Deficient ocean&ndash;atmosphere feedbacks constrain seasonal NAO prediction

Kolstad, Erik W.

doi:10.5194/egusphere-2025-5075

Preprints

https://doi.org/10.5194/egusphere-2025-5075

Preprints

17 Oct 2025

| 17 Oct 2025

Deficient ocean–atmosphere feedbacks constrain seasonal NAO prediction

Erik W. Kolstad

Abstract. As the North Atlantic Oscillation (NAO) accounts for a dominant share of wintertime weather variability across the North Atlantic basin, it is a coveted target for seasonal prediction. Yet dynamical forecast systems continue to exhibit limited skill, in part due to deficiencies in representing ocean–atmosphere feedbacks. Here, mediation analysis – a statistical framework from causal inference – is applied to identify and quantify feedback pathways linking late-autumn North Atlantic sea surface temperature (SST) anomalies to the subsequent winter NAO. This approach is attractive because it is straightforward to apply, easy to interpret, and can be used directly on observations-derived data like reanalyses without requiring idealised model perturbation experiments.

The analysis reveals a physically coherent feedback sequence. Anomalous November SST patterns promote the gradual formation of a surface-pressure dipole rotated clockwise relative to the canonical NAO structure. This dipole induces advection anomalies in the western North Atlantic, which in turn modulate surface fluxes in the Subpolar Gyre and lower-tropospheric baroclinicity in the storm-track entry region east of Newfoundland. These changes nudge the NAO, which, once established, feeds back onto the fluxes and baroclinicity, reinforcing the anomaly and sustaining the circulation pattern.

A central finding is that a state-of-the-art seasonal prediction system fails to capture these feedback mechanisms. The baroclinicity pathway, the process through which changes in eddy growth reinforce the circulation anomaly, is particularly deficient, accounting for only 2 % of the lagged SST–NAO correlation in SEAS5 compared with 44 % in the ERA5 reanalysis. This misrepresentation likely represents a fundamental barrier to improved NAO forecast skill.

More broadly, the results demonstrate the potential of mediation analysis as a diagnostic tool for disentangling coupled feedbacks directly from observations, evaluating their representation in models, and guiding targeted improvements that could enhance seasonal prediction of the NAO.

Received: 14 Oct 2025 – Discussion started: 17 Oct 2025

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Journal article(s) based on this preprint

24 Mar 2026

Deficient ocean–atmosphere feedbacks constrain seasonal NAO prediction

Erik W. Kolstad

Weather Clim. Dynam., 7, 507–522, https://doi.org/10.5194/wcd-7-507-2026,https://doi.org/10.5194/wcd-7-507-2026, 2026

Short summary

Erik W. Kolstad

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2025-5075', Anonymous Referee #1, 27 Oct 2025

This article analyses the relationships between N Atlantic SST, heat fluxes and the North Atlantic Oscillation in a seasonal forecast system. The questions it asks are well thought out and the study is timely, relevant and of interest to many readers of this journal. However, while it has the potential to be excellent on all counts, I have had to mark it 'fair' for scientific content as it stands, because if I understand correctly how the analysis has been done, then there is a potentially large error in the analysis method related to the use of ensemble means as explained below.
MAJOR POINTS:
A) I remain unconvinced about the use of October hindcasts. November starts are normally used for DJF forecasts so why not use the forecasts that are relevant to the problem? We should at least be reassured that November forecasts show similar, if perhaps weaker errors.
B) The analysis is novel, relevant and interesting but there is a serious flaw. The analysis is carried out entirely on ensemble means (L186) and then compared to the observations (L325, L360 and throughout). This comparison is not valid. A simple example can illustrate why: assume for example that the NAO is entirely formed from unpredictable variability or 'noise'. In this case there would be no ensemble mean signal and no regressions between the modelled variables. However, the observational analysis will still show relationships, albeit from unpredictable 'noise'. In reality the difference will be less extreme as the NAO contains predictable and unpredictable components but the presented analysis would only be valid if the NAO is formed from entirely predictable variability. Fortunately, the problem is easily corrected as it simply needs to be redone on ensemble members. I hope this can be done as I still think this has the potential to be a very useful contribution but it is essential before publication.
MINOR POINTS:
The article seems to be overly positive about empirical forecast methods. Several of the examples cited have not performed well after publication in real out of sample cases. This is often the case with such methods which have often been inadvertently tuned to non-causal relationships in sections of the past observational record. Please therefore refine the language to better represent this, for example by saying "...achieved potentially useful levels of skill (but note the comments below about real time forecast skill)..." and at L34: "often appear to outperform" as this is not really outperforming if based on noncausal factors.
L45: Suggest "high surface NAO" as some studies claim NAO skill from high level circulation fields that is not reflected in surface NAO predictions
L46: Baker et al 2024 reported similar levels of skill for the NAO from later generations of forecasts and similar ranking of systems so a better phrasing here would be "However, there is a wide range of performance between systems and system upgrades have not significantly improved overall skill". Please also remove comments about reducing skill as the reported changes are not significant.
L110: typo "aa"
L138: I did not understand why this implies 'many pathways'
Sec3.1: why is this particular system (ECMWF SEAS5) used? Is it because it has lower skill than some of the others (c.f. Sec 4.1) and so useful to detect errors? If so please say this.
L201-205: How are anomalies calculated in SEAS5 and ERA5?
P7 line 1: This seems odd as there are only N values to start with so by definition there are many repeates and samples are not independent. This will reduce spread and affect results like those in Fig.5. Is there a simple inflation of spread that can be done to correct and compensate for this?
L268: what is the mean bias in the NAO?
L290: typo 'gyrefor'
L297: please state of this represents a positive feedback
L384: robust
L394, L405: grammar at the start of these sentences, please reword

