In their manuscript, Savelli et al. describe their implementation of river fluxes in the ECCO-Darwin model, and evaluate the performance of the model after this implementation. The paper is well written, the methods are generally sound, and the analysis of the effects of river fluxes in the model is well reflected and seems robust. The manuscript is also well suited for GMD. While I think the paper is close to publication, it might lack a bit of really novel aspects, since the implementation of river fluxes has been described in a few GOBMs in recent years, as cited in the study. I believe it would be relatively straight forward to add a few more interesting aspects originating from the implemention into the ECCO-Darwin model specifically, and would strongly recommend to do this (phytoplankton species shifts? More detailed process-based explanations of divergent FCO2 responses in the different regions?). I also have a few major points that should be clarified and I hope they will also improve the manuscript.

• I would not refer to the implementation as a critical one, as in the title, since the effects of the implementation shown for the global ocean are shown to be quite limited here. While it would be a different case if the model was focussing on coastal fluxes, there does not seem to be any other advancements in this direction presented in this paper.
• I think the introduction could be improved. While the important points are there in my opinion, it reads a bit disconnected. I would try to streamline and especially underline the following points: 1. Rivers transport carbon, nutrients and alkalinity to the ocean, 2. These transports are central for biogeochemistry and biological life in coastal regions. They also can affect open ocean biogeochistry due to offshore transport. 4. Models of the current generation do not well represent these transports and their implications.
• The methodologies section is missing the component of describing general nutrient an carbon sources and losses in the model, which I think is highly relevant to understanding the role of river inputs and their fate in the ocean. Where was biogeochemical matter originating from previous to the river implementation. How does the loss through burial work in the model? Maybe this is less relevant for ECCO-Darwin due to corrections made through assimilation, but it should still be described.
• The river implementation accounts for present-day river fluxes as inputs, and the authors use these fluxes to spinup the model, if I understand correctly. These fluxes have however been subject to strongly dynamical changes over the past century. Due to the longtime scales in the ocean, most of the ocean is thus likely more closely equilibrated with preindustrial fluxes. Thus spinning up the model with present-day fluxes will likely overestimate their contributions in the open ocean (which the authors explain due to offshore transport processes solely). I think this should definitely be discussed and taken account for future work.
• The CO₂ source simulated by the model is strongly underestimated compared to what is currently estimated and used in the Global Carbon Budget (Regnier et al., 2022; Friedlingstein et al., 2024). The magnitudes of C, N and alkalinity river inputs, seem however consistent with literature values, which are thought to favor CO₂ outgassing taking account input-to-export/burial ratios. Could the authors potentially better explain the discrepencies of the flux simulated in the model with presently used values (Is it a question of timescale of the spinup? Assuming present-day atmospheric CO2 versus preindustrial concentrations? Stoichiometries?).

Regnier, P., Resplandy, L., Najjar, R.G. et al. The land-to-ocean loops of the global carbon cycle. Nature 603, 401–410 (2022). https://doi.org/10.1038/s41586-021-04339-9

• I would suggest additionally using regional coastal water residence times estimated in literature and their differences between regions to explain differences for the different coastal responses in different regions of focus (e.g. regional values in Liu et al., 2019; Lacroix et al., 2021). For instance, high residence times in Arctic region could favor more outgassing of terrestrial organic material, versus less uptake in these light-limited regions through the nutrient inputs.

Liu, X.,  Dunne, J. P.,  Stock, C. A.,  Harrison, M. J.,  Adcroft, A., &  Resplandy, L. (2019). Simulating Water Residence Time in the Coastal Ocean: A Global Perspective. Geophysical Research Letters,  46,  13910–13919. https://doi.org/10.1029/2019GL085097

Lacroix, F., Ilyina, T., Laruelle, G. G., & Regnier, P. (2021). Reconstructing the preindustrial coastal carbon cycle through a global ocean circulation model: was the global continental shelf already both autotrophic and a CO2 sink?. Global Biogeochemical Cycles, 35, e2020GB006603. https://doi.org/10.1029/2020GB006603

Specific Comments

L17 “At the same time, most of the refractory part of riverine organic carbon is transported offshore from river mouth regions as it is remineralized at slower turnover rates.” This is a bit of a jump from the previous sentence. Did you mean to add that river transports play a central role for biogeochemical processes in the coastal ocean first?

L25 I would also add that terrestrial OC is thought to cause a source of CO2 to the atmosphere (after degradation).

L27 “Globally, this lateral input increases ocean primary productivity and contributes to an estimated coastal-ocean sink of∼ 0.25 Pg C yr−1, which is roughly 17% of the global-ocean sink (Cai, 2011; Lacroix et al., 2021; Gao et al., 2023).”

I would use Dai et al. (2022) and Resplandy et al. (2024) here as more recent estimates:

Dai, M., Su, J., Zhao, Y., Hofmann, E. E., Cao, Z., Cai, W. J., ... & Wang, Z. (2022). Carbon Fluxes in the Coastal Ocean: Synthesis, Boundary Processes, and Future Trends. Annual Review of Earth and Planetary Sciences, 50, 593-626.

Resplandy, L., Hogikyan, A., Müller, J. D., Najjar, R. G., Bange, H. W., Bianchi, D., ... & Regnier, P. (2024). A Synthesis of Global Coastal Ocean Greenhouse Gas Fluxes. Global Biogeochemical Cycles, 38(1), e2023GB007803.

L157 “Additionally, the data-based products exhibited lower surface-ocean pCO2 compared

to ECCO-Darwin Baseline (Figure 1i) in the Arctic Ocean and near the periphery of Antarctica; regions where observations are highly limited in space and time.”

