Dear Authors,

I have carefully reviewed your manuscript entitled "Hydrological regime shifts in Sahelian watersheds: an investigation with a simple dynamical model driven by annual precipitation." This study presents a novel, parsimonious modelling approach to investigate regime shifts in Sahelian runoff dynamics, a particularly relevant topic given the hydroclimatic complexity of the West African drylands. The manuscript is based on a clear and well-motivated hypothesis—the Sahelian paradox as a manifestation of hydrological regime shifts—and it advances a simple yet insightful dynamical model incorporating precipitation and runoff feedbacks. The combination of lumped modelling, ensemble simulation, and bifurcation analysis is commendably applied to long-term observational datasets.

However, there are some areas that require improvement before this work can be considered for publication.

Lines 45–50:



You introduce a model with precipitation as the sole external forcing. While conceptual simplicity is appreciated, the omission of known key drivers like land use changes (e.g., deforestation, cropland expansion, crust formation) and rainfall intensity is somehow concerning. Given existing knowledge on Sahelian hydrology, this simplification may lead to misleading causal inferences. The rationale for excluding these variables needs to be better justified, and at minimum, the implications of this omission must be critically discussed earlier. Also, not all readers are familiar with the term “attraction basin”, which needs explaination beforehand.

Lines 100–110 (Eq. 1 and surrounding text):



The functional form used to relate S, P, and K is not adequately justified from a physical or empirical standpoint. For instance, the role of the parameters aa and bb in shaping the runoff response curve requires clearer explanation. Why not explore more physically based alternatives or benchmark this against empirical runoff-precipitation relationships?

Lines 105–110 (Eq. 2):



The formulation of the “indicator of wetness” I is intuitive, but its dependence on the parameter f introduces confusion, especially since ff also appears in Eq. 1. The choice to divide by f in this context is not well motivated—wouldn't this imply higher f leads to lower wetness, contrary to physical intuition?

Lines 109–115 (Eq. 3):



Equation 3 includes a third term µ(1-S) that is introduced as a stabilizer. This is acceptable, but it remains ad hoc and may significantly affect long-term trajectories of the model. Please include a sensitivity analysis of this parameter or offer more detailed justification of its value and range.

Lines 115–125 (Model calibration):



While you cite equifinality to justify using an ensemble, you could improve the reproducibility of your methodology by clarifying the basis for choosing the “top 1,000” parameter sets. Why not explore a weighted ensemble or Bayesian approach to deal with parameter uncertainty more formally?

Lines 125–135:



You define bistability based on attractor separation, but the use of arbitrary thresholds like 2000 mm precipitation and 10,000-year simulations raises concerns. These choices might significantly affect the classification of parameter sets. You should evaluate how sensitive the bistability classification is to these design choices.

Lines 145–155 (Eq. 4 and definition of regime):



The operationalization of regime shifts via S=(↑S+↓S)/2 is a critical assumption. This midpoint criterion might not capture the actual dynamics of transition in transient regimes. Alternative definitions (e.g. basins of attraction) or at least a justification for this heuristic are needed.

Figure 5 / Lines 155–170:



The mismatch between observed runoff coefficients and the simulated ensemble spread—especially for the Sirba and Nakanbé basins—is troubling. It casts doubt on whether the model can adequately capture year-to-year variability or nonlinear transitions. Please provide a quantitative assessment of performance beyond RMSE (e.g., Nash-Sutcliffe efficiency, bias).

Lines 180–190 and Figure 7:



The definition of the “regime shift year” as the first time when more than 50% of ensemble members enter the high regime seems arbitrary. Why not use a probabilistic or statistical breakpoint analysis? The current criterion could lead to inconsistencies in estimating regime shift timing, as seen in the Gorouol case.

Lines 200–220 (Discussion):



You rightly acknowledge that the model underrepresents interannual variability and that precipitation alone is insufficient. However, this admission seems to undercut the core claim that the model can meaningfully identify regime shifts. This contradiction should be addressed more transparently. Can regime shifts truly be inferred from such a limited model?

