Improved teleconnection between Arctic sea ice and the North Atlantic Oscillation through stochastic process representation

Strommen, Kristian; Juricke, Stephan; Cooper, Fenwick

doi:https://doi.org/10.5194/wcd-3-951-2022

Articles | Volume 3, issue 3

https://doi.org/10.5194/wcd-3-951-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/wcd-3-951-2022

© Author(s) 2022. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 3, issue 3

Research article

|

17 Aug 2022

Research article |

| 17 Aug 2022

Improved teleconnection between Arctic sea ice and the North Atlantic Oscillation through stochastic process representation

Kristian Strommen, Stephan Juricke, and Fenwick Cooper

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Final revised paper (published on 17 Aug 2022)
Preprint (discussion started on 01 Oct 2021)

Interactive discussion

Status: closed

RC1:
'Comment on wcd-2021-61', Anonymous Referee #1, 04 Nov 2021

This study examines the effects of stochastic parameterizations on the link between November sea ice and the winter NAO in historical coupled model simulations. The authors find that in the control simulations the connection is weak and opposite of what is seen in observations. When they add the stochastic parameterizations to the ocean and sea ice model components, the connection between the November sea ice and winter NAO switches sign and becomes closer to the observed value. They attribute the differences to improved ice-ocean-atmosphere coupling. I think that this an interesting study with potentially important results worthy of publication. However, I do have a number of issues that need to be addressed, so my recommendation is for major revisions.

Major comments:

1.The use of different sea ice regions for the model and observations is problematic. The authors have correlated the NAO with sea ice concentration at all gridpoints and cherry-picked the regions with the largest correlations (which is different in the model and observations). Given the weak correlations combined with large internal variability, there is a good chance the internal variability is contributing to the regions with the highest correlations. This means all the subsequent analysis and discussion about statistical significance is not reliable because the region was not selected a priori. The authors should use the Barents-Kara (BK) Sea for both observations and model correlations. I don’t even think this will have that large of an effect on the analysis and conclusions because there are clearly differences in correlations over just the BK Sea (Figure 4).

The justification for this is not at all convincing. The authors claim that because models have different biases, the regions with the most sea ice variability is different across different models and the real world. However, The sea ice in the BK Sea in the OCE does not look that different than in ERA5, so I don’t see why they cannot use the same region. The leading EOF in ERA5 looks very similar around the BK region (Figure 2). I can see maybe shifting the regions slightly to account for biases (e.g. if the model ice edge is 1° too far south in the model, shift the region definition 1° to the south), but to use a very different region is not justifiable and introduces additional issues.

2. The model the authors use may be an outlier and the results may not be that relevant to other models. This is very briefly mentioned in the discussion, but I think there are reasons to think this may not work as well in other models. Most models tend have a weak connection between reduced sea ice and a negative NAO. In addition, as mentioned in the introduction, model experiments forced with reduced sea ice also tend to show a weak negative NAO response. However the control model used here shows the opposite sign correlation compared to most models, and a previous study (Ringgaard et al. 2020, doi:10.1007/s00382-020-05174-w) shows that a version of this model shows no NAO response to reduced sea ice in the BK Sea. In addition, the improved correlation in the OCE version are still weak. Could it not be the case that the OCE is just improving the flaws in this particular model, which brings it more in line with other models? This would then mean that applying the same methods in other models may not have as large of an effect.

3. The authors claim that mean state changes cannot explain the differences, but I don’t find their arguments that convincing. They argue that AMIP ensemble with prescribed SSTs and sea ice show weak correlations. First of all, taking the correlations of the AMIP ensemble at face value would suggest that close to half of the difference can be explained by the mean state. Second, there are many other difference related to the coupling of sea ice and SSTs that could cancel out the improvements made by correcting the mean state biases in the AMIP experiments. It is likely that the improved mean state explains at least some of the differences and it can’t be ruled out that it is entire explanation.

4. The authors conclude that the link between sea ice and the NAO is stronger because of improved ice-ocean-atmosphere coupling. This is a bit vague and could be investigating a little further. What about the coupling is actually being improved? Because the authors argue that coupling on short timescales can explain the difference, there could be a lot value in doing similar analysis to what was done in Figure 7, but with other variables. For example, does the OCE ensemble have a stronger upward heat flux and temperature response following reduced sea ice?

5. The title and abstract need to be more specific. Many different links between the Arctic and the midlatitudes have been hypothesized via a number of different mechanisms. It is misleading to refer to Arctic-midlatitude links very generally, when the authors have only investigated one specific link between November Barents-Kara sea ice and the winter NAO in interannual variability. Even with this correlation, the authors have only looked at one mechanism (they have not investigated the stratospheric mechanism).

Other comments:

L35: What is meant by ‘More seriously’? Are the model experiments with imposed sea ice anomalies not serious?

L35-38: Another recent study that could be cited/discussed here is Siew et al. 2021 (doi:10.1126/sciadv.abg4893).

L30-42: Somewhere in this discussion it should be mentioned that observed correlation seems to be highly intermittent when looking at the much longer record (Kolstad and Screen 2019, doi:10.1029/2019GL083059). In the middle of the 20th century, the sign of the connection appears to be opposite compared to the recent period.

L38-42: This is not an accurate description of Blackport et al. 2019. This study has nothing to do with the connection between November BK sea ice and the winter NAO and is not that relevant for this study. A much more relevant study that argues that the correlation between November BK sea and winter NAO may not be causal is Peings, 2019 (doi:10.1029/2019GL082097).

L41: Warner et al. 2020 do not suggest tropical forcing as a common driver of sea ice and the NAO. They did suggest this may be the case for other aspects of the mid-latitude circulation, but not the NAO.

L198-207/Figure 1: The main takeaway from this is that OCE reduces the sea ice everywhere. The changes in variability are also entirely consistent with just a reduction in sea ice extent everywhere .

Figure 1 and 3: I think that it would be more useful to show plots for OCE-ERA5 as well to make the improvements easier to see.

Figure 2: What does the sea ice variability look like in the Barents-Kara sea in CTRL? There is substantially less variability connected with the EOF1, but is that because it is in other EOFs or because there is substantially less variability? I don't think it is latter based on Figure 1.

L218: sea surface temperatures

L243: Blackport et al. 2019 did not do this and has little to do with the NAO.

L279-281: I don’t understand this. The Bering sea is a completely different region which will have different impacts on the circulation, so I don’t see how it can be the equivalent to the BK Sea.

L281-283: There has been a lot more work looking at the response/correlation to sea ice in different regions than what is portrayed here (e.g. Screen 2017 doi :10.1175/JCLI-D-16-0197.1, McKenna et al .2017 doi:10.1002/2017GL076433, Blackport et al. 2019). The reason there has been more on the Barents-Kara is because there are stronger links in both observations and models.

L307: I don’t think any study, including Koenigk and Brodeau (2017), state that the observed signal is a spurious signal. This study, and others like it, express caution that it could be. There is a lot internal variability and spurious signals can arise in model simulations of similar length to the observed record even when there is no/weak signal overall. It also the case that the recent observed correlation appears to be unusually high compared to the longer record(Kolstad and Screen 2019).

