the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 15 Jul 2026
Impact of ocean-forcing temporal resolution on biogeochemical dynamics and forecasting in the Mediterranean Sea
Abstract. The temporal forcing frequency of ocean dynamic fields used to drive transport–biogeochemical models in off-line coupling configurations can critically affect model performance, especially when mesoscale and high-frequency biogeochemical variability are resolved. This study demonstrates the benefits of using high-temporal-frequency ocean dynamics to force biogeochemical simulations within the Mediterranean Sea forecasting system of the EU Copernicus Marine Service. The OGSTM–BFM transport–biogeochemical model was forced with 6-hourly and 24-hourly averaged outputs from the Mediterranean Forecasting System (MedFS, based on NEMO–WW3-OceanVar) with particular attention to the role of vertical transport processes in regulating primary productivity. Validation against BGC-Argo and satellite observations revealed that the 6-hourly forcing improved the timing of phytoplankton blooms across several Mediterranean subbasins, as well as the spatial distribution of chlorophyll and nutrient concentrations—most notably in the western Mediterranean and Ionian Sea during winter. Enhanced sub-daily advection in winter and intensified mixing in summer were identified as the dominant processes driving these biogeochemical responses, leading to better representation of winter surface blooms and a broader deep chlorophyll maximum layer in summer. Although basin-scale primary productivity patterns remain broadly consistent, local productivity intensity varies in response to the altered vertical transport regime.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2026-3413', Anonymous Referee #1, 20 Aug 2026
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RC2: 'Comment on egusphere-2026-3413', Anonymous Referee #2, 26 Oct 2026
# egusphere-2026-3413
Impact of ocean-forcing temporal resolution on biogeochemical dynamics and forecasting in the Mediterranean Sea
Decision: Rejection
There are some good findings in this study, and the objectives and experimental settings are legitimate. However, I do not think the manuscript is ready for peer review for the reasons outlined below. Substantial work is needed before reviewers can properly evaluate its scientific quality and value. I recommend resubmission after improving the presentation, eliminating inconsistencies and speculative descriptions, and thoroughly cleaning up the document.
General comments:
Scientific significance
This study aims to investigate the impact of 6-hourly physical forcing on the biogeochemical state in the offline-coupled BFM biogeochemical module configured for the Copernicus Med-MFC modelling system, compared with its 24-hourly forcing setup. The experiments use the same model with two different forcing frequencies, and differences in primary productivity and associated parameters in the upper 200 m of the ocean are analysed. The analysis reveals region- and season-dependent responses to changes in the temporal resolution of physical forcing, and the underlying dynamical and mechanistic causes are investigated and discussed.
BGC-Argo float data are used to validate whether the model system benefits from the introduction of higher-frequency forcing. Temporally better-resolved vertical eddy diffusivity and vertical advection are the two main forcing terms contributing to changes in the BGC state. Their relative contributions depend on the season (winter or summer) and region (western or eastern basin), owing to differences in stratification and ecosystem regimes.
Scientific quality
The experimental settings and results are legitimate and provide meaningful and useful knowledge for the operational oceanography and coupled BGC modelling communities. However, I found the manuscript very difficult to read, mainly because of its poorly structured logical flow, grammatical and editorial issues, inconsistencies among statements, and numerous claims that are not necessarily supported by the material provided.
For example, the manuscript states in L.193: "Validation consists of RMSD and bias values for the 16 sub-basin subdivision (Salon et al., 2019) shown in Fig. 2." However, Tables 3, 4, and 5 present RMSD and correlation, and there is no bias assessment throughout the rest of the manuscript. In addition, the description of one of the sub-basins, AEG, is missing from the caption of Fig. 2, and the tables do not include an analysis of AEG, although it is evaluated in Fig. 9.
There are also issues with the validation design of the two experiments. For example, the validation metrics against BGC-Argo profiles include RMSD and correlation but not bias, even though the high-frequency forcing may introduce fundamental changes in the dynamical response of the BGC module, such as changes in bloom onset timing, as reported in this manuscript. This choice of metrics obscures an overall assessment of the model response to high-frequency physical forcing.
