The manuscript investigates how the probability distribution evolves over time under non-stationarity and how this affects the estimated return period over a given time interval. The authors argue that the classical formulation of the return period—strictly valid only under stationarity—can still be applied under nonstationary conditions when temporal variability is sufficiently weak. They also provide a closed‑form solution for the limiting behavior of the GEV parameters under simplified conditions. The idea is both scientifically valuable and relevant for practical applications. I believe that the manuscript deserves publication; however, I have some concerns regarding the presentation of the work. Although generally clear, the manuscript would benefit from a more explicit framing within the existing scientific literature to clarify how the proposed approach relates to recent developments. Moreover, the authors could provide clearer guidance on how the method can be implemented in practice. In my view, addressing these aspects would improve both the readability and the applicability of the study.

In line with my general comment, I report below some specific remarks.

Is the approach similar to that used in GAMLSS when time is adopted as an explanatory variable, or, for example, to the method of Šraj et al. (2016)? Please consider adding a brief comparison among these approaches. I also suggest commenting on the results of previous works employing similar methodologies for nonstationary GEV estimation, especially concerning the range of variability in the estimated parameters.

• Šraj, M., Viglione, A., Parajka, J., & Blöschl, G. (2016). The influence of non-stationarity in extreme hydrological events on flood frequency estimation. Hydrol. Hydromech, 64(4), 426-437.

Line 16. I assume that the process is independent in time, or, if temporal persistence is present, that the authors are referring to the marginal distribution of the process. Since non-stationarity and time persistence are distinct properties, this point should be briefly explained or at least mentioned.

Line 52. Additional relevant studies addressing nonstationary frameworks could be cited, such as Read and Vogel (2015) and Vogel and Castellarin (2017).

• Read, L. K., & Vogel, R. M. (2015). Reliability, return periods, and risk under nonstationarity. Water Resources Research, 51(8), 6381-6398.
• Vogel, R. M., & Castellarin, A. (2017). Risk, reliability, and return periods and hydrologic design. Handbook of applied hydrology, 78-1.

Lines 56-58. I suggest explicitly stating the definition of the return period adopted here under non-stationarity (currently given only at lines 83–84). Indeed, only under the i.i.d. assumption do different definitions coincide with the formula in Eq. (1). At line 63, the authors state that the return period corresponds to the first-order moment of the distribution of extreme events; it would be clearer to state from the beginning that the return period is the mean of the inter-arrival time distribution.

Line 66. The infinite summation in Eq. (2) arises because the return period is the expected value of a probability mass function. In practice, this issue is often addressed by using its empirical counterpart—the sample mean—whose computational cost and estimation uncertainty depend on sample length. Note also that, in some cases, the sum is limited to a finite bound due to non-stationarity. This is closely related to the temporal evolution of the GEV parameters, which is examined in this work.

Lines 107-112. In Eq. (1), Δτ corresponds to one year for annual maxima or to the sampling interval in a POT framework (the inverse of the average number of events per year). In Eq. (5), the authors assume that the process is stationary within Δτ, i.e., within one year in the case of annual maxima or within a generally shorter period in POT applications. Assuming for simplicity that we are working with annual maxima, the GEV parameters are estimated across multiple years (as in the numerical example). Thus, t is much larger than Δτ, within which the process is assumed stationary. Consequently, one must assess whether the process remains weakly nonstationary within time t so that Eq. (5) can be used instead of Eq. (2). Is this interpretation correct?

Eq. (10). The term Δτ appears to be missing from the expression. The mathematical reason is not clear. Under stationarity (a=1), Eq. (12) should correspond to Eq. (1) (or Eq. (5) under stationarity), where Δτ is still present. Please verify or add a brief explanation (e.g., assuming annual maxima with Δτ=1 year).

Line 142. While the interpretation of Eq. (13) is straightforward, its derivation should be explained more thoroughly. Further, the parameter a plays a key role here; what is its acceptable order of magnitude? For example, a=1, 0.1, 0.01?

Regarding Figs. 2 and 3: as far as I understand, they depict the acceptable range of variability of the GEV parameters over given time frames for specific return period values. In other words, they represent isolines of T₀ and T₀ +a t — under the weak non-stationarity assumption and for a=1 — for a specific value of x (and thus a specific T₀), as functions of the parameter values. In this sense, these figures could be used as an abacus to evaluate estimated time‑varying GEV parameters, for instance using the approach of Salas and Obeysekera (2014).

Figure 4. Is a=1?

Line 222. “.. it allows for performing a return period analysis strictly valid within Δτ, ..”. If Δτ=1 year, does the analysis refer to a 1-year window? This should be clarified.

Line 231-232. The change in return period cannot be infinite in the case of decreasing return period; since it is bounded below to Δτ. I suggest rephrasing the sentence to clarify that the “change” refers to the admissible variation in the parameter values.

