The Spatiotemporal Distribution of Dissolved Inorganic Carbon in the Global Ocean Interior: Reconstructed through Machine Learning

Ehmen, Tobias Friedrich; Mackay, Neill Sutherland; Watson, Andrew James

doi:10.5194/egusphere-2026-3396

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https://doi.org/10.5194/egusphere-2026-3396

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02 Sep 2026

| 02 Sep 2026

Status: this preprint is open for discussion and under review for Biogeosciences (BG).

The Spatiotemporal Distribution of Dissolved Inorganic Carbon in the Global Ocean Interior: Reconstructed through Machine Learning

Tobias Friedrich Ehmen, Neill Sutherland Mackay, and Andrew James Watson

Abstract. The oceans mitigate climate change by absorbing 25–30 % of anthropogenic carbon emissions. Decadal variability in the ocean carbon sink has been suggested by pCO₂-based reconstructions of the ocean uptake, but these variations are less apparent in reconstructions based on global ocean biogeochemistry models (GOBMs) which also predict a slower increase in the ocean sink over the period from 2000 to 2015, raising concerns about our ability to accurately project future changes. An independent method to study the uptake uses interior observations to calculate how dissolved inorganic carbon (DIC) is changing. To address the sparsity of interior data, machine learning techniques have been applied, but as yet, global, full-depth reconstructions of the complete inventory of DIC have not been produced. Here we develop such a full-depth reconstruction, from the 1990s to 2019, using "ResNet-DIC", a deep neural network trained on GLODAPv2.2023 observations. Atmospheric CO₂, location, temperature, and salinity from EN4 analysis are used as predictors. Our method shows good predictive power when validated using independent data sets and model subsampling experiments. We diagnose the total oceanic DIC pool as 37,508 ± 274 Pg C in 2019 with an average rate of increase of 2.64 ± 0.13 Pg C/year over the whole time period. The global change in the DIC inventory exhibits pronounced peaks in decadal variability, especially in the early 2000s, driven primarily by intermediate waters at depths of 300–1000 m, particularly in the Atlantic, Indian, and Southern Oceans, and to a lesser extent in the Pacific. The accumulation rate of DIC increases steadily from the mid-2000s.

Received: 10 Jun 2026 – Discussion started: 02 Sep 2026

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Tobias Friedrich Ehmen, Neill Sutherland Mackay, and Andrew James Watson

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RC1:
'Comment on egusphere-2026-3396', Daniel Burt, 17 Sep 2026 reply
Peer Review of
The spatiotemporal distribution of dissolved inorganic carbon in the global ocean interior: Reconstructed through machine learning
Authors: Tobias Friedrich Ehmen, Neill Sutherland Mackay, and Andrew James Watson

Dear Editor,

I believe the reviewed work is scientifically significant and presents necessary development in the field of ocean biogeochemistry reconstruction. I believe the methods largely sound and the work well presented. I believe the reviewed manuscript should proceed to publication with minor revisions. I include my comments below.

Scientific Comments:
The authors analyse decadal variability in the manuscript but are limited to a time period of 30 years by the availability of predictor data. The authors also express that the start and end of the 30-year prediction should be treated with caution due to temporal edge effects (lines 393-398). Furthermore, it is noted that the author’s describe a negative bias in section 4.2 at lines 387-388 and reference section 3.1, but in the referenced section, appear to describe the evolution of the prediction bias in time (Fig. 5 & 6) rather than directly addressing the bias in the trend itself. Overall, the reviewer is not confident that the product describes a clear decadal variability (line 477). Though the reviewer does agree that the product is able to capture the observed and modelled trends over the full prediction period.

The authors do not describe the treatment of predictor data to the satisfaction of the reviewer. Given the 4-dimensional nature of the prediction; how is 3-dimensional atmospheric CO₂ data treated? The authors do not appear to acknowledge the lack of spatial heterogeneity in atmospheric CO₂ by using a monthly mean value from Mauna Loa globally. Furthermore, are the GLODAPv2.2023 observational data binned (though the duplicates described at line 251 suggests data were not binned) or otherwise processed prior to training?

