the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 19 Jun 2026
Lateral Transport Controls Particulate Organic Carbon Stocks and Fluxes in the Baltic Sea
Abstract. The sediments of the Baltic Sea represent a substantial regional carbon sink. Yet, detailed mapping of organic carbon (OC) content and stock in the Baltic Sea is lacking, and our understanding of the transport pathways of particulate OC (POC) in the water column is limited. Here, we generate high-resolution (500×500 m) maps of surface OC content from available data using a deep neural network. The results are combined with porosity and Holocene sediment thickness maps to derive OC stocks per maritime zone of each Baltic Sea country. The total surface (top 10 cm) OC stock is estimated to 1.29 ± 0.36 GtC and the spatially averaged surface stock to 3.14 ± 0.86 kgC m-2. A process-based, 3D numerical model is then used to simulate fluxes of resuspended POC. The results imply that horizontal transport of resuspended POC, rather than in-situ biological production, is the key factor determining the flux and distribution of sediment OC. Net horizontal transport of resuspended POC across maritime boundaries reaches the order of 1 MtC yr-1, with substantial interannual variability. These fluxes are in the same magnitude as the recent net OC accumulation rate, underscoring the importance of laterally derived, allochthonous carbon in sedimentary Blue Carbon habitats. Regional numerical modelling may be useful in addressing the issues of double counting and additionality in Blue Carbon accounting and management.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-3315', Anonymous Referee #1, 25 Jul 2026
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RC2: 'Comment on egusphere-2026-3315', Anonymous Referee #2, 27 Jul 2026
The manuscript by Porz et al presents high resolution maps of the sedimentary organic carbon content and stock in the Baltic sea, derived from available observation data using DNN and MC dropout. These maps are used to initialize a numerical ocean and sediment transport model to simulate lateral fluxes of resuspended POC across the Baltic sea and its maritime boundaries. The authors conclude that the lateral transport of resuspended POC is a key factor shaping the spatial distribution of sedimentary OC and that cross boundary POC fluxes are of the same magnitude as long-term burial rates, with implications for Blue Carbon accounting.
The manuscript is well written and addresses a relevant topic at the intersection of marine geosciences and carbon budgeting. However, I have concerns regarding the ML methodology, the evaluation strategy for the OC prediction model and the interpretation of the model uncertainty. I also find the connection between ML mapping and the numerical model insufficiently exploited and I believe the manuscript would benefit from a major revision, particularly with respect to ML methodolgy and its evaluation. My major and general comments are provided below:
Major comments1. The ML model is effectively a spatial interpolator, and its marginal improvement over Kriging is not adequately discussed
The DNN uses 4 input features: latitude, longitude, water depth, and distance from coast. Two of these (latitude, longitude) are spatial coordinates, meaning the model is primarily learning a nonlinear mapping from geographic location to OC content. This makes the DNN functionally similar to a spatial interpolation method, which is precisely what Kriging is designed for. The marginal improvement in prediction accuracy (RMSE: 1.75 vs. 1.81 wt%; R2: 0.664 vs. 0.656) is probably consistent with this interpretation. The DNN offers little additional predictive power beyond what spatial autocorrelation already provides.
The authors should discuss more explicitly why the DNN achieves only a marginal improvement which, in principle, is a more flexible model. I suspect it is because the feature set does not contain information beyond what spatial proximity already encodes. If the primary advantage of the ML approach is the finer-scale spatial pattern (as argued in lines 174–176), the authors need to demonstrate that this finer-scale structure is physically meaningful and not an artifact of local overfitting to nearby training points. Independent validation at the fine scale, or at least a comparison of the ML-derived patterns against known geological or bathymetric features, would help.
Furthermore, the statistical significance of the improvement over Kriging should be assessed. With a single train/test split, the observed difference in RMSE could easily fall within the range of sampling variability. I recommend either k-fold spatial cross-validation or repeated random splits to provide confidence intervals on the performance metrics.
Finally, the paper would benefit from comparisons with simpler ML baselines (e.g., Random Forest, Gradient Boosted Trees, or even linear regression with polynomial features), if it is not out of the scope of the paper. In many cases it has been proved that the tree based models perform well for some datasets, especially tabular datasets(spatial converted to tabular) like yours. Without such baselines, it is unclear whether the DNN architecture itself contributes meaningfully to the prediction, or whether any nonlinear regression method with the same four features would perform comparably.
