the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 21 Feb 2023
Sea ice in the Arctic Transpolar Drift in 2020/21: thermodynamic evolution of different ice types
Abstract. Sea ice properties are extremely inhomogeneous, in particular on the floe-scale. Different characteristic local features, such as melt ponds and pressure ridges, profoundly impact the thermodynamic evolution of the ice pack even in a kilometre-scale domain, and the associated processes are still not well represented in current climate models. To better characterize the freezing and melting of different types of sea ice, we deployed four sea ice mass balance buoys on an ice floe close to the North Pole during the second drift of the Multidisciplinary drifting Observatory for the Study of Arctic Climate (MOSAiC) in August 2020. The study sites included level first-year ice, an open melt pond, and an unconsolidated ridge. The floe slowly drifted southwards from October 2020 to early March 2021 but shifted to a more rapid drift from March to July 2021. This drifting pattern, together with a large snow accumulation, relatively warm air temperatures, and a rapid increase in oceanic heat close to Fram Strait, determined the seasonal evolution of the ice mass balance. Storms, accompanied by higher air temperatures and enhanced ice dynamics, were the main cause of the formation of snow ice or superimposed ice. Although the 0.24-m deep melt pond was completely refrozen by 5 September, the relatively large snow accumulation and the heat storage with the rotten ice layer delayed ice basal growth beyond the last observation at this site in mid-February 2021. At the ridge site, the macroporosity of the unconsolidated layer was estimated between 0.005 and 0.755. The freezing of internal voids also delayed the ridge basal growth, which was not observed until 26 April 2021. Thus, the refreezing of ponded ice and voids within the unconsolidated ridges amplifies the anisotropy of the heat exchange between the ice and the lower atmosphere/upper ocean. Our results provide an important physical background for further interdisciplinary studies related to the MOSAiC observations and can be used to optimize the parameterization of freezing processes related to melt ponds and ice ridges in sea ice numerical models.
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RC1: 'Comment on tc-2023-25', Anonymous Referee #1, 16 Mar 2023
The manuscript by Lei and co-authors presents a data set from ice mass balance buoys that drifted from the North Pole to Fram Strait, at a time of year where there is fairly little data in the region, this aspect makes the data set quite valuable. Given the author-list I had fairly high expectations when starting reading the manuscript, but while reading this I felt this manuscript was hastily put together, and reads more like data report that does not meet the standards of The Cryosphere.
As a reviewer I felt that this was not good use of my time when such a potluck of results are submitted, and the mansucript lacks a clear vision of what the true new results are. A fundamental issue is the lack of proper description and acknowledgement of existing work, this is very surprising given the list of authors that should be aware of much this work (and some is their own).
Thus, in its current form I cannot recommend this paper even for major revisions, because I feel it needs to be complete rewritten to meet the requirements of The Cryosphere. Therefore I only provide some major comments/suggestions here to help design this work in a way that its of value to the community. Some detailed suggestions are given in the annotated ms.
Major flaws;
1) The paper does not make an attempt to include relevant literature from the area (or subject matter) to be able to place this work in context. Ample literature exists, also from the co-authors, that needs be presented to place this work in context, before arguing for novelty, when similar work already exists. To me this is such a fundamental flaw that alone merits "rejection". I have added a list (by far not exhaustive) of papers on snow on sea ice, ocean heat flux, ice-break up and flooding, storms (warming events), and ridge thermodynamics and melt that are all relevant to place the work in proper context (see the bottom of this reply).
2) At the core of the paper is the interpretation of the temperature (and heating?) data from the SIMBA buoys. This has not been explained at any level that this can be reproduced or evaluated. The assumptions behind the interface locations are practically not described at all (was it automated, or manually done while looking at the data, or a combination). This needs to be significantly improved and documented properly, if there is a slightest chance for the reader to try and assess the quality if the work done. No unertanties are given, which in the case of e.g. estimated ocean heat fluxes are important to know. The macroporosity estimates in the ridge has such large range, that is hard to understand what the value of reporting them are?
3) Related to the above (2), one of the co-authors is an expert in thermodynamic modeling. It would strethen the paper if the modeling can support the derived fluxes and interfaces from the SIMBAs (As the authors have done in earlier papers). I find it strange that e.g. the ridge at nearly 3 m depth suddenly grows very rapidly, when there is no noticeable change in the other thinner ice, can this be only due to thicker snow on level ice? Typically ridge sails also accumulate a lot of snow, even if the crest does not. A thermodynamic model would at least be able to support/strengthen the work in my opinion.
