Dear authors,
many thanks for your replies to the reviewer comments. Please provide a thoroughly revised version, addressing each of the comments and ensuring that your responses are reflected by changes in the manuscript. Please see my editorial notes below to help responding to some of the comments.
Best wishes,
Sönke

I don’t think that the terminology of ’pre-photosynthetic’ vs. ‘post-photosynthetic’ N limitation is useful. Rather I would recommend to state that either photosynthesis or growth is assumed to acclimate to N availability.

The use of gross photosynthesis is not really helpful when defining intrinsic water-use efficiency, because as a consequence of the varying temperature response of A and leaf dark respiration IWUE will vary with temperature, which it should not. I do not see a justification for not using An

Please provide a reference for the discrimination values.

Your response to 1.12 is unsatisfying: How can GPP at the ecosystem level not be dependent on An on the leaf level. This makes absolutely no sense at all.

Your response to 1.16. It should still be possible to calculate the fraction of LE which is driven by transpiration and therefore identity whether the canopy or soil fluxes contribute to the WUE bias.

Dear Dr. Raczka et al.,

first of all, my sincere apologies for the delay in deciding about your manuscript. I provide my own review of the revised manuscript down here.

Overall I feel that the manuscript has improved. However, I have a list of comments that require addressing before this manuscript can be published in Biogeosciences. While most of these are mostly editorial matters, some require some further attention and clarification.

My main concern is that the method you describe is not particularly clear (I do realise that this is a tough job). My main concern about the current description are the following items:

- P6 Why is only Ac explained, but not Aj or Ap? Are they not relevant for the study? I think these should be mentioned, though for the sake of the paper, eq 2 and 3, as well as their Aj and Ap counterparts could become part of an methodological Appendix.

- Eq 11: Explain why An is assumed to be reduced, but gs not. This violates eq 4. Also verify scaling coefficients for gb and gs. My textbook says the diffusion correction factors are 1.37 for boundary layer and 1.6 for stomate's whereas your equation suggests the inverse. This will obviously have a fairly significant effect on the predicted ci and thus discrimination!

- P8 L10: It is unclear where this nitrogen is then coming from? Does this not break the logic of CLM 4.5’s closed N budget and introduce an unknown source of N? Or is this only assumed in eq 11 (then be more precise as to how this is implemented, and what happens to the extra C assimiation).

A further point needing attention is that I think labelling your Vcmax tuning a calibration is misleading, because the calibration directly includes the observed and simulated GPP as a factor, depends on time-varying site-data, and is not useful outside without site-data. This approach does override a lot of the model's internal dynamics and exceeds what is conventionally called "calibration". It is not surprising that the “calibrated” model performs better, because you prescribe the seasonal course of GPP. Section heading 2.4 and associated text is hence misleading.

Because this is the case, I don’t think that there is a need to emphasise differences between the off-the-shelf CLM 4.5 and your improved version. This is particularly the case as this manuscript focusses on the use of 13C as a constraint. I therefore don't see the relevance of presenting the off-the-shelf parameterisation in 3.1. specifically if the model behind the seasonal dynamics of GPP are fundamentally different between the two. The discussion of how to improve the seasonal representation of GPP also seems off topic as it does not involve the use of isotopes, and I would therefore suggest to drop this.

The results section contains large stretches of classical discussion (Sections 3.3 and 3.4). They should be part of a discussion section and not the results, as such as no new evidence is presented and they distract the reader from the results you present.

The abstract is currently very long. Please try shortening it a bit. Pre- and post-photosynthetic N limitation are CLM construct and thus not clear to the general readership. I would reformulate this to read that the default An-gs coupling of CLM failed, but a revised formulation coupling An and gs did successfully capture the observed dynamics without mentioning the CLM-terms, which are ok to use (though still awkward) in the manuscript).

Best wishes,
Sönke Zaehle


Detailed comments:

P3 L 11 (add "depending on for instance" to both brackets).

P3 L 17 Provide a reference for the fact that discrimination is indeed affected by nutrient availability in the real world.

P4L7ff can be removed.

P4 L20: It does not really become clear here why you would think this is an issue that needs particular addressing. Isn't is logical that the offset between the 13CO2 at site and global mean values must be important when looking at the absolute delta13CO2 values? So why would one use a global mean value to start with?

P4 L24: water-use efficiency

P6 L 14ff: Include beta_t into eq 3 if it's used there. Otherwise the current paper reads as if only the intercept of the Ball&Berry relationship is affected by soil moisture. While doing this, clarify whether beta_t also affects Ap and Aj?

