I previously provided a detailed review of the initial submission of this paper. Unfortunately, in their resubmission, the authors have not adequately addressed serious issues with the work. Below I have given feedback on the authors' responses to the main comments from the previous review. Since the main points have not been well addressed I have not gone through the responses to the detailed specific comments.
From initial review: "(1) It is unclear what is novel about this work. The conclusion states that the authors' use of a variable drag formulation is unique. However, Tsamados et al. (2014) previously incorporated a variable atmospheric and oceanic form drag into the CICE model. The paper has been cited by the authors, but they do not describe how their implementation of this method is related to any of their results. At the most basic level, the authors should show results with and without this formulation.
The statement that other centres do not provide details of parameters other than ice concentration or thickness is inaccurate, particularly as many of those centres are also using the same CICE model as the authors, with the same available parameters. The main conclusion of the results seems to be that assimilating observations brings the model output closer to reference observations, which is not a new result. Perhaps the differences in results when using thin ice of < 60 cm compared to < 30 cm might be an interesting angle, but this is not explored."
Authors' response: "The authors would like to thank the reviewer for the comments and suggestions.
It is true Tsamados et al. (2014) has incorporated a variable atmospheric and oceanic form drag into the CICE model, but have not been used with a data assimilated model that produced parameters such as freeboard, sail, keel measurements. The forecast centers are using CICE model a constant variable drag formulation. Moreover, the used models are coupled with ocean models."
New review comment: "This does not adequately address the comment that the authors have not demonstrated that any of their results are related to the variable atmospheric and oceanic form drag. Other comments have not been addressed."
From initial review: "(2) The statements throughout the paper, that the model fits the validation observations well, are not backed up by the results themselves. Although the assimilation improves results, there remain clear systematic differences between the model output and the reference observations."
Authors' response: "The study estimates the bias observed over years and will use it for further tuning of the model."
New review comment: "This does not address the statements in the paper that the model fits the validation observations well."
From initial review: "(3) There are many omissions in explanation of methods, several contradictions in the text, confusing wording, and the paper is missing references to current literature and relevant similar systems, e.g. TOPAZ, RIPS/RIOPS, ACNFS. Also missing is a description of how the authors' system differs and improves on these, and indeed what the purpose of the new system is. A number of the citations given are conference papers or otherwise unpublished works, which are not peer-reviewed and should not form a significant basis of citations."
Authors' response: "The assimilation and tuning of the model is still an ongoing work and will be compared with RIPS and other models in the future. Moreover, the cited conference papers include the developments of RIPS. The novelty of the manuscript is the regional implementation of the uncoupled model."
New review comment: "This particular comment was not a suggestion to quantitatively compare results with other systems, but to describe the purpose of the authors' system and how it fits in with (and enhances) current work."
General comments
From initial review: "The relevance of how this work fits in with the published literature needs to be discussed, along with other regional modelling systems. How do the results compare to e.g. coupled ocean-ice systems?"
Authors' response: "The coupled ice-ocean systems are more complex and require additional tuning of ocean parameters. The purpose of the study was to go without an ocean model using a mixed layer parametrization and data assimilation to produce the best results. Coupling would require extensive work and is out of the scope of the current work."
New review comment: "This was not a suggestion to do this work, but to compare your results with those already available in the literature."
From initial review: "What is the benefit of only using an SST parametrization? Is this system to be used for operational or research purposes? A large number of the references used in this paper are unpublished or non peer-reviewed works including conference papers. A more complete discussion of the peer-reviewed literature is necessary."
Authors' response: "Please note that the SST parametrization was discussed earlier in Parasad et al. (2015). Similar to RIPS 2016 the model used the same density parametrization but with a different criteria for forwarding the slab ocean model parametrization."
New review comment: "This does not address the need to include a more complete discussion of the peer-reviewed literature, or to add information on the purpose of the system."
From initial review: "The paper needs more information on all the input and validation data sets, including descriptions and data access information. The authors also need to ensure that all the datasets used are properly cited."
Authors' response: "All the input and validation data sets had been described and properly cited."
New review comment: "Do you mean this has now been updated? This was not in the first draft of the paper."
From initial review: "Why is the assimilation system set up to weight heavily in favour of the model rather than giving equal weight to the observations?"
