Initial shifts in nitrogen impact on ecosystem carbon fluxes in an alpine meadow: patterns and causes

Song, Bing; Sun, Jian; Zhou, Qingping; Zong, Ning; Li, Linghao; Niu, Shuli

doi:https://doi.org/10.5194/bg-14-3947-2017

Articles | Volume 14, issue 17

https://doi.org/10.5194/bg-14-3947-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/bg-14-3947-2017

© Author(s) 2017. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 14, issue 17

Research article

|

13 Sep 2017

Research article |

| 13 Sep 2017

Initial shifts in nitrogen impact on ecosystem carbon fluxes in an alpine meadow: patterns and causes

Bing Song, Jian Sun, Qingping Zhou, Ning Zong, Linghao Li, and Shuli Niu

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Final revised paper (published on 13 Sep 2017)
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Preprint (discussion started on 10 Nov 2016)
Supplement to the preprint

Interactive discussion

Status: closed

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

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RC1: 'Review', Anonymous Referee #1, 30 Nov 2016
RC2: 'Review', Anonymous Referee #2, 08 Dec 2016
AC1: 'response letter - reply to the referee comments', Bing Song, 26 Jan 2017

Peer-review completion

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

ED: Reconsider after major revisions (02 Feb 2017) by Michael Bahn

AR by Bing Song on behalf of the Authors (12 Mar 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (15 Mar 2017) by Michael Bahn

RR by Anonymous Referee #1 (22 Mar 2017)

Suggestions for revision or reasons for rejection

I have carefully read the manuscript and I think it still has the same issues I have raised in my first review of this manuscript. I still feel confused about the main story told here and the mechanisms invoked to explain main changes in NEE.

1) I understand that rates of NEE increase (i.e. more negative values) under mid levels of N additions 8 and16 g N m-2 yr-1 in 2015 (second year of experiment), which seems to be the case when looking for example at Fig. 2d (this may suggest the occurrence of some sort of ‘saturation’ response, whose causes are far from clear).
2) I am confused for example when the authors say that (page 14, line 18):”The saturation responses of NEE and ER were mainly caused by N-induced decreases in aboveground plant respiration and soil microbial respiration under high N addition rates”. However on page 13 line 21 the authors stated the opposite that: “In this study, greater plant growth and aboveground biomass under N addition enhanced aboveground plant respiration and thus stimulated ER”. In the results section (page 9 line 5), the authors also state that: “Rabove increased with increasing N addition rates in 2014 (Fig. 4b) but got the maximum value at N16 in 2015 (Fig. 4e). If I look at Figs 4 d and e, these figures exactly show that plant respiration increased under increasing N additions. So why do the authors in the Conclusions state the opposite? Second, the negative trend of microbial respiration with N addition rates is not clear. If I look at Fig. 3d I don’t understand why Rmic for example decreases around 16 g N m-2 yr-1 but then almost increases again under the 32 g N m-2 yr-1. Also if ER (ecosystem respiration) overall increases in 2015 and microbial respiration decreases in the same year, how could it be possible that the two data points are positively correlated in Fig. 6C? I think this graph should only show data for 2015 and not for 2014.

Overall, these contradictions and the lack of clarity in showing and linking the results with main discussion and conclusions make it very difficult to understand the potential contribution of this study to present knowledge.

The manuscript would need more language editing. These below are some suggestions:

I would rephrase the first sentence (page 1, line 10) as:
“Increases in nitrogen (N) deposition can greatly stimulate ecosystem net carbon (C) sequestration through positive N-induced effects on plant productivity”.

Would rephrase second sentence (page 1, line 11) as: “However, how net ecosystem CO2 exchange (NEE) and its components might respond to increases in N deposition remains unclear”.

Last sentence in abstract could be changed to: “Our findings bring evidence of short-term responses to increases in N deposition, which should be considered when predicting long-term changes in ecosystem net C sequestration”.

Page 3 lines 16, change to: “It is not clear when and how ecosystem C fluxes…”

First sentence of Discussion should be changed to: “Our results show that initial ecosystem C fluxes (NEE, ER, and GEP) in 2014 suggest ecosystem N limitation, whereas in 2015 these C fluxes clearly suggest N saturation under high N addition rates”.

Lines 9-12, page 10, needs to be changed to: “These findings not only confirm the N saturation hypothesis for the response of NPP to N addition (Aber et al., 1998; Aber et al., 1989; Lovett and Goodale, 2011), but also provide comprehensive evidence of potential relationships between various ecosystem C fluxes and ecosystem N dynamics”.

Line 12, page 10: remove “most’

Line 14, page 10, change to: “Using one level of N addition only might not be enough to capture and quantify complex ecosystem responses to N addition…”

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RR by Anonymous Referee #3 (19 Apr 2017)

