on the cloud dependence. There is no cloud-independent temperature dependence which one might evaluate without further sensitivity experiments. In the current sensitivity experiment, all differences between the model simulations can be considered as a consequence of the additionally introduced cloud dependence. We will clarify this point in the revised version of the manuscript.
3. How skillful is this model in the study period?
The model used for this study is not a new development. The model has been used for a couple of Arctic climate studies in the past, and its skill to simulate sea ice has been evaluated by Dorn et al. (2019, https://doi.org/10.3390/atmos10080431) and Yu et al. (2020, https://doi.org/10.5194/tc-14-1727-2020). The model was recently also applied to the MOSAiC period by Aue et al. (2023, https://doi.org/10.3389/feart.2023.1112467). They found that the model is able to capture the synoptic situation and produce a realistic spatial pattern of sea-ice concentration changes. It should be noted that the two simulations shown in the manuscript use the same nudging procedure to ERA5 as the simulation by Aue et al. (2023). This nudging suppresses internal model variability and is applied to reproduce the observed synopic and large-scale atmospheric conditions (as already mentioned in lines 50-53). Therefore, the skill of the model simulations with respect to the atmospheric circulation can be considered as high.
Nevertheless, even with virtually correct atmospheric conditions, sea ice may develop in an unrealistic way, depending on uncertainties in various parameterizations that affect the sea ice in different ways. Some of these uncertainties may be significant, others rather insignificant. As demonstrated in the manuscript, one of the significant parameterizations is the parameterization of the snow albedo. Other parameterizations are not subject of the present study. It is important to note that we don't claim that a cloud-dependent snow albedo parameterization leads to realistic sea ice in the model, we don't even claim that the consideration of a cloud-dependent snow albedo parameterization leads to an improved simulation of sea ice in the model, since we know about potential counteracting effects of uncertainties in other parameterizations. Above all things, we don't claim that our model is closer to reality or even better than others. In the revised version of the manuscript, we will expand on the improvements in the sea-ice simulation (in our model) and will discuss the improvements in the context of the above argumentation.
Response to the Minor Concerns
1. Manuscript structure:
The manuscript was initially designed as "brief communication" in The Cryosphere, but turned out in the end to be a little too long for this manuscript category. Due to the design of the manuscript as brief communication, the manuscript is concise and a lengthy discussion of the results has been omitted. We will discuss the results in greater detail in the revised version of the manuscript. However, we disagree that key methodological details are missing. Information that we rated as being not absolutely necessary has indeed been omitted, but all relevant information on the changes in the albedo parameterization and on the experimental design is given. For more details on the albedo parameterization or on the model as a whole as well as on the observational data, there are references to the respective papers. Nonetheless, we think it might be helpful to see the underlying equations, since there are misinterpretations of the changes in the albedo parameterization with respect to the temperature dependence. We will show these equations in the revised version of the manuscript.
2. Open data:
The model data were solely produced for the current sensitivity study and will very likely not be used beyond that, neither by us nor by anybody else. The huge effort of a data publication with DOI is therefore not justifiable. The provision of model data via Swift has proven to be fast and simple for everybody. Nevertheless, we will think about enabling to access the model data under a persistent weblink at DKRZ. The section "Code availability" is missing indeed. We will add a corresponding section to the manuscript.
3. Ice types:
The new snow albedo parameterization was derived by Jäkel et al. (2019, https://doi.org/10.5194/tc-13-1695-2019) from measurements during the ACLOUD/PASCAL campaigns. The primary ice type during these campaigns was mostly first-year ice of varying thickness (Nicolaus, 2018, https://doi.org/10.1594/PANGAEA.889264). The results of the present study show that the new snow albedo parameterization also leads to improvements over second-year ice. It should be noted that there is no distinction of ice types in the model. The sea ice in a model grid cell usually represents a conglomerate of first-year and multi-year ice with different surface characteristics. The parameterization needs to reproduce the mean effect of all these characteristics. Different temperature dependence of the albedo of different surfaces is certainly relevant for the overall performance of the albedo parameterization, but not relevant for the present study which emphasizes the importance of the cloud dependence.
4. Figure 3: ("it seems like, if this pattern continues, the difference in SIV might continue to increase?")
It is right that the new albedo parameterization ends up in a new equilibrium state with thinner sea ice and less SIV. We will demonstrate this in the revised version of the manuscript using the new long-term sensitivity simulations.
