Dear authors,

many thanks for your comments and also for providing a quantitative response to the criticism raised by the reviewers. The proposed revisions are of a nature that suggest that a suitably revised and reworked manuscript may become acceptable to Biogeosciences. Please make sure that the revised manuscript reflects all points raised by the reviewers, and provides a balanced discussions of these points raised. At this stage, I do not provide detailed comments or a profound assessment, but offer some further guidance for revision with respect to your responses, should you decide to submit a revised version of the manuscript. Please note that a revised manuscript would undergo a full second round of peer-review.

The new model version has a much improved estimate of BNF, which makes the results appear more plausible. However, how you have gotten to this result remains unclear from the revisions. I would recommend to detail the changes you have made between the first submission and the revised version (that could be an Appendix), and also offer some key statistics as to how the models differ (e.g. global BNF, NPP, C storage, N leaching and total N gas loss). Since BNF in your model seems to be calibrated by the N immobilisation process, a more in-depth description on how this process works would be appreciated. Somewhere in the model description it reads that the immobilisation process was introduced later into the LPJ-DyN, which is a curious statement, given that N immobilisation is an essential part of the SOM decomposition process, and it is hard to imagine that one can describe a model as prognostic and full representation of the N cycle if this process is not represented.

It is surprising that you can tune the model to have a five-fold difference in BNF, but no perceivable difference in C and N cycle trajectories across the LGM to present-day discussion. This fact deserves some discussion (because this is certainly not the case for other N modelling concepts), in particular if the claim is that increased BNF is an important cause of the observed N2O increase.

It is OK to down-tone the hypotheses behind your research criticised by reviewer #1. However, this does not change the fact that in your model, BNF is assumed to occur free of cost and irrespective of an biochemical constraints whenever the decomposition process is limited by N, which, by default increases N cycling and therefore N2O losses whenever productivity increases. It would be beneficial to include a comprehensive discussion of how other hypotheses on how BNF is controlled (as implemented in other global models) would respond to the C and N cycle changes you simulate with the aim to elucidate whether your response is a genuine characteristic of N cycle models, or a feature of your model (for which you can provide of course justification). It would also be important to elucidate on the alternative causes of changes in terrestrial N (given that LPX-Bern does not fully simulate the timing and magnitude of N2O change), in particular relating to the question that the nitrification and denitrification processes appear to be linear with soil moisture (if my reading of Xu-Ri et al. 2008 is correct), which may impair the model’s ability to adequately simulate the response of N2O emissions to climate change.

I do not see the need to explicitly refer to rock-based N weathering in this manuscript. The BNF in LPX-Bern is driven by the litter-layer decomposition process (which is largely devoid of weathering material), and does not depend on deeper soil layers N production rate (nor does it reflect the geographic patterns of weathering and lithology). As far as I understand, the essence of BNF in LPX-Bern is asymbiotic, and it would be clearer if that was stated rather than subsuming it with many terms that aren’t actually represented in the model.

Best wishes,
Sönke

Dear authors,

My sincere apologies for the delay in coming to a decision with regard to your manuscript. This was partly due to the IPCC internal deadlines, but also because the two reviewer assessments had diverging views on the merit of the revised draft (accept as is / reject).

The revised manuscript by Joos et al. is somewhat improved with respect to the overall plausiblity of the N cycle simulation (in particular related to the magnitude of the pre-industrial terrestrial N source (in the wording of the authors), and also with respect to removing the hypotheses critisied by one reviewer. There is a suitable set of analysis to understand the trends simulated by the model. There is a extensive discussion of the results, which in some cases could be shortened and focussed.

The dilemma with the current version of the manuscript is that the model does not convincingly capture the magnitude of the LGM to Holocene N2O compared to what has been inferred in a companion paper based on icecore data. The authors provide an assessment of the underlying model trends, which is an interesting model exercise. However, the lacking ability of the model to reproduce the terrestrial N2O increase makes it questionable whether the increase in biologically driven N fixation is indeed a major cause for the increase in the terrestrial N2O source between LGM and Holocene as put forward by the authors, or the consequence of other processes or process rates not represented well in the model, or perhaps also issues with using the climatic reconstruction as input for the biosphere model. This weakens the message of the paper.

Unfortunately, I furthermore find the presentation of the results overreaching and misleading. This primarily relates to the following points:

1) In abstract and conclusion, the authors write that their study results are in reasonable agreement with the observations, which they are clearly not. While the N2O emissions increase from LGM to Holocene, the magnitude of this increase is at best 2/3 (probably even less) of the inferred increase from ice cores, decidedly outside the error range of that estimate. In addition there is a time-delay in that response compared to the icecores, and the temporal development in the Holocene is opposite to the trend in the ice-cores. This misrepresentation is emphasised even clearer in the main text, where the auhors state (p 22 L 32-33) that the model results are at the lower bound of the reconstructed range, whereas Fig. 3 clearly shows this not to be the case.

