Understanding dominant controls on streamflow spatial  variability to set up a semi-distributed hydrological  model: the case study of the Thur catchment

Dal Molin, Marco; Schirmer, Mario; Zappa, Massimiliano; Fenicia, Fabrizio

doi:https://doi.org/10.5194/hess-24-1319-2020

Articles | Volume 24, issue 3

https://doi.org/10.5194/hess-24-1319-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

Special issue:

Linking landscape organisation and hydrological functioning:...

https://doi.org/10.5194/hess-24-1319-2020

© Author(s) 2020. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 24, issue 3

Research article

|

20 Mar 2020

Research article |

| 20 Mar 2020

Understanding dominant controls on streamflow spatial variability to set up a semi-distributed hydrological model: the case study of the Thur catchment

Marco Dal Molin, Mario Schirmer, Massimiliano Zappa, and Fabrizio Fenicia

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Final revised paper (published on 20 Mar 2020)
Preprint (discussion started on 08 Mar 2019)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'Review Molin et al.', Anonymous Referee #1, 02 Apr 2019
- AC1: 'Reply to Anonymous Referee #1', Marco Dal Molin, 22 May 2019
RC2: 'Review', Lieke Melsen, 03 Apr 2019
- AC2: 'Reply to Dr. Lieke Melsen', Marco Dal Molin, 22 May 2019

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (further review by editor and referees) (29 May 2019) by Conrad Jackisch

AR by Marco Dal Molin on behalf of the Authors (09 Jul 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (22 Jul 2019) by Conrad Jackisch

RR by Anonymous Referee #3 (21 Aug 2019)

Suggestions for revision or reasons for rejection

Main comments
Dal Molin and colleagues submitted their revised manuscript entitled “Data analysis and model building for understanding catchment processes: the case study of the Thur catchment” to Hydrology and Earth System Sciences (HESS) Special Issue: Linking landscape organisation and hydrological functioning: from hypotheses and observations to concepts, models and understanding. The manuscript was substantially improved after major modifications following first iteration with reviewers and editors and I enjoyed reading it. However, I failed to identify a major scientific contribution in terms of processes understanding supported by hydrological interpretations, which makes me feel that authors are targeting the proposition of the regional modelling framework rather than the potential hydrological insights of the modelling exercise. In that sense, there are some issues that need to be addressed in order to achieve a replicable regional modelling framework, which are discussed in details below.

1) Section 3 still worries me a bit. First, the climate indices presented in Addor et al (2017) were selected to be representative in large-scale studies (e.g., CAMELS) where a large climatic gradient is the main control of catchment’s streamflow spatial variability. This is not necessarily a valid assumption for regional studies where climate variability (across space) is much smaller and variables are highly correlated (as per Fig 3). Second, the correlative nature of analysis underpinning decisions in the process-based hydrological modelling is a weakness. A more comprehensive metrics assessment would benefit the manuscript (see second point below). Third, the final “expert judgment” adds subjectiveness and undermines replicability of modelling framework. The other way around would be more intuitive – i.e., run the “expert judgment” prior in order to select relevant metrics and establish a process-based conceptual (see third point below) model taking accounting relevant specificities of study area (see point 4 below) and then the metrics assessment part.

2) Highly correlative nature of section 3: in the metrics assessment part (section 3), essentially, criteria for metric selection should go beyond correlation and represent similarity, dissimilarity, complementarity and/or importance of metrics and uncertainty. Bray-Curtis ordination or PCA could be helpful to understand data structure and complementarity and random forests could be used to calculate importance of metrics (see Kennard at al (2010) River Res Applic and Trancoso et al (2016) JoH for analytical examples). That would strength the analytical component of section 3.

3) A conceptual model would be helpful on section 3 to understand how selected metrics represent catchment processes.

4) Metrics from continental scale studies are a good starting point but should not be the final call – there are also other relevant metrics that could be tested such as phase-offset between the seasonal cycle in precipitation and potential evaporation – see Donohue et al (2010) JoH for details.

5) Manuscript structure is a bit unusual and not easy to navigate. It looks more like a thesis/report than a paper. Would be better to group all the methods and results together instead of presenting them separately on sections 3 and 4.

