Dear authors,
many thanks for your detailed comments. Please provide a suitably revised manuscript including a point-by-point explanation on how (and where) you have addressed each of the reviewer comments in the revised manuscript.
Best wishes,
Sönke Zaehle

Dear authors,

my apologies for the delay in getting back to you. I was hoping to find an expert reviewer, but failed, such that I ended up writing my own review. While the reviewer and I feel that your manuscript has improved, we also found a range of issues that we would like to see addressed before this manuscript can be accepted for publication in Biogeosciences. If you decide to submit a revised version, please provide a point-by-point response regarding the issues raised by the reviewers.

Best wishes,
Sönke Zaehle

Dear authors,

many thanks for your revised manuscript, which have generally improved the quality of the manuscript. After reading the revised version I regret to inform you that there is a lot of editorial matters (and one important scientific issue), which you will need to address point-by-point, including a statement on how you have changed the manuscript, before your manuscript can be published in Biogeosciences.

Best wishes,
Sönke Zaehle

The GRACE analysis is not helpful as it currently is. a) Is the PDF of the correlation coefficient correct? The visual impression of the map suggests much more positive and negative correlation than near-zero correlation, whereas the PDF suggests that the correlation is centred around zero nearly in a bell-shaped form with few values above 0.4. The latter suggests to me a rather random agreement with no model skill. b) You cannot blame snow melt on the lacking correlation between GRACE and WECANN, as snow melt does not change the water storage. c) Snowmelt also does not explain the main other regions (typically with low LE), which have inverse correlation to GRACE.

Specific comments:

There is no such thing as model validation. Please use the term evaluation or similar instead.

Sorry for being pedantic, but GPP is the gross primary production of the vegetation and cannot be observed directly. GPP contributes to the net exchange of CO2 between ecosystems and the atmospheric boundary layer, of which the overwhelmingly turbulent part is observed as net ecosystem exchange. It is incorrect to refer to GPP as a turbulent flux, as it is also not correct to insinuate that GPP was directly measured by eddy covariance (P2 L4). GPP is derived from NEE measurements using a flux partitioning algorithm. Please revised all instances in the text and title to clarify the issue.

Abstract

The abstract is not written very effectively. E.g. sentence two and three each mention three data sets / sources, but it isn’t clear whether they are the same, or different and what these are. Similar, somewhat later you state that the retrievals are evaluated against FLUXNET observations, but then a sentence later refer to these as in situ eddy covariance measurements. Again, it is unclear whether that’s the same or not, and why this needs to be mentioned twice. The abstract also misses that other studies in the past have used SIF, the point here is that it’s (probably) the first JOINT retrieval of H, LE and GPP. In L21, please be more specific about what WECANN produces.

It is not clear to me what “is constrained by SIF information” means. Of course WECANN is constrained by SIF because its used in the training - be more specific about what SIF contributes to the study.

The last sentence does not make a lot of sense. The uncertainty analysis has nothing to do with the extreme event analysis. I also disagree with the ENSO link, which is not demonstrated in either the extreme event analysis nor in Figure 14 (too few El Ninos in there to make a case).

Introduction

For me, the flow of the introduction would be more easy to follow if the sentence on p2 L 17 was move to after P3 L1 (new paragraph after “in addition to GPP), because then all the information about your novelties are in one place. To help the reader, you could also add in p 2 L8, “Alternatively, as done here, one can…”.

P3 L1 “Using our machine learning technique…” This sentence comes a bit out of nowhere: in the previous sentence, you talk very generally about the potential of SIF, but this sentence now talks about something that will be the outcome of your study. For me, this would be more fitting to the conclusion section than here.


Data

Add reference to Table 1/2 to first view sentences of the Section “2 Data” at the respective places. (then nobody wonders where to find the reason for the 1° resolution.)

Use of FLUXNET data. It is not redundant to clarify the stations you’ve used, because you apply a filter on the number of stations used (clearly not all 750 stations are used, assuming that not 653 are coastal stations), and add (without providing any motivation or reasoning) other data-bases.
It is important to clarify, which station has been used, and for which years, and why data from the LBA and La Thuille dataset have been used.
It is important to document, which stations and data have been used. The supplementary table is a good start, if you added the exact site-years used.

In the description of the FLUXENT evaluation data, it’s worth mentioning that WECANN and the data are not fully independent, because the FLUXNET-MTE used for the training relies on these data. This does not preclude you from using these data to evaluate your product, but it needs to be mentioned somewhere.

For consistency reasons, I would move the description of the ET estimates based on runoff also into the Data section.

Method


I don’t see how you’ve addressed my comment on previous version P3 L9 in the revised manuscript. For me this is a point that merits discussion in the discussion section of the ms.
E.g. P7 L19 is a place at which it is worthwhile pointing out that no assumptions are made that H LE and GPP are in anyway connected, i.e. any correlation between them entirely relies on the training data sets.

Results

Supplementary tables: you should provide average statistics of every metric used for the FLUXNET evaluation (such as the bias), as it is meaningful to know whether the a product on average is higher or lower than the other estimates. Of course, one single metric does not provide a full insight into whether a product is better or worse than another.

P12 L 24: this analysis is not at the global scale.

Section 4.5: As said above, the first few lines should be presentation of the data set in Section 2. It is unclear to me whether or not the difference is an absolute number, or whether the outcome is that WECANN is always larger than the other estimate?

Given the focus of this manuscript on SIF, it would make a stronger case in Section 4.8 if Figure 6 & 7 also contained the WECANN-NDVI and WECANN-EVI.

Figure R1 is much more informative about the model and its anomalies in time than Figure 14. You can keep the bar plots for WECAN, but it would be much more informative if you plotted the FLUXNET-MTE alongside with it. The text associated with this Figure should briefly state, how much (if any) information on the inter annual variation in WECAN is derived from FLUXNET-MTE.

Dear authors,
many thanks for the revised version, which I'm happy to accept for publication in Biogeosciences, subject to the following technical corrections.

In the abstract, you mention the El Nino 2015/2016, whereas your study period only covers the year 2015. Please remove the reference to the year 2016.

In the supplementary tables, there are a range of sites, which have not been used. Please remove these from the tables, as there is not point in reporting them, unless you provide a reason for why this information is useful. Please adjust the number of sites listed in the manuscript used to the final count if that has previously included sites for which no site-years have been used.

Best wishes,
Sönke