Overall, there are too many issues for me to list them all here, but the critical points are outlined in the specific comments below.
Presentation quality
The overall quality of the figures is relatively poor, mainly because of numerous editorial errors, a poorly structured introduction, and images that have not been carefully cropped and contain text that is too small. Some figures are not effective in supporting the discussion in the manuscript.
As mentioned above, many statements in the Results and Discussion sections cannot be validated using the figures provided and sometimes appear merely speculative. Another major issue is the frequent emphasis on the impacts of mesoscale and submesoscale dynamics on primary productivity, despite these impacts being barely analysed in the manuscript. The manuscript ultimately concludes that vertical eddy diffusivity and advection are the main contributors to the observed changes. This creates considerable confusion for the reader. I provide further details point by point in the specific comments up to P14 below.
Specific comments
L.27–29: "Among these processes,..."
The first paragraph of the Introduction ends by emphasising the importance of submesoscale dynamics (SMD) for marine productivity. This is the beginning of the confusion, since SMD is clearly not the focus of this study. Why did the authors choose this opening statement?
L.38–39: "but risk losing..."
Mesoscale dynamics typically operate on synoptic timescales in the ocean, ranging from approximately one day to one week. I agree that the physical model needs to run with a sufficiently small time step to resolve mesoscale or submesoscale dynamics, but this does not necessarily mean that the offline input to the BGC module needs to have high temporal resolution. I also could not find such a statement in Alvarez et al. (2022).
L.40–45: "Temporal interpolation schemes..."
I do not understand the intention, meaning, or structure of this paragraph. Why does temporal interpolation in offline coupling cause inertial oscillations?
L.45–52: "Previous studies examining..."
This entire paragraph is difficult to follow. For example, in L.45–48, are the authors referring to the coupling frequency in a coupled atmosphere–ocean model system or to the frequency of atmospheric forcing supplied to an ocean model?
L.55: "experiments"
Were these experiments conducted in the cited studies by Levy et al. (2012) and Oschlies et al. (2002)?
L.59–62: "Nonetheless,..."
I cannot understand the structure of this sentence. Why would high-frequency (HF) coupling "amplify" the effects of "unresolved small-scale variability", "approximations in interpolation and parameterizations"? Furthermore, what do these terms mean in the first place?
L.115: "NEMO-WW3 ocean model"
Can the authors specify the temporal frequency of the atmospheric forcing applied to the ocean model?
L.123: "Daily..."
Vertical material transport in a numerical ocean model is normally represented through three processes: (1) advection by vertical velocity, (2) vertical eddy diffusion, and (3) convective adjustment. The first two can readily be incorporated into offline coupling, as mentioned here, but the third is more complicated. Is any form of convective adjustment used in the NEMO configuration? If not, how is winter convective mixing treated? Is it represented through enhanced vertical eddy diffusivity?
L.172: "Winter Bloom Layer (WBL)"
The authors chose to use WBL rather than Chl-a or phytoplankton biomass to diagnose the impact of HF forcing on the BGC state. I assume that WBL is used as a proxy for winter bloom strength rather than simply to identify the depth of the productive layer. Otherwise, it is not easy to connect changes in WBL with primary production and oxygen in the surface layer, as discussed later. I suggest that the authors explain more clearly why WBL is relevant for diagnosing changes in primary productivity.
L.175: "Nutricline Depth (NUTR)"
This is the only place where NUTR is defined, and this index is never used again throughout the manuscript. Instead, NITR2 in Table 2 is used as a proxy for NUTR. It is difficult for readers to understand the relationship between these two metrics at a glance. Please explain their relationship clearly here.
L.178: "Euphotic Layer Depth"
To use ZEU as a metric, the authors first need to explain that the PAR profile is influenced by the Chl-a concentration. Please describe this process in Section 2.1.