2. The evaluation strategy conflates model selection and model testing, and the Farthest Point Sampling scheme may not be appropriate for evaluating ML models
I have several concerns about how the model is evaluated:
(a) A cross validation technique could be useful in this case where we have less number of data to choose the best hyperparameters. Why was it not done? Is there a specific reason?
(b) The Farthest Point Sampling (FPS) procedure selects test points to maximize geographic distance between them. However, the ML model uses a four-dimensional predictor space (latitude, longitude, depth, distance from coast), where "distance" has a different meaning than in geographic space. Two points far apart geographically may be similar in predictor space (e.g., two deep basins), and vice versa. The authors should justify why spatial distance is an appropriate proxy for predictor-space distance, or alternatively perform the split in normalized feature space.
(c) The additional FPS constraint, that the nearest neighbor of each test point remains in the training set, guarantees that every test point has a nearby training example. While this is practical, it systematically biases the evaluation toward favorable conditions. Both ML and Kriging will perform artificially well when the nearest data point is guaranteed to be in the training set. This may partly explain why both methods achieve similar R2 values and why neither shows strong degradation in sparse regions. The authors should report performance separately for test points in densely and sparsely sampled regions to assess whether this bias affects their conclusions.
3. The Monte-Carlo Dropout uncertainty estimate is not calibrated and conflates different sources of uncertainty
The standard deviation map from the Monte-Carlo Dropout procedure (Figure 3b) shows a spatial pattern that closely resembles the OC content map itself: high absolute uncertainty where OC content is high. This raises important questions:
(a) Is this pattern driven by heteroscedasticity (the model's absolute prediction variance scaling with the target magnitude), by epistemic uncertainty (insufficient training data in high-OC regimes), or by both? The paper does not attempt to disentangle these contributions. Presenting a map of relative uncertainty (coefficient of variation = standard deviation / mean) would be informative: if relative uncertainty is spatially uniform, the pattern is primarily heteroscedastic; if it varies, genuine knowledge gaps exist.
(b) The MC Dropout uncertainty is not calibrated against observed prediction errors. For the uncertainty estimate to be meaningful, the predicted confidence intervals should contain the observed values at approximately the expected rate (e.g., ~68% of observations should fall within one standard deviation). Without such calibration, the uncertainty map provides a sense of relative model disagreement across space but cannot be interpreted as a reliable quantification of prediction error.
(c) The methods section states a dropout rate of 20% (line 81), but the hyperparameter search yields an optimal dropout rate of 10% (line 85). The dropout rate used for the final Monte-Carlo uncertainty estimation is ambiguous. Since the magnitude of dropout directly affects the spread of MC predictions (higher dropout = larger spread = larger standard deviations), this inconsistency has practical consequences for the reported uncertainties and the propagated stock estimates.
(d) The MC Dropout uncertainty captures only one component of the total prediction uncertainty. Structural uncertainties, such as the choice of features, network architecture, or training data composition, are not included. Given that the ML and Kriging maps differ by more than 5 wt% in some areas (Figure 3d), the structural uncertainty may substantially exceed the MC Dropout uncertainty in those regions.
4. The connection between the ML-based OC mapping and the numerical transport modelling is underexploited
The paper presents the OC mapping and the lateral transport simulation as largely independent analyses, connected only by the initialization of the sediment model with the ML-derived OC map. However, a more integrated analysis could substantially strengthen the paper's central conclusion that lateral transport controls OC distribution:
(a) The OC map from the ML model is used to initialize the transport model, but no sensitivity analysis is presented to show how the results would differ if the Kriging map were used instead. Given the pronounced differences between the two maps (Figure 3d, >5 wt% in some areas), the simulated lateral fluxes could differ substantially. If the flux results are robust to the choice of initialization map, this would strengthen confidence in the transport conclusions. if not, it would highlight a key source of uncertainty.
(b) The simulated near-bottom transport fields could be used as additional features in the ML model to directly test whether lateral transport explains observed OC patterns. If including simulated transport improves prediction accuracy and shows high feature importance (e.g., via SHAP values, could be included if it is not too much out of the scope), this would provide model-based evidence for the paper's main claim, rather than relying on the indirect argument that flux magnitudes are "of the same order" as burial rates.
5. The sediment transport model lacks validation for the quantities of interest
The hydrodynamic model is validated against MARNET monitoring data for salinity and current velocity (Appendix B), which is appropriate for the hydrodynamic component. However, the sediment transport module, which produces the central results on lateral POC fluxes , has no validation against observed suspended sediment or POC concentrations. The authors acknowledge this (lines 416–424) but proceed to draw quantitative conclusions about POC fluxes at the MtC/yr scale. This is a significant limitation that should be discussed more prominently, not only in the limitations section but also when presenting the flux results.
