the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 11 Sep 2023
How economically and environmentally viable are multiple dams in the Upper Cauvery basin, India? A hydro-economic analysis using a landscape-based hydrological model
Abstract. The construction of dams threatens the health of watershed ecosystems. The purpose of the study is to illustrate how multiple dams in a basin can impact hydrological flow regimes and subsequently aquatic ecosystems that depend on river flows. The approach assesses the ecosystem services, including the tradeoffs between economic and ecological services, due to altered the flow regimes. It uses a previously developed model that integrates a landscape-based hydrological model with a reservoir operations model at basin scale and at daily time scale. The approach is unique not only because it offers the analysis of alterations in ecosystem services at daily scale but also because dams can be synthetically placed anywhere in the river network and the corresponding alterations in flow regimes simulated in a flexible manner. As a proof of concept, we analyse the economic and ecological performances of different spatial configuration of existing reservoirs in the Upper Cauvery River basin in India. Such a study is timely and being conducted for the first time, especially in the light of the calls to assess cascade of reservoirs in India and regions elsewhere where pre-dam data is unavailable. The hydrological impact of different configurations of reservoirs is quantified using Indicators of Hydrologic Alteration (IHA). Additionally, the production of two major ecosystem services that depend on the flow regime of the river, as indicated by irrigated agricultural production and fish species richness, is estimated, and a trade-off curve, i.e. a production possibility frontier, for the two services is established. Results show that smaller reservoirs on lower-order streams that maximize the economic value of water stored are better for the basin economy and the environment than larger reservoirs. Cultivating irrigated crops of higher value can maximize the value of stored water and, with lower storage, generate similar economic value than with lower value crops while reducing hydrological alterations. The proposed novel approach, especially when simulating synthetic spatial configurations of reservoirs, can help water and river basin managers to understand the provision of ecosystem services in hydrologically altered basins, optimize dam operations, or even prioritize dam removals with a balanced provision of ecosystem services.
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RC1: 'Comment on hess-2023-204', Anonymous Referee #1, 04 Oct 2023
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.
Citation: https://doi.org/10.5194/hess-2023-204-RC1 -
AC1: 'Reply on RC1', Saket Pande, 04 Oct 2023
Thank you for the opportunity to discuss the comments in this interactive session. Please see below our first response to the referee comments. We are looking forward to a fair and constructive discussion on the merit of this manuscript by further clarifying and responding to subsequent comments of the referee.
Response to comment 1. Our revised manuscript clearly states that this paper is a first study of its kind to assess tradeoff between two ecosystem services as indicated by income from agricultural production and fish species richness in Indian context. This study sacrifices high accuracy in predicting fish species richness for modelling tradeoffs between agricultural production and fish species richness (FSR). The limited prediction accuracy has been acknowledged and it has been highlighted that this needs more field campaigns and left for future research.
However we would like to highlight that our model of FSR is not as simplistic as the referee suggests, that it is only a function of mean flow. It is not. Even though we agree that we are modelling first order variation of FSR but it is with various characteristics of stream flow variation such as of low flows, high flows and its timing (please see equation 5) in addition to log of mean flow but also log of catchment area. This falls in line with extensive literature on the use of species discharge relationships (SDR) and species area relationships (SAR) in assessing variability in biodiversity as a function of discharge at the scales of our study (>500 sq. km and averaged over time). See e.g. Schipper and Barbarossa (2022) and extensive recent related literature on drivers of variability in biodiversity cited within along these lines that indeed suggest that discharge (not just mean but other characteristics as well) and area have large power in explaining FSR. Other factors such as human pressure may influence higher order effects in these relationships. Therefore we do claim significant changes in stream flows characteristics would lead to significant changes in FSR using a synthesis of such effects explored by experts via the equation 5.
Response to comment 2. We agree that we should not use the term validation and it was an unfortunate use of the term. We will refrain from its use and constraint ourselves to the use of empirical equation.
Response to comment 3.The construction of the convex hull is indeed due to the discrete but realistic nature of the problem. There may be a continuum but that continuum is neither real (because we only have the mentioned four reservoirs in the basin and therefore only 16 possible combinations of realities depending on how these existing reservoir could be removed in the future) nor is in the scope of the current study as we have already highlighted in the current study. Given only finite amount of points, creating a convex hull to represent a convex production set makes minimal assumptions and is consistent with the economics literature (see e.g. Ginsburgh and Keyzer, 1997). We can further expand along the above line in our revised manuscript.
Response to comment 4. The modelling additions we have made are in response to the referee comments which we believe is fair also for this paper to be complete on its own.
Response to comment 5. Our model is adequate because mean absolute error of simulated when compared to observed is low: 0.71 to 2.92 (106 m3 day-1) compared to mean annual flows > 17 (106 m3 day-1), meaning that on average the absolute error is one or two orders of magnitude smaller than mean annual flows. NSE ranges between 0.51 and 0.73 (mostly > 0.6 for reservoir operations; please see supplementary material). It is because of this that we state that the model is adequate, especially since it has daily reservoir operations modelled within, which is a difficult modelling task.
We acknowledged such a limitation as no model is perfect and the model can improve in performance. Currently the reservoirs operatiosn at daily scale are based on trigonometric functions that do not incorporate incidental dam specific releases but only incorporates water demand by various command areas as the dominant driver of reservoir releases. Accommodating dam specific water releases might improve the simulation of intra-monthly variability in streamflow (see its discussion in Ekka et al. 2022). Whether this leads to changes in the conclusions drawn based on the possibility frontier shown in Figure 12 is beyond the current scope but even if we assume log effects of mean annual flow on FSR, changes in flows of one or two order would in log scale not affect the conclusions drawn (since FSR is a function of log of mean flows and other streamflow characteristics). Therefore reservoir configuration that brings about significant changes in streamflow characteristics (not one or two order of magnitude lower or higher than mean flows) would still drastically influence FSR and therefore for it to remain a pareto superior choice, it should significantly add more economic value. Reservoirs that significantly alter flow regimes but do not add significant value should be discouraged since it would be a pareto inferior choice, which is one of main conclusions drawn.
Citation: https://doi.org/10.5194/hess-2023-204-AC1 -
AC2: 'Reply on AC1', Saket Pande, 04 Oct 2023
Here by the references of our response:
Schipper, A. M. & Barbarossa, V. (2022). Global congruence of riverine fish species richness and human presence. Global Ecology and Biogeography, 31, 1501–1512. https://doi.org/10.1111/geb.13519
Ginsburgh, V. I. C. T. O., & Keyzer, M. A. (1997). The structure of applied general equilibrium models. The MIT Press.
Citation: https://doi.org/10.5194/hess-2023-204-AC2 -
RC2: 'Reply on AC2', Anonymous Referee #1, 05 Oct 2023
The authors claim that this is a first-time assessment and that low precision is acceptable for such a study. While this may be a valid point, it actually distracts from the central point of the comment. I must clarify that the issue is not the precision of the study, but rather the fundamental epistemological inadequacy of the proposed approach. My central point is that a model developed to assess variability in biodiversity is not equivalent to a predictive model to explore causality between processes (such as how changes in flows can cause changes in biodiversity).
The results presented highlight the unreasonableness of the proposed apprach. According to the manuscript, the basin should have already experienced the extinction of ~100 fish species due to the allocation of water for irrigation, however no evidence of such an ecological disaster is presented. Conversely, if some reservoirs are removed, will numerous fish species appear in this basin? This may sound like a caricature, but unfortunately it is at the heart of the analysis presented. Again, this is a clear misuse of a regression model and the published literature on SDR and SAR; it is fundamentally a failure to distinguish between correlation and causation.
