Estimation of annual runoff by exploiting long-term spatial patterns and short records within a geostatistical framework

Roksvåg, Thea; Steinsland, Ingelin; Engeland, Kolbjørn

doi:https://doi.org/10.5194/hess-24-4109-2020

Articles | Volume 24, issue 8

https://doi.org/10.5194/hess-24-4109-2020

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

https://doi.org/10.5194/hess-24-4109-2020

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

Articles | Volume 24, issue 8

Research article

|

21 Aug 2020

Research article |

| 21 Aug 2020

Estimation of annual runoff by exploiting long-term spatial patterns and short records within a geostatistical framework

Thea Roksvåg, Ingelin Steinsland, and Kolbjørn Engeland

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Final revised paper (published on 21 Aug 2020)
Preprint (discussion started on 24 Sep 2019)

Interactive discussion

Status: closed

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

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- Supplement

RC1: 'Review', Gregor Laaha, 11 Oct 2019
- AC1: 'Response to Dr. Gregor Laaha', Thea Roksvåg, 25 Oct 2019
SC1: 'Interactive comment', Joris Beemster, 07 Nov 2019
- AC2: 'Response to Joris Beemster', Thea Roksvåg, 14 Nov 2019
RC2: 'Journal-Solicited Review', Anonymous Referee #2, 15 Nov 2019
- AC3: 'Response', Thea Roksvåg, 29 Nov 2019
RC3: 'Review of "A geostatistical framework for estimating flow indices by exploiting short records and long-term spatial averages – Application to annual and monthly runoff"', Jon Olav Skøien, 22 Nov 2019
- AC4: 'Response', Thea Roksvåg, 05 Dec 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) (22 Dec 2019) by Harrie-Jan Hendricks Franssen

Dear Dr Roksvag,

Your manuscript “A geostatistical framework for estimating flow indices by exploiting short records and long-term spatial averages – Application to annual and monthly runoff” has been reviewed now by four persons, three of them invited by the journal and one spontaneous review. Two reviewers recommend major revision and two others minor revision. Taken all comments together, there are serious concerns raised by the reviewers and the amount of comments to be handled is large. The authors should check whether a revision is feasible. I recommend major revision of the manuscript.

The main points to be handled in the revision are:
1. There are methodological concerns regarding the ”areal model”. The “areal model” is one of the main (claimed) innovations of the paper. The authors should provide evidence that the areal model indeed improves results. Significance testing is an option here. The paper should also dig deeper in the issue of mass conservation of the “areal model”.
2. The test cases presented in the results section should be re-considered. The reviewers suggest that some cases could be omitted from the manuscript. On the other hand, reviewers suggest to extend the partially gauged case including more observations there.
3. The discussion should be re-organized. Part of the discussion is repetition of results and a more strict division between the results and discussion sections can be made. Next, it is important to extend the discussion regarding the generalization of your results. It is important to discuss how the method could work in other flow regimes and climates. The role of human intervention (e.g., dams) is also an important point to be discussed.
4. Please consider also sharpening your conclusions.

In your answer to the main points and detailed comments, please indicate how comments have been handled exactly, indicating also whether text has been deleted and what the position of newly included text blocks is. I am looking forward to the new version of the paper.

Best regards,

Harrie-Jan Hendricks Franssen – editor

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AR by Thea Roksvåg on behalf of the Authors (31 Jan 2020) Author's response Manuscript

ED: Referee Nomination & Report Request started (02 Feb 2020) by Harrie-Jan Hendricks Franssen

RR by Anonymous Referee #2 (13 Feb 2020)

Suggestions for revision or reasons for rejection

I reviewed an earlier version of this manuscript, and this version is a substantial improvement. The authors propose and evaluate a Bayesian geostatistical framework to estimate annual and monthly streamflow values in Norway. While the authors are unable to demonstrate the superiority of their method, they provide some evidence that the new method makes better use of short records (the main goal of the paper). The revision more clearly states the goal of the paper and addresses some major concerns but does not address all reviewer concerns. The response to authors leaves whole section of the reviewer comments unaddressed. While the manuscript has improved, I remain concerned.

In the previous version, almost all reviewers expressed concerns about the claims of the areal method. The revision and response do much to soften the claims of the areal method. However, the main claim remains: That the areal method conserves mass. This remains undemonstrated. The authors have claimed it is proven in a companion arXiv article, but arXiv is self-administered repository that is not peer-reviewed. This advantage of the areal model, if it is important, should be demonstrated in peer-reviewed literature. For more questions, see my comments on an earlier version.

