Assimilating solar-induced chlorophyll fluorescence into the terrestrial biosphere model BETHY-SCOPE v1.0: model description and information content

Norton, Alexander J.; Rayner, Peter J.; Koffi, Ernest N.; Scholze, Marko

doi:https://doi.org/10.5194/gmd-11-1517-2018

Articles | Volume 11, issue 4

https://doi.org/10.5194/gmd-11-1517-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/gmd-11-1517-2018

© Author(s) 2018. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 11, issue 4

Model description paper

|

17 Apr 2018

Model description paper |

| 17 Apr 2018

Assimilating solar-induced chlorophyll fluorescence into the terrestrial biosphere model BETHY-SCOPE v1.0: model description and information content

Alexander J. Norton, Peter J. Rayner, Ernest N. Koffi, and Marko Scholze

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Final revised paper (published on 17 Apr 2018)
Preprint (discussion started on 21 Feb 2017)

Interactive discussion

Status: closed

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

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- Supplement

SC1: 'Executive Editor Comment on "Assimilating solar-induced chlorophyll fluorescence into the terrestrial biosphere model BETHY-SCOPE: Model description and information content"', Astrid Kerkweg, 24 Feb 2017
- SC2: 'Edit to title', Alexander Norton, 20 Mar 2017
RC1: 'comment', Anonymous Referee #1, 21 Apr 2017
- AC1: 'Author Response (pdf supplement)', Alexander Norton, 21 Jul 2017
SC3: 'Paper Comments', Andrew Schuh, 12 May 2017
RC2: 'Review', Anonymous Referee #2, 07 Jun 2017
- AC2: 'Author Response (pdf supplement)', Alexander Norton, 21 Jul 2017

Peer-review completion

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

AR by Alexander Norton on behalf of the Authors (18 Aug 2017) Manuscript

ED: Referee Nomination & Report Request started (05 Sep 2017) by Tomomichi Kato

RR by Anonymous Referee #2 (19 Sep 2017)

Suggestions for revision or reasons for rejection

First of all, I thank the authors for their effort in addressing the referee’s comments, and indeed the manuscript is now much clearer. However, I am still not convinced by the way the authors circumvented the issue of estimating the total observational error. This is why I suggest to revise it before being considered for publication, and below is a more detailed account.

• The authors claim in section 1.1.1 of their response, and as a reason for leaving aside the structural/model uncertainty in posterior error propagation, that this uncertainty cannot be estimated prior to performing a full assimilation. This is simply not true. One of the diagnostics provided by Desroziers et al. (2005) calculates the observational uncertainty (model + measurements) as the difference between prior model-data mismatch and propagated prior parameters error (Eq. 1 therein), which is one of the method put into application by Kuppel et al. (2013) (see Eq. 1 therein). Therefore, nothing prevents the authors from using this method. All the more because neglecting the model error in the covariance matrix CD could significant impact the large uncertainty reduction estimates currently presented in the manuscript. All the more that this study presents a novel couplings of model components where the structural uncertainty is essentially unknown. Ignoring this central aspect seriously undermines the impact of this paper.

• On page 8, lines 21-24, it seems to me that there is a confusion between structural and systematic errors; a probabilistic framework (such as that used by Kuppel et al. (2013)) can only characterize random errors (as opposed to systematic ones). Thus nothing really can be stated about systematic errors in the model, and it cannot be opposed to the systematic errors of measurements. Note that, as stated in the original report, using ‘observations’ on line 23 is rather confusing, data/measurements would be more appropriate. In addition, I don’t understand what kind of ‘structural uncertainty’ the authors are talking about on line 24, since just before they talk about systematic error in observations; did you mean ‘systematic error’? As stated above, I think this section requires further analysis.

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ED: Reconsider after major revisions (05 Oct 2017) by Tomomichi Kato

AR by Alexander Norton on behalf of the Authors (17 Nov 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (22 Nov 2017) by Tomomichi Kato

RR by Anonymous Referee #2 (03 Dec 2017)

Suggestions for revision or reasons for rejection

First, regarding the observation error, which includes data, model (and representation) errors. I agree the χ2r test is a good way to assess the observational error is well defined. However, for the optimisation problem at hand, I have three comments:

1. this test is chi-squared per degrees of freedom: χ2r = χ2 / N, where N is the number of degrees of freedom, i.e., number of observations minus number of parameters (e.g., Taylor, 1997). By including only the formed, the authors might thus underestimated the value of χ2r.

2. the authors state that “Because representation errors will be large at low-resolution this analysis cannot be performed using the low-resolution model used elsewhere in this analysis.” (P7, L7-8). I wonder then what is the informative value of a test performed on a different configuration than that used for the rest of the study? All the more that this “representation error” directly influence the value of χ2r, as it is included in the observational covariance error matrix Cd.