4) I was surprised of the minimal comparison to the conditions during the first MOSAiC drift (where the same author published another paper). although not the same year, the comparison of these two regions would possibly be an aspect to include. At least I find the differentece os "low snow" and "high snow" regions along the TPD intriguing aspect. Regionality in the Arctic is often overlooked.
5) Generally the motivation for this work and conlusions are a potluck of things and very vague. It simply lacks a clear statement of what is actually the value of this work and primary motivation. What new is presented that would truly change the way sea ice is modeled? Abstract mentions aspects I do not necessarily see in the paper itself, or are extrapolated beyond what I believe can be exploited from the data at hand. I think a complete rewrite of manuscript with clear idea of what are truly the novel aspects of this work would help to pin down the emphasis, and possibly bring the ms to the standards that need to be met to publish in TC.
******************************
There is now ample literature from this area with thicker snow, and the effect of this thicker snow on the sea ice. These works needs to referred to place this work better in context, earlier observations have in fact already observed similar episodes where thick snow, winter storms (warming events) have ample effects on the sea ice. Same goes with some observations of ridge thermodynamics. There is also work on observations of ocean heat fluxes (directly and indirectly) that should be compared to. I am also suprised the work in the exact same area with ice mass balance buoys and ocean heat fluxes from one of co-authors (Perovich) are not referred or comapred to as far as I can see.
To me this is quite a breach of good practice, not to acknowledge earlier work properly, and claiming novelty. This work needs to do much better job to refer to earlier work, and place this work better in context before making claims of novelty.
I propose that the authors read up on the literature that exists (especially in the study region), and this can help place the current observations in historical context (has things changed since the 1980s?, was this winter "normal" in terms of storms (warming events), similar effect of the thick snow, how did it compare to the first mosaic drift etc.):
Perovich, D. K., Tucker, W. B., & Krishfield, R. A. (1989). Oceanic heat flux in the Fram Strait measured by a drifting buoy. Geophysical Research Letters, 16(9), 995–998. https://doi.org/10.1029/GL016i009p00995
Perovich, D., Richter-Menge, J., Polashenski, C., Elder, B., Arbetter, T., & Brennick, O. (2014). Sea ice mass balance observations from the North Pole Environmental Observatory. Geophysical Research Letters, 41(6), 2019–2025. https://doi.org/10.1002/2014GL059356
Wang, C., et al.(2016). Atmospheric conditions in the central Arctic Ocean through the melt seasons of 2012 and 2013: Impact on surface conditions and solar energy deposition into the ice-ocean system. Journal of Geophysical Research: Atmospheres, 121(3), 1043–1058. https://doi.org/10.1002/2015JD023712
Meyer, A., Fer, I., Sundfjord, A., & Peterson, A. K. (2017). Mixing rates and vertical heat fluxes north of Svalbard from Arctic winter to spring. Journal of Geophysical Research: Oceans, 122(6), 4569–4586. https://doi.org/10.1002/2016JC012441
Peterson, A. K., Fer, I., McPhee, M. G., & Randelhoff, A. (2017). Turbulent heat and momentum fluxes in the upper ocean under Arctic sea ice. Journal of Geophysical Research: Oceans, 122(2), 1439–1456. https://doi.org/10.1002/2016JC012283
Merkouriadi, I., et al. (2017). Winter snow conditions on Arctic sea ice north of Svalbard during the Norwegian young sea ICE (N-ICE2015) expedition. Journal of Geophysical Research: Atmospheres, 122(20), 10,837-10,854. https://doi.org/10.1002/2017JD026753
Merkouriadi, I., et al. (2017). Critical Role of Snow on Sea Ice Growth in the Atlantic Sector of the Arctic Ocean. Geophysical Research Letters, 44(20), 10,479-10,485. https://doi.org/10.1002/2017GL075494
Provost, C., et al. (2017). Observations of flooding and snow-ice formation in a thinner Arctic sea-ice regime during the N-ICE2015 campaign: Influence of basal ice melt and storms. Journal of Geophysical Research: Oceans, 122(9), 7115–7134. https://doi.org/10.1002/2016JC012011
Rösel, A., et al. (2018). Thin Sea Ice, Thick Snow, and Widespread Negative Freeboard Observed During N-ICE2015 North of Svalbard. Journal of Geophysical Research: Oceans, 123(2), 1156–1176. https://doi.org/10.1002/2017JC012865
Batrak, Y., & Müller, M. (2019). On the warm bias in atmospheric reanalyses induced by the missing snow over Arctic sea-ice. Nature Communications, 10(1). https://doi.org/10.1038/s41467-019-11975-3
Graham, R. M., et al. (2019). Winter storms accelerate the demise of sea ice in the Atlantic sector of the Arctic Ocean. Scientific Reports, 9(1), 9222. https://doi.org/10.1038/s41598-019-45574-5
Merkouriadi, I., et al. (2020). Effect of frequent winter warming events (storms) and snow on sea-ice growth – a case from the Atlantic sector of the Arctic Ocean during the N-ICE2015 campaign. Annals of Glaciology, 61(82), 164–170. https://doi.org/10.1017/aog.2020.25There are also relevant earlier work on ridges, this includes e.g.