At line 162, the authors address the greater availability of temperature and salinity data in the EN4 dataset compared to the availability of oxygen, which is a reasonable argument. However, the authors do not appear to put this in context of the even lower availability of dissolved inorganic carbon data in GLODAPv2.2023, which is also described to be O(10⁵) (Lauvset et al., 2024). This context would appear to weaken the justification for not using additional biogeochemistry predictors due to data availability, especially given the importance of biogeochemistry predictors indicated in Figures 2 and A14. The reviewer would like the authors to expand and clarify this justification.

The authors cite Turner et al. (2023) as justification that temperature and salinity are well-suited for reconstructing dissolved inorganic carbon. However, Turner et al. (2023) conclude that temperature and salinity may be insufficient and with increasing errors below 1000m depth. The authors do not appear to acknowledge this limitation despite the prediction being presented as performing better at depths greater than 1000m throughout the manuscript. The reviewer would like the authors to address how much of this predictive success may be due to the slow-varying concentrations in the deep ocean as opposed to the predictive power of temperature and salinity.

The authors describe validation of the machine learning model in section 3.1 and highlight “any model likely represents a system of lower complexity than the real ocean” (lines 260-261). The authors proceed to describe a marginally poorer prediction with larger magnitudes of RMSE and bias for NorESM and ECCO-Darwin model data than for the real-world observations being validated. The reviewer acknowledges the successful validation but finds that the authors weaken their own validation as the machine learning model could be expected to have greater predictive power for a less complex system. The authors do not appear to address this point. A potential explanation for why this is the case may counteract the weakening by raising these points.

The reviewer is concerned by the spread of ensemble members described in section 4.2 (lines 393-398). The reviewer is not familiar with Residual Neural Networks but it is not uncommon for other machine learning reconstruction methods to tend towards the mean and therefore produce a smaller ensemble spread around the mean year (e.g. 2005) but here the authors find a reduced ensemble spread around the year 2000 and also note that this is a year with low training data availability. The reviewer finds the authors explanation that “there may be additional uncertainties introduced through temporal edge effects” to be insufficient explanation, especially when taken in addition to the previous concerns expressed about the impact of temporal edge effects on the decadal variability conclusions over a 30-year prediction period. The reviewer invites the authors to expand on the explanation of why the ensemble spread is smaller around a year with low data availability.

The authors raise the point that the Residual Neural Network method employed is highly computationally efficient (lines 492-494) but elected to produce an ensemble of 15 members, lower than typical statistical standards. The reviewer queries this choice.

Language/ Text Comments:
Line 56: “If the variability it is real…” grammatically incorrect.

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Citation: https://doi.org/10.5194/egusphere-2026-3396-RC1
RC2: 'Comment on egusphere-2026-3396', Anonymous Referee #2, 30 Sep 2026 reply

