The manuscript applies a FEM-BV-VAR reduced-order framework combined with a sliding-window transition-matrix approach to investigate persistent atmosphere–sea-ice states during three recent Antarctic low sea-ice years (2016, 2021, and 2023). The topic is timely, and the effort to move beyond fixed temporal averaging is valuable, with a potentially useful methodological contribution in identifying variable-length persistent events. However, the presentation and organization of the manuscript are difficult to follow, and the authors are encouraged to substantially revise the text to improve clarity.

General comments

1）The methodological description needs to be improved. At present, it is hard to understandwhat FEM-BV actually is, how it is implemented, and how the resulting states should be physically interpreted.

2）The manuscript lacks clarity regarding the training and validation strategy of the machine learning framework. In general, ML-based approaches require a clear separation between training and validation (or testing) datasets to ensure robustness and avoid overfitting. While the authors mention the use of cross-validation in terms of RMSE minimization, it remains unclear how the data are actually split (e.g., temporally, randomly, or using block cross-validation), and whether the temporal dependence in the data is properly accounted for. This is particularly important for climate time series, where autocorrelation can bias standard validation approaches. A more detailed description of the data partitioning strategy and its implications for model robustness is needed.

3）The presentation of the results is currently somewhat limited and relies heavily on qualitative interpretation of composite maps. While the figures provide useful visual information, the analysis would benefit from more quantitative diagnostics to support the main conclusions.

4）The analysis is limited to three specific years (2016, 2021, and 2023), which represent extreme low sea-ice conditions. While these case studies are relevant, the sample size is relatively small, raising concerns about the generality and robustness of the conclusions. It would strengthen the manuscript to extend the analysis to a broader range of years, including both extreme and more typical conditions. In particular, a quantitative comparison between extreme low sea-ice years and climatologically normal years would help to better assess whether the identified patterns are robust features or case-specific behavior.

Specific comments

1）Lines 131-152: Please clarify the provenance and reliability of the NNR1 sea-ice concentration data before 1979. Was the FEM-BV model trained on the full 1959-2024 period?

2）Lines 155-173: The preprocessing needs more detail. Please specify how anomalies are computed, what climatological base period is used, how the daily/unit matrix normalization affects amplitude information, and how many PCs are retained and why?

3）Lines 211-219: The choice of the final day as the representative day is reasonable; however, it would be helpful to assess how sensitive the results are to this assumption. For example, would using the first day instead lead to different identified patterns?

This manuscript investigates the relationship between persistent synoptic-scale atmospheric features and recent Antarctic sea-ice anomalies, with particular emphasis on the low sea-ice years 2016, 2021, and 2023. The authors develop a reduced-order coupled atmosphere-sea-ice model using reanalysis data and apply the FEM-BV-VAR framework together with a non-stationary transition-matrix approach to identify persistent background states of varying duration. The manuscript argues that persistent synoptic patterns strongly influence the rate and spatial structure of sea-ice variability. During periods of relatively weak synoptic variability, a large-scale Antarctic warming pattern becomes the dominant influence on sea-ice retreat. The topic is interesting and potentially important. However, in its current form, I do not think the manuscript is yet ready for publication. My main concern is that the physical interpretation remains insufficiently developed, and several key methodological and diagnostic issues need to be addressed before the conclusions can be considered robust.

1. The most important weakness of the manuscript is that the results are primarily presented as statistical or pattern-based associations, but the underlying physical processes are not sufficiently explained. At present, the analysis supports physically plausible relationships, but it does not yet provide a sufficiently clear process-based interpretation of how the identified synoptic states lead to sea-ice growth or retreat. The paper would be much stronger if the authors could provide more detailed discussion of the relevant physical mechanisms, for example through thermodynamic, dynamic, or regional process diagnostics.

2. Related to the previous point, the manuscript often goes beyond what the analysis can firmly support. The current framework is useful for identifying covariation  and persistent background states, but it does not by itself establish strict causal attribution. Some conclusions therefore appear overstated. The authors should be more cautious in distinguishing between statistical association, dynamical interpretation, and formal attribution.

3. The manuscript refers to a “climatological anthropogenic warming pattern” as a dominant influence during periods of weak synoptic variability. However, the present study does not perform a formal attribution analysis separating externally forced and internally generated variability. Therefore, this terminology is too strong in the current context. The authors should either soften this statement or provide stronger justification for using such wording.

