This study focuses on understanding the interannual and decadal variability in Southern Ocean CO2 fluxes and their links to the Southern Annular Mode (SAM). This research is particularly significant because few numerical modeling studies investigate anthropogenic and natural carbon fluxes separately. As a result, this study is unique, aligns well with the scope of the journal, and makes a meaningful contribution to the existing literature.

Throughout the manuscript, I encountered difficulties following the connection between the figures and the text (see specific comments below). Additionally, certain statements in the manuscript are difficult to comprehend within the context provided (see specific comments below). Revising some of these points to create a more concise and coherent format would greatly benefit the manuscript.

Moreover, the authors emphasize that their study differs significantly from Lovenduski et al. (2008) due to the use of a high-resolution model. As a reader, when going through the introduction, I anticipated a more extensive discussion and conclusion section addressing the impact of using eddy-resolving models. Additionally, I expected to see some recommendations as a conclusion. However, this was not the case, as it was only briefly mentioned in one or two sentences in the discussion section. I suggest expanding the discussion on the effects of using high-resolution models in such studies, even in a broader context.

Specific comments and minor changes

Methods:

Line 94: "has many improvements“

Could you provide more specific details regarding the improvements in the model? Additionally, please explain why the inclusion of "ocean biogeochemistry with two-way coupling to nutrient and algae carried in the sea ice model" is important for this study?

Line 106: "The air-sea CO₂ exchange is a function of ….."

When reading this sentence, it seems to suggest that there is no effect of DIC concentration. However, this is not true. The authors also mention in the results (line 228, line 258-259) that outgassing primarily results from an increase in surface nDIC concentration.

Line 132: "To better understand ….."

With the limited description provided, it is challenging to comprehend the method employed by the authors. They reference a substantial book that may not be accessible to everyone. As a result, a more detailed explanation of the equations (1 and 2) is essential in this manuscript.

Results:

Line 154-155:

"tco2 fluxes can be compared to observational ….."

A more detailed description of the observations and the model, along with quantification, is needed. I expect the authors to present a comparison, explaining their approach and how the models and observations compare. Furthermore, the manuscript contains a statement about being in agreement with observations. How and where can a reader verify this? If applicable, please clarify the connection to the relevant figures.

Line 164:

"While simulated nco2 ….."

What is the reason for the sudden comparison of these two specific time periods (1980-1984 and 2017-2021)?

Line 167:

"Through Ekman transport ….."

There seems to be no link between this statement and the figures included in the paper, so I suggest establishing a connection with the appropriate figure. Moreover, the manuscript first mentions the impact of phytoplankton on DIC here. I recommend elaborating on this effect in the methods section. If the effect is substantial, a more detailed description of the biogeochemical model (WOMBAT here) and a summary figure would be beneficial.

Line 171:

"The nco2 ….. "

Could you please provide a reference to a particular figure where this information can be easily followed?

Line 171:

"While this is compared SAM index ….. "

The comparison made by the authors is not evident within the paper, requiring readers to consult the Marshall 2003 paper. For improved clarity, could you add Marshall's data to the relevant figure and mention that figure in this statement?

Line 178:

"The nco2 ….. "

The authors suddenly give a spatial pattern. What is the reason for this? It does not appear to be relevant to this subsection.

Line 185:

Similar to the previous comment for line 178. The authors suddenly report a spatial pattern.

Line 189-193:

Is a correlation alone enough to indicate agreement with the observations? A more comprehensive explanation would be helpful.

Line 196:

"The detrended tco2 ….. "

This statement needs to be linked to a particular figure for better understanding.

Line 205:

"Changes in SST ….. "

This information is not visible or easily accessible to the reader.

Line 208:

" On the other hand ….. "

The year 2015/16 is unexpectedly mentioned. What is the reason for this, and where can we locate this information?

Line 214:

" The inter-basin….. "

This point requires a clearer association with the relevant data or figures.

 Line 220-225:

The explanation is not easily understandable.

Line 250-251:

"This is however ….. "

Why is this the case? Where can the reader locate information that supports this statement?

Line 265:

The abbreviation AABW has not been mentioned in the text previously.

Line 268:

It's unclear from the sentence which figure supports this statement. What is the relation between oxygen and remineralized DIC in your model, can you provide some more explanation?

Line 271-275:

This paragraph cannot be fully understood or supported by the figures presented in the manuscript. If the authors claim a relationship between a specific variable and weak biological pump efficiency, they should provide a clear link between their statements and the relevant figures. However, it appears that the claim of weak biological pump efficiency is not presented or supported by any of the figures in the manuscript. Therefore, the authors should consider revising their analysis or adding a new figure to better support this claim or revise their statements to more accurately reflect the evidence presented in their figures. In general, it's important for authors to ensure that their claims are well-supported by the evidence they present and to provide clear links between their statements and the relevant figures to help readers understand and interpret their results.

Line 278:

The abbreviation "NADW" is not introduced or defined in the manuscript.

