the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Jun 2025
High-resolution global map (100 m) of soil organic carbon reveals critical ecosystems for carbon storage
Abstract. Uncertainty in soil organic carbon (SOC) stocks and fluxes resulting from land disturbance and recovery processes remains a significant challenge for closing the global carbon budget, accurately quantifying the land carbon sink, and assessing restoration carbon credits in nature-based climate solutions. To address this, we develop a spatially resolved SOC estimate at a 1-hectare resolution globally, aligning with the scale of land-use disturbances, to significantly improve carbon accounting accuracy and reduce uncertainty across multiple use cases. We compile and harmonize a global SOC inventory, incorporating 84,880 (30 cm depth) and 44,304 (100 cm depth) measurements. Additionally, we identify high-resolution remote sensing and in situ spatial covariates to map SOC using advanced, biome-specific machine learning algorithms.
We measure global SOC stocks of 1,049 Pg C at 30 cm and 2,822 Pg C at 100 cm. Our results reveal a 31 % increase in SOC at 30 cm and a 45 % increase at 100 cm compared to the average of prior estimates. Our model indicates that peatlands including peat-in-soil mosaics store 146 Pg C at 30 cm depth and 344 Pg C at 100 cm depth, accounting for 14 % and 12 % of global SOC stocks respectively. Mangrove ecosystems have some of the highest soil carbon densities among global biomes, and hold 1.3 Pg C at 30 cm depth and 4.4 Pg C at 100 cm depth, despite covering a relatively small global area. We find that biome-level SOC estimates strongly depend on biome area and its changes over time. Our analysis indicates that annual wildfire dynamics and shifts in agricultural land can influence SOC by 132 Pg C and 140 Pg C at 30 cm, and by 345 Pg C and 368 Pg C at 100 cm, representing approximately 13 % of the global stocks. The SOC maps from this study, including pixel-level 95 % confidence intervals to quantify model uncertainty, are hosted on a Zenodo repository. These data will be made publicly available upon publication to support large-scale carbon accounting and integration by the scientific and policy communities. The repository is accessible through the reviewer link (Creze et al., 2025): https://zenodo.org/records/15391412?preview=1&token=eyJhbGciOiJIUzUxMiJ9.eyJpZCI6ImNjZjk2YTM5LTQyM2ItNDZiMC1iY2RlLTg0ZTA1ZjU1MDZjNSIsImRhdGEiOnt9LCJyYW5kb20iOiIxMjc1YmI0OTZhOTNiMmQyNTIxYjYyNzRiM2ZlZjBmMyJ9.M5VUSwR4GkeoKV1Kno1v3b3qLUAzErns1Zh6u0om2HhVDrnxcjKJS3WCOVAoJlSyxt-5Kbc809apXwYmAnMqyQ.
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RC1: 'Comment on essd-2025-294', Anonymous Referee #1, 20 Jul 2025
This study leveraged a rich collection of global soil organic carbon (SOC) data to create an updated, high-resolution map of the spatial distribution of SOC storage at the top 30 cm and 100 cm. The motivation for developing a spatially resolved, high-resolution soil C map for better land management, C accounting, and global C monitoring is strong. The resulting map can be valuable to the urgent need of accurate monitoring and estimation of soil carbon removal impacts through climate solutions around agricultural and natural ecosystems. Overall, this work is a good contribution to the soil community, but I have a few concerns about the delivery of results and the writing. Therefore, I recommend this manuscript to be published on ESSD if a major revision can fully address the main concerns.
First, the good things:
I appreciate that the authors harmonized and cleaned up a massive collection of layered soil data rigorously. For example, they used only samples with bulk density measurements, adjusted measurement values according to sampling protocols, and filtered out redundant points. The authors dealt with SOC stock calculations and layered data at different depths responsibly.
The authors also fitted separate models for peatland and mangroves, which seems reasonable. This approach implies an assumption that relationships between SOC storage and predictor layers are different for these two ecosystems compared to the rest of global ecosystems.
