The manuscript presents results from developing and analyzing a high resolution hindcast of total water levels for Europe. The authors address the important topic of including wave contributions into TWL calculations and subsequent flood impact/risk analysis. They use different approaches to derive wave setup estimates and quantify the effect of the methodological choice on the resulting flood extent. They also test the effect of using different thresholds in the extreme value analysis that is applied to derive the 100-year TWL levels, which are then used for the static flood mapping. The manuscript is very well written and I commend the authors for the comprehensive analysis. I have few general comments and some minor ones listed below which I believe should be addressed to further improve the quality of the paper.

General comments:

1. The authors emphasize that their new hindcast has an unprecedented spatial resolution of 1km. This is great! However, it is never shown how going from a coarser resolution (for which other hindcasts already exist) to a finer resolution affects the flood hazard assessment, does it make any difference whether I use 1km or 10km or 25km? Personally, I would find this a more interesting sensitivity analysis than, for example, the sampling in the POT approach (which has been done in previous studies for different locations).
2. The authors go into a lot of detail about different EVA methods, specifically the choice of distribution and threshold selection, but pass over other relevant aspects quickly such as the declustering window to derive independent events; they use a constant value following other studies (but no references are provided); that’s also an assumption (e.g., https://doi.org/10.1016/j.wace.2024.100701) with potential impact (as shown in the Arns et al., 2023 study).
3. Overall, the paper is very long, especially introduction and discussion (but then there are no conclusions). The intro, for example, includes a lot of textbook style information about extreme value analysis, while the discussion repeats some info that is already touched on in the results section. I don’t mind reading a longer paper, but the large amount of (sometimes tangential) information distracts a bit from what I think is the biggest novelty, namely the effect of using different approaches to account for wave contributions. I think with some additional effort it can become more concise while highlighting the key novelties and related conclusions.

Specific comments:

31 river discharge effects are not included, something worth mentioning somewhere, maybe when discussion limtations

75-105 This part includes a lot of basic information that can be found in text books. At the same time it doesn’t touch on more recent developments in extreme value modelling (for example, the approach proposed by Calafat and Marcos: https://www.pnas.org/doi/10.1073/pnas.1913049117, or approaches where distributions are fitted to the stochastic components of TWL after removing deterministic tides).

157-159 something is wrong with this sentence

166 “global median beach slopes reported locally” sounds very strange and I am not sure what it is supposed to mean

205-210 I got very confused here because the same numbering style is used for the list and the equations; I suggest switching to i, ii, iii or a, b, c for the list and keep (1) (2) style for the equations

215 Refer to table 1 when mentioning approach A. I was wondering what it is and only realized on the next page.

235 “two extreme events per year”

242 “reconstructed…hindcast”; I would drop one

277 “Elbe Estuary”

310-315 (and other places) When the tides are the main driver, does it make sense to fit an extreme value distribution because its assumptions are not met? I know it’s a commonly used approach, but that doesn’t make it necessarily right.

348 delete “the”

Figure 7 (and related text) How does it look when no wave contributions are included (which is still often the approach used for large-scale assessments)

392-403 This and other parts of the results section read more like Discussion.

492 delete “an”

506 “applying a specially variable” (or “thresholds”)

Supp. Fig. 8 “significancy” should be “significance” in the title

In this paper, titled “Assessing extreme total water levels across Europe for large-scale coastal flood analysis”, the authors present a modelling chain for computing high-resolution extreme sea levels along the European coast. I believe this manuscript may be of interest to NHESS readers; however, I do not recommend it for publication in its current form. Several aspects, mainly related to the manuscript structure, methodology, and model validation, need to be improved. I recommend resubmission, subject to the authors addressing the main specific comments outlined below:

1. Manuscript structure. This study is based on the results of a model chain. Therefore, in my opinion, a detailed description of the modelling system and its validation must be included in the main manuscript rather than relegated to the supplementary material. A Conclusions section is missing.

2. Modelling system. The total water level is computed by linearly summing tidal, storm surge, and wave contributions. These three components are simulated using different numerical models, each with distinct domains, resolutions, and bathymetry. This could lead to inconsistencies at the selected coastal locations, and this issue must be discussed in the manuscript. Furthermore, the supplementary material indicates that the ROMS model is used to simulate sea levels induced by tidal and meteorological forcing. This approach captures the non-linear interactions between tides and storm surges (i.e., tidal fluctuations affecting storm surges and vice versa). It is therefore unclear why the authors de-tided the ROMS sea levels and used only the residual component to estimate the still water level. Is ROMS less accurate than TXPO9 in reproducing tidal dynamics? The authors must justify this choice and provide evidence that the selected approach yields the best results. Moreover, the coarse resolution of the ROMS model (5-11 km as stated in line 144) is a limiting factor in the reconstruction of the TWL at a 1 km resolution. Since the model results are extracted at the coast, the authors should specify the minimum bathymetric values used in the grids of the different models.

