Dear editor/authors:

After reviewing the new preprint, I am concerned that several of the most important comments to the original submission have not been addressed. While the new version of the paper and the accompanying responses from the authors provide extensive explanations of the previous assumptions and rationale of the study, they unfortunately do not address some of the fundamental methodological flaws and misconceptions I identified in the initial review. 

In particular, in the new version of the paper, the authors have not provided a satisfactory response to the comments about the misuse of the fish species richness distribution concept. The new version insists on applying a global statistical model developed for the purpose of estimating the global distribution of fish biodiversity to predict local changes in biodiversity. I strongly believe that this is an unfortunate extrapolation and NOT appropriate, as the rationale and purpose of the original FSR model by Iwasaky et al. is NOT to explain the phenomenon the authors claim to study (i.e., how water reallocation to change the mean flow of a river reach over a few years could increase or decrease biodiversity in a basin).

Furthermore, in their response, the authors provide a "validation" of the results of the FSR model. However, the original model predictions range from 20 to 250 (~1200% range of variance), which in practice demonstrates that the model's predictive power is basically null: this range basically represents most medium-sized basins on the planet.

The new version of the paper also doesn't provide a satisfactory answer to the extrapolation of the shape of the Pareto frontier of the PPF, assuming that there is a potential continuum and ignoring the discrete nature of the decision problem.  

It is also important to emphasize that with the clarifications of the new version of the paper, a large part of the manuscript consists of results related to the hydrological model development already published in Ekka et al. 2022. A simple citation and quotation of the previous results might be sufficient instead of reproducing the text here.

In some cases, the answers given are also contradictory. In response to the comment of the difficulty of applying a method like IHA to estimate flow regime alterations given the potential uncertainty and errors in modeling the system, the authors claim that the model is adequate.  However, the limitations sections of the revised manuscript claims that  "It is acknowledged that specific water releases from specific dams may not have been accurately captured by the reservoir operations model". so how can hydrologic alteration be correctly assessed if operations are not accurately captured?

As a result, my assessment is that the new version of the manuscript should be rejected. In any case, I hope that the authors can make use of these comments to perform a comprehensive revision of critical components of their study.

Sincerely.

This paper develops a complex methodology that combines ecological and agricultural methods to estimate the economic and environmental viability of constructing multiple dams along the Cauvery Basin in India. The paper has merit and offers a novel approach to compare economy-environment tradeoffs through the PPF. The main strength of the model lies in its hydrologic component and the capacity of the model to represent the water system, including the location of built and hypothetical reservoirs. I note throughout the methods an imbalance between the detail in the ecological analysis and that of the socioeconomic analysis. The structure is adequate, and the flow of the paper is easy to follow. Not being an ecological researcher, I will refrain from assessing deeper the merits of the ecological modeling, and will focus rather on the socioeconomic component of the model.

The use of a PPF is clever and provides a useful visualization of the tradeoffs. However, the economic analysis is rather an agronomic analysis of production (ET function) to obtain yield quantities, which are later on multiplied by a constant price. This approach has a number of limitations:

-Authors seem to assume that agricultural land allocation remains constant. That is, if farmers receive 50% of the water right, they irrigate each crop applying 50% of their ET and maintain land use shares. This precludes extensive (shifting to rainfed agriculture) , super extensive (shifting to other crop) and intensive margin adaptation (selective deficit irrigation, where some crops receive less water and some others are fully irrigated). This approach lacks realism as demonstrated in the agecon literature (Graveline and Mérel, 2014). I reckon this is a very common assumption in hydrologic and ecohydrologic models – but it is nonetheless a gross simplification that, although common in the literature, has to be properly acknowledged in the text as a key assumption and limitation of the research. Authors are invited to read about economic calibrated models and even normative models used to assess land and water reallocations based on utility / profit maximization (Adamson et al., 2017; Graveline, 2016; Sapino et al., 2020).

-Authors use constant prices. This has to be properly justified. If the basin is large enough, droughts and reduced water allocations will reduce yields, which will constrain supply and can therefore significantly affect prices. Note that agricultural demand is highly inelastic so significant changes in supply may lead to abrupt changes in prices. This can partly mitigate agricultural losses due to reduced water availability during droughts (Haqiqi et al., 2023, 2022; Parrado et al., 2019).Again, this is an even more common assumption in water system models and even economic models, so this is acceptable—but should nonetheless be acknowledged as a limitation, particularly considering the economic relevance of the basin, which occupies a large territory.

