General:

This paper builds off previous literatures by using a different machine learning method (neural networks) to generate a global prediction of seafloor total organic carbon. The paper primarily differs from other papers in the machine learning approach that is utilized. This paper will also release a new higher density observational dataset and discusses carbon stocks over regional areas in more detail than other literatures. Since a major highlight of this paper is the comparison of NN to other ML methods, the paper needs some significant work on technical details in this manner. This work does not achieve any higher resolution or spatial coverage than other more recent works, it also utilizes very old datasets which should be noted in the manuscript. Inevitably, the best predictions are a result of the best features and observational datasets not always the ML algorithm used. Special care in discussing this in the manuscript is vitally important.

Overall, this paper is worthy of publication. In my opinion, the paper is worthy not so much for the ML and technical approach used (as previously mentioned the method is always problem-specific) but mostly due to the discussion of carbon stocks and trends that may be revealed in final predictions. I think most of these trends are likely apparent in any of the three discussed ML algorithms. Potentially making these points the highlight of the paper would strength the paper and lead to a heavily cited paper.

Technical (specific) notes: See attached pdf for comments.

Grammar:  See attached pdf for comments.

Other: Saving this data in a more universal format (.xyz, netCDF, etc) would be advantageous for others to use. .npy files are not always suitable for everyone. Further, something to understand specifically what these files are would be useful. Some of the short hand is difficult to interpret (e.g., prediction_map_TOC_supervised_men_CS_noconstraint.npy, prediction_map_TOC_noconstraint_supervised_men_DO.npy). I assume CS for continental shelf and DO for deep ocean but being explicit would be best.

In this manuscript, the authors provide a new method to predict the OC content in marine sediments using sparse data, in order to then calculate total OC stocks, providing a step forward to properly quantifying the OC budget in marine sediments. However, there are several studies over the last decade that have modelled the OC content in marine sediments, so the authors have to highlight better the novelty of their work and how it improves previous models and their estimates. They do so by comparing their model performance to random forest and k-nearest neighbors, the two machine learning models used in recent studies, but the comparison is insufficient. I highlighted a few sections where I think this can be improved. In addition, the authors discuss their outcomes very superficially, and do not provide greater insight of the complex mechanisms that affect OC content in marine sediments. This study has a lot of potential and the authors should emphasize their outcomes to enhance the impact of their work within the scientific community. I hope my comments below will help improve this manuscript.

General comments

1. The authors cleverly divide the global ocean into two regions (shelf and deep-sea) to ensure that the model performs well in these unique environments and avoid the model to simply predict lower TOC concentrations in the deep-sea and higher TOC concentrations on the shelf, and instead ensure that the model captures nuances in each of these settings (which can be highly heterogenous as the authors explain in lines 40-49). The authors use as a cut-off of 200 m. Is this the optimal cut-off? Did they test different water depths? How would the model have performed if the shelf and deep-sea would have not been separated? Is it an improvement to train and validate 2 models? You would need more data to train 2 models than to train one model.
   
   Have the authors considered doing a third model for the Arctic Ocean? Arctic sediments are affected by OC permafrost and is hence a unique setting. In fact, (Wang et al., 2024) performed 2 models (Arctic and non-Arctic) to predict the radiocarbon signature of surficial sediment on continental margins.
2. A model is just as good as the data that is inputted in it, which is why I went over the 139 features used to train the models, which are listed in Annex C, and the TOC data used in this model.
   
   In Annex C, the authors provide a table describing each of the features and its sources. In addition to these columns, it would be useful if the authors added an additional column where they argue the importance of including this feature in their models. For instance, bathymetry could affect the OC concentration given the longer transit time through the water column before its deposition on the seafloor. I suggest to do this because there are a lot of features that I don’t understand why they are included (e.g., Coriolis).
   
   I also have several questions about some of these features which I include below:
   
   How can the coastline be a feature? A feature should cover the whole region where the model is to be applied to, hence, the whole ocean. Likewise, how can the characteristics of river mouths (carbon dioxide, DOC, bicarbonate, POC, TSS flux at river mouths) be used as a feature in this model?
   
   What is the difference between GL_COAST_FROM_LAND_IS_1.0_ETOPO2v2.5m.nc and GL_COAST_FROM_LAND_IS_1.0_ETOPO2v2.r50km.men.5m.nc?
   
   Correct grammar for: “Distance OF ocean grid points to the nearest coast”
   
   Instead of “elevation data”, the authors should be using “bathymetric data”, or am I not understanding well this feature?
   
   The explanation of Hart-Davis et al.’s (2021) features has a typo (remove “are provided”)
   
   Specify the time range of clorophyll-a concentrations during summer and winter.
   