Major concern 1:My first major concern is that the entire article showed lots of summarized total SOC storage at biome, regional, and global level, but none of these estimates come with an uncertainty range or confidence interval in the main text or the supplemental material. Although pixel level uncertainties were shown as main figures, the authors should still report uncertainties on the estimated global and regional SOC stocks in the abstract and throughout the result sections. This should be easy given the authors already fitted 20 models from bootstrapped training data. The CIs (and bootstrap distributions) can be derived once the regional and global estimates were calculated from each of the 20 models. The lack of regional uncertainties makes some of the conclusions unconvincing. For example, in section “3.2.1 Global fires”, the authors concluded that adding fire as a predictor layer increased global top 30cm SOC but decreased top 1m SOC. However, the difference for SOC at 1m is only 1% of the total estimated SOC (28 out of 2822, line 552-553). I don’t know whether the CIs of the estimated 2850 PgC and 2822 PgC overlap with each other. If so, this evidence can’t convince me that “fire can be a significant source of carbon emission”. Another concern about this paragraph (line 551-555) is that, although adding fire as a predictor seems ecologically reasonable, I’d still expect to see the authors show that the model performance increased after adding fire as a predictor, in order to make that final conclusion. Without proving fire as a statistically justifiable predictor, this result might point to some artefacts rather than an improvement in the model due to fire data. Another way to look into fire’s effect is to predict the global SOC stock from the fitted model (with the fire layer), in a scenario where no fire happens on Earth, and then compare the no-fire prediction to global SOC stock estimate with real fire frequencies (Perhaps this is what you did. Am I misunderstanding?).
Major concern 2:
It seems like land cover is not an explicit predictor in the model. It gives me two questions.
(1) It is hard for me to understand that without this predictor, how does the model discern different SOC contents between a forest and a nearby cropland that shares essentially the same environmental condition? Perhaps you expect the Landsat bands to give such information implicitly?(2) The peatland and mangrove models were fitted by points within their remote sensing extents. Is it possible to find ground-truth information on whether a soil sampling belongs to peatland or mangroves? Because small-scale farming can make patchy drained lands within such systems (as you mentioned), it is likely that some points within the peatland/mangrove extent weren’t in fact peatland or mangrove, raising potential bias to the biome-specific models. It would be great if the authors could validate the peatland/mangrove extent with their ground truth land cover—if you have some site-level information from the data source, what proportion of peatland/mangrove sites were and weren’t included in the peatland and mangrove masks? And how many sites that weren’t peatland/mangrove end up within the masks?
Major concern 3:
The soil data were sampled at different times spanning 1950s to 2020s, but the goal of this work is to represent a static map of global SOC stock distribution. It is common and maybe justifiable to use all historical data for mapping a static global SOC stock distribution, but I wish the authors could extend more discussion on how they expect readers to use this data product. The authors motivated this work with the recent need for soil carbon removal and land management, but how will this map of static SOC stock estimation help with these motivations, building upon the previous global SOC maps? I was excited to read an insightful reasoning of how this work is needed in the context of climate solution, policy making, and land management (which was pitched as the motivation), but I find it lacking in both the introduction and discussion. I hope the authors can elaborate more explicitly and clearly on the real impact and value of this data product, acknowledging that land use management and carbon removal programs would deal with SOC change over a short period of time (5-10 years). Some relevant literature on the perspective of natural climate solutions and carbon removal include https://www.nature.com/articles/s41558-024-02182-0 and https://www.nature.com/articles/s41467-023-44425-2.
Major concern 4:
There are no plots showing the effect of each covariate on SOC storage in the fitted model. I understand if the work doesn’t want to emphasize the fitted relationships in the model (which can be messy to interpret), but I think it should be reported in the supplemental material for transparency. A group of partial dependence plots for each biome-specific model would suffice, so that the readers don’t wonder if model predictions are driven by one or two strong but non-physical effects.
Minor comments:
Line 22-24, Abstract. “Our analysis indicates that annual wildfire dynamics and shifts in agricultural land can influence SOC by 132 Pg C and 140 Pg C at 30 cm, and by 345 Pg C and 368 Pg C at 100 cm, representing approximately 13% of the global stocks.”