Shestov, A., Høyland, K., & Ervik, Å. (2018). Decay phase thermodynamics of ice ridges in the Arctic Ocean. Cold Regions Science and Technology, 152(April), 23–34. https://doi.org/10.1016/j.coldregions.2018.04.005
Amundrud, T. L., Melling, H., Ingram, R. G., & Allen, S. E. (2006). The effect of structural porosity on the ablation of sea ice ridges. Journal of Geophysical Research: Oceans, 111(6), 1–14. https://doi.org/10.1029/2005JC002895
Shestov, A., & Ervik, Å. (2016). Studies of Drifting Ice Ridges in the Arctic Ocean during May-June 2015. Part II. Thermodynamic properties and melting rate. In 23rd IAHR International Symposium on Ice. Ann Arbor, Michigan.-
AC1: 'Reply on RC1', Ruibo Lei, 07 Apr 2023
The comment was uploaded in the form of a supplement: https://tc.copernicus.org/preprints/tc-2023-25/tc-2023-25-AC1-supplement.pdf
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AC1: 'Reply on RC1', Ruibo Lei, 07 Apr 2023
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RC2: 'Comment on tc-2023-25', Anonymous Referee #2, 26 Jun 2023
The paper of Lei et al develops analyses of ice mass balance buoy data deployed at the end of MOSAiC field work. The paper is focused on ponded and ridged ice thermodynamics. The paper looked promising, some of the stories developed in the paper are of potential interest I reckon, however my main issue is that I found myself unable to believe in these because of the lack of rigor and precision. Because I do not see how to sort this out in any other way than reshape and rewrite, I suggest to reject the paper, and did not write an extensive review of the paper which I would view as pointless in this context. I develop below a few elements that I base this evaluation upon.
Lack of rigor in the presentation of the sources
Data sources include buoy, satellite and reanalysis data. In many instances these sources are mixed without specification of which is which. For instance, each time thickness is presented, I do not know whether the authors present satellite data or buoy data. Regarding buoy-based thickness data, I would have doubts that they are at all meaningful, since they are based on a temperature discontinuity (line 168), which is generally not equivalent to thickness. But then, Line 201-202, ice growth rate is introduced, and there is no indication of on based of which source it is calculated? Without clear identification of ice thickness retrieval method and associated detailed validation of thickness measurements, I have no confidence in the growth rate data presented in the paper.
Figure 4 is also quite ambiguous in terms of sources I found. ERA5 net surface heat flux could mean many things, and there is no single line of text in the paper describing what it means. Does that include or exclude open water fraction of grid cells ? Does that include conductive heat flux or not ? What is the source for ice thickness data presented in the figure ? Same for precipitation? Without clear specification, this figure is not informative.
Lack of rigor in the evaluation of methods
The lack of independent evaluation is a problem for the thickness retrievals based on IMB as I developed above. A similar issue arises for the retrieval of superimposed ice from IMB data. L. 169 - It seems that you use IMB signals to identify snow ice and superimposed ice. You cite Jackson et al to claim this is possible. However, there is no mention of such possibility in this paper (I checked thoroughly, and did not find anything), and you do not show any observation or evidence that one can do that. Again, I end up with no confidence on what is argued in the paper.
Originality, progress beyond state of the art
Another possible issue I see is originality, though I think that could somehow be easily fixed. I found the focus on growth and melt of ponded ice and ridged ice types potnentially interesting. This is not the first time these are investigated, and therefore I would tend to think that the intro lacks a a proper review of state of the art. I found the lack of comparison to SHEBA findings to be a major gap of the paper as it is written. In particular, Perovich et al (JGR 2003) and Perovich and Elder (GRL 2002) discuss the thermodynamic behaviour of those ice types and their findings are not summarized in the introduction. Also, studies of ridge consolidation by Marchenko and coauthors are overlooked, wheras they brought significant progress on the thermodynamics of ridges. Likewise, the Reading group has made progress on the thermodynamics of melt ponds (papers by Flocco, Feltham, ...). How does your work relates to those should probably be developed. More generally referring to model studies would be highly benefitial. All in all, I had a hard time to identify progress made in your paper, compared to what I knew before.