5. Internal variability:
Since the two simulations use identical initial conditions and identical boundary forcing, the differences between the two simulations are only a response to the changed albedo parameterization. If we had used different initial conditions in the two simulations, we would have seen a superimposing effect of internal model variability. This effect may potentially be as large as or even larger than the signal due to the changed albedo parameterization. The role of internal model variability in the simulation of Arctic sea-ice extent and volume was already demonstrated by Dorn et al. (2012, https://doi.org/10.5194/tc-6-985-2012). With the identical setup used here for the two simulations, however, internal variability can be completely excluded as reason for the differences. We will clarify this point in the revised version of the manuscript. With respect to the sensitivity of SIE/SIV to small changes in the initial conditions we will quantify the signal-to-noise ratio by calculating the "signal" from the mean difference between the new long-term sensitivity simulations and the "noise" from the ensemble standard deviation of a 10-member ensemble of simulations with the new albedo parameterization, which will be finished soon.
6. Sea ice initialisation:
Sea ice and ocean were initialized with fields from January 1, 2019, 00 UTC of an earlier long-term simulation. Indeed, this information is missing in the manuscript and will be added in the revised version. To demonstrate that the response of the sea ice to the changed albedo parameterization does not significantly depend on the sea ice initialization, we will repeat the sensitivity experiment using initial data from the ORAS5 reanalysis. The sea ice evolution in the four simulations will then be compared with available observations and reanalysis data such as ORAS5 and PIOMAS.
7. Comparison with MOSAiC data: ("I found the comparison of the model parametrization with MOSAiC data slightly odd")
The suggested first step, to test the parametrization by calculating the albedo with the in-situ observed snow temperature and cloud covers, was already done by Jäkel et al. (2019, https://doi.org/10.5194/tc-13-1695-2019) in the course of the parameter adjustment and was recently also applied to the complete albedo parameterization and to other data sets from different years and seasons by Jäkel et al. (2023, https://doi.org/10.5194/egusphere-2023-1337). We will refer to these papers in the revised version of the manuscript. In the present paper, we take the second step, evaluating the albedo parameterization in fully coupled model simulations, and above all, we demonstrate how important it is (or could be in other models) to consider a cloud dependence in the snow albedo parameterization of a coupled model system. The latter is the main purpose of the manuscript. We will keep our focus on this purpose and will substantiate our findings in the revised version by adding the aforementioned new simulations.
Citation: https://doi.org/10.5194/egusphere-2023-634-AC1
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AC1: 'Reply on RC1', Wolfgang Dorn, 24 Nov 2023
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RC2: 'Comment on egusphere-2023-634', Anonymous Referee #2, 05 Oct 2023
Dear Authors
Your paper 'On the importance to consider the cloud dependence in parameterizing the albedo of snow on sea ice' has been carefully reviewed to provide my first round of comments. The paper compared snow albedo model parametrization in a RCM against MOSAiC Arctic data and shows correlation. Here are some major comments (for the first round) followed by my suggested decision for this round.
-- Although the paper shows promise towards better understanding of how temprature affects albedo, I find the analysis incomplete especially with how the analysis is generalized just from one year of data from MOSAiC.
-- Also, with the amount of meteorological parameters collected during MOSAiC, why is only temperature and clouds, the only two parameters that are being investigated? Aren't there other met and geophysical parameters that affect albedo?
-- One of my concerns is that, the paper idealizes data from MOSAiC as representative at pan-Arctic scales, but I feel that a more exhaustive analysis from different Arctic sectors need to be incorporated to generalize your findings at a pan-Arctic scale.
Although my comments are short now, I think the authors need to address/defend my comments before I can work on specific comments in my second round of edits.
The paper of course shows promise and require major revisions based on my comments before it can be published in TC.
Citation: https://doi.org/10.5194/egusphere-2023-634-RC2 -
AC2: 'Reply on RC2', Wolfgang Dorn, 24 Nov 2023
We thank Referee #2 for the time and effort he/she spent reading the manuscript and providing some major comments. Referee #2 noted a few times that there will be a second round with specific comments, but it remains unclear what he/she actually expects. Specific suggestions as to how we can or should improve the manuscript are missing. The following response to the major comments is therefore more what we think might help to improve the manuscript.
