The authors use a neural network model to generate a pCO₂ product for the global ocean using the SOCAT data, and combine these pCO₂ estimates with a wind speed product to compute the CO₂ flux.  The ensemble model results compare well overall to the observations, and the carbon flux estimates are in-line with the literature.  My main comments concern how novel these results are compared to the extensive literature on the topic, and the interpretation of some of the model statistics.

There is a lot of previous literature using spatially and temporally sparse observations of surface pCO₂ to generate global data products and provide estimates of ocean carbon uptake, some of which use very similar methods to those in this present manuscript.  The authors cite this previous literature, but there’s very little discussion of it.  Consequently, I found it difficult to interpret how the present authors’ methods and results are novel and differed from these previous studies.  The motivation appears to be in lines 41-46, however, I don’t follow how the previous literature did not incorporate “space-time varying uncertainty estimates”?  It would also appear that the incorporation of the coasts is relatively new, though the authors then cite a few recent studies and declare that it’s a closed gap?  I suggest that the introduction needs to contain a much clearer description of how the methods used here compare to previous studies, and what is new about this analysis.

I think the methods section is missing a few key details that will help support this manuscript.  First, it would be helpful for the authors to explain how to interpret and compare the RMSD and r^2 values for each region.  The reason being, that these values are listed for each ocean region, but it’s a little unclear what differences in these values between regions is saying about the model estimate.  For example, I was surprised by how low the RMSD value for the Southern Ocean is (slightly lower than the global mean), despite the somewhat limited observational data and well documented, substantial inter-annual variability.  However, the Southern Ocean does have a lower r² value, which the authors seem to attach a greater weight to in their interpretation.  Second, I’m a little confused by equation (2).  Why is the equation for the mean squared deviation (MSD) shown when it’s the root mean squared deviation (RMSD) which is calculated throughout the manuscript?  Also, the text refers back to this equation for the definition of the σ misfit, but this definition is itself within the MSD equation and is not clearly labeled on its own.  Lastly, I think the description of the wind speed product used should be included in the main text rather than the supplementary, considering that this will have a large impact on the overall flux numbers (which the authors do highlight in the results). 

I suggest re-working the 2^nd paragraph of the abstract.  This paragraph currently reads like a laundry list of different regions and where they fall in terms of largest total source/sink, largest flux density source/sink, along with coastal and open ocean qualifiers.  This many iterations of “X is the greatest …” makes it difficult to follow-along and is not particularly interesting (e.g. the equatorial Pacific as the strongest source of carbon to the atmosphere is not a surprising result).  Instead, highlight some of the other key findings, like the increase in ocean carbon uptake over the 1985-2019 timeframe (right now the mean is just listed, but the change is highlighted in the conclusion).

Other comments

Lines 37-40:  Should all the manuscripts be separated with a comma rather than a semicolon?  And why is the Rödenbeck et al., 2015 manuscript specifically highlighted as “other mapping methods”?

Line 139:  How is the variability in “analytical equipment” accounted for here?

Figure 2: I suggest directly labeling each region in the figure with the abbreviated label (i.e. SpA for subpolar Atlantic) for clarity.

Figure 5 and 8:  The tick marks in the colorbar for these figures are relatively large and look like a negative sign, I’d suggest making them much smaller.

At present, there are many data products in marine physics, such as temperature and salinity products, but there are few data products in marine chemistry. I support the publication of more marine chemistry data products.

The author reconstructed surface ocean pCO₂ based on FFNN with region divided by latitudes and similar predictors with previous researches was used, which is not novel. The reconstruction of pCO₂ and sea-air CO₂ flux over global coastal oceans are interesting works but the author needs to do much more works on the validation of coastal results. Because a standard deviation of 41.79 µatm between pCO₂ results and SOCAT observations possibly leads to opposite results in the estimate of coastal CO₂ flux.  In general, this manuscript needs to be further improved for the following reasons:

1) The validation of pCO₂ reconstruction was completely based on SOCAT dataset itself. The author did not compare the result with any independent observations from time series stations, such as HOT, BAT and ESTOC station. Especially in the coastal ocean, the author will find their pCO₂ product surprisingly deviated from the independent observations from time series stations if a comparison was carried out. In addition, reconstruction of pCO₂ based on machine learning methods has been attempt in several previous researches, such as Landschützer 2016, Denvil-Sommer et al. 2019, and comparison with these existing results was not found in the manuscript.

2) The CHL data used was only from 1992 to 2019, and was not available in the Arctic and the Southern Ocean in winter, the details about how the reconstruction was carried out when CHL was not available should be declared clearly in the method section.

3) The subskin temperature correction (Watson et al. 2020) should be considered in the estimate of sea-air CO₂ flux.

4) The author should reconsider the topic of this manuscript. If the author want focus on the CO₂ flux of global open oceans, additional work was necessary rather than only discussing spatial distribution or interannual variability, because the reconstruction method in this manuscript and the results was not novel. If the author want focus on the CO₂ flux of global coastal oceans, which was still a research gap, much more works are needed to make the result convince.

5) Line 76: “An ensemble of 100 FFNNs was used to reconstruct monthly pCO2 fields……”, How are these 100 models built? Why did you do that? How are the results of 100 models selected?

