Global climate models are of questionable utility in many regions due to poor spatial resolution and a poor reproduction of riverine inputs and other critical determinants of biogeochemical processes. Downscaling approaches are therefore critical in many regions. Zhang and Zhu present a new “downscaling” of CMIP6 model output for the region surrounding the Gulf of Mexico, and they draw conclusions about recent changes in the region’s carbon dynamics. The model used by Zhang and Zhu appears equally or more robust than prior models of the regional carbon budget. This is therefore potentially interesting and relevant work. However, in its present form the manuscript is  needlessly confusing and misleading and features some potentially major methodological issues. I therefore recommend that the authors carry out a thorough revision of the manuscript text and to clarify methodological issues. The core contribution of this study is to provide updated (and potentially more robust) estimates of carbon fluxes in this region and to estimate temporal trends in variables such as pCO2 and pH. This is a valuable contribution to the literature as these values continue to have high uncertainties, and I hope the authors can address the concerns below.

1) It is highly misleading to call this a “downscaling” of a CMIP6 model.

At present, the title, abstract and introduction misrepresent the work in the paper.

The title of the manuscript claims this study downscales the global CESM2-WACCM-FV2 model. Conventionally, this should mean that all possible driving data is derived from the global model. Critically, any climate forcings should come from the global model. However, as stated on page 7 of the manuscript, the only things taken from the CESM2-WACCM-FV2 model are the initial conditions and boundary conditions on the geographic boundary. Atmospheric forcings etc. are not taken from the CESM2-WACCM-FV2 model. I therefore view this as a hindcast, where the authors were forced to use the CESM2-WACCM-FV2 model for geographic boundary conditions as a compromise. In no real sense is it a downscaling of a CMIP6 model. 

This is a major problem for the paper as there are, at present, many inaccurate statements. For example, the abstract claims this: “The model’s biogeochemical cycle is driven by the Coupled Model Intercomparison Project 6-Community Earth System Model 2 products (CMIP6-CESM2)…” This is clearly not true, as surface temperature, air PCO2, riverine inputs and most of the variables driving the carbon dynamics do not come from the CMIP6 product.

The title, and aims of the paper should therefore be revised.

The paper really appears to be a new estimate of carbon fluxes in the region. It should therefore be rewritten accordingly. Critically, the authors should make it clearer how, as claimed, the estimates in this study are more reliable than previous methods. The evidence provided for this are not extensive.

2) Use of the CESM2-WACCM-FV2 global model should be clarified

Output of the CESM2-WACCM-FV2 model are used for both initial and boundary conditions.

The authors do not state why they used the CESM2-WACCM-FV2 model for the boundary conditions. Was this model more accurate in the region than other CMIP6 models or reanalysis products that are available? This is a critical question, as it is possible the choice has reduced the reliability of the carbon budget estimates. There are also specific issues surrounding the use of this dataset.

First, this model can have negative values for nitrate, and presumably other variables. I viewed one of the historical files (http://esgf-data.ucar.edu/thredds/fileServer/esg_dataroot/CMIP6/CMIP/NCAR/CESM2-WACCM-FV2/historical/r1i1p1f1/Omon/no3os/gn/v20191120/no3os_Omon_CESM2-WACCM-FV2_historical_r1i1p1f1_gn_200001-201412.nc) for this model and negative values for nitrate appear very frequently across the boundary. Translating these values into boundary conditions is not a trivial issue as mass conservation etc. is ambiguous. The authors need to explain this thoroughly. Negatives at the boundary also result in average conditions that are far lower than those you would get from the NOAA World Ocean Atlas. Potentially this has been corrected for in some way by the authors, but if it has not it is not clear if the treatment of the boundary conditions is sensible. Likewise, there are negative values in the first time step in 2000, which the authors presumably used in some way to generate their initial conditions.

The authors state on p. 19 that this study’s estimates of air-sea CO2 fluxes are “more reliable than previous GoM model studies”. However, without showing whether the boundary conditions are reliable it is difficult to assess this claim. This is especially true, given the authors state that Xue et al. 2016 used over-simplified boundary conditions. There is therefore real potential that the boundary conditions used here are no more reliable than those in Xue et al.

Based on a comparison of this study with others, the approach to most variables is more robust than prior work, so the boundary conditions are likely the only major concern.

3) The model spin up period is potentially too short.