Line 281:

"At both ….. "

What is visible? If it is visible, please provide a reference to the relevant figure to support your claim or statement.

Line 292-295:

Please provide a clear link to the relevant figure to support your claim or statement.

Line 296-299:

How can the reader follow the CDW in Figure 7? It needs a better description of the figure.

Discussion and conclusion:

Line 315-316:

What are the numbers. Please quantify.

Line 318-319:

"It should be noted …. "

What are the authors trying to convey with it? It would be better to be more specific.

Line 320-321:

"In addition, underestimation …. "

Does your model have this problem? If so, could you please mention it and show it first in the results section?

Line 345:

"we find that biological processes …. "

How did the authors reach this conclusion? There was not much related to biological processes throughout the results section. Could you please specify what you mean by 'biological processes'?

Figures:

Figure 1:

I suggest adding the PF and SAF contours to subfigure a.

It would be helpful to provide the full names of the abbreviations 'PF' and 'SAF' in the figure label.

Figure 2:

The x-axis should also include a tick mark for the year 1970.

Figure 3:

The x-axis should also include a tick mark for the year 1980.

Figure 4:

The unit of nCO2 flux (mol C/ m2/yr) like in Figure 1?

Figure 5:

What is the maximum and minimum extent of the y-axis in the plots?

What is meant by detritus flux, is it export production?

What is meant by "actual data"?

Figure 7:

Why were these two time periods chosen for analysis?

Why is the contour in Figure 7(j) different from those in Figures 7(c), 7(f), and 7(l)?

What is it being compared to Gruber et al. 2019. ?

Figure 8:

Please specify the time frame being discussed to avoid confusion.

Menviel et al. analysed the Southern Ocean CO₂ sink using an eddy-rich global ocean biogeochemical model. Based on the results of their model, they argued that variations in the Southern Ocean CO₂ sink are mainly driven by changes in the outgassing of natural CO₂ and are related to the Southern Annular Mode (SAM). This variability in CO₂ flux could be explained by variations in surface dissolved inorganic carbon (DIC).

Such a modelling study, using a high-resolution ocean model, is essential as most of the currently used global ocean biogeochemical models cannot resolve eddies. The results presented in this study could help to improve our understanding of the Southern Ocean CO₂ sink. However, I have some questions about some of the results presented in this study (major comment). Therefore, the paper will probably be a significant scientific contribution with some revisions.

Major comments:

1) Authors mentioned that they model can reproduce some decadal variabilities of the Southern Ocean CO2 sink suggested by an observation-based product (i.e., SOM-FFN), and suggested an influence of the SAM, line 5: “The simulated total CO2 flux exhibits decadal scale variability […] in phase with observations and with variability in the Southern Annular Mode (SAM). Notably, a stagnation of the total CO2 uptake is simulated between 1982 and 2000, while a re-invigoration is simulated between 2000 and 2012.”

These statements seem to be supported by the lines:

• Line 173: “nCO2 fluxes are strongly correlated with the SAM index calculated from the JRA-55do dataset (R=0.62 for annual mean data and R=0.82 with a 5-year smoothing, Figs. 2b and S3)”
• Line 192: “The simulated and observational estimates of tCO2 flux are well correlated (R=0.55) and both display minimum tCO2 uptake in 2000-2001, and maximum in the early 1990s and early 2010s.”
• Line 197: “The nCO2 flux variability dominates the changes in tCO2 uptake with a strengthening of the winds and a poleward shift both reducing the tCO2 uptake (Figs. 2c,g and S3).”

Did the authors remove the trends from the time series of nCO2, tCO2 (from their model and from SOM-FFN) and SAM before calculating the correlation coefficients? If not, the correlation coefficients between nCO2 and SAM, or between simulated and observed tCO2 estimates, are mainly influenced by the linear trend and do not provide information on the phasing between observed and simulated signals.

Furthermore, according to Figure 2, the stagnation in tCO2 uptake suggested by SOM-FFN is limited to the 1990s and not between 1982 and 2000 as the model simulated. In SOM-FFN, a reinvigoration occurred between 2000 and 2012, while the model simulated a reinvigoration only in the early 2000s (as the authors also mention in line 335: “In agreement with observations, a re-invigoration of tCO2 uptake is simulated in the early 2000s.”). Therefore, the statement “in phase with observations” in the abstract is misleading and does not seem to be supported by the authors' results. The relationships presented in this manuscript are specific to their model and cannot be fully used to explain the variations in the Southern Ocean CO2 sink suggested by the observation-based method.

If possible, and to better assess the added value of using a high-resolution ocean model, a comparison between tCO2 in the Southern Ocean simulated by the eddy-rich model presented here and by a global ocean biogeochemical model with lower spatial resolution should be added to Figure 2 (and in the manuscript).

2) An important result from this modelling study is that “The total SO CO2 uptake capability thus reduced since 1970 in response to a shift towards positive phases of the SAM.” (line 13).

