Review for “System dynamics perspective: lack of long-term endogenous feedback accounts for failure of bucket models to replicate slow hydrological behaviors”

This paper investigates the factors long-term endogenous feedback soil water-vegetation feedback loop through the system dynamics perspective. It is an interesting topic and is widely concerned. However, there are several problems that needs to be revised.

The products of actual evapotranspiration contain much uncertainties. The authors should be very careful with the products and validation of the accuracy in the region is recommended.

 There is a hydrological model adopted. How the parameters are determined, including VEG and GP? Why the model is adopted? To my knowledge, process-based hydrological model is rarely used at annual scale.

The desired (expected) soil moisture stock ESMS is key parameter in the hydrological model. The meaning of ESMS need to be further explained. The discussion in Section 4.1 seems too general.

Fig 4. What’s the meaning of model Z. Could the causal relationship be used to generate better hydrological series compared the the process-based hydrological model?

Future dynamics of hydrological systems under three climatic scenarios are shown in Fig 7. But could not catch what the key points the author wanted to address.

A general description of the hydrological properties of the catchments is needed.

The use of "bucket models" in the title seems inappropriate.

Line 116. Using ΔS to indicate water budget seems not suitable.

Lines 208-211. It is inappropriate to put the discussion there.

Lines 210-214. The brief description of hydrological characteristics of the wet and dry phase is suggested. Why the wet-dry phase be determined by wavelet coefficient instead of annual precipitation or aridity index?

Fig 2. Subtitle of the figure needs to be labelled and also for other figures.

Fig 5. What’s the meaning of the three sub-figures for Fig 5(a).

Lines 327-328. Penman-Monteith model is used for calculating the potential ET instead of actual ET.

Line 331. What's the specific of instantaneous scale?

The study uses a system dynamics approach aiming to reveal endogenous factors that account for the long-term slow dynamics of a catchment hydrological system. The paper addresses relevant problem within the scope of HESS, the topic is interesting and widely discussed. However, my recommendation is major revision due to several significant issues in the methodology that seem inadequate for addressing the posed research questions. Further justification is also necessary for the conclusions made. Below are my main concerns.

First, I did not find confirmation that the studied basin demonstrates “slow hydrological behaviors.” If I understand correctly, the authors believe that such confirmation is provided by the obtained results of wavelet analysis. I do not think so. Wavelet analysis evaluates the coincidence or difference in the phases of oscillations of various hydrological variables, which can be useful for assessing the cause-and-effect relationships between them as well as for identifying long-term wet-dry periods, as was shown in the paper. But the results presented, in particular the fact of a lag in the response of evapotranspiration to precipitation, do not indicate per se the slow behavior of the system. Such evidence could follow from an analysis of the presence of a long-memory effect in the studied hydrological time series. (Note, that in a paper devoted to the problems of detecting slow hydrological behaviors and the physical mechanisms that control this behavior, it would be appropriate to reference at least the most well-known hydrological publications in this area (e.g., some of them cited by O’Connell et al. (2016)). However, the results of the description of hydrological processes in the studied catchments using standard autoregressive models presented in the paper (Fig. 4) allow us to doubt that these are long-memory processes.

Second, if there is evidence that the dynamics of the system can be interpreted in the desired way, then the use of standard wavelet analysis, which was developed for processes with short memory, is questionable. For such processes, the analysis has to be modified (see, e.g., Percival and Guttorp, 1994; Hsu, 2006).

Third, as an alternative that allows one, in contrast to the bucket model, to describe “slow hydrological behaviors,” a simple linear model of annual changes in the components of the water balance of the river basin under study is proposed. In the paper, I was unable to find results demonstrating that such a model has an advantage in describing the slow dynamics of a system, so I see no reason to consider the proposed model a reasonable alternative. The calculation results for ET, Q and TWS (Fig. 6 and Figs. in Suppl. Materials) are poor, i.e. the suggested model not only does not reproduce the desired effects, but also does not meet the performance measures adopted for hydrological models (the values of the coefficient of determination given in the paper confirm my opinion).

Thus, I have to conclude that the title of the paper does not reflect the content of its current version, since it does not provide any evidence that “lack of long-term endogenous feedback accounts for failure of bucket models to replicate slow hydrological behaviors.”

