In their manuscript, Habib et al. presents a new and well-executed analysis of the mechanisms controlling dissolved oxygen dynamics in the Levantine Sea using a high-resolution coupled physical-biogeochemical model. The manuscript is generally well written, supported by observational validation, and provides valuable insights into the seasonal and interannual variability of dissolved oxygen budget, as well as the key physical-biogeochemical processes involved. I have a few minor comments, outlined below:

• It would be useful to include a brief discussion on potential sources of uncertainties in the oxygen-heat budget terms (e.g., on gas transfer velocity; L138-140).
• Since the modelling framework and methods closely follows those used in a previous study by Ulses et al., (2021), I suggest adding a short discussion (and/or in the Introduction) clarifying how the present analysis differs from and builds upon that earlier work. Highlighting the new scientific contributions that emerge from focusing on the Levantine basin will help underline the novelty of the manuscript.
• Consider linking the results to broader implications for regional biogeochemical research and/or Earth system modelling.

• L90-91: please add a reference.
• L149-150: specify which product is used.
• L451: correct the dots in the parentheses.
• L483-495: the sentences “This aligns … distribution of chlorophyll” seem tangential and could be shortened for clarity.
• Fig. 11: add a note clarifying the sign convention (i.e., positive/negative = upward/downward fluxes).

References:

Ulses et al., 2021; doi: https://doi.org/10.5194/bg-18-937-2021 

General comment

The manuscript entitled “Driving mechanisms of the dissolved oxygen budget in the Levantine Sea: a coupled physical-biogeochemical modelling approach” addresses a very interesting and relevant topic. The objectives are undoubtedly important for understanding the variability of the Levantine Basin, a region characterized by high complexity.

However, there are several aspects of the work that I find critical and believe should be discussed and reconsidered, as well as some more formal issues.

Major technical issues 

1) The most important aspect of the study is to clearly define the driving mechanisms. I would expect a graphical or quantitative synthesis illustrating the relative contribution of each process to the observed oxygen variability. However, the manuscript reaches the conclusions without discussing the results in sufficient depth in relation to these mechanisms, focusing instead almost exclusively on the oxygen budget. Furthermore, the role of the Rhodes Gyre appears inconsistent throughout the paper. In the abstract, this structure is presented as a key element (which is indeed justified given its importance), but in the conclusion, you state: “Further investigations on the role of the various cyclonic and anticyclonic eddies will be conducted in the future”. It would be particularly valuable to assess how these mesoscale structures modulate oxygen variability, not only the Rhodes Gyre, especially since numerous studies have emphasized their importance compared to multi-annual averages, which tend to underestimate total variability.

I am not suggesting that your approach is incorrect, but rather that it should account for these processes and their influence on the overall oxygen budget.

Another relevant aspect that is not addressed concerns the effect of marine heatwaves. I suggest referring to Figure 3 of the paper “Co-Occurrence of Atmospheric and Oceanic Heatwaves in the Eastern Mediterranean over the Last Four Decades”. Similarly, the potential influence of Medicanes (see Menna et al., 2022; Jangir et al., 2023) should at least be briefly discussed. If the manuscript aims to identify and quantify the main mechanisms, these phenomena cannot be entirely overlooked.

2) In Estournel et al. (2021) the authors clearly state: “It should also be kept in mind that our simulation is also related to a period characterized by cyclonic circulation in the Ionian Sea.” Later in your discussion section, you write: “Our results on lateral oxygen exchanges are also in agreement with previous studies describing the general circulation in the eastern Mediterranean Sea.” However, it is not entirely clear whether these previous studies describe the classical Levantine Basin circulation or rather conditions associated with an EMT-type regime. For instance, I am not convinced that Zodiatis et al. (1993) depicts the same circulation pattern between Cretan Sea and Levantine Basin described in your work.

Since your model are forced by that physics what extent does the biogeochemical component depend on them? This is a crucial issue, as the eastern Mediterranean is an extremely complex area where both mesoscale and basin-scale variability strongly influence the oxygen dynamics.

The Levantine Basin experiences thermohaline oscillations driven by the Ionian circulation (as you mention in your conclusions and in to the introduction citing Marvopoulou et al., 2020 and Ozer et al., 2022). During anticyclonic phases in the Ionian, the inflow of Atlantic water is reduced, leading to increased salinity in the Levantine basin. This affects not only surface layers but also intermediate and deep waters, both in the Levantine Basin (as discussed by Ozer et al. 2022) and in the Adriatic (Martellucci et al., 2024; Civitarese et al., 2023), showing opposite behavior between the two basins. This inverse relationship is also evident in Mavropoulou et al. (2020, Fig. 9). Furthermore, Liu et al. (2021) (Fig. 4a, Drivers of the decadal variability of the North Ionian Gyre upper layer circulation during 1910–2010) clearly shows how oxygen minima and maxima alternate following the variability of the NIG at longer time scale.