As mentioned by the authors in the introduction, Line 66: “More recently, by analysing changes in SO tCO2 fluxes between 1980 and 2016, Keppler and Landschützer (2019) suggested that the net effect of the SAM on tCO2 uptake was nil and that instead the variability was arising from regional shifts in surface pressure linked to zonal wavenumber 3.”

The authors need to discuss the discrepancy between their results and the results from Keppler and Landschützer (2019). Is a trend toward more positive SAM the only reason to explain a reduced CO2 uptake capability by the Southern Ocean since 1970? What about the other factors that could induce a long-term increase in the vertical stratification of the Southern Ocean and reduce its ability to absorb anthropogenic CO2 (e.g., Bourgeois T, Goris N, Schwinger J, Tjiputra JF. Stratification constrains future heat and carbon uptake in the Southern Ocean between 30°S and 55°S. Nat Commun. 2022, 13(1))? Although the SAM index could have an influence, it seems that other mechanisms can also influence the long-term changes in the Southern Ocean CO2 sink and need to be evaluated and discussed.

Minor comments:

3) Several references could be added in the introduction section and help the discussion. For example, studies that are partly based on observations and that have also demonstrated the influence of the SH westerlies on the air-sea CO2 flux:

• Gregor L, Kok S, Monteiro PMS. Interannual drivers of the seasonal cycle of CO2 in the Southern Ocean. Biogeosciences. 2018, 15(8), 2361–78.
• Nevison CD, Munro DR, Lovenduski NS, Keeling RF, Manizza M, Morgan EJ, et al. Southern Annular Mode Influence on Wintertime Ventilation of the Southern Ocean Detected in Atmospheric O2 and CO2 Measurements. Geophys Res Lett. 2020, 47(4), e2019GL085667.

An important modelling study that focuses on natural carbon variability:

• Resplandy L, Séférian R, Bopp L. Natural variability of CO2 and O2 fluxes: What can we learn from centuries-long climate models simulations? J Geophys Res Oceans. 2015, 120(1), 384–404.

The most recent review about the ocean CO2 sink variability:

• Gruber N, Bakker DCE, DeVries T, Gregor L, Hauck J, Landschützer P, et al. Trends and variability in the ocean carbon sink. Nat Rev Earth Environ. 2023, 4(2), 119–34.

4) Line 120: “Biogeochemical fields other than oxygen were initialised at the start of cycle 4 (1958). A uniform 0.01 mmol m−3 initial value was used for phytoplankton, zooplankton, detritus and CaCO3. […] Here, we skip the first twelve years of the fourth cycle (i.e. 1958-1970) from our analysis to allow the simulation to recover from the reset at the end of the previous cycle”

Twelve years is a relatively short period for the model to reach a steady state or recover from the reset. Could you provide in supplementary figures evidence that the biogeochemical fields have reach a steady state?

Could this influence the conclusion that (line 345) “we find that biological processes do not significantly impact air-sea CO2 fluxes on decadal-time scales, and that the changes in surface nDIC arise from changes in oceanic circulation”?

5) Line 155: “…from autonomous biogeochemical floats (Gray et al., 2018; Prend et al., 2022).” In figure 1 caption, it says Bushinsky et al. (2019). Which one is used?

6) Line 161: “…highlighting an uptake of aCO2 everywhere south of 35°S (Fig. 1d), with a maximum south of the PF (∼56.3◦S, Fig. S2d).” This is quite surprising. Normally, most of the aCO2 uptake should occur more north between the Polar Front and the Subpolar Front. For example, in:

• Gruber et al. (2019 – Annu. Rev. Mar. Sci.): “In contrast to natural CO2, the entire Southern Ocean south of 35°S is a sink for anthropogenic CO2 […] The majority of this uptake occurs between the Antarctic Polar Front and the Subpolar Front, leading to a distinct ring of high-uptake fluxes at the latitudes between 45°S and 55°S.”
• See also figure 4 in Gruber et al. (2023 – Nat. Rev. Earth Environ.).

Could you explain the reason for this misrepresentation of the aCO2 uptake, and how is this impacting the conclusion (line 305) “the strengthening and poleward shift of the SH westerlies only had a small impact on aCO2 uptake “?

7) Line 176: “…similar correlation…” The correlation value needs to be provided in the text.

8) Line 178: “The nCO2 outgassing occurs in…” and line 185: “The increase in aCO2 uptake occurs everywhere…” These sentences can be removed as the information was provided in the previous section 3.1.

9) Line 183: “A weak correlation…” is the correlation statistically significant or not?

10) Figure 3 and Line 202: “As the outgassing of nCO2 occurs south of the SAF, we focus our analysis on that region. The natural pCO2 increase south of 50°S…”. A clear definition and location of the front is provided (e.g., Figure 1). Instead of using the 50°S limit, the values should be averaged exactly is the area south of the front.

11) Section 3.4. “Changes in oceanic DIC”. This section presents results which are not used in the following discussion. Furthermore, the figure 7 is the same as figure S8. These results need to be compared and discussed with published studies, otherwise this section should be removed.