Dear Carlos,

I'd like to thank you and your co-authors for your thorough and considered responses to the two referee reports. The verdicts of both referees on the scientific merit differ markedly, but both acknowledge the value of introducing CBS as a meaningful concept.

Given the substance of critical comments, I have decided that you should have the opportunity to submit a substantially revised manuscript, which will be reviewed again before a final decision about acceptance. You indicate a range of revised sections in the manuscript in your response, and I hope that you are able to alleviate all concerns by these. I think that the main objective of your contribution should be the introduction of the CBS as a novel concept (if not metric), rather than a simulation study attempting to compute carbon cycle feedbacks.

Best wishes,
Jens

Dear Carlos,

I have received three reports for your manuscript. These are generally supportive, and I would like to encourage you to address the points raised by referees. One referee report was not uploaded to the editorial system, but I include the comments below with apologies for this slightly unconventional way of getting these to you.

Whilst the referees raise a number of issues, I think that these can be addressed in another round of revisions, and would like you to address the points by referee 1 and referee 3 (below).

Best wishes,
Jens


Recommendation: Revisions

The manuscript submitted by Sierra et al introduces the maths behind a useful metric for quantifying “The Climate Benefit of Carbon Sequestration” as the title suggests. The work focuses on a simple concept that needs to be understood more broadly – that a unit of carbon removed from the atmosphere by net ecosystem productivity in a given year does not have an infinite lifetime in that ecosystem and that the timing of its return to the atmosphere should be factored into the accounting of climate benefits. Indeed, this time element of accounting is critical for a full assessment of the true climate benefits of emissions and sequestration, and has been particularly underappreciated when assessing climate change mitigation opportunities via a sequestration pathway.

This idea is not new to those with expertise in the coupled carbon-climate system, but the introduction of this quantitative metric provides a new tool in the toolbox that should improve the work of scientists, policymakers and managers alike. Unfortunately, the paper does a poor job of displaying and communicating the application of this metric for real-world situations. As previous reviewers have noted, the examples are hard to follow and are not clearly illustrative. It would be nice to see the manuscript revised to make the examples more accessible. This is not a requirement for the current paper to make a contribution, but some mostly subtle changes would lay the foundation for a broader audience to understand and perhaps adopt this new approach. Also, a few errors need to be corrected.

Major concerns are listed in order of presentation in the paper, not their importance, but ** has been placed in front of the most important concerns.

P6, L148: The timing of carbon release from ecosystems to the atmosphere often involves stochastic processes in the real world, such as with punctuated events of windthrow-driven tree mortality or from wildfires. The simple model of ecosystem carbon flows and ensuing ecosystem respiration is not capable of accommodating this stochasticity. While acceptable in the current form, mention of this here is warranted, as is some discussion of this in the discussion section.

P6, L163 / Eq 10: Is the IRF for emission reversible, that is, is it invertible for carbon removals as sequestration? This property is implied by the approach in Eq 10, yet the underlying biological and physicochemical processes might not behave in exactly this way. I suspect they are, particularly for ocean uptake / release, and agree that this is the standard assumption (one I too have relied upon). However, for the land response I am more suspicious and seeing it written here made me wonder. Land biospheric uptake of CO2 is not symmetric with release of CO2 so I suspect that at least that portion of the IRF is not exactly reversible.

P10, L30: As noted by R2, uptake rate (u) and transfer fates (B) are not independent in many real-world ecosystems (forests make an easy example). Some discussion of the degree to which this alters (or undermines?) the current simplified approach is warranted, with mention here and a 2 to 3 sentences in the discussion.

** Throughout, the paper’s use of the term “uptake” seems badly misleading. NPP is not uptake, and u is carbon inputs to ecosystems in the sense of net productivity. This is wholly different from ecosystem uptake and this oversight is surprising and even embarrassing given the subject of this manuscript, which is to point out that sequestration benefits need to separate carbon inputs from carbon releases. See more in the next comment.