These numbers seem to be calculated from the total estimated SOC stock in global areas that fall within the agricultural and fire-prone extent (line 619). Indeed, the theoretical maximum potential of SOC loss driven by any disturbances is always bounded by the total SOC stored in a given area, so the sentence is technically correct. However, this sentence reads like “we formally analyzed the effect of recent/near-future fire and agricultural dynamics on SOC change, which show that these activity poses a readily threat to this much SOC stock in the next several decades”. This does not accurately summarize the relevant results (line 619). In the fire-prone pixels defined by “average annual number of burned days >1” (line 296-297), such fire dynamics very likely do not pose an immediate threat to the entire soil C pool in every fire-prone pixel (the author also pointed out multiple times that fire has mixed effects to SOC change yet to be understood). The same point applies to agricultural activities. To avoid misrepresenting the main result of this work, please adjust the phrasing of this sentence. Maybe something like “estimate shows that XXX PgC of soil carbon sits in fire-prone area and/or area with ongoing agricultural activities…”
Line 505. “Our study suggests considerably greater carbon storage in the Amazon Basin.”
Is it because your study better predicts the large carbon storage inthe Amazon peatland (your next paragraph)? If so, explain explicitly here.
Line 551-555.
See major concern 1.
Line 685 “Our data indicates that 35% of the Cerrado is used for agriculture (72/204 Mha)”
And Line 689 “Our map highlights high fire activity in the Matopiba region”
If I understand correctly, the agricultural land extent is cited from another product, and the fire activity extent is indicated by the MODIS fire frequency map. How is that “your map” and your data? (I would’ve assumed these terms to refer to your SOC data product in this manuscript.) It kind of confuses and distracts readers from focusing on what’s truly your valuable map and your data product —the SOC stock maps at two depths.
Line 699-703
The authors have already discussed the mixed and unknown impact of fire on soil in the global fire section and the grassland section (lines 556-565, lines 424-426). Coming after these sections, these lines read redundant. Perhaps all of these can be consolidated better into the global fire section (the paragraph of lines 556-565)
Citation: https://doi.org/10.5194/essd-2025-294-RC1 -
RC2: 'Comment on essd-2025-294', Anonymous Referee #2, 04 Aug 2025
The authors utilized 84880 and 44304 field measurements at 30cm depth and 100cm depth and combined with biome-specific machine learning approaches to map SOC at 100m spatial resolution. This novel idea would provide significant spatially explicit information in reducing uncertainties related to SOC estimation. However, there are a few issues that need to be addressed before the paper being accepted. The detailed comments are as follows:
Line 13, 1-hectare refers to the area, instead of the spatial resolution of the map, please make this consistent with the “100m” spatial resolution that mentioned in the title.
Line 18, What is the “average of prior estimates”, which research?
Line 110, Please add a map to provide the spatial distribution of all the field measurements. Also, please add a table describing the basic information of sampled points in each biome, such as the total number of samples, mean and standard deviation values of soil samples in each biome.
Line 153, This approach may introduce mistakes in treating gridded products as ground truth, leading to biased models, especially in data-scarce regions where underlying map quality is uncertain. Additionally, subsampling and binning may not fully capture spatial or ecological variability, and global performance metrics can obscure significant local errors. I suggest the authors provide (1) analysis that does not include samples that are sampled from these maps (2) model metrics and R2 that are not including these samples. As samples collected from maps are not ground truth, which will change the model’s performance.
Line 177, The differences in SOC lab methods (e.g., dry combustion vs. Walkley-Black) are not accounted for. Could this introduce systematic regional bias in SOC predictions?
Line 197, Please replace “Environment” with “environment”.
Line 213, Please justify why ET was included for SOC estimation.
Line 219, Is fire frequency also derived from MODIS based products?
Line 222, Please specify which years’ ALOS2 data have been utilized.
Line 225, Please replace NiR with “NIR” and justify why these bands in Landsat8 were selected?