As it stands, the study provides an assessment of change in some aspects of freshwater habitat integrity, not fish biodiversity. I'd respecfully encourage the authors to consider declining the current submission, and reformulating the paper to explore the trade-offs in those terms.Citation: https://doi.org/10.5194/hess-2023-204-RC2 -
AC3: 'Reply on RC2', Saket Pande, 06 Oct 2023
We thank the referee once again for a critical take on our manuscript and look forward to further engaging the referee on clarifying our approach. The authors still find it difficult to understand why the use of the empirical equation of species richness is inappropriate. The authors of this manuscript may not be as conversant as the referee on the epistemological and ontological meanings of the research but we will do our best to respond to this comment which pertains to causality vs correlation and prediction vs assessment. First we would like to present our argument for why we used the SDR equation and then present a constructive way forward to address the comment of the referee.
Species Discharge relationships (SDR) have been derived based on data of large basins (>500 sq km) globally to explain long run riverine fish species richness (FSR) as a function of discharge and other variables (Schipper and Barbarossa, 2022 and references within). Our study basin is >10000 sq km, at which scale “for riverine fishes, discharge is a key variable explaining differences in species richness” (quoting Schipper and Barbarossa, 2022). The explanatory power of discharge is, in our interpretation, of the long run diversity, i.e. after several years of alteration at large spatial scales. We use the equation therefore to assess changes for the same basin (keeping area and latitude constant to incorporate fixed effect of the basin being the same). The is very similar to the use of Budyko curve derived from basin data sets across the globe in hydrology, e.g. for space for time substitution to assess impacts of changes in precipitation on rainfall partitioning in basins in the long run (Bouaziz et al., 2022). We understand the concern of the referee not to confuse correlation for causation. For example, occurrence of solar flares may be correlated with earthquakes but the former does not explain the latter. However discharge is not synonymous with solar flares if FSR were earthquakes in our case, because discharge does explain variability in FSR.
We had also clarified in our new version of the manuscript that we are not interested in predicting FSR and that this manuscript is not just about FSR. We can further clarify that the idea here is to assess differences in species richness in the long run (or how it varies with different reservoir induced discharge scenarios) based on a SDR for 16 possible future realities if each occur independently only once (space for time substitution and as a virtual experiment). Our use of FSR should be seen more as a means to assess the capacities to have certain levels of diversity in various reservoir scenarios – in case of damming this means loss of diversity (see e.g. Zarfl et al., 2019; Ganassin et al., 2021) while the case of less dams leads to higher capacity and species recovery (see e.g. Bednarek, 2001; Hansen and Hayes, 2012). Such evidence therefore also supports our intended use of the SDR that dams alter flow regimes that result in loss of diversity in the long run (or removal of dams leads to revitalization).
We understand and respect the sensitivity of the referee to the way we have used FSR in our manuscript. For our scale of study, FSR serves as an indicator of an important ecological service that quantifies environmental quality as seen through the lens of biodiversity and how its provisioning varies with more or less dams in the same basin. As also suggested by the referee, we therefore propose to rescale our estimate of FSR to define an index between 0 and 1, by dividing the estimated FSR of a scenario with one or more dams with the FSR of the scenario when there are no dams and call it “SDR based habitat integrity index.” Closer to 1 would mean higher habitat integrity. Our conclusions would remain unaffected, except that they would be interpreted in terms of the defined habitat integrity index as the indicator of environmental quality.
References:
Bednarek, A (2001). Undamming Rivers: A Review of the Ecological Impacts of Dam Removal. Environmental Management 27, 803–814. https://doi.org/10.1007/s002670010189
Bouaziz, L. J. E., Aalbers, E. E., Weerts, A. H., Hegnauer, M., Buiteveld, H., Lammersen, R., Stam, J., Sprokkereef, E., Savenije, H. H. G., and Hrachowitz, M. (2022). Ecosystem adaptation to climate change: the sensitivity of hydrological predictions to time-dynamic model parameters, Hydrol. Earth Syst. Sci., 26, 1295–1318, https://doi.org/10.5194/hess-26-1295-2022.
Ganassin, M J M, Muñoz-Mas, R, de Oliveira F J M, Muniz, C M, dos Santos, N C L, García-Berthou, E, Gomes, L C (2021). Effects of reservoir cascades on diversity, distribution, and abundance of fish assemblages in three Neotropical basins, Science of The Total Environment, Volume 778, https://doi.org/10.1016/j.scitotenv.2021.146246.
Hansen JF, Hayes DB (2012) Long-term implications of dam removal for macroinvertebrate communities in Michigan and Wisconsin rivers, United States. River Research and Applications 28: 1540–1550.
Schipper, A. M. & Barbarossa, V. (2022). Global congruence of riverine fish species richness and human presence. Global Ecology and Biogeography, 31, 1501–1512. https://doi.org/10.1111/geb.13519.
Zarfl C, Berlekamp J, He F, Jähnig SC, Darwall W, Tockner K (2019). Future large hydropower dams impact global freshwater megafauna. Sci Rep. Dec 6;9(1):18531. doi: 10.1038/s41598-019-54980-8. PMID: 31811208; PMCID: PMC6898151.
Citation: https://doi.org/10.5194/hess-2023-204-AC3 -
RC5: 'Reply on AC3', Anonymous Referee #1, 10 Oct 2023
Dear authors,
I appreciate your effort to develop an argument for your perspective on why it is appropriate and sufficient to use the SDR approach to model the effects of local flow changes on fish biodiversity, and to constructively provide some options.
I also understand the authors' urge to find a way to extend this study to the "environmental" domain: otherwise there would be no point in claiming in the title that this is an "economic and environmental" assessment: there wouldn't be two axes of tradeoff analysis. However, since it is treated as a central part of the work, it needs to be rigorously revised. I cannot accept the authors' argument that this paper is not about FSR, or that this discussion is about "the reviewer's sensitivity to the way we used FSR in our manuscript". On the contrary, scientific novelty, merit and rigor must be appropriately addressed following the authors' decision to use biodiversity as the "environmental" component of their study.
I find your reference to Budiko fortunate. It may be a good example to help clarify the difference between correlation and causation. Let's do a mental experiment: A researcher, using the available global data of actual evapotranspiration (ETa) and runoff from energy-limited basins (that is, where PET < precipitation), performs a regression between these two variables and finds that there is a significant correlation of these fluxes, and publishes the results about this correlation. This is indeed a valid correlation (not spurious like earthquakes and solar flares) showing that around the world, basins with higher runoff tend to have more ETa.
Later, another study in a single basin where reduced streamflow has been observed in a river reach, attempts to estimate changes in ET in that basin. This authors find the previously published regression model and use it to estimate the basin's reduction in ETa. The authors argue that this is a valid scientific result because there is a proven global correlation between these two fluxes. They also propose an "ET-R informed index" to assess the change in ET in this basin.
[As you are probably aware, based on the understanding of the mechanisms that determine the interaction of water budget components, a decrease in runoff may be the result of increased ET at local scales for instance s water is used in irrigation, the opposite of what the correlation implies. It is therefore incorrect to assume that because there is a correlation between ET and runoff across geographic areas that there is an implied causality, and more importantly, that the direction of the correlation stands outside the domain of the original analysis].
