the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 27 May 2026
The Role of the Atmosphere during the 2023 Antarctic Sea Ice Minimum
Abstract. In February 2023, Antarctic sea ice extent reached a record minimum, yet the mechanisms driving this event remain debated.
Here we use a coupled ocean–sea ice model (NEMO-SI3) forced by two different atmospheric reanalyses, ERA5 and JRA-55-
do, to investigate the drivers of the 2023 minimum and assess the sensitivity of inferred mechanisms to reanalysis choice. Both
simulations capture exceptionally low February sea ice extent during the 2022/23 melt season, though neither atmospheric5
reanalysis reproduces 2023 as a record minimum, with JRA-55-do showing closer agreement with observations. Substantial
regional differences emerge between the two simulations in February 2023: JRA-55-do produces greater sea ice coverage in
the Amundsen–Bellingshausen and Ross sectors, while ERA5 yields higher concentrations in the Weddell and Indian Ocean
sectors. We further investigate the atmospheric differences between the atmospheric reanalyses - differences in downwelling
longwave radiation are the strongest disparity in October, whereas shortwave radiation is the primary disparity in February-10
suggesting a role for these atmospheric differences in the differing sea ice outcome between the two simulations. Much of the
existing literature attributes the 2023 minimum to mechanisms inferred from a single reanalysis, most commonly ERA5. Our
results demonstrate that reanalysis choice produces markedly different regional sea ice responses, with implications for the
interpretation of both thermodynamic and dynamical drivers. We therefore recommend caution when diagnosing real-world
sea ice events from reanalysis-forced simulations and that multiple reanalysis products could be employed to improve the15
robustness of inferred mechanisms
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Status: open (until 19 Jul 2026)
- RC1: 'Comment on egusphere-2026-2719', Anonymous Referee #1, 26 Jun 2026 reply
-
RC2: 'Comment on egusphere-2026-2719', Anonymous Referee #2, 03 Jul 2026
reply
This study makes an interesting point about the senstivity of sea ice to the prescribed atmospheric reanalysis that is used to force sea ice and ocean models. To the extent that integrations forced in this way are still appearing in the literature, this result is valuable.
General Comments
It is inescapable that the feedbacks at the surface are incorrect when atmospheric forcing is prescribed. It is good to see this mentioned in a few places, but I'm left wondering why ignore your own words of caution and carry on doing more uncoupled runs. Relaxing the winds or temperature in a fully coupled model is a better option. It would be good to write this paper in a way that informs relaxation efforts too since the target of relaxation is generally reanalyses.
it would be more valuable if the study could say which field or fields are the culprit for driving the sea ice differences that they found. The evaluation of differences between the reanalyses in this study is helpful, but doesn't go far enough. Plus the figures are quite hard to interpret when the range of the colorbar is so large.
Sorting out which fields matter in an uncoupled framework is easy to do in simulations forced by hybrid versions of the reanalysis. I'd be interested to see at least the following additional simulations. First, a pair of integrations with JRA-55-do for all fields but with ERA5 winds and vice versa. Second, a pair of integrations with JRA-55-do for all fields but with ERA5 air temperatures and vice versa. The integrations done in this study are coarse resolution and only 14 years long, so four more simulations is relatively little computing.
In any case, prescribed atmosphere integrations are problematic because the prescribed air temperature strongly controls the sea ice edge in summer (less so in winter). However, the experiments I suggested with hybrid forcing could at least rule out whether the air temperature differences in the reanalysis are driving differences in the simulations.
I did enjoy reading the Intro and Discussion and applaud the effort to summarize the findings about 2023 and their reliance on reanalysis. It does read a bit like a review, and might be better framed as such if the authors can't do more simulations to strengthen their own findings.
Specific Comments
1. Figure 1. I suggest that you show sea ice area and not extent since the grids are grossly different between the coarse-resolution model and the sea ice products. The excuse to avoid area because satellites confuse open water and meltponds is not relevant in the Antarctic. The seasonal cycles could be very different in area, and you may come to different conclusions.
2. Figure 5. The statement "October relative to the 2010– climatology" in the caption is pretty awkward. I'm guessing what is meant is the mean of 14 Octobers minus October 2010. I think this is a nice way of computing anomalies and presnting differences so the reader can gauge how the difference compares to recent trends.