Response to the major comments
-- Although the paper shows promise towards better understanding of how temprature affects albedo, I find the analysis incomplete especially with how the analysis is generalized just from one year of data from MOSAiC.
The temperature effect on the albedo is not the topic of the present study. The study only concentrates on the cloud dependence of the snow albedo. Although the albedo values for cold, dry snow and warm, wet snow were modified, they were basically only separately defined for overcast and non-overcast conditions. When averaging the albedo for overcast and non-overcast conditions relative to the frequency of the conditions, the albedo values are almost equal in the two parameterizations. Changes in the temperature dependence take only effect in conjunction with the cloud dependence. All differences between the model simulations can thus be considered as a consequence of the additionally introduced cloud dependence. We will clarify this point in the revised version of the manuscript. Furthermore, the analysis of the effects of a cloud-dependent snow albedo parameterization on the sea ice will be expanded in the revised version of the manuscript to corresponding long-term sensitivity simulations for the period 1979-2021 which have recently been completed.
-- Also, with the amount of meteorological parameters collected during MOSAiC, why is only temperature and clouds, the only two parameters that are being investigated? Aren't there other met and geophysical parameters that affect albedo?
As aforementioned, the study only concentrates on the cloud dependence of the snow albedo. Temperature effects are present in both parameterizations and can not be evaluated separately without further sensitivity experiments in which the temperature dependence of the albedo is independent from the cloud dependence. There are certainly other parameters that affect the snow albedo, as for instance black carbon deposits, the solar zenith angle, or snow age and depth, but such dependences are not included in the present snow albedo parameterization. Therefore, there is little point in evaluating the albedo against corresponding MOSAiC data.
-- One of my concerns is that, the paper idealizes data from MOSAiC as representative at pan-Arctic scales, but I feel that a more exhaustive analysis from different Arctic sectors need to be incorporated to generalize your findings at a pan-Arctic scale.
The new parameterization was derived from observations north of Svalbard in May/June 2017 and is in the present paper evaluated against independent data obtained from observations in the central Arctic in 2020. This is the regular procedure, detecting a physical principle from one data set and evaluating it against an independent other data set. Unfortunately, there are not many observations from the central Arctic against which the new parameterization can be evaluated. A more exhaustive evaluation of the complete albedo parameterization was recently made by Jäkel et al. (2023, https://doi.org/10.5194/egusphere-2023-1337). They evaluated the parameterization in offline and online application also against other Arctic data sets from different years and seasons. We will refer to this paper in the revised version of the manuscript. Beyond that, the generalization of our findings is valid as long as there is no reason that indicates the contrary. The theory that the cloud dependence of the snow albedo holds true for the entire Arctic can be tested by others and conceivably proven false (known as the Falsification Principle). The latter is not our task. Our task is to support our theory by solid arguments. We will expand on these arguments in the conclusions of the revised version of the manuscript.
Citation: https://doi.org/10.5194/egusphere-2023-634-AC2
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AC2: 'Reply on RC2', Wolfgang Dorn, 24 Nov 2023
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2023-634', Anonymous Referee #1, 09 May 2023
Synopsis
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.
Major Concerns
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?
Minor Concerns
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.
Citation: https://doi.org/10.5194/egusphere-2023-634-RC1 -
AC1: 'Reply on RC1', Wolfgang Dorn, 24 Nov 2023
We thank Referee #1 for the time and effort he/she spent reading the manuscript and providing extensive comments. We also appreciate the enormous number of potential suggestions for improvements and further investigations. Since some of these suggestions go far beyond the purpose of what we actually have intended to demonstrate, we realize the need to explain the purpose in more detail.
The main purpose is to demonstrate that the consideration of a simple cloud dependence in the here applied broadband albedo parameterization is able to mimic the cloud effect on snow surface albedo reasonably. This means that it is not absolutely necessary to switch to a physically more consistent, but also computationally more complex waveband-dependent albedo parameterization, which implicitly would include a cloud effect on the albedo. The second and main purpose is to demonstrate that this rather minor modification of the snow albedo parameterization has a significant impact on the sea ice in a coupled model system due to its influence on the positive surface albedo feedback. We will better emphasize these two points in the revised version of the manuscript.