Citation: https://doi.org/10.5194/egusphere-2025-5075-RC1
- AC1:
  'Reply to RC1', Erik Kolstad, 28 Oct 2025
  
  I thank the reviewer for their thoughtful and constructive comments, which will be very helpful in improving the manuscript. I am encouraged by the reviewer’s assessment that the study is timely and relevant. Below I address the two major points raised; detailed revisions and responses to minor comments will be provided in the formal response.
  Major point A: Use of October hindcasts
  
  The motivation for using the October initialisations was to ensure sufficient variation in the November SST states. In the November runs, SSTs are nearly identical across ensemble members due to inertia, which I reckoned would reduce the usefulness of the data for mediation analysis. Nevertheless, I agree that November forecasts are operationally the most relevant for DJF predictions. I have therefore decided to base the analysis on the November initialisations. As stated in the paper, these results confirm that the main conclusions are not sensitive to this choice. The biases are somewhat smaller, but the mediation remains weak. For the November runs, the anomaly correlation coefficient between the modelled and observed NAO is 0.29 (p = 0.06), which is consistent with the findings of Baker et al. (2024), while for the October runs it was non-significant. Within SEAS5, the SST–NAO correlation is 0.19, smaller than for the October runs, indicating that the errors are not reduced as hypothesised.
  Major point B: Use of ensemble means
  
  I fully agree with the reviewer that comparing ensemble-mean relationships to observational relationships is problematic, as the ensemble mean effectively filters out much of the internal variability. I had in fact originally used individual ensemble members but switched to ensemble means for simplicity. Following the reviewer’s suggestion, I have now repeated the analysis using all ensemble members. The results are broadly consistent with those based on ensemble means, though the relationship between the SST–NAO correlation and the indirect effect (Fig. 5) strengthens for SEAS5. In my opinion this reinforces the conclusion that feedback mechanisms play a central role in determining NAO predictability.
  Additionally, I have discovered a data-handling error affecting the Eady growth rate (EGR) calculations for the October runs. After correcting this issue, the indirect effect through baroclinicity increased and spatially it now more closely resembles the ERA5 result. As in ERA5, baroclinicity emerges as the dominant mediator (higher indirect effect than for the surface fluxes). I am grateful that the reviewer’s comments prompted this revision, which has clarified the results and improved the manuscript.
  
  Citation: https://doi.org/10.5194/egusphere-2025-5075-AC1
  - AC2: 'Reply on AC1', Erik Kolstad, 30 Oct 2025
    
    I have identified and corrected a data-handling error in the processing of the model data. This issue affected the calculation of the indirect (mediated) effects, particularly for the baroclinicity (Eady growth rate) pathway.
    In the corrected analysis, the model performs slightly better in reproducing the indirect effect – especially through the baroclinicity pathway. Broadly speaking, the main conclusions of the study stand, but the numerical results have been revised.
    Following the editor’s suggestion, I have sent the corrected manuscript directly to the editor, who will share it with the remaining reviewer(s). This ensures that the remaining review is based on the corrected version, while keeping the discussion open and transparent for all readers.
    
    Citation: https://doi.org/10.5194/egusphere-2025-5075-AC2
AC3: 'Correction of data handling error', Erik Kolstad, 05 Nov 2025

I identified a data-handling error in the processing of the model data, related to the incorrect chronological sorting of years when concatenating files. I have now corrected this issue and re-run the analysis. Overall the results have changed slightly, but the main conclusions remain qualitatively the same. The PDF file contains new figures and summarises the updates to the findings.