The authors have failed to respond to the editor’s and reviewers’ comments on the significance of performance differences. In my review, I discussed how tables 1, 2 and 3 show only average performance and do not interpret the significance (or some proxy thereof) of the differences across methods. The editor raised this as a concern as well. The revision continues to ignore the question of significance (whether formal significance or some proxy). Without this information, we evidence of differences in performance is weak.

The authors have done a better job of acknowledging that their proposed method does not improve over standard methods in the UG case. They appropriately highlight the marked improvement in performance with the introduction of a single observations. This is a very interesting finding and worthy of publication. It shows how their method can better leverage sparse information. However, in order to strengthen this case, the authors should consider how to demonstrate that the increases (though large) are a result of improvements and not random selection of years (i.e., an approach to testing significance is needed here as well).

When considering the PG case, the authors continue to use a regression based on two data points. I raised this concern in my previous comments, and the authors did not respond. It is wholly inappropriate to build a regression on two data points. The result would just be a straight line, from which it would be impossible to conduct any statistical inference (e.g., intervals, significance, etc.). (This can be showing by considering the denominator of most of the OLS formula, which have n (number of observations; here, 2) – k (number of slopes; here, 1) – 1 (for the intercept term). The result is zero in the denominator. The linear regression used for comparison must use more than two data points.

This revision is a great improvement over the previous version. In considering many of the reviewer comments, the authors have improved the directness of their manuscript. The scope has been substantially reduced to focus on how the newly proposed method (with better descriptions thereof) can benefit from short records in ways that the previous methods cannot. However, as always, there remains room for improvement. Many of the kriging applications in hydrology have shown how average variograms (rather than using year-specific variograms) can improve regional performance; this could be relevant in that so-called “average” variograms can absorb partial record information. While probably beyond the scope of this work at the time, it seems like it should be acknowledged that others have proposed different methodologies for incorporating partial records (I’m thinking of the entire field of record augmentation, including MOVE methods and the like).

Thanks for continuing with this work! I look forward to more discussion.

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RR by Jon Olav Skøien (05 Mar 2020)

Suggestions for revision or reasons for rejection

This is a second and very much improved version of the manuscript describing a methodology that estimates runoff based on a combination of long and short records. I have a few comments and suggestions below; all of them can easily be integrated if the authors agree. I think a minor revision is sufficient before the manuscript can be published.

The authors have updated the text with the number of catchments with observations length 1-3, showing that these are not as rare as one could expect. As an additional possible use case, the manuscript could be used as motivation for installing new (maybe temporary) stations, as they can improve long-term estimates only a year after installation.

The text on P23 refers to how the methods fail for some catchments, based on the RMSE. However, as the runoff values are much higher in the catchments in western Norway, the RMSE might not be the best measure for capturing the prediction performance. This could at least be mentioned.

The authors now refers to lognormal being an option, but not compatible with the linear aggregation assumption, what I mentioned in the previous review. I am fine with the authors not testing this. However, one should be careful dismissing a method only for violating one of the assumptions, when they are most likely already violated to some degree in other ways, probably similar to a large number of interpolation use cases found in the literature. The suggested framework can handle heteroscedasticity better than TK, as this is already a violation of the assumptions behind kriging. However, it is never tested if the assumptions of runoff data is actually Gaussian, and I doubt that a test would confirm it. Runoff is truncated at zero, which is the reason for the problem with negative estimates. A lognormal transformation could solve this violation, but instead create a new.

The difference between the centroid model and the areal model is small for most cases and catchments. It can be mentioned that this is somewhat expected, as it has also been shown for ordinary kriging vs top-kriging, by e.g. Farmer (2016) and Skøien et al. (2014).

It could also be mentioned in the discussion that it would be possible to use Top-kriging on residuals in the partially gauged case, which might improve the performances of the method. It is fair not to include this in the comparison, as there are different possible ways to implement such a procedure, and that is out of scope for this study.

The discussion around transferability of observations from neighbouring catchments and gauging density could maybe have a reference to Patil and Stieglitz (2012).

