Mechanisms influencing seasonal to inter-annual prediction skill of sea ice extent in the Arctic Ocean in MIROC

Ono, Jun; Tatebe, Hiroaki; Komuro, Yoshiki; Nodzu, Masato I.; Ishii, Masayoshi

doi:https://doi.org/10.5194/tc-12-675-2018

Articles | Volume 12, issue 2

https://doi.org/10.5194/tc-12-675-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/tc-12-675-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 12, issue 2

Research article

|

26 Feb 2018

Research article |

| 26 Feb 2018

Mechanisms influencing seasonal to inter-annual prediction skill of sea ice extent in the Arctic Ocean in MIROC

Jun Ono, Hiroaki Tatebe, Yoshiki Komuro, Masato I. Nodzu, and Masayoshi Ishii

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Final revised paper (published on 26 Feb 2018)
Supplement to the final revised paper
Preprint (discussion started on 14 Jul 2017)
Supplement to the preprint

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review of “Mechanisms influencing seasonal-to-interannual prediction skill of sea ice extent in the Arctic Ocean in MIROC” by Ono et al.', Anonymous Referee #1, 18 Aug 2017
- AC1: 'Response to Anonymous Referee #1', Jun Ono, 09 Oct 2017
RC2: 'Review', Anonymous Referee #2, 07 Sep 2017
- AC2: 'Response to Anonymous Referee #2', Jun Ono, 09 Oct 2017

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

AR by Jun Ono on behalf of the Authors (09 Oct 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (12 Oct 2017) by Dirk Notz

RR by Anonymous Referee #2 (26 Oct 2017)

Suggestions for revision or reasons for rejection

Overall the authors have done a good job at revising their mansucript. They have invested significant extra work in response to the reviewer comments, which I very much appreciate. In my view the results of the paper do merit publication, but I think that the points listed below still need to be addressed so that the results are not over-interpreted.

The numbers in the following refer to the numbering of author comments in the response of the authors.

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Major points:

20: The authors have followed the suggestion to compute OHC in a way so it better reflects actual temperature variations rather than shifts in the mixed-layer depth, which I think is very good. The resulting new Fig. 4 in my view confirms that the "advection story" is not really supported by the results. However, the authors now use the argument that "the direct heating and cooling of atmosphere are considered to influence the above OHC through the sea surface" to explain why they base their further interpretation rather on the OHC according to the old definition (integral between MLD and 200m), which in my view is still questionable. Also, the statement "Correlation patterns between the SIE_AO and OHC [...] are not significant during the winter when the MLD is below a depth of 200 m" is in my view misleading: it suggests that statistical significance is involved, although the OHC values just become "undefined". Based on the old OHC definition, the authors state (first with some caution) that "the negative correlation and regression patterns appear to propagate from the North Atlantic to the BS", but then (less cautiously and without any revision): "Hence, the OHC anomalies initialized in the North Atlantic flow into the BS through advection, subsequently emerge at the surface due to vertical mixing in winter, and affect the December sea ice distribution in the BS and eventually in the Arctic Ocean." Accordingly, the corresponding statement in the abstract still reads: "This skill is attributed to the subsurface ocean heat content originating in the North Atlantic. The subsurface water flows into the Barents Sea from spring to fall and emerges at the surface in winter by vertical mixing, and eventually affects the sea ice variability there." I think this is an over-interpretation of the results.

13 (and 15, 23): I am not convinced by the offered explanation why December SIE_AO should be better predictable from January than from April. It may well be related to the result that "the RMSE for April SIC in the Barents Sea is larger in the April hindcasts than the January hindcasts" (as shown in Fig. B2) - but this only shifts the problem to the question why that should be so! As SIC is assimilated, the April SIC field should be much closer to observations right after initialisation (at 0-months lag) than after an initialisation in January (at 3 months lag), no? Is something going wrong with the assimilation/initialisation? Maybe it's just me, but in my view it would be important to explain this properly.

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Minor point:

7 (and 8, 12): I would argue that in the referenced paper, as you say, statistical significance has been used to distinguish "significant predictability" from "no predictability", but in that case it's clear that "no predictability" implies just not sufficient signal to exceed the noise level given the sample size in that study. However, you translate this into the statement "the study has shown that the potential predictability for sea ice extent is continuously one to two years" - which has lost the link to any quantitative threshold. If you'd rather say something like "in that study, potential predictability remained statistically significant at lead times up to 1-2 years", I think that would be more sound.

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RR by Anonymous Referee #1 (08 Nov 2017)

Suggestions for revision or reasons for rejection

Review of revised manuscript: Mechanisms influencing seasonal-to-interannual prediction skill of sea ice extent in the Arctic Ocean in MIROC” by Ono et al.

This is a review of the revised manuscript. The authors have taken some effort to address my and the other reviewer’s comments. However, I still have two major concerns with the manuscript in its present form: (1) the choice of Arctic domain and its influence on the results and conclusions of the study; and (2) the proposed advective ocean mechanism for winter prediction skill. These major concerns and some additional minor comments are outlined below.