It has never been the purpose to demonstrate that the sea-ice simulation is closer to reality by considering a cloud dependence in the albedo parameterization. Even though this is actually the case in our model simulations, we had decided to exclude praising our own model, since we aware that the grade of sea ice in a coupled model depends on many parameterizations, not only on the albedo parameterization. Some of these parameterizations are usually subject of a kind of tuning to obtain more realistic sea ice in the model as for instance discussed by Mauritsen et al. (2012, https://doi.org/10.1029/2012MS000154). Therefore, it doesn't mean much whether the modeled sea ice is better or worse than before as long as tuning of parameters in other process descriptions, which are not well established by observations, were applied to counteract the biases of a previously more unrealistic albedo parameterization. In particular, it doesn't disqualify the added value of considering the cloud dependence in parameterizing the snow albedo.
Response to the Major Concerns
1. Interannual Variability of the Pan-Arctic Findings
Corresponding long-term sensitivity simulations for the period 1979-2021 have recently been completed and will be discussed in the revised version of the manuscript. These simulations were running without nudging to ERA5 data, meaning that the model is allowed to diverge from the observed atmospheric circulation so that internal variability becomes more relevant.
2. Separability of Cloud and Temperature Dependence
The new snow albedo parameterization basically uses the same temperature dependence as the original snow albedo parameterization, only the values of the parameters are separately defined for overcast and non-overcast conditions. When averaging the albedo for overcast and non-overcast conditions relative to the frequency of the conditions, the albedo values are almost equal in the two parameterizations. This means that changes in the temperature dependence effectively depend on the cloud dependence. There is no cloud-independent temperature dependence which one might evaluate without further sensitivity experiments. In the current sensitivity experiment, all differences between the model simulations can be considered as a consequence of the additionally introduced cloud dependence. We will clarify this point in the revised version of the manuscript.
3. How skillful is this model in the study period?
The model used for this study is not a new development. The model has been used for a couple of Arctic climate studies in the past, and its skill to simulate sea ice has been evaluated by Dorn et al. (2019, https://doi.org/10.3390/atmos10080431) and Yu et al. (2020, https://doi.org/10.5194/tc-14-1727-2020). The model was recently also applied to the MOSAiC period by Aue et al. (2023, https://doi.org/10.3389/feart.2023.1112467). They found that the model is able to capture the synoptic situation and produce a realistic spatial pattern of sea-ice concentration changes. It should be noted that the two simulations shown in the manuscript use the same nudging procedure to ERA5 as the simulation by Aue et al. (2023). This nudging suppresses internal model variability and is applied to reproduce the observed synopic and large-scale atmospheric conditions (as already mentioned in lines 50-53). Therefore, the skill of the model simulations with respect to the atmospheric circulation can be considered as high.
Nevertheless, even with virtually correct atmospheric conditions, sea ice may develop in an unrealistic way, depending on uncertainties in various parameterizations that affect the sea ice in different ways. Some of these uncertainties may be significant, others rather insignificant. As demonstrated in the manuscript, one of the significant parameterizations is the parameterization of the snow albedo. Other parameterizations are not subject of the present study. It is important to note that we don't claim that a cloud-dependent snow albedo parameterization leads to realistic sea ice in the model, we don't even claim that the consideration of a cloud-dependent snow albedo parameterization leads to an improved simulation of sea ice in the model, since we know about potential counteracting effects of uncertainties in other parameterizations. Above all things, we don't claim that our model is closer to reality or even better than others. In the revised version of the manuscript, we will expand on the improvements in the sea-ice simulation (in our model) and will discuss the improvements in the context of the above argumentation.
Response to the Minor Concerns
1. Manuscript structure:
The manuscript was initially designed as "brief communication" in The Cryosphere, but turned out in the end to be a little too long for this manuscript category. Due to the design of the manuscript as brief communication, the manuscript is concise and a lengthy discussion of the results has been omitted. We will discuss the results in greater detail in the revised version of the manuscript. However, we disagree that key methodological details are missing. Information that we rated as being not absolutely necessary has indeed been omitted, but all relevant information on the changes in the albedo parameterization and on the experimental design is given. For more details on the albedo parameterization or on the model as a whole as well as on the observational data, there are references to the respective papers. Nonetheless, we think it might be helpful to see the underlying equations, since there are misinterpretations of the changes in the albedo parameterization with respect to the temperature dependence. We will show these equations in the revised version of the manuscript.