Could this potentially also be a sea ice representation problem?

L193 “the increase of NPP” -> The areal increase in NPP?

L197 “In Baseline, ARCT results in a CO2 uptake of roughly 0.21 Pg C yr−1.” This reads as if ARCT was a simulation, would slightly revise the wording.

Table 4. In terms of global FCO2, I would add the estimates of Aumont et al., 2002 and Lacroix et al., 2020. The table also only shows model derived estimates, whereas some budget-derived estimates also exist and are, as of now, preferably used in assessments (e.g. Regnier et al., 2022).

Aumont, O., J. C. Orr, P. Monfray, W. Ludwig, P. Amiotte-Suchet, and J.-L. Probst (2001), Riverine-driven interhemispheric transport of carbon, Global Biogeochem. Cycles, 15(2), 393–405, doi:10.1029/1999GB001238.

The manuscript describes impacts of adding observationally constrained rates of riverine input of DIC, DOC, DIN, DON and DSi to the global multi-functional type biogeochemical ECCO-Darwin model. The impact of various combinations of riverine carbon and nutrient supplies on model-data misfits with respect to surface pCO2 and air-sea CO2 fluxes are investigated, and some improvements are found, particularly when riverine DOC supply is simulated. 

The study adds some information to other recent efforts to address the historical lack of realistic descriptions of the land-ocean interface in current global marine biogeochemical models. Results are relatively unsurprising, i.e. CO2 emissions from the ocean increase when DOC with a lifetime of 100 days is added to the ocean surface at river mouths, and CO2 uptake by the ocean increases in some regions where additional nutrients are added by rivers. The design of the study results in only limited gain in terms of scientific understanding. I have three main concerns about the present version of the study that limit the gain in scientific understanding:

• First, the riverine input of biogeochemical tracers is added to a calibrated model run without riverine input, which -presumably- tries to make up for the missing river input by adjusting model parameters or other control variables. The model configuration with riverine input is not calibrated. Thus, the comparison is between a calibrated and an uncalibrated model version. Difficult to asses. Results are more a sensitivity analysis rather than an assessment of structural model improvements.
• Second, the simulations with riverine inputs are, if I understand correctly, run only from year 1992 to 2019, i.e. 28 years, of which the first 8 years are taken as spin-up, and 2000-2019 as analysis period. Particularly for the addition of nutrients, this is likely insufficient to reach a steady state. Some time series of relevant model output (NPP in different regions, nutrient and carbon concentrations) needs to be shown to allow the reader to assess the issue of inferring general results from short decadal-scale simulations only.
• Third, several implicit and explicit assumptions may have relevant impacts on the results shown. Some assumptions are stated, e.g. the assumed 100 day lifetime of riverine DOC, or the assumption of zero phosphorus input from land while dissolve silica is included, others are not, such as the presence of denitrification and/or nitrogen fixation. In order to provide “a critical step forward’, as stated in the title of the manuscript, a more comprehensive sensitivity analysis with respect to major assumptions would be required, possibly extending the analysis to riverine supply of phosphorus.

Overall, I find the direction of the manuscript scientifically useful, but the results and the analysis shown do not match the high ambitions raised by the title of the manuscript. There are a number of individual points that need attention, as listed below. I recommend a major revision before the manuscript should be accepted for publication.

Individual points:

l.17 ‘slower’ than what?

l.24/25 ‘excess of alkalinity relative to DIC’ Does this refer to concentrations or to fluxes? How does this fit to outgassing (a flux)?

l.27 There does not always have to be alkalinity production, e.g. when calcifiers are involved.

l.28 ‘estimated coastal-ocean sink’ of what ? Total carbon, riverine carbon, marine carbon?

l.84 does ‘particulate organic matter’ mean detritus or phytoplankton and zooplankton as well?

l.93. Does this mean there is only 8 years of spin-up? Is the biogeochemistry in some form of steady state after such a short period, and if so, in what regions?

l.96ff The model evaluation addresses surface pCO2 and air-sea fluxes of CO2 only. It would be useful to provide some assessment of simulated NPP, biomass and nutrient distributions.

l.138 Would be good to add if the extreme value was high or low, and also provide a very brief explanation for why (only) this value had to be corrected. 

Table 2: The units are unclear and likely wrong. If Tg/yr, then the assumed stoichiometry of at least DOC, DIN needs to be provided. References provided in Table 2 are too generic, e.g. some labeled 1-3 do not even mention DSi. 

Fig.3: color scale does not seem optimal. A log-scale might allow easier interpretation. 

Table 3. Air-sea CO2 fluxes seem to have the wrong sign

l.186. Presumably t_DIC plays only a small role compared to t_DOC because of the assumed compensation to DIC input by ALK input? Might be good to say this here.

l.224 ‘and freshwater discharge’ is misleading. If I understand correctly, freshwater discharge is identical in all simulations?

l.235 ‘of dissolved carbon input’ - should it read dissolved organic carbon input?

l.237 please provide a brief explanation of why model skill decreases here.

l.248 why do you think input might be overestimated rather than underestimated? Could there be positive feedbacks, for example via redox-sensitive Fe and P cycling? 

l.282ff would be good to mention possible effects of explicitly accounting for denitrification, as done in some previous studies cited by the authors.

l.296 why overestimated and not underestimated?

l.297 why only faster degradation and not slower? 

l.332 I do not understand ‘lack of nitrogen and silica-limited taxa’ The model explicitly resolves diatoms and 4 other phytoplankton species. Aren’t diatoms nitrogen and silica-limited in your model?

l.362. I do see that this ‘study is a critical step forward’. This would have to be justified in more detail.

l.403 why only overestimated and not underestimated?