No changes in overall AMOC strength  in interglacial PMIP4 time slices

Jiang, Zhiyi; Brierley, Chris; Thornalley, David; Sax, Sophie

doi:https://doi.org/10.5194/cp-19-107-2023

Articles | Volume 19, issue 1

https://doi.org/10.5194/cp-19-107-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/cp-19-107-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 19, issue 1

Research article

|

12 Jan 2023

Research article |

| 12 Jan 2023

No changes in overall AMOC strength in interglacial PMIP4 time slices

Zhiyi Jiang, Chris Brierley, David Thornalley, and Sophie Sax

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Final revised paper (published on 12 Jan 2023)
Supplement to the final revised paper
Preprint (discussion started on 22 Aug 2022)

Interactive discussion

Status: closed

RC1:
'Comment on cp-2022-63', Anonymous Referee #1, 09 Sep 2022

Review of

No changes in overall AMOC strength in interglacial PMIP4 timeslices

by Z. Jiang et al.

Here the authors discuss a very important topic in paleoclimatology. In the last decades, the role of AMOC and its variability in the past has been researched on with emphasis on glacial and deglacial climates. Now there is a shift in the focus towards climate conditions more similar to pre-industrial. Hence, the topic is very timely and the study is very welcome.

The manuscript makes use of new available simulations by direct comparing the simulated AMOC regimes for the Holocene and the last interglacial. The study may be of interest beyond the modelling community and should thus provide more information and justifications for the approach taken.

The manuscript is well written starting with a helpful introduction. Overall I recommend publication with CoP.

Details:

Line 7: better introduce the examined time periods in the abstract instead of using experiment abbreviations such as lig127k.

Line 33: its not so clear to me how past changes in the AMOC can “… explain the recent global temperature changes…”

Line 38: during tWo interglacials

Line 38-39: midHolocene is the simulation’s abbreviation, not an interglacial. The abbreviation lig127k should be defined (last interglacial is not mentioned before). Further, 6 and 127 ka are time slices no period. What is the rationale for choosing this time slices. With >10 kyrs of duration for the Holocene, what makes 6 ka so special? Why not e.g. 4.2 ka representing the onset of the last Holocene subdivision? Same for the Eemian.

Line 45: GHG is not introduced.

Line 46: “…interglacial period with orbital forcing being the main difference” to what? “…, while other forcing” which? “…remains very similar to thepiControl…” add space.

Line 61: what would be inappropriate methods?

Line 76: what is meant by “data availability”. All available models have been used? Are there others? Why are these not available?

Line 77: ‘msftmz’ and ‘msftmyz’ are cryptic and non-introduced abbreviations not understandable by non-specialists.

Line 79: “The data from FGOALS-f3-L …” this is a very detailed information about a single model output and should be moved from the main text.

Line 87: “… is computed as zonal average…” what does that exactly mean. From the very eastern to western grids coast to coast? Is there a water depth threshold?

Tab.1 : what is the significance of the Length parameter? It differs up to ~25 times between the simulations. Already add references (from A1) here. I’m concerned about the huge range of resulting AMOCs for PI (12 to 33 Sv). Instead of showing the individual simulation compared to themselves in Fig. 1, it would be more helpful to show an inter-model comparison better reflecting the absolute uncertainties on the resulting AMOCs, as well as highlighting unrealistic outputs. What are the (likely) reasons for some models clearly under/over- estimating PI AMOC? I think this an important lesson we can learn from this study. In particular, when (from line 96 on) secondary fingerprints of AMOC on the wider climate patterns are examined. The relevance of modelled T and precipitation is questionable, when the underlying AMOCs are already inconsistent (e.g. in line 216 the authors claim that there is a strong relationship between AMOC changes and T).

Line 120: I can’t see the feature described in front of “Fig.1” in th figure.

