The manuscript by Richaud et al., “Underestimation of oceanic carbon uptake in the Arctic Ocean: Ice melt as predictor of the sea ice carbon pump” investigate how the oceanic carbon uptake is strongly modulated by sea ice. They base their work on previous studies showing that the ratio of alkalinity to dissolved inorganic carbon in sea ice is higher than in the underlying water and previous suggestions that this storage amplifies the seasonal cycle of sea water pCO2 and leads to increased carbon uptake in the ocean. They have two independent approached; a theoretical framework and a simple parameterization of carbon storage in sea ice in a 1D physical-biogeochemical ocean model. Sensitivity simulations show a linear relationship between ice melt and an amplified seasonal carbon uptake. In addition, they estimate a 30% increase in carbon uptake in the Arctic Ocean compared with no ice amplification. Applying this ice melt parameterization to future scenarios of an Earth System Model suggest that the Arctic Ocean carbon uptake is underestimated by 5 to 15%.

Overall comment:

The paper provides new and valuable results for our understanding of the biogeochemical processes in sea ice and how sea ice modulate the air to ocean carbon transfer in the Arctic Ocean and ice covered seas. The paper is well structured, well written and the results highly interesting to a broader scientific audience interested in global warming. Therefore, I will recommend the publication of this work if the authors consider the minor comments below.

Specific comments

Line 37. Suggest to provide an additional reference to Rysgaard et al. 2013 (doi:10.5194/tc-7-707-2013) where the link between ikaite crystals trapped within the sea ice matrix and the distribution of alkalinity are shown for winter ice conditions.

Line 42. After DIC ratio, I suggest to provide a reference to Rysgaard et al. 2012 (doi:10.5194/tc-6-901-2012) where ikaite dissolution is shown for melting sea ice and how this affect pCO2 and pH levels in Arctic surface waters.

Line 89. I’m not sure DIC and alkalinity are homogeneous in sea ice. They are probably more C shaped. However, it is a fair assumption considering the few existing observations in different forms of sea ice.

Line 188-190. I am surprised the biological terms had a negligible impact on carbon uptake. Could you elaborate a little more why that is? 

Line 325. The assumption of a constant mixed layer is a good beginning. However, I expect leeds and polynyas (ice fabrics) could elevate the carbon uptake. I’m aware that this will require very high-resolution modelling, but could be very interesting thing to look into after your present work. Looking forward to a follow up study later.

Line 355. Here you state that models without the ice pump parametrization may underestimate carbon uptake over seasonally ice-covered areas by 10-15%. In the abstract this number is 5 to15%. 

Line 360. I’m happy to see that your estimated supplementary carbon flux is consistent with numbers provided by Rysgaard et al 2011. Do your model also include the Southern hemisphere and would it be possible to provide a number for sea ice Antarctica? Could be a really interesting follow up study after this work.

Lime 370. Your statement regarding the importance of high vertical resolution in the model to represent the shallow mixed layer is an important one. In order for the carbon pump to work, the CO2 released from ikaite production in sea ice only has to go below a thin mixed layer to prevent (or greatly reduce) exchange with the atmosphere in the Arctic Ocean due to an impermeable sea ice cover (autumn, winter and spring). As this cold water below the mixed layer meets warmer and saltier Atlantic water on its way out of the Arctic Ocean it will sink in the Denmark Strait. At the same time melting sea ice in the summer will be in contact with the atmosphere and result in dissolution of ikaite and release of excess alkalinity to surface waters and hereby stimulate CO2 uptake from the atmosphere. Could be interesting to look into regional differences in air-ocean CO2 uptake.

Line 395. Polynyas and leads. Interesting and I would love to see more on this modelling in the future. 

Summary: I really enjoyed reading this study.

General comment

This is a study on the effect of sea ice on the carbon exchanges in ice-covered seas, based on a rather conceptual approach and an offline ESM application. I find the paper reasonably well presented, yet insufficiently developed and subject to important methodological ambiguities.