Line 229, The spatial resolution of all the remote sensing data or remote sensing-based products are not the same, how the mismatch in spatial resolution was handled? Please provide more details. Also, how did the temporal mismatch between different Earth Observation sources and the temporal mismatch between SOC data and EO were handled? SOC maps often combine soil profile data collected over decades with environmental covariates reflecting more recent conditions. This ignores soil property changes over time, particularly in areas affected by land-use change or degradation.
Line 250, The abstract mentioned a bio-specific machine learning approach for mapping SOC, more details needed to describe the bio-specific approach.
Line 251, How the parameter of “mtry” has been trained and specified in the random forest model?
Line 325, Does the average represent all the aforementioned SOC products? Please consider adding the average SOC of each SOC map.
Line 267, Please provide other model evaluations metrics for mapping SOC such as RMSE instead of only R2.
Line 356, Please position the captions below the figure, same comment for all the figures.
Line 202, The authors mentioned that they used SoilGrids2 data as the inputs of the models. However, SoilGrids2 itself is a modeled product with known spatial biases and uncertainties. Could the authors clarify what steps were taken to mitigate the risk of error propagation from SoilGrids2 into the final SOC predictions?
Citation: https://doi.org/10.5194/essd-2025-294-RC2 -
RC3: 'Comment on essd-2025-294', Anonymous Referee #3, 05 Aug 2025
General comments:
This manuscript mapped global 100-m resolution SOC through compiling 84,880 topsoil, 44,304 subsoil SOC samples and covariates to multi-sources remote sensing and other data products as extra layers for training biome-specific random forest models. This high spatial resolution product is an important resource for future studies on soil carbon management, thus the major outcome from this work is useful and timely needed for soil biogeochemistry and carbon cycle modeling communities. The comprehensive data inputs authors used, random forest based geospatial predictive mapping are popular and robust methods, thus the quality of the produced SOC map is partially justified. However, the writing of the discussion section in this manuscript, justification of bias correction and missing attribution of different uncertainty sources, have not been addressed properly. In addition, I checked the data product and found lots of missing points in the uploaded geotiff file. Overall, this is a solid and interesting work, but I would only recommend it for publication at ESSD after major revisions to address my following concerns.
Specific comments:
1. Histogram-based bias correction can be tricky. Authors claim the better match is achieved after bias-correction, but the correlation of SOC stock to environmental covariates and categorical datasets for training are forced to be changed. Since Soilgrid's product did not show biased results after training, I wonder if any of these covariates and categorical maps added to layers in your training model are the reason? Could you explain the reason causing this bias and justify that the overall uncertainty of the data product is not largely affected by your bias-correction?
2. The highlight of this work is the ultra fine 100-m resolution product, which is unique product. But in your manuscript, I cannot find any discussion on how you get a meaningful high resolution data product. By just using soil profiles to evaluate your model, I entrust your model to mapping the non-linear correlation of SOC stock to other covariates. But without high resolution input, your 100m resolution is less persuasive, such as Soilgrids 250m product using some 250m input covariates like MODIS products. In your study, I did not see any very high resolution products for model training. I would suggest explaining what high resolution products you're used to increase the credibility of your high resolution product.
3. Authors described SOC stock results over specific regions/categories, but also wrote lengthy discussion with lots of statements only weakly related to the SOC stock product itself. I feel like reading a review paper and lots of results are just descriptions of categorical or environmental covariates input. I recommend authors to simplify your writings in the results section and focus on discussing SOC stock. I have one example in additional points, but expect authors to double check the whole manuscript.
4. This concern is related to my point #3. I found the discussion on uncertainty is missing in the results section. I appreciate authors separately discussing their results under different categories like fire-prone region, agriculture land and peatland, but a word or two to summarize the uncertainty from your data products over these regions can be valuable evaluation and probably can help you find the source of bias when training your model with raw data?
5. It is not reasonable to use bbox for calculating averaged or total SOC stock for specific geopolitical regions. Please use maps for masking geopolitical regions. Also, since some of the categorical maps are overlapping each other, for example, agriculture and fire-prone areas, I have an extra suggestion that you can prepare a global map to depict different categories you discussed with different colors, so readers will have a better idea.
6. The data product contains lots of missing points for no reason. Shall double check your uploaded geotiff files or explain the reason why you have these missing values.