Figure 5a: The fact that all simulations start off with a higher correlations than over the whole period intrigues me. Because all simulations start of the same ocean state, is it possible that they happened to be initialized in particular state of low frequency variability that contributes to a stronger correlation?

L317-319: I don’t understand why that would suggest it is coincidental. You wouldn’t be able to rule it out, but that is very different from suggesting that it is.

L322-323: Is it actually the case that each 30 year period is statistically significant from 0? I doubt that this is the case given that some 30 year periods show correlations close to 0.

L328: How often do they attain correlations that exceed the observed correlation?

Figure 5b: I think it is misleading to plot it this way because the overlapping 30 year periods are obviously not independent. There are really only about 6 independent data points in the OCE distribution. I don’t doubt that the differences are statistically significant, but this plot likely exaggerates the perceived significance.

L350-352: Isn’t it more relevant to know whether or not these correlations are statistically different from the correlations in OCE or CTRL?

L360-368: The regressions of November zg500 on November sea ice is likely not the response to the sea ice anomalies(at least not entirely). Instead, a large part of it is the atmospheric circulation that forces the sea ice anomalies. The sign of the NAO is opposite to what would be expected if it was the response. Unless the authors are arguing that the initial response to reduced sea ice is a positive NAO, but that contradicts what is shown in Figure 7.

L380-385:This negative feedback between the sea ice and NAO was identified in a number of studies including Strong et al. 2009,doi:10.1175/2009JCLI3100.1 .

L435: This is not reproducing the result of Blackport et al. 2019. They examined the regression between winter circulation and winter sea ice, not November sea ice.

L425-456/Figure 9. I am not sure I understand the point of this analysis. The authors have already established that feedback between sea ice and the NAO, so I don’t see how the NAO forcing of the sea ice could explain the difference between OCE and CTRL. There could potentially by a stratospheric pathway where there are causality issues, as suggested by Peings 2019, but the authors have effectively argued against this being the reason for the improvement by showing that difference can entirely be explain based on the daily coupling. The authors should more clearly explain the motivation for it, or remove it.

L463:Figure 9->Figure 10

L516: How would the varying model biases contribute to the inconsistencies within long simulations from a single model? Note that there also appears to be large inconsistencies between short periods in observations as well (Kolstad and Screen 2019).

-What do the trends in NAO look like? If the improved correlations represent a response to sea ice loss, it may be expected that there is more negative NAO trends in the OCE simulations. This could have implications for the midlatitude response to sea ice loss and global warming, not only for seasonal predictions. This may be a bit beyond the scope of the study, and a larger ensemble may be needed to find robust differences, but it would really simple to check.

Citation: https://doi.org/10.5194/wcd-2021-61-RC1
- AC1:
  'Reply on RC1', Kristian Strommen, 14 Feb 2022
  We thank the reviewer for their constructive and insightful feedback. Before responding to the key points made, we need to point out that last November the authors were able to obtain additional supercomputing units and have since used these to double the ensemble size from 3 to 6. The new ensemble members have proven to be consistent with the original members, which adds considerable confidence to the hypothesis that the stochastic schemes are genuinely improving the teleconnection. All Figures and diagnostics in the revised version of the paper have therefore been expanded to include these members. As a result of this, some details of the discussion have changed. Because most of these changes are in line with suggestions made by the reviewers, we hope this will not cause a nuisance to the reviewers, who might rightfully wish we had waited with submitting in the first place until this larger ensemble was obtained. Unfortunately, it was not clear prior to submission if the required computing units would be obtainable.
  Concerning the choice of sea ice region, we agree that a differing choice for the model and observations leaves us open to accusations of cherry-picking, and at the very least some discussion of sensitivity of results to the choice should have been included. We have now done more extensive testing of the use of different regions and can report the following. If one uses Barents-Kara for all data sets, then the conclusions are qualitatively similar, in that there is a consistent improvement of the ice-NAO correlations when adding stochasticity, and these improvements can be explained using the LIM model. However, quantitatively speaking the results are somewhat weaker, with the correlations in OCE being generally smaller (and not as comparable in magnitude to ERA5) when using Barents-Kara as opposed to Barents-Greenland. We also found that using just the Barents sea for the model gave quantitatively almost identical results to using Barents-Greenland, and the increased ensemble size now singles out the Barents sea anyway (revised Figure 4). On the other hand, the Barents November sea ice in ERA5 has zero correlation with the NAO: it is definitely necessary to extend the region out to the Kara sea for ERA5.
  
  After careful consideration, we believe it is still justifiable to somewhat adjust the sea ice region in the model compared to observations. The results discussed above have led us to use Barents-Kara for ERA5 and Barents for EC-Earth. The difference between the two regions is therefore even smaller now, with EC-Earth simply omitting the Kara sea. An equivalent table to Table 1 which uses Barents-Kara for all data sets will be included in Supporting Information of the revised paper, and we will clearly highlight and discuss the fact that qualitatively (but not quantitatively) similar results are obtained with this uniform choice. We hope this will go a long way towards addressing the reviewer’s objections.
  
  We now expand on our justification. There are two key points. The first is that both the mean state and the seasonal evolution of the sea ice edge is clearly different in CTRL compared to ERA5.It’s true that the bias of CTRL and OCE in the mean sea ice in the Kara sea (Figure 1a,b) is on the order of 10% less ice than in ERA5, and this not huge on the face of it. But the biases in the standard deviation (Figure 1c) clearly point to a big change in how far equatorward the ice edge tends to extend to every year: the sign of the pattern (negative near pole, red equatorwards) says that in CTRL, the ice edge tends to extend further outwards. This is important because the heatflux anomalies are dominated by the variations in the location of the ice edge: if the ice edge has moved, so will the largest heatflux anomalies. The 10% difference in the mean state is therefore in all likelihood misleadingly small, smoothing out more important interannual variations in the ice edge in the Kara sea. This change in the seasonal ice edge evolution in EC-Earth3 is further corroborated by the visibly different EOFs (Figure 2). It is true as the reviewer states that the local magnitude of the patterns in the Barents-Kara region are similar between ERA5 and OCE, but clear visible differences still remain. In ERA5, the typical November pattern is evidently an increase (decrease) of ice in Barents-Kara and a decrease (increase) in the Barents sea closer to Russia as well as in the Laptev sea. In OCE, the typical behaviour is an increase/decrease along the entire ice edge from Greenland up to Chukchi. In particular, sea ice anomalies in Barents-Kara may, in the model world, be expected to often come hand-in-hand with sea ice anomalies elsewhere that don’t look anything like that of observation. Since it has been noted in previous papers ([1,2] and others that the reviewer themselves provide) that sea ice anomalies in regions other than Barents-Kara may have different, even opposing, impacts on the atmospheric circulation, we do not think such possible effects can be considered negligible.
  
  The second key point is, as discussed in our paper, that there is evidence in the literature that the teleconnection depends on the atmospheric mean state, in particular the position of the storm track. Since the storm track is almost always biased to some degree in climate models, it does not seem unreasonable to suggest that the sea ice region in models best placed to interact with the storm track is slightly different than that in observations.
  