This hypothetical scenario is basically analogous to the case the authors make. Your assumption of using an SDR equation to assess changes in biodiversity goes beyond the rationale of the original regression. Correlations are used to exploit mutual information between variables (usually proxies) to identify patterns, but do not necessarily imply causality between variables or even mechanisms of interaction. There may be many reasons why runoff and fish biodiversity exhibit mutual information across large geographic areas and evolutionary scales: factors that determine large runoff and variability patterns, such as the size and heterogeneity of freshwater habitats, do indeed influence the diversification of a fish in a basin. These processes should not be confused with short-term and small-scale effects. Smaller-scale changes in fish assemblages may indeed be related to stressors such as flow alteration, but typically in the context of combined effects of other spatially dependent factors (which may be even more important), such as reservoir effects of fragmentation and loss of access to functional habitats, water quality degradation, changes in sediments and nutrients regime, geomorphological changes, etc.
Most of the scientific literature that the authors cite to support their "intended use of the SDR that dams alter flow regimes resulting in long-term loss of diversity" actually disproves their point: these studies look spatially at multiple factors affecting fish biodiversity, and not surprisingly, none make claims as extreme and sensational as those implied by the FSR equation used in this study, of reductions >70% in fish biodiversity (~100 species) at the basin scale. Likewise, according to your recommended references, Barbarossa et al. document a positive correlation between human transformation and fish biodiversity. By the same logic, should your study argue that the current fish biodiversity in the Cauvery has been positively influenced by the reservoirs in the basin? Why cherry pick factors?
I hope at this point you realize that extrapolating the purpose of a correlation analysis is not a straightforward process as you claim. Your suggestion to rescale the FSR analysis into an "SDR-based habitat integrity" is then misleading; it aims to mask this fundamentally flawed equivalence.
Let me insist. As it stands, the study provides an assessment of changes in some aspects of freshwater habitat integrity, not fish biodiversity. I'd respectfully encourage the authors to withdraw the current submission and reformulate the paper to explore the trade-offs in those terms, and avoid stretching the results to claim that this study incorporates fish biodiversity.
Citation: https://doi.org/10.5194/hess-2023-204-RC5 -
AC6: 'Reply on RC5', Saket Pande, 13 Oct 2023
We thank the referee for a thoughtful and detailed response. We are glad to see the reference to Schipper and Barbarossa (2022) that we have cited in this discussion. This helps us to further clarify the use of the methodology below and discuss its novelty, merit and rigor. We look forward to continuing the discussion.
Our manuscript has highlighted that it provides a proof of concept of applying a novel methodology to analyse a tradeoff between two dominant ecosystem services in Upper Cauvery under plausible changes in reservoir configurations. As also stated in our response to referee 3, the novelty is the tradeoff analysis that is unique to India based on model simulations that incorporates model simulations at daily scale. Daily scale simulations are necessary for the analysis presented because the two indicators of ecosystem services chosen, FSR and agricultural production, need calculations at daily scale and therefore does the tradeoff analysis. Our motivation is to use FSR as an indicator of environmental quality and not to predict fish biodiversity/ species richness. Further, in our revised manuscript we will discuss the limitations such as that the equation used for FSR is a statistical one and does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related interventions, amongst other discussion points below.
We have therefore been very careful on how to use the equation before implementing this equation and have been clear about the motivation to use it. This choice of regression equation was suitable for our analysis since our underlying model does not consider water quality (and others aspects) and therefore our scenarios only consider possible combinations of current four reservoirs in the basin that dominantly lead to changes in streamflow. “for riverine fishes, discharge is a key variable explaining differences in species richness” (quoting Schipper and Barbarossa, 2022) therefore applies in our case and useful for us to use discharge characteristics as a means to assess variability of FSR based indicator of environmental quality. Taking solar flares – earthquake example, we would be unable to suggest whether one can explain the other but can only correlate. Therefore unless it is possible to state that species richness explains variability in streamflow characteristics, our use of using discharge characteristics to explain variability in FSR as an indicator of environmental quality is valid.
This manner and use of the FSR equation was confirmed in private communication with Dr. Yoshikawa (Yoshikawa et al., 2014) before and after we applied this method to assess environmental quality for various scenarios as we sought advice by experts on whether our application is appropriate. What further demonstrates our careful use is the scale at which it has been applied. The equations has been estimated based on a global data sets for basins that also have basins similar to upper Cauvery. The data of upper Cauvery lies in the span of the data used for regressing the equation, so we are interpolating within the range of FSR that can be modelled by the equation. Further, we donot claim anything other than what the equation has been made for and do not go for interpreting the dynamics of change in FSR. Just as we would do in the case of Budyko curve, where we would not use it to interpret how irrigation may explain this relationship but only use it, for example, for assessing changes long run rainfall partitioning to runoff under climate change for pristine basins without any irrigation. Therefore we emphasize its use is appropriate for large time/spatial scales and for interpolation, only for describing variability in FSR based indicator of environmental quality as a function of streamflow characteristics.
Equations such as Budyko curve and equation 5 are in particular useful for space for time substitution analysis, i.e. to imagine that a basin undergoes a change with respect to its independent variable and how that changes the outcome variable. In terms of data, on the basis of which the equations have been estimated, it means to find a basin very similar to the basin under study in terms of its changed independent variables (or characteristics) keeping all other remaining/unknown variables as constant and use the outcome of the identified similar basin to assess change. This is how we are using equation 5: from within the data (now made ‘dense’ by interpolation by the equation) we are looking for basins similar to upper Cauvery with respect to its streamflow characteristics as it changes with changing reservoir combinations, keeping all other remaining/unknown variables constant.
If the effect of unknown variability on outcome (here FSR), which we are assuming to be zero under change, is larger than known variability (due to reservoir combination) in this space for time substitution (time being loosely associated with scenarios happening one at a time in the long run) then indeed we cannot rely on the changes explained by equation 5 because the parameters of equation 5 may no longer be significant. Alluding to the referee’s comment on human footprint and fragmentation, these variables are the variables unknown to equation (5) (and donot change by construct/assumption of our model/methodology) and can lead to bias (Schipper and Barbarossa 2022). However Schipper and Barbarossa (2022) conclude that “Although the directions of the relationships between fish species richness and the other covariates were mostly consistent between the different model structures .., we found differences in the effect sizes of the covariates between the default model and the main basin model.” (quote from Schipper and Barbarossa, 2022). This implies that how streamflow explains changes in FSR remains unchanged.
We acknowledge the limitation of equation 5 that in explaining the variability in FSR it does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related intervention. Same holds for our model. We cannot verify what FSR values are for the hypothetical scenarios since they are counterfactuals. But based on the data used for estimating equation 5, such a drop is possible, as explained before, when unobserved/unknown variables remain constant across the scenarios. Also, the observed FSR around the gauging station where equation 5 is being used to assess the environmental quality of various scenarios via FSR is around 25 (estimated to be 30 by equation 5 for the current state as the scenario with all reservoirs in place - the only scenario that is factual). And by using the relative index proposed, our analysis densensitizes the use of absolute numbers of FSR (and absolute changes) and thus focus more on relative ranking of one scenario in the tradeoff space in terms of proxies of environmental quality and agriculture. Therefore to answer “By the same logic, should your study argue that the current fish biodiversity in the Cauvery has been positively influenced by the reservoirs in the basin?”, our methodology will not do so given its assumptions to generate the reservoir scenarios/counterfactuals.
Our study is first of its kind and its methodology can be made more complicated in follow up studies (and beyond the scope of the current study), e.g. incorporating water quality and other non-dam related aspects, a continuum of hypothetical reservoir combinations upstream, more ecosystem services, utility/profit maximization based on obtained production set of the basin and more. To incorporate any of these would defeat the purpose of this study to introduce the simple methodology as a first step. We have therefore proposed in our revision to discuss the limitations and improvements that are possible, e.g. in our use of using equation 5, emphasizing its use not for predicting FSR but for an index of environmental health in a two dimensional tradeoff analysis of dominant ecosystem services that are affected by plausible reservoir combination scenarios dominantly affect streamflow.