The origin of the latter could be that the paper has not taken full benefit of the literature, ignoring key processes (subduction of carbon below the mixed layer) and progresses in the definintion of the sea ice carbon pump.

There is space for a conceptual study of the seasonal cycle of air-sea carbon exchanges in ice-covered seas, however important aspects (including basic calculations and experimental design for model experiments) would need to be reworked, in my opinion, before the paper represents significant progress against state-of-the-art.

More detailed comments

The key question, as presented in the abstract « how the storage of carbon in sea ice affects air-sea CO2 flux and quantify its dependence on the ratio of TA vs DIC in ice », was central to two contributions on the topic by Grimm et al (2016) and Moreau et al (2016).

Both studies are cited in the submitted paper, however two key progresses that these made were not considered in the submission.

First, both author teams conclude that the subducted fraction of the carbon anomaly generated in the mixed layer during sea ice growth is a key player in the intensity of the sea ice carbon pump (SICP). Rysgaard et al assumed a 100%-efficiency of carbon subduction below the mixed layer (leading to maximum efficiency), whereas both Moreau et al and Grimm et al suggest the subduction efficiency could be less than 5%, which would drastically decrease the intensity of the SICP compared to the large numbers of Rysgaard et al 2011. This finding is not mentionned and not accounted for in the conceptual model presented in the submitted paper, which I find problematic as subduction efficiency is a key player and source of uncertainty.

Second, Moreau et al and Grimm et al decomposed the sea ice carbon pump into several sub-components. The decomposition of the SICP has important implications on the requirements for what the reference control case should be in model experiments, in order to draw proper conclusions on the sea ice carbon pump. Both aforementioned studies acknowledge that the SICP results from mostly three groups of processes. (i) Sea ice growth, which implies an uptake of freshwater from the ocean to the ice, (ii) brine rejection, which proportionally decreases the uptake of solutes in sea ice, and (iii) active biogeochemical processes, which modify the TA/DIC ratio in sea ice.

In this context, depending on the question of interest, the reference point for « no sea ice » could be several things, and basically two points of view are used in the literature. A first point of view (#1) is to assume no freshwater and no solute uptake/release associated with sea ice, wherease point of view #2 assumes no solute uptake, but some freshwater uptake associated with sea ice. #1 (no fw and no solute uptake) was generally adopted by Moreau et al and Grimm et al and implies that there is virtually no change in surface concentrations due to sea ice at all in their CTRL experiment. #2 assumes full rejection of solutes and would lead to the strongest effect of sea ice on surface concentrations.

Both points of view can be justified depending on what one is looking for. However, the issue with the submitted study is that, in my understanding, points of view #1 and #2 are adopted in different parts of the paper without notice, which I view as problematic because the conclusions drawn are be completely different if one or the other point of view is adopted. Section 2 (conceptual study) assumes point of view #2. In this context, comparing CTRL and ICE differentiates between the effects of full rejection of solutes minus brine rejection (which I find not so useful scientifically, but possibly useful as a technical stage meant to fully decompose things). In Section 3 (1D model), I’m not really sure which point of view is adopted. Table 1 says TA=DIC=0 (point of view #1), whereas the text says no ice-ocean carbon flux (line 235), which would correspond to point of view #2. As far as I understand it, the default approach in PISCES assumes point of view #2. Finally, regarding the ACCESS-ESM application, where the analytic perturbation is applied, there is no mention of what is assumed in that ESM for TA and DIC concentrations in sea ice, hence we don’t know the point of view adopted. Clearly, applying the perturbation would require point of view #1, for consistency with the analytical calculations. However, it could well be that model developers would have adopted point of view #2 (I know of many ESMs which adopt point of view #2). In that case, the ESM outputs and the diagnosed perturbation on carbon fluxes would be incompatible, and any finding based on their association would be wrong, I’m afraid.

This ambiguity on the relevant reference point of view cast doubt (on my side at least) on the findings presented. Properly defining the sea ice carbon pump, translating that into a fit-for-purpose experimental design in all sections of the paper, and making appropriate connexions to concluding statements on the sea ice carbon pump should be clarified before anything else, I reckon.