2. Open data:
The model data were solely produced for the current sensitivity study and will very likely not be used beyond that, neither by us nor by anybody else. The huge effort of a data publication with DOI is therefore not justifiable. The provision of model data via Swift has proven to be fast and simple for everybody. Nevertheless, we will think about enabling to access the model data under a persistent weblink at DKRZ. The section "Code availability" is missing indeed. We will add a corresponding section to the manuscript.
3. Ice types:
The new snow albedo parameterization was derived by Jäkel et al. (2019, https://doi.org/10.5194/tc-13-1695-2019) from measurements during the ACLOUD/PASCAL campaigns. The primary ice type during these campaigns was mostly first-year ice of varying thickness (Nicolaus, 2018, https://doi.org/10.1594/PANGAEA.889264). The results of the present study show that the new snow albedo parameterization also leads to improvements over second-year ice. It should be noted that there is no distinction of ice types in the model. The sea ice in a model grid cell usually represents a conglomerate of first-year and multi-year ice with different surface characteristics. The parameterization needs to reproduce the mean effect of all these characteristics. Different temperature dependence of the albedo of different surfaces is certainly relevant for the overall performance of the albedo parameterization, but not relevant for the present study which emphasizes the importance of the cloud dependence.
4. Figure 3: ("it seems like, if this pattern continues, the difference in SIV might continue to increase?")
It is right that the new albedo parameterization ends up in a new equilibrium state with thinner sea ice and less SIV. We will demonstrate this in the revised version of the manuscript using the new long-term sensitivity simulations.
5. Internal variability:
Since the two simulations use identical initial conditions and identical boundary forcing, the differences between the two simulations are only a response to the changed albedo parameterization. If we had used different initial conditions in the two simulations, we would have seen a superimposing effect of internal model variability. This effect may potentially be as large as or even larger than the signal due to the changed albedo parameterization. The role of internal model variability in the simulation of Arctic sea-ice extent and volume was already demonstrated by Dorn et al. (2012, https://doi.org/10.5194/tc-6-985-2012). With the identical setup used here for the two simulations, however, internal variability can be completely excluded as reason for the differences. We will clarify this point in the revised version of the manuscript. With respect to the sensitivity of SIE/SIV to small changes in the initial conditions we will quantify the signal-to-noise ratio by calculating the "signal" from the mean difference between the new long-term sensitivity simulations and the "noise" from the ensemble standard deviation of a 10-member ensemble of simulations with the new albedo parameterization, which will be finished soon.
6. Sea ice initialisation:
Sea ice and ocean were initialized with fields from January 1, 2019, 00 UTC of an earlier long-term simulation. Indeed, this information is missing in the manuscript and will be added in the revised version. To demonstrate that the response of the sea ice to the changed albedo parameterization does not significantly depend on the sea ice initialization, we will repeat the sensitivity experiment using initial data from the ORAS5 reanalysis. The sea ice evolution in the four simulations will then be compared with available observations and reanalysis data such as ORAS5 and PIOMAS.
7. Comparison with MOSAiC data: ("I found the comparison of the model parametrization with MOSAiC data slightly odd")
The suggested first step, to test the parametrization by calculating the albedo with the in-situ observed snow temperature and cloud covers, was already done by Jäkel et al. (2019, https://doi.org/10.5194/tc-13-1695-2019) in the course of the parameter adjustment and was recently also applied to the complete albedo parameterization and to other data sets from different years and seasons by Jäkel et al. (2023, https://doi.org/10.5194/egusphere-2023-1337). We will refer to these papers in the revised version of the manuscript. In the present paper, we take the second step, evaluating the albedo parameterization in fully coupled model simulations, and above all, we demonstrate how important it is (or could be in other models) to consider a cloud dependence in the snow albedo parameterization of a coupled model system. The latter is the main purpose of the manuscript. We will keep our focus on this purpose and will substantiate our findings in the revised version by adding the aforementioned new simulations.
Citation: https://doi.org/10.5194/egusphere-2023-634-AC1
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AC1: 'Reply on RC1', Wolfgang Dorn, 24 Nov 2023
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RC2: 'Comment on egusphere-2023-634', Anonymous Referee #2, 05 Oct 2023
Dear Authors
Your paper 'On the importance to consider the cloud dependence in parameterizing the albedo of snow on sea ice' has been carefully reviewed to provide my first round of comments. The paper compared snow albedo model parametrization in a RCM against MOSAiC Arctic data and shows correlation. Here are some major comments (for the first round) followed by my suggested decision for this round.
