Waelbroeck et al. present a manuscript that interprets observed changes in δ¹³C following the transition between Heinrich Stadial 4 (HS4) and Greenland Interstadial 8 (GI8). The paper has potential in that it is one of the few existing model-data comparison works in a dynamical perspective. However, some issues associated with the methodology require further attention. 

General comments:

The authors first describe their δ¹³C records, which consist of 110 Atlantic sites. Due to the resolution needed to correctly capture a rapid climate change scenario such as the end of HS4 the analysis is made with only 18 of those sites. They then run a simulation with a global ocean model where a hosing experiment is used to generate an AMOC slowdown and shallowing typical of a HS scenario. δ¹³C from the simulations is computed from PO4 and is an approximation. As shown in Fig. S1, the model-data agreement is challenging due to offsets and also differences in trends. To circumvent this, the authors compare δ¹³C changes (Δδ¹³C) between after and before the end of the hosing with GI8-HS4 reconstructed δ¹³C changes. This arises some questions that need to be addressed in the paper: 

How are the sigma uncertainties from the data calculated? Are they the standard deviation associated with the averaging of the data in two 500 y intervals? The authors should specify this in the text. 

One problem associated with using Δδ¹³C is that these differences are of the same order of magnitude than the propagated uncertainties expressed in terms of σ. Following Table 1 it seems that σ is larger than Δδ¹³C for sites TN057-21, MD03-2698, KNR191-CDH19, SU90-44, U1308, MD07-3076Q, and MD95-2040. This means that in those sites either a decrease or an increase in the δ¹³C computed from the models could agree with the data. The authors should either remove these sites from the analysis, or make a further statistical test to show the significance of the mean Δδ¹³C at each site taking into account the plus minus σ reported. For example, calculating the 5% and 95% confidence intervals. 

The computed Δδ¹³C from the models, as well as those from the data, are very small. The authors show the model-data comparison for one computer simulation experiment. With such small numbers and big uncertainties, I am curious to know if a similar plot as Fig. 1 could be generated with other scenarios. For example, would a reverse climate scenario (from strong to weak AMOC) to the one presented here show a similar agreement between model calculated and Cibicidoides Δδ¹³C? This is like reversing the y-axis in Fig. 1; in principle it seems that several sites would still have horizontal uncertainties falling into the 1:1 line. What about using two random years of the simulation (either during the hosing or outside that time interval)? Could a Δδ¹³C computed from the internal variability of the model produce a plot like Fig. 1, with a majority of sites having their horizontal uncertainty fall into the 1:1 line? Fig. 1 is the corner stone of this paper. The authors should give evidence that their result of good model-data agreement for a "during hosing-after hosing" transient model scenario is significant, and that within the ability of their methodology the solution is unique. The analysis that follows in the paper, regarding nutrients and water mass distribution is interesting and could be innovative. But it would only be conclusive if the authors show evidence that, with the available data, the scenario they suggest from Δδ¹³C is the most likely for the HS4-GI8 transition. 

Minor comments:

Both in Table 1 and Fig. 1 the authors show that some sites result in poor model-data agreement (i.e., they don't fall into the 1:1 line). The authors mention the position of some of these sites and suggest reasons for the disagreement. However, the paper would benefit from both a map and a depth-latitude section where the reader could see where exactly the three types of sites are located (black, green, and red according to Fig. 1 and Table 1). I think these two plots could be added as extra panels in Figure 1. This would help for example to see if all major regions of the Atlantic are covered by the "good agreement" sites. The significance of the nutrients, preformed nutrients, and remineralized nutrients analysis that you present later in the paper will be stronger if all the Atlantic regions where you discuss possible water mass distribution changes are covered by the data. 

In this work, the authors combined Cibicides d13C records from the Atlantic Ocean with a common chronological scale with the NorESM1-F model simulation results to evaluate the influence of different factors on d13C across the HS4-GI8 transition. Since the NorESM1-F model is not isotope-enabled, the authors calculated d13C-BIO values that were assumed to reflect circulation changes. The fresh water perturbation was carried out to mimic the HS4-GI8 transition. Then, the difference of d13C-BIO across the transition (delta d13C-BIO) was compared to delta Cibicides d13C. Based on the general correlation between the delta d13C-BIO and the delta Cibicides d13C, they validated their simulation and quantified the influence of water mixing ratio of NSW and SSW and of organic matter remineralization on d13C-DIC.

The used proxy records are selected from a large database that the authors have created with considerable efforts. Even if the model is not isotope-enabled, the hosing experience under glacial condition with active biogeochemical module is highly interesting. I would like to see this work published in Climate of the Past. I have several major concerns before the definite acceptance of the present work.

1. The way of validation of simulation results

The data-model comparison that validate the modelling approach resides essentially on the relationship between delta d13C-BIO and 18 records of delta Cibicides d13C (Fig. 1).  All the observed disparities between them were explained by the problem of proxy records (Mackensen effect and low sedimentation rate). Even if I generally agree with the authors, potential bias on simulation side should be explained briefly. Indeed, the authors indicated the possibility of such offsets on lines 162-163.