The POC sediment class is parameterized identically to inorganic silt (Table A1: same settling velocity, critical shear stress, and erosion rate), which is a substantial simplification. OC-rich aggregates typically have lower density than mineral silt, affecting both settling and erodibility. No sensitivity analysis is presented for these parameters. Given that the simulated fluxes span orders of magnitude (Figure 6), even moderate changes in critical shear stress or settling velocity could substantially alter the flux magnitudes and patterns.
General comments
L17–18: The term "maritime boundaries" in the abstract is ambiguous. It should be clarified that these refer to boundaries between countries' maritime zones (EEZs, territorial seas, etc.), and the relevance for national carbon budgets should be stated explicitly.
L60–63: The three OC datasets are combined without specifying how overlapping measurements are handled. Were duplicate locations averaged, preferentially selected from one dataset, or retained as separate points? This could affect both the spatial density weighting and the model training.
L65: The four features are described as "input features (predictor variables)," but latitude and longitude are spatial coordinates rather than predictive features in the traditional ML sense.
L67–68: The spatial density weighting is described as "weighted inversely with the number of points within a defined radius," but the radius is not specified here (it appears later as the hyperparameter "spatial weighting radius: 0.25 degrees"). This should be described more completely, including how extreme weights for isolated points in sparse regions are handled.
L81 vs. L85: The dropout rate is stated as 20% in the methods description but 10% in the optimal hyperparameters. Please clarify which value is used for the final MC Dropout runs.
L89–92: The heuristic constraint in FPS (nearest neighbor of each test point remains in training) should be discussed in terms of its potential bias on the evaluation metrics, as noted in Major Comment 2c.
L110–114: The stock calculation chain (OC content x dry bulk density x thickness) involves multiple intermediate maps, each with their own uncertainties. The propagation of uncertainty through this chain should be described more formally, and the assumption of Gaussian error propagation should be justified.
L133: The simulation period 2010–2015 is relatively short. Given the high interannual variability shown in Figure 7, the authors should discuss whether 6 years is sufficient to derive representative mean fluxes and whether the choice of period (which includes the exceptionally strong 2014/2015 MBI) biases the results.
L149–150: The claim that the OC sediment class represents "recalcitrant OC" is not supported by the data description. The OC measurements used for mapping (Section 2.1) appear to be total OC from surface sediments, with no indication that labile and refractory fractions were distinguished. This should be clarified.
L169–170: The statement that "the ML method achieves slightly more accurate predictions" should be tempered. A reduction in RMSE from 1.81 to 1.75 wt% (3.3% improvement) based on a single train/test split may not be statistically significant. The authors should either provide confidence intervals or refrain from drawing conclusions about relative performance.
L174–176: The claim that the ML method provides "much more detailed and finer-scale distribution pattern" is presented as an advantage, but it could equally reflect overfitting to local training data. Without independent validation at the fine scale, the physical reality of these patterns cannot be assessed.
L210: "top meter" ? should this be "top 10 cm"?
L271–275: The comparison with Parameswaran et al. (2025) is based solely on the basin-mean OC content (3.06% vs. 3.03%). Agreement in the mean does not imply agreement in spatial patterns. To support the claim that four features suffice, the authors should compare spatial patterns at the regional level, particularly in data-sparse regions where the 139-feature model might capture process information that geographic proxies cannot.
L277–281: The authors argue that additional features may introduce biases from hydrodynamic model outputs. While this is a valid concern, it applies equally to the numerical transport model used later in the paper, which also relies on prescribed bottom roughness and other poorly constrained parameters. This argument is therefore somewhat self-contradictory.
L376–378: The attribution of the stock difference with Parameswaran et al. to porosity assumptions is plausible but not tested. A direct sensitivity analysis — recomputing the stock with the Martin et al. (2015) global porosity map — would strengthen this claim.
L389–395: The discussion of pre-Littorina vs. post-Littorina OC content is important but would benefit from acknowledging that anthropogenic perturbations over the last ~100 years (eutrophication, soil erosion, land-use change) may have also induced significant shifts in OC burial that are distinct from the Littorina transgression signal.
L400–406: The distinction between "stable" and "fresh" POC is central to the transport modelling but is not operationally defined. How was the recalcitrant fraction identified or quantified from the available OC measurements? If the surface OC data represent total OC, the initialization of the transport model with total OC as "recalcitrant POC" requires justification.