Citation: https://doi.org/10.5194/hess-2023-204-AC6
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AC6: 'Reply on RC5', Saket Pande, 13 Oct 2023
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RC5: 'Reply on AC3', Anonymous Referee #1, 10 Oct 2023
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AC3: 'Reply on RC2', Saket Pande, 06 Oct 2023
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RC2: 'Reply on AC2', Anonymous Referee #1, 05 Oct 2023
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AC2: 'Reply on AC1', Saket Pande, 04 Oct 2023
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AC1: 'Reply on RC1', Saket Pande, 04 Oct 2023
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RC3: 'Comment on hess-2023-204', Anonymous Referee #2, 07 Oct 2023
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
Citation: https://doi.org/10.5194/hess-2023-204-RC3 -
AC4: 'Reply on RC3', Saket Pande, 11 Oct 2023
We thank the referee for the constructive comments and look forward to any further discussion. We agree with the simplistic visualization of the tradeoff, it being the main contribution of the paper, and we will provide the clarifications as needed in our revised manuscript.
Response to comment 1: We agree that it is a simple model where land allocation remains constant and we are only discussing what production is possible within the basin given this assumption. We are therefore still not engaging with utility/profit maximization since we only define our production set and calibrating utility/profit functions based on what is being currently observed is a next step. We will discuss these assumption in the light of literature mentioned.
Response to comment 2: We agree that if the basin is large enough to dominate the domestic market in terms of production of certain crops then shocks in supply can adversely affect the prices. Please note that crops specially cereals and pulses are also consumed in the basin while coffee, spices and few horticultural crops are exported outside the basin. In either case markets are well developed in the basin and well connected to other domestic and international markets outside the basin. In case of less produce they would compensate from neighboring places unless there is a significant supply shock.
Response to comment 3: We agree and have acknowledged in the manuscript that dams affect various ecosystem services and that we used agriculture because it dominates the economic value produced in the basin. We have also highlighted that a comprehensive economic and non-economic valuation of all these services is needed but requires extensive data and resources. It is also beyond the scope of the current study and is left for future studies.
Citation: https://doi.org/10.5194/hess-2023-204-AC4
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AC4: 'Reply on RC3', Saket Pande, 11 Oct 2023
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RC4: 'Comment on hess-2023-204', Anonymous Referee #3, 09 Oct 2023
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.
Citation: https://doi.org/10.5194/hess-2023-204-RC4 -
AC5: 'Reply on RC4', Saket Pande, 11 Oct 2023
We thank the referee for the constructive comments. Below are our responses and will provide the clarifications as discussed in our revised manuscript. We look forward to further discussing our manuscript.
Response to comment 1: We will discuss the limitations such as that the equation used is a statistical one and does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related interventions and how it builds further on the work of Iwasaki et al. (2012) and Yoshikawa et al. (2014) in the revised version of the manuscript.
The use of term validation was unfortunate. We are, like Yoshikawa et al., (2014) applying the equation to our basin and extending their application of Iwasaki et al. (2012) for space for time substitution (by time here we mean occurrence of different scenarios). As have already acknowledged, our manuscript is not just about FSR and its prediction but it is to use it as an indicator to assess how environmental quality varies with different reservoir configurations and how it trades off with agricultural production. This is also in line with the use of SDR equations to explain variations in FSR as an indicator of environmental quality.
Therefore the innovation indeed lies not in applying the same equation but building on Iwasaki et al. (2012) and Yoshikawa et al. (2014) to apply the equation for various configurations of existing dams and how that is used in the tradeoff analysis. Kindly note that Yoshikawa et al. (2014) provided a sensitivity analysis based on reducing flows of a certain basin by certain percentage, suggested consideration of sensitivity analysis in future studies. The construction of our production possibility frontier in this regard can be seen as a sensitivity analysis where various combinations leads to scenarios of streamflow alterations due to dam regulation, irrigation and other uses and how FSR based on equation 5 is sensitive to it. To keep the index of environmental quality comparable between the scenarios (where reservoirs are placed or removed in combinations upstream), we only applied the equation at the most downstream gauge. We will provide sensitivity of the conclusions derived based of the tradeoff/PPF analysis when data for different time periods are considered in our revised manuscript.
We acknowledge that equation 5 is based on observed data from a global data set (including our latitude but none in India) and the equation reports only significant coefficients that indeed may change if more data is added to the regression analysis. We agree that if the data points for our FSR assessment, which are in the ranges of the data used to derive equation 5, were outside the domain of the regression then the regression results are less reliable. We will acknowledge it. Further given our motivation to use it only as an indicator of environmental quality to compare across the scenarios, we will rescale it and allude to it as “SDR based habitat integrity index,” so that it used only as a means to compare one scenarios with the other in relative terms of the provision of an ecosystem service rather than FSR.
This manner of our application of equation that acknowledges its limitations was also confirmed in private communication with Dr. Yoshikawa before and after we applied this method to assess environmental quality for various scenarios as we sought advice by experts on whether our application is appropriate.
Response to comment 2: We will change the terminology to “configuration of existing dams.” As however could be noted that we have already highlighted the strength as suggested that it can extended to full spatial configuration of dams.
Response to comment 3: mm/day is obtained by dividing volumetric flow rate by the area contributing flow to the gauge station. We will add this clarification in our revised manuscript.
Response to comment 4: I believe that this is a mistake made in our response to call Figure 6 a hydrograph. We will reinsert mean annual flow in Table 2 and replace current Figure 6 with mean monthly flows for all 16 combinations. The time period for the analysis of 16 scenarios is 2011-2016 due to availability of relevant agricultural data.
Response to comment 5: We agree that cereals may have more intrinsic value to farmers, even if it has low market value, than the monetary value offered by horticulture crops. What we have assumed is that farmers can always buy cereals in the market at prices lower than the prices at which they sell horticulture crops and still save. Therefore implicit is the assumption that markets are well connected to other domestic (out of basin) and international markets and local scarcity of certain crops does not significantly affect its prices.
Response to comment 6: We will add the explanation as suggested, also equation 4 is missing a summation size in front of the ET ratio which we will amend. The equation presents end of season yield as a fraction of optimal yield that depends on how much daily evaporation is accumulated by the crops over the season compared to the respective evaporation demands (optimal evaporation). Yearly production value is obtained by multiplying average area of each crop with average simulated yields and prices over 2011-2016.
Response to comment 7: Kindly note that variables FL2 (coefficient of variation of mean frequency of low flow per year) and TL2 (coefficient of variation in the Julian date of the annual minimum flow) in equation 5 are coefficient of variations that need multiple year simulations of flow at daily scale. Also, the reliability of various other variables in the equation increase if more number of years are used. Due to limitation on the years for which crop prices were available, we used 6 years of simulations 2011-2016 to estimate flow related quantities needed in equation 5.
Response to comment 8: To our knowledge such a tradeoff analysis is unique to India based on model simulations that incorporates model simulations at daily scale. Daily scale simulations are necessary for the analysis presented because both FSR and agricultural production need calculations at daily scale. Please see above.
As mentioned in our response to the previous comment, FSR needs multi-year simulations of flows at daily scale, e.g. in addition to FL2 and TL2, TH3 (maximum proportion of the year (number of days /365) during which floods have occurred) also needs daily scale simulations. Mean annual flows are also annual average of daily flows and in case of multiple years, these calculations are done so by averaging over the years. Also in response to comment 6, please note that evaporation deficit that provides an estimate of yield are based on calculations of evaporation at daily scale. These also need model simulations at daily scale.