Authors' response: "The assimilation followed work of Lindsay et al. Further tuning of the model physics and assimilation schemes have to be done to better understand the model behavior. The system is actually weighted heavily in marginal ice zones where significant bias can occur."
New review comment: "This doesn't actually answer the question on why it was set up this way."
From initial review: "The paper repeatedly states that AVHRR data was assimilated. Actually, it looks like the authors are assimilating the AVHRR-only OISST analysis product, which although based on observations, is an analysis product. This needs to be made clear, along with information on the temporal resolution, timeliness etc of the product. Additionally, this product uses SSM/I and SSMIS information to create proxy SST observations for assimilation at high latitudes. This means the SST observations also include input from ice concentration data. Therefore, they are not independent from the SSM/I and SSMIS data being used for validation."
Authors' response: "Yes, SST used an analysis product since model is assimilated over its domain including at ice edges where ice concentration has lower values. It was clarified in the paper that AVHRR-only OISST analysis product uses ice information to retrieve SST only for regions where ice concentration is greater than 0.5. The following sentence has been included for clarity " The analysis product estimates SST from ice concentration only in regions where ice concentration is greater than 50%, otherwise uses satellite data to retrieve SST values."
New review comment: "This additional sentence only partly addresses the points raised in the comments."
From initial review: "More detail and justification of which thickness ranges of SMOS and CryoSat-2 observations are being used is needed."
Authors' response: "The justification has been provided in the paper "Also, it is strictly recommended not to use the SMOS data with an uncertainty greater than one meter (Tian-Kunze and Kaleschke, 2016) for practical applications." This has been clearly stated in the user manual of the SMOS product. For Cryostat-2 freeboard measures had been used for comparison. Since thickness estimates of CryoSat 2 is derived from freeboard estimates we think that it would be best to compare freeboad estimates with Cryosat-2 instead of thickness estimates."
New review comment: "Data provided by CryoSat-2 and SMOS have very different characteristics. Using the uncertainty to reject SMOS data is a reasonable method, but what range of thickness data does that mean you are using? What about CryoSat-2 data? The point still stands even if you are using freeboard rather than thickness. There is a lot of information available in the literature. Different users make different decisions on what data to accept or reject, but justification of the decisions is necessary."
From initial review: "What real benefit is the assimilation giving? Figures 5-7 show that it brings the model closer to the observations, but it still deviates and all modelled ice thickness is too high. It is not convincing to state that the M2 model has good correspondence with the observations due to being in the uncertainty range, as even the free-running model is also managing that most of the time. Assimilating SST in addition to sea ice concentration produces better results, but few if any operational centres will not already be assimilating ice concentration and not SST observations."
Authors' response: "All modeling centres assimilate SST in Ocean model and passe the information to sea ice model. Here, we state that if we use analysis product of SST in the ice model itself it produces better results."
New review comment: "In order to make that statement, a quantitative comparison needs to be given in the paper. No evidence for this is provided."
Authors' response: "Moreover, operational centers give information on ice concentration but ice thickness significant biases are observed also, other information such as ridge height, keel depth, freeboard data are rarely discussed."
New review comment: "Are you planning to make this information available operationally? If so, should be stated in the paper."
From initial review: "The authors acknowledge that the assimilation is not optimized. If changing the value of alpha or adjusting the nudging timescale is expected to improve results, why has this not been done? Similarly for the relationship between ridge and keel."
Authors' response: "This is a parameter sensitivity study and is an ongoing work."
New review comment: "If key work is still ongoing, it needs to be considered if the work is in a position for publication."
No author response given to any of the following comments from initial review: "The authors need to also include RMS (or standard deviation) statistics, as well as mean difference when discussing how well models match validation observations.
For figures 5,6,7 the modelled ice is too thick for all model runs after January. Although results for the M2 model are closer to observations than the M0 or M1 models, results are still not very good, which is not mentioned in the paper. In general throughout the paper, systematic biases or errors which are large in proportion to the model variable values are not addressed, or are dismissed as being within uncertainty levels. This shows a poor understanding of the validation results.
For results where the model thickness < 30 cm (figures 9,10,11), the models seem to be underestimating ice thickness rather than overestimating. This difference to the results seen in figures 5,6,7 needs to be addressed in the paper.
For figures 9,10,11 the modelled thin ice thickness remains roughly constant from December, and also the assimilation makes little difference. Reasons for this need to be addressed in the paper." |
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