Between 2013 and 2020, three circulation inversions occurred, influencing both the surface water inflow and the distribution of the Oxygen Minimum Layer (OML) associated with Transitional Mediterranean Water. For instance, Manca et al. (2004) and earlier studies report OML depth variations ranging from 500 to 1700 m,:

1987: OML at 1700 m (Souvermezoglou et al., 1992)

1995: OML at 1100 m (Klein et al., 1999)

1999: OML at 650 m (Manca et al., 2003)

2011: OML at 1000 m (Cardin et al., 2015)

In the text, you say that it is located between 600 and 1200, referring to Tanhua et al. (2013). It doesn’t seem to me that Tanhua et al., 2013 says the OML is located between 600 and 1200, “In the eastern basin, the OML core lies in the depth range of 500–700 m, well below the layer of maximum S occupied by the LIW”

In light of these considerations, the statement at lines 170–171 (“In this study, we will be focusing on the first two layers, as changes at greater depths are very slow over the 8-year period and barely detectable”) should be reconsidered. Variability at intermediate depths may significantly affect the driving mechanisms of oxygen dynamics.

Additionally, the sentence at line 70 (“The Levantine Basin shows spatial changes in oxygen content occurring at short, annual, and decadal time scales”) appears inconsistent with the above assumption.

3) Another aspect that needs to be clarified concerns the statement:

“we found that oxygen is laterally transported from the Ionian Sea into the basin, and from the basin towards the Aegean Sea.”

This pattern appears to be strongly influenced by what is shown in Figure 15 of Estournel et al. (2021), where water enters the Aegean through the Kasos–Karpathos straits, exits through the Kythira and Antikythira passages, and, according to your schematic, re-enters the Levantine Basin. This circulation scheme seems rather unusual: it would imply that water does not flow outward from the Levantine Basin but instead recirculates continuously through its northern part (see Malanotte-Rizzoli et al., 1999). 

It is well established that the Levantine Intermediate Water (LIW) flows east-to-west (as you correctly mention at line 50). In terms of oxygen dynamics, this reflects a net wintertime atmospheric uptake associated with the formation of intermediate water that subsequently exits the Levantine Basin (zonal thermohaline circulation). In your conclusion, however, the oxygen transport is directed toward the Levantine Basin, which needs to be further explained and justified. 

For reference, Taillandier et al. (2022), a key experimental study that clearly describes the circulation pattern during part of your study period, reported a particular circulation between 2018 and 2019, when most of the LIW was formed in the Cretan Basin. To what extent does this anomalous LIW formation affect your diagnosed drivers and the oxygen budget?

4) In the conclusions, the authors state that a longer simulation period and a larger domain would be desirable. This raises the question of why the Levantine Basin was treated separately, instead of analyzing the same spatial domain as Estournel et al. (2021). The Cretan Passage is a wide and dynamically active area where mesoscale structures strongly influence water transport, and excluding it may limit the representativeness of the results.

Another point that deserves clarification is the choice of the simulation period. Why was only a 7-year period analyzed? Such a short time span may not adequately capture the full range of variability associated with the oxygen budget, which requires a longer record to be properly understood, for instance, including the EMT and post-EMT periods. These are mentioned in the text but not further discussed.

5) As a suggestion, since the paper aims to explain the drivers and the oxygen budget, it would be valuable to complement the modeling results with additional biogeochemical datasets. For example, the free Copernicus biogeochemical reanalysis and observational data (including BGC-Argo) could be used to estimate the oxygen budget from independent sources. Both CMEMS and Argo data are publicly available, and several field campaigns have already provided supporting measurements. In particular, Argo oxygen profiles could be used not only for model validation but also to estimate the budget directly, possibly through binning or averaging approaches. During your study period, approximately 13000 Argo oxygen profiles are available in the area of interest. Ship-based data could also be considered, for example, as highlighted in the final conclusions of D’Ortenzio et al. (2021): “An unprecedented BGC-Argo observation system was implemented in the Levantine area of the Mediterranean Sea in 2018–2019. It was supported by an equivalent and concomitant ship-based effort (three seasonal surveys from May 2018 to March 2019) to elucidate the impact of physical forcing on the biogeochemical dynamics of the basin.”

If another author were to reproduce the oxygen budget using the Copernicus biogeochemical model or observational data following your approach, the results would likely differ, affecting the interpretation of the underlying mechanisms. Incorporating multiple datasets may require additional effort, but it would strengthen your estimates and make the analysis more consistent with the study’s stated objectives and title.