Additional points:
Line 158: Explain how you bin the samples, by SOC stock?
Line 173: Shall explain: D is the soil layer depth (cm), and equals to 30cm for topsoil and 70cm for subsoil in this study?
Line 331: R square is a metric to show how large a fraction of the variance of a dependent variable explained by the independent variable. Since it is a fraction, the relative magnitude of SOC from dependent and independent variables cancels out each other, and does not affect the R square. Please revise or remove your conclusion.
Line 355: What are these underrepresented regions?
Line 386: Delete one "and"
Line 423: Which data you used for global fire?
Line 442: "Our value at 100 cm is similar to the carbon density of 361 t C/ha found by Sanderman et al. (2018)." But authors mention that total SOC stock to be 45% less from Sanderman's study compared to this work, with similar mangrove extent from both studies. Need to clarify.
Line 464: I'm more interested in the peatland SOC stock between northern peat and tropical peat, not SOC stock from Northern-Hemisphere, since you discuss these two separated regions later.
Line 470: How did you combine these datasets? By calculating the maximal extent that any dataset shows peatland coverage? Also, what threshold did you use (e.g., 1% of the grid cell)?
Line 481: Did you calculate the peatland extent or you used a dataset? I got the feeling that you obtained the peatland extent through a dataset but you claimed this as "finding", which means the peatland extent is the output of your trained model? Please correct.
Line 512: "Mapping peatlands across the Amazon Basin has largely depended on modelling approaches". I'm still curious about how you model the peatland extent. Is it just constrained by several datasets?
Figure 5. It may be better to have another subplot to the right showing relative uncertainty (% of uncertainty to the SOC stock)
Figure 6. What is the mask map you used for fire-prone land?
Line 537: "This represents 13% and 12% of the global SOC total". This is interesting to show a large difference from Pellegrini's work on Nature Geosciences. My understanding is still that your fire-prone area mask is much smaller compared to the previous one. Please explain.
Line 562: I have a feeling that lots of discussion in this manuscript is not closely related to the data product itself. For example, "In tropical forests, fires can generate feedback loops as they alter forest understory fuels, making forests more vulnerable to further fire degradation (Dwomoh & Wimberly, 2017; Wimberly, 2024). The impact of fire on long-term carbon stocks remains under investigation." stated the importance of understanding how aboveground carbon stock and residence time respond to wildfire, which is not closely relevant to your fine resolution SOC stock dataset. I would suggest either shortening or removing unnecessary discussions. Also see my major concern #3.
Line 615: "We find that 17% of fire-prone land (351/2,109 Mha) is located in agricultural zones.". Here I found evidence that you have overlaid analysis from different categories. This may cause potential confusions so I would suggest clearly defining the boundary of each category in a map. See my major concern #5.
Line 631: "bbox: -25.136719, -34.597042, 55.722656, 38.822591 degrees" Does this mean your calculated statistics for Africa based on this bbox extent? Or you accounted for the whole geographical Africa? Since Africa is a geopolitical region with a defined extent, you shall use a certain regional map as a mask.
Line 667: "Our findings further confirm that agricultural activities place substantial pressure on the region's natural peatlands." I doubt a one time snapshot of SOC product itself can show how agricultural activities place substantial pressure on peatland. Here is another example that discussions are not closely related to your data product and not enough reasoning in your statement. Either simplify/remove or present your complete logical reasoning on how you “confirmed” your conclusions.
Line 689: "Our map highlights high fire activity in the Matopiba region, likely linked to land clearings." Another example of weak relevance to your SOC stock data product. I doubt you can find evidence of land clearings from your SOC stock data product. Please revise.
Line 703: "Our data, accounting for spatial variation, suggests that fire impacts on soil carbon in the Cerrado may be mostly noticeable in deeper soils." Authors should also add “fire and agriculture impacts” here.
Fig S3. Missing colorbar.
