I have read the manuscript “Decadal variability in the Eastern and Western Mediterranean sea level trends” by Borile et al., submitted for publication to State Of The Planet. The authors compute decadal (10-year) sliding sea-level trends over 1998-2024 in the Mediterranean Sea using satellite altimetry and tide gauge observations. They also use temperature and salinity data from reanalyses to estimate the relative thermosteric and halosteric contributions to these trends. The results show substantial fluctuations in decadal sea-level trends, both at the basin scale and at coastal locations. These fluctuations can be quite different from one coastal location to another. The authors also find that the thermosteric and halosteric components often compensate each other, though not always. The agreement between tide-gauge and altimetry trends is an interesting finding.

While the fluctuations in decadal sea-level trends reported here are real, they are not, by themselves, a novel scientific finding. They are perfectly expected and have been documented before. In my view, the main novelty of this work lies in presenting updated estimates of these decadal sea-level changes and their steric contributions, although the latter are only analysed at the sub-basin scale.

My overall impression is that this study has the potential to be suitable for publication in State Of The Planet as it addresses a timely and relevant topic. However, the manuscript needs significant further work to better justify its motivation, provide clearer detail on the methods and data processing, and, especially, clarify the interpretation and implications of the findings.

I recommend publication after major revisions to address the concerns and comments outlined below.

Best regards,

Francisco Calafat, UIB

General comments

One of my main concerns is that the variations in 10-year trends appear to be interpreted as reflecting changes in the rate of climate-change-driven sea-level rise. For instance, the manuscript includes statements such as: (line 16) “this study investigates the decadal variability of sea level rise”, (line 20) “in the WMED, sea level rise has recently accelerated”, (line 222) “the results confirm that sea level rise in the Mediterranean is not a linear process”. This interpretation is misleading because decadal trends primarily reflect internal climate variability (NAO, regional wind changes, etc.) and would still occur in the absence of anthropogenic forcing. I would recommend that the authors reword the relevant parts of the manuscript to make this distinction clear and adjust the interpretation of the results accordingly.

The point raised in the preceding comment is important, as it directly affects the relevance of the results for adaptation planning. In this regard, the manuscript appears to overstate the implications of the variations in the 10-year trends for coastal adaptation. The authors suggest that these variations should be considered when defining adaptation strategies. I agree but would like to emphasize that these variations have always existed (similar variations would be found in pre-industrial records) and they are already implicitly accounted for in planning practice through design levels and allowances. The need for adaptation arises because mean sea level is moving outside the historical range of variability due to anthropogenic climate change, reducing the safety margins that were previously sufficient. I would like the authors to consider this distinction and adjust the discussion accordingly.

Data processing. Both the satC3S and satCMEMS altimetry products are usually provided with the barotropic effects of atmospheric pressure and wind changes removed (the so-called dynamic atmospheric correction). For time scales longer than about 20 days, this correction is equivalent to removing the inverse barometer (IB) effect. The authors do not appear to have applied the same correction to the tide gauge data, which makes the trend comparison between altimetry and tide gauges inconsistent. Atmospheric pressure variations can produce significant long-term sea-level trends in the Mediterranean (Gomis et al., 2008; Calafat et al., 2022). Therefore, I would recommend adjusting the tide gauge records for IB effects (or adding IB effects back to the altimetry data).

Uncertainty estimation. The authors compute trends using the Theil–Sen estimator after deseasoning and low-pass filtering the sea-level time series and use bootstrapping to estimate trend uncertainty. While the trend point estimates are likely robust, further details on the bootstrapping method are needed to assess whether the reported uncertainties are reliable. Sea-level time series are intrinsically autocorrelated, and the applied low-pass filter further increases this autocorrelation. It is unclear which type of bootstrap was used; a standard “vanilla” bootstrap assumes independent observations, an assumption likely violated here. If independence is not accounted for, the uncertainty of the Theil–Sen trend will be underestimated. Could the authors clarify whether the bootstrap procedure accounted for serial correlation? If not, I would encourage them to do it.

Steric calculation (Eq. 1). Both alpha and beta vary strongly with depth (as they depend on temperature, salinity, and pressure), yet the authors seem to assume constant coefficients. Could the authors assess how this assumption affects their estimates of the thermosteric and halosteric sea level? 

Specific comments:

Lines 21-22: abstract. The authors write “… with the remaining contribution linked to changes in the sea level mass component”. However, the mass contribution to sea-level trends is not quantified in this study. I would suggest rewording this sentence to “with the remaining contribution likely due to changes in the sea-level mass component”.

Lines 26-27: “these results demonstrate that…”. The presence of decadal sea-level variability in the Mediterranean, which will manifest as variations in 10-year trends, has been documented before. I would suggest replacing “demonstrate” with “confirm” or a similar word.

Introduction. I recommend that the authors highlight more clearly the novel aspects of their study relative to previous work. In this regard, several past studies should be cited and discussed, as they are directly relevant to this topic, including Marcos et al. (2008), who also analysed 10-year sea-level trends.

Line 56. Are daily SLAs averaged into monthly anomalies?

Lines 67-68. Please provide more details on how the seasonal cycle was estimated. Did the authors use a linear or a non-linear regression model, and did they remove only the annual component or also the semi-annual cycle?

Lines 56-65. Has the GIA contribution been removed from the altimetry data? GIA affects altimetric sea surface heights without reflecting actual ocean mass/volume changes. If the goal is to quantify ocean-driven sea-level changes, including GIA could bias the trends. I therefore suggest removing it.