This manuscript presents ResNet-DIC, a machine-learning reconstruction of global interior-ocean DIC extending to nearly full ocean depth. I think the development of a full-depth, observation-based DIC reconstruction is timely and potentially valuable. In particular, the attempt to use discrete GLODAP observations rather than mapped biogeochemical climatologies is interesting.
However, I have several substantial concerns regarding the choice of predictors, the validation strategy, and the interpretation of changes in total DIC as changes in the ocean carbon sink. I also found the methods difficult to follow in their current organization. I think these issues need to be addressed before the robustness of the reconstructed temporal variability can be assessed.
Major comments
In my opinion, the methods need substantial restructuring. The current methods mix descriptions of the input datasets, neural-network architecture, justification relative to previous products, predictor-selection experiments, and validation results. This makes it difficult to determine exactly what data enter the reconstruction and how the final product is generated.
At present, Section 2.1 moves from ResNet to SOM-FFN and back to ResNet, while Section 2.2 contains substantial discussion of MOBO-DIC and already begins presenting predictor-performance results. The reader mainly needs to know what was done and why. Comparison with previous reconstruction approaches could be shortened substantially here and moved to the Discussion.
This would also help clarify Figure 1b. At present it is not obvious that temperature and salinity both constitute predictor information and define the EN4 mapping grid. The manuscript states that the trained model is subsequently mapped onto EN4 temperature and salinity fields, but the schematic visually separates these concepts in a confusing way.
I am not yet convinced that temperature and salinity are sufficient predictors for reconstructing temporal changes in total DIC. Temperature and salinity contain substantial information about water masses, circulation, mixing, and preformed carbon, but remineralization and other biogeochemical processes strongly affect interior DIC. I am therefore concerned that a reconstruction based primarily on temperature, salinity, location, depth, and atmospheric CO2 may reproduce the large-scale distribution of DIC (likely preformed increasing with CO2?) while failing to reproduce the processes responsible for its temporal evolution.
The authors already show that adding oxygen reduces GLODAP RMSE from approximately 7.9 to 7.0 µmol kg-1, and adding oxygen, nitrate, and silicate reduces it further to approximately 5.2 µmol kg-1. I do not think the relatively modest difference in global RMSE is sufficient to demonstrate that these variables are unnecessary.
The relevant test is whether the scientific conclusions about DIC variability and trends are robust to predictor choice. I strongly encourage the authors to train at least an alternative T/S/O2 model and compare, for example: vertical or basin-scale DIC sections; spatial patterns of DIC change; trends at HOT/BATS or other long-term observational locations; basin and depth-resolved inventory changes; and ideally, the reconstructed temporal evolution shown in Figures 11 and 13. If the T/S-only and T/S/O2 reconstructions produce similar temporal and spatial changes, that would provide much stronger support for the chosen predictor set. If they do not, then the interpretation of ResNet-DIC as a reconstruction of total DIC variability, rather than predominantly the component associated with hydrographic/water-mass changes, needs to be reconsidered. This concern is particularly important because the headline result of the manuscript is not simply reconstruction accuracy, but decadal variability in DIC storage.
Also, to me, the observational validation needs to be made more independent and more stringent. The manuscript withholds complete vertical profiles rather than individual measurements, which is preferable to a point-wise random split. However, profiles from the same cruises and nearby regions/times can still be highly correlated. The authors themselves show that cruise-based withholding results in poorer predictive performance on the observational data. So for a global reconstruction intended to infer temporal variability, I think withholding entire cruises is a more appropriate test of observational generalization than randomly withholding profiles. I therefore find the statement that profile-based splitting is adopted because the objective is “global reconstruction rather than prediction for entirely unseen campaigns” unconvincing: predicting regions/times that are not directly observed is precisely the purpose of the reconstruction.
I would also strongly recommend that cruise-based validation be treated as a primary validation rather than an appendix sensitivity analysis. It would also be useful to show the spatiotemporal distribution of the held-out observations. A random percentage alone does not establish that the product is tested adequately across basins, depths, and decades.
The ECCO-Darwin and NorESM subsampling experiments are valuable and I would retain them, but they should not be described as equivalent to independent validation against observations. A neural network trained and evaluated within a model-generated ocean tests the consequences of sampling a known internally consistent system; it cannot establish that the corresponding relationships hold in the real ocean.This also makes the independent HOT, BATS, and Drake Passage comparisons therefore particularly important, but three locations cannot provide global observational validation.