Minor edits
P1L11-13 The sentence is long and difficult to read correctly, consider rephrasing.
P3L29 maybe add “with a spatial support” at the end of the sentence?
P6, Fig2 caption: I think rarely or barely cross is better than almost don’t cross.
P6L18 remove “the” at start of line.
P6L19 I think the first “annual” should be changed to “montly”?
P8L5 maybe better with “or the 5th percentile flow”?
P13L27 remove comma after “choice”.
P14 Maybe better with “… and IN this way”?
P14L10 “defined by that there is “ -> doesn’t sound well, rephrase.
P16L30 Fig 6 is good, but the text (or caption) could mention how many or which grid points there are in each subcatchment, I think this would make it easier to understand the figure and the explanation.
P23, Table 1: The model with the best coverage of 95% could also be in bold
P26L5 and Fig 10 caption: The first reference to years is 1997 and 1998, whereas the second one is for 1996 and 1997.
P31Fig14 caption: I think it would be better with “… length one (PG1, middle) and five (PG5, right).”
P34L10 I think “could” could be added before “still”

Farmer, W. H.: Ordinary kriging as a tool to estimate historical daily streamflow records, Hydrol. Earth Syst. Sci., 20(7), 2721–2735, doi:10.5194/hess-20-2721-2016, 2016.
Patil, S. and Stieglitz, M.: Controls on hydrologic similarity: role of nearby gauged catchments for prediction at an ungauged catchment, Hydrol. Earth Syst. Sci., 16, 551–562, 2012.
Skøien, J. O., Blöschl, G., Laaha, G., Pebesma, E., Parajka, J. and Viglione, A.: rtop: An R package for interpolation of data with a variable spatial support, with an example from river networks, Comput. Geosci., 67, 180–190, doi:10.1016/j.cageo.2014.02.009, 2014.

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RR by Gregor Laaha (10 Apr 2020)

Suggestions for revision or reasons for rejection

The authors have carefully revised the MS, which is now a really nice piece of work, nearly ready for publication, subject to a few specific comments that still need to be addressed.

Section 2, Study area:
Please describe and plot only the catchments used in the evaluations, not others that are not used. In detail:
The second sentence (It consists of … 450 catchments … is misleading, as this data set has not been used in the study. Please delete.
p5, L4: “In total 53 of 180 catchments used for cross-validation were nested” – Add: “(30%)” as the degree of nestedness is quite important.
P7: There are two data sets mentioned, consisting of 260 and 83 catchments, respectively. This is a gain quite confusing. If my guess is right, the 83 have finally be used – so please delete the part describing 260, and add the number and ratio of nested catchments instead.

Section 4.2.2 The water-balance constraints of the areal model:
Figure 6 and text: The problem here is that the example gives no valid estimation problem for Top-kriging, so it cannot be used for demonstrating the superiority of the areal method. Note that Top-kriging is defined to estimate discharges at river sites, and is not defined for disaggregating these discharges into sub-catchments. When reformulating this setting into a valid estimation problem for Top-kriging, there would be one gauge at the outlet of u1+u2+u3, and a gauge at the outlet of the entire catchment u1+u2+u3+u4+u5. As kriging is an exact interpolator, the discharges at the gauges are exactly predicted, and the derived flow difference from the predictions would be 2500 mm/year. Top-kriging implicitly conserves the water balance without requiring additional discharge constraints.
p17, L12 is therefore not valid for Top-kriging.

Sections 5.1 and 5.2:
I guess that the climatic GRF c(u) was updated in the cross-validation at each turn, when one catchment / one fold of catchments was left out? Pls. specify.
P22, Eq. 15: The r² is an unusual, not recommended measure as it is seemingly (or often confounded with) the coefficient of determination R², but subtracts any biases and is therefore misleading in case of systematic errors. Suggest that you report the coefficient of determination (R²) instead.

Section 6.2 Predictions of mean annual runoff (1981-2010)
Fig 15: Please use the coefficient of determination (R²) instead to cover possible biases (see my previous comment).

Section 7 Discussion
p32 L4: Please be exact: For data set 1, 70% of catchments are not nested (rather than “more than 50%). How is I for data set 2?xy

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ED: Reconsider after major revisions (further review by editor and referees) (10 Apr 2020) by Harrie-Jan Hendricks Franssen

AR by Thea Roksvåg on behalf of the Authors (03 May 2020) Manuscript

ED: Referee Nomination & Report Request started (12 May 2020) by Harrie-Jan Hendricks Franssen

RR by Jon Olav Skøien (15 May 2020)

Suggestions for revision or reasons for rejection

This is the second revised version of the manuscript describing a geostatistical framework for exploiting spatial patterns and short records for interpolation of annual runoff. For me the manuscript has been further improved, and can be published after correcting a few minor issues.