2. Limited data-model comparison

The story presented in this work is strongly dependant on simulation results. It will be interesting to add more comparison with other proxy records to further strengthen the message. For example, deep water stratification proposed by this study could be examined using benthic foraminiferal d18O without distinguishing temperature and salinity component as proposed by Lund et al. (2011). A small d18O amplitude compared to laboratory offsets could be a problem but this possible bias would be reduced by the use of delta Cibicides d18O like delta Cibicides d13C. Ideally such a comparison would be realized for the 18 records used for delta Cibicides d13C.  I understand that there are few other proxy records that allow comparison with simulation results of this study because of a large chronological uncertainty, a poor temporal resolution and a low sedimentation rate of archives. Nevertheless, additional data-model comparison of other proxy records could be helpful (ex. Piotrowski et al., 2008; Gutjahr et al., 2010; Bohm et al., 2015).

3. Interest in the HS4-GI8 transition

Only a rapid increase in Greenland and North Atlantic surface temperatures is indicated as a motivation of the study period. The interest in the HS4-GI8 transition should be more developed to better justify the focus of the study taking into account the scarcity of available data and the chronological uncertainty of the selected period. Did the authors consider this interval as a key period to examine model performance for the future projection? Please add more explanation.  

A comparison of HS4-GI8 transition with other stadial-interstadial transitions would be also interesting. For instance, an essential role of organic matter remineralization on d13C was proposed for the HS1- LGM transition (Gu et al., 2021), which contrasts with the results of the present study. It is true that HS1- LGM transition is not during the last glacial period, but the comparison may provide further insight into the mechanism. Since the manuscript is rather short, the authors are invited to add these points to discussion.

I recommend to accept this work after minor revision.

Minor / specific comments

Throughout the text. Both “Cibicides d13C” and “Cib. d13C” are used. It is better to uniform the term.

Line 51. Replace “neodymium radiogenic isotopes” by “neodymium isotopic composition”.

Line 52. Add corresponding references after “Cd/Ca” to the indicated proxies.

Line 82. Replace “concentration” by “composition”.

Lines 122-127. About BGC simulation. Once the BGC component is activated, BGC module is fully coupled to physical model? Which size of BGC tracer changes as a function of time are considered as a satisfactory quasi-equilibration state? As the authors mentioned, equilibrium time for BGC tracers should be very long.

Lines 134-135 and 139. “by (Jansen et al., 2020)” should be replaced by “by Jansen et al. (2020)”.

Line 135. Remove “in” after “500 years”.

Line 139. “As shown by (Janssen et al., 2020)” should be corrected to be “As shown by Janssen et al. (2020)”.

Line 204-205. “Therefore, this would warrant to expand the model time scale by a factor of ~2.” This sentence is unclear for me.

Lines 214-217. Here the authors mentioned Mackensen effect as one of the possible reasons for the disagreement between simulated delta d13C–BIO and delta Cib d13C. Since the different d13C values between C. kullenbergi and C. wuellerstorfi is cited, it will be helpful to add considered benthic foraminiferal species to Table S1.

Fig. 1. I believe that this is a key figure of the present study and I would like to see whether there is any spatial trend. It will be useful to show the same figure using a colour code with (i) latitude and (ii) water depths.

Fig. S1 caption. Add “black curve” and “symbols” after “d13C-BIO” and “times series”, respectively.

References

Bohm, E., Lippold, J., Gutjahr, M., Frank, M., Blaser, P., Antz, B., Fohlmeister, J., Frank, N., Andersen, M. B., and Deininger, M.: Strong and deep Atlantic meridional overturning circulation during the last glacial cycle, Nature, 517, 73-76, 2015.

Gutjahr, M., Hoogakker, B. A. A., Frank, M., and McCave, I. N.: Changes in North Atlantic Deep Water strength and bottom water masses during Marine Isotope Stage 3 (45–35kaBP), Quat. Sci. Rev., 29, 2451-2461, 2010.

Lund, D. C., Adkins, J. F., and Ferrari, R.: Abyssal Atlantic circulation during the Last Glacial Maximum: Constraining the ratio between transport and vertical mixing, Paleoceanography, 26, PA1213, 2011.

Piotrowski, A. M., Goldstein, S. L., R, H. S., Fairbanks, R. G., and Zylberberg, D. R.: Oscillating glacial northern and southern deep water formation from combined neodymium and carbon isotopes, Earth and Planetary Science Letters, 272, 394-405, 2008.

Dear authors:

I have a comment on your manuscript, regarding time scales. Since your model does not include prognostic d13C, you approximate it to d13C from remineralization origin (d13Cbio) via an expression that relates d13Cbio with PO4. That relation has been tested in Edie et al., 2017 for the preindustrial equilibrium state. However, in your manuscript you assume that the relationship is still valid for a change in d13C, between two time intervals from your simulations. Since the equilibrium time for d13C is slower than for PO4, do you have any evidence that the d13C - d13Cbio - PO4 relationship is still valid in a transient simulation?

Thank you for the response.