Dear Klaus Wallmann,

Thank you for your responses to the review comments. I would like to invite you to submit a revised manuscript version that addresses carefully all of the substantive reviewer comments that have been raised.

However, the manuscript revisions should be ‘major’, in the sense that, in addition to making specific clarifications, they should also reflect a significant change in the way that the interpretations and conclusions are reported. More specifically I would urge you to address the second reviewer’s comment (regarding ‘over confidence’) by carefully revising the precision of the language used to describe the model results and conclusions. While I agree that it is warranted to have confidence in the robustness of the model methodology per se, this does not mean that it is warranted to have complete confidence in the specific scenario that has been chosen here, let alone any conclusions regarding what actually happened over the last glacial cycle. Indeed, the manuscript currently reads throughout as a description of what happened in the past, rather than what happened in the model (e.g. “nutrient and CO2 concentrations in surface waters of the Southern Ocean were reduced by iron fertilization … The remaining portion of the interglacial-to-peak glacial pCO2 drop by 13 ppmv down to the final LGM value of 190 ppmv was induced by ocean dynamics…”). Similarly, it is surely important (especially in a model study such as this) not to confuse hypothesized proximal causes in the past (e.g. ‘iron fertilization’) with ultimate causes in the model (e.g. arbitrarily increased export productivity). I think that carefully revising the entire manuscript text to address this issue of semantic precision is not merely stylistic, as it ultimately may be seen as affecting the accuracy and therefore the legitimacy of the claims made in the paper. In my view, a reader of this study would primarily (though of course not exclusively) be rewarded with a novel consideration of the effects on atmospheric CO2 of POM and nutrient cycling at continental margins under eustatic sea-level change (albeit in a highly idealized manner), which should be accompanied by a clear description of the limitations of these processes (e.g. for explaining very rapid changes in carbon cycling). In light of this, I would also suggest that the last two paragraphs are somewhat speculative and represent more of a starting point (i.e. a set of hypotheses; mostly well established in the literature), rather than a clear set of conclusions that emerge from this study specifically.

I look forward to receiving your revised manuscript and feedback.

Sincerely,

Luke Skinner

Dear Klaus Wallmann,

My apologies for the delay in responding to your revised manuscript submission, and my thanks for your patience.

It seems to me that nearly all of the comments made by the reviewers have been adequately addressed. However, i think there is one (potentially important) comment that demands further clarification or revision. There are also a few comments of my own that i would add; along with apologies for not delivering these to you previously. I hope that these further comments are welcome.

The main review comment that i think demands further attention is the one regarding atmospheric d13C. You state that this cannot be simulated by the model because it depends on fine-scale processes that are not resolved by the model (esp. in the Southern Ocean). I would propose that this is not obviously true. If the carbon fluxes to/from the atmosphere from the various other reservoirs (the ocean in particular) are correct then the d13C of the atmosphere should reflect this, in the same way that the d14C of the atmosphere should. Furthermore, while it is true that the ocean's d13C is not going to be affected much by imposing a fixed atmospheric value, it is also true that the atmospheric d13C value will also represent a very sensitive indicator of whether or not the fluxes of atmospheric carbon to/from the various other reservoirs ARE correct. If the model struggled to simulate atmospheric d13C accurately, is this not a clear indication that something is amiss with the model processes?

A further comment of my own, which is related to the above, is that i am not sure that it is sensible to have simulated the atmospheric 14C production rate in a manner that arbitrarily adds/removes radiocarbon from the system in order to restore atmospheric radiocarbon to observed values. The accuracy of doing this depends on the accuracy of your modelled processes - assuming they are correct would be circular. Indeed, like with d13C, the atmospheric d14C represents a very sensitive indicator of whether or not the fluxes of carbon to/from the various other reservoirs from/to the atmosphere are indeed correct. Therefore, the use of radiocarbon production rates that are defined so as to reconcile the prescribed ocean/weathering etc... processes with observed atmospheric d14C would appear to 'beg the question' with respect to the accuracy of the prescribed ocean/weathering etc.. processes. Or, put another way, like with d13C, atmospheric d14C is being passed up as a very sensitive test of the processes that are prescribed in the box model. My own experience (limited compared to yours i am sure) is that glacial-interglacial atmospheric d13C and d14C can indeed be readily simulated in box models so as to mimic observed values, but that the problem is (as i am sure you would agree) in knowing that this agreement has been achieved for the right reasons. As you correctly point out in the appendix, atmospheric d14C is a very sensitive marker of the balance of radiocarbon production and ocean-atmosphere carbon exchange (and i would add the details of what parts of the ocean are connected to the atmosphere and on what timescale), and for this reason i would propose that your method of forcing it to agree with observed values (e.g. rather than using estimated of production rates from e.g. palaeomagnetic intensity/10Be fluxes) may not only be problematic with respect to correctly simulating the global radiocarbon budget but may also represent a missed opportunity to validate the model premises.

I would make a few other minor comments that i invite you to consider:

1. I would suggest to add something to the title to indicate that this is a model study, for example adding "Simulated" at the beginning, or ":a model study" at the end.

2. Page 12, lines 3-12: Please add a note of when these processes occurred (e.g. glacial, deglaciation?). Also, the last line is perhaps overly vague: is it really just a model/detail problem; what about clues from timing and timescales (e.g. the observed centennial/millennial pulses in CO2 and their occurrence during North Atlantic D-O onsets/stadials)? Are the latter consistent with permafrost melting or volcanism due to lithospheric adjustments? Perhaps lengthy comment is not warranted here in the manuscript, but i wonder if a less vague statement can be made?

3. Page 11, lines 25-30: regarding "The subsequent restoration of the vertical DIC gradient induced the pCO2 decline observed in the model from 10 to 8 ka." Perhaps add a note indicating what process(es) ensured that the restoration of the DIC gradient was a slow process (millennia).

4. Page 15, lines 24-27: How does enhanced production of CaCO3 and pelagic carbonate burial (sourced from the surface ocean) lead to net removal of (dissolved) CO3-- from the DEEP ocean?

Thank you again for your patience these past weeks. I sincerely hope that these comments are found to be constructive, and that once they are addressed your manuscript may move towards eventual publication.

Sincerely,
luke

Dear Klaus,

Thank you for your response to my last comments on your manuscript, in addition to the reviewers comments. While i understand fully your reasons for adopting the approach to modelling the atmospheric carbon isotopes, i am afraid that i am not in agreement with all of your claims. In particular i remain convinced that atmospheric D14C represents the combined effects of two main contributions (in addition to decay): 1) production rates; and 2) carbon exchange with the ocean (and biosphere/lithosphere), which in turn depends on ocean circulation and also affects atmospheric CO2. You aim to constrain the latter via simulations, but you also constrain atmospheric D14C by assuming knowledge of the latter (i.e. the production rates you determine are the ones *needed* to reconcile observed atmospheric D14C with your simulated marine carbon cycling); to me this is indeed somewhat circular.

Notwithstanding these concerns of my own, i am happy to accept your manuscript for publication in Climate of the Past, based on the formal review comments, which clearly support publication. As you say, your methods are clearly described and are open to falsification, or otherwise.

Thank you very much for your patience and participation this review process. I look forward to seeing your manuscript in print in due course.

All the very best,
Luke