The issue of mass conservation was discussed by the other reviewers, and also discussed in relationship with top-kriging. There is maybe a confusion here – whereas TK is based on the assumption that the variable is linearly aggregated and mass-conserved, it does not have constraints for preserving the mass balance between subcatchments and the basin. This is something that was done in a slightly different approach by Sauquet et al. (2000), introducing the mass balance as extra constraints in the kriging equation. On the other hand, the authors answer that TK cannot predict outside the observation range because the sum of the weights is equal to 1, and have also added this to the text. This is not correct and should be corrected (P10 L20-22 and P18 L13-15). Kriging methods can interpolate outside the range as long as negative weights are allowed. The sum of the weights is one, but the sum of the norm of the weights can be above 1.
Another confusion in the understanding of the figure 6 might also be that the areal method, as far as I understand, is trying to predict at the grid nodes, whereas TK only uses the grid nodes to establish the statistical relationships between subcatchments, hence no prediction for the individual grid points.

Fig 1 caption: 30% OF THE involved catchments…?
P11 L9 It should be clearer from the text what MOVE methods are.
P18L8 As far as I can see, the exact result from Eq (13) should rather be 2667 mm/year? Please check.
P33L7 “there are a higher percentage” – there is?
P33L16 “ITS run time” – remove no apostrophe

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RR by Anonymous Referee #2 (21 May 2020)

Suggestions for revision or reasons for rejection

I reviewed a couple of earlier versions of this manuscript, and this version shows that the authors have deeply considered reviewer comments. The manuscript is very good. This Norwegian case study looks at estimating annual and monthly streamflow values using Bayesian geostatistical methods. The authors provide some evidence that the new method makes better use of short records (the main goal of the paper) and could be useful in some situations. I have no new concerns about this manuscript.

I remain concerned with the use of regression for partially gauged sites. I’ve raised this before, so I’m sure the authors are not happy to hear it again, but I do want to log my concern. I suspect that the authors will disagree, which is fine, and, as other may feel similarly, it might be a point for discussion.

In their experiment.to replicate partially gauged sites, the authors compute a regression with two observations of paired years at the target and donor site. My concern is that this is far two few points to build a meaningful regression. Most statisticians will tell you that, as a rule of thumb, you would want roughly ten data points per predictor variable. Obviously, this is a rule of thumb, not strict policy, and would probably defeat the purpose of a partially gauged site, but the impacts of having fewer data are important. As the authors have fit a model without an intercept, thereby creating the point (0,0), the mathematical formulas for OLS regression will work. That doesn’t mean that is a good idea. Most of the inference built around OLS assumes a certain residual behavior and a model with an intercept. This alone causes this application to be suspect (by that I mean that the limitations should be acknowledged, not that this work should be cut). Furthermore, the idea of having two points and two unknowns is problematic. One of the unknowns is the variance of the errors (residuals). Surely no one would suggest that two points are useful in estimating a variance.

However, this application of regression is only used for a point of comparison. I think the lack of data provides a bit of a disadvantage to LR, but I still believe that the novel method would outperform the best use of LR. As that is my belief, it may not be useful to change the methodology, but rather to provide a discussion of the implications of a limited use of LR.

This work makes a very interesting paper, and I am excited to see it the literature. I hope my comments are not taken as overly critical, as I really do think this is a strong work. Thank you for your consideration!

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RR by Gregor Laaha (27 Jun 2020)

ED: Publish subject to minor revisions (review by editor) (28 Jun 2020) by Harrie-Jan Hendricks Franssen

AR by Thea Roksvåg on behalf of the Authors (29 Jun 2020) Author's response Manuscript

ED: Publish as is (15 Jul 2020) by Harrie-Jan Hendricks Franssen

AR by Thea Roksvåg on behalf of the Authors (19 Jul 2020) Manuscript

Short summary

Annual runoff is a measure of how much water flows through a river during a year and is an important quantity, e.g. when planning infrastructure. In this paper, we suggest a new statistical model for annual runoff estimation. The model exploits correlation between rivers and is able to detect whether the annual runoff in the target river follows repeated patterns over time relative to neighbouring rivers. In our work we show for what cases the latter represents a benefit over comparable methods.