P.6, Table 1
The periods defined as "summer" and "winter" are not specified before this table. The only indications are in L.171, "summer stratification period (Apr–Oct)", and L.172, "the winter-spring bloom period (Jan–Mar)". Please clarify the definitions of "summer" and "winter" before introducing this table.
L.193
The manuscript states that "Validation consists of RMSD and bias values for the sub-basin subdivision". However, Tables 3, 4, and 5 present RMSD and correlation, and no bias assessment is provided throughout the rest of the manuscript.
P.7, Fig. 2
The sub-basin names are not readable on the map, particularly NWM and AEG. The description of sub-basin AEG is also missing from the figure caption.
L.245: "While the systematically..."
The sentence is incomplete.
L.261: "However, energetic zones persist..."
I do not see a persistent energetic zone in the Sicily Channel during summer (Fig. 4b).
L.260, L.265, L.286
Three different expressions, "Sicily Strait", "Sicily Channel", and "Sicily channel", are used to refer to the Sicily Strait in this manuscript. Please use consistent terminology throughout.
L.274: "with winter values..."
I do not see evidence in Figs. 5a and 5b that the winter values are "one order of magnitude higher than in summer". Can the authors identify the sub-basins in which this large seasonal difference is observed?
The manuscript demonstrates a positive correlation between total kinetic energy (TKE) and NPP during summer, whereas NPP appears insensitive to TKE during winter. This seasonal difference is attributed to the strength of stratification and, consequently, nutrient availability.
L.310: "This is indicative of..."
This is an interesting finding, suggesting that higher-frequency forcing does not necessarily lead to greater vertical redistribution of biogeochemical tracers. Does this mean that the net nutrient flux associated with vertical advection is lower in the 6H run than in the 24H run?
L.329–331: "In winter,..., in the 24H run"
The anomaly patterns at the three Argo float locations show quite different spatiotemporal characteristics, making it difficult to identify the common pattern described here. For example, the "negative anomaly in winter surface nitrate" does not appear in Fig. 6a1 during winter. In addition to the lack of common patterns across the three sites, the described pattern of "an opposite positive anomaly just below the surface" is not evident in Figs. 6a2 and 6a3 during winter and spring.
P.12, Fig. 6, and P.13, Fig. 7
The legend entry "Nitrcl", used in the nitrate figures (Figs. 6a1, 7a1, and 7d1), is never defined in the manuscript. I assume that it refers to NITR2. Please clarify this.
P.14
Why have the line numbers been reset on this page?
P.14, L.2–5: "Nitrate anomaly..."
The pattern described as common to the three sites (Figs. 7a1, 7a2, and 7a3) is clearly evident only in Figs. 7a2 and 7a3. The anomaly pattern at float 6902903 does not appear to match this description at all.
P.14, L.5–7: "NITR2 (Fig. 6) slightly changes... with the latter showing higher fluctuations..."
I cannot see these "higher fluctuations" in the figures. The two lines for "Nitrcl 6H" and "Nitrcl 24H" appear to overlap almost exactly most of the time. Can this statement really be supported by these figures?
P.14, L.7–8: "In the 6H run..."
If the statement that the DCM layer becomes shallower and broader during summer is correct, it contradicts the earlier observation on P.14, L.1–2: "In summer differences are minor but systematic: the 6H run produces a broader DCM with reduced Chl-a peak values, similarly to a distribution with greater variance but similar mean."
Figs. 5b2 and 5b3 appear to support this earlier observation, showing a negative anomaly along the DCM in the 24H run, while the DCM in the 6H run appears to overlap almost perfectly with that in the 24H run. Where, then, does the conclusion about the shallowing of the DCM layer come from?
P.14, Table 2
As pointed out above, please include bias alongside correlation to assess the differences in model skill between the 24H and 6H runs.
P15 and later
There are too many problems in the rest of this manuscript. Please cleanup the mess first before resubmission.