   When you say “Gradient of elevation”, do you mean “slope”? If that’s the case, please modify.
   
   Why would you need to have as a feature “Land mask data”. The features should be preprocessed so that they are exclusively of the area of interest. The model shouldn’t learn that if the land is masked, it shouldn’t provide an output.
   
   Specify what decade is used for the mean sea density, sea bulk modulus (what is that?), average conductivity of seawater, averaged dissolved sea oxygen, sea oxygen percentage saturation, pressure, salinity, oxygen utilization, temperature (etc.), instead of simply saying “over a decade”.
   
   How does the coastline data “SF_COASTLINE_IS_1.05m.nc” differ from the previous coastline data provided? Again, how can this be a feature if it doesn’t cover the whole area of interest (the ocean)?
   
   The authors use bottom current data of December 2012, but their TOC dataset encompasses several years. Hence, this feature is not representative of the environmental processes occurring then. The authors should be using average data that encompasses their whole dataset.
   
   Sea surface density is extracted from sea surface salinity from the Aquarius project. Why not simply use sea surface salinity instead of sea surface density? Also, please specify the time period averaged to get this feature.
   
   What is the Free-air and Bouguer gravity anomaly?
   
   Please specify the time period used to extract the maximum and minimum depth of the mixed layer, mean PAR, mean wave direction/height/period, wind speed.
   
   
   
   Finally, regarding the TOC data:
   
   Why not use the updated MOSAIC database? (Paradis et al., 2023)
   
   What section depths are included in this dataset? Based on the text, I suppose that TOC concentrations from the upper 10 cm were used, although this is not stated in the Materials section. If so, the same location may have several TOC measurements from the same sediment core, but different section depths (e.g., 0-1 cm, 1-2 cm, 2-3 cm, etc.). TOC concentrations tend to show an asymptotic decrease with depth in a core, being highest at the surface. Hence, TOC measured in different section depths in the same core need to be somehow integrated. How was this done? I imagine the authors did not integrate it using the variance analysis explained in lines 108-112.
   
   What if a location only had TOC concentrations in the upper 1 cm and not deeper (down to 10 cm), this location would have substantially higher TOC concentration than another core that had measured TOC concentrations down to 10 cm depth.
   
   The database includes a total of >110’000 datapoints, including duplicates. How were the duplicates accounted for? If they were accounted through the variance analysis explained in lines 108-112, then the duplicate datapoints would be creating a bias in this variance analysis! Note that these duplicate datapoints (the same sample is reported in more than one dataset) are not duplicate measurements (the same location analyzed in different cruises, or the same sample analyzed in different laboratories).
3. In this study, the authors compare the performance of their DNN model along with the most often used models in geosciences, k-nearest neighbors and random forest, to prove that their approach is better. However, more detail should be given to how these machine learning models were built. For instance, how were their hyperparameters tuned? What cross-validation approach was used to train the model? This could be explained in Annex A to keep the text simpler.
   
   Regarding all three models:
   
   How was the train and test dataset generated? Was it random, or did it account for the spatial distribution of the data (ensure that the test dataset comes from all geographical regions), or the feature space (ensure that the test dataset covers a broad range of feature space), or the distribution of the label (ensure that train and test dataset had the same distribution of TOC values as the whole dataset so that the model is trained with all possible TOC values).
   
   Were the three models only evaluated once (Table 1)? To properly assess the performance of all three models, it would be better to perform several evaluations with different test datasets, in case the DNN approach happened to perform better using the test dataset presented in this paper.
4. Regarding DNN’s model performance:
   
   According to Figure 2, the model underestimates TOC concentrations at high label values. What could be the cause of this? How could the model be improved? Since this is an EGU Geoscientific Model Development manuscript, this should be discussed in more detail.
   
   It would also be more informative to plot the spatial distribution of the residuals, to assess whether the residuals present any spatial correlation, as done in the Supplementary Figures S4-S8 of (Paradis et al., 2024).
5. The authors identify that, despite the heterogenous settings in continental margins, the mean TOC concentrations in continental margins (0.69 %) is similar to the mean TOC concentrations in deep-sea sediments (0.66 %). They provide several reasons that could lead to lower TOC concentrations on continental margins such as the effect of sediment reworking, dilution by lithogenics, strong bottom currents, and the effects of bottom trawling. They then state that “According to our DNN-model, these factors decrease TOC concentrations in shelf sediments” (line213). How does the model show that these are the factors responsible to decreasing TOC concentrations? If bottom trawling is a significant factor, then the authors should include it in their model as a feature, and see if this feature is relevant in controlling the distribution of TOC concentrations.
6. One of the novelties of this manuscript is the determination of “information gain”, the identification of key regions where more TOC measurements would improve the model’s performance and reduce the uncertainties in these areas, which could be used to guide future research campaigns and fill these gaps. However, this is barely discussed in the text, and in a very confusing way:
   
   Line 215: The choice of words is a bit confusing. It sounds as if the high TOC concentrations in the Norwegian Trench should make this area have a high uncertainty and a high information gain. Please revise.
   
