See the review in the attachment

This manuscript presents a large-sample, pan-European analysis of streamflow elasticities to precipitation and sensitivities to temperature, including mean and extreme flows. The dataset is impressive in scope, and the topic is timely and relevant for understanding hydroclimatic variability and change across Europe. The spatial patterns identified are interesting and potentially valuable for both science and water management.

However, in its current form, the manuscript suffers from some conceptual, methodological, and presentation weaknesses that limit the robustness and interpretability of the conclusions. In particular, issues arise regarding (i) the definition and interpretation of “resilience”, (ii) statistical robustness of regression and Random Forest analyses, (iii) insufficient data description, and (iv) weak integration between the main text and the Supplementary Material. Addressing these issues would substantially strengthen the paper.

I have reported below the major and minor comments the authors could consider to improve the manuscript:

1. The manuscript interprets elasticities of annual maximum flows to mean annual precipitation as a measure of resilience to extreme flows (Section 3.2 and Figure 5). While the figure is informative and the spatial patterns are interesting, this interpretation is conceptually problematic.

Annual maximum flows are typically generated by event-scale precipitation (sub-daily to multi-day), whereas mean annual precipitation reflects a yearly integrated climatic state. Consequently, the elasticity metric used here does not directly represent resilience to extreme precipitation events, but rather the sensitivity of flood magnitudes to interannual hydroclimatic wetness and antecedent catchment conditions.

This interpretation is, in fact, supported by the Supplementary Material. There, the authors test two hypotheses to explain the similarity between elasticities of mean and maximum flows: (1) a correlation between mean and maximum precipitation, and (2) the control of antecedent wetness and landscape state on flood response. Their analysis (Figure S4) shows that the correlation between mean and maximum precipitation is weak and spatially scattered at the European scale, suggesting that hypothesis (2) dominates. This indicates that the derived elasticities primarily reflect state-dependent flood amplification rather than resilience to event-scale extreme precipitation.

While the metric itself is not meaningless, the terminology “resilience to extreme flows” risks overstating what is actually quantified. I therefore recommend explicitly acknowledging the time-scale mismatch, aligning the main-text interpretation more closely with the Supplementary findings, and softening or rephrasing the resilience terminology accordingly.

In addition, the use of mean annual precipitation derived from gridded datasets such as E-OBS introduces further uncertainty, particularly in southern Europe, where station density is very low and precipitation extremes are known to be less reliably represented (see here: https://climatedataguide.ucar.edu/climate-data/e-obs-high-resolution-gridded-meanmaxmin-temperature-precipitation-and-sea-level). This adds another layer of uncertainty when relating annual precipitation metrics to extreme flows in these regions.

2. The use of a multiple linear regression framework to estimate elasticities and temperature sensitivities is appropriate. However, statistical significance in such models must be assessed at the parameter level, not merely at the level of model fit.

This is especially relevant for the temperature coefficient, which explains a very small fraction of variance (R² ≈ 0.03 when used alone). As far as I understood, while the authors state that parameter-level p-values are used, the manuscript does not clearly show how often temperature coefficients are statistically significant, nor this is clear from the figures and whether inclusion of temperature significantly improves the model relative to precipitation-only models.

Without this information, temperature sensitivities risk being over-interpreted. I suggest, to explicitly report the fraction of catchments with statistically significant temperature coefficients, and clarify the added explanatory value of temperature relative to precipitation-only regressions.

3. The Random Forest analysis is used to infer which catchment characteristics “shape” elasticities. However, several methodological aspects are insufficiently documented or justified:

• The paper does not clearly present training vs. testing performance, nor any assessment of robustness across multiple splits or cross-validation.
• Reported R² values (≈0.30–0.51) indicate that a substantial fraction of variability remains unexplained, which is understandable but limits interpretability.
• Feature importance is derived from impurity-based metrics, which are known to be biased in the presence of correlated predictors, a major issue given the strong interdependence among climate, soil, and landscape variables. While predictor independence is not required for RF prediction, it strongly affects feature importance interpretation, which here is framed in physical terms. In this respect, I suggest to clarify that random forest results should be interpreted as associative rather than causal, discuss limitations of impurity-based importance under collinearity, and provide clearer information on model validation and robustness.

4. The manuscript relies on numerous datasets (streamflow, precipitation, temperature, catchment attributes, human influence metrics), many of which are introduced with minimal or no description. Key information is often missing, including:

• Histograms with area of the basins.
• data sources and spatial resolution for climate variables,
• temporal aggregation and handling of missing data,
• spatial aggregation and handling of small catchment precipitation representativenss vs precipitation and temperature spatial resolutions.
• whether predictors are static or time-varying,
• uncertainty and limitations of human influence datasets.

I think that referring readers to EStreams alone is not sufficient, given the interpretive nature of the study. Adding a concise but explicit data description section or table summarizing sources, resolution, temporal coverage, and key preprocessing steps would clarify better the paper and its potential effect. Also, consider adding potential limitations of the datasets. 

5. Several essential analyses (regression diagnostics, correlation structures, robustness checks, RF diagnostics) are relegated to the Supplementary Material, but their implications are not consistently summarized or integrated into the main text. Conversely, some sections of the main text are overly long and repetitive. I think that this creates a disconnection that makes it difficult for readers to fully evaluate the robustness of the results without repeatedly consulting the Supplement.

Minor comments

• Environmental zones are introduced without prior definition.
• Chiew et al. 2006 are not properly defined. Please add a and b as one study refers to Australia and one is global.
• Lines 50-52. Can you be more precise with “narrow climate change” here?
• The distinction between statistically significant and insignificant elasticities is visually unclear in several figures.
• Lines 273–275: Additional recent literature could be acknowledged, including Nanda et al. (2023),
  
  https://journals.ametsoc.org/view/journals/hydr/26/7/JHM-D-24-0143.1.pdf
• Line 298: See also Massari et al. (2024) for a more recent contribution:
  
  https://www.sciencedirect.com/science/article/pii/S002216942300954X.
• Lines 350-353. Possible effect of soil crusting?
• Line 405. “The most”?
• The manuscript is considerably longer than typical journal standards and could be substantially shortened without loss of scientific content.