Citation: https://doi.org/10.5194/egusphere-2025-5075-AC3
RC2:
'Comment on egusphere-2025-5075', Anonymous Referee #2, 17 Nov 2025
This paper uses a statistical casual framework called mediation analysis to diagnose atmosphere-ocean feedbacks associated with NAO predictability and to compare them between ERA5 and the seasonal prediction system SEAS. It finds that surface heat fluxes and Eady growth rate mediate the effect of November SST on DJF NAO, which the paper refers to as an “indirect effect”. These indirect effects are found to be substantially weaker in SEAS than ERA5.
I find this to be an interesting and well written paper, albeit with some potentially important interpretation issues in its current form. My chief concerns are that the autocorrelation of the NAO is not considered, that much of the results hinge on the potentially coincidental correlation between the DJF NAO and the particular November SST pattern studied, and that nothing about the analysis demonstrates a causal role of subpolar heat fluxes in the SST-to-NAO feedback. I foresee that these issues could be addressed with some additional analyses and more careful wording, which could be addressed in a round of major revisions.
Please note that this review is based on an updated version of the manuscript, provided by the editor, in which the data handling error was corrected and where individual ensemble members were used instead of ensemble means.
Major Comments:
When the effects X -> Z -> Y are discussed, X -> Y -> Z is considered as an alternative, which motivates Figs. 3b, 3e, 4b, 4e. This is all fine and well, but the paper does not consider the alternative that Y -> X and Y -> Z. That Y -> X may seem a bit silly when Y is DJF NAO and X is November SST, but not necessarily if the autocorrelation of the NAO is considered. To rule this out, I think it is necessary (1) to consider the correlation between November NAO and DJF NAO and/or (2) to investigate the sub-seasonality of the X -> Y relationship. I can see in Kolstad and O’Reilly that this effect is largest in February, which certainly helps to address this concern, but I still more discussion of this is needed in this paper.

A related concern is that the mediation effect αβ could simply be the coincidental agreement between α and β. This is easy to imagine, because β is strong (everything co-varies with the NAO, albeit usually with NAO as the causal driver). Then any α that are large by coincidence (and of the same sign) will show as a strong indirect effect. My concern is that the correlation between the NAO and the November SST pattern is at least partially coincidental (combined with choices made to maximize this correlation, as discussed in the text). Then the comparison SEAS analysis is at a disadvantage in terms of correlations (compared to ERA5) throughout the rest of the analysis, because the ERA5 SST pattern was chosen, rather than choosing whatever November SST pattern would maximize the correlation in SEAS. To address this, I think at minimum requires repeating the SEAS analysis with the November SST pattern most correlated with the DJF NAO within the model.

Even after the above two statistical issues are addressed, I still don’t think it’s possible to fully conclude that DJF subpolar heat fluxes play a causal role in mediating the relationship between November SSTs and the DJF NAO. The reason is that heat fluxes in this region are strongly correlated with the NAO, where this primarily represents the reverse causality (i.e., NAO -> subpolar heat fluxes). This means that ANY other causal pathway that relates the November SST pattern to the DJF NAO will also show up as a strong mediation effect in the heat fluxes. I think this requires much more careful discussion throughout the manuscript as well as softening of the conclusions relating the role of subpolar heat fluxes. This all of course applies to Eady growth rate as well, but there the underlying physical explanations in the manuscript make more sense.

References to the subpolar gyre, or in some cases even just “the Gyre” are vague. When discussing the heat flux biases and heat flux mediation plots, the subpolar gyre was referring to a small northern part of the Gyre near Iceland (most egregiously on L. 273). Then the references to the gyre were to a location further south when the Eady growth rate results were discussed. Additionally, there are unlabeled emphasis boxes on several figures, which are not in the same place across figures. References to the subpolar gyre should be made with a map of the subpolar gyre streamfunction in mind, and the paper needs clearer labeling of which regions are being referred to where (especially the averaging regions used in Figure 5).

While the term “suppression” makes sense, and it seems that “inconsistent mediation” comes from the literature, I think the term “correct mediation” is misleading, because it’s also possible for there to be other effects (i.e., in completely other problems) where the correct effect (i.e., in reality) is one of inconsistent mediation or suppression. Is there another term that could be used for this? This terminology sometimes comes off as overconfident about the true direction of the various effects in reality (e.g., on lines 373-375).

Line Comments:
Figure 1: The figure caption should specify that the SEAS values are from the ensemble mean

72-79: After the preceding discussion about S2N paradox, I thought this paragraph could benefit from distinguishing between what has been found based on observations and what has been found based on models.

102-106: Of these 3 extensions, it seems to me like the first has already been done by Kolstad and O’Reilly (2024) and deserves less emphasis

218: “appropriate latitude-based weighting” is not specific enough, because there are two common choices, one where the data is cos(lat) weighted and one where the data is sqrt(cos(lat)) weighted such that the covariance matrix is area weighted. See discussion at https://climatedataguide.ucar.edu/climate-tools/empirical-orthogonal-function-eof-analysis-and-rotated-eof-analysis and in Baldwin et al. 2009 (https://doi.org/10.1175/2008JCLI2147.1).

229: Just checking, this is still the SST field and not the surface temperature field, right? Surface temperature has sea-ice surface temperature, which can be much colder than the freezing point, whereas SST should be no less than the freezing point (approx. -4°C).

302: “Its close resemblance to the indirect-effect pattern in the Subpolar Gyre underscores the feedback nature of this coupling” – It’s not a feedback on the NAO, because the NAO is forcing the heat fluxes, not the other way around. So maybe the heat fluxes of the same sign can be said to reinforce the heat fluxes, but this wording seems to be implying a feedback on the NAO, which cannot be diagnosed from the sign of the heat fluxes alone

Figure 2: Caption is for 6 panels instead of 8, 2 missing.