Last, although I’m not an expert ecologist but you are assessing environmental – economy tradeoffs as a relationship between fish biodiversity and agricultural production. I understand agriculture is the main and least valuable economic use so this makes sense. But are not there other relevant ecosystem services affected by the dams? Such as aesthetic amenities, tourism, etc.? Why are you not including them? A justification here would be necessary.

Overall, the paper has value and potential but clarifications are needed to put this in context of existing socioeconomic literature.

Adamson, D., Loch, A., Schwabe, K., 2017. Adaptation responses to increasing drought frequency. Australian Journal of Agricultural and Resource Economics 61, 385–403. https://doi.org/10.1111/1467-8489.12214

Graveline, N., 2016. Economic calibrated models for water allocation in agricultural production: A review. Environmental Modelling & Software 81, 12–25. https://doi.org/10.1016/j.envsoft.2016.03.004

Graveline, N., Mérel, P., 2014. Intensive and extensive margin adjustments to water scarcity in France’s Cereal Belt. Eur Rev Agric Econ 41, 707–743. https://doi.org/10.1093/erae/jbt039

Haqiqi, I., Bowling, L., Jame, S., Baldos, U., Liu, J., Hertel, T., 2023. Global drivers of local water stresses and global responses to local water policies in the United States. Environ. Res. Lett. 18, 065007. https://doi.org/10.1088/1748-9326/acd269

Haqiqi, I., Perry, C.J., Hertel, T., 2022. When the virtual water runs out: local and global responses to addressing unsustainable groundwater consumption. Water International 47, 1060–1084.

Parrado, R., Pérez-Blanco, C.D., Gutiérrez-Martín, C., Standardi, G., 2019. Micro-macro feedback links of agricultural water management: Insights from a coupled iterative positive Multi-Attribute Utility Programming and Computable General Equilibrium model in a Mediterranean basin. Journal of Hydrology 569, 291–309. https://doi.org/10.1016/j.jhydrol.2018.12.009

Sapino, F., Pérez-Blanco, C.D., Gutiérrez-Martín, C., Frontuto, V., 2020. An ensemble experiment of mathematical programming models to assess socio-economic effects of agricultural water pricing reform in the Piedmont Region, Italy. Journal of Environmental Management 267, 110645. https://doi.org/10.1016/j.jenvman.2020.110645

The authors have improved the manuscript from the earlier version, particularly on scope, aims, description of models, and parameterizations. Thank you for providing responses to earlier comments. However, there are still critical aspects of methods, analysis and interpretation of results which should be significantly revised.

Major comments:

1). The authors have directly implemented empirical equation for fish species richness (FSR) as an indicator for ecosystem health as proposed by Iwasaki et al. (2012), authors further argue that in lines 536-537, that Yoshikawa et al. (2014) validated the empirical equation in 84 basins. However, that is not true! In the second study, the comparison of linear and non-linear form of FSR was done and applied for different basins. Both of these studies discuss the limitations and mentions that FSR varies across upstream to downstream. Yet the response on previous comment, “does a single FSR value enough for whole river network?”, was not adequately answered.

The key limitation should be well taken into consideration, that the empirical equation is not based on the actual physical processes and is derived through observed data. Hence, the regression coefficients of the equations are subject to vary based on new data and across river basins. It is also be noted that sample data on those studies are not from this river basin or the latitude of this study area.

Adopting the same equation is not a novel contribution. At the least, the authors should build upon the studies by Iwasaki et al. (2012) and Yoshikawa et al. (2014) and discuss implications in this basin. Additionally, authors may consider sensitivity analysis and observe how FSR varies spatially along the river or temporally over the years. But this is just a suggestion. However, authors should address this from methods to results and discussion.

2). Line 18, 28 and overall: “Spatial configuration” term is still vague and might be confusing to readers. Spatial configuration means finite number of configurations of existing four or more dams (if added) to other feasible locations, it could also mean changing storage capacities of the dams (or changing locations of 4 existing dams). Authors did not do this but claimed this can be done (as mentioned in lines 82 and 319). The 16 scenarios are indeed created by strategically deleting one, or combination of two, three or four dams. “Configuration of existing dams” is more clear phrase. However, it is appropriate to write that the strength of this approach is it can be extended to full spatial configuration of dams (i.e., addition/deletion of new/old dams at existing/new locations etc.).