Specific technical comments

6) Another aspect that should be clarified concerns oxygen solubility and seasonal variability. Beyond this, I would also recommend showing surface oxygen saturation (%) in the figures, as it would help interpret the observed patterns more effectively. It is expected to observe undersaturation during winter and oversaturation during summer, primarily due to temperature variations: as temperature changes rapidly, oxygen solubility adjusts more slowly, preventing immediate re-equilibration. This process is clearly discussed in Ulses et al. (2021), where the authors attribute it to temperature-driven solubility effects. In contrast, in your manuscript (lines 502–505), the phenomenon is mainly associated with vertical mixing with underlying waters. I am not suggesting that this explanation is incorrect, but as currently written, it seems to imply that mixing is the sole mechanism responsible for these variations.

7) A similar clarification applies to the Subsurface Oxygen Maximum (SOM). Oxygen tends to remain trapped within this layer because a density barrier develops during summer stratification, preventing outgassing. This oxygen is later reintroduced into the surface layers during autumn mixing. This mechanism is, however, inconsistent with your statement that:

“During the stratified period, primary production in the surface layer leads to oxygen oversaturation and subsequent outgassing, with a maximum oversaturation of 0.6% observed in summer.” The apparent contradiction between the expected seasonal trapping and release of oxygen and the interpretation provided in the manuscript should be addressed and discussed in more detail. Perhaps the vertical layer subdivision used in the analysis should be reconsidered to better capture these seasonal processes (e.g. differences between SOM and surface layer).

8) Another important aspect concerns the use of linear correlations to assess the impact of physical and biogeochemical drivers. It is important to recognize that when two variables share a strong seasonal cycle, their correlation will inevitably appear high, regardless of whether a true causal relationship exists. Moreover, if the variables are not independent, correlation coefficients can be artificially inflated. For instance, in your Figure 2 (which also uses the same float data as in Habibi et al., 2023), you compare modeled and observed surface oxygen and solubility. Since both variables are primarily driven by temperature and thus follow a strong seasonal pattern, a simple regression analysis will necessarily yield high correlations. The same limitation applies to the comparison with Argo data (i.e. Figure 2), which remains difficult to interpret in its current form. As a result, such analyses often provide only a static and potentially misleading view of the relationships between variables. A more robust approach would involve Empirical Orthogonal Function (EOF) analysis to explore the variability associated with different drivers. This method has been successfully applied in Di Biagio et al. (2022), where the authors decomposed the variability of oxygen and related parameters into dominant spatial and temporal modes, and subsequently correlated these modes with environmental drivers. EOFs allow one to isolate the main patterns of variability and to assess their temporal evolution, providing a more dynamic understanding of the underlying mechanisms. 

Applying EOF analysis would enable you to correlate the principal modes of oxygen variability with specific physical and biogeochemical drivers, leading to more robust and physically meaningful correlations (see Korres et al., 2000; Lionello, P., & Sanna, A. 2005, Pisacane et al., 2006 Alvera-Azcárate et al., 2007; Skliris et al.,2012; Escudier et al., 2021, Menna et al.,2022 ; Di Biagio et al., 2022; and…). Using this type of metric would strengthen your results, as it better captures the underlying variability and allows its evolution to be evaluated over time.

Minor comments / Formal aspects

9) From a structural point of view, the manuscript would benefit from substantial streamlining and reorganization. At present, there are too many figures, several of which are not clearly legible, and the amount of text accompanying them appears disproportionately small. Your main Results section spans from line 273 to 455, yet there are 52 lines occupied by captions and subheadings. This leaves approximately 130 lines of text for nine figures in the main text and seven in the supplementary material, an evident imbalance. 

Overall, the text is somewhat fragmented and hard to follow, partly due to an excessive subdivision into subsections. Additionally, in several cases, the chosen color scales make interpretation difficult.

10) The section describing the model setup is overly long. As already highlighted in the manuscript, this model has been validated in numerous previous studies across the Mediterranean; therefore, there is no need to restate these findings. I would suggest condensing everything between lines 185 and 273 into a brief summary of just a few sentences. Furthermore, considering your main scientific goal, to identify and analyze the driver mechanisms, the model comparison should not be treated as a result per se. Instead, it represents a methodological validation step that supports the credibility of your subsequent model-based analyses and process interpretations.

11) The Discussion section currently lacks depth and does not adequately address or interpret the defined driver mechanisms; in fact, these mechanisms are not clearly introduced in the Introduction.

12) Regarding references, this section requires careful revision. For example, when you state:

“underlying intermediate layer from 150 to 400 m where LIW flows, and the deep layer below 400 m (Estournel et al., 2021).”