Lines 68-69. Please provide more details on the low-pass filter applied to the time series (type of filter, cutoff frequency, etc.).

Lines 73-74. The authors mention that “the uncertainties obtained in our analysis are higher than those reported by Prandi et al. (2021).” However, I think that this comparison is not meaningful. Prandi et al. (2021) accounted for multiple error sources in addition to statistical uncertainty, including errors from orbit determination, geophysical corrections applied to the altimetry data, inter-mission biases, and the GIA correction. It is unclear whether the authors have accounted for all these error sources. Without accounting for them, the comparison with Prandi et al. is misleading. Could the authors please clarify?

Equation (1). Please define eta_S explicitly (i.e., steric sea level).

Line 78. Please be more specific when defining alpha and beta: coefficients of thermal expansion and haline contraction.

Lines 82-83. Each RLR Tide gauge record from the PSMSL has been carefully reduced to a common datum, ensuring a consistent reference level throughout the record, which is crucial for the analysis of long-term sea-level changes. Has the same datum consistency been ensured for the tgCMEMS dataset? 

Caption Figure 3. Replace “corrected from” with “adjusted for”.

Section 3.2. Could the authors clarify why the steric contributions were not analysed at the local scale?

References

Calafat, F. M., Frederikse, T., & Horsburgh, K. (2022). The sources of sea-level changes in the Mediterranean Sea since 1960. Journal of Geophysical Research: Oceans, 127, e2022JC019061. https://doi.org/10.1029/2022JC019061.

Gomis, D., Ruiz, S., Sotillo, M. G., Álvarez-Fanjul, E., & Terradas, J. (2008). Low frequency Mediterranean Sea level variability: The contribution of atmospheric pressure and wind. Global and Planetary Change, 63 (2–3), 215–229. https://doi.org/10.1016/j.gloplacha.2008.06.005.

Marcos, M. and Tsimplis, M.N. (2008), Coastal sea level trends in Southern Europe. Geophysical Journal International, 175: 70-82. https://doi.org/10.1111/j.1365-246X.2008.03892.x.

The manuscript presents diagnostics related to sea level rise (and its partitions) and could be a valuable contribution to understanding sea level variability in the Mediterranean Sea; however, it requires a more targeted discussion to be ready for publication, in my opinion.

General comment: while there is quite good material in the manuscript, the main conclusions seem quite weak (non-linearity of sea level in the Med Sea appears to be the main point) and do not exploit the full set of information presented. I recommend reframing the conclusions to better exploit what was offered in the paper, including, for instance, trends, partition of sea level components, asymmetric behavior of thermo-halo variations between the western and eastern Med, etc.

L23, L223: the manometric sea level variability is mentioned in several places as the main basin-wide driver of sea level rise, but never discussed in detail. It should be recalled, at the very least, how much it contributes to the two basins (WMED and EMED) based on recent literature and quantitatively, and how and why it shapes the basin-averaged sea level rather than local variations.

L26: It seems like VLM is the main factor of possible disagreement between satellite altimetry and tide gauges. Further to the fact that processing might be different and needs to be discussed in more detail (e.g., how consistent are the atmospheric corrections in SLA with tide gauge data processing? How can the spatial and temporal filtering applied to SLA impact the difference between the two networks?), There may be processes at a scale that altimetry cannot resolve, and all these points need to be better discussed and addressed, with reference to the relevant literature. Sometimes it appears like altimetry is being validated against tide gauges (e.g., L155, but also elsewhere). Still, the two networks inherently bear different information due to different spatio-temporal scales spanned, and the data processing.

Equation (1): The approximation implied in using constant Tf, Sf versus spatially varying Tf, Sf seems quite crude and needs to be justified.

Section 3.1: The section will benefit from having a Table summarizing, for the WMED and EMED basins, the 1993-2024 trend (e.g., as average of the “moving trend” in the figures) and the acceleration (e.g., as slope of the “moving trend”); this would be very useful for further studies and comparisons, and can be done for the different components and data.

Also, section 3.1 appears somewhat inconclusive. I recommend the authors speculate on the reasons why WMED exhibits strong thermo/halo compensation, while EMED does not, i.e., why adiabatic processes dominate in the western MED compared to the EMED. This is an important point to discuss.

Table 2. I suggest adding a column either with the adjusted values (Absolute – VLM) or the residuals (Absolute – VLM - Relative), so that one can more easily understand when there is statistically significant consistency of the datasets or not. Detailed comments about this last point can be added as well.

Typos

L32: “broad picture”: maybe “integrated picture” or similar

L71: does not allow FOR the acceleration…

In addition to comments raised by other two reviewers, what I am missing in the manuscript is connection between large-scale circulation changes and changes in sea level decadal trends. The most prominent quasi-decadal oscillation is Adriatic-Ionian Bimodal Oscillating System (BiOS; Gačić et al., 2010, https://doi.org/10.1029/2010GL043216; Civitarese et al., 2023, https://doi.org/10.1016/j.pocean.2023.103056), which is so strong that it can be reconstructed from centennial sea level data in the Mediterranean (Meli, 2024, https://doi.org/10.1038/s41598-024-55579-4). From Meli et al. (2023) and other literature on BiOS (see Civitarese et al., 2023), it seems that BiOS is not just affecting the Ionian Sea, but is part of a greater basin-wide circulation variability that may refect in basin-wide SLA values. This topic deserves an appropriate attention and extensive discussion in the manuscript, and currently it is not mentioned et all.