  The fundamental issue here is that external forcing, including that from teleconnections, very often projects onto the dominant modes of variability (e.g. [3,4]). Not only do these differ between models and observations (Figure 2), but in the case considered here, there is non-linearity embedded at both ends: with sea ice as discussed in [1] and with the North Atlantic Oscillation in the visible multimodal behaviour of the jet [5]. We therefore take the view that model biases, in both the mean and the variability, cannot be easily ignored, and indeed many studies have examined the influence of such biases on teleconnections (e.g. [6] for just one recent example). There are also several precedents in the literature for using sea ice EOFs to compute Arctic-NAO teleconnections (e.g. Wang, Ting and Kushner 2017, or the Strong et al paper you pointed us to in your comments), and such approaches would inevitably highlight different regions in models vs observations. It is certainly true that allowing for regions or patterns to shift in models opens up the possibility of cherry picking, and so sensitivity to such shifts should be clearly discussed, which we failed to do. But the flip side is that allowing for no model-dependent diagnostics may overly penalise models and give the impression that model skill (or inter-model consensus) is weaker than it is.
  
  It is the authors’ impression that there has perhaps been too little consideration in the literature on potential (small) shifts in the key sea ice region, and we think this is an important point that we wish to highlight as part of our work. The revised version will expand on all the above points to better justify the choice made. Of course, we accept that the reviewer may disagree on some or indeed all of the above points, or be of the opinion that a proper justification of the above points would require more work which would likely be inappropriate to include in this paper. We hope that if this is the case, that our emphasis of the qualitatively similar results obtained with Barents-Kara, and the change from using Barents-Greenland to Barents for the model, will nevertheless allow you to consider your objection adequately addressed.
  
  We would challenge the assertion that “most models tend to have a weak connection”. The range of correlations between Barents-Kara and the NAO found across the coupled CMIP6 models is very well approximated by a normal distribution with mean 0, standard deviation 0.17 and a 95% confidence interval of 0.28. While the exact mean of 0.018 is positive, almost half the CMIP6 models have negative correlations. The EC-Earth3 CTRL ensemble, with its average correlation of -0.06, is in no way an outlier in this distribution and is in fact dead average: this was extremely briefly noted in the submitted paper (line 337), and we have now made this more clear by revising Figure 5 to include the CMIP6 distribution. The inclusion of additional ensemble members has also now produced CTRL members with slightly positive correlations in the period 1980-2015, so there seems to be even less cause to find EC-Earth3 particularly objectionable. Its biases in the mean ice state are also in no way notably worse than many other models.
  
  Note that the slightly positive mean of the CMIP6 distribution is consistent with findings in earlier literature reviews which report that `most’ models show a positive association, but it is clear that this consensus is weak. Another point here is that many of the experiments carried out in the literature are not directly comparable with each other: e.g. many model experiments analysing the role of sea ice use fixed anthropogenic forcings, while the models we consider here are using historical forcings. This may account for any remaining discrepancies.
  
  That being said, the point that the stochastic schemes may have differing impacts in other models should have been emphasised more. There are examples from earlier work which show consensus across models in some cases and lack of consensus in others. This will be expanded on in the revised manuscript.
  
  The potential importance of the mean state is a point raised by all of the reviewers, and upon further consideration we agree. It is actually even clearer after having increased the ensemble size that coupling alone isn’t sufficient, and it is likely a combination of coupling and mean state. This will be expanded upon further in a response to another reviewer.
  
  References:
  1. Koenigk, T., Caian, M., Nikulin, G. et al. Regional Arctic sea ice variations as predictor for winter climate conditions. Clim Dyn 46, 317–337 (2016). https://doi.org/10.1007/s00382-015-2586-1
  
  2. Sun, L., Deser, C., & Tomas, R. A. (2015). Mechanisms of Stratospheric and Tropospheric Circulation Response to Projected Arctic Sea Ice Loss, Journal of Climate, 28(19), 7824-7845.
  
  3. Shepherd, T. Atmospheric circulation as a source of uncertainty in climate change projections. Nature Geosci 7, 703–708 (2014). https://doi.org/10.1038/ngeo2253
  
  4. Corti, S., Molteni, F. & Palmer, T. Signature of recent climate change in frequencies of natural atmospheric circulation regimes. Nature 398, 799–802 (1999). https://doi.org/10.1038/19745
  
  5. Woollings, T., Hannachi, A. and Hoskins, B. (2010), Variability of the North Atlantic eddy-driven jet stream. Q.J.R. Meteorol. Soc., 136: 856-868. https://doi.org/10.1002/qj.625
  
  6. Karpechko, AY, Tyrrell, NL, Rast, S. Sensitivity of QBO teleconnection to model circulation biases. Q J R Meteorol Soc. 2021; 147: 2147– 2159. https://doi.org/10.1002/qj.4014
  
  Citation: https://doi.org/10.5194/wcd-2021-61-AC1
RC2:
'Comment on wcd-2021-61', Anonymous Referee #2, 19 Nov 2021

Strommen and Juricke explore the question of why Arctic-midlatitude teleconnections in climate models are generally weaker than observed by employing a modified version of EC-Earth3 which includes stocasticity in the sea ice and ocean components. The study finds that the Nov. sea ice - winter NAO teleconnection is improved in the model integrations with stocasticity and this appears to be mainly related to stocasticity in the sea ice component. I find this result very interesting; however, like the authors, I am left wondering whether OCE may be getting "the right answer for the wrong reasons". I recommend some major revision of the manuscript to address the key issues below:

1. The authors argue with respect to Figure 9 that OCE and ERA5 have similar daily timescale forcing, suggesting that OCE is getting things right for the right reasons. I'm not entirely convinced of this given that the b coefficient in OCE is larger than ERA5. It would be interesting to see the coupling between ice and other variables using the LIM to provide a bit more evidence that OCE is getting things right, for example the relationship between ice and a variable that is more thermodynamically connected to ice. The authors also note that the difference seen in Figure 9 could be due to chance. If so, can you show similar plots as Figure 9 for each ensemble member of OCE? If chance plays a role maybe there is some evidence of this if all ensemble members are examined individually.

2. Figure 9h and 9i seem to suggest something is quite unrealistic about how this model represents fall sea ice variability. In the Blackport et al. (2019) paper, they examine a version of EC-Earth, EC-EarthV2.3, I believe. Are you able to reproduce their findings with EC-Earth3P used here for the CTRL runs (it would be great to see plots similar to their Fig. 4c, f, and i? It seems that you are getting very different patterns (Fig. 9h), which makes me concerned about the suitability of this model for this study.

3. Could the direct effect of mean state changes be quantified using AMIP-style runs with monthly sea ice and SSTs from the coupled OCE runs? I think it is important to get a better sense of what is going on - is it the stocasticity itself or the effect of the stocasticity on the mean state. Untangling this has implications in terms of how this study informs model development.

Minor comments:

1. lines 25-30: lots of issues with parentheses that need to be tidied up.

2. line 27: You may want to say "negative NAO" rather than just "NAO" for clarity.

3. Section 2: there are many different abbreviations/acronyms for the model used in this section. After you finish describing the various configurations, can you tell the author which name you are going to stick with throughout the paper? Something like, "Hereafter, the model will be referred to as...".