The distinction between total-DIC inventory changes and anthropogenic carbon uptake needs to be much sharper. This issue becomes increasingly important in Sections 4.2–4.3 and the conclusions. The manuscript correctly acknowledges that changes in total DIC are not equivalent to anthropogenic carbon uptake, because natural-carbon variability can contribute. However, the terminology subsequently shifts repeatedly toward “uptake,” “carbon sink,” and comparison with anthropogenic carbon-sink estimates. For example, the authors obtain a mean DIC accumulation of 2.64 Pg C yr-1 and compare this with an anthropogenic carbon sink estimate of 2.7 Pg C yr-1. Later, the reconstructed 2015–2020 accumulation reaches approximately 5.9 Pg C yr-1, substantially exceeding contemporary estimates of anthropogenic uptake. The paper interprets much of this variability in terms of weakening and strengthening of the ocean carbon sink. I think the manuscript needs to distinguish consistently between change in total ocean DIC inventory; anthropogenic carbon accumulation; and net air–sea CO2 uptake. Agreement between their long-term magnitudes is interesting, but they are not interchangeable quantities. This is especially important on the five-year timescales emphasized here, where redistribution and natural carbon-cycle variability may matter. So I would therefore temper statements that ResNet-DIC provides an “independent estimate of the ocean carbon sink” unless the authors can demonstrate that the reconstructed total-DIC changes can reliably be interpreted that way.
Finally, the robustness of the temporal variability (the central result) needs stronger demonstration. The most interesting result is the slowdown around the early 2000s followed by a strong acceleration, yet this is also where several methodological concerns converge.The manuscript acknowledges temporal edge effects, sparse observations at the beginning and end of the reconstruction, increased ensemble spread after approximately 2016, and a sharp decline in available data toward the end of the period. The inferred 2015–2020 accumulation rate is also extremely large relative to established estimates. I think the paper would benefit from explicit sensitivity analyses demonstrating that these temporal features are not artifacts of changing GLODAP sampling density or changes in EN4 observational coverage; also the use of atmospheric CO2 as the temporal predictor or predictor selection; and temporal extrapolation near the ends of the training period.
Eg. a useful experiment could be pseudo-hindcasting: truncate the training observations at an earlier year and test whether the model reconstructs subsequently observed DIC evolution. The existing model-subsampling experiments are informative, but I would like to see stronger observational evidence before attributing the reconstructed peaks to real changes in the ocean carbon sink.
Minor and specific comments
Abstract: “An independent method to study the uptake uses interior observations to calculate how dissolved inorganic carbon (DIC) is changing.” This is awkward and non-specific. Perhaps: “An alternative, observation-based approach is to infer carbon storage changes from changes in interior-ocean dissolved inorganic carbon (DIC).”
Abstract: “global, full-depth reconstructions … have not been produced” should be nuanced. There are existing interior carbon/DIC reconstruction efforts, including MOBO-DIC and TRACEv1, although with different depth ranges, target variables, and methodologies. The novelty should be stated precisely rather than implying that no comparable products exist.
Abstract/throughout: Is “ResNet-DIC” the name of the machine-learning architecture/method, or the resulting reconstruction/product? Please use the term consistently.
L26: If the diagnosed inventory is similar to previous estimates, I would state this explicitly rather than simply giving the value.
L42 onward: The p in pCO2 should be italicized consistently throughout.
L56: “If the variability it is real” → delete “it”.
Around L65–75: I suggest first acknowledging existing interior-DIC products and then clearly explaining what limitation the present work addresses. I also do not understand why the use of remote-sensing information by previous studies is presented as a disadvantage in itself. Surface observations could provide useful information about processes propagating into the interior; indeed, later in the manuscript the authors acknowledge that satellite information could improve near-surface predictions.
End of Introduction: The final two paragraphs still read largely as background/methodological justification. I suggest replacing them with a more conventional “Here we…” paragraph stating the objectives, approach, and principal questions addressed.
L95: This appears inconsistent with the earlier suggestion that full-depth/global DIC reconstruction products do not exist. Please sharpen the distinction among total DIC, anthropogenic carbon, depth coverage, and geographic coverage.
L102: A ResNet is a neural network; specifically a deep neural network with residual/skip connections. The wording should make this explicit rather than presenting the two almost as separate model types. The architecture in Figure 1a indeed looks like a neural network because it is one.
L111: Replace “recent version” with the explicit version number, GLODAPv2.2023.
L117: The reconstruction begins in 1990. Please discuss the implications of the history of certified reference material (CRM) use for the comparability/quality of early carbonate-system observations. Is 1990 an appropriate starting date for DIC training data, or would a later start produce a more homogeneous observational constraint? A sensitivity test could be useful.
Figure 1b: I found this confusing. Temperature and salinity are predictor variables but are also supplied through the EN4 mapping grid. The diagram should distinguish clearly between variables in the GLODAP training dataset and gridded predictor fields used for prediction.