268: High west of Gibraltar = Azores High

Figure 3, 4: It’s important to note somewhere that the boxes added for emphasis are not in the same place across figures

322: “broadly negative” is not correct. Approximately just as much positive as negative.

332: “strengthens horizontal temperature gradients and reduces lower-tropospheric stability” – have you checked this, or is this an inference?

339: “unmistakable” is a bit strong. They look similar in pattern, but different in amplitude. Keep in mind that there hasn’t been any statistical test of the amplitude difference, just the sign

368: typo in p-value?

416-420: A larger feedback of the ocean is not necessarily all about ocean resolution. See for example Czaja et al. 2019 (https://doi.org/10.1007/s40641-019-00148-5) and Wills et al. 2024 (https://doi.org/10.1029/2023MS004123) on the role of atmospheric resolution
Citation: https://doi.org/10.5194/egusphere-2025-5075-RC2

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2025-5075', Anonymous Referee #1, 27 Oct 2025

This article analyses the relationships between N Atlantic SST, heat fluxes and the North Atlantic Oscillation in a seasonal forecast system. The questions it asks are well thought out and the study is timely, relevant and of interest to many readers of this journal. However, while it has the potential to be excellent on all counts, I have had to mark it 'fair' for scientific content as it stands, because if I understand correctly how the analysis has been done, then there is a potentially large error in the analysis method related to the use of ensemble means as explained below.
MAJOR POINTS:
A) I remain unconvinced about the use of October hindcasts. November starts are normally used for DJF forecasts so why not use the forecasts that are relevant to the problem? We should at least be reassured that November forecasts show similar, if perhaps weaker errors.
B) The analysis is novel, relevant and interesting but there is a serious flaw. The analysis is carried out entirely on ensemble means (L186) and then compared to the observations (L325, L360 and throughout). This comparison is not valid. A simple example can illustrate why: assume for example that the NAO is entirely formed from unpredictable variability or 'noise'. In this case there would be no ensemble mean signal and no regressions between the modelled variables. However, the observational analysis will still show relationships, albeit from unpredictable 'noise'. In reality the difference will be less extreme as the NAO contains predictable and unpredictable components but the presented analysis would only be valid if the NAO is formed from entirely predictable variability. Fortunately, the problem is easily corrected as it simply needs to be redone on ensemble members. I hope this can be done as I still think this has the potential to be a very useful contribution but it is essential before publication.
MINOR POINTS:
The article seems to be overly positive about empirical forecast methods. Several of the examples cited have not performed well after publication in real out of sample cases. This is often the case with such methods which have often been inadvertently tuned to non-causal relationships in sections of the past observational record. Please therefore refine the language to better represent this, for example by saying "...achieved potentially useful levels of skill (but note the comments below about real time forecast skill)..." and at L34: "often appear to outperform" as this is not really outperforming if based on noncausal factors.
L45: Suggest "high surface NAO" as some studies claim NAO skill from high level circulation fields that is not reflected in surface NAO predictions
L46: Baker et al 2024 reported similar levels of skill for the NAO from later generations of forecasts and similar ranking of systems so a better phrasing here would be "However, there is a wide range of performance between systems and system upgrades have not significantly improved overall skill". Please also remove comments about reducing skill as the reported changes are not significant.
L110: typo "aa"
L138: I did not understand why this implies 'many pathways'
Sec3.1: why is this particular system (ECMWF SEAS5) used? Is it because it has lower skill than some of the others (c.f. Sec 4.1) and so useful to detect errors? If so please say this.
L201-205: How are anomalies calculated in SEAS5 and ERA5?
P7 line 1: This seems odd as there are only N values to start with so by definition there are many repeates and samples are not independent. This will reduce spread and affect results like those in Fig.5. Is there a simple inflation of spread that can be done to correct and compensate for this?
L268: what is the mean bias in the NAO?
L290: typo 'gyrefor'
L297: please state of this represents a positive feedback
L384: robust
L394, L405: grammar at the start of these sentences, please reword

Citation: https://doi.org/10.5194/egusphere-2025-5075-RC1
- AC1:
  'Reply to RC1', Erik Kolstad, 28 Oct 2025
  
  I thank the reviewer for their thoughtful and constructive comments, which will be very helpful in improving the manuscript. I am encouraged by the reviewer’s assessment that the study is timely and relevant. Below I address the two major points raised; detailed revisions and responses to minor comments will be provided in the formal response.
  Major point A: Use of October hindcasts
  
