Review of “Recent timescale transition from interannual to decadal variability in January sea ice area over the Bering Sea”

This article presents an exploration of the processes underlying a documented recent timescale transition in Bering Sea ice area from interannual to decadal variability. The mechanisms, as suggested by the authors, are a negative feedback wherein wind field anomalies resulting from sea ice area anomalies (due to localized atmosphere-ocean heat flux changes) induce changes in wind field divergence which impact subsequent sea ice area, and a positive feedback wherein wind field anomalies resulting from sea ice area anomalies impact oceanic heat transport which then impacts subsequent sea ice area. A change in the relative prevalence of these processes over time is suggested as an explanation for the transition from interannual to decadal variability.

The ideas presented are scientifically interesting and the overall structure of the article is reasonably good. The quality of the figures is good overall. I think some of the points in Section 3 could be de-emphasized as I discuss below, for clarity and brevity, since it appears to me that the more substantial points are in Section 4. The dynamical/thermodynamical reasoning in the manuscript is reasonable to me, but I have some questions about the robustness of some of the arguments used to substantiate this reasoning. Furthermore, I found it was often difficult to ascertain in the article where there are novel findings and where findings are being cited/reproduced from previous work to provide context for the article’s findings. Because of this, I think the manuscript would require some substantial revisions before being suitable for publication.

My general comments are included below, followed by line-by-line comments and technical corrections.

General comments:

A portion of this manuscript is closely connected to results from previous work by the authors; e.g. Wang et al. 2022, Wang et al. 2023, and Wang et al. 2024 a,b (as cited in the article references). Some of the panels in the figures are also found in previous work, and although the studies are referenced, it is not always clear which figure panels contain new work. I appreciate that the authors want to build up context from previous work to situate the current findings, but this makes it difficult for me to ascertain where the novel results in this article are located. I will try to indicate in my line-by-line comments where I see this happening but overall, I think many parts of Section 3 need revision to make it clearer where figure panels and results are reproduced from previous work.

In general, parts of Sections 3.1 and 3.2 appear to be somewhat redundant to me; I think they could be condensed or partly moved to supplements. Because the timescale transition has been documented in previous work, I do not think as much detail is necessary in establishing the context except for the specific novel results on the specific timing of the transition, as applicable.

The authors categorize December SIA years into five categories based on normalized values which is a reasonable approach, but I wonder at how representative the heavy-ice year composites are, since only ~5 years are included. Since much of the analysis seems focused on the extremes, I wonder if the authors could consider reducing the number of categories to simplify interpretation and streamline the results (i.e. reduce to 3 categories, either combine the low/high categories into the normal category, or group them with the extremes).

The information flow argument for causal influence is broadly reasonable to me; given that the SLP captured by EOF3 appears to align with the SLP patterns during extreme high and low sea ice years, the statistically significant causal influence of SIA12 on EOF3 makes sense to me, although this influence appears to have a somewhat small magnitude. The relationship to wind divergence during extreme events is also fairly convincing. I have one question on this point: why is the same causality analysis not carried out for other quantities such as SST and heat transport? Would we not expect them to also be causally linked to SIA12?

The reasoning around Figure 13 seems tenuous to me. The authors present time series of sea surface temperature, wind divergence, and heat transport in Figure 13, and discuss the trends in these quantities, using the differing trends to provide an interpretation for the change from interannual to decadal variability due to the dominance of differing contributing factors over the years. The physical explanation does seem reasonable to me, and earlier analysis in the manuscript does seem to substantiate it. However, the use of trends in Figure 13 weakens the argument for me because the trends are quite small and furthermore, they do not meet the 95% confidence level (I assume due to the high interannual variability). This is particularly apparent to me for the SST, where the authors report a decline followed by an increase as per the trend lines drawn in the plot, but equally, I could see a claim to be made for a decline from 1980 to ~2013, followed by a later increase, or also a relative lack of trend overall from 1979-2023, depending on where one would choose to place the discontinuity in trend lines. The heat transport is also highly variable and could also be interpreted to e.g. have a declining trend since ~2014. I would be more convinced if the authors could show that the relative magnitude of the driving factors changes, of which I am not convinced from Fig 13. I would appreciate if the authors could justify their inclusion of this analysis or make the argument using more robust data.

With the discussion of horizontal sea ice convergence/divergence, a consideration that is missing to me is sea ice thickness. With sea ice convergence comes thicker ice which can have thermodynamic and dynamic impacts, e.g. stronger inhibition of air-sea heat fluxes and impacts on ice motion. I would appreciate hearing at least a brief mention of what impacts the authors could expect from thicker ice.

I will leave this point to the authors’ discretion, but I would find it helpful to have a more specific title (e.g. mention that the article is examining the role of mesoscale processes in the timescale transition).

Specific comments:

• L105: Why was ERA5 relegated to the supplement rather than NCEP? To my understanding it’s a more contemporary dataset than the NCEP product with a higher resolution, which is particularly helpful when considering processes such as wind where capturing small scales is important
• L106: Reanalysis products are not observations, please take care with not referring to them as such here and throughout the article
• L188: Please cite the “several studies” that have substantiated this transition
• L190: The motivation for the use of IMFs here is not entirely clear to me; has the onset of the transition not been documented sufficiently in previous work?
• L198-200/Figure S5: it’s unclear to me how this figure illustrates the timescale transition mentioned in the text, since those figures are just time series, and they do not include any sort of analysis of variability. If this is a result shown more clearly in previous work, I request that the authors state this more explicitly.
• Figure S2, re: the wavelet transform: how reliable can some of these results be given that the edge effect influence extends quite far into the time series?
• Figure 4: Could you explain why the MODWT is unable to separate multiyear and decadal variability? Is it a matter of the time series not being long enough?
• Figure 5 a): the coloured dots were initially somewhat confusing to me since they do not line up with the ice categories: consider changing them so that each category has a different colour or simply having all dots the same colour. The caption says 4 categories but there are 5.
• L252-253: “only a single interannual variation feature is evident” could you clarify what you mean here? Is this a result from Wang et al. 2023?
• L260: Please rephrase, you say "significant" but the correlation not marked as statistically significant until after 2010 as per the green dots in Fig 5b
• L370: Maybe better to say the results are discussed further in Wang et al. 2022 rather than saying "corroborated" since that study is not entirely independent from this one (Figure 9b appears to have the same information as Fig 4b from that article)
• Figure 11: Please specify that dots indicate statistical significance in the caption
• L427/fig 12b: Minor phrasing consideration: the anticyclonic circulation only appears substantial north of the Bering Strait towards the East Siberian Sea

Technical corrections:

• L60: are -> is
• L131: “within annual” -> “within the annual”
• L295: "drivers" -> "drives"
• L307: anomalies.. -> anomalies.
• L311: I think this should be S3 not S1?
• L360: During -> during
• L379: influence -> influences
• L406: missing numbers for PC2 and PC3 in math text
• L415: exert -> exerts
• L480: exacted -> extracted?
• L491: the -> The