Formal issues
I found the introduction always at the edge of overinterpretation or improper use of references. For instance, one could think that increase in ridged ice production is established when reading line 46. There an increase in ridging is backed up by references to Weeks and Strub-Klein and Sudom, which are studies of the ridging process. However those do not back up an increase in ridging at all. There are many other examples of that sort I would say. I also found the result section is mixing results and discussion, sometimes very speculative. I also found no trace of recommendations for future work or to modelling group based on your findings.
Citation: https://doi.org/10.5194/tc-2023-25-RC2
Status: closed
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RC1: 'Comment on tc-2023-25', Anonymous Referee #1, 16 Mar 2023
The manuscript by Lei and co-authors presents a data set from ice mass balance buoys that drifted from the North Pole to Fram Strait, at a time of year where there is fairly little data in the region, this aspect makes the data set quite valuable. Given the author-list I had fairly high expectations when starting reading the manuscript, but while reading this I felt this manuscript was hastily put together, and reads more like data report that does not meet the standards of The Cryosphere.
As a reviewer I felt that this was not good use of my time when such a potluck of results are submitted, and the mansucript lacks a clear vision of what the true new results are. A fundamental issue is the lack of proper description and acknowledgement of existing work, this is very surprising given the list of authors that should be aware of much this work (and some is their own).
Thus, in its current form I cannot recommend this paper even for major revisions, because I feel it needs to be complete rewritten to meet the requirements of The Cryosphere. Therefore I only provide some major comments/suggestions here to help design this work in a way that its of value to the community. Some detailed suggestions are given in the annotated ms.
Major flaws;
1) The paper does not make an attempt to include relevant literature from the area (or subject matter) to be able to place this work in context. Ample literature exists, also from the co-authors, that needs be presented to place this work in context, before arguing for novelty, when similar work already exists. To me this is such a fundamental flaw that alone merits "rejection". I have added a list (by far not exhaustive) of papers on snow on sea ice, ocean heat flux, ice-break up and flooding, storms (warming events), and ridge thermodynamics and melt that are all relevant to place the work in proper context (see the bottom of this reply).
2) At the core of the paper is the interpretation of the temperature (and heating?) data from the SIMBA buoys. This has not been explained at any level that this can be reproduced or evaluated. The assumptions behind the interface locations are practically not described at all (was it automated, or manually done while looking at the data, or a combination). This needs to be significantly improved and documented properly, if there is a slightest chance for the reader to try and assess the quality if the work done. No unertanties are given, which in the case of e.g. estimated ocean heat fluxes are important to know. The macroporosity estimates in the ridge has such large range, that is hard to understand what the value of reporting them are?
3) Related to the above (2), one of the co-authors is an expert in thermodynamic modeling. It would strethen the paper if the modeling can support the derived fluxes and interfaces from the SIMBAs (As the authors have done in earlier papers). I find it strange that e.g. the ridge at nearly 3 m depth suddenly grows very rapidly, when there is no noticeable change in the other thinner ice, can this be only due to thicker snow on level ice? Typically ridge sails also accumulate a lot of snow, even if the crest does not. A thermodynamic model would at least be able to support/strengthen the work in my opinion.
4) I was surprised of the minimal comparison to the conditions during the first MOSAiC drift (where the same author published another paper). although not the same year, the comparison of these two regions would possibly be an aspect to include. At least I find the differentece os "low snow" and "high snow" regions along the TPD intriguing aspect. Regionality in the Arctic is often overlooked.
5) Generally the motivation for this work and conlusions are a potluck of things and very vague. It simply lacks a clear statement of what is actually the value of this work and primary motivation. What new is presented that would truly change the way sea ice is modeled? Abstract mentions aspects I do not necessarily see in the paper itself, or are extrapolated beyond what I believe can be exploited from the data at hand. I think a complete rewrite of manuscript with clear idea of what are truly the novel aspects of this work would help to pin down the emphasis, and possibly bring the ms to the standards that need to be met to publish in TC.