4. Line 153: What prescribed SSTs and sea ice?

5. line 162: extra parentheses

6. line 218: Figures -> Figure and ssea -> sea

7. Table 1 caption: there is a missing section number - just shows ??

8. line 405-406: I don't think this is the correlation you are showing. It's sea ice and NAO, correct?

9. FIgure 9i does not really look like Figure 9g to me. And it seems a bit strange that Fig. 9h does not look anything at all like Fig. 9g.

10. line 463: FIg. 9 -> Fig. 10

Citation: https://doi.org/10.5194/wcd-2021-61-RC2
- AC2: 'Reply on RC2', Kristian Strommen, 14 Feb 2022
  
  We thank the reviewer for the insightful comments, and bring their attention to the increased ensemble size obtained since submission: see the response to RC1 for further details.
  The main concern raised is about Figure 9, which suggested that perhaps OCE was recovering a correct looking teleconnection for the wrong reasons. After doubling the ensemble size the mismatch with observational data has been notably reduced. The improved teleconnection in OCE still appears more driven by the forcing of the ice on the atmosphere, but a clear NAO signal is now also seen for years where the atmosphere drives the ice. We hope this will help reassure the reviewer.
  It is perhaps also worth pointing out that we are either way still suggesting that there is “something quite unrealistic” about the CTRL model, to paraphrase the reviewer. We are suggesting that the lack of a teleconnection is unrealistic, and that its improvement in OCE is a genuine improvement. The point being that this is an important result even if CTRL is unrealistic in some ways, because it implies that the considerable intermodel spread in reproducing the observed teleconnection may to a large extent be due to model biases rather than internal variability. If that is the case, then the teleconnection may be much more robust than many studies suggest it is. But in any case, EC-Earth3 does not seem to be a particularly poor model: see the response to RC1 for more on that.
  Note that the EC-Earth figures from Blackport et al. 2019 are not reproducible with our data. While the model used is closely related, the EC-Earth experiments considered in Blackport et al essentially use fixed forcings (they use 400 5-year simulations each covering the same period), while our experiments are 65 successive years with historical forcings. Identical diagnostics would not be expected as a result, so we don’t see any discrepancies here as a point of concern.
  
  As for plots elucidating the mechanisms more clearly, we produced some additional lag correlation/regression plots between sea ice and heatfluxes (this also being suggested by RC1) as well as some other diagnostics to help clarify. While these do hint at some small improvements in OCE to the daily time-scale local coupling between ice and heatfluxes, our analysis generally suggests that the flaws in CTRL are not clearly visible in the local thermodynamic coupling. Instead, the errors in CTRL appear to be primarily due to errors in the subsequent adjustment and growth of the initial pressure anomaly across the North Atlantic and ice edge more broadly. In fact, this is already what the LIM results suggest, but this was not really made clear in the submitted manuscript. All this will be discussed (and the relevant new plots included) in the revised paper. Unfortunately, a thorough analysis of errors in the more remote response is not going to be possible to include in this already lengthy paper and will have to be left for future work (though we include some speculation).
  Finally, regretfully no time or resources are available to carry out experiments of the sort you describe at present, though we agree they would help. The role of the mean state (also raised by the other reviewers) is discussed in more detail in the revised manuscript in any case, but it has not proven possible to decisively nail down the contribution of mean state vs coupling in our analysis. Besides the complications of local vs remote responses discussed above, it is likely that the inherently non-linear component to ice/heatflux coupling plays a role which our analysis, entirely based on anomalies, cannot detect. Possible non-linear diagnostics that could be explored in follow-up work are discussed in, e.g. Caian et al. An interannual link between Arctic sea-ice cover and the North Atlantic Oscillation (2018), Clim Dyn. We hope that the extra diagnostics and discussion, including of potential future work, will satisfy the reviewer anyway.
  
  Citation: https://doi.org/10.5194/wcd-2021-61-AC2
RC3:
'Comment on wcd-2021-61', Anonymous Referee #3, 01 Dec 2021

This is an interesting paper on Arctic-midlatitude teleconnections. While focusing on the role of stochastic parameterizations, the paper also provides useful and novel physical insight into the possible factors affecting the representation of this teleconnection in climate models. The paper was clearly and logically written, and the results interesting, so I enjoyed reading it. I do however have several comments regarding the physical interpretation of the findings.

Main comments:

1) Interpretation of Fig. 6

I’m not sure I fully agree with the interpretation of the lagged relationships between Z500 and sea ice – or I may have misunderstood the authors. The text L360–368 seems to imply that the Z500 anomalies are a “response” to the sea ice at all lag times. This makes sense at positive lags (December onwards, when Z500 lags the sea ice), but for the November anomalies (1st row of Fig. 6) we also need to consider the possibility that it is the circulation driving the sea ice, rather than the other way around. I think this is indeed what is happening: the Z500 anomalies are consistent with northerly flow into the Barents sea area, which would drive enhanced sea ice concentration. I believe this also explains why the November Z500 anomalies are so consistent among ERA5, CTRL and OCE. In any case, the possible two-way interaction between Z500 and the sea ice needs to be discussed in the context of Fig. 6.

2) AMIP results

I am still unclear as to why the AMIP simulations show no midlatitude response to the sea ice anomalies. I understand the result in Fig. 7 that there is two-way coupling, and the NAO → ice effect is absent from AMIP. But the ice → NAO effect should be in AMIP, so why don’t we see that? Also, is this result consistent with any prior work looking at AMIP runs with other climate models?

3) Coupling timescales

I feel some clarification is needed on the timescales at play in the sea ice–NAO coupling. Figure 7 suggests the coupling happens on daily timescales; but it’s not obvious how to reconcile this with the finding that the NAO responds to November sea ice anomalies on the timescale of a *season* (DJF). My interpretation would be that the sea ice anomalies are relatively persistent (Fig. B5), so the November anomalies are a skillful predictor of those occurring later in the winter season – and these anomalies continue forcing the NAO through the winter. Is this consistent with the authors’ thinking? Please clarify in the paper.

4) Coupling in CTRL

Figure 8b suggests the BG sea ice in CTRL does have a measurable impact on the NAO, which appears at odds with the lack of an ice → NAO relationship in Fig. 7. Is this because the BG sea ice varies so little in CTRL – so that even though the effect is there, the impact is minimal because there’s almost no forcing?

5) NAO definition

I was unclear as to the NAO metric as defined L166, and since this is key to the result, the definition seems important. I don’t understand the subtraction of the daily climatology after the calculation of the PC. Why not deseasonalize the data beforehand? If using non-deseasonalized data, there is a risk that the EOFs are capturing the seasonal cycle (an externally forced signal), rather than the true internal atmospheric variability. It was also unclear to me whether the EOFs were calculated for each CTRL and OCN realization separately, or whether these realizations were concatenated prior to computing the EOFs. While it probably makes little difference, I’d favor the latter, which should give more robust EOFs – and ensures any differences among the realizations aren’t due to differences in the EOF basis.

Minor comments:

1) Please fix the citation format – the parentheses are often in the wrong places. I suspect this may be due to mixing the Natbib commands \citet and \citep in LaTeX. One example is L25, where it should be “(Hoskins and Karoly 1981)”, “(Garcia-Serrano et al. 2015)”.