Line 130: “a changes”

Line 141: check grammar

Fig.1: the legend and caption of Fig.1 is very confusing. Actually whole Fig. 1 is confusing. E.g. what is the orange triangle? What are the Brierley et al 2020 simulations, and why are they shown at all? The numbers of symbols is higher than the simulations listed in Tab.1. Why are there no error ranges shown for individual simulations? Maybe indicate OSNAP and RAPID by arrow and name. Sometimes 30° and 50° is indicated sometimes not. Please revise the concept of the figure.

Line 156: what is meant by shallow and deep branches. Its not clear to me what the paragraph is telling us.

Figure 3: its hard to see what we can learn from this figure with the x-axes varying for each simulation. Please keep the axis constant to allow for inter-model comparison.

Line 181: grammar

Line 204: I don’t understand this sentence.

Line 208: show(s)

Line 235: its not clear to me why the similarity to hosing experiments demonstrates any appropriateness.

Section 4.2: this part seizes a considerable part of the manuscript. In my opinion, this section should be shortened down and the study should keep the focus on AMOC itself, as the reader would expect from the title.

Figs. 4+5: what are the criteria for showing “selected” model outputs.

Fig.5 caption: what is “low contribution”?

Fig. 6: due to the hatched areas there is little to see, please revise concept of figure.

Section 5: compared to section 4 the discussion is too short and only comprises the comparison to observational data. Better insert here a detailed discussion on why the models partly differ so strongly from OSNAP, RAPID and from each other. Besides, it is interesting to see that paleoceanographic reconstructions by PA/Th indicate similarly constant interglacial AMOCs.

Line 276: Bradtmiller et al. 2014 focuses on Heinrich AMOC. Better cite the ground-breaking McManus et al. 2004 along with Yu et al. 1996 when it comes to introducing the proxy.

Line 279: There are a number of (low resolution) Pa/Th time series available, which, however, comprise more data points for the Holocene than the ones mentioned here: Negre, C., et al. (2010). Nature, 468; Lippold, J., et al. (2016). Earth and Planetary Science Letters, 445, showing indeed a faint AMOC weakening during the course of the Holocene. This is, however, NOT supported by both high-resolution studies, which indicate no observable change but stay fairly constant.

Line 282: Guihou et al. 2010 is not sufficient for refering to the existing data base. There are Böhm, E. et al. (2015). Nature, 517, Guihou, A., et al. (2011). Quaternary Science Reviews, 30, and Jonkers, L., et al. (2015). Earth and Planetary Science Letters, 419 covering this time period in higher temporal resolution, all indeed showing values in support of the statement made at line 283.

Line 285: I don't understand this sentence.

Lien 293: In the meantime there are a number of more sophisticated recent proxy-enabled models available giving more information on proxy related response uncertainties: Missiaen, L., et al. (2020). Climate of the Past, 16; Rempfer, J., et al. (2017). Earth and Planetary Science Letters, 468; Sasaki, Y., et al. (2022). Geosci. Model Dev., 15; van Hulten, M., et al. (2018). Geoscientific Model Development, 11.

Line 314: This statement is very true and I expected more detailed explanations for this inconsistency.

Citation: https://doi.org/10.5194/cp-2022-63-RC1
- AC1: 'Comment on cp-2022-63', Zhiyi Jiang, 18 Oct 2022
  
  We would like to thank the two reviewers for their efforts reading and commenting on our research. They make several suggestions of ways that we could improve the manuscript. We intend to implement many of them, and are taking this opportunity to outline our proposed responses.
  
  Both reviewers expressed surprise, and also some concern, at the large spread in amplitude of the AMOC strengths in the preindustrial control simulations. This is an unfortunate feature of the wider CMIP6 and CMIP5 ensembles (e.g. Xie et al., 2021). Disappointingly the uncertainty in modern-day oceanographic observations is such that none of the simulations can be categorically ruled out (Frajka-Williams et al., 2019; Beadling et al., (2018)). In a revised manuscript, we would incorporate a discussion evaluating the models against modern-day observations based on results in the published literature. We would also look at alternative approaches to plot this information to provide a clearer visualisation of the AMOC changes – for example, using multiple histograms. We had included the previously published scatterplot from Brierley et al (2020), but clearly this was not properly explained, and we would aim to do better in a revised version.
  