4. Data: The study uses daily SIC from NCEP, but the comparison with NSIDC appears to be limited to monthly-scale analysis. Monthly comparison alone is not sufficient, especially given that the manuscript focuses on synoptic events. The authors should provide a more detailed validation of the daily SIC fields, including spatial patterns and event-scale behavior, rather than relying only on monthly anomaly comparison. For atmospheric fields, it is not clear how robust the results are to the choice of reanalysis. The manuscript should discuss whether the same persistent patterns and event structures would be obtained using ERA5 instead of NCEP, or at least assess the differences between the two products for the key variables used in the analysis. At present, the sensitivity of the conclusions to the reanalysis dataset remains unclear.

5. The manuscript spends considerable space describing the methodology, while the physical interpretation of the results is comparatively brief. I suggest streamlining the methodological description in the main text and moving some technical details to an appendix or supplement, in order to leave more room for discussion of the physical implications of the identified patterns.

6. The identified events have very different durations. This raises an important question: are the events with different lengths dynamically comparable? Do they represent similar mechanisms, or are they fundamentally different types of processes being grouped within the same framework? The authors should discuss whether the same interpretation applies across events of very different duration, and whether duration itself carries physical significance.

7. The manuscript focuses strongly on atmospheric driver, but the role of the ocean and sea-ice dynamics is not sufficiently considered. Given the current understanding of Antarctic sea-ice variability, it is important to clarify to what extent the identified atmospheric patterns act alone, and to what extent oceanic forcing or sea-ice dynamical processes may also be essential. At minimum, the limitations of excluding these factors from the main analysis should be discussed more explicitly.

8. The wind vectors in the figures are very difficult to read. In their current form, I cannot clearly determine their direction or magnitude. The figure design should be improved. Moreover, some figures appear to lack units. All plotted variables should include clear and consistent units in the color bars, captions or axis labels.

The manuscript considers three years (2016, 2021, 2023) with anomalously low Antarctic sea-ice extends and aims to identify atmospheric patterns that played a role in these events. The approach of the authors is based on the FEM-BV-VAR learning algorithm. The analysis seems interesting , however, the methodology is explained insufficiently to the point that it is hard to pinpoint exactly what the results of the manuscript are. The main aspects that remain unclear are as follows:

1) The FEM-BV-VAR learning algorithm is mentioned, and Axelsen et. al. (2025) is cited, but there is no description of what the algorithm does. It is not necessary to describe the algorithm in detail; for details a reference is sufficient; but the following point should be clear: What is the input to the algorithm? What is the output of the algorithm? What are the parameters K, M, p, and what role to they play in the algorithm? Similarly, the principal component analysis should be elaborated on: What objects are the principal components? How are they determined? Overall, the introduction of the methodology would greatly benefit from some more rigorous mathematical notation.

2) The paragraph 167-174 seems to describe the construction of some matrices which would become much more comprehensible with some more mathematical notation.

3) Equation (1) defines the root mean square error. It seems that the model output o_j and the training data s_j have not been mentioned before. It should be clarified exactly what the model output is and what is being used as the training data.

4) In 186-189 the affiliation sequence is mentioned. Apart from Γ(t) being a probability vector, it is unclear what this vector describes and how it is obtained. 

5) In the paragraph 203-234 a transition probability matrix in a time window [t₀, t₁] is considered. They are defined by Equation (3) but it is unclear where the probabilities Pr(k_t+1 = j | k_t=i) come from. Additionally, the right-hand side of the definition depends on t∈[t₀, t₁] while the left-hand side does not depend on t. Additionally, it is unclear how the time windows [t₀, t₁] are determined.

6) It should be elaborated what type of LOWESS method is used and with which parameters.

Some other remark regarding the manuscript:

7) I recommend to make clearer what the results of the paper are. It seems that the qualitative discussion of the driving factors for anomalously low sea-ice extend is based largely on a direct observation of the data presented in Figures 4-6. Are the GPH and temperature values which are shown in Figures 4-6 output of the model or simply the NNR1 data? If this is the NNR1 data, then it seems that the main contribution of the algorithmic approach is the determination of certain events within the considered timespan. Either way, I recommend including a discussion about which results of the manuscript can be tested in some way (e.g. against some null-hypothesis), and which results are 'validated' based on phenomenological observations. 

8) In Figure 2 it seems that increasing K improves the RMSE. Why have no values of K larger than 4 been considered?