3. Figure 5 The evidence of the sea ice edge in surface wind speed and downwelling shortwave is odd. Please explain. Also, I think it would be valuable to show the wind direction differences since the direction has such an important impact on sea ice transport and ocean upwelling.
4. Figures 6 Please change the range of the colorbars independently for Figs 5 & 6, especially for 2m air temperature in Feb. If this field differs by even a few tenths of a degree, I'd expect it to make a big difference to the sea ice. With a 20 deg C range, I can't tell whether the difference is substantial or not.
5. Line 272 caught me by surprise. EOF2 is also a typical difference pattern, just less typical than EOF1 by the ratio of their explained variances. So I don't think 2023 is atypical. In fact, it occured quite strongly in the last three years of the integration.
6. Line 286 What pronounced peak? I'm seeing 3 years in a row, which I'd call a pronounced plateau.
7. Line 346 Why have you used the term "represented"? Is it intentional to indicate that strong winds may not have been present in nature? In any case, this claim surprised me since other parts of the paper emphasized the large differences between the reanalyses winds.
8. Line 346-7 says "strong wind anomalies in October and February 2023 were consistently represented between ERA5 and
JRA-55-do, lending confidence to conclusions that emphasise wind-driven dynamical mechanisms." But this is a weak statement since it is merely correlation, and no experiment has been shown that this is key to driving anomalies in your simulations. It could equally be due to the trends in surface air temperatures. A version of this was repeated in #6 of the conclusions, which I don't think is justified.9. Do the authors think that ERA5 causes greater errors in the integration forced with ERA5? The integration with JRA-55-do could have compensating errors, such that the model errors are somewhat masked, making that intergration seem more successful due to the forcing. However, a different model may have the reverse result. To be clear, I think the point that that the reanalysis causes differences is not in question. I only question drawing conclusions about which is "better". Conclusion #1 is already worded conservatively. But readers may still come to the conclusion that JRA-55-do is better, unless you tell them they should not. I suggest including some words of caution in Conclusion #1
10. Line 460 Conclusion #4. While the downwelling longwave differences are big, this study hasn't shown (yet) that the sea ice is most sentsitive to this difference in this field. I see the word "suggesting" used, but I still think this statement is too bold based on the results presented. To draw such a conclusion, this forcing should be isolated in additional experiments where only the downwelling longwave differs.
Citation: https://doi.org/10.5194/egusphere-2026-2719-RC2
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General Comments
This manuscript simulates the Antarctic sea ice minimum that occurred in February 2023 using two different atmospheric reanalysis datasets. It presents the differences in the simulation results and attributes them to variations in atmospheric forcing. This work highlights the importance of selecting appropriate atmospheric forcing data in Antarctic sea ice modeling. It points out that many previous studies on the 2023 summer sea ice minimum relied on ERA5 as the atmospheric forcing field; thus, the resulting attributions and mechanistic analysis may be heavily dependent on this specific dataset. The paper serves as a valuable reminder for future numerical modeling studies to carefully consider how different atmospheric forcing choices impact simulation outcomes and subsequent scientific conclusions. However, there are some shortcomings in the analysis and discussion of the results that need to be addressed before the manuscript can be considered for publication.
Specific Comments
1. The current title does not accurately reflect the content of the manuscript. It should explicitly indicate that this is a comparative numerical simulation study based on two different reanalysis datasets used as atmospheric forcing.
2. In the Introduction (Lines 63–94), the author introduces the application and performance of various reanalysis datasets in Antarctica. However, this section reads like a mere list of literature and fails to provide justification for selecting the two specific datasets used in this study. While Section 4 indicates that ERA5 is commonly used in numerical studies of the 2023 Antarctic sea ice extent minimum, there is a lack of background information on JRA-55-do. The manuscript would benefit from a brief discussion explaining why these two specific reanalysis datasets were chosen over others.
3. Conclusion 3 is derived from Lines 224–226: "By December, however, pronounced regional contrasts emerge. JRA-55 simulates higher SIC relative to ERA5 in the Amundsen, Bellingshausen, and Ross sectors, while ERA5 shows higher SIC in the Weddell and Indian Ocean sectors." This statement is presumably intended to correspond to Figure 2. However, the spatial distribution in Figure 2 for December does not entirely match this description; ERA5 still exhibits higher SIC across all marginal ice zones. The same discrepancy applies to the distributions in January and February. Furthermore, Conclusion 3 fails to specify which month this comparison refers to.