Nan-Jung Hsu (2006) Long-memory wavelet models. Statistica Sinica 16, 1255-1271

O’Connell P.E. et al. (2016) The scientific legacy of Harold Edwin Hurst (1880–1978), Hydrological Sciences Journal, 61:9, 1571-1590, DOI: 10.1080/02626667.2015.1125998

Percival, D.B. and Guttorp, P. (1994) Long-Memory Processes, the Allan Variance and Wavelets, Editor(s): Efi Foufoula-Georgiou, Praveen Kumar, Wavelet Analysis and Its Applications, Academic Press, 4, 325-344

Specific and technical comments

1. Lines 148-151: This describes the Granger's Causality Test for determining the dependence of X on Y (Y causes or does not cause X), while equation (2) describes the dependence of Y on X.Change either the description on lines 148-151 or equation (2).
2. Line 239: If ET Granger-causes S, and ΔS Granger-causes ET, then the question is: what is the cause and what is the effect?
3. Fig. 4: Change "cause" to "causes".
4. Fig. 4: What does AR(1) mean? First order autoregressive model? What, then, is AR(1,1)? Explanation required.
5. Fig. 5: It is not clear what results allowed the authors to conclude that reinforcing feedback (1) exists.
6. Line 257: Until now, there has been no talk about hysteresis effect. Explanation required.
7. Lines 268-270: It is necessary to expand the description of the solution to equations (3)-(12). In particular, explain how the variables VEG(t), K(t), ESMS are determined (in the equations, the latter is designated as a constant). How are the constants C1, C2, C3, C4 determined?
8. Lines 271-272: The presented results do not confirm the statement that “Simulated Q and ΔS captured both the annual fluctuations and the long-term trends”.
9. Fig. 6 and Figs. in Suppl. Materials: The calculation results for ET, Q and TWS are poor. Herewith, good results were obtained for ΔS. Why? I believe that these results are achieved by adjusting the calibration factors and variables. In this case, coefficients C1-C4 have no physical content and can take on any values. For ΔS, this adjustment made it possible to compensate for the poor calculation results of other variables. Please comment.
10. Fig. 6: What is ET1, ET2, Q1, Q2, ΔS1, ΔS2, TWS1, TWS2? What is TWSA?
11. Lines 298-302: How were anthropogenic impacts (VEG, GP) set for the future period? How were coefficients C1-C4 set? The same as for the historical period? On what basis, if these are purely empirical coefficients reflecting data for the observation period? Overall, I see no point in using an ineffective hydrological model to estimate the future state of a hydrological system. In addition, these experiments are not relevant to the main content of the paper. I suggest removing them.
12. The reasoning in subsection 4.1 is correct in essence but has no relation to the results obtained. The listed physical, chemical, and biological mechanisms influencing changes in soil water retention are not described by the extremely simple model proposed. Therefore, the fact that the desired soil moisture turned out to be higher in the dry phase has nothing to do with these mechanisms but, as I assume, is only an accidental consequence of the calibration procedure.
13. Also, the reasoning in subsection 4.2 is not relevant to the results obtained. The previous sections do not show that vegetation changes, "such as tree growth and mortality, have become significant factors influencing ET over climate". It is not clear what long-term delay in hydrological response the authors are talking about. No results were presented to support the presence of such relationships. The conclusion that “persistent hydrological shifts and especially flow reductions such as those caused by the increasing and enduring multi-year drought can only be described accurately with the system dynamics approach” is not supported by the presented results.

This study seeks to look at the problem of "slow hydrological behaviours" via a different lens, namely that of system dynamics.  I certainly agree that this is a pressing problem that needs some fresh thinking, since many current "bucket" models do a poor job at simulating such behaviours.  The system dynamics approach may be relevant here, but I'm concerned that there are multiple serious issues with the implementation here, as follows.