   Line 217: The authors mention that there is a scarcity of data from the Gulf of Mexico (in addition to other areas), but in the Materials section, they mention that they had large regional datasets from the northern Gulf of Mexico (line 105). Please correct this contradiction.
   
   Lines 219-220: The choice of words here is also confusing. In this paragraph, we have the impression that data clusters present lower information gain whereas areas with scarce datapoints have higher information gain. However, this sentence then states that “our analysis also reveals that an abundance of measurements does not necessarily correspond to lower information gain, and vice versa”. Please revise this section so that the reader is not confused by the contradicting sentences.
   
   Lines 220-222: The authors explain here that the information gain is a balance of the amount of datapoints and their proximity to parameter space and congruency of the measurements made there. This is very relevant and the authors should emphasize this better. What parameter space is seldomly sampled? Which regions show a low information gain despite the scarcity of datapoints? Why is this the case? What features make these regions have a low information gain? Similarly, which regions show a high information gain due to variability in the measurements? What would be the reason behind this variability in the measurements? Is it seasonality? This would be very insightful and give more relevance to this manuscript.
7. According to the model output, deep-sea basins have large TOC stocks, as was observed in previous modelling approaches (Atwood et al., 2020), and the authors mention that “this underscores the importance of deep-sea environments in the global carbon cycle”. However, the large TOC stock is essentially due to the vastness of deep-sea basins, and doesn’t necessarily mean that they are more important than continental shelved in the global carbon cycle. Moreover, when accounting for OC burial in marine sediments, the large TOC stock of deep-sea sediments would be reduced due to the low sedimentation rate in these regions in comparison to continental shelves. Hence, the TOC stocks in continental shelves and deep-sea basins are actually not really comparable (at least not to conclude that deep-sea basins are more important in the global carbon cycle). To make this clearer, I suggest the authors discuss the influence of sedimentation rate and the influence of the sediment age at the depth employed (10 cm). See for instance the recent study by (Bradley et al., 2022).
8. The authors conclude that “In conclusion, our study contributes to a better understanding of global TOC distributions and stocks, shedding light on the complex interplay between biological, physical, and geological processes in marine sedimentary environments. The insights gained from our modeling approach can inform future research and management efforts aimed at preserving and managing marine carbon sinks.” (lines 243-246). However, the manuscript doesn’t discuss the complex interplay between biological, physical and geological processes in marine sedimentary environments, which would be very insightful for the scientific community. In addition, while the manuscript does an excellent job at identifying future research efforts (albeit it could be improved with the suggestions provided in comment # 6), the authors don’t identify regions where management efforts should be made to preserve and manage marine carbon sinks (i.e., vulnerable areas where high TOC contents could be affected by anthropogenic activities if unprotected). The authors should either modify this concluding sentence or modify the manuscript to discuss the OC mechanisms and vulnerable areas that require preservation.
9. The authors present additional information in their supplementary information that is not discussed in the text that would be very relevant for this study. For instance, in Appendix E, the authors discuss the model’s interpretability and the influence of different features. Although the authors state that “All effects describe the behavior of the model and are not necessarily causal in the real world” (lines 306-307), this analysis could be used to better understand the spatial distribution of TOC (see earlier comment). For instance, why is sediment porosity the most important feature in the DNN model? What are the implications of this? The authors should include a section in the manuscript addressing the model’s interpretation.
   
   In Appendix F, the authors visualize the TOC stocks using different visualization techniques, but don’t reference it in the text. In my opinion, this does not add additional scientific insight to the manuscript, and since it is not even discussed in the manuscript, I would remove it.
10. Finally, I suggest the authors to remove “NN-TOC v1” from their title, as this naming convention is not used throughout the manuscript.

Specific comments

Lines 37-39: This sentence is very important in terms of the objectives of the study. However, it cites a paper that already quantifies OC stocks, so what’s the novelty of this study?

Lines 40-49: The authors very nicely explain the heterogeneity of continental shelves and deep-sea sediments and how the OC content varies in these different settings. To the best of my knowledge, this study discusses, for the first time, the spatial distribution of relict sands, but this is not a feature that is included in the model. In addition, what about the OC content in other unique geomorphological features, such as fjords and canyons, that should also be taken into account considering their global extension? Finally, the authors finish this paragraph with an estimation of the global mean TOC concentration, which is not only not insightful for this paragraph, but also it is not clear how this was calculated and if the authors have considered the spatial extension of the different regions they have described (deltas, upwelling margins, relict sands, etc.). Instead, I suggest the authors highlight that marine sediments are highly heterogeneous, which complicates a proper quantification of TOC concentrations in marine sediments and its spatial distribution, which is the purpose of this study. This is especially important and novel since they highlight that they will “improve the accuracy of highly heterogenous and undersampled geological settings” (line 78).