This is a modeling reference, which is perfectly valid, but it may not be the most appropriate justification for defining layer boundaries. You could instead complement it with observational or climatological references (for instance, from the SeaDataNet Mediterranean Temperature and Salinity climatology). Alternatively, you could justify your choice explicitly by stating that: “The vertical layers were defined according to the thermohaline structure identified by the physical model.”

Additionally, several recent and relevant studies for the basin are missing. For example, Pirro et al. (2024) highlights the strong coupling between Ionian surface circulation and mesoscale structures in the Levantine Basin; Velaoras et al. (2017) discusses dense water formation events in the Cretan area. More recent biogeochemical process studies should be considered, as they rely on improved datasets compared to older works.

You might also consider adopting the standardized acronyms proposed in Schroeder et al. (2024) for the Mediterranean Sea, which would help maintain consistency with current literature.

Specific comment

Abstract

Line 1 – It’s generally better to avoid expressions such as “for the first time.” They don’t add much value, especially considering that several studies have already addressed oxygen dynamics in this area — we’re not exactly at Nielsen’s times anymore.

Lines 27–29 – This statement seems to contradict the classic pattern of the Mediterranean zonal circulation.

Lines 30–31 – The concept expressed here appears inconsistent with what you mention in lines 25–26. Clearly, both processes occur during the year, but this needs to be rewritten considering seasonality.

Introduction

Overall, the introduction doesn’t follow a clear informational structure that moves from a general introduction to the specific context of your study. Instead, it shifts somewhat abruptly between topics. You don’t necessarily need to follow a rigid scheme, but it’s important to avoid repetition and ensure a smooth, logical flow of ideas.

Lines 36–40 – There’s a lack of key references in this section, particularly regarding how oxygen influences biogeochemical cycles and the main drivers of oxygenation. The latter point should be expanded with recent literature (e.g. review articles) to help readers understand the mechanisms at play, listing the drivers alone isn’t sufficient.

Lines 41–48 – This part feels too long and lacks recent references.

Lines 49–50 – Why are the study objectives presented before the section on the Mediterranean context?

Lines 51–62 – This section is rather brief and also lacks up-to-date references (for instance, I don’t see why the work by Taillandier et al., 2022…). More importantly, it omits a crucial aspect when discussing the Eastern Mediterranean, the decadal variability of the NIG, which you mention later in the conclusions and should introduce earlier, and discuss it in the Discussion section.

Line 67 – “The vertical distribution…” – what exactly do you mean here? It seems you’re referring to the first ~100 m of the water column, but this should be clarified or rewritten for precision.

Lines 68–71 – You mention that during summer stratification there is a supersaturated surface layer and the SOM, and this two are related to processes such as biological production (which makes sense) and subduction. Are you sure the surface supersaturation is not instead driven mainly by temperature-related changes in solubility?

Lines 72–73 – Could you clarify what you mean by “related to the atmosphere”?

Lines 74–75 – The oxygen minimum in the Levantine Basin oscillates in phase with the NIG rotation.

Line 78 – As written, this statement sounds speculative. However, if you explain it and link it to NIG variability, the point would become much stronger and more meaningful.

Material and Methods

In my opinion, it’s not necessary to re-explain concepts that have already been well described in previous studies.

Section 2.1.3 – I don’t see why the study area needs to be reintroduced here if it has already been described in the introduction, and also why it’s presented together with the budget section.

Suggestions for improving the manuscript

To enhance the clarity, impact, and scientific robustness of the manuscript, I suggest the following:

o    Reduce the number of figures and ensure that each figure is clear, legible, and directly supports the main results.

o    Incorporate Empirical Orthogonal Functions (EOFs) to decompose the variability in dissolved oxygen and associated parameters.

o    Plot the leading EOF modes and relate them to specific physical and biogeochemical drivers.

o    Include a dedicated subsection discussing the influence of mesoscale features (e.g., cyclones, anticyclones, gyres) on oxygen dynamics. Explore how these structures modulate oxygen variability at short timescales and intermediate layers, providing a more complete view of the system beyond long-term averages also here you can use the EOF analysis.

o    Evaluate the difference related to the NIG variability.

o    Where possible, complement model results with available observational datasets, such as Argo floats, ship-based surveys, and CMEMS biogeochemical products.

o    Clearly define the driver mechanisms in the Introduction.

o    Focus discussion on the interpretation of results in terms of these drivers, rather than reiterating model validation details that are already established in the literature.

o    Consider reorganizing the Results and Discussion sections to highlight the relationship between observed/modelled oxygen variability and the identified drivers, including a quantitative assessment where feasible.

Overall, these improvements will enhance the readability, scientific rigor, and interpretative power of the manuscript, providing a clearer link between oxygen dynamics and the underlying physical and biogeochemical processes.

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