3). Previous comment on “..calibration metric was used as mm/day for streamflow..” to which authors response was, “The Flex-Topo model operates on a daily time scale, and it relies on forcing data expressed in mm/day. Consequently, when calibrating the model's simulated discharge, the observed discharge in cubic meters per second (cumec) is converted into mm/day”.

It is confusing to me, since [L/T] is the unit of velocity. Did the authors consider cross-sections of the river to convert discharge to velocity? Otherwise, how mm/day for discharge was obtained? Please explain this.

4). Previous comment on, “Figure 6: It is redundant with Table 2 (Mean annual flow column). Presenting hydrographs would be more informative than Figure 6 since there are only 16 scenarios and expanding the discussion on the role of reservoirs and seasonal streamflow.” to which authors responses was, “The Table 2 is deleted, and the figure is modified to hydrograph as suggested.”

Figure 6 is not the hydrograph! It is in fact same figure as previous version of Figure 6. Authors just changed horizontal bars to vertical.

My suggestion is mean annual flow column should not be removed from table 2. And hydrographs of mean monthly flow (Jan to Dec), or similar figure should be added to discuss seasonality, change in minimum flow, peak flow etc.

In addition, authors presented the time periods for calibration and validation. But what is the time period the analysis of 16 scenarios?

5). I am confused with how the authors compared high value crops for basin (of smaller dams), with less value crops for basin (with larger dams). It is difficult to understand why such comparisons are made. May be the cereal has more value compared to horticulture crops for livelihood of the community, although the monetary value may be opposite. I am not sure how appropriate it is to recommend switching to different crops just for monetary value, since water management is multi-stakeholders decision, not just driven by monetary gain.

6). Section 2.7.1: Since, the model was simulated at daily time steps, how was the agricultural production computed? Equation 4 do not describe this. Perhaps you can add another equation to elaborate how it was implemented in the model, and how the yearly agricultural production (as shown in figure 10) was computed. Please indicate the correct units of the variables implemented in your model.

7). Equation 5: Similar to the comment on equation 4. But is this computed once per year? Does it vary each year? How the single value of FSR as shown in Figure 11 was obtained over the time period of simulation, assuming it was multiyear simulation?

8). Line 15: It is a unique approach or unique for Upper Cauvery basin, India, or first study using this approach in this basin. Agriculture value and fish species richness was quantified as a single value per scenario not analyzed at daily scale, so the statement is incorrect. Also, how the use of daily scale is unique contribution?

Other comments:

9). Line 60-70: Upon quickly verifying these by google search, this list is not updated. There are several more studies on cascade or multiple dams – and its environmental implications.

10). Line 67-69: What are pre-dams data? Please check the validity of this statement.

11). Figure 1. Calibration can be omitted from this flowchart, since it was done in previous paper and not part of this paper.

12). Section 3.1: Since, calibration and validation are not part of this study, but was taken from previous study, it is not necessary to present it in result section. A separate section on “Description of model” or merging it in introduction with supporting supplementary material would be better.

13). Equations 1, 2, 3: Please write the units of the variables used in descriptions.

14). Figure 3, legend on size of point symbols can show the range of minimum to maximum area of command area. Another question, is size of the command area reflective of the number of populations living in that area, or the size of irrigated land? If not, what is the relevance of the size of command area!

References

Iwasaki, Y., Ryo, M., Sui, P. and Yoshimura, C., 2012. Evaluating the relationship between basin‐scale fish species richness and ecologically relevant flow characteristics in rivers worldwide. Freshwater Biology, 57(10), pp.2173-2180.

Yoshikawa, S., Yanagawa, A., Iwasaki, Y., Sui, P., Koirala, S., Hirano, K., Khajuria, A., Mahendran, R., Hirabayashi, Y., Yoshimura, C. and Kanae, S., 2014. Illustrating a new global-scale approach to estimating potential reduction in fish species richness due to flow alteration. Hydrology and Earth System Sciences, 18(2), pp.621-630.