Suggestions for revision or reasons for rejection

This study assesses the effect of nitrogen addition on ecosystem CO2 fluxes across a nitrogen addition gradient in an alpine meadow. Hence, this set up allows for testing nonlinear effects and for saturation of responses to N addition. By inserting collars into the soil, authors also partitioned soil respiration into root and microbial respiration, addition to the process understanding of responses to N addition.
Before this manuscript can be accepted for publication, I think some aspects need to be improved.
1. Deep versus shallow collars were used to partition root from microbial respiration. This is a commom technique to use for this purpose, but just like other partitioning techniques, it does have some limitations. This should be discussed in the manuscript and also its implications for the observed responses of Rmic and Rroot need to be discussed. For example, changes in plant C allocation in response to N addition can have a strong effect on Rmic, but are excluded by the deep collar method for Rmic assessment. Hence, authors could argue that Rmic responses are not solely plant-mediated.
2. The pH effects are overstated. A regression for Rmic versus pH is the only indication for a pH effect on Rmic, but this relationship is not necessarily causal. If authors would have had an indicator for N availability (e.g. NH4 and NO3 concentrations in soil), they would have found a strong relationship with Rmic too. To find out if pH is really a potential driver of Rmic, one would have to include multiple potential drivers (like NH4 and NO3 concentrations) to test which of the drivers best predicts Rmic.
3. Statistical analyses can be improved. Instead of averaging values over the year to assess the treatment effect, a linear mixed model with time as a random factor would be more appropriate.
Also the use of R2 as a criterion for selecting a linear or a quadratic function is not the best. R2 does not penalize overfitting, and thus gives a slight advantage to the quadratic function. Using for example AIC or BIC avoids this problem.

Specific comments:
bottom p2 - top p3: this needs rephrasing. Authors say that NEE may respond nonlinearly to a N addition gradient because GPP and ER can respond nonlinearly, but that is not totally correct. If GPP and ER respond nonlinearly in the same way, NEE does not change at all.

p3, l15: 'at which time' should be 'at what N level' I suppose

p 5, l7: was the same amount of N given each month?

p6, l16: CO2 fluxes in deep collars represent a proxy for Rmic (instead of Rmic) - see also earlier comment.
p11, l14: authors state that the decline in Rmic was primarily due to the pH effect, but this statement is not well supported as no other potentially important factors were assessed. I suggest authors read for example Janssens et al (2010, Nature Geoscience) to find out about other potential reasons for Rmic to decline in response to N addition. One other possibility for reduction of Rmic in response to N addition could be a shift towards more C efficient but N demanding microbial species (Agren et al 2001, Oecologia).

p 13: authors compare their results with those of other studies. In this, they totally ignore the initial N availability as well as presence of N fixers. Both are essential though to understand differences in N effects, N saturation and the reasons behind it. I assume N availability was not measured in this experiment, or in others, but authors should recognize its importance and make readers aware that N availability needs to be assessed to further improve the understanding (differences in) responses to N addition.

Last, although the manuscript reads quite well, it still contains quite a number of grammatical errors (like missing articles in several places) and weird phrasings. Thorough language editing is thus needed.

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ED: Reconsider after major revisions (24 Apr 2017) by Michael Bahn

AR by Bing Song on behalf of the Authors (04 Jun 2017) Author's response Manuscript

ED: Referee Nomination & Report Request started (08 Jun 2017) by Michael Bahn

RR by Anonymous Referee #3 (19 Jun 2017)

Suggestions for revision or reasons for rejection

I reviewed this paper previously, but am not satisfied with the responses of the authors. The following points that I raised previously were not incorporated in an appropriate way.

1) The partitioning issue is mentioned (last lines of p14), but in a way that doesn’t clearly indicate how it may have influenced the results. I have the feeling that the authors did not really understand my suggestion that the response of Rmic from these collars that exclude roots indicates the N response of Rmic in the absence of plant C inputs. This could be used as an advantage (mechanistic insight into microbial responses in the absence of plant effects) but instead authors only defend their approach by saying that it has been used in many other studies.
On the other hand, potential artifacts should also be acknowledged. I wonder if the negative relationship between Rmic and N addition in year 2 may be related to the increase of Rmic with N addition in year 1. Is it possible that microbes changed from being N limited in year 1 to being C limited in year 2 - something that may not be the case in the presence of plant C inputs.
2) More importantly: the authors' statement that pH is driving Rmic responses is not well supported. Previously, authors had not tested any other variable, and just used the relationship between Rmic and pH to argue that pH was driving the Rmic response. In the revised version, they made 2 extra correlations: Rmic vs NH4 and Rmic vs NO3. Correlation coefficients were 0.77 for pH effect, 0.68 for NH4 effect and 0.76 for NO3 effect. This minor difference in correlation coefficients is then used to support that pH was most important, but in my view, it is not obviously better than NO3 (and I think NO3 + NH4 should have been tested too – but in a better approach). More decent statistics (e.g. stepwise regression analysis) would be needed to separate the pH effect from the NO3 effect, and if these cannot be distinguished, it should at least be shown and discussed.
3) I asked to use AIC instead of R2 to compare goodness of fit for quadratic vs linear functions. While authors indicate the AIC results in the response letter, they do not use it in the manuscript but use again R2. Even if the results are the same, this needs to be corrected.
4) I asked to improve the comparison with other experiments by considering the fact that initial nutrient availability may have been very different, and responses likely differ in nutrient-poor vs nutrient-rich systems. They did not do this, and in the response letter only show that they measured NH4 and NO3 and that it increased with N addition. This is not what I asked for. When comparing the N response of different ecosystems, the original N status should be considered. An infertile system likely responds very differently than a fertile system. If the fertility of other systems (to which the current study is compared) is unknown, authors should at least mention the relevance of it.

In addition, also language editing is still needed. Even though authors say the manuscript has been checked by a native English speaker, I found several grammatical errors (e.g. missing articles in several places, just like in the previous version).

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ED: Publish subject to minor revisions (Editor review) (29 Jun 2017) by Michael Bahn

AR by Bing Song on behalf of the Authors (12 Jul 2017) Author's response Manuscript

ED: Publish subject to minor revisions (Editor review) (31 Jul 2017) by Michael Bahn

AR by Bing Song on behalf of the Authors (02 Aug 2017) Author's response Manuscript

ED: Publish as is (04 Aug 2017) by Michael Bahn

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