4. Conclusion 5 is drawn from the last two paragraphs of Section 3.2. This conclusion appears to be a mere speculation based on the temporal evolution of the SIC differences between the two simulations from December to February. There is no additional supporting evidence provided for the ice-albedo feedback, such as changes in incoming shortwave radiation or variations in ocean temperature. Such speculation is insufficient to serve as a formal conclusion. I recommend either removing this point or providing robust evidence to support it.
5. Section 4 provides a detailed discussion of recently published numerical modeling studies on the 2023 summer Antarctic sea ice extent minimum. Most of these studies utilize ERA5 as the atmospheric forcing field, and this manuscript explores the potential implications of this choice. This discussion is highly instructive for future modeling efforts. However, the current discussion is somewhat fragmented. I recommend conducting a deeper analysis and synthesis to extract generalized insights, which could then be incorporated into the Conclusions.
6. Many studies emphasize the critical role of the ocean. Since the model outputs in this study include ocean variables, a comparative analysis of these oceanic fields should be conducted to provide a more comprehensive understanding of the impacts caused by differences in atmospheric forcing.
7. The authors mention melt ponds in both the model setup (Lines 124–127) and the results section (Lines 195–196). However, melt ponds are rare on Antarctic sea ice and their impact on simulations and satellite remote sensing is not significant. The relevant model setup and the cited literature (Aparício et al., 2025) are specifically tailored for Arctic sea ice.
8. Line 265: The text states "negative anomalies in the northern sea ice edge and Ross Sea", but this is inconsistent with what is shown in the corresponding figure.
9. Lines 268–269: "The PC1 time series remains weak during December–February (DJF) 2022/23, while PC2 exhibits a pronounced peak." This description contradicts the features displayed in Figure 4. Furthermore, Figure 4 only presents results for February. A similar issue occurs at Lines 285–286.
10. Section 3.4 primarily discusses atmospheric anomalies in October, with only a brief mention of February at the very end. Please clarify the rationale for this approach. Additionally, the paragraph starting at Line 323 discusses "a modest positive sea ice concentration anomaly in October." Given that the focus of this manuscript is on the sea ice extent minimum, shouldn't the emphasis be on negative SIC anomalies? Finally, the term "circulation" mentioned at Line 340 does not appear to have been introduced or discussed previously in the text.
Technical Corrections
1. Figures should generally be placed immediately after the text where they are first mentioned. Please adjust the positions of Figures 1, 5, etc., accordingly.
2. Several abbreviations (e.g., ERA, JRA) are not defined at their first occurrence. Please provide their full names.
3. Please ensure consistency in naming the two datasets throughout the manuscript: use ERA5 and JRA-55-do.
4. Line 30: Does "1979-" refer to "1979–2023"? Please specify the end year.
5. Line 111, "We use two coupled NEMO - SI3 (Vancoppenolle et al., 2023) ocean sea ice model simulations." Could it be changed to "We use two coupled ocean-sea ice model simulations performed with NEMO-SI3 (Vancoppenolle et al., 2023)."
6. Line 112, "2 degree": The spatial resolution of the model is unlikely to be so coarse. Is this a typographical error?
7. In Figure 1d, the satellite remote sensing results are plotted with a solid line, which does not match the line style indicated in the legend.
8. Line 214: The unit "km" should not be italicized.
9. The statements in the beginning of Section 3.2 should be supported by referencing the corresponding figure numbers.
10. In the last sentence of the caption for Figure 2, should "JRA-55-do" actually be "ERA5"?
11. Section 3.3 states: "The analysis was applied to the annual series of each monthly mean separately, in order to minimise the influence of the seasonal cycle and to instead emphasise inter-annual variability." However, both the text and Figure 4 only present results for February. This limitation should be explicitly stated in both the main text and the caption of Figure 2.
12. Line 261: The phrase "the EOF is positive" is an inappropriate expression. Please rephrase.
13. Line 300: The term "the Amundsen-Bell region" has not been defined previously. Should this be standardized to "the Amundsen–Bellingshausen and Ross sectors"?
14. Line 315: The description "the West Pacific sector" is inaccurate.
15. Line 321: For the phrase "sea ice concentration by February 2023", please add the corresponding figure number.
16. At Lines 9–11 and other locations, sentences contain parenthetical insertions starting with hyphens or em-dashes ("- " or "— "). I feel this specific writing style is strongly indicative of AI-generated text. Please revise the phrasing to ensure a natural academic tone.