Citation: https://doi.org/10.5194/essd-2025-294-RC3 -
RC4: 'Comment on essd-2025-294', Anonymous Referee #4, 05 Aug 2025
General Evaluation
This manuscript presents a 100-meter resolution global soil organic carbon (SOC) map at 30 cm and 100 cm depths, built using a harmonized collection of over 120,000 point measurements and remote sensing covariates. The authors use random forest (RF) models, with special treatment of peatlands and mangroves through ecosystem-specific models, and provide uncertainty maps based on bootstrap ensembles.
The development of a globally consistent, fine-resolution SOC map is highly relevant and potentially valuable for applications in carbon accounting, land restoration planning, and natural climate solutions. However, while the dataset is promising in scope and spatial granularity, the manuscript currently lacks structural completeness, spatial transparency, and modeling rigor necessary for scientific reproducibility and policy relevance.
I recommend major revision before the manuscript is considered for publication. Below are my detailed comments.
Major Comments
1. Biome- and Region-specific SOC Estimates, Uncertainty, and Validation Are Missing
While the authors emphasize the use of biome-specific models and regionally tuned data inputs (e.g., for mangroves, peatlands), they do not provide SOC estimates, confidence intervals (CI), or model performance metrics at these spatial units. Readers cannot evaluate whether modeling SOC separately by biome or region has indeed improved performance.
Additionally, there is no validation of these outputs against either prior SOC products (e.g., GSOCmap, SoilGrids, WISE30sec) or independent in-situ observations within these biomes or regions.
Recommendation:· Present SOC maps, uncertainty maps, and model metrics stratified by biome and/or key geographic regions (e.g., Amazon, SE Asia, Congo Basin).
· Compare SOC estimates for each biome with existing datasets and, if available, ground truth values.
· Consider including these outputs in main figures or supplementary materials.
2. Model Accuracy is Low and Methodological Alternatives Are Not Explored
The global model shows modest predictive accuracy (R² = 0.35–0.38) and suffers further degradation post bias-correction. Yet, only a single modeling method—random forest—is used, with no evaluation of alternative algorithms or ensemble strategies.
This is concerning given the complexity of SOC drivers and the goal of high-accuracy mapping at fine resolution.
Recommendation:· Compare multiple modeling approaches (e.g., XGBoost, LightGBM, Cubist) and report their relative performance.
· Explore ensemble or stacked models to increase generalization and reduce bias.
· Report R², RMSE, and MAE for each biome or region and for each model tested.
3. Data Sparsity in Key Regions Remains Unresolved
Although the manuscript compiles an impressive collection of point data, it is unclear whether it significantly improves training sample density in previously under-sampled areas (e.g., SE Asia, Amazon peatlands, Congo Basin, boreal permafrost zones).
Recommendation:· Provide maps or histograms of sample density by region or biome.
· Quantify the number and proportion of new samples added to underrepresented areas.
· Compare data coverage with existing global SOC datasets to clarify how this product advances spatial completeness.
4. No Connection Between Static SOC Map and Dynamic Carbon Policy Use
The authors claim their product supports natural climate solutions and carbon removal strategies. However, the map reflects a static snapshot of SOC conditions and does not account for management interventions or disturbance effects.
Recommendation:· Clearly position this dataset as a static SOC baseline and discuss its potential role in MRV (Monitoring, Reporting, Verification) systems.
· Provide examples or scenarios where SOC stocks are compared under different management or fire regimes using model predictions.
· Alternatively, simulate SOC distributions under no-fire or no-agriculture scenarios using the trained models to demonstrate potential use in change detection or policy design.
5. No Analysis of Predictor Effects Across Biomes or Regions
The manuscript includes no interpretation of model behavior through partial dependence plots (PDPs), SHAP values, or marginal effect visualizations. This is a major weakness given the low model R² and the ecological complexity of SOC formation.
Understanding how each covariate influences SOC predictions is critical to evaluate whether the model captures realistic biogeochemical relationships or is driven by spurious correlations.
Recommendation:· Provide variable importance rankings and partial dependence plots for key predictors (e.g., pH, CEC, clay, NDVI, temperature).
· Stratify these analyses by biome or region to highlight differences in covariate effects.
· Comment on whether the model’s response patterns are ecologically interpretable and consistent with known SOC mechanisms.