3. Tide-surge-wave non-linear interactions. According to Arn et al. (2020; https://doi.org/10.1038/s41467-020-15752-5), tide-surge non-linear interactions are relevant in several European locations. However, in line 120, the authors state that they reconstruct TWL by “linear summing time series of wave setup, storm surges, and astronomical tides”. This suggests that non-linear interactions among tides, surges, and waves are not explicitly accounted for in the TWL reconstruction. Nevertheless, the supplementary material indicates that the ROMS model is used to simulate sea levels induced by tidal and meteorological forcing, which is intended to capture non-linear interactions between tides and storm surges (see my comment 2). It is therefore unclear which specific non-linear processes are considered in this study and how they are incorporated into the overall analysis.

4. Wave contribution to sea level. A critical aspect of computing total water levels at the coast is evaluating the wave contribution (wave setup and run-up). I commend the authors for their thorough sensitivity analysis of the wave contribution formulation. However, the approach adopted in this study uses a foreshore slope parameter derived from modelled wave properties rather than actual coastal characteristics. The authors should validate their slope estimation using literature data or values from topo-bathymetric datasets (e.g., EMODNET). Additionally, site-specific geomorphological features must be considered. For example, gravel beaches and rocky cliffs - common in many Mediterranean coastal locations - require different methodologies for estimating wave run-up. Ignoring coastal characteristics could lead to unrealistic wave setup estimations, resulting in erroneous evaluations of the relative wave contribution to total water levels, both locally and at regional or basin scales.

5. Model validation. The supplementary material presents an incomplete validation of the numerical models used. I strongly suggest improving this section as outlined below and including the main validation results in the manuscript.

• • Tidal model. It is stated “Comparison of the tide simulated from the TPX09v5 outputs and measured by the tide gauges shows a near-perfect agreement, indicating a good non-stationary reconstruction of both tidal amplitudes and phases”. However, no statistical metrics are provided. Are the tidal water levels or the tidal amplitudes and phases being evaluated? Why is the term 'non-stationary reconstruction' used? How is non-stationarity assessed? The authors must provide a comprehensive validation of the tidal model.
  • Storm surge model. See my comment 2. A correlation coefficient between model results and observations should be provided, along with RMSE and BIAS. What are the reference datums of the tide gauges and the storm surge model used to compute BIAS?
  • Wave models. The statistical metrics for both the offshore and the nearshore datasets must be provided.
  • TWL reconstruction. The authors validated the TWL reconstruction by comparing the estimated values against previously observed historical storms across the study area, based on previous studies (the list of which is reported in the supplementary material). It is not clear at all how this validation was performed. Did the authors consider only the maximum values during specific storm events? If so, the date of the events must be provided as well. Were the values taken directly from the publications or from tide gauge databases? My main concern regarding the TWL validation is the assumption that the observations account for the wave contribution to the sea level. However, several tide gauges (Catania, Venice, Marina di Campo, Santander and others) are located in protected harbours or behind jetties, and therefore are not exposed to wave action. It appears that the addition of the wave setup contribution merely compensates for an underestimation of the still water level. In conclusion, these observations cannot be used, and a proper TWL validation is missing.

My additional minor suggestions for ameliorating the manuscript are listed here:

• Line 8: … the primary driver of coastal flooding.
• Lines 15-17: Please reformulate these sentences. It is not the Atlantic coast affected by the wave dataset, but the TWL estimation along the Atlantic coast that is affected by the wave dataset. And so on.
• Line 18: “no regions have extreme events dominated by wave setup”. Maybe this is a problem of the adopted approach, which is not able to properly assess the wave setup contribution.
• Line 154: Why do you use the nearest grid point instead of using an interpolation method?
• Line 176: You should justify the use of a 72h time interval for separating different extreme events.
• Lines 201-203: the flood model must be described together with the modelling systems.
• I suggest merging sections 2.6.1 and 2.6.2 and creating a table listing all TWL reconstruction approaches.
• Equations 5 to 7 should be moved to section 2.3.
• Line 244: The location of the test points should be shown in the manuscript and not in the supplementary material.
• Line 246: More details on the clustering techniques must be provided.
• Figure 3 and lines 267-272: I suggest removing panel (e) and the mentioned lines since there is no reason to mix the different approaches.
• Line 293: More details on ice modelling must be provided.
• Lines 352-353: It is not clear what the authors meant by "average conditions." Which supplementary material should provide insights into this?
• Figure 6: Tide, Storm surge and Wave setup should also be reported in panels g, h and i.
• Figure 9: Doesn't the POT threshold with λ = 1 equal the Annual Maxima (AM) method?
• Lines 499-509: These sentences summarise the results and would be more appropriately placed in the Conclusions section rather than in the Discussion.
• Lines 524-525: This sentence is not clear. Please reformulate it.
• Line 540: 111 km resolution?