******************************
There is now ample literature from this area with thicker snow, and the effect of this thicker snow on the sea ice. These works needs to referred to place this work better in context, earlier observations have in fact already observed similar episodes where thick snow, winter storms (warming events) have ample effects on the sea ice. Same goes with some observations of ridge thermodynamics. There is also work on observations of ocean heat fluxes (directly and indirectly) that should be compared to. I am also suprised the work in the exact same area with ice mass balance buoys and ocean heat fluxes from one of co-authors (Perovich) are not referred or comapred to as far as I can see.
To me this is quite a breach of good practice, not to acknowledge earlier work properly, and claiming novelty. This work needs to do much better job to refer to earlier work, and place this work better in context before making claims of novelty.
I propose that the authors read up on the literature that exists (especially in the study region), and this can help place the current observations in historical context (has things changed since the 1980s?, was this winter "normal" in terms of storms (warming events), similar effect of the thick snow, how did it compare to the first mosaic drift etc.):
Perovich, D. K., Tucker, W. B., & Krishfield, R. A. (1989). Oceanic heat flux in the Fram Strait measured by a drifting buoy. Geophysical Research Letters, 16(9), 995–998. https://doi.org/10.1029/GL016i009p00995
Perovich, D., Richter-Menge, J., Polashenski, C., Elder, B., Arbetter, T., & Brennick, O. (2014). Sea ice mass balance observations from the North Pole Environmental Observatory. Geophysical Research Letters, 41(6), 2019–2025. https://doi.org/10.1002/2014GL059356
Wang, C., et al.(2016). Atmospheric conditions in the central Arctic Ocean through the melt seasons of 2012 and 2013: Impact on surface conditions and solar energy deposition into the ice-ocean system. Journal of Geophysical Research: Atmospheres, 121(3), 1043–1058. https://doi.org/10.1002/2015JD023712
Meyer, A., Fer, I., Sundfjord, A., & Peterson, A. K. (2017). Mixing rates and vertical heat fluxes north of Svalbard from Arctic winter to spring. Journal of Geophysical Research: Oceans, 122(6), 4569–4586. https://doi.org/10.1002/2016JC012441
Peterson, A. K., Fer, I., McPhee, M. G., & Randelhoff, A. (2017). Turbulent heat and momentum fluxes in the upper ocean under Arctic sea ice. Journal of Geophysical Research: Oceans, 122(2), 1439–1456. https://doi.org/10.1002/2016JC012283
Merkouriadi, I., et al. (2017). Winter snow conditions on Arctic sea ice north of Svalbard during the Norwegian young sea ICE (N-ICE2015) expedition. Journal of Geophysical Research: Atmospheres, 122(20), 10,837-10,854. https://doi.org/10.1002/2017JD026753
Merkouriadi, I., et al. (2017). Critical Role of Snow on Sea Ice Growth in the Atlantic Sector of the Arctic Ocean. Geophysical Research Letters, 44(20), 10,479-10,485. https://doi.org/10.1002/2017GL075494
Provost, C., et al. (2017). Observations of flooding and snow-ice formation in a thinner Arctic sea-ice regime during the N-ICE2015 campaign: Influence of basal ice melt and storms. Journal of Geophysical Research: Oceans, 122(9), 7115–7134. https://doi.org/10.1002/2016JC012011
Rösel, A., et al. (2018). Thin Sea Ice, Thick Snow, and Widespread Negative Freeboard Observed During N-ICE2015 North of Svalbard. Journal of Geophysical Research: Oceans, 123(2), 1156–1176. https://doi.org/10.1002/2017JC012865
Batrak, Y., & Müller, M. (2019). On the warm bias in atmospheric reanalyses induced by the missing snow over Arctic sea-ice. Nature Communications, 10(1). https://doi.org/10.1038/s41467-019-11975-3
Graham, R. M., et al. (2019). Winter storms accelerate the demise of sea ice in the Atlantic sector of the Arctic Ocean. Scientific Reports, 9(1), 9222. https://doi.org/10.1038/s41598-019-45574-5
Merkouriadi, I., et al. (2020). Effect of frequent winter warming events (storms) and snow on sea-ice growth – a case from the Atlantic sector of the Arctic Ocean during the N-ICE2015 campaign. Annals of Glaciology, 61(82), 164–170. https://doi.org/10.1017/aog.2020.25There are also relevant earlier work on ridges, this includes e.g.