P6: Equation 6 define LAIsunlit/shade how calculated or provide a reference.

P7 L22: Provide a reference for these values. Explain how ci depends on shaded and sunlit leaves, and how this affects the leaf ci calculations and total discrimination of the An flux?

P8 L7: should this not read nitrogen-limited rather than limited nitrogen? Assuming that the actual N-limitation of the ecosystem is identical between the runs, and its only a question of whether GPP is assumed to be down-regulated with N limitation or not? It seem so because that's what is said later?

P8 L9: idem

P8 L13: Add a note that all this is very specific to the set-up of CLM and not representative of the wider class of biosphere models.

P12 L28: What happened to Jmax?

P13 L14-22. Not necessary

P15 L31. The FLUXNET data do not provide evidence for the response of stomates to CO2, they simply suggest a trend in WUE with time, which may (or may not) be related to increasing CO2. I would rather recommend to quote a study relating stomatal conductance to elevated CO2 experiments.

P16 L 1 Is this change in ci:ca really a consequence of changes in CO2, or concurrent climatic changes? Because eq 4 should imply constant ci:ca...

P17 L 7: In the model, or in the data? Explain briefly how VPD is affected by your model formulation - not everybody will get this.

P17 L12: This is a good example of a paragraph that would be better suited in a different, separate discussion section, as it is distracting from the line of results presented. This is particularly true because another discussion of gm is on P19 L3ff

P17 L30: I must have missed this: which global simulation. So far, you only talked about Niwot ridge.

P18 L 3. Why is this equation introduced here and not in the Methods?

P19 L18. which mixing model?

P19 L30ff This may either be the introduction to this section or removed, because at this stage, you are simply repeating what's been said before.

P20 L6 ff: Isn't this all simply a consequence of the model tuning via a time-dependent Vcmax while not touching leaf respiration? This must yield unrealistically high ci:ca and thus discrimination values. Given that this is an artefact of the way you've matched the seasonal cycle and it will be specific to CLM4.5, is it really worth discussing this here?

P22 L25. Please define what you mean by "categorial differences." It is not correct to state that CLM4 did not capture the NPP response only because it had too little initial N availability. We have demonstrated clearly that it was lacking important functional features of the response such as the too strong carbon-nitrogen coupling of biomass production (Zaehle et al. 2014). CLM4 had the lowest WUE response in the ensemble (de Kauwe et al, 2013).

P23 L4. This is not correct, because you do not update foliar N to calculate Vmax (with all the consequences for the N requirement of biomass etc.), but prescribed a time-dependent Vcmax scaled to the observed GPP independent of foliar N (unless your description in Sect 2.4 is inaccurate).

P25 L22: No land surface model qualifies as highly mechanistic.

P25 L22L What you have shown is that if employing eq 4 on the "true" An, all is fine, but if you follow the standard CLM approach, the results are not as good. What you have not shown is that if one uses foliar N to diagnose Vcmax, this improves the simulation of discrimination. You have not, because you calibrate for each day Vcmax based on its difference to the observed GPP, implying that there are variations of Vcmax,25 on a day-to-day basis unrelated to any changes in foliar N. The latter would be what "foliar-N" models do. Therefore, your claim that you are mimicking the functionality of a foliar N model is unsubstantiated.

Figures: Please label all sub-plots with consecutive letters and refer to these in the caption

Figure caption 1: “The N-limitation is determined by required N availability to meet demand from C:N ratio based on CF.” Isn’t the available soil N determining whether or not the growth is N limited? Also I wonder if this Figure could be made clearer by having two arrows between the box of eq 8 and eq2 indicating for both scheme the direction if information (ie is it growth or Vcmax determining photosynthesis and conductance?).

General remark: carefully revise writing and punctuation

Dear authors,

many thanks for your extensive edits. Most of this is fine, but two minor edits I feel are still necessary:

point #2: The text explaining eq 11 still need to be modified to state that eq 11 attempts to mimic eq5, but fails to do so. Much of what you are investigating is the unintended consequence of a model implementation, which focusses on N limitation for biogeochemical, but not biogeophysical processes. It needs to be clear to the reader that one could have derived a “correct” implementation by adjusting gs in concert with An, and therefore that eq 11 does not satisfy eq 5.
point #25: The boundary conditions for the global simulation are not clear. If there is no published reference, then in the main text, include, […driven by observed historical climate etc.… , (unpublished, K. Lindsay 20XX)]. Because the global simulation was not introduced in the Methods, I would prefer if you could also state “a global CLM4.5 run with historic climate” the second time you mention this.

Best,
Sönke