Other comments
Manuscript title is focused on methods rather than contribution. Currently title is a bit vague and not attractive as most hydrological modelling papers do data analysis and model building to understand catchment processes. Therefore, there is nothing new in the title and many potential readers might skip it if the title is kept the same (It is likely I would be one of them). I strongly recommend changing it focusing on the main contribution.
L1-2: “The development of semidistributed hydrological models that reflect the dominant processes controlling streamflow spatial variability is a challenging task” – Irrelevant, every science has challenges, otherwise would not be science.
The term “semidistributed” sometimes appears as semi-distributed. Better standardise.
Figure 1c: Forest and pasture are not easy to distinguish. Suggest use different colour for pasture.
Figure 7 uses line plots to show variability of model performance across study catchments. Choice of plot type is a bit misleading as line plots are usually used to show continuity across the x-axis, such as time-series plots. Suggest use only dots / jitters instead to avoid misinterpretation.
Most figures refer to metrics acronyms and a lot of back and forth is needed to find their definition and keep on track with reading. If authors do not want to redefine acronyms on figure captions, suggest present all the metrics in a table and cite table on figure captions.
P28 L2 – “varied considerably between catchments” – I think it should be among instead of between as several catchments are assessed.
P28 L7-8: “based on correlation analysis and expert judgment, we determined that climatic variables, especially the precipitation average, are the main controls the on streamflow average yearly values” – that’s well known and trivial. I would expect more elaborated hydrological insights. Main issue is that section 3 is not robust enough to offer in-depth interpretations.

References
Addor, N., Newman, A. J., Mizukami, N., and Clark, M. P.: The CAMELS data set: catchment attributes and meteorology for large-sample studies, Hydrol Earth Syst Sc, 21, 5293-5313, 10.5194/hess-21-5293-2017, 2017.
Donohue, R. J., Roderick, M. L., & McVicar, T. R. (2010). Can dynamic vegetation information improve the accuracy of Budyko’s hydrological model?. Journal of Hydrology, 390(1-2), 23-34.
Kennard, M. J., Mackay, S. J., Pusey, B. J., Olden, J. D., & Marsh, N. (2010). Quantifying uncertainty in estimation of hydrologic metrics for ecohydrological studies. River Research and Applications, 26(2), 137-156.
Trancoso, R., Larsen, J. R., McAlpine, C., McVicar, T. R., & Phinn, S. (2016). Linking the Budyko framework and the Dunne diagram. Journal of Hydrology, 535, 581-597.

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RR by Shervan Gharari (06 Sep 2019)

Suggestions for revision or reasons for rejection

Review of “Data analysis and model building for understanding catchment processes: the case study of the Thur catchment”