Minor Comments
1. Abstract (Lines 22–24): Rephrase “can influence SOC by 132 Pg C…” to avoid misinterpretation as quantified changes. Suggest: An estimated 132 Pg C of SOC is located in areas affected by wildfire and 140 Pg C in agricultural areas.
2. Line 505: If the increased Amazon SOC estimate is driven by better mapping of peatlands, please state that explicitly.
3. Line 551–555: The difference between SOC estimates with and without fire (28 Pg C at 100 cm) is small (~1%). Confidence intervals should be reported to assess significance. Also clarify whether adding fire improved model performance.
4. Figures 1–5: Add consistent color bars, units (e.g., t C/ha), and labels for clarity.
5. Line 685 & 689: The phrase “our map shows high fire/agriculture activity” may confuse readers. Clarify that these are input datasets, not part of the new SOC product.
6. Line 699–703: Discussion of fire impacts here is redundant with earlier sections. Consider consolidating to avoid repetition.
Citation: https://doi.org/10.5194/essd-2025-294-RC4 -
RC5: 'Comment on essd-2025-294', Anonymous Referee #5, 10 Aug 2025
The production of global maps of SOC stocks is valuable research and the dataset is of high interest for the global community. This manuscript is therefore timely. The current methodology and datasets used to build the maps, however, have several very fundamental issues that need to be resolved before any publication is made. For several of these issues, well-accepted solutions exist in the literature, and it is not clear if the authors are proposing something new (in which case, it should first be tested), or if they simply decided not to account for past developments. The manuscript suggests an important lack of familiarity with the current state of the art in soil science and digital soil mapping. All of the above is common knowledge and not prone to any specific discussion in the field.
I focused on the very major comments because I see that the other reviewers mentioned several minor issues.
The key issues are (explained in more details below):
- Predictions should be made for depth intervals, not exact depths.
- Depth harmonization (e.g. mass-preserving splines) is required to address differing sample supports.
- Input datasets (e.g. RaCA, Australia) require quality checks and better sources.
- Clarification needed on coarse fragment data and SOC measurement methods.
- Modeled data should not be mixed with measured data.
- Pseudo-observations should be added for areas with no SOC (e.g. deserts).
- The choice of 100 m resolution should be justified.
- Cross-validation, not single data splits, should be used.
- Bias correction is unusual and needs justification.
- Uncertainty assessment should use prediction intervals (e.g. quantile regression forest).
- Check for residual autocorrelation and consider kriging residuals if needed.
- Depth intervals. In soil science, predictions are made for depth intervals, not specific depths as the authors did here for 30 and 100 cm. The concept of calculating a stock at exactly 30 cm or 100 cm depth does not make scientific sense. A stock is based on volume, i.e., a depth interval. The authors justify this in Section 2.1 by stating “… continuous soil depth functions (Malone et al., 2009), which have shown significant variability in results.” Using depth functions is the standard in soil science because soil samples are collected at different depth intervals (e.g., 0–10 cm or 5–15 cm) and need to be harmonized before use. This is a necessary pre-processing step. It becomes very clear in the next sentence of the same section why it is needed: “At a depth of 30 cm, we included 84,880 ground truth data points.” What does this mean exactly? Did you merge together samples collected for any interval between 0 and 30 cm? What did you do for samples that were collected, for example, on the interval 0–40 cm? This shows that using depth harmonization is a prerequisite as much as calculating the stock for a depth interval. The justification given in Section 2.1.4 for depth harmonization does not make sense. I invite the authors to read the papers on depth harmonization in the soil science literature, where the approach given here seems outdated and not correct.
- Further on this matter of the depth interval, the authors are currently mixing samples with different supports. It is not the same to estimate the SOC stocks for a sample obtained on a 0–5 cm interval compared to a sample with a 0–30 cm depth support. These are very different, yet the authors are putting everything together and considering it the same measurement. This again supports the need for using a mass-preserving spline as a basic pre-processing step for SOC stock data.