  One of the reviewers has suggested that using spectral analysis can be more accurate in estimating low frequency variability of AMOC. We have already performed the power spectral analysis. However, some models have relatively short simulation years, it is difficult to visualise, especially when trying to figure out the lowest frequency in the simulation by looking at the plot. Hence, we decided to use the Pearson’s r to evaluate whether the simulation has substantial low frequency variability or not. Moreover, the reviewer was concerned that the length of each simulation can affect the significance of the Pearson’s r. In response to this, we have computed the p-values of the correlation coefficients and they are statistically significant (apart from the FGOALS-f3 PI experiment whose r value is not statistically significant, possibly due to the short run length of just 50 yrs, as we use historical experiment in this model to substitute the PI experiment (see Tab 1 captions)).
  
  For Sect. 4.2, one reviewer suggested that we should shorten this part and focus more on the AMOC itself as expecting from the title, while the other reviewer wanted more investigations on the AMOC’s impacts on tropical precipitation centre. Considering both comments, we will have more concise descriptions on the AMOC’s fingerprint in the revised manuscript, but also investigate more on the impacts of AMOC changes on the shifts in precipitation centre (e.g. by regressing the changes in the core location of the ITCZ onto the AMOC changes, etc.). However, how the sea-ice would response and potentially feed back to the AMOC changes are for future work, as our current approach is not sufficient to identify the direction of any feedbacks.
  
  We apologise for having only written a cursory discussion of the existing literature on proxy data. In a revised Sect. 5, we will add further detail on the palaeo-data side using the existing literature of more detailed modern oceanography studies. Meanwhile, we will add all the references when referring to the existing palaeo data base.
  
  For all other comments (such as the ‘rationale for choosing the timeslice’), grammar and spelling mistakes, explanation for a specific sentence, etc., we will make corrections and add explanations for them.
  
  Citation: https://doi.org/10.5194/cp-2022-63-AC1
RC2:
'Comment on cp-2022-63', Anonymous Referee #2, 13 Sep 2022

Review of “No changes in overall AMOC strength in interglacial PMIP4 Timeslices ” by Jiang et al.

This manuscript examines modelled AMOC and its impact on surface temperature and precipitation in PMIP4 mid-Holocene (6 ka) and LIG (127 ka) simulations in comparison to the pre-industrial control. It is found that PMIP4 models generally show no significant changes in AMOC strength during the past interglacials and imply limited forcing effects of the orbital parameters. The authors also discussed the influence of AMOC on the surface climate, which is not obvious during the interglacials. Based on these results the authors argued that interpretations of proxy reconstructions as driven by AMOC may not be evident during the past interglacials. The manuscript is generally clearly written and easy to understand its message. I recommend its publication pending a few minor revisions, as follows.

L45 The continental configuration should be specified. It will also be useful to include a figure showing the insolation differences between interglacials and PI as a function of calendar month and latitude.

L39&L78&Table1 More models doing MH simulations compared to LIG simulations should be consistent with the definition of Entry card.

L87&L91 The observation periods of RAPID and OSNAP are just a couple of years, and should be reflected in the comparison and discussion. The difference in AMOC strength between PI and present-day can be mentioned (e.g. Dima et al. 2022).

L104-110 Please reorganize this part of data processing to make it easier to read.

L143 Max AMOC strength at 10.3 Sv is very small.

L187onwards I think a spectral analysis can be more accurate in estimating low frequency variability of AMOC. Also, the different lengths of each simulation can affect the significance of r2.

L205 Please rephrase 1.3x here.

Sec 4.2 The impacts of AMOC on the N-S surface temperature gradient and shift in precip center (e.g. ITCZ location) can also be quantified by regression. The conclusion in L272 may need to be modified.

L279 The reconstructed AMOC provides useful constraints for the model. These results should also be included in the abstract.

L287 Provide more details for changes in the atmospheric circulation.

