This study is an important example of analysis of oceanic carbonate systems based on observation data from the western Mediterranean Sea, and the measurement methods and data processing are generally appropriate. However, the structure of the Discussion and Conclusion is poor, and it is very difficult to understand the novelty that should be claimed in this paper. The authors should significantly revise the structure of the Discussion and Conclusion to clarify the appeal points of this paper to the readers.

Major comments

Most description in the Discussion and Conclusions are repetitions of the Result. For example, Chapters 4.1 and 4.2 are unnecessary and should be deleted. The current description that merely lists data is redundant, and make it difficult to understand new findings that should be claimed in the paper. The structure of these sections should be substantially revised by deleting unnecessary descriptions.

The multivariable Taylor expansion is performed in Equation (6), but in this paper, TA is calculated as a linear equation of salinity, so there should be very strong multicollinearity between SSS and TA. Therefore, I am very suspicious of the results of this equation. We have to clear the problem of multicollinearity by removing one of the variables or by using methods to avoid multicollinearity (e.g., PLS regression).

I would also like to know how SSS and TA, which are less accurate in Equation (10), affect the results of the Taylor expansion. The author should calculate the error and clarify whether the Taylor expansion results are significant or not.

The discrete description of the study area is difficult to understand for those who are not familiar with this area. Thus, a "Study area" or similarly named subchapter should be added in Chapter 2 to describe the contents at Line 56-124, the hydrographical conditions, and previous studies of carbonate observations.

Line 287 Since river water does not reach zero alkalinity even with zero salinity (see Friis et al., 2003), the effect of river cannot be excluded with this method.

Minor comments

Line 56 Abbreviations that appears for the first time in the maintext should be explained in the maintext.

Line 187 Is the error in the instrument itself or is it due to the temperature difference between the ocean and the intake?

Line 226 One extra comma.

Line 295 What is different between S and SSS?

Line 318 The first paragraph of this chapter should be moved to the beginning of chapter 2.3. Also, if equation (10) is being applied to the data used in equations (6)-(9), it should be listed before those equations.

Line 399 Is this mean that the 11 points were determined by the seasonal variation of related parameters? If so this section should be moved to the second paragraph of the Result.

Line 557 The description about the SST reanalysis data should be moved to the Material and Method.

Line 657 The description should be moved to the Material and Method, or the Result.

Figure 2 It would be better to make the fCO2 and pH graph in Fig. 2 the Supplementary and nCT and nAT in the maintext.

General comment

The topic is interesting, and the authors have worked a lot on several aspects of the marine carbonate systems and air – sea CO₂ fluxes in the study area. The methodologies and analysis follow robust techniques which help to support the results and discussion. The analysis of the trends shows how significant the observed trends are however a 6-year period is rather short and an inherent limitation. This is acknowledged by the authors and the high statistical significance is a good indicator of the validity of the assumptions. The authors do compare some of their findings (e.g. SST trends) to others, however, the comparison has limitations as they are made against datasets/products that cover the entire Mediterranean Sea and in some cases areas that are in the Atlantic (the ESTOC site is not very far but still the physical characteristics should be distinctively different). Since the main finding of this work is the strong relationship between SST increase and subsequent changes in CO2 fluxes and MCS, a more concise SST trends analysis will help the document.

The authors haven’t investigated any other data sources that can be used as quality control for their data and/or gap filling. As an example, a simple search in SOCAT shows that there are 90 datasets in the area from 2010 until 2023 and 27 datasets from 2019 – 2023.

The use of English is average, and in some cases it’s difficult to follow sentences. There are numerous cases where grammar, syntax, words, entire sentences and small sections need to be edited/changed.

There are good elements in this work which are worth publishing. Reducing the size and trying to focus on a specific question (e.g. CO2 fluxes, with only the minimum input of MCS or vice versa) improving the use of English and reducing the size will also help. A lot of work is done but still some work is needed to refine the document.

Specific comments on sections

Abstract

Line 16: The 45-83% referring to the fCO2 or the SST? As “fluctuation”, do you mean variability? If there’s an offset, then what’s the final seasonal magnitude? A bit confusing.

The statement in the abstract that the CO2 sink has reduced 40-80% since 2019, is strong, however 40 – 80 % is a very large margin and it will be more concise if there is a (very) brief explanation for this margin.