  The motivation for using the October initialisations was to ensure sufficient variation in the November SST states. In the November runs, SSTs are nearly identical across ensemble members due to inertia, which I reckoned would reduce the usefulness of the data for mediation analysis. Nevertheless, I agree that November forecasts are operationally the most relevant for DJF predictions. I have therefore decided to base the analysis on the November initialisations. As stated in the paper, these results confirm that the main conclusions are not sensitive to this choice. The biases are somewhat smaller, but the mediation remains weak. For the November runs, the anomaly correlation coefficient between the modelled and observed NAO is 0.29 (p = 0.06), which is consistent with the findings of Baker et al. (2024), while for the October runs it was non-significant. Within SEAS5, the SST–NAO correlation is 0.19, smaller than for the October runs, indicating that the errors are not reduced as hypothesised.
  Major point B: Use of ensemble means
  
  I fully agree with the reviewer that comparing ensemble-mean relationships to observational relationships is problematic, as the ensemble mean effectively filters out much of the internal variability. I had in fact originally used individual ensemble members but switched to ensemble means for simplicity. Following the reviewer’s suggestion, I have now repeated the analysis using all ensemble members. The results are broadly consistent with those based on ensemble means, though the relationship between the SST–NAO correlation and the indirect effect (Fig. 5) strengthens for SEAS5. In my opinion this reinforces the conclusion that feedback mechanisms play a central role in determining NAO predictability.
  Additionally, I have discovered a data-handling error affecting the Eady growth rate (EGR) calculations for the October runs. After correcting this issue, the indirect effect through baroclinicity increased and spatially it now more closely resembles the ERA5 result. As in ERA5, baroclinicity emerges as the dominant mediator (higher indirect effect than for the surface fluxes). I am grateful that the reviewer’s comments prompted this revision, which has clarified the results and improved the manuscript.
  
  Citation: https://doi.org/10.5194/egusphere-2025-5075-AC1
  - AC2: 'Reply on AC1', Erik Kolstad, 30 Oct 2025
    
    I have identified and corrected a data-handling error in the processing of the model data. This issue affected the calculation of the indirect (mediated) effects, particularly for the baroclinicity (Eady growth rate) pathway.
    In the corrected analysis, the model performs slightly better in reproducing the indirect effect – especially through the baroclinicity pathway. Broadly speaking, the main conclusions of the study stand, but the numerical results have been revised.
    Following the editor’s suggestion, I have sent the corrected manuscript directly to the editor, who will share it with the remaining reviewer(s). This ensures that the remaining review is based on the corrected version, while keeping the discussion open and transparent for all readers.
    
    Citation: https://doi.org/10.5194/egusphere-2025-5075-AC2
AC3: 'Correction of data handling error', Erik Kolstad, 05 Nov 2025

I identified a data-handling error in the processing of the model data, related to the incorrect chronological sorting of years when concatenating files. I have now corrected this issue and re-run the analysis. Overall the results have changed slightly, but the main conclusions remain qualitatively the same. The PDF file contains new figures and summarises the updates to the findings.

Citation: https://doi.org/10.5194/egusphere-2025-5075-AC3
RC2:
'Comment on egusphere-2025-5075', Anonymous Referee #2, 17 Nov 2025
This paper uses a statistical casual framework called mediation analysis to diagnose atmosphere-ocean feedbacks associated with NAO predictability and to compare them between ERA5 and the seasonal prediction system SEAS. It finds that surface heat fluxes and Eady growth rate mediate the effect of November SST on DJF NAO, which the paper refers to as an “indirect effect”. These indirect effects are found to be substantially weaker in SEAS than ERA5.
I find this to be an interesting and well written paper, albeit with some potentially important interpretation issues in its current form. My chief concerns are that the autocorrelation of the NAO is not considered, that much of the results hinge on the potentially coincidental correlation between the DJF NAO and the particular November SST pattern studied, and that nothing about the analysis demonstrates a causal role of subpolar heat fluxes in the SST-to-NAO feedback. I foresee that these issues could be addressed with some additional analyses and more careful wording, which could be addressed in a round of major revisions.
Please note that this review is based on an updated version of the manuscript, provided by the editor, in which the data handling error was corrected and where individual ensemble members were used instead of ensemble means.
Major Comments:
When the effects X -> Z -> Y are discussed, X -> Y -> Z is considered as an alternative, which motivates Figs. 3b, 3e, 4b, 4e. This is all fine and well, but the paper does not consider the alternative that Y -> X and Y -> Z. That Y -> X may seem a bit silly when Y is DJF NAO and X is November SST, but not necessarily if the autocorrelation of the NAO is considered. To rule this out, I think it is necessary (1) to consider the correlation between November NAO and DJF NAO and/or (2) to investigate the sub-seasonality of the X -> Y relationship. I can see in Kolstad and O’Reilly that this effect is largest in February, which certainly helps to address this concern, but I still more discussion of this is needed in this paper.