Citation: https://doi.org/10.5194/egusphere-2026-3413-RC2
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- 1
This manuscript seeks to evaluate how and whether higher frequency temporal forcing of a BGC-model in the Mediterranean Sea improves the representation of BGC variables, especially with respect to phytoplankton and the processes that affect their growth. This is overall a useful thing to do, and I appreciate the explicit investigation of links to the physics and how they are resolved. However, there are a few points, outlined below, that puzzle me with respect to the evaluation. The way the results are currently presented, I am not convinced that they support all the claims, especially since statistical significance is not reported. I hope that my suggestions for improvements are useful.
Written text:
The Introduction and Methods are overall well written, so I don’t have many comments for these. The discussion of physics results also makes sense to me (though I am not an expert in this field). However, the Results section is overall a bit repetitive and formulaic, and the Discussion is poorly organized and would benefit from sub-headers and a clearer focus. For the Results section, a structure along these lines could be considered:
Analysis:
Regarding float data: My main “sticky point” with the results is that the 3 BGC floats are under-utilized in their ability to be “points of truth” for the two model runs. For example for Figure 7, why not calculate the difference between float data and the 6H run, and also float data and the 24 H run? That appears to be an important step to me, because a priori I am not ready to accept that the 6H run is “better” than the 24H. The way the abstract and discussion are currently written, they really call for this kind of reality check. With such a figure you can pin-point where the improvements are, e.g. in the vertical distribution of properties. In my understanding (and based on my reading of the abstract), the ultimate question shouldn’t be “which run resolves more variability”, but “which run is more realistic”? These two concepts get a bit muddled in the current manuscript. I also suggest showing the actual float data the same way that model data is shown in Figure 6.
Regarding Table 2: I’m not sure that these numbers are meaningful. An “annual mean correlation” is likely largely driven by the seasonal progression, which you’d hope even crude models get right. The 6H run is after resolving small-scale processes (in time, and also space possibly), so showing such a crude correlation is not very meaningful. The observed differences between the 6H and 24H run are also rather small. Are they statistically significant? A more meaningful table would report correlations (between model runs and Argo float data) for the BGC metrics described in Table 1.
Regarding npp: I note that the npp estimates from the model are never directly compared to observational data (from satellites or BGC-Argo floats). This may be a deliberate choice, as the observational data are not without flaws, but it would be useful to be a bit more explicit about this. Direct comparisons are being made for chlorophyll and nitrate, so not taking this direct comparison step for npp is worthy of an explanation.
Statistic significance – is rarely mentioned when you make comparisons. More detailed comments in the below, but overall, this is something that should be reported when making comparisons between things like RMSD, model to model.
More specific comments:
Given how much the results and discussion rely on differences (between the two models, and between models and Argo data): it would make sense to define parameters for these differences (call them “delta” or something along those lines), that way it’s always clear what was subtracted from what. This information is currently lacking for quite a few figures.
Frequently, when “improvements” or changes are discussed (e.g. p19, l130), it would be informative to also mention the %change. Being told that npp increases in one run by 3 g C m-2 yr-1 doesn’t mean much to the reader if the context isn’t given. This is also very much true for Figure 9, where the changes appear miniscule to the eye. How big are the differences in %? And are any of them statistically significant?
Figure 6: npp is not a concentration, and the white and black lines in the section plots are not defined
Figure 7: Nitraclines are hard to see and don’t always seem to align with what is shown in Figure 6; they are also missing from the third row of section plots (oxygen)
Figure 11 and its discussion: the numbers discussed don’t align with what is in the Figure. So I can’t comment on this part, but this obviously needs tidying up.
All figures would benefit from bigger axes labels
Tables 3-5: suggest putting these in the supplementary and only pull out some meaningful metrics that are worth discussing in more detail (maybe that will be covered with my suggestions for Table 2 above). Also, are any of the RMSD comparisons statistically significant? I’m also unsure that “vertical correlations” between profiles are useful metrics, as these will be largely driven by profile shapes, which you’d hope are overall in agreement.