Introduction

In line 63 it is mentioned that the NW Med is a relatively weak sink for atm CO₂, while in line 70 it is mentioned that the same area has a strong atm CO₂ uptake. A bit confusing.

Line 105: what does exitance mean? Is it exit, is it existence?

Line 126: The sentence “an alternatively …” doesn’t make sense. Why is the methodology alternative? It’s robust and powerful but alternative to what?

Line 140: Improve our knowledge of what?

Methods

Minor comment: Can the authors clarify whether the VOS is operating under the WMO / GOOS network? The term SOOP in the document is for Surface Ocean Observation Platform, yet in ICOS this is defined as a Ship Of Opportunity? Acronyms are very confusing and might be necessary to use established ones.

Line 167: What is defined as “low atmosphere”? How high was the intake.

What is the actual performance of the NDIR on the 2 modes (seawater and atmospheric)?

Have you compared the fCO_2,ATM  with any gridded products or from different sources/stations (e.g. ATM station nearby, satellite products, Jena Carboscope, NOAA OCADS,…). Differences are to be expected but since other studies are using this data it might be useful to explain and justify the data used in this study. The work on fluxes requires this level of scrutiny.

Line 196: It will be informative if the “difference in the order of millibars” is better defined as this can be a crucial source of error for the final fCO₂.

It’s not clear where the A_T and C_T data from the discrete seawater samples are used. I suspect that the A_T discrete water samples were used to produce equation 1, but where are the C_T discrete water samples used? Are they used in Fig 2(?) and or Fig Sup 4? Are they used to “check” the calculated C_T?

Line 227: C_T is not determined via titration but usually by adding acid and stripping the CO2 from the sample and measuring the amount stripped in a coulometer or CO2 detector.

Line 237: The reported error of 17.1 umol/kg is very large and limits the use of A_T as a parameter for calculating other parameters in the carbonate system (check this documented by T. Steinhoff; Uncertainty analysis for calculations of the marine carbonate system for ICOS-Oceans stations; doi: 10.18160/vb7c-z758).

Line 277: The term ΔfCO₂ is introduced but without explanation. I suspect it’s the fCO_2,SW  - fCO_2,ATM (?)

Section 2.3.4: Following from comments on the performance of the NDIR for both modes, and since errors/uncertainties in the ΔfCO₂ term propagate and become significant, it will be beneficial if the authors elaborate on how the flux errors have been calculated.

Line 331: Is this

Results

Line 358: Sentence starting from “Based on differences…” is confusing and difficult to follow. Please rephrase. Also what are the hydrodynamical processes and oceanographic features?

Fig 3: Will be useful if the authors elaborate more on the poor fit of fCO2 in S1 and for pH in all regions.

Both Fig 3 and 4 are crowded (especially the fCO2 plots that have many elements). Maybe show fco2 total and have the components in the supplementary section.

Fig 7: It will be informative if you can include error bars (at least on the annual trend).

Surprised that there are no results for fluxes. They are presented in the discussion and at the same time discussed, which has its merits but makes the document inconsistent.

Table 1 and 2: is the term “Ratio ^oC yr^-1” the trend? If so why not call it “Trend”?

Discussion

Line 581: The 2000-2019 warming is 0.1 and 0.06 ^oC/yr for S and E section however in Table 1 I can see 0.03 and 0.05 respectively. Is it possible to clarify?

Line 586: “in warming.” Of what? Atmospheric warming? General increase in sea surface temperature?

Line 589 - 594: Skeptical on the validity of this comparison. Basically you are comparing a local 5 year trend against a global and 2 decades product.

Line 758: What does “isolated eventual improved injections” mean? Where do these waters come from?

Line 761: Very surprised and confusing to start with “The Eastern Boundary of the Med Sea…”. Is this a typo? Is this the eastern part of the study area? Please clarify/correct.

Line 861: The use of different units for the flux is confusing. For example, in line 849 the unit is mol/(m²yr) and in is TgCO₂/yr.

Can’t understand which finding contributed to the assessment made in 2005 by Borges and 2013 by Chen? If these values are from the 2005 and 2013 studies are they still valid ?

Conclusion

The section is relatively long and will be beneficial if it’s shortened. Especially since parts of this section fit better in the discussion.

The part starting in line 896 repeats what is mentioned in line 872.

Line 934: The sentence starting “This research…” doesn’t make sense.