Lines 205–210 (Gorouol case):



The early regime shift in the Gorouol basin (before observed droughts) is indeed counterintuitive. It may reflect model artefacts from initialization, especially since 40% of ensemble members already start in the “high” regime. This undermines the claim of detecting shifts dynamically. Please explore whether this result is robust or an artefact of initial conditions.

Lines 215–220:



The interpretation of monostable vs. bistable ensemble members is important, but underdeveloped. If 10% of simulations do not undergo regime shifts, does this reflect real watershed variability or model limitations? Some exploration of this heterogeneity would enrich the discussion.

A minor and general comment: the writing is generally clear, but at times overly dense with jargon. Consider simplifying key explanations, especially around dynamical systems concepts, to enhance accessibility for a broader hydrological audience. Also, Figures (in general) are informative, though Figures 4 and 6 could benefit from clearer legends and a brief description of axis choices (e.g. why is S bounded between 0–0.7?).

The manuscript presents a deterministic approach to examine annual runoff regime shifts in four catchments of the Sahel. Specifically, a simple ordinary differential equation for the runoff fraction is proposed, parameter sets are then sampled (using Latin hypercubes) and then used to approximate stable states using temporal simulations of the ODE. The simulations are then partially evaluated against observations and then used to approximate the attractor and estimate when each catchment was in each state.

Overall, the paper is clearly written and I am pleased to see the authors attempting to quantify hydrological attractors. The methods adopted are, however,  seriously lacking and do not adequately draw on the considerable body of literature on this topic. These concerns are expanded on below and some options for improvement are given:

1. The introduction presents a cursory outline of existing work on hydrological regime shifts. Importantly, a shift in runoff per unit rainfall (e.g. Saft et al., 2015) is not evidence a regime shift to an alternate attractor. Doing this requires cessation of the disturbance and evidence of non-recovery, as demonstrated by Peterson et al. (2021). Additionally, the mechanisms for regime shifts is vague (Peterson et al., 2012), the role of forcing on regimes is not examined (Peterson et al., 2014; Peterson and Western, 2014) and informative case studies using numerical hydrological models are overlooked (Anderies, 2005; Anderies et al., 2006). Additionally, the many efforts by others to identify the timing of shifts (Peterson et al., 2021) and the hydrological mechanisms is overlooked (Fowler et al., 2016, 2020; Saft et al., 2016).

2. The MS asks did these regime shifts occur? Given well established statistical models and code exist for this, e.g. Hidden Markov Models (Peterson et al., 2021), it is very unclear why the proposed approach is appropriate.

3. The use of an ODE to identify attractors etc is interesting. The ODE developed, however, lacks a clear hydrological basis and does not draw on well established hydrological processes. Overall, it appears to be drawn from the school of ecosystem resilience that has for too long relied on toy models that are incapable of explaining observations or offering practical insights (Newton, 2016). I urge the authors to develop a model that is based on hydrological mechanisms.

4. The approach for identifying the steady state regimes (i.e. attractors) and the fold points is very problematic. The MS presents an ODE but then uses time-solutions rather than bifurcation (Eq 4). Very well established analytical and numerical methods exist that estimate stable and unstable states with a forcing variable and then also the fold points, i.e. the thresholds between states. I urge the authors to look at these hydrological studies (Peterson, 2009; Peterson et al., 2012; D’Odorico and Porporato, 2004; D’Odorico et al., 2005), worked examples (Ludwig et al., 1997) and mathematical references (Kuznetsov , 2004; Dhooge et al., 2003). Using such methods, it should be possible to probabilistically quantify the regimes and thresholds with significantly more confidence.

5. Section 3.2 states that the ODE is calibrated. This is not correct. The MS samples the parameter space but does not use any objective function to

either reject implausible parameters (e.g. GLUE), or estimate formal likelihoods (e.g. Vrugt, 2016). Similarly, the approach cannot also be called sensitivity analysis, given the lack of quantitative evaluation against observed flow. Additionally, the predictor (rainfall) is not independent of the predicted variable (i.e. runoff ratio) because it is used in the denominator of the runoff ratio. I urge the authors to develop a formal likelihood function for flow (not runoff ratio) and then do MCMC estimation of the parameter uncertainty.

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