Lines 283-284. I suggest adding a short paragraph describing how the method could be applied to a real case study: i) fitting a time-varying GEV model to the data; ii) evaluating the parameters to check if the weak non-stationarity condition holds depending on a - for the return period of interest T and the relevant time horizon t; iii) computing the quantile of interest under weak non-stationarity using Eq. (5), to be used for design purpose. The procedure could be also framed within a cost-benefit analysis for system design.  

The manuscript proposes a “weakly non-stationary” framework for return period estimation under trends. This is a well-written and rigorous contribution with a clearly defined scope. The paper is well-structured and the derivations are presented with clarity. Nevertheless, there are several conceptual and practical aspects that require further clarification and strengthening, particularly regarding the definition and interpretation of "weak non-stationarity", its relation to existing non-stationary extreme value approaches, and its practical applicability.

The definition of a “weakly non-stationary” process appears somewhat arbitrary, as it depends on the subjectively defined parameter α, which ultimately controls all results. There is no objective or physically grounded criterion provided for selecting α. A process is, in principle, either stationary or non-stationary. Introducing an intermediate category based on a threshold for the rate of change of the return period requires stronger justification. The authors should clarify how should this parameter be selected in practice. Should it relate to acceptable design risk?

In addition, the relationship between the proposed “weakly non-stationary” framework and established time-varying GEV models (e.g., GEV with covariates, or other trend-based nonstationary EVA methods) should be clarified. Since these models already allow the parameters of the GEV distribution to vary in time, it would be helpful to explain how the proposed framework relates to such approaches. Is the primary contribution a diagnostic criterion for admissible trend magnitudes, or does it offer advantages in estimation or design that cannot be achieved with existing nonstationary EVA methods?

In the discussion of trends and non-stationarity, an important nuance seems to be missing. The presence of a statistically significant trend in hydroclimatic data does not automatically imply non-stationarity of the underlying process for at least two reasons: (a) trends may emerge as manifestations of natural long-term variability or persistence, without implying a structural change in the generating mechanism, (b) stationarity and non-stationarity are modeling assumptions about the system's dynamics, not purely empirical properties to be inferred from finite data samples. As argued in the literature^1,2, invoking non-stationarity presupposes strong physical evidence of systematic alteration of the system’s dynamics (e.g., land-use change, regulation, urbanization). Therefore, the authors should clarify whether their framework is intended for cases with physically justified structural change, or for any statistically detected trend. This distinction is crucial.

In non-stationary extreme value analysis, the main challenge is estimation uncertainty. It could be argued that the computational burden emphasized by the authors is becoming less critical with modern computational resources. In contrast, uncertainty in parameter estimation, which is already substantial in stationary extreme value analysis, becomes amplified under non-stationarity due to additional trend parameters and temporal extrapolation. How does the proposed framework account for uncertainty in estimated time-varying parameters? If trend coefficients have confidence intervals, does the “weakly non-stationary” condition become probabilistic as well? At minimum, a discussion of uncertainty propagation and its interaction with the parameter α should be included.

The framework assumes local stationarity within Δτ, implying that the time-varying distribution parameters are well defined and estimable from the observed record. This assumption deserves further clarification, as classical ergodicity presupposes stationarity. The relationship between stationarity and ergodicity within the proposed framework should therefore be explicitly discussed. Under what conditions can parameters of a time-varying distribution be consistently estimated from a single realization? Since ergodicity affects both return period interpretation and parameter estimation from observed data, it would be beneficial to introduce and clarify this conceptual link earlier in the manuscript.

The paper is highly theoretical. While the mathematical derivations are clear, it may not be obvious to the average HESS reader what the practical contribution is. The authors should more clearly articulate: What specific research question this framework answers? In which typical hydrological scenario it would be preferable over existing methods and how it would be implemented in practice? Could the authors provide empirical examples where the temporal evolution of the distribution parameters is sufficiently gradual, relative to typical design horizons (e.g., 20–100 years), to justify the weak non-stationarity assumption? At present, the practical usefulness is not sufficiently highlighted.

In Figures 2a, 2c, and 3a, the magenta solid line corresponding to the larger time horizon is not shown. Although the text mentions a limitation related to the asymptotic condition of Eq. (11), this is not immediately evident from the figures. I suggest clarifying this point in the caption or adding a brief explanation to improve readability.

¹Montanari, A. and Koutsoyiannis, D., 2014. Modeling and mitigating natural hazards: Stationarity is immortal!. Water resources research, 50(12), pp.9748-9756.

²Koutsoyiannis, D. and Montanari, A., 2015. Negligent killing of scientific concepts: the stationarity case. Hydrological Sciences Journal, 60(7-8), pp.1174-1183.