2) Consider clarifying the definition of the word “deterministic” – not being a stochastic parameterization expert, I initially thought this might mean “prescribed SST” as opposed to coupled, when actually this means “not stochastic”.

Typos etc:

L52: “are a manifestation”

L169: “are computed”

L208: “to reduce”

L218: “sea surface”

L229: “Examination… supports”

L297–300: This text is a repetition of L179–183, so I suggest deleting.

L405: Strictly speaking, Table 1 shows the correlations between the LIM NAO and LIM sea ice – not LIM NAO with true NAO. The latter is shown in Fig. B6.

L423: “may have changed” → I think you mean “between CTRL and OCN”, but it’s not entirely obvious from the phrasing.

Caption of Table 1, L3: broken link to section 5.2

Figures 4 and 6: Suggest highlighting the BK and BG regions with boxes in the maps

Citation: https://doi.org/10.5194/wcd-2021-61-RC3
- AC3:
  'Reply on RC3', Kristian Strommen, 14 Feb 2022
  We thank the reviewer for the insightful comments, and bring their attention to the increased ensemble size obtained since submission: see the response to RC1 for details.
  
  About Figure 6, yes you are absolutely right that there is a 2-way interaction there which we failed to comment on. This will be included in the revisions.
  
  Yes, there is evidence in prior literature that this teleconnection is weaker in AMIP models. This was mentioned in line 520, citing Blackport and Screen (2021), though we believe earlier studies (cited in their paper) had pointed to this as well. For EC-Earth in particular, the study Caian et al. An interannual link between Arctic sea-ice cover and the North Atlantic Oscillation (2018), Clim Dyn, showed that ice/NAO links are weaker in an AMIP simulation than a coupled simulation, something they attributed to the missing coupling. Our paper provides further evidence to the importance of coupling to get a good teleconnection, though several questions remain about exact mechanisms. We show that while the initial, local ice->heatflux response appears similar for both CTRL and OCE, the subsequent growth and evolution of the anomaly is significantly better in OCE. Presumably, as you point out, the initial local anomaly would be highly realistic in the AMIP simulations, but the failure to propagate the anomaly would likely be even worse given the total lack of coupling. Caian et al. includes some other discussion on possible mechanisms here. We will discuss some simple hypotheses as well, including the alignment of the sea ice edge with the eddy-driven jet, and the importance of sea ice adjustments further afield from the source region (Barents/Barents-Kara). This will be discussed in the revised paper.
  
  Yes, exactly: the initial anomaly is long-lasting due to the persistence of sea ice, but is ultimately damped away by the opposing response of the NAO. We will revise the paper to make this clearer. More discussion about the initial local response vs more remote adjustments are also included, as per point 2 above.
  
  All reviewers have commented on the mean state, and in hindsight the minimal role we ascribed to the mean state wasn’t justified. We can’t see any meaningful difference in the November 1st initial conditions (of the ice and NAO) between CTRL and OCE, but the LIM model takes anomalies as input, which ignores any non-linear effects. Since such non-linearity is likely to be present here, our analysis can’t really address this. On balance, it is likely that the improvements in OCE are due to both the mean state and the coupling, and we will make this clearer in the revised paper.
  
  The NAO EOF was computed separately for each dataset, to allow the centers of NAO action to shift between each dataset according to differences in the mean state: this will be made clearer in revisions. We believe it is important to allow for some shifts between models to not obscure signals or overly penalise models (i.e. penalising both for mean state biases and changes to modes of variability). That being said, in this case there is little difference between the CTRL and OCE NAO, with a pattern correlation between the two of around 0.97. The results are therefore highly unlikely to change if using the exact same NAO pattern for CTRL and OCE. This will be mentioned in revisions.
  
  Citation: https://doi.org/10.5194/wcd-2021-61-AC3
EC1: 'Comment on wcd-2021-61', Camille Li, 02 Mar 2022

Thanks to the referees for their in-depth reviews and the authors for their careful consideration of the points raised. Because of rather substantial edits and a re-interpretation of the results in response to the reviews, I'm offering the referees a chance to comment further on the revised manuscript.

Citation: https://doi.org/10.5194/wcd-2021-61-EC1

Peer review completion

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

AR by Kristian Strommen on behalf of the Authors (21 Feb 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (02 Mar 2022) by Camille Li

RR by Anonymous Referee #3 (16 Mar 2022)

For final publication, the manuscript should be

accepted as is

accepted subject to technical corrections

accepted subject to minor revisions

reconsidered after major revisions

rejected

Were a revised manuscript to be sent for another round of reviews:

I would be willing to review the revised manuscript.

I would not be willing to review the revised manuscript.

Suggestions for revision or reasons for rejection

Overall, I think the authors have done a good job addressing the review comments, and the paper is nearly ready for publication. I have two remaining general comments:

First, it looks like the authors missed part of my comment #5 in the previous review, so I’m reiterating this here. For the NAO index calculation, I didn’t get why they are using non-deseasonalized data for their EOF analysis, and removing the seasonal cycle only in a second step (L175). This choice would make sense if the seasonal cycle is seen as an important component of the variability, but that’s not the case here (since the authors are deseasonalizing anyway). I’d recommend deseasonalizing before the EOF analysis. It’s entirely possible it would make very little difference to the results, but would seem cleaner to me.

Secondly, section 5.3 was somewhat hard work to read, so I’d encourage the authors to simplify the text if possible. For example, is the paragraph starting L482 useful? The following paragraph states there is a better way to test the LIM hypothesis, so why not jump to that straight away?

Minor comments:
L175: Is the EOF analysis based on NDJF data only? Please clarify.
L189: “the period is”
L235: “suggest that”
L281: “heat flux anomalies”
L337: “concerning both the”
L391–394: This is unimportant, but I think the logic behind this statement is flawed, or at least I didn’t follow it. If Kara sea ice is highly correlated with Barents sea ice, then I’d expect Kara sea ice to correlate with the NAO even in the absence of a direct physical link between the two.
L400: Does this mean the ERA5 correlation would be improved if only the Kara sea region were used?
L407: To clarify, the AMIP ensemble uses the OCE SSTs and sea ice, not the CTRL values?
L568: Word missing after the period
L651: Missing “The”
L699: “The study *of* Juricke et al.”
Caption of Fig. 4: “The ensemble members” (extra x)
Fig. 8: I’d recommend plotting this as a barplot, or at least expanding the y-axis to encompass 0. That would make it much easier to compare the magnitudes of the coefficients among CTRL, OCE and ERA5.

Hide

RR by Anonymous Referee #2 (22 Mar 2022)

RR by Anonymous Referee #1 (29 Mar 2022)

For final publication, the manuscript should be

accepted as is

accepted subject to technical corrections

accepted subject to minor revisions

reconsidered after major revisions

rejected

Were a revised manuscript to be sent for another round of reviews:

I would be willing to review the revised manuscript.

I would not be willing to review the revised manuscript.