The paper tries to rationally build/infer an appropriate model suture based on data for Thur catchment. The authors have tried their best to answer to the reviewers’ comments. Reading the manuscripts, reviewers’ comments on the work and authors’ replies, I have a feeling that most of the reviewers’ concerns including myself is coming from the fact that the manuscript lack some fundamental direction which in turn might be the result of lack of proper research question. I personally don’t have any issue with the choice of signatures and correlation analysis. At the end of the day this is an engineering decision that any modeller will make and there is little to back them even if correlation exists (present or absence of causation).
The first question the authors should answer is the real purpose of this study. The spatial variability can have a wide range of interpretation. For example spatial variability to streamflow, or spatial variability to account for slope and aspect and etc. The authors should clearly make this case what spatial variability they are talking about (variability is case dependent). In this study, it is all about the streamflow as the models are calibrated against the streamflow. Streamflow is often easy to predict (calibrate). So the author should show the clear gain by moving toward spatially distributed input and spatial data such as slope and aspect, vegetation, geology, etc. In its current format the manuscript is lacking this direction. In the beginning, the manuscript promises to account for various processes but it is kind of missed in the manuscript or boiled down to very basic or common knowledge interpretation of the processes for streamflow simulation. Sth else that I don’t understand is the choice of model, for example from M0 to M1, if temperature is always above the threshold there will be no phase change for the precipitation. Then why even bother having model M0? The choice of the model is decided by the data itself (for example a land surface models have always snow component but if simulated for warm region they never simulate any snow). Moreover, the fact that the precipitation is first order control is also a bit obvious. If a multiplier is used to scale precipitation up and down it will be the most sensitive parameter of the model which in turn shows that the simulation is heavily affected by precipitation (or the driving force). Following that, I don’t see much translation of the observed processes into the model and I don’t see the added value of the added heterogeneity in the spatial models simulation etc. This can be further improved by the authors. Following this point, the choice of the models and the modeling looks a bit sloppy; in the sense that the continuum of model, spatial data is not very well visible. I think this can be further improved by the authors in the revised manuscript (maybe adding more model or stepwise introduction of spatial variability). I also suggest the author to have a more structural in to the paper by organizing the signatures that they use for model evaluation. These signatures can be grouped into four main categories (1) the signatures that are coming from the spatial heterogeneity of the topography, geology, soil, land cover etc. (2) the signature that are coming from the response that the model is built to replicate such as flow duration curve, flashiness, etc, (3) the signatures that are coming from the forcing to the system including the precipitation etc (4) hybrid such as runoff ratio. Each of these signatures have their own effect on the modeling result as some are used for calibration and some are not. I would suggest the author to segregate them more carefully in the test and analyses.
Is it surprising M0 can do well for the annual average? In my experience, a single reservoir with evapo-transpiration function can get the annual mean streamflow perfectly well, while it cannot get the correlation and variability.
I am interested to know how the authors dealt with the nested gauges. The information/correlation in nested gauges can be replicated. Howe the correlation plays in for these nested basin. Any comment on that.
Why did the authors have use NS and likelihood at the same time? What would it add…?
I think both in the modeling set up and also discussion a significant elements regarding the scale is missing. For example, have refereed to some work, Kuentz et al., 2017, that did a large sample hydrology. Is the manuscript really is about large sample hydrology and if the study area is following large sample hydrology or is it about how the Thur catchment is functioning and how it is modelled.
I would also suggest the author to look into the signature before and after bias correction or accounting for orographic effects. As mentioned earlier changing in forcing can drastically change the model output therefore it should also be noted how different the forcing becomes when is downscaled. Maybe I missed but how did the author include slope and aspect in their model?
I believe the manuscript can be an interesting contribution but in its current format it is far from being in perfect shape. The story needs to follow smoothly and the merit of this work should be better presented.
With kind regards
Shervan Gharari

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ED: Reconsider after major revisions (further review by editor and referees) (12 Sep 2019) by Conrad Jackisch

AR by Marco Dal Molin on behalf of the Authors (22 Oct 2019) Author's response Manuscript

ED: Referee Nomination & Report Request started (14 Nov 2019) by Conrad Jackisch

RR by Anonymous Referee #3 (19 Dec 2019)

Suggestions for revision or reasons for rejection

Authors have substantially improved the manuscript (MS) with regards to structure and readability. My comments have been mostly addressed and I believe the MS is in better shape for publication now. The discussion is not optimum yet and my suggestion is that it should undergo minor revision before publication.

Authors have developed some interesting explanations while answering reviewers' comments, which I think could be worthwhile to explore when revising the discussion. The points are highlighted below:

1) Sample size influence on approach choice - that would be useful to let people know and point out other approaches suitable for larger catchment samples:
"The possibility to use more advanced methods for metrics selection has been considered in the process of our study; the reason why we eventually selected a simple method is that the sample size of this study is relatively small. We are in fact limited to only 10 catchments. Studies that use complex regression techniques like random forests use a much larger sample of catchments; for example, the work proposed by Trancoso et al. (2016) deals with 355 catchments. Using such techniques risks to result in models that overfit the data, especially considering the fact that we would need to split the catchments in a calibration and a validation group. "

2) Other potential metrics that can suit best other regions"
"The number of signatures and indices proposed in literature to represent streamflow and climate is enormous (e.g. 120 metrics considered by Kennard et al. (2010)); therefore we had to limit our selection and we decided to use the one proposed by Addor et al. (2017) since we think they cover a wide range of characteristics of the time series that they synthetize."

3) These are interesting hydrological interpretations:
"Although it is known that precipitation has a strong control on average streamflow, this is not granted in some cases where, for example, regional groundwater flow alters the water balance of the catchments. "

"It is clear that when there is snow (as in this case) the model needs to have a snow component. It is less obvious (at least just by looking at hydrographs) how much of the differences in seasonality of the streamflow response between catchments are due to snow. Due to the large lag time between snowfall and hydrograph response it would be difficult to quantify this aspect without model experiments and the main result of the comparison between M0 and M1 is that the attribution of difference in seasonality (represented by the mean half streamflow date) is due to the spatial variability of snow processes."