L298-300 In an equilibrated state there can be intrinsic multi-centennial AMOC variability, e.g. as proposed by Li and Yang (2022), even after the abrupt events.

L322 This is a strong statement. I feel it is not fully supported by the current results. More analysis on the impacts of AMOC on precip center (as I mentioned before) can make it more convincing.

Fig. 4 The surface temperature changes due to AMOC forcing are robust in the Nordic Seas. I am curious how the sea-ice would respond and potentially feed back to AMOC strength.

Refs

Dima, M., Nichita, D. R., Lohmann, G., Ionita, M., & Voiculescu, M. (2021). Early-onset of Atlantic Meridional Overturning Circulation weakening in response to atmospheric CO2 concentration. Npj Climate and Atmospheric Science, 4(1), 1-8.

Li, Y., & Yang, H. (2022). A Theory for Self-Sustained Multi-Centennial Oscillation of the Atlantic Meridional Overturning Circulation. Journal of Climate, 1-48.

Citation: https://doi.org/10.5194/cp-2022-63-RC2
- AC1: 'Comment on cp-2022-63', Zhiyi Jiang, 18 Oct 2022
  
  We would like to thank the two reviewers for their efforts reading and commenting on our research. They make several suggestions of ways that we could improve the manuscript. We intend to implement many of them, and are taking this opportunity to outline our proposed responses.
  
  Both reviewers expressed surprise, and also some concern, at the large spread in amplitude of the AMOC strengths in the preindustrial control simulations. This is an unfortunate feature of the wider CMIP6 and CMIP5 ensembles (e.g. Xie et al., 2021). Disappointingly the uncertainty in modern-day oceanographic observations is such that none of the simulations can be categorically ruled out (Frajka-Williams et al., 2019; Beadling et al., (2018)). In a revised manuscript, we would incorporate a discussion evaluating the models against modern-day observations based on results in the published literature. We would also look at alternative approaches to plot this information to provide a clearer visualisation of the AMOC changes – for example, using multiple histograms. We had included the previously published scatterplot from Brierley et al (2020), but clearly this was not properly explained, and we would aim to do better in a revised version.
  
  One of the reviewers has suggested that using spectral analysis can be more accurate in estimating low frequency variability of AMOC. We have already performed the power spectral analysis. However, some models have relatively short simulation years, it is difficult to visualise, especially when trying to figure out the lowest frequency in the simulation by looking at the plot. Hence, we decided to use the Pearson’s r to evaluate whether the simulation has substantial low frequency variability or not. Moreover, the reviewer was concerned that the length of each simulation can affect the significance of the Pearson’s r. In response to this, we have computed the p-values of the correlation coefficients and they are statistically significant (apart from the FGOALS-f3 PI experiment whose r value is not statistically significant, possibly due to the short run length of just 50 yrs, as we use historical experiment in this model to substitute the PI experiment (see Tab 1 captions)).
  
  For Sect. 4.2, one reviewer suggested that we should shorten this part and focus more on the AMOC itself as expecting from the title, while the other reviewer wanted more investigations on the AMOC’s impacts on tropical precipitation centre. Considering both comments, we will have more concise descriptions on the AMOC’s fingerprint in the revised manuscript, but also investigate more on the impacts of AMOC changes on the shifts in precipitation centre (e.g. by regressing the changes in the core location of the ITCZ onto the AMOC changes, etc.). However, how the sea-ice would response and potentially feed back to the AMOC changes are for future work, as our current approach is not sufficient to identify the direction of any feedbacks.
  
  We apologise for having only written a cursory discussion of the existing literature on proxy data. In a revised Sect. 5, we will add further detail on the palaeo-data side using the existing literature of more detailed modern oceanography studies. Meanwhile, we will add all the references when referring to the existing palaeo data base.
  
  For all other comments (such as the ‘rationale for choosing the timeslice’), grammar and spelling mistakes, explanation for a specific sentence, etc., we will make corrections and add explanations for them.
  