Suggestions for revision or reasons for rejection

The authors have significantly improved the manuscript in response to my comments, but I don’t feel my comment about the use of different regions for the models and observations has been adequately addressed. The authors have changed the regions so that they are not as different as they were in the original manuscript, but they are still different and it is still a problematic. The authors go into detail about why there could be plausible physical arguments for using different regions for the comparisons (L274-288 and much longer discussion in their response). However, they do not actually use any of these physical arguments to justify the specific regions chosen. The authors do state in a few places that the choice is based in the results in Figure 1 and 2 (e.g. L626-628), but I do not see what they are seeing in these figures. There is clearly sea ice variability in both the Barents and Kara seas in both ERA5 and OCE (Figure 2) and if anything, I see bigger differences in the means and stds in the Barents compared to the Kara sea (Figure 1). This is the opposite of what is claimed. In my view, the main reason the authors use different regions is still that there is a stronger correlation in the model when only considering only the Barents Sea.

The authors have included some analysis showing that it makes only a small quantitative difference if they use the Barents-Kara Sea for all analysis and then use this to justify the use of different regions. But then why not use the same region for all analysis? This would be simpler, avoids the possibility of cherry-picking (or the appearance of cherry-picking), and is more consistent with past work that focuses on Barents-Kara sea. It also would help shorten the paper, which is quite long. It just seems like the authors are over-complicating the analysis for little benefit and plenty of downsides.

Other comments:
L40-41: This mention of Blackport at al. 2019 is misleading and unnecessary, so can be deleted. It is not about the sea ice-NAO connection (more about this later).

L79: Similar to Blackport et al 2019, Mori et al. 2019 is about the ‘warm Arctic cold Eurasia’ pattern and has little to do with the sea ice-NAO connection, so should not be presented as such. If anything, the results presented in Mori et al. 2019 would suggest that there is positive NAO response to reduced Barents-Kara sea ice and that models are underestimating this. This is the opposite of what is suggested here, so does not support this work.

L260-273: It seems unnecessary to provide these arguments to use an EOF-based method to identify the critical sea ice regions and then not even use these methods to then identify the region.

L274: “Besides the somewhat abstract consideration of modes of variability…” But the modes of variability are not even used to identify the region?

L350-353: The lack difference in trends is intriguing and could be highlighted and discussed in more detail. This would seem to contradict the idea that the differences in correlations in CTRL and OCE are because of the CTRL (and models more generally) underestimating the response to sea ice anomalies. Why would the differences in interannual variability not translate into differences in trends in the NAO? This is particularly important because I could see the results presented here regarding the interannual correlations be misinterpreted to have implications for climate change, when it appears to have little effect. It is also interesting that the models show a robust negative NAO trend over 1950-2015, while the observed winter NAO trend is clearly positive and well outside of the model distribution shown Figure 2 of the response. Because this is outside the scope of the paper, the authors do not need to do additional analysis, but some discussion would be useful.

Section 4.2: What are the differences in CTRL and OCE over the entire period (1950-2015)? Looking at Figure 5a, the differences will likely be much smaller than only over the most recent period.

Figure 5 caption: ‘three’ should be ‘six’

L365: Another difference is the exact months used. A number of studies have looked at the correlation between November-December sea ice and the subsequent February circulation (e.g. Blackport and Screen 2021, De and Wu 2019 doi: 10.1007/s00382-018-4576-6).

L368-369: While CTRL may not be unusually weak compared to CMIP6 mean, they are more negative than the CMIP6 mean. This would be a lot easier to see if the CTRL values were plotted on Fig 5b like they are with the OCE.

L369-371: Whether the CMIP6 distribution changes or not seems like an irrelevant point, so should be deleted. This will depend more on the size of the CMIP6 ensemble than how well the CMIP6 and CTRL ensemble agree or not.

L425-431: Blackport et al. 2019 is not relevant in other places in the manuscript, but it is relevant for this discussion. The pattern seen in the instantaneous November regressions are very similar to the instantaneous DJF regressions found in Blackport et al. 2019 that they concluded were because of the atmosphere forcing the sea ice.

L566-576: The authors are again misrepresenting Blackport et al. 2019. They show that a positive NAO is associated with a negative sea ice anomaly in DJF. This is clearly not 'nearly identical' and is in fact the opposite to what is found in Figure 9 here. More generally, it is somewhat concerning that the authors are continuing to misrepresent a number of different studies on this topic even after it is pointed out. It makes me wonder whether the authors are misrepresenting other studies that I am not as familiar with and do not have time to carefully check.

L591-592: Are there citations for this statement?

L651: It looks like the start of the sentence was cutoff?

L653: Again, Mori et al. 2019 is not about the sea ice-NAO connection.

Hide

ED: Publish subject to revisions (further review by editor and referees) (20 Apr 2022) by Camille Li

I’ve now reviewed the reports of the three referees along with the revised manuscript. The reports are quite disparate in their opinions on the manuscript, and I believe I understand why. I tend to agree that this is a very worthwhile set of experiments showing new and interesting results, but also that the manuscript as it stands is not quite ready for publication.

Overall, the result that the ice-NAO correlation is different in OCE versus CTRL is convincing, and as such, an exploration of the reasons is certainly warranted. The authors have performed a number of analyses to get at the reasons. I believe where the third reviewer’s concerns lie is in the interpretation of these analyses, which is very difficult to follow in places, and could use more balance/transparency. There are statements appearing in different places in the manuscript that seem contradictory, some statements seem at odds with what I see in the figures, and at times the discussion has an appearance of over-emphasizing certain points while dismissing others. In short, it is clear that the stochastic schemes are doing something to the ice-NAO teleconnection – probably related to the ability of ice to influence the NAO, according to the LIM analysis. However, I’m not sure the conclusion that it is due to differences in local ice-atmosphere coupling is well supported by the manuscript as it stands.

Here are some examples of where I had difficulty seeing/following the arguments (more examples in the report of referee #3).

- Lagged correlations: I find Fig. 7 and Fig. B7 equally important, and Fig. B7 especially so for understanding mechanisms, and thus am not sure why both should not be in the main text. Furthermore, I don’t understand some of the statements made about B7. Fig. 7 shows that, when ice leads the NAO, OCE and ERA5 are behaving in a similar way while CTRL is doing womething different (all okay until here). But Fig. B7 shows that the ice-flux lead-lag relationships (i.e., the processes) are operating the same way in both CTRL and OCE. Why do you say that Fig. B7 demonstrates that “the CTRL model is simply failing to propagate the same initial anomaly correctly” (L524) while not mentioning that the same holds for OCE? Also, it doesn’t seem to me that this statement is accurate either: “Figure B7 gives some hint that the way the ice in the CTRL model adjusts to heatflux forcing is unrealistic, which may result in biases in the non-local adjustment. The same Figure suggests that these biases are reduced in OCE, suggestive of improved coupling.” In fact, doesn’t Fig. B7 suggest that it’s not the local coupling that is making the difference between OCE and CTRL?
- Related to the above, it seems like one of the main points is that atmosphere-ice coupling (and not atmosphere-ocean coupling) is key to getting the teleconnection, but the discussion seems to circle the point in many places. For example, while much is made of the generally “improved” coupling in OCE compared to CTRL, section 6.3 (especially statements like L617-619) and the concluding point on L657 talk specifically about how the atmosphere-ocean coupling does very little. It seems like it would have been useful to run an experiment with just the stochastic ice scheme (not the ocean schemes), which would allow firmer conclusions and cleaner/more direct writing.
- Fig. 9: Shouldn’t the top row be the same as the bottom row of Fig. 6? The “ERA All” pattern is dominated by “ERA Atmos2ice”, while for both CTRL and OCE, the All pattern is dominated by Ice2atmos. How does this fit with the LIM or the idea that the ice forcing is somehow stronger/better in OCE?