Shestov, A., Høyland, K., & Ervik, Å. (2018). Decay phase thermodynamics of ice ridges in the Arctic Ocean. Cold Regions Science and Technology, 152(April), 23–34. https://doi.org/10.1016/j.coldregions.2018.04.005
Amundrud, T. L., Melling, H., Ingram, R. G., & Allen, S. E. (2006). The effect of structural porosity on the ablation of sea ice ridges. Journal of Geophysical Research: Oceans, 111(6), 1–14. https://doi.org/10.1029/2005JC002895
Shestov, A., & Ervik, Å. (2016). Studies of Drifting Ice Ridges in the Arctic Ocean during May-June 2015. Part II. Thermodynamic properties and melting rate. In 23rd IAHR International Symposium on Ice. Ann Arbor, Michigan.-
AC1: 'Reply on RC1', Ruibo Lei, 07 Apr 2023
The comment was uploaded in the form of a supplement: https://tc.copernicus.org/preprints/tc-2023-25/tc-2023-25-AC1-supplement.pdf
-
AC1: 'Reply on RC1', Ruibo Lei, 07 Apr 2023
-
RC2: 'Comment on tc-2023-25', Anonymous Referee #2, 26 Jun 2023
The paper of Lei et al develops analyses of ice mass balance buoy data deployed at the end of MOSAiC field work. The paper is focused on ponded and ridged ice thermodynamics. The paper looked promising, some of the stories developed in the paper are of potential interest I reckon, however my main issue is that I found myself unable to believe in these because of the lack of rigor and precision. Because I do not see how to sort this out in any other way than reshape and rewrite, I suggest to reject the paper, and did not write an extensive review of the paper which I would view as pointless in this context. I develop below a few elements that I base this evaluation upon.
Lack of rigor in the presentation of the sources
Data sources include buoy, satellite and reanalysis data. In many instances these sources are mixed without specification of which is which. For instance, each time thickness is presented, I do not know whether the authors present satellite data or buoy data. Regarding buoy-based thickness data, I would have doubts that they are at all meaningful, since they are based on a temperature discontinuity (line 168), which is generally not equivalent to thickness. But then, Line 201-202, ice growth rate is introduced, and there is no indication of on based of which source it is calculated? Without clear identification of ice thickness retrieval method and associated detailed validation of thickness measurements, I have no confidence in the growth rate data presented in the paper.
Figure 4 is also quite ambiguous in terms of sources I found. ERA5 net surface heat flux could mean many things, and there is no single line of text in the paper describing what it means. Does that include or exclude open water fraction of grid cells ? Does that include conductive heat flux or not ? What is the source for ice thickness data presented in the figure ? Same for precipitation? Without clear specification, this figure is not informative.
Lack of rigor in the evaluation of methods
The lack of independent evaluation is a problem for the thickness retrievals based on IMB as I developed above. A similar issue arises for the retrieval of superimposed ice from IMB data. L. 169 - It seems that you use IMB signals to identify snow ice and superimposed ice. You cite Jackson et al to claim this is possible. However, there is no mention of such possibility in this paper (I checked thoroughly, and did not find anything), and you do not show any observation or evidence that one can do that. Again, I end up with no confidence on what is argued in the paper.
Originality, progress beyond state of the art
Another possible issue I see is originality, though I think that could somehow be easily fixed. I found the focus on growth and melt of ponded ice and ridged ice types potnentially interesting. This is not the first time these are investigated, and therefore I would tend to think that the intro lacks a a proper review of state of the art. I found the lack of comparison to SHEBA findings to be a major gap of the paper as it is written. In particular, Perovich et al (JGR 2003) and Perovich and Elder (GRL 2002) discuss the thermodynamic behaviour of those ice types and their findings are not summarized in the introduction. Also, studies of ridge consolidation by Marchenko and coauthors are overlooked, wheras they brought significant progress on the thermodynamics of ridges. Likewise, the Reading group has made progress on the thermodynamics of melt ponds (papers by Flocco, Feltham, ...). How does your work relates to those should probably be developed. More generally referring to model studies would be highly benefitial. All in all, I had a hard time to identify progress made in your paper, compared to what I knew before.
Formal issues
I found the introduction always at the edge of overinterpretation or improper use of references. For instance, one could think that increase in ridged ice production is established when reading line 46. There an increase in ridging is backed up by references to Weeks and Strub-Klein and Sudom, which are studies of the ridging process. However those do not back up an increase in ridging at all. There are many other examples of that sort I would say. I also found the result section is mixing results and discussion, sometimes very speculative. I also found no trace of recommendations for future work or to modelling group based on your findings.
Citation: https://doi.org/10.5194/tc-2023-25-RC2
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