Please be a little bit more descriptive with the Figure captions. Figure 4’s caption is: “TOC stock map”. You could specify in the figure caption the section depths included in the calculation (for Figure 3 as well), how the TOC stocks were calculated (using porosity map provided by Martin et al., 2015 and sediment density of 2.6 g/cm3), and also note that the colormap is in logarithmic scale. With respect to Figure 5, does Information gain have a unit? I imagine that more sampling should be done in areas that have an information gain of 1 rather than 0. Please include all this relevant information in the figure caption.

Appendix A: A description of Figure A1 is given, but not of Figure A2. Please be consistent and describe the output of both figures.

How does the spatial resolution of this output compare with previous work by Lee et al. (2019) and Atwood et al. (2020)?

Technical corrections

Line 23: Against what background? What are the authors referring to here?

Line 31: Sala et al. (2021) focus their work on the effect of bottom trawling on OC, and not on marine sediment resuspension and erosion. I would suggest citing (Oberle et al., 2016).

Line 32. Remove additional “of” in: “It is composed of of both”

Line 72: Refer to “TOC stocks” instead of “TOC inventory” for Atwood et al. (2020) example, to be consistent with the use of this terminology

Line 74: Avoid using “this background”. Makes the user have to interpret what you mean.

Lines 100-101: Instead of saying that the feature list are in the Supplementary Information, state where we can find it (Appendix C). The same should be done for Line 149 regarding the mathematical formulation of the entropy (Appendix B). Similarly, state that further description of the results of the different models is given in Appendix A in lines 164-165. Finally, restructure the Supplement in order of appearance in the text. Right now, Appendix C is referenced before Appendix B, Appendix B is referenced before Appendix A, and Appendix E and F are not even referenced.

Line 190: I imagine you are referring to TOC stocks, and not TOC concentrations.

Line 229: Remove this sentence from the conclusions.

Line 274-275: This sentence is not grammatically correct. I wouldn’t know what change to suggest since I’m not sure I understand it.

Line 277: DKL is always “positive and” remains well-defined […]

Line 294: Provide Zenodo link

Table 2: Note the typo in the units of TOC stock ($Pg$).

References in this review:

Atwood, T. B., Witt, A., Mayorga, J., Hammill, E. and Sala, E.: Global Patterns in Marine Sediment Carbon Stocks, Front. Mar. Sci., 7, doi:10.3389/fmars.2020.00165, 2020.

Bradley, J. A., Hülse, D., LaRowe, D. E. and Arndt, S.: Transfer efficiency of organic carbon in marine sediments, Nat. Commun., 13(1), 7297, doi:10.1038/s41467-022-35112-9, 2022.

Oberle, F. K. J., Storlazzi, C. D. and Hanebuth, T. J. J.: What a drag: Quantifying the global impact of chronic bottom trawling on continental shelf sediment, J. Mar. Syst., 159, 109–119, doi:10.1016/j.jmarsys.2015.12.007, 2016.

Paradis, S., Nakajima, K., Van der Voort, T. S., Gies, H., Wildberger, A., Blattmann, T. M., Bröder, L. and Eglinton, T. I.: The Modern Ocean Sediment Archive and Inventory of Carbon (MOSAIC): version 2.0, Earth Syst. Sci. Data, 15(9), 4105–4125, doi:10.5194/essd-15-4105-2023, 2023.

Paradis, S., Diesing, M., Gies, H., Haghipour, N., Narman, L., Magill, C., Wagner, T., Galy, V. V., Hou, P., Zhao, M., Kim, J.-H., Shin, K.-H., Lin, B., Liu, Z., Wiesner, M. G., Stattegger, K., Chen, J., Zhang, J. and Eglinton, T. I.: Unraveling Environmental Forces Shaping Surface Sediment Geochemical “ Isodrapes ” in the East Asian Marginal Seas, Global Biogeochem. Cycles, 38(4), doi:10.1029/2023GB007839, 2024.

Wang, C., Qiu, Y., Hao, Z., Wang, J., Zhang, C., Middelburg, J. J., Wang, Y. and Zou, X.: Global patterns of organic carbon transfer and accumulation across the land–ocean continuum constrained by radiocarbon data, Nat. Geosci., doi:10.1038/s41561-024-01476-4, 2024.