I ask the authors to revise the manuscript taking into account all the comments of the referees, as well as some additional comments from me below. This would include addressing the two main comments of referee #1 (removing seasonal cycle and clarifying text) and the various comments of referee #3 about clarifying/streamlining the text and using references appropriately. I leave it to the authors to decide whether or not to change the definition of the Barents-Kara region, but the comments of referee #3 on improving the discussion of similarities/differences in Figures 1 and 2 should be considered regardless. (Related to this, the colour scale of Fig. 4 should probably be adjusted to better show spatial features of the correlation structure, and also to show more of what’s happening in CTRL. In c-f, the 95% ci is +/- 0.13 right? So it would be fair to show correlations at least as small as around 0.1.)

Following comments from referee #1, #3 and my own assessment, I would also encourage the authors to step back and reassess the manuscript as a whole in doing these revisions. I believe it would benefit the manuscript if the authors were to reorganize / eliminate / streamline the text rather than to just add more text.

Other points:

The new text in 4.1 justifying the use of different sea ice regions could be presented in a much clearer and more condensed way. The EOF methods are set up as somewhat of a strawman (text starting L266 “This latter method has the advantage…”) only to be taken down later (starting L289). I understand that this text was added to address one of the reviewers concerns, but I think this is better done via (a) the sensitivity tests presented later and (b) discussion/interpretation of the results.

L32-35: These two sentences as written could be interpreted as separate, contradictory findings. I think this text need some editing to reflect the fact that ice-NAO correlations are weak when the averaging period/simulation is long (first sentence), but can be stronger and positive or negative when the averaging period is shorter, i.e., long simulations are subsampled (second sentence). This second part is actually true for many models, not just a single one – e.g., CESM as shown in Kolstad and Screen, and a range of LENS experiments and CMIP5/6 models as shown in Siew et al.

L161: “in the same way by initial condition perturbation” -> “by initial condition perturbation, as above”

L185-187: What about the additional simulations (SPHINX, CMIP6, HighResMIP)?

L196: Can you add one sentence explaining why different statistical tests are used for the std dev of SST and sea ice?

L257-259: “to have a bigger impact” compared to what?

L263:264: Not sure this makes sense - to regress a “region” against gridded pressure data or the NAO index? Also small grammar issue with “regressing”.

Fig. 2 – EOF1 of SIC for OCE doesn’t look more realistic than that for CTRL – in fact, maybe less.

Footnote 2: I understand the first part of the sentence, that the teleconnection might only emerge when the storm track is in a favourable position, but how does it follow that climate model biases would promote shifts in the key region? Perhaps part of the problem is that I’m not clear what biases or shifts we’re talking about – storm tracks, ice line, something else?

L291: “prescribe Barents-Kara across all models” needs rewording

Fig. 5: In panel b, where is there only one one OCE member (dashed blue line) with correlation greater than ERA5 (dashed black line), while Table 1 suggests there should be 2 members?

Section 5.1: Section 3 shows small improvements in the mean state of OCE compared to CTRL for some features (e.g., sea ice in the Barents-Kara) but certainly not others (L246 mentions that the mean SST bias shows no improvement. This makes the hypothesis stated on L405 a bit confusing/misleading. In addition, I’m not sure Fig. 3 should be referenced on L548, as it more or less contradicts the comment on L246.

Sections 5.1/5.2: The AMIP experiments certainly suggest that the ocean mean state is not the answer, but it in the interest of understanding the implications, it should be mentioned that if internal atmospheric variability plays a role, then prescribing sea ice would also be expected to destroy the ice-NAO correlation. The Blackport and Screen 2021 JClim paper is very relevant for this interpretation (even though it does not address the ice-NAO teleconnection directly).

Section 6: The goal should be either to provide a more balanced discussion of the existing results or to really pin down the ice-atmos coupling as critical. Please consider whether this section is necessary.

Discussion/summary: In general, I like the idea of bullet points in the summary, but eight is probably a bit too many. Also, please be sure that summary statements about the role of mean state vs coupling in creating the differences are accurate and well supported by what has been presented in the manuscript, i.e., what is actually improved or not improved in OCE versus CTRL should be clear from figures, try to summarize if a certain feature seems to contribute to OCE vs CTRL differences in one analysis but not in another, etc.

* In addition, please proofread for small typos, grammatical errors, missing articles, etc. throughout.

Hide

AR by Kristian Strommen on behalf of the Authors (30 May 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (07 Jun 2022) by Camille Li

RR by Anonymous Referee #1 (21 Jun 2022)

For final publication, the manuscript should be

accepted as is

accepted subject to technical corrections

accepted subject to minor revisions

reconsidered after major revisions

rejected

Were a revised manuscript to be sent for another round of reviews:

I would be willing to review the revised manuscript.

I would not be willing to review the revised manuscript.

Suggestions for revision or reasons for rejection

Overall, the manuscript is substantially improved. I like that the authors have shortened and simplified the paper. There are still a number of issues with the paper, however, I don’t think they should be too difficult to address. It is still not clear what about the ice-ocean-atmosphere coupling is causing the changes in the OCE. The authors discuss some ideas, but it is very speculative, not clear, or is sometimes contradicted by what is shown in the figures (see specific comments). I recommend acceptance after these comments are addressed:

Abstract: I think the authors should say something in the abstract about how it is not clear what is causing the stronger correlations in the simulations with stochastic parameterizations.

L33: I don’t understand this statement. Why would the signal be much smaller over shorter time periods? Wouldn’t it be that the signal is the same over shorter time periods, but that it is harder determine the signal because there is too much noise?

L38/footnote 1: I certainly agree with the authors that the sea ice record is more uncertain further back in time, which questions some of the results from Kolstad and Screen 2019, particularly the results from the early 20th century. However I think the authors are still misrepresenting their analysis and results here. They use multiple datasets, not only the HadISST and some of the strongest negative correlations are seen in more recent periods (after 1950) which likely are more certain.

L53: This is misrepresenting Blackport and Screen 2021, or maybe I am not understanding what the authors are saying about it. What does “the overall signal is too small to be robust” mean? Blackport and Screen 2021 find that there is a weak signal between sea ice and the NAO in coupled models.

L313-330: I am not sure how useful this discussion is. It is very speculative, but it could be interesting if it was backed up by analysis. For example, what does the sea ice variability look like before 1980 vs after in OCE? Is there substantial variability in the Greenland Sea before 1980, but not after? How do these compare to observations (not only the differences like is shown in Fig 1, but the actual variability in each)?

L369: Strong et al 2009 is an observational study with no climate model analysis, so shouldn’t be included here.

L382-385: What am I supposed to be looking at in Fig B4? OCE and CTRL look very similar around the Barents-Kara Sea. There are differences in the North Atlantic, but these are likely driven by the NAO and are likely not a driver of the NAO.