A related concern is that the mediation effect αβ could simply be the coincidental agreement between α and β. This is easy to imagine, because β is strong (everything co-varies with the NAO, albeit usually with NAO as the causal driver). Then any α that are large by coincidence (and of the same sign) will show as a strong indirect effect. My concern is that the correlation between the NAO and the November SST pattern is at least partially coincidental (combined with choices made to maximize this correlation, as discussed in the text). Then the comparison SEAS analysis is at a disadvantage in terms of correlations (compared to ERA5) throughout the rest of the analysis, because the ERA5 SST pattern was chosen, rather than choosing whatever November SST pattern would maximize the correlation in SEAS. To address this, I think at minimum requires repeating the SEAS analysis with the November SST pattern most correlated with the DJF NAO within the model.

Even after the above two statistical issues are addressed, I still don’t think it’s possible to fully conclude that DJF subpolar heat fluxes play a causal role in mediating the relationship between November SSTs and the DJF NAO. The reason is that heat fluxes in this region are strongly correlated with the NAO, where this primarily represents the reverse causality (i.e., NAO -> subpolar heat fluxes). This means that ANY other causal pathway that relates the November SST pattern to the DJF NAO will also show up as a strong mediation effect in the heat fluxes. I think this requires much more careful discussion throughout the manuscript as well as softening of the conclusions relating the role of subpolar heat fluxes. This all of course applies to Eady growth rate as well, but there the underlying physical explanations in the manuscript make more sense.

References to the subpolar gyre, or in some cases even just “the Gyre” are vague. When discussing the heat flux biases and heat flux mediation plots, the subpolar gyre was referring to a small northern part of the Gyre near Iceland (most egregiously on L. 273). Then the references to the gyre were to a location further south when the Eady growth rate results were discussed. Additionally, there are unlabeled emphasis boxes on several figures, which are not in the same place across figures. References to the subpolar gyre should be made with a map of the subpolar gyre streamfunction in mind, and the paper needs clearer labeling of which regions are being referred to where (especially the averaging regions used in Figure 5).

While the term “suppression” makes sense, and it seems that “inconsistent mediation” comes from the literature, I think the term “correct mediation” is misleading, because it’s also possible for there to be other effects (i.e., in completely other problems) where the correct effect (i.e., in reality) is one of inconsistent mediation or suppression. Is there another term that could be used for this? This terminology sometimes comes off as overconfident about the true direction of the various effects in reality (e.g., on lines 373-375).

Line Comments:
Figure 1: The figure caption should specify that the SEAS values are from the ensemble mean

72-79: After the preceding discussion about S2N paradox, I thought this paragraph could benefit from distinguishing between what has been found based on observations and what has been found based on models.

102-106: Of these 3 extensions, it seems to me like the first has already been done by Kolstad and O’Reilly (2024) and deserves less emphasis

218: “appropriate latitude-based weighting” is not specific enough, because there are two common choices, one where the data is cos(lat) weighted and one where the data is sqrt(cos(lat)) weighted such that the covariance matrix is area weighted. See discussion at https://climatedataguide.ucar.edu/climate-tools/empirical-orthogonal-function-eof-analysis-and-rotated-eof-analysis and in Baldwin et al. 2009 (https://doi.org/10.1175/2008JCLI2147.1).

229: Just checking, this is still the SST field and not the surface temperature field, right? Surface temperature has sea-ice surface temperature, which can be much colder than the freezing point, whereas SST should be no less than the freezing point (approx. -4°C).

302: “Its close resemblance to the indirect-effect pattern in the Subpolar Gyre underscores the feedback nature of this coupling” – It’s not a feedback on the NAO, because the NAO is forcing the heat fluxes, not the other way around. So maybe the heat fluxes of the same sign can be said to reinforce the heat fluxes, but this wording seems to be implying a feedback on the NAO, which cannot be diagnosed from the sign of the heat fluxes alone

Figure 2: Caption is for 6 panels instead of 8, 2 missing.

268: High west of Gibraltar = Azores High

Figure 3, 4: It’s important to note somewhere that the boxes added for emphasis are not in the same place across figures

322: “broadly negative” is not correct. Approximately just as much positive as negative.

332: “strengthens horizontal temperature gradients and reduces lower-tropospheric stability” – have you checked this, or is this an inference?

339: “unmistakable” is a bit strong. They look similar in pattern, but different in amplitude. Keep in mind that there hasn’t been any statistical test of the amplitude difference, just the sign

368: typo in p-value?

416-420: A larger feedback of the ocean is not necessarily all about ocean resolution. See for example Czaja et al. 2019 (https://doi.org/10.1007/s40641-019-00148-5) and Wills et al. 2024 (https://doi.org/10.1029/2023MS004123) on the role of atmospheric resolution
Citation: https://doi.org/10.5194/egusphere-2025-5075-RC2

Peer review completion

AR – Author's response | RR – Referee report | ED – Editor decision | EF – Editorial file upload

AR by Erik Kolstad on behalf of the Authors (11 Dec 2025) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (23 Dec 2025) by David Battisti

RR by Adam Scaife (07 Jan 2026)

RR by Anonymous Referee #2 (10 Jan 2026)

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 author has made a thoughtful and thorough revision. However, I think some of the new analyses illustrate the issues with the overall interpretation, which are related to the issues I already raised with the previous version. Due to these issues, I do not believe the manuscript addresses two of the things it sets out to do, namely (1) clarify the causal directionality of the relationship between the NAO and SHF/baroclinicity and (2) to assess whether biases in the mediation relationship underly the limited NAO prediction skill in SEAS5. I appreciate the authors approach and think there are some interesting results, but I think the paper still needs a lot of work on the overall framing of what it aims to do and what can be concluded from the analysis.