- Missing processes, and conceptual confusion, regarding evapotranspiration. The authors don't seem to be taking into account the concept of evaporative demand - that is, they are neglecting the fact that the actual ET is a function of two things: (1) how hot and dry the near-surface atmosphere is, as captured in the concept of Potential Evapotranspiration (PET); and (2) the subsurface water availability, eg. in soil moisture.  (1) seems to be missing so let's focus on that.  At line 177 it says "while traditional hydrological models usually use physical process-based models such as the Penman or the Thornthwaite models to calculate ET...".  [NB: By "ET", I believe the authors here mean actual evapotranspiration (AET), because this is how they have used that acronym throughout the manuscript - which is part of the confusion.] Anyway, no, that is not what "traditional" models do - typically, methods such as Penman are used to estimate PET, not AET; such methods produce a PET timeseries which becomes an *input* to the modelling processes.  In other words, whereas the modelling here seems to use only one input, precipitation, traditional modelling uses two, precipitation and PET.  So the present method seems to be neglecting the reality that a hotter drier atmosphere can result in a greater proportion of precipitation being lost to AET, all else being equal.  I presume the same framework could be altered to add this additional driving variable, but I'm unsure.  In any case, the modelling is subsequently applied to a climate change scenario which invariably means a hotter (if not drier) world, and yet the modelling seemingly cannot account for one of the most basic elements of the climate change signal (ie. rising temperatures)—this is unacceptable.  I note that I may have misunderstood something here so I'd be happy to be corrected by the authors.  

- The chosen approach induces memory that is too long for some system components.  The calculation of key fluxes (AET, Q, recharge) depends upon the discrepancy, DISC, between soil moisture and the assumed ideal or "expected" soil moisture storage. The trouble is that since the equations are being solved at a yearly timestep, this means the AET, Q and recharge don't respond to a high rainfall value until the year after it happens.  Basic common sense would seem to ward against this - ie. the flood doesn't come the year after the rainstorm.  I wonder if this could be solved if the same approach were used on a shorter timestep and/or if the equations were solved in such a way that the equations took account of forcing fluxes from the same timestep than the one being solved.  

- The conceptualisation is seemingly ill-suited in the case of streamflow.  The observed peaks in streamflow are absent, associated with severly underestimated streamflow variability.  The streamflow is calculated as the aforementioned discrepancy in soil moisture multiplied by a calibratable parameter.  Since soil moisture is a state variable that is only allowed to vary on annual timesteps, it is rather slow moving, not episodic, and this property is then translated to streamflow dynamics as well.  

MINOR COMMENTS:

Line 109: I suggest that "AET" is used instead of "ET" throughout - this will minimise confusion with PET

117: It would be good to discuss the uncertainty of information being used here, particularly remotely sensed AET.  Given the uncertainty in the RS AET, it's illadvised to calculate change in S by subtracting RS AET from precip (for an example of how a study accounted for this uncertainty by water-balance-based factoring, see here: https://doi.org/10.1029/2022WR033538).  

136: Many readers will not have a background in the concepts and/or methods used.  Please explain the concept of a mother wavelet.

In general, much of the language used anthropomorphises the system, such as saying it has a "goal" ("[balancing feedback loops are] aiming for stability").  Also, where it is said that it "desires" a certain soil moisture.  

196: Better to call it "precipitation input" rather than "precipitation inflow" as the latter is too close to language used for streamflow.  Likewise the other "outflows" would be better as "outputs".

200: "Correction coefficients" makes it sound like something is incorrect.  Perhaps "coefficients that determine the rapidity with which the system self-corrects after a disturbance" or "responds after a disturbance"

215: This is method and needs to be moved to the methods section. 

Figure 2.  The choice of colour is confusing - Greens and blues are typically reserved for fluxes like precip and streamflow, while reds and yellows for ET. So, swap colour of P and ET. 

252 onwards: There needs to be a subsection in the methods section that explains the broad logic of doing this (even though it won't yet be possible to be specific since the results are yet to be presented).  That is, you need to say that you build the model based on the causal links seen in separate analysis. 

264: the remotely-sensed vegetation indices are discussed as if the authors are unaware that remotely-sensed AET is itself calculated from one of these indices (eg. NDVI)

301-02: No, that's not the way to interpret GCM sequences because, although it is hoped that their climate sequences are realistic overall (ie. have similar statistics to reality for the sequence pre-2024), the exact timing of dry periods and wet periods is decoupled from reality; ie. the simulated sequence is purely synthetic (thus, the droughts that appear in the pre-2024 simulated sequence are not timed with historic droughts).

Figure 6: the bottom right hand panel is cheating a bit: while it's ok to shift the lines vertically to emphasise the match, the rate of change per unit length should be identical.  In other words, since the axis range on the right is 2000 (ie. simulated TWSA has maximum 2000, minimum 0), the other axis (for observed TWSA) should have a range of 2000 also (ie. perhaps -500 to +1500). The current arrangement artificially inflates the apparent match.