The use of daily scale calculations are also unique because the daily scale model setup allows us to substitute space for time when using SDR based FSR and construct alternate realities of how agricultural production would trades off with it for various reservoir combinations. It is therefore assumed that all other potential factors remain fixed in these scenarios because the basin remains the same, except for the implications that various reservoir combinations have for base flow.
Response to comment 9: We agree, our intention was not to cite all but we will few more recent studies on multiple dams
Response to comments 10, 11 and 13: We will do as suggested.
Response to comment 12: We will refer to the supplementary material for calibration and validation and remove section 3.1 (since similar text also appears in the supplementary material)
Response to comment 14: We can adapt the size. Kindly note that a command area of a reservoir refers to the irrigation area commanded by the reservoir. We will define this when command area is used for the first time.
Citation: https://doi.org/10.5194/hess-2023-204-AC5
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AC5: 'Reply on RC4', Saket Pande, 11 Oct 2023
Status: closed
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RC1: 'Comment on hess-2023-204', Anonymous Referee #1, 04 Oct 2023
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.
Citation: https://doi.org/10.5194/hess-2023-204-RC1 -
AC1: 'Reply on RC1', Saket Pande, 04 Oct 2023
Thank you for the opportunity to discuss the comments in this interactive session. Please see below our first response to the referee comments. We are looking forward to a fair and constructive discussion on the merit of this manuscript by further clarifying and responding to subsequent comments of the referee.
Response to comment 1. Our revised manuscript clearly states that this paper is a first study of its kind to assess tradeoff between two ecosystem services as indicated by income from agricultural production and fish species richness in Indian context. This study sacrifices high accuracy in predicting fish species richness for modelling tradeoffs between agricultural production and fish species richness (FSR). The limited prediction accuracy has been acknowledged and it has been highlighted that this needs more field campaigns and left for future research.
However we would like to highlight that our model of FSR is not as simplistic as the referee suggests, that it is only a function of mean flow. It is not. Even though we agree that we are modelling first order variation of FSR but it is with various characteristics of stream flow variation such as of low flows, high flows and its timing (please see equation 5) in addition to log of mean flow but also log of catchment area. This falls in line with extensive literature on the use of species discharge relationships (SDR) and species area relationships (SAR) in assessing variability in biodiversity as a function of discharge at the scales of our study (>500 sq. km and averaged over time). See e.g. Schipper and Barbarossa (2022) and extensive recent related literature on drivers of variability in biodiversity cited within along these lines that indeed suggest that discharge (not just mean but other characteristics as well) and area have large power in explaining FSR. Other factors such as human pressure may influence higher order effects in these relationships. Therefore we do claim significant changes in stream flows characteristics would lead to significant changes in FSR using a synthesis of such effects explored by experts via the equation 5.
Response to comment 2. We agree that we should not use the term validation and it was an unfortunate use of the term. We will refrain from its use and constraint ourselves to the use of empirical equation.
Response to comment 3.The construction of the convex hull is indeed due to the discrete but realistic nature of the problem. There may be a continuum but that continuum is neither real (because we only have the mentioned four reservoirs in the basin and therefore only 16 possible combinations of realities depending on how these existing reservoir could be removed in the future) nor is in the scope of the current study as we have already highlighted in the current study. Given only finite amount of points, creating a convex hull to represent a convex production set makes minimal assumptions and is consistent with the economics literature (see e.g. Ginsburgh and Keyzer, 1997). We can further expand along the above line in our revised manuscript.
Response to comment 4. The modelling additions we have made are in response to the referee comments which we believe is fair also for this paper to be complete on its own.
Response to comment 5. Our model is adequate because mean absolute error of simulated when compared to observed is low: 0.71 to 2.92 (106 m3 day-1) compared to mean annual flows > 17 (106 m3 day-1), meaning that on average the absolute error is one or two orders of magnitude smaller than mean annual flows. NSE ranges between 0.51 and 0.73 (mostly > 0.6 for reservoir operations; please see supplementary material). It is because of this that we state that the model is adequate, especially since it has daily reservoir operations modelled within, which is a difficult modelling task.
We acknowledged such a limitation as no model is perfect and the model can improve in performance. Currently the reservoirs operatiosn at daily scale are based on trigonometric functions that do not incorporate incidental dam specific releases but only incorporates water demand by various command areas as the dominant driver of reservoir releases. Accommodating dam specific water releases might improve the simulation of intra-monthly variability in streamflow (see its discussion in Ekka et al. 2022). Whether this leads to changes in the conclusions drawn based on the possibility frontier shown in Figure 12 is beyond the current scope but even if we assume log effects of mean annual flow on FSR, changes in flows of one or two order would in log scale not affect the conclusions drawn (since FSR is a function of log of mean flows and other streamflow characteristics). Therefore reservoir configuration that brings about significant changes in streamflow characteristics (not one or two order of magnitude lower or higher than mean flows) would still drastically influence FSR and therefore for it to remain a pareto superior choice, it should significantly add more economic value. Reservoirs that significantly alter flow regimes but do not add significant value should be discouraged since it would be a pareto inferior choice, which is one of main conclusions drawn.
Citation: https://doi.org/10.5194/hess-2023-204-AC1 -
AC2: 'Reply on AC1', Saket Pande, 04 Oct 2023
Here by the references of our response:
Schipper, A. M. & Barbarossa, V. (2022). Global congruence of riverine fish species richness and human presence. Global Ecology and Biogeography, 31, 1501–1512. https://doi.org/10.1111/geb.13519
Ginsburgh, V. I. C. T. O., & Keyzer, M. A. (1997). The structure of applied general equilibrium models. The MIT Press.
Citation: https://doi.org/10.5194/hess-2023-204-AC2 -
RC2: 'Reply on AC2', Anonymous Referee #1, 05 Oct 2023
The authors claim that this is a first-time assessment and that low precision is acceptable for such a study. While this may be a valid point, it actually distracts from the central point of the comment. I must clarify that the issue is not the precision of the study, but rather the fundamental epistemological inadequacy of the proposed approach. My central point is that a model developed to assess variability in biodiversity is not equivalent to a predictive model to explore causality between processes (such as how changes in flows can cause changes in biodiversity).
The results presented highlight the unreasonableness of the proposed apprach. According to the manuscript, the basin should have already experienced the extinction of ~100 fish species due to the allocation of water for irrigation, however no evidence of such an ecological disaster is presented. Conversely, if some reservoirs are removed, will numerous fish species appear in this basin? This may sound like a caricature, but unfortunately it is at the heart of the analysis presented. Again, this is a clear misuse of a regression model and the published literature on SDR and SAR; it is fundamentally a failure to distinguish between correlation and causation.
As it stands, the study provides an assessment of change in some aspects of freshwater habitat integrity, not fish biodiversity. I'd respecfully encourage the authors to consider declining the current submission, and reformulating the paper to explore the trade-offs in those terms.Citation: https://doi.org/10.5194/hess-2023-204-RC2 -
AC3: 'Reply on RC2', Saket Pande, 06 Oct 2023
We thank the referee once again for a critical take on our manuscript and look forward to further engaging the referee on clarifying our approach. The authors still find it difficult to understand why the use of the empirical equation of species richness is inappropriate. The authors of this manuscript may not be as conversant as the referee on the epistemological and ontological meanings of the research but we will do our best to respond to this comment which pertains to causality vs correlation and prediction vs assessment. First we would like to present our argument for why we used the SDR equation and then present a constructive way forward to address the comment of the referee.