** P10, L261: The nature of the experiment in Fig 4 needs to be clarified. Is this a pulse experiment or a step experiment? The caption describes the experiment as “instantaneous carbon uptake at any given time, but what that means is puzzling. Perhaps I have misunderstood. It sounds like a pulse experiment but that does not seem correct. Instead, the experiment appears to involve a sustained boost in uptake rate (NPP?) that leads to a steady-state carbon balance as ecosystem stocks accumulate in response to the sustained elevation of NPP and then ultimately lead to a balance of inputs and outputs. However, NPP is not ecosystem uptake, and it is badly misleading to define it as such. In fact, I suggest modifying the symbology and the name of this term to be “p”, productivity, or “i”, inputs. Expand the figure to show a time series of “u”, your so-called ‘uptake’, a time series of “r” respiration, a time series of their net balance, and also the pools over time. Including such figures for each of the experiments will greatly improve clarity and improve the communication of the time-dynamics of the CBS metric.

** Fig 4 and 6: The captions suggests that the experiment involves a fixed total uptake of 6.64 MgC ha^-1 that lead to a steady-state carbon stock response of +240ish Mg C. That is illogical. Is the ‘uptake’ meant to be an annual input of carbon to the ecosystem? Must be. The units should be 6.64 MgC ha^-1 yr^-1.

** P10, L271: It looks to me as though the labels might be wrong for the PI100 and PD100 curves in Fig 4c. Removing CO2 from an atmosphere that has more CO2 should cause a smaller cooling effect than the same removal applied to an atmosphere that has less CO2. Haven’t I got this right?: The radiative efficiency of CO2 decreases with increasing CO2 concentration. Your results seem to suggest the revers in Fig 4, though Fig 5 looks correct.

** P15, L417: R2 correctly pointed out that it is badly misleading to suggest that CBS W m-2 could be directly compared to the terms in the surface energy balance that also have W m-2. This sentence must be removed or rephrased. A top-of-atmosphere radiative forcing is comparable to the CBS measure but not a surface energy flux perturbation. For example, a change in latent energy flux of X W m-2 does not have a comparable effect on the planetary energy budget, only on the local surface, and the associated energy is returned to the lower atmosphere as heat when that water vapor is condensed. This statement contributes to a continuing misunderstanding even among scientists that really needs to be corrected.

Minor Comments:

P3, L 69 / Eq 1: K_co2 is also time varying as it depends on atmospheric composition changing over time and as it influences the radiative efficiency of any particular GhG. This is noted on P4, L100 but it struck me as missing already here.

Figures 4 and 5: In the figure caption, write out the definitions of PI100 and PD100.

Dear Carlos,

Many thanks for the revision of the manuscript following the latest round of reports. I think that you have addressed the substance of the queries well, and that the manuscript will make a meaningful contribution to debates on carbon sequestration and climate impacts. I have only a few minor queries listed below that caught my eye when reading the new manuscript. Most are a matter of formatting, but clarification regarding potentially additional material (final one in the list below) would be important before final acceptance.

My apologies for the very protracted review process and delays in getting back to you.

All the best,
Jens

Detailed queries:
Line 146, 163, 193 and 255: Please refer to specific appendices.
Lines 260 and 367: Capitalise “Appendix” here and anywhere where you refer to a specific appendix.
Line 354: “range”, rather than “rage”.
Line 355: “ecosystems” (i.e. plural).
Line 470: By “supplemental material”, do you mean calculations presented in Appendix B here? Or is there further material associated with this submission?

Dear Carlos,

Many thanks for implementing the final edits. This has been quite a lengthy review process, with quite substantial changes to your initial submission. I'd like to thank you for accommodating the different reviewer requests, and hope that you find that the final paper and your argument for incorporating the turnover of sequestered carbon into global warming potentials has been strengthened by it.

All the best,
Jens