3. More generally, it seems to me that the value of χ2r should anyway expected to be larger than one. Indeed, no optimization is performed in this study, so that model-data won’t likely be excellent, and the χ2r value precisely translates a goodness-of-fit given the trust put in the observations. Contrarily to what is stated in that paragraph (P7, L5-11), my understanding is that having a value of χ2r lower than one should not be a target as it translates overfitting and underestimation of observational error (too much trust in the observations, i.e. model outputs and/or data), all the more if the prior model-data fit is not expected to be great. Note that in (Kuppel et al., 2013), χ2r was estimated using the optimised model (Eq. 6) –albeit with a slightly different formulation following (Tarantola, 2005).

I would thus recommend the authors to assess the reduced chi-squared statistics at the same resolution as that used for the rest of the analysis, and discuss on this basis. The advantage is that the impacts of both neglected structural and representation errors are included here. If the value of χ2r is significantly larger than one, it can arise from underestimated structural error, underestimated representation error, and/or model-data misfit. Acknowledging this from the start and for the discussion of the presented parametric uncertainty reduction would give more depth to the paper.

Second is the systematic error. I have a hard time understanding how the author can propagate a “systematic error of unknown sign”, for two reasons:

1. the very basis of error propagation used in this study assumes Gaussian error that can be propagated linearly, i.e., using matrices (P3, L14-22). The fact that the sign of the systematic error is not known does not necessarily make it suitable for statistical analysis, let alone be characterized as Gaussian. How are the authors including this “systematic random error” of ± 0.1 W.m-2.μm-1.sr-1 in their propagation framework? What “seasonality” is applied to it? Note that the sign of a bias is indeed generally known and its magnitude rarely is, but that is not enough for statistical analysis (Richardson et al., 2012, pp. 175-177).

2. The author claim (P9, L21-22) to perform “a sensitivity test of incorporating this systematic uncertainty into the error propagation system to indicate how an error in the zero-level offset may propagate through to uncertainty in GPP.” Following my previous comment, I was curious to see how the authors applied their methodology. However, I could not find where the results are reported. What is then the basis for asserting that “We also find that the effect of incorporating the error from the zero-level offset in the SIF observations is negligible on posterior parametric uncertainties” in the Discussion (P19, L19-20)?

3. Later in the Discussion, the authors state that “A known systematic error in forcing variables (e.g. Boilley and Wald, 2015) cannot be considered in the present error propagation system, however, in such a case a correction to the data should be performed as it will bias carbon flux estimates”. Why not apply the same framework for measurement error?
As it is formulated, the methodology is imprecise and the result not reported, so it is hard to assess what the authors have effectively done.

Other comments

• This is more of personal preference, but I think Eq. (6) should read $d_i = d^t_i + \epsilon_i + z$
In my view, this translates more clearly the fact that retrieved measurements derive from a true value affected by random and systematic errors, and not the other way around.

• Some questions marks are present in the revised manuscript where references should be, presumably from missing LateX bibliography pointers.

References
Kuppel, S., Chevallier, F. and Peylin, P.: Quantifying the model structural error in carbon cycle data assimilation systems, Geosci. Model Dev., 6(1), 45–55, doi:10.5194/gmd-6-45-2013, 2013.
Richardson, A. D., Aubinet, M., Barr, A. G., Hollinger, D. Y., Ibrom, A., Lasslop, G. and Reichstein, M.: Uncertainty quantification, in Eddy Covariance, pp. 173–209, Springer., 2012.
Tarantola, A.: Inverse problem theory and methods for model parameter estimation, Society for Industrial and Applied Mathematics, Philadelphia, PA., 2005.
Taylor, J.: Introduction to error analysis, the study of uncertainties in physical measurements., 1997.

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ED: Publish subject to minor revisions (review by editor) (08 Dec 2017) by Tomomichi Kato

AR by Alexander Norton on behalf of the Authors (05 Jan 2018) Author's response Manuscript

ED: Publish as is (01 Mar 2018) by Tomomichi Kato

AR by Alexander Norton on behalf of the Authors (11 Mar 2018)

Short summary

It is difficult to estimate how much CO₂ plants absorb via photosynthesis and even more difficult to model this for the whole globe. Here, we present a framework to combine a new satellite measurement "solar-induced chlorophyll fluorescence" with a global photosynthesis model. We then quantify how this new measurement constrains model uncertainties and find highly effective constraint. These results pave a novel pathway for improving estimates and modelling abilities of photosynthesis globally.