Figure 8/10: The sign conventions for the lags are confusing for Fig 8 and 10. Figure 8 has negative lags for sea ice leading the NAO, but figure 10 has negative lags corresponding to sea ice lagging the heatflux. Because sea ice is the common variable between the two plots it would make more sense to be consistent and have negative lags in both plots correspond to sea ice leading (or have them both lagging). It would also be helpful to have labels on the plots what is leading and lagging (e.g. "sea ice leading the NAO" on the left hand side of Fig 8).

L476-484: I don’t follow the logic here. Why would the decreased between-realization variability of the sea ice - heat flux relationship lead to a more realistic sea ice - NAO teleconnection? Why would this be more important than the ensemble mean?

L491: What about Figure 10 suggests this?

L492: Why would the anomalous upward heat fluxes around the Greenland and Labrador sea lead to a positive NAO? These differences in heat flux can be explained by the NAO forcing the sea ice/ocean. A positive NAO leads to cooling around Greenland (seen in Fig B5), which leads to the anomalous heat flux from the ocean to atmosphere.

L485-498:Aren’t these explanations contradicted by Figure 8 and 9? Figure 8 and 9 suggest that the differences between OCE and CTRL occur because of the initial response to the NAO on daily timescales, but this explanation requires processes that would occur on weekly and monthly timescales.

L537-538: I don’t think this accurately reflects the results of Blackport and Screen 2021. They show good agreement across models (the models agree that the connections are weak).

L537-539: I don’t follow the logic here. Why would models having inadequate coupling lead to larger spread between models or even within a model? If anything, CTRL has less spread across the ensemble (Fig 3), which would contradict this statement.

Hide

RR by Anonymous Referee #2 (28 Jun 2022)

For final publication, the manuscript should be

accepted as is

accepted subject to technical corrections

accepted subject to minor revisions

reconsidered after major revisions

rejected

Were a revised manuscript to be sent for another round of reviews:

I would be willing to review the revised manuscript.

I would not be willing to review the revised manuscript.

Suggestions for revision or reasons for rejection

Overall, I find the organization and readability of this paper much improved. I think the streamlining the authors have done around the speculation of mechanisms is helpful, although I also appreciated the thorough analysis in the previous iterations. I think the challenge of writing about the influence of stochastic parameterizations in climate models is explaining why they lead to the improvements that they do. I think this paper is a valuable contribution to the literature in the sense that it demonstrates that a more robust connection between Nov. BKS SIC anomalies and the NAO can be achieved, but there is more work to be done to understand why. Further experiments are needed and the authors have added more about proposed new experiments in the Discussion section.

Main Comment:
I still find the discussion of the LIM somewhat hard to follow. I guess my question is: if the assumptions of the LIM are not appropriate for the CTRL simulation, as the authors conclude, then what does the LIM analysis add to the paper? As a reader, I am left wanting to gain more insights from this section.

Minor Comments:
Line 95: extra “the” before “land surface”.
Lines 324-326: this seems quite speculative. are there no studies that have looked at this in other models for pre-industrial control integrations?
Figure 10: I am a bit confused about Figure 10 and what we can conclude from this. If I consider the arguments of Blackport et al. (2019), at negative lags, when the correlation is positive, doesn’t this represent a situation where the atmospheric circulation is driving the ice? Should we not be considering the positive lags to better understand the implications for the Nov. BKS-DJF NAO relationship? Can the authors clarify?

Hide

ED: Publish subject to minor revisions (review by editor) (01 Jul 2022) by Camille Li

AR by Kristian Strommen on behalf of the Authors (11 Jul 2022) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (19 Jul 2022) by Camille Li

Thanks to the referees for their thoughtful reviews, and congratulations to the
authors for a nice study on the role of stochasiticity in surface coupling for
teleconnections in climate models. I am happy to accept this manuscript for
publication subject to a number of final technical corrections.

TECHNICAL CORRECTIONS

There are inconsistencies in the spelling of heatflux / heat flux throughout
the manuscript.

L35: long climate simulations of just a single model -> long climate model
simulations OR long climate simulations of CMIP5 and CMIP6 models OR similar...

L39: Suggest to remove "seriously", but keep the footnote, as I believe this
will strike a good balance wrt reviewer #1's concerns.

L54-57: The addition of Baker et al. 2018 is useful here - I agree that their
study tells us we should not expect all climate models to represent the
relevant ice-NAO processes correctly. I believe the last two sentences are not
quite accurate, however - they suggest that Blackport and Screen 2021 and Siew
et al. 2021 may find that the multi-model mean ice-NAO relationship is too weak
because it is heavily influenced by the "bad" models. In fact, both Blackport
and Screen 2021 (Fig. 9) and Siew et al. 2021 (figures in supplementary
material) also look at individual models, and none produce a long-term ice-NAO
relationship as strong as the 35-year relationship which is the focus here. I
don't think it's necessary to go into more detail on individual models here,
but I would recommend the authors remove/modify the last two sentences, and
perhaps just use Baker et al. to make the valuable point that we cannot rule
out the possibility that model error causes the signal to be underestimated in
climate models.

L402: signs -> sign seems to sound better, especially with "has" later in the sentence?

L404: "A positive sea ice anomaly..." - there's a grammar problem with this sentence.

L409: to support -> for supporting

L420: coupled variables -> coupling between variables ... seems better?

L438: straight forward -> straightforward

L455: Suggest adding "(see further discussion in section 5.4)" to end of sentence (cf reviewer #2).

L545: Grammatical problem with the "who" clause in this sentence.

L548-L551: I think it's nice to mention these previous studies in the wrap-up
interpretation of the results here, but similar to the comment above, I believe
there is some vague/imprecise wording here. The "inconsistency" in models is
really the fact that the autum ice - winter NAO correlations over periods
similar in length to the reanalysis exhibit a large spread and can be positive
or negative. The CMIP6 results in Fig. 3 are essentially in agreement with
CMIP5 historical runs (Fig. 2 Siew et al.), large-ensemble historical runs
(Fig. 9 in Blackport & Screen uses several different models, Siew et al. use
just one) as well as CMIP5 and CMIP6 pre-industrial runs (Fig. 2 in Siew et
al., appropriately bootstrapped). Both Blackport & Screen and Siew et al.
show the ensembles as well as individual model results using very similar
boxplots as shown in Fig. 3. So one point is that the weak correlations aren't
just a function of averaging across many models, but also long simulation
periods versus more satellite-length periods. I would suggest modifying the
sentence to clarify these points, for example (but of course the authors can
rewrite any way they choose): Thus, inadequate coupling could be behind coupled
historical runs exhibiting a wide spread in ice-NAO correlations spanning both
positive and negative correlations (K&B, Siew), as well as the weak
correlations seen when averaging over many ensemble members or longer
simulation periods (B&S, Siew)."

Hide

AR by Kristian Strommen on behalf of the Authors (24 Jul 2022) Author's response Manuscript

Short summary

Observational data suggest that the extent of Arctic sea ice influences mid-latitude winter weather. However, climate models generally fail to reproduce this link, making it unclear if models are missing something or if the observed link is just a coincidence. We show that if one explicitly represents the effect of unresolved sea ice variability in a climate model, then it is able to reproduce this link. This implies that the link may be real but that many models simply fail to simulate it.