Major Comments:

1) Choice of Arctic domain

In my first review (RC1), I outlined a number of concerns directly related to the author’s choice of using an Arctic domain defined as all gridpoints north of 65N. This choice creates confusion throughout the manuscript, making the results difficult to interpret (see RC1, major comment 1). In my opinion, the authors’ response to RC1 has not provided a compelling justification for this choice. If the authors insist on retaining this domain choice, the results throughout the manuscript need to be carefully caveated, so that readers do not misinterpret the findings. Below are some changes that would need to be included if the choice of domain is retained (note that this list may not be exhaustive).

3.33: A line needs to added here explicitly stating that these results are not directly comparable with other hindcast studies. For example, “It should be noted that the results of this study are not directly comparable with other hindcast studies that focus on pan-Arctic SIE (e.g., Chevallier et al., 2013; Sigmond et al., 2013; Wang et al., 2013; Msadek et al., 2014; Peterson et al., 2015; Guemas et al., 2016; Sigmond et al., 2016), due to this choice of Arctic Ocean domain.”

4.11-12: I recommend explicitly noting the reason for this discrepancy: Winter SIE_AO variability is dominated by changes in the Barents and GIN Seas, which have long persistence timescales relative to other regions of winter ice variability.

4.21-22: This sentence should be removed, as a comparison with Tietsche et al. (2014) is not appropriate given the different domains used in these studies.

4.13-30: To alleviate issues with the choice of Arctic Ocean domain, the authors should consider using a normalized RMSE (NRMSE) metric, where the RMSE values are normalized by the standard deviation of each month. As it currently stands, these RMSE values are difficult to interpret giving the large seasonal cycle in RMSE. Put differently, it is hard to know from Fig. 2b what is a “good” or “bad” RMSE value.

5.10-19: The authors have chosen to remove Fig. S3 of the previous supplementary material. This Figure should be added back into the supplement, as it provides important context for the results of the study. Also, a comment should be added to the text that summer-to-winter differences in SIV-SIE correlations are much less pronounced when using a northern hemisphere domain for SIE.

2) Advective ocean mechanism for winter prediction skill

The authors claim that Figs. 4c-f provide evidence for subsurface OHC anomalies advected from the North Atlantic. While plausible, this mechanism is not convincingly shown by Fig. 4. Aside from a small patch of positive correlation west of Novaya Zemlya in panels 4c and 4d, there is no clear evidence of OHC anomaly advection. Rather, the main signal appears to be a large stationary patch of OHC anomalies throughout the Barents and GIN Seas, which is present at lags of 9, 6, 3, and 0. The origin of these anomalies is not clear from Fig. 4.

The authors claim that OHC anomalies “flow into the BS through advection.” What is the evidence for this? Either more evidence needs to be provided or the statements about regarding the advection mechanism need to be appropriately qualified. For example, the advection hypothesis could be referred to as a “plausible mechanism.”

5.33-6.1: As mentioned in RC1 and RC2, this apparent advection from the North Atlantic is likely an artefact of only defining OHC below the mixed layer. When North Atlantic mixed layers deepen, this quantity becomes undefined, creating the undefined regions seen in Fig. S4. Therefore, this sentence should be removed.

Minor Comments:

3.26-27: This statement remains unclear. How are the drifts removed? An additive correction? A regression based approach? Is the drift removal lead-time dependent? More detail is needed here.

4.4: The autocorrelation coefficients are the skill of a persistence forecast. I recommend changing this line to: “We first examine the potential predictability of SIE_AO (Fig. 1), based on lagged auto-correlation coefficients, which is the skill of a persistence forecast.”

4.9: Change to “…similar to those…”

4.10: Change to “…due to differences in the observational time period.”

4.25: Change to “…mid-1980s and mid-1990s.”

5.14: Change to “…similar features…”

5.17: I believe Fig. S3 here is referring to the old Fig. S3 (which is no longer in the supplement)

5.21: Change to “…model-predicted December SIE_AO”

6.20: Rather than sampling uncertainty, I would suggest that a more likely explanation is errors in sea ice thickness initial conditions and model drift.

7.1-3: This sentence needs to be removed (the author’s claimed to have removed it in their response, but seem to have forgot).

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ED: Reconsider after major revisions (10 Nov 2017) by Dirk Notz

AR by Jun Ono on behalf of the Authors (22 Dec 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (08 Jan 2018) by Dirk Notz

RR by Anonymous Referee #1 (12 Jan 2018)

ED: Publish as is (15 Jan 2018) by Dirk Notz

AR by Jun Ono on behalf of the Authors (19 Jan 2018)

Short summary

Sea ice in the Arctic Ocean has experienced rapid decline since the beginning of satellite observations. To assess the predictability of sea ice extent (SIE) in the Arctic Ocean and to clarify the underlying physical processes, we conducted prediction experiments using an initialized climate model (MIROC5). The present study suggests that subsurface ocean heat content originating from the North Atlantic contributes to the skillful prediction of winter SIE at lead times up to 11 months.