Section 3.3 / Figures 6–8: It would be valuable to assess sensitivity of the simulated fluxes to the choice of OC initialization map (ML vs. Kriging). If the flux patterns are robust, this strengthens the transport conclusions; if not, it highlights a key uncertainty.
Overall, it is a very nice paper and has a lot of potential. This could be very useful for carbon budgeting in the Baltic which has a lot of uncertainties, although there is a lot of data points compared to other marine regions in the world.
Citation: https://doi.org/10.5194/egusphere-2026-3315-RC2
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The manuscript by Porz et al. investigates the potential role of lateral transport in shaping the spatial distribution of sedimentary organic carbon (OC) stocks across the Baltic Sea. To this end, the authors use a comprehensive dataset of observed surface-sediment OC concentrations. However, the observations are unevenly distributed across the Baltic Sea, with particularly poor coverage in some regions, such as the Gulf of Bothnia. They apply a machine-learning (ML) model based on spatial variables (latitude, longitude, water depth, and distance from shore) to produce a map of surface-sediment OC concentrations, which they compare with a corresponding map generated by kriging interpolation. The resulting maps are then combined with independent maps of sediment thickness and bulk density to estimate OC stocks in the upper 10 cm and throughout the entire Holocene sediment column. Moreover, the authors combine the map of OC density in the surface layer with an ocean-current and sediment-transport model to estimate potential lateral OC fluxes near the seafloor and assess their importance relative to sediment OC stocks and estimated burial rates.
Although the manuscript is very well written, I have substantial concerns regarding the methodology, particularly the production of the prediction maps, the estimation of OC stocks throughout the Holocene sediment column, and the approach used to demonstrate the importance of near-bottom lateral OC fluxes in shaping the spatial distribution of sedimentary OC stocks. Nevertheless, I believe that this study could make a valuable contribution to the journal following major revision. To support such a revision, I provide three major comments below, followed by several more general comments.
Major comments:
1. Predicted maps of OC concentrations
The authors use kriging and a deep neural network based on four predictors, all of which are related to location: latitude, longitude, water depth, and distance from shore. Although the ML approach also relies primarily on spatial information, the two methods produce markedly different spatial patterns. The authors should explore in greater detail why these differences arise. For example, does the ML model assign greater importance to water depth and distance from shore, potentially explaining the sharper spatial gradients? To what extent can the relative influence of the different predictors be assessed? I understand that deep neural networks are not inherently interpretable, but it should nevertheless be possible to investigate feature importance using appropriate methods.
Given the pronounced differences between the two approaches, I suggest adding predictions from tree-based ML models. Such models would also allow the authors to examine feature importance and use partial-dependence plots to interpret the relationships between individual predictors and predicted OC concentrations. Predictions based on alternative ML methods would help assess the robustness of the results and better characterize the uncertainty associated with the spatial predictions.
I also do not understand why the ML model uses only these four spatial variables as predictors. This limited predictor set likely weakens the model’s capacity to extrapolate to areas of the Baltic Sea with sparse observations, such as the Gulf of Bothnia. It would be preferable to include predictors that are more directly and causally related to OC production, inputs, transport, and deposition. For instance, remotely sensed chlorophyll-a concentrations could provide a useful indicator of autochthonous OC production that may ultimately contribute to sedimentary OC. The manuscript itself refers to previous Baltic Sea studies using this type of information.
Furthermore, the manuscript argues that lateral OC transport is an important control on sediment accumulation. To test this hypothesis more directly, the simulated near-bottom sediment transport could be included as a predictor in an interpretable ML model. The authors could then assess its importance, for example through SHAP analysis, and its effect on predicted OC concentrations using partial-dependence plots. The sediment-thickness map used to estimate total OC stocks might also be a useful predictor
Other potentially relevant predictors include riverine inputs of water, sediment, and terrestrial particulate OC, perhaps derived from existing spatially explicit estimates such as Liu et al. https://www.nature.com/articles/s41561-024-01524-z. More advanced bathymetric variables that may be relevant to sediment transport and accumulation, including seabed slope and compound topographic index, could also be derived from the Baltic Sea bathymetry data.
2. Calculation of total Holocene sedimentary OC stocks
The study estimates total Holocene sedimentary OC stocks by multiplying the predicted OC concentration in the surface layer by the total sediment thickness reported by Miluch et al. and by sediment bulk density. It is unclear whether the bulk-density data are representative of the entire sediment column or only of the surface layer.