  Citation: https://doi.org/10.5194/cp-2022-63-AC1
AC1: 'Comment on cp-2022-63', Zhiyi Jiang, 18 Oct 2022

We would like to thank the two reviewers for their efforts reading and commenting on our research. They make several suggestions of ways that we could improve the manuscript. We intend to implement many of them, and are taking this opportunity to outline our proposed responses.

Both reviewers expressed surprise, and also some concern, at the large spread in amplitude of the AMOC strengths in the preindustrial control simulations. This is an unfortunate feature of the wider CMIP6 and CMIP5 ensembles (e.g. Xie et al., 2021). Disappointingly the uncertainty in modern-day oceanographic observations is such that none of the simulations can be categorically ruled out (Frajka-Williams et al., 2019; Beadling et al., (2018)). In a revised manuscript, we would incorporate a discussion evaluating the models against modern-day observations based on results in the published literature. We would also look at alternative approaches to plot this information to provide a clearer visualisation of the AMOC changes – for example, using multiple histograms. We had included the previously published scatterplot from Brierley et al (2020), but clearly this was not properly explained, and we would aim to do better in a revised version.

One of the reviewers has suggested that using spectral analysis can be more accurate in estimating low frequency variability of AMOC. We have already performed the power spectral analysis. However, some models have relatively short simulation years, it is difficult to visualise, especially when trying to figure out the lowest frequency in the simulation by looking at the plot. Hence, we decided to use the Pearson’s r to evaluate whether the simulation has substantial low frequency variability or not. Moreover, the reviewer was concerned that the length of each simulation can affect the significance of the Pearson’s r. In response to this, we have computed the p-values of the correlation coefficients and they are statistically significant (apart from the FGOALS-f3 PI experiment whose r value is not statistically significant, possibly due to the short run length of just 50 yrs, as we use historical experiment in this model to substitute the PI experiment (see Tab 1 captions)).

For Sect. 4.2, one reviewer suggested that we should shorten this part and focus more on the AMOC itself as expecting from the title, while the other reviewer wanted more investigations on the AMOC’s impacts on tropical precipitation centre. Considering both comments, we will have more concise descriptions on the AMOC’s fingerprint in the revised manuscript, but also investigate more on the impacts of AMOC changes on the shifts in precipitation centre (e.g. by regressing the changes in the core location of the ITCZ onto the AMOC changes, etc.). However, how the sea-ice would response and potentially feed back to the AMOC changes are for future work, as our current approach is not sufficient to identify the direction of any feedbacks.

We apologise for having only written a cursory discussion of the existing literature on proxy data. In a revised Sect. 5, we will add further detail on the palaeo-data side using the existing literature of more detailed modern oceanography studies. Meanwhile, we will add all the references when referring to the existing palaeo data base.

For all other comments (such as the ‘rationale for choosing the timeslice’), grammar and spelling mistakes, explanation for a specific sentence, etc., we will make corrections and add explanations for them.

Citation: https://doi.org/10.5194/cp-2022-63-AC1

Peer review completion

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

ED: Publish subject to minor revisions (review by editor) (30 Oct 2022) by Laurie Menviel

Dear Zhiyi Jiang,

I have assessed the Reviewers’ reports as well as your response and I am happy to invite you to submit a revised version. At the end of this email, I also include some comments that you may consider. Please note that a point-by-point response to all the reviewers’ comments should be included, as well as a tracked-changes version of your revised manuscript.

Looking forward receiving your revised manuscript.
Best regards,
Laurie

Table 1: It would seem appropriate to me to include references to the model descriptions and/or mid-Holocene and lig127k simulations. Readers might want to go back to the original work to obtain more information on methods and climatic states.
Please be more precise in the caption regarding “Simulation length”. You are not showing the total length of the simulations, but instead are showing the length you are using for your analysis (I guess). This is probably determined by what is currently available on the ESGF website.