Major comments:
1. Problems with ratio used to infer direction of Y/Z relationship: You’ve introduced on line 170 a ratio of regression coefficients with different orders of predictor and predictand to assess which direction of relationship is stronger. I would urge caution about introducing such an approach without a careful discussion of regression dilution. Regression dilution biases the OLS regression coefficient towards zero when there is noise in the independent variable, which means that this ratio will be highly influenced by which variable has more noise in it.

However, I think the problems with the inferences from this ratio (gamma/beta) run deeper than just regression dilution. Thinking about the model world (SEAS5), in equation 5 you are regressing out a significant relationship between X and Z when determining the relationship between Y and Z, but in equation 2 you are regressing out an insignificant relationship between X and Y when determining the relationship between Z and Y. However, the relationship between X and Y is significant in ERA5, and I think the model-ERA5 differences in this ratio is therefore telling you about differences in the relationship between X and Y between SEAS5 and ERA5 and not about the differences in direction of Y->Z or Z->Y relationship. Any analysis that is telling you that SHF->NAO is more important than NAO->SHF should be taken with extreme skepticism given the extensive literature about the importance of atmosphere driven SHF (one recent example out of many: Patterson et al. 2024, https://doi.org/10.1175/JCLI-D-23-0602.1).

Additionally, I believe there is a mistake in the equation for the ratio (line 170), since beta has units of Y/Z, whereas gamma has units of Z/Y, such that one or the other is inverted before the ratio is taken. This is true even if all quantities are normalized.

2. Remaining interpretive issue affecting most conclusions: Figure 7 is an excellent demonstration of an interpretive issue that I believe runs throughout this analysis. As I’ve mentioned in my comments on the previous version, if there is a coincidental correlation between the November SST pattern and the DJF NAO, this will show up as a large mediated effect, because both of the mediated fields are strongly correlated with the NAO (with the causality primarily NAO -> mediator, at least for SHF). I do see your point in the last paragraph of 4.5 that the NAO skill is a measure that doesn’t depend on the SST or mediator fields, and I therefore agree that this analysis is showing a relationship between the NAO skill and total effect of X on Y (as was already shown in Fig. 2). However, bootstrapped samples that have a large skill/total effect will necessarily have a large alpha, because the mediators are strongly correlated with the NAO. And since beta is always large (the mediators are strongly correlated with the NAO), this will show up as a large mediated effect.

From this, I think one can conclude that there will be a large apparent mediated effect when there is coincidentally a large SST-NAO relationship, even if the mediators play no causal role whatsoever. While you could point to the small direct effect in something like Eq. 2, all this really shows is that the contemporaneous mediators are more correlated with the DJF NAO than the November SSTs, such that they are given more weight in the multiple linear regression. However, it is still valid to interpret the mediators as being caused by the NAO, since there are also problems with the analysis used to infer the directionality of this relationship.

I want to acknowledge that Section 5 (lines 459-462, 469-473) does discuss these potential issues with some nuance, however, I think this raises doubt as to the importance of the mediation pathways introduced, which in turn partially undermines the premise of the study. I think there is still value in the analysis presented, but quite some work is needed on how it is framed and interpreted.