Species Discharge relationships (SDR) have been derived based on data of large basins (>500 sq km) globally to explain long run riverine fish species richness (FSR) as a function of discharge and other variables (Schipper and Barbarossa, 2022 and references within). Our study basin is >10000 sq km, at which scale “for riverine fishes, discharge is a key variable explaining differences in species richness” (quoting Schipper and Barbarossa, 2022). The explanatory power of discharge is, in our interpretation, of the long run diversity, i.e. after several years of alteration at large spatial scales. We use the equation therefore to assess changes for the same basin (keeping area and latitude constant to incorporate fixed effect of the basin being the same). The is very similar to the use of Budyko curve derived from basin data sets across the globe in hydrology, e.g. for space for time substitution to assess impacts of changes in precipitation on rainfall partitioning in basins in the long run (Bouaziz et al., 2022). We understand the concern of the referee not to confuse correlation for causation. For example, occurrence of solar flares may be correlated with earthquakes but the former does not explain the latter. However discharge is not synonymous with solar flares if FSR were earthquakes in our case, because discharge does explain variability in FSR.
We had also clarified in our new version of the manuscript that we are not interested in predicting FSR and that this manuscript is not just about FSR. We can further clarify that the idea here is to assess differences in species richness in the long run (or how it varies with different reservoir induced discharge scenarios) based on a SDR for 16 possible future realities if each occur independently only once (space for time substitution and as a virtual experiment). Our use of FSR should be seen more as a means to assess the capacities to have certain levels of diversity in various reservoir scenarios – in case of damming this means loss of diversity (see e.g. Zarfl et al., 2019; Ganassin et al., 2021) while the case of less dams leads to higher capacity and species recovery (see e.g. Bednarek, 2001; Hansen and Hayes, 2012). Such evidence therefore also supports our intended use of the SDR that dams alter flow regimes that result in loss of diversity in the long run (or removal of dams leads to revitalization).
We understand and respect the sensitivity of the referee to the way we have used FSR in our manuscript. For our scale of study, FSR serves as an indicator of an important ecological service that quantifies environmental quality as seen through the lens of biodiversity and how its provisioning varies with more or less dams in the same basin. As also suggested by the referee, we therefore propose to rescale our estimate of FSR to define an index between 0 and 1, by dividing the estimated FSR of a scenario with one or more dams with the FSR of the scenario when there are no dams and call it “SDR based habitat integrity index.” Closer to 1 would mean higher habitat integrity. Our conclusions would remain unaffected, except that they would be interpreted in terms of the defined habitat integrity index as the indicator of environmental quality.
References:
Bednarek, A (2001). Undamming Rivers: A Review of the Ecological Impacts of Dam Removal. Environmental Management 27, 803–814. https://doi.org/10.1007/s002670010189
Bouaziz, L. J. E., Aalbers, E. E., Weerts, A. H., Hegnauer, M., Buiteveld, H., Lammersen, R., Stam, J., Sprokkereef, E., Savenije, H. H. G., and Hrachowitz, M. (2022). Ecosystem adaptation to climate change: the sensitivity of hydrological predictions to time-dynamic model parameters, Hydrol. Earth Syst. Sci., 26, 1295–1318, https://doi.org/10.5194/hess-26-1295-2022.
Ganassin, M J M, Muñoz-Mas, R, de Oliveira F J M, Muniz, C M, dos Santos, N C L, García-Berthou, E, Gomes, L C (2021). Effects of reservoir cascades on diversity, distribution, and abundance of fish assemblages in three Neotropical basins, Science of The Total Environment, Volume 778, https://doi.org/10.1016/j.scitotenv.2021.146246.
Hansen JF, Hayes DB (2012) Long-term implications of dam removal for macroinvertebrate communities in Michigan and Wisconsin rivers, United States. River Research and Applications 28: 1540–1550.
Schipper, A. M. & Barbarossa, V. (2022). Global congruence of riverine fish species richness and human presence. Global Ecology and Biogeography, 31, 1501–1512. https://doi.org/10.1111/geb.13519.
Zarfl C, Berlekamp J, He F, Jähnig SC, Darwall W, Tockner K (2019). Future large hydropower dams impact global freshwater megafauna. Sci Rep. Dec 6;9(1):18531. doi: 10.1038/s41598-019-54980-8. PMID: 31811208; PMCID: PMC6898151.
Citation: https://doi.org/10.5194/hess-2023-204-AC3 -
RC5: 'Reply on AC3', Anonymous Referee #1, 10 Oct 2023
Dear authors,
I appreciate your effort to develop an argument for your perspective on why it is appropriate and sufficient to use the SDR approach to model the effects of local flow changes on fish biodiversity, and to constructively provide some options.
I also understand the authors' urge to find a way to extend this study to the "environmental" domain: otherwise there would be no point in claiming in the title that this is an "economic and environmental" assessment: there wouldn't be two axes of tradeoff analysis. However, since it is treated as a central part of the work, it needs to be rigorously revised. I cannot accept the authors' argument that this paper is not about FSR, or that this discussion is about "the reviewer's sensitivity to the way we used FSR in our manuscript". On the contrary, scientific novelty, merit and rigor must be appropriately addressed following the authors' decision to use biodiversity as the "environmental" component of their study.
I find your reference to Budiko fortunate. It may be a good example to help clarify the difference between correlation and causation. Let's do a mental experiment: A researcher, using the available global data of actual evapotranspiration (ETa) and runoff from energy-limited basins (that is, where PET < precipitation), performs a regression between these two variables and finds that there is a significant correlation of these fluxes, and publishes the results about this correlation. This is indeed a valid correlation (not spurious like earthquakes and solar flares) showing that around the world, basins with higher runoff tend to have more ETa.
Later, another study in a single basin where reduced streamflow has been observed in a river reach, attempts to estimate changes in ET in that basin. This authors find the previously published regression model and use it to estimate the basin's reduction in ETa. The authors argue that this is a valid scientific result because there is a proven global correlation between these two fluxes. They also propose an "ET-R informed index" to assess the change in ET in this basin.
[As you are probably aware, based on the understanding of the mechanisms that determine the interaction of water budget components, a decrease in runoff may be the result of increased ET at local scales for instance s water is used in irrigation, the opposite of what the correlation implies. It is therefore incorrect to assume that because there is a correlation between ET and runoff across geographic areas that there is an implied causality, and more importantly, that the direction of the correlation stands outside the domain of the original analysis].
This hypothetical scenario is basically analogous to the case the authors make. Your assumption of using an SDR equation to assess changes in biodiversity goes beyond the rationale of the original regression. Correlations are used to exploit mutual information between variables (usually proxies) to identify patterns, but do not necessarily imply causality between variables or even mechanisms of interaction. There may be many reasons why runoff and fish biodiversity exhibit mutual information across large geographic areas and evolutionary scales: factors that determine large runoff and variability patterns, such as the size and heterogeneity of freshwater habitats, do indeed influence the diversification of a fish in a basin. These processes should not be confused with short-term and small-scale effects. Smaller-scale changes in fish assemblages may indeed be related to stressors such as flow alteration, but typically in the context of combined effects of other spatially dependent factors (which may be even more important), such as reservoir effects of fragmentation and loss of access to functional habitats, water quality degradation, changes in sediments and nutrients regime, geomorphological changes, etc.
Most of the scientific literature that the authors cite to support their "intended use of the SDR that dams alter flow regimes resulting in long-term loss of diversity" actually disproves their point: these studies look spatially at multiple factors affecting fish biodiversity, and not surprisingly, none make claims as extreme and sensational as those implied by the FSR equation used in this study, of reductions >70% in fish biodiversity (~100 species) at the basin scale. Likewise, according to your recommended references, Barbarossa et al. document a positive correlation between human transformation and fish biodiversity. By the same logic, should your study argue that the current fish biodiversity in the Cauvery has been positively influenced by the reservoirs in the basin? Why cherry pick factors?