2) To this effect, the key figure of this manuscript, Figure 3, shows two model results in support of the results discussed in the abstract, one with the N source fixed and consequently little change in N2O, and another one with the full simulation, which produces ~2/3 or less of the signal. This would have been sufficient to make the case the authors presented in the abstract. It remains unclear to me (and misleading) why Figure 3 also displayes a third model output (which coincidentally is the only model configuation that nearly reaches the lower confidence bound of the N2O source inferred from the ice-cores in agreement with the main text p22 L 32-33), based on the completely unrealistic assumption that land mass change did not change from LGM to present-day. While it is a useful scientific question to ask whether changes in N fixation did contribute to the change in terrestrial N2O, it is not a reasonable to assume that between LGM and Holocene neither sea level nor glacial extend did change. It is therefore unclear why it has been included here.

3) The model has undergone extensive calibration to address the reviewer concerns of round 1. The current version of the manuscript compares the old and the new models versions, as if this was a simple sensitivity study. This glosses over the fact that the updated version from the previous manuscript now has N2O yield increasing with temperature, without there being a clear explanation for the experimental basis of this function, and the fact that literature cited by the authors suggests the opposite (their page 19, L 9, Firestone and Davidson, 1989). This is noteworthy, because this model change contributes to an increase of N2O of about half of the simulated LGM to Holocene increase in Fig 3. This fundamentally undermines the authors assertion that the previous and revised model versions show comparable changes in LGM to Holocene N2O irrespective of the pre-industrial or glacial N source magnitude, because this was only achieved by adding an additional temperature sensitivity on top of the temperature sensitivities of organic N turnover and that of nitrification and denitrification.

4) The manuscript further suffers from a misrepresentation of their model. In P1 L28 and elsewhere, the authors claim that their N source estimates are plant-demand based, implying that changes in plant growth and/or N limitation would have direct consequences for fixation, ecosystem N availability (and thereby N2O emissions), but this is not the case: neigher the N requirement for growth nor the lack of N availability for plant uptake do not enter the calculation of the N source. Rather it is simply based on the stoichiometric N requirement for litter decomposition compared to the soil N availability. If anything therefore, this representation is a soil decomposer demand based N fixation model. Other models have been published in which plant N demand for growth enters the calculation (Gerber et al. 2010, Meyerholt et al. 2016), and the labelling of the scheme of this paper as pland N demand based is therefore highly misleading. It is also incorrect to label such a representation of the nitrogen cycle as mechanistic (p 12 L 14), when it is based the assumption that biological N sources are in fact simply the consequence of the difference between organic N accumulation and ecosystem N losses (p 6 L 21-22).

5) All these above points reduce the validity of the claim that these results adds confidence of future simulations (p. 24 L 21) of this model published by Stocker et al. 2013, because the model has been strongly modified in terms of the N source, the scaling of N2O emissions to N availability and the temperature sensitivity of that scaling of N2O emissions. Together with the lower than inferred changed in the terrestrial N2O source, these results would if anything suggest that the climate-N2O feedbacks suggested by Stocker et al. is low biased.

While I do realise that the authors have put a lot of effort into addressing the comments of the authors during revision, and there is no question that this modelling effort is novel, the combination of a model that does only capture a proportion of the observed signal with the overreach of the presentation of the results leads me to follow the recommendation of reviewer #2 and deny publication of the manuscript in Biogeosciences.

Sincerely,
Sönke Zaehle

Dear Authors,

You will now have an opportunity to upload a revised manuscript and then I will start a new round of peer review.

Many thanks for your patience,

Martin De Kauwe

Dear Authors,

I now have two reviews of your manuscript. Despite reservations about the process and previous revisions of the manuscript, R1 deems your manuscript suitable for publication. The second reviewer is more positive about the contribution of your work and also agrees that this should be published. I have read their assessments and upon reading your manuscript myself, I am recommending minor revisions. I think this paper makes an interesting contribution to the literature despite some reservations in the model-data disagreement (and so interpretation). As well as revising your manuscript to address the reviewer comments, I make three further points.

1. Whilst I appreciated the effort to contextualise the importance of your study and relationship to future predictions, I struggled with the considerable focus afforded mycorrhizal association/systems in the introduction. It seems very (completely?) unrelated to the focus on your manuscript. You might say the same about the Reich citation, it is a stretch - at best. I'd really prefer to see a few lines afforded your period of interest and a better link to the study in part 1.

2. In the discussion of modelling BNF - one (potentially) overlooked point is that while models that simulate BNF as a function of ET may not simulate marked change, they will simulate different magnitudes if they simulate different ET (which they do). Overall I do take your point in the discussion about it being hard (but by no means very difficult) to carry out a more quantitative assessment about how BNF approaches may impact your results. Nevertheless, as I look at Figure 3 I can't help wondering how robust the interpretation can be to the assumed BNF method. If a model makes an alternative BNF assumption, they likely arrive at a different answer and so interpretation. I don't have a specific recommendation here beyond highlighting how I suspect others may interpret the results.

3. The key point for me is how well the model captures the data and as such what the interpretation of the drivers can be. The text points out that the model simulates the increase in N2O to be about 47% lower. That is a sizeable amount. I do not currently feel that the abstract appropriately captures the remaining gap. Arguably, you will suggest that the model-based analysis has closed some of this gap (potentially), which is fair. But I think a reader may well expect to see a more open concluding sentence about the need to search for alternative or complementary explanations. I'd expect to see this sentiment in the discussion too.

Best wishes,

Martin De Kauwe

Dear Authors,

I've read through your responses and I'm happy to recommend your manuscript for publication, many congratulations.

Best wishes,

Martin De Kauwe