6) Line 84-85: “The random extraction and the FFNN training were repeated 100 times so that 100 versions of the monthly FFNNs have been obtained”, Why is it the "100 times"? How is the "100 times" determined? Does it converge after 100 iterations?

7) Table 2, What is the meaning of two numbers in the rightmost column of Table 2, for example: 0.07±0.04, 0.30±0.13

8) Line 444-446: “The global open ocean uptake obtained in this study of 1.344±0.111 PgCyr−1 lies between the observation based net sink estimate by Wanninkhof et al. (2013) (1.18 PgCyr−1) and the global sum of regional best estimates given in Table 2 (1.8 PgCyr−1)”. In table 2, I can’t find the value of 1.8 PgCyr−1

9) Line 462-463: The discrepancy is possibly due to an overestimation of Arctic pCO2 by the CMEMS-LSCE-FFNN (see in Sect. 3.1.2) and to the lack of estimates over a large portion of the seasonally sea–ice covered regions. This sentence means that the data in the Arctic are not accurate at present. So the data in the Arctic is not suitable for use at present.

The authors present an estimate of global air-sea CO2 fluxes based on interpolating gridded SOCAT pCO2 data. They use an ensemble of 100 feed-forward neural network models (FFNN) and sea surface height, sea surface temperature, sea surface salinity, mixed layer depth, chlorophyll-a, atmospheric mole fractions, a pCO2 climatology and position data as drivers. They present an uncertainty analysis based on their ensemble spread as a semi-independent parameter, which is better than many available air-sea flux products. However, there are a few things that should be improved.

One point that needs improvement is the description of the driving data, where some important information is missing. The driving data that were used are not available for the full period for which the authors present flux maps. How did you deal with that? Did you use a climatology for CHL, SST, MLD etc. before the early/mid 90s? If so, what was this based on? This information is crucial for interpreting interannual variability prior to the mid-90s.

Another thing that I want to point out, is the inconsistent and partly misleading use of the terms ‘observations’, ‘sample’ and ‘data’. The authors base their product on a gridded version of the SOCAT data set (monthly, 1x1˚). In order to avoid confusion, the term ‘observations’ should be reserved for data that has been retrieved from field work, in the case the original pCO2 measurements in the SOCAT database. The gridded version contains monthly, 1x1˚ averages of these pCO2 measurements. When the authors write about ‘X observations’ in a certain region, they actually mean ‘grid boxes with observations’. Please make sure that this becomes clearer. In line 195 for example, the authors write 50 to 220 samples per year’. Here the authors should specify that they mean ‘grid boxes with data’ as the reader easily can assume that there were only 50-220 pCO2 observations every year.   

I also want to comment on Figure S1. Here the authors show the coverage of the gridded SOCAT product and its variability where they mention ‘pCO2 individuals’. I don’t understand if this means the original SOCAT pCO2 observations (i.e. a measure of how well the gid box mean represents the actual conditions), or the pCO2 of the gridded version (showing the variability within the gridded product).  

Please go through your manuscript with these comments in mind and make sure, that different terms are consistently used and that it is clearly stated what you mean.

I understand that the authors used the subocean divisions from RECCAP 1. This of course increases the comparability to the results of RECCAP 1, but also this makes the results difficult to interpret. Using a biome scheme such as used in RECCAP 2 (e.g. after Fay and McKinley (2014)) would have led to a clearer separation of regions with similar characteristics, and thus increased the interpretability. I also miss a discussion of how this product performs in comparison to other global air-sea CO2 flux products.

Minor comments:

L 40: pCO2 was not introduced as an abbreviation

L 59: Tr is not described

L 86: change to: p is the number of grid cells with observations

Figure 3: The yellow bars in panel c) are very difficult to read, especially the first one. Additionally change STD to s.  Go through the manuscript and make sure, that you use consistent terminology.

L 140: add: temporal offset from the cell center. In many regions this will be the dominant one, especially during the productive season.  

Figure 4a/b: You show the number of observation (or grid cells with observations) per year. Please change that.

L 182: Be aware that Laruelle et al. 2107 and Landschützer et al. 2020 are climatologies.

L 307: Please round the uncertainties to 2 significant digits (or less if it seems unrealistically low) and the measured value to the same number of digits, for example 2.336 +/- 0.104 to 2.34 +/- 0.10. Please do so for all uncertainties in the manuscript.

L 328/330: Please correct this. Primary production and respiration have usually only a very small influence on alkalinity (if we neglect anerobic remineralization processes for the moment): primary production increases alkalinity, while remineralization processes reduce alkalinity

L 332: Another important influence factor in coastal regions is the inflow of terrestrial POC, e.g. in the southern North Sea, leading to the release of CO2 to the atmosphere.

L 376-377: Are these really the dominant factors? After you argumentation for why the open ocean region is neutral (vertical convection brings up old, DIC rich water which balances the influx during summer) I would expect the absence of this deep mixing in coastal, shallow regions to be one of the major reasons why the coastal regions are a larger sink than the open ocean.

Figure 9:  To be honest, I can’t really see from this figure that it covaries with the ENSO mode. As I see it the flux increases equally often during La Nina as during El Nino. It would be more interesting to see a comparison of the interannual variability with other air-sea flux products.