L. 179-180: There is a problem with that sentence.

Figure 5 (and associated section 4.2): As is, this figure worries me and in fact could be misleading. For example, it shows that large areas of the Arctic/North Atlantic eastern Europe TAS changes are only due to AMOC changes (100%). Without seeing the absolute TAS changes between the mid-Holocene and PI, one could wonder whether the results shown in Fig. 5 are all relevant/significant. If the mid-Holocene TAS changes in a particular location are not significant to begin with, this percentage analysis might give biased results. In addition, deconvolving changes due to orbital parameters and AMOC might not be that straightforward. This can be illustrated by the results shown for the IPSL. It is noted that in this mid-Holocene simulation more than 40% of the changes can be explained by AMOC changes, while the AMOC is only 0.5 Sv lower, which is not statistically significant (as per Tables 1 and 2). So how come a non-statistically significant and very small AMOC weakening explain large areas of the mid-Holocene TAS changes?
I suppose that one way around that would be to show the absolute mid-Holocene TAS changes for the simulations, with statistical significance overlaid and next to it show the absolute TAS changes that could be attributed to the AMOC, also including statistical significance. Please also modify section 4.2 accordingly.

L. 251: The IPSL mid-Holocene AMOC is slightly weaker than at PI (and not statistically significant).

Discussion: I agree with the Reviewers that a more extended discussion of AMOC inferences from paleoproxy records is needed. You might also want to look at https://cp.copernicus.org/articles/17/507/2021/ , which suggested that there was no no significant difference in the latitudinal and depth extent, as well as mean transport of North Atlantic Deep Water (NADW) between the LIG and the Holocene (7-2ka) using an updated d13C compilation.

Hide

AR by Zhiyi Jiang on behalf of the Authors (16 Nov 2022) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (26 Nov 2022) by Laurie Menviel

Dear Zhiyi Jiang,

Thank you for submitting your revised manuscript “No changes in overall AMOC strength in interglacial PMIP4 timeslices”. While you have tried to appropriately answer the Reviewers and my comments, I still have an issue with Figures 5 and 6 and the associated text as detailed below. In addition, most of the additional text is not grammatically correct, making it difficult to understand its meaning. I thus suggest you consider the appropriateness of trying to highlight how the AMOC could impact regional climate, while there are no significant changes in AMOC. In addition, please seek help from your co-authors to provide a grammatically correct text.

Best regards,
Laurie

Figure 5 bottom row: I do not see the point in adding these 2 figures. If there are no significant AMOC changes, then the AMOC changes cannot explain any of the temperature changes.

Figure 6: 90% of the globe falls in the 0 to 10% band. Noting that only 3 models display an AMOC change greater than 5% at the mid-Holocene and that for the LIG 3 display a stronger AMOC while one displays a weaker AMOC, the results are not surprising, but I don’t think they add any information. Noting that multi-model means of mid-Holocene and LIG precipitation anomalies are shown elsewhere, I would suggest to remove that figure and the associated discussion.

Minor issues, mostly due to language. Please note that the line numbers refer to the manuscript version with tracked changes.
L. 6: rephrase to “3 experiments representing different interglacial conditions”
Paragraph starting L. 25: Please note that AABW is also part of the AMOC
L. 49: remove “The”
L. 140-155: There are many typos, repeats, and inconsistencies in these paragraphs. Please check them carefully, making sure the grammar is correct and therefore the meaning is also correct.
L. 176-177: I don’t understand what you mean here
L. 290-291: grammar inconsistency
L. 347: Remove “across the global”
L. 381: They do not indicate substantial changes in AMOC strength.
L. 388: Please replace “In addition” by “even though”

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AR by Zhiyi Jiang on behalf of the Authors (13 Dec 2022) Author's response Author's tracked changes Manuscript

ED: Publish as is (14 Dec 2022) by Laurie Menviel

AR by Zhiyi Jiang on behalf of the Authors (15 Dec 2022) Author's response Manuscript

Short summary

This work looks at a series of model simulations of two past warm climates. We focus on the deep overturning circulation in the Atlantic Ocean. We show that there are no robust changes in the overall strength of the circulation. We also show that the circulation hardly plays a role in changes in the surface climate across the globe.