Only a single year is used for model spin up. It is not clear if the model will really have settled down by that point. Many regional models require 5 years to spin up, so one year is possibly questionable, especially given model output is used for temporal trend analysis.

Starting conditions are used from the CESM2-WACCM-FV2 model, and quasi-equilibrium conditions for this model will differ (perhaps quite dramatically) from the regional model. The authors justify using a one-year spin up by saying “the global model has been well stabilized up to the year 2000 from its ‘pre-industry’ experiment”. This does not say much about the stability of the regional model used. Given the issues mentioned above about negative nitrate values in the global model, it seems questionable whether the starting conditions are close to a stable state in the regional model. Furthermore, it is plausible that riverine inputs are drastically better resolved in the regional model than the global model. This is particularly important given the conclusion of the importance of the carbon inputs from the Mississippi River.

The spin-up timing issue is also particularly relevant for the “no rivers” experiment. This experiment essentially removes rivers at the start of 2000, but assumes that the model is effectively spun-up to “river-free” conditions by the end of 2000. The authors need to show that this is credible. Otherwise, some of the results in the experiments section may not be robust.

4) Model validation needs to be improved

Overall, the model seems to do a reasonable job compared with observations. However, at present the model validation lacks rigorous statistics and is purely visual. There are 3 figures comparing model results and observations. However, there is a failure to show how close the model is to observations. I recommend the authors add correlation coefficients, RMSE and bias values for model-observation comparisons where relevant. These should give reasonable results based on the figures. This is particularly important for figure 5 comparing surface pCO2 between model and observation/ML model. The authors should also consider carrying out a similar analysis of pCO2 for the global climate model used to help assess the reliability of the boundary and initial conditions.

5) Figures should be made colour-blind friendly and made more clear

I recommend the authors ensure that all figures are colour-blind friendly. At least 7 of the figures are not. Figure 11 is very difficult to understand. Double y-axes should generally be avoided, and in this case they just serve to confuse. The axis units are also not stated.

6) Discussion and results should not be mixed up

At present, the results section includes discussion and the discussion includes results. Comparisons of the results with other studies (p. 19) should be moved to the discussion. Furthermore, the sensitivity analysis should be in the results section, not the results.

7) Temporal resolution of forcings should be clarified

The forcing data used is of varying temporal resolution, and some of it (such as oxygen) is only available as a climatology. The authors should clarify which driving data is actually changing during the 2001-2019 time period, and which are essentially unchanging. At present it is not fully clear what can and cannot be driving the temporal trends in carbon fluxes etc.

To what extent are the riverine inputs climatological? P. 7 states “Missing river alkalinity values are interpolated from climatological values, and missing river DIC values are calculated from pH and alkalinity…” An indication of how well varying riverine inputs are represented would clarify this.

The driving data sets mostly seems to be the best available, so minor clarifications are only needed.

Review of “Downscaling CMIP6 Global Solutions to Regional Ocean Carbon Model: Connecting the Mississippi, Gulf of Mexico, and Global Ocean”

This paper presents a 20-year simulation of the Gulf of Mexico with a coupled physical biogeochemical model including carbon chemistry.  The paper provides a validation of the model against observations. It also presents two perturbed experiments, “Bry” and “NoR”, “Bry” has fixed the DIC and TA boundary conditions for the year 2000 and “NoR” has no rivers.  Furthermore, the carbon budget and how different processes such as temperature, primary production and mixing attribute to the total is presented, which was very interesting to see.  The presentation is focused on the Northern Gulf of Mexico and the open ocean Gulf of Mexico, though some other regions are also discussed.  This work is interesting and worthy of publication, but a major revision of how the results are presented is necessary before publication.  Here are the major points:

• The title promises a downscaling of the Gulf of Mexico using a regional model. I was expecting an actual downscaling in a global model, including a historical simulation and forward projection. However, the presented model appears more like a hindcast forced by NCEP reanalysis with initial and boundary conditions from the climate model rather than a full downscaling.   Several questions arise related to this: 
  • Why was this climate model selected?
  • Why was a climate model selected for the boundary and initial conditions as opposed to either climatology or a global ocean reanalysis?
  • What is the biogeochemical model that was used in the climate model and is it of a similar complexity to NEMURO?
• Validation: It is very good that more than one type of observation is used, but the results are presented only graphically. I would like to see some statistical quantities such as bias and rmse. Additionally, the differences could be shown: for example in Figure 5, I would have preferred to see seasons rather than month, but then adding the plots for differences. 
  • An important motivation for doing the study was the improved quality of this downscaling compared to the earth system model, to demonstrate that, also some error estimated from the ESM should be included for comparison.
• Structure: In the results the main run is presented and then discussed against previous estimates. Then in the discussion, results from the two perturbed experiments are presented.  In my view the discussion of the main run against other studies belongs in the discussion, while the presentation of the perturbed runs belongs in the results.
• Clarity on analysis: I spent a fair amount of time trying to understand the distinction between the different “types” of CO2 in the analysis as described by equations 4, 5 and 7. There is no equation (6) it seems.  First of all, these could all be presented together and some work is needed to make this more understandable.  Additionally it would help if in table 3 also the actual pCO2 was presented.  I assume the triangular bracket is the temporal mean, but it should be stated.  Why compute the contribution from GPP and not NPP?  Furthermore the thermal contribution I would understand as “How much higher or lower the pCO2 is because the temperature is either higher or lower than the mean”.  Here however the number presented is of same order as the actual pCO2.  I would also expect that the thermal and the non-thermal part would add up to total pCO2, however adding equation 4 and 5 does not yield pCO2.  So better explanation is needed in this part. I find the labeling “mixing” of the last pCO2-term presented in eq. 7 misleading, see my comment further down.
• The results are very focused on the surface, it would have been interesting to see more of what goes on below the surface, for example it would be interesting to see the depth of the dissolution horizon for calcite and aragonite.

Specific comments:

Title

 “…Model: Connecting the GoM to the Mississippi and the Global Ocean" would be more correct as this study does not address the influenc of GoM on rivers or the global ocean. 

As mentioned above, “Downscaling CMIP6” is misleading as to the nature of the simulations presented.

Abstract

Line 8: “ …reduce uncertainties in spatial…” I do not agree that models reduce uncertainties in estimates, they do however complement observations to fill spatial and temporal gaps in the observation record (with some uncertainty).

Line 20: “confirms”: Also write what it confirms, previous models, observations, both? 

Line 23: Be more specific on how the Mississippi inflow influences the carbon cycle.

The last sentence seems obvious as those are the places with inflow to the GoM, but really, when comparing “His” and “Bry”, the results are so close to each other I would say a more accurate conclusion from that perturbation experiment is that interannually varying lateral boundary conditions are not necessary on this timescale.   

Introduction

Line 39 “works” should be “studies”

Methods

Line 120: Be more specific: which variables were originally in NEMURO, which have been added?

Line 134 and onwards: could be helpful with a table where each process added is connected to the relevant publication.

What is the temporal resolution of the boundary conditions?

Validation

Figure 4: Stretching the y-axis on the upper part of the water-column and putting a black dot in the middle of the observation circle could help to better visualize the difference between the model and observations.

Results 

Figure 7: Why are pCO2th and pCO2nt, which have a very similar range, displayed with different colormaps?  That makes them hard to compare.

Line 338: Suggest “combination” instead of “synthesis”

Line 405: Is this the timestep of the NEMURO, it would be more appropriate to mention this in “Methods”.

Line 414: Please, spell out approximately how large the error is in Gomez (2020) compared to what is the typical discrepancy of this study.

Line 415-422.  The region considered by the observational studies are not mentioned, is it gulf-wide?  It is correct that this study gives a larger estimate on the shelf, but according to table 2, the open ocean and Gulf-wide estimate is larger in Xue 2016.  So is it correct to conclude that this model is “more reliable” everywhere?

Discussion

Line 440: What is the meaning of “heterogenous” here:

Line 441” It can also be considered as the pCO2 level determined by the water with a multiyear mean temperature and without the influence from gross primary production or air-sea CO2  flux.” But other processes than mixing, for example horizontal advection, will contribute to this pCO2, therefore I find labeling this term “mixing” misleading.

The authors discuss “sources of uncertainty to the model”, but they do not present actual model uncertainty, so I would change the heading 5.1 accordingly.

Conclusion

Line 565: As mentioned below the abstract, I disagree with the conclusion that the boundary conditions had a very strong effect on the results, maybe on longer time-scales, as the trends changed slightly, but not for a 20-year simulation.