- Problems with input point datasets. There are several known problems with the datasets the authors used. Most of the US data are based on the Rapid Carbon Assessment (RaCA) dataset. This dataset is known to have several issues. First, most values in this dataset are not measured, but predicted with infrared spectroscopy, which introduces an additional source of error. Second, there is a high likelihood of issues with bulk density measurements. The authors should contact the dataset maintainers to get more information. This dataset should at least be checked carefully and harmonized to retain the highest-quality bulk density measurements. As an example, the best mapping paper so far on soil properties in the US did not incorporate the RaCA dataset as input (https://acsess.onlinelibrary.wiley.com/doi/10.1002/saj2.20769). Another concern is the lack of real data for Australia. The authors randomly sampled an old map to generate data (note that this 2014 map has been updated in 2022 with entirely new predictions). This is problematic. There is a wealth of publicly available datasets in Australia that the authors could use, available through the SoilDataFederator. Alternatively, the authors could contact the authors of the recent paper on mapping SOC stocks in Australia to obtain their pre-processed data.
- Two major attention points are raised with the SOC stock calculation:
o Coarse fragments are notoriously difficult to obtain and predict. How did the authors obtain these data? It is not mentioned anywhere except for a brief statement that “it is not available everywhere.” This needs to be made very clear because it will substantially affect the SOC stock calculation.
o The authors ignored the difference between SOC obtained by dry combustion and the Walkley–Black method. They cite one paper to justify this, but the difference between methods can be significant. It is standard to apply a correction or otherwise account for this difference. - Mixing measured and modeled data. The use of map sampling to generate observations for model fitting is a serious problem. The authors have combined observations from measured SOC stocks (derived using various calculation methods) with values obtained from SOC stock maps. This is problematic, as the map values are already modeled predictions, not direct measurements. They are smoothed and often carry significant uncertainties. The authors should avoid this practice.
- Ignoring zero-SOC areas. The authors ignored areas that contain no SOC in soils, such as deserts. It is common procedure to add pseudo-observations in such areas to prevent the model from predicting SOC stocks where there should be none (because of smoothing effects) and to reduce uncertainty in total SOC stock estimates.
- The specific resolution chosen (100 m) is not justified. We know that it is simply a matter of computing power and that predictions could be made at 10 m if desired. However, many researchers refrain from using such fine resolutions for global products because these products tend to perform poorly locally and can mislead soil management decisions. The resolution choice should be justified.
- Model validation. The authors used model validation based on data splitting. Repeated cross-validation should be used instead. Data splitting can lead to accidentally high or low validation statistics depending on the split, and it might also be susceptible to fraud if one were to select a split that yields better results. It should be replaced.
- Bias correction. Applying a post-processing bias correction is, to my knowledge, never seen in digital soil mapping. This is because most models we use (geostatistics, random forest) have little to no bias. Are there even biases in the predictions? This is not common for random forest, and the explanation given by the authors on this aspect does not seem relevant to the work (particularly for users applying the map for soil carbon accounting).
- Uncertainty assessment. The uncertainty assessment needs to be completely redone. In digital soil mapping, one is interested in a prediction interval, not a confidence interval. This is common knowledge and can be found in standard DSM textbooks and papers. A confidence interval is of limited interest, as it does not inform us about the uncertainty of new observations. The authors should therefore obtain a prediction interval. Second, the idea of bootstrapping a random forest model is not meaningful. Random forest already uses bootstrapping internally, so the authors are effectively bootstrapping twice. A much simpler approach, and one that is widely implemented, is to use quantile regression forest, which directly reports a prediction interval. This is probably the most common procedure in DSM to generate uncertainty intervals with machine learning. Third, the approach based on Z-scores relies on the assumption of normally distributed errors, which is generally not valid for machine learning.
- Residual autocorrelation. Once the above issues are addressed, the authors should check for residual autocorrelation and report the fitted variograms. It may be that kriging of the residuals is needed if autocorrelation remains.
The many major comments above suggest that the maps may present a misleading representation of the spatial patterns and average or total stocks. These points need to be addressed very seriously, and the authors should ensure familiarity with the state of the art in digital soil mapping, as most of these are standard procedures in the field.
Citation: https://doi.org/10.5194/essd-2025-294-RC5
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