I hope at this point you realize that extrapolating the purpose of a correlation analysis is not a straightforward process as you claim. Your suggestion to rescale the FSR analysis into an "SDR-based habitat integrity" is then misleading; it aims to mask this fundamentally flawed equivalence.
Let me insist. As it stands, the study provides an assessment of changes in some aspects of freshwater habitat integrity, not fish biodiversity. I'd respectfully encourage the authors to withdraw the current submission and reformulate the paper to explore the trade-offs in those terms, and avoid stretching the results to claim that this study incorporates fish biodiversity.
Citation: https://doi.org/10.5194/hess-2023-204-RC5 -
AC6: 'Reply on RC5', Saket Pande, 13 Oct 2023
We thank the referee for a thoughtful and detailed response. We are glad to see the reference to Schipper and Barbarossa (2022) that we have cited in this discussion. This helps us to further clarify the use of the methodology below and discuss its novelty, merit and rigor. We look forward to continuing the discussion.
Our manuscript has highlighted that it provides a proof of concept of applying a novel methodology to analyse a tradeoff between two dominant ecosystem services in Upper Cauvery under plausible changes in reservoir configurations. As also stated in our response to referee 3, the novelty is the tradeoff analysis that is unique to India based on model simulations that incorporates model simulations at daily scale. Daily scale simulations are necessary for the analysis presented because the two indicators of ecosystem services chosen, FSR and agricultural production, need calculations at daily scale and therefore does the tradeoff analysis. Our motivation is to use FSR as an indicator of environmental quality and not to predict fish biodiversity/ species richness. Further, in our revised manuscript we will discuss the limitations such as that the equation used for FSR is a statistical one and does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related interventions, amongst other discussion points below.
We have therefore been very careful on how to use the equation before implementing this equation and have been clear about the motivation to use it. This choice of regression equation was suitable for our analysis since our underlying model does not consider water quality (and others aspects) and therefore our scenarios only consider possible combinations of current four reservoirs in the basin that dominantly lead to changes in streamflow. “for riverine fishes, discharge is a key variable explaining differences in species richness” (quoting Schipper and Barbarossa, 2022) therefore applies in our case and useful for us to use discharge characteristics as a means to assess variability of FSR based indicator of environmental quality. Taking solar flares – earthquake example, we would be unable to suggest whether one can explain the other but can only correlate. Therefore unless it is possible to state that species richness explains variability in streamflow characteristics, our use of using discharge characteristics to explain variability in FSR as an indicator of environmental quality is valid.
This manner and use of the FSR equation was confirmed in private communication with Dr. Yoshikawa (Yoshikawa et al., 2014) before and after we applied this method to assess environmental quality for various scenarios as we sought advice by experts on whether our application is appropriate. What further demonstrates our careful use is the scale at which it has been applied. The equations has been estimated based on a global data sets for basins that also have basins similar to upper Cauvery. The data of upper Cauvery lies in the span of the data used for regressing the equation, so we are interpolating within the range of FSR that can be modelled by the equation. Further, we donot claim anything other than what the equation has been made for and do not go for interpreting the dynamics of change in FSR. Just as we would do in the case of Budyko curve, where we would not use it to interpret how irrigation may explain this relationship but only use it, for example, for assessing changes long run rainfall partitioning to runoff under climate change for pristine basins without any irrigation. Therefore we emphasize its use is appropriate for large time/spatial scales and for interpolation, only for describing variability in FSR based indicator of environmental quality as a function of streamflow characteristics.
Equations such as Budyko curve and equation 5 are in particular useful for space for time substitution analysis, i.e. to imagine that a basin undergoes a change with respect to its independent variable and how that changes the outcome variable. In terms of data, on the basis of which the equations have been estimated, it means to find a basin very similar to the basin under study in terms of its changed independent variables (or characteristics) keeping all other remaining/unknown variables as constant and use the outcome of the identified similar basin to assess change. This is how we are using equation 5: from within the data (now made ‘dense’ by interpolation by the equation) we are looking for basins similar to upper Cauvery with respect to its streamflow characteristics as it changes with changing reservoir combinations, keeping all other remaining/unknown variables constant.
If the effect of unknown variability on outcome (here FSR), which we are assuming to be zero under change, is larger than known variability (due to reservoir combination) in this space for time substitution (time being loosely associated with scenarios happening one at a time in the long run) then indeed we cannot rely on the changes explained by equation 5 because the parameters of equation 5 may no longer be significant. Alluding to the referee’s comment on human footprint and fragmentation, these variables are the variables unknown to equation (5) (and donot change by construct/assumption of our model/methodology) and can lead to bias (Schipper and Barbarossa 2022). However Schipper and Barbarossa (2022) conclude that “Although the directions of the relationships between fish species richness and the other covariates were mostly consistent between the different model structures .., we found differences in the effect sizes of the covariates between the default model and the main basin model.” (quote from Schipper and Barbarossa, 2022). This implies that how streamflow explains changes in FSR remains unchanged.
We acknowledge the limitation of equation 5 that in explaining the variability in FSR it does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related intervention. Same holds for our model. We cannot verify what FSR values are for the hypothetical scenarios since they are counterfactuals. But based on the data used for estimating equation 5, such a drop is possible, as explained before, when unobserved/unknown variables remain constant across the scenarios. Also, the observed FSR around the gauging station where equation 5 is being used to assess the environmental quality of various scenarios via FSR is around 25 (estimated to be 30 by equation 5 for the current state as the scenario with all reservoirs in place - the only scenario that is factual). And by using the relative index proposed, our analysis densensitizes the use of absolute numbers of FSR (and absolute changes) and thus focus more on relative ranking of one scenario in the tradeoff space in terms of proxies of environmental quality and agriculture. Therefore to answer “By the same logic, should your study argue that the current fish biodiversity in the Cauvery has been positively influenced by the reservoirs in the basin?”, our methodology will not do so given its assumptions to generate the reservoir scenarios/counterfactuals.
Our study is first of its kind and its methodology can be made more complicated in follow up studies (and beyond the scope of the current study), e.g. incorporating water quality and other non-dam related aspects, a continuum of hypothetical reservoir combinations upstream, more ecosystem services, utility/profit maximization based on obtained production set of the basin and more. To incorporate any of these would defeat the purpose of this study to introduce the simple methodology as a first step. We have therefore proposed in our revision to discuss the limitations and improvements that are possible, e.g. in our use of using equation 5, emphasizing its use not for predicting FSR but for an index of environmental health in a two dimensional tradeoff analysis of dominant ecosystem services that are affected by plausible reservoir combination scenarios dominantly affect streamflow.
Citation: https://doi.org/10.5194/hess-2023-204-AC6
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AC6: 'Reply on RC5', Saket Pande, 13 Oct 2023
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RC5: 'Reply on AC3', Anonymous Referee #1, 10 Oct 2023
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AC3: 'Reply on RC2', Saket Pande, 06 Oct 2023
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RC2: 'Reply on AC2', Anonymous Referee #1, 05 Oct 2023
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AC2: 'Reply on AC1', Saket Pande, 04 Oct 2023
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AC1: 'Reply on RC1', Saket Pande, 04 Oct 2023
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RC3: 'Comment on hess-2023-204', Anonymous Referee #2, 07 Oct 2023
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
Citation: https://doi.org/10.5194/hess-2023-204-RC3 -
AC4: 'Reply on RC3', Saket Pande, 11 Oct 2023
We thank the referee for the constructive comments and look forward to any further discussion. We agree with the simplistic visualization of the tradeoff, it being the main contribution of the paper, and we will provide the clarifications as needed in our revised manuscript.