Minor comments:
• Just a note that if you detected slight disapproval of the term “indirect effect”, it was only because this is commonly used for aerosol effects on climate. However, the context is sufficiently distinct that I didn’t find it too confusing. Nevertheless, it’s nice to use “mediated effect” to avoid this terminology overlap.
• Line 26: I suggest “regional” instead of “local”, since the latter implies a more grid-cell-level relationship (at least to me)
• Line 60: Consider adding a bit more transition here from the previous sentence to help the reader understand the overall flow of the introduction
• Line 81: I am always a bit skeptical of statements such as this about its previous use in a field. I recently became aware of a land-atmosphere interactions paper (Khanal et al. 2024) that uses partial correlations in a similar way, although they do not spend as much time writing out the formalism. Still, it seems that this sub-field is somewhat aware of this type of approach. I don’t have a specific recommendation here, but consider watering down this statement.
• Line 90: I was anticipating O’Reilly et al. 2024 (https://doi.org/10.1038/s41612-023-00335-0) to be an example here (but I don’t have a strong opinion about whether you should include it or not)
• Line 106: Italics on “informed” implies it is defining a term, when that doesn’t really seem like it is the case here. I’m also not entirely convinced by this word choice
• Line 112: Is the word “observed” necessary?
• Line 116: Avoid “it is obvious” without an explanation. I’m assuming you mean because of the time offset (among other reasons)?
• Line 123: “absurd” is a word I generally don’t recommend in scientific writing
• Line 148-149: Isn’t the last sentence only true if the other mediator were correlated with Z, and if so, is it maybe worth adding “if they are correlated with Z” at the end?
• Line 158-161: Too much going on in this multi-part sentence. Please break it up for readability.
• Line 163: Since the mediators have not been introduced yet, please add “that we consider” or similar somewhere in this sentence
• Line 185: Presumably you mean “ordinary least squares” (this is an important distinction to make, related to my major comment about regression dilution)
• Line 212: “qualitatively similar” would be better than “qualitatively identical”, because “identical” is more of a quantitative statement
• Line 272: “still weaken” is confusing. I think you mean “weaken further”
• Line 273: “The sample parameter used in the remainder of the analysis” doesn’t make it very clear what this is, i.e., that it is the member-level regression coefficient. Please also quote the range across ensemble members for this and for the correlation coefficient
• Line 315-317: This sentence is confusingly worried. Also, it’s necessary to call this a weak negative SHF bias, because it is hardly visible compared to the surrounding positive biases. This will also help readers understand what anomalies you are referring to.
• Line 357: I am getting tripped up by “it is useful” here. Specifically, it is not clear whether “it” refers to the hypothesized X -> Z -> Y relationship (I don’t think so, because this wouldn’t make sense to me) or whether “it is
• Figure 6a,d: Are these DJF SST and SLP? I assume so, because I don’t think November SST and SLP would make sense here, but the caption and text don’t really state this as far as I can see.
• Line 379: Typo. There should be no X here.
• Line 385: It would be helpful to clarify that this sentence only applies to the suppression in the Gulf Stream region and not to the SHF relationship as a whole (e.g., the positive mediation in the subpolar region that dominates the full mediated effect)
• Line 396-398: I think this summary text understates the importance of NAO-> mediator feedbacks that are evident in the differences between equivalent panels of Fig. 6 and Fig. 4/5.
• Line 399: Your analysis does not demonstrate “the model’s essentially one-way representation of these pathways”. See major comment 1.
• Line 496: I don’t know what is generally recommended on this, but it seems strange to me to acknowledge a tool that itself does not acknowledge its sources.

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ED: Publish subject to revisions (further review by editor and referees) (15 Jan 2026) by David Battisti

AR by Erik Kolstad on behalf of the Authors (19 Jan 2026) Author's response Author's tracked changes Manuscript

ED: Publish subject to revisions (further review by editor and referees) (21 Jan 2026) by David Battisti

ED: Referee Nomination & Report Request started (03 Mar 2026) by David Battisti

RR by Robert Jnglin Wills (07 Mar 2026)

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

I thank the author for his careful revisions. I think the switch from a ratio of regression coefficients to a comparison between alpha and alpha-prime is a good methodological improvement. I also see the authors point that the NAO forecast skill is “external” to the analysis of the SST-NAO relationship, and thus that the correlation between the mediation effects and the NAO skill is an important result. I still think caution may be warranted given existing unintuitive seasonal prediction findings such as the signal-to-noise paradox, but I find the current version of the manuscript to be sufficiently careful with the interpretation of results, and I therefore recommend publication. I have a few minor comments below that could be addressed before publication.

Thanks for the interesting discussion throughout the review process.

Robert Jnglin Wills

Minor wording comments:
• Line 9: Reconsider the wording “To examine its implications”. It sounds to me more like this is investigating the origins of this relationship, not the implications.
• Line 10: I think it would be clearer and more accurate if “These mechanisms” was dropped
• Line 119: With the sentence at the beginning of the section deleted compared to the previous version, this section now starts abruptly, and it feels like something is missing
• Line 174-175: I find this to be an unusual framing of the null hypothesis. Isn’t the sign consistency test also falsifying a zero alpha-prime null hypothesis (which would be more intuitive)?

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ED: Publish subject to minor revisions (review by editor) (07 Mar 2026) by David Battisti

AR by Erik Kolstad on behalf of the Authors (08 Mar 2026) Author's response Author's tracked changes Manuscript

ED: Publish as is (09 Mar 2026) by David Battisti

AR by Erik Kolstad on behalf of the Authors (15 Mar 2026) Author's response Manuscript

Journal article(s) based on this preprint

24 Mar 2026

Deficient ocean–atmosphere feedbacks constrain seasonal NAO prediction

Erik W. Kolstad

Weather Clim. Dynam., 7, 507–522, https://doi.org/10.5194/wcd-7-507-2026,https://doi.org/10.5194/wcd-7-507-2026, 2026

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Erik W. Kolstad

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I investigated why predicting winter weather over the North Atlantic remains difficult by studying how autumn ocean conditions influence the atmosphere. Using a method called mediation analysis, I uncovered a sequence of feedbacks linking sea surface temperatures to changes in winds and storm tracks. These feedbacks are poorly captured in current forecast models, which helps explain their limited skill and points to ways they can be improved.


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