More importantly, this calculation assumes that OC concentrations are constant throughout the sediment column, which is highly debatable. One could hypothesize that anthropogenic soil erosion and eutrophication have increased OC inputs and burial in recent periods, resulting in higher OC concentrations near the sediment surface than in older deposits. Conversely, post-depositional decomposition would generally be expected to reduce OC concentrations with sediment depth. The calculation therefore also appears to assume that OC decomposition within the sediment column is negligible.
The authors argue that their estimates mainly represent refractory sedimentary OC, for which decomposition may be limited. However, based on the Methods section and the description of the OC concentration data, it is unclear whether - and, if so, by which methods - the refractory OC fraction was distinguished from more reactive OC. I therefore have substantial concerns about the validity and uncertainty of the estimates of total Holocene sedimentary OC stocks and burial rates presented in the study. At a minimum, the authors should justify these assumptions, assess their sensitivity, and clearly characterize the resulting estimates as approximate if depth-resolved observations are unavailable.
3. Calculation of near-bottom POC transport
The study combines the predicted map of surface-sediment OC density with an ocean-current and sediment-transport model to estimate the potential magnitude of near-bottom OC transport. It is problematic that these flux estimates cannot be evaluated against observations, although I recognize that this reflects a lack of suitable observational data rather than a shortcoming that the authors can readily resolve.
Nevertheless, I wonder whether the observed surface-sediment OC concentrations could be used to test the relevance of the simulated lateral transport more directly. I strongly recommend including variables derived from the simulated near-bottom sediment transport as predictors of surface-sediment OC concentrations. If the authors could demonstrate that these transport variables explain a substantial proportion of the spatial variation in observed OC concentrations, this would provide much stronger support for their conclusion that lateral transport drives the spatial pattern of OC burial across the Baltic Sea.
For this purpose, it may be preferable to use a more interpretable ML method, such as a random forest or another tree-based model. Such models would facilitate analyses of feature importance and partial dependence and may be more appropriate than a deep neural network for a moderately sized dataset.
General comments:
L17-18: From the abstract itself it is not fully clear what you mean with “maritime boundaries”. You should make clearer that this refers to boundaries between countries, maybe by linking to the relevance of these fluxes for national carbon budgets.
L67-70: Here I miss some details about the data. That is all sediment OC concentration in the top 10 cm? Or does the depth of that top layer varies between the datasets?
Section 2.2: In how far have these models been validated against observations?
L131: Where do you have “deep ocean” in your study area?
L133: Are those six years representative for the period over which the top 10 cm of sediments were deposited?
L149: Not clear how you estimated the recalcitrant fraction of the OC in the surface sediments from the data and extrapolation methods you have used.
Figure 3: It would be great to have a map of the bathymetry maybe in the supplement. That could help with the interpretation of panels a) and d), as the spatial patterns here are likely driven by water depth, which was used in the ML model, but not in the Kriging based interpolation.
L210: Instead of “top meter”, do you mean “top 10 cm”?
Section 3.3: Have at least the water and sediment fluxes been validated against observations? It is also not clear to me if you only used the predicted map of surface sediment OC densities based on the ML model, or if you also performed these analyses with the result from the Kriging-based interpolation. It would be interesting to see in how far the results vary based on the predicted sediment OC map.
L271ff: In how far can you say that you obtain similar results? Do you only compare the average surface sediment OC concentration, or have you also compared the spatial patterns in these OC concentrations? Only if you get a similar spatial pattern, you can convince me that you get similar results with so much less predictors.
L277: But you conclude that lateral transfers have a strong impact of the distributions of surface sediment OC concentrations. If you could show that including bottom current strength improves the performance of your ML model, this would strongly support your conclusion.
L331-333: But the estimate by Thomas et al. seems very close to your estimate.
L335-336: Ok, this means that these estimates are not comparable. You could have started with that.
L351ff: In how far would it be necessary to distinguish terrestrial fraction from the authochthonous (produced within the marine ecosystem) fraction of the buried OC?
L389-392: What about shifts over the last 100+ years following eutrophication, soil erosion, overfishing etc.? Wouldn’t these anthropogenic perturbations induce substantial shifts in OC burial?
L400: Again, it is not clear how you defined and quantified the stable POC. Is that already given in the observation you used?
L410: In how far could that driver be represented by the distance to shore predictor? In how far do you think this biases your prediction maps, in particular for the near shore areas?