Response to comment 1: We agree that it is a simple model where land allocation remains constant and we are only discussing what production is possible within the basin given this assumption. We are therefore still not engaging with utility/profit maximization since we only define our production set and calibrating utility/profit functions based on what is being currently observed is a next step. We will discuss these assumption in the light of literature mentioned.
Response to comment 2: We agree that if the basin is large enough to dominate the domestic market in terms of production of certain crops then shocks in supply can adversely affect the prices. Please note that crops specially cereals and pulses are also consumed in the basin while coffee, spices and few horticultural crops are exported outside the basin. In either case markets are well developed in the basin and well connected to other domestic and international markets outside the basin. In case of less produce they would compensate from neighboring places unless there is a significant supply shock.
Response to comment 3: We agree and have acknowledged in the manuscript that dams affect various ecosystem services and that we used agriculture because it dominates the economic value produced in the basin. We have also highlighted that a comprehensive economic and non-economic valuation of all these services is needed but requires extensive data and resources. It is also beyond the scope of the current study and is left for future studies.
Citation: https://doi.org/10.5194/hess-2023-204-AC4
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AC4: 'Reply on RC3', Saket Pande, 11 Oct 2023
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RC4: 'Comment on hess-2023-204', Anonymous Referee #3, 09 Oct 2023
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.
Citation: https://doi.org/10.5194/hess-2023-204-RC4 -
AC5: 'Reply on RC4', Saket Pande, 11 Oct 2023
We thank the referee for the constructive comments. Below are our responses and will provide the clarifications as discussed in our revised manuscript. We look forward to further discussing our manuscript.
Response to comment 1: We will discuss the limitations such as that the equation used is a statistical one and does not consider other chemical and biological factors since it is solely based on assessment of changes in water quantity and not quality and not of impacts of other non-dam related interventions and how it builds further on the work of Iwasaki et al. (2012) and Yoshikawa et al. (2014) in the revised version of the manuscript.
The use of term validation was unfortunate. We are, like Yoshikawa et al., (2014) applying the equation to our basin and extending their application of Iwasaki et al. (2012) for space for time substitution (by time here we mean occurrence of different scenarios). As have already acknowledged, our manuscript is not just about FSR and its prediction but it is to use it as an indicator to assess how environmental quality varies with different reservoir configurations and how it trades off with agricultural production. This is also in line with the use of SDR equations to explain variations in FSR as an indicator of environmental quality.
Therefore the innovation indeed lies not in applying the same equation but building on Iwasaki et al. (2012) and Yoshikawa et al. (2014) to apply the equation for various configurations of existing dams and how that is used in the tradeoff analysis. Kindly note that Yoshikawa et al. (2014) provided a sensitivity analysis based on reducing flows of a certain basin by certain percentage, suggested consideration of sensitivity analysis in future studies. The construction of our production possibility frontier in this regard can be seen as a sensitivity analysis where various combinations leads to scenarios of streamflow alterations due to dam regulation, irrigation and other uses and how FSR based on equation 5 is sensitive to it. To keep the index of environmental quality comparable between the scenarios (where reservoirs are placed or removed in combinations upstream), we only applied the equation at the most downstream gauge. We will provide sensitivity of the conclusions derived based of the tradeoff/PPF analysis when data for different time periods are considered in our revised manuscript.
We acknowledge that equation 5 is based on observed data from a global data set (including our latitude but none in India) and the equation reports only significant coefficients that indeed may change if more data is added to the regression analysis. We agree that if the data points for our FSR assessment, which are in the ranges of the data used to derive equation 5, were outside the domain of the regression then the regression results are less reliable. We will acknowledge it. Further given our motivation to use it only as an indicator of environmental quality to compare across the scenarios, we will rescale it and allude to it as “SDR based habitat integrity index,” so that it used only as a means to compare one scenarios with the other in relative terms of the provision of an ecosystem service rather than FSR.
This manner of our application of equation that acknowledges its limitations was also confirmed in private communication with Dr. Yoshikawa before and after we applied this method to assess environmental quality for various scenarios as we sought advice by experts on whether our application is appropriate.
Response to comment 2: We will change the terminology to “configuration of existing dams.” As however could be noted that we have already highlighted the strength as suggested that it can extended to full spatial configuration of dams.
Response to comment 3: mm/day is obtained by dividing volumetric flow rate by the area contributing flow to the gauge station. We will add this clarification in our revised manuscript.
Response to comment 4: I believe that this is a mistake made in our response to call Figure 6 a hydrograph. We will reinsert mean annual flow in Table 2 and replace current Figure 6 with mean monthly flows for all 16 combinations. The time period for the analysis of 16 scenarios is 2011-2016 due to availability of relevant agricultural data.
Response to comment 5: We agree that cereals may have more intrinsic value to farmers, even if it has low market value, than the monetary value offered by horticulture crops. What we have assumed is that farmers can always buy cereals in the market at prices lower than the prices at which they sell horticulture crops and still save. Therefore implicit is the assumption that markets are well connected to other domestic (out of basin) and international markets and local scarcity of certain crops does not significantly affect its prices.
Response to comment 6: We will add the explanation as suggested, also equation 4 is missing a summation size in front of the ET ratio which we will amend. The equation presents end of season yield as a fraction of optimal yield that depends on how much daily evaporation is accumulated by the crops over the season compared to the respective evaporation demands (optimal evaporation). Yearly production value is obtained by multiplying average area of each crop with average simulated yields and prices over 2011-2016.
Response to comment 7: Kindly note that variables FL2 (coefficient of variation of mean frequency of low flow per year) and TL2 (coefficient of variation in the Julian date of the annual minimum flow) in equation 5 are coefficient of variations that need multiple year simulations of flow at daily scale. Also, the reliability of various other variables in the equation increase if more number of years are used. Due to limitation on the years for which crop prices were available, we used 6 years of simulations 2011-2016 to estimate flow related quantities needed in equation 5.
Response to comment 8: To our knowledge such a tradeoff analysis is unique to India based on model simulations that incorporates model simulations at daily scale. Daily scale simulations are necessary for the analysis presented because both FSR and agricultural production need calculations at daily scale. Please see above.
As mentioned in our response to the previous comment, FSR needs multi-year simulations of flows at daily scale, e.g. in addition to FL2 and TL2, TH3 (maximum proportion of the year (number of days /365) during which floods have occurred) also needs daily scale simulations. Mean annual flows are also annual average of daily flows and in case of multiple years, these calculations are done so by averaging over the years. Also in response to comment 6, please note that evaporation deficit that provides an estimate of yield are based on calculations of evaporation at daily scale. These also need model simulations at daily scale.
The use of daily scale calculations are also unique because the daily scale model setup allows us to substitute space for time when using SDR based FSR and construct alternate realities of how agricultural production would trades off with it for various reservoir combinations. It is therefore assumed that all other potential factors remain fixed in these scenarios because the basin remains the same, except for the implications that various reservoir combinations have for base flow.
Response to comment 9: We agree, our intention was not to cite all but we will few more recent studies on multiple dams
Response to comments 10, 11 and 13: We will do as suggested.
Response to comment 12: We will refer to the supplementary material for calibration and validation and remove section 3.1 (since similar text also appears in the supplementary material)
Response to comment 14: We can adapt the size. Kindly note that a command area of a reservoir refers to the irrigation area commanded by the reservoir. We will define this when command area is used for the first time.
Citation: https://doi.org/10.5194/hess-2023-204-AC5
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AC5: 'Reply on RC4', Saket Pande, 11 Oct 2023
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