-- Although the paper shows promise towards better understanding of how temprature affects albedo, I find the analysis incomplete especially with how the analysis is generalized just from one year of data from MOSAiC.
-- Also, with the amount of meteorological parameters collected during MOSAiC, why is only temperature and clouds, the only two parameters that are being investigated? Aren't there other met and geophysical parameters that affect albedo?
-- One of my concerns is that, the paper idealizes data from MOSAiC as representative at pan-Arctic scales, but I feel that a more exhaustive analysis from different Arctic sectors need to be incorporated to generalize your findings at a pan-Arctic scale.
Although my comments are short now, I think the authors need to address/defend my comments before I can work on specific comments in my second round of edits.
The paper of course shows promise and require major revisions based on my comments before it can be published in TC.
Citation: https://doi.org/10.5194/egusphere-2023-634-RC2 -
AC2: 'Reply on RC2', Wolfgang Dorn, 24 Nov 2023
We thank Referee #2 for the time and effort he/she spent reading the manuscript and providing some major comments. Referee #2 noted a few times that there will be a second round with specific comments, but it remains unclear what he/she actually expects. Specific suggestions as to how we can or should improve the manuscript are missing. The following response to the major comments is therefore more what we think might help to improve the manuscript.
Response to the major comments
-- Although the paper shows promise towards better understanding of how temprature affects albedo, I find the analysis incomplete especially with how the analysis is generalized just from one year of data from MOSAiC.
The temperature effect on the albedo is not the topic of the present study. The study only concentrates on the cloud dependence of the snow albedo. Although the albedo values for cold, dry snow and warm, wet snow were modified, they were basically only separately defined for overcast and non-overcast conditions. When averaging the albedo for overcast and non-overcast conditions relative to the frequency of the conditions, the albedo values are almost equal in the two parameterizations. Changes in the temperature dependence take only effect in conjunction with the cloud dependence. All differences between the model simulations can thus be considered as a consequence of the additionally introduced cloud dependence. We will clarify this point in the revised version of the manuscript. Furthermore, the analysis of the effects of a cloud-dependent snow albedo parameterization on the sea ice will be expanded in the revised version of the manuscript to corresponding long-term sensitivity simulations for the period 1979-2021 which have recently been completed.
-- Also, with the amount of meteorological parameters collected during MOSAiC, why is only temperature and clouds, the only two parameters that are being investigated? Aren't there other met and geophysical parameters that affect albedo?
As aforementioned, the study only concentrates on the cloud dependence of the snow albedo. Temperature effects are present in both parameterizations and can not be evaluated separately without further sensitivity experiments in which the temperature dependence of the albedo is independent from the cloud dependence. There are certainly other parameters that affect the snow albedo, as for instance black carbon deposits, the solar zenith angle, or snow age and depth, but such dependences are not included in the present snow albedo parameterization. Therefore, there is little point in evaluating the albedo against corresponding MOSAiC data.
-- One of my concerns is that, the paper idealizes data from MOSAiC as representative at pan-Arctic scales, but I feel that a more exhaustive analysis from different Arctic sectors need to be incorporated to generalize your findings at a pan-Arctic scale.
The new parameterization was derived from observations north of Svalbard in May/June 2017 and is in the present paper evaluated against independent data obtained from observations in the central Arctic in 2020. This is the regular procedure, detecting a physical principle from one data set and evaluating it against an independent other data set. Unfortunately, there are not many observations from the central Arctic against which the new parameterization can be evaluated. A more exhaustive evaluation of the complete albedo parameterization was recently made by Jäkel et al. (2023, https://doi.org/10.5194/egusphere-2023-1337). They evaluated the parameterization in offline and online application also against other Arctic data sets from different years and seasons. We will refer to this paper in the revised version of the manuscript. Beyond that, the generalization of our findings is valid as long as there is no reason that indicates the contrary. The theory that the cloud dependence of the snow albedo holds true for the entire Arctic can be tested by others and conceivably proven false (known as the Falsification Principle). The latter is not our task. Our task is to support our theory by solid arguments. We will expand on these arguments in the conclusions of the revised version of the manuscript.
Citation: https://doi.org/10.5194/egusphere-2023-634-AC2
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AC2: 'Reply on RC2', Wolfgang Dorn, 24 Nov 2023
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