"It is clear that precipitation is a first order control on streamflow. Less clear, at least before carrying out any analysis, is if the spatial variability in streamflow average is only due to precipitation: several authors, for example, pointed out the role of regional groundwater flow and incorporated this possibility in the models; GR4J, for example, has a parameter that quantifies catchment gains or losses. This shows that a-priori there are several processes that can affect the water balance; our analysis is intended to understand which modeling decisions are relevant in this case study"

4) Good to bring on board in the discussion as well:
"To avoid misunderstandings, we have clarified that we are interested in explaining the hydrograph spatial variability. "

5) This could be reinforced and explored together with point 1 above:
"We have clarified that the paper is not about large sample hydrology but about distributed modeling (e.g. see first paragraph of the introduction). In order to formulate model decision we have used elements of catchment classification studies.

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RR by Lieke Melsen (23 Dec 2019)

Suggestions for revision or reasons for rejection

Dal Molin et al did a great job in incorporating feedback and improving the manuscript. The selection of signatures and indices is now more transparent and tested for mutual correlations, the hypotheses are now more directly linked to the correlation results, and the model results show interesting relations to the predefined hypotheses.

I have only one major concern left, and that is the interpretation of model results solely based on correlation (Figure 8, 9, 10). Correlation clearly does not account for bias (as becomes specifically apparent in Figure 10) and therefore does not guarantee “good” model results. In the text (Section 4.2) the correlation is now discussed as indicator to demonstrate which model performs best for which signature. A suggestion could be to include bias and variability (the KGE-terms) also in the same figures (or use the NSE?). Unless the authors have good reasons to do it the way they did, but then please clarify.

Minor point;

I would expect the lower right panel (M1, HFD) of figure 8 to be the same as the third row first column panel (M1, HFD) of figure 9, but they are different. Is this because in Figure 8 only snow catchments are included, and in Figure 9 all? If so, please put more clearly and also explain why for figure 9 no snow-catchment selection was made.

Textual;
> “an uniform” -> “a uniform” (several times)
> “not represents well extreme values ” -> “not represents extreme values well”
> “which therefore represents an independent evaluation metrics” -> “which therefore represents independent evaluation metrics”

Suggestions;

I have a few suggestions that might improve the conveyance of the conclusions. This is not based on the content, and therefore beyond the scope of my role as reviewer. As such, it is up to the authors to decide whether they agree and if it is worth the effort.

I think the manuscript can benefit from leaving the traditional ‘methods-results’-structure. For instance, the results on the mutual correlation of the metrics and indices could be presented right after the introduction of these metrics and indices. After that, the second part of the paper can focus solely on the modelling. Also, I think it would be insightful if the Results-section follows the structure of the four hypotheses. Hypothesis 1 is on precipitation as main driver. Then the first sub-section should be on testing this hypothesis, and so on. Now, the results-section is a little bit of everything, and the hypotheses are only clearly discussed again in 4.2.4. Which is a pity given that I think you chose an elegant way of approaching semi-distributed modelling.

In the same way, I think the manuscript could benefit from one clear conceptual figure that demonstrates the approach and the conclusions. For me, the main value of this paper is in demonstrating a way to thoughtfully develop a semi-distributed model. This procedure can be schematized and as such better convey the message to future-semi-distributed-model-developers. The same is true for the hypotheses and the different model structures; a simple figure showing the different model structures, the hypothesis, and whether the hypothesis was confirmed or rejected could summarize all insights from this study. If number of figures becomes too high, the signature/indices-correlation figures can be considered for supplementary material.

Overall, I think, besides the few small points I raised that might be clarified by the authors, the manuscript is in good shape for publication.

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ED: Publish subject to minor revisions (review by editor) (23 Dec 2019) by Conrad Jackisch

AR by Marco Dal Molin on behalf of the Authors (17 Jan 2020) Author's response Manuscript

ED: Publish subject to minor revisions (review by editor) (24 Jan 2020) by Conrad Jackisch

AR by Marco Dal Molin on behalf of the Authors (07 Feb 2020) Author's response Manuscript

ED: Publish as is (10 Feb 2020) by Conrad Jackisch

AR by Marco Dal Molin on behalf of the Authors (11 Feb 2020)

Post-review adjustments

AA: Author's adjustment | EA: Editor approval

AA by Marco Dal Molin on behalf of the Authors (17 Mar 2020) Author's adjustment Manuscript

EA: Adjustments approved (17 Mar 2020) by Conrad Jackisch