L140–145: The discussion that salinity affects alkalinity does not establish that salinity can represent temporal variations in DIC due to biological processes. Please avoid implying a mechanistic adequacy that has not been demonstrated.
L146: Which atmospheric CO2 product/quantity is used exactly? The Methods later indicate deseasonalized Mauna Loa atmospheric CO2. Please specify whether this is mole fraction (xCO2) or atmospheric partial pressure and use the terminology consistently.
Section 2.2: I would separate methodological choices from results. Figure 2 and the RMSE/bias comparison are effectively a predictor-selection experiment and could be presented in a dedicated subsection, rather than interwoven with the description of predictor variables.
Around L173: “Compared to GLODAP” is unclear. Presumably this means predicted DIC versus withheld GLODAP DIC observations. Please specify.
Figure 2 / predictor testing: Because the models including oxygen/nutrients use a different subset of observations, please explain how the comparisons are made fairly. Ideally, predictor sets should be evaluated on the same observations; otherwise differences in RMSE may partly reflect differences in sample composition.
L205: Explain the data partitioning more explicitly rather than simply referring to a “15% train/test split.” In machine-learning terminology, the manuscript actually appears to use training, validation, and a further hold-out test set, so the terminology should be made consistent.
Figure 4: The overall relationship is strong, but I would investigate the scattered high-error observations rather than relying primarily on R2. Are they concentrated in particular basins, depths, water masses, years, or hydrographic regimes? Those points may be disproportionately informative about processes that the predictor set misses.
Section 3.3: The representation uncertainty of 16 µmol kg-1 is adopted from an estimate for total alkalinity. This is a substantial component and apparently dominates the final uncertainty. Please provide stronger justification for transferring this value to DIC, or test sensitivity to this assumption.
Section 3.3 / uncertainty: EN4 uncertainty is explicitly excluded from the propagated reconstruction uncertainty even though EN4 supplies the gridded temperature and salinity fields on which the reconstruction depends. This should be made especially clear when interpreting inventory uncertainties; the quoted ±274 Pg C should not appear to represent all relevant sources of uncertainty.
Section 4.3: I was surprised by the replacement of predicted DIC in semi-enclosed seas with a global mean depth profile for the inventory calculation. Even if the global impact is small, this is an ad hoc correction. Please identify exactly which regions are replaced, justify the procedure, and provide the inventory both with and without this modification.
Around L430 onward: Calling the diagnosed DIC inventory change an “uptake rate” risks conflating inventory redistribution/storage changes with air–sea CO2 uptake. I suggest using “DIC accumulation rate” unless referring specifically to air–sea carbon uptake.
Late-period trend: The 2015–2020 estimate of ~5.9 Pg C yr-1 is extremely high and the authors themselves note both increased ensemble spread and declining data availability. I think this result should be treated much more cautiously in the abstract/conclusions unless additional validation demonstrates its robustness.
Figure 13: The caption states that the reconstruction extends from 1990 to 2023, whereas the abstract and main description state 1990–2019. Please clarify the actual product period and the period used for scientific interpretation.
Around L444: “GLODAPv2.2013” appears to be a typo for GLODAPv2.2023.
Around L390: There are several unit/typographical errors such as “Pg Pg C/yr” and “Pg C Pg C/yr”.
Summary and outlook: The statement that the reconstruction “partly corroborates” variability inferred from surface pCO2 products seems too strong given that the manuscript subsequently acknowledges that this variability may be an artifact of sparse observations. I would phrase this as qualitative similarity rather than independent corroboration unless the robustness tests above support the stronger interpretation.
Summary and outlook: “ResNet-DIC offers an independent observation-based reconstruction suitable for assessing long-term variability and trends in the ocean carbon sink” similarly seems stronger than justified at present. It clearly provides a reconstruction of total interior DIC; whether that reconstruction can quantitatively diagnose variability in the ocean carbon sink is one of the central questions the paper still needs to establish.

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Citation: https://doi.org/10.5194/egusphere-2026-3396-RC2

Tobias Friedrich Ehmen, Neill Sutherland Mackay, and Andrew James Watson

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Data product and code for: Spatiotemporal Distribution of Dissolved Inorganic Carbon in the Global Ocean Interior - Reconstructed through Machine Learning Tobias Ehmen, Neill Mackay, Andrew Watson https://doi.org/10.5281/ZENODO.14575968

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Tobias Friedrich Ehmen, Neill Sutherland Mackay, and Andrew James Watson

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Short summary

The ocean slows climate change by absorbing a large share of human carbon emissions, but estimates of how this uptake changes over time remain uncertain. We used machine learning and ocean observations to create a global map of interior ocean carbon stored throughout the ocean from the 1990s to 2019. Our results reveal substantial year-to-year and decade-to-decade changes in ocean carbon storage and provide an independent way to assess long-term trends in the ocean carbon sink.


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