In this study, Weng et al. explore the important question of how competition alters the responses of the vegetation to elevated CO2. They simulated forest responses to eCO2 along a N availability gradient using fixed and "competitively-optimal" allocation strategies. For such an important plant response (i.e. change in allocation) to global change, the detail afforded in most global models is troubling, so a study like this is very timely. Overall, I found this study interesting and one that I would like to see published in Biogeosciences. Nevertheless, I think this study will require some further revisions, particularly focussing issues of clarity (hopefully I've helped outline a few places).
My main suggestion would be to think a bit more about the discussion ...
- What do the authors want the reader to take from this study? For example, the authors open their discussion by saying: "Our model predicts increased root allocation at all nitrogen levels in response to elevated [CO2] in the competition runs." This is fine, but why not tell the reader why this happens mechanistically? What about your approach leads to this? Is it simply a consequence of what you assumed, or something more emergent? Also, what magnitude of change do you predict? And how does this vary with N availability? This seems more insightful than root allocation increased and this is broadly what you see in FACE experiments.
- Exploring this further, in the discussion about increased "fine-root overproliferation" being an emergent outcome of your simulations, could you talk a bit more about how this happens? As I understand it, you use a saturating N uptake function of root mass. In my experience, this does what it says on the tin, so there is only limited benefit in terms of increasing N with greater root investment. So, how does this differ in this study? One logical way would be if root allocation was very low to begin with, is this true here? I would suggest that the saturating root function is consistent with some of the FACE results, i.e. there is a benefit in increased N uptake, but this saturates. So, this leads me to ask how this leads to such a strong response in your experiments, over such a long time period ... This is interesting and worthy of discussion.
- It would be good to talk about competition for water and explore how both this and climate might change your model predictions. I make this point below so I won't repeat it. Particularly when you make the link to the shift to competition for light (paragraph ln 725 onwards). Those cited studies that your model result are consistent with, don't as I recall, consider an explicit role for water either ...
- Line 791: This argument is completely true, but it also stands to reason that such approaches also need to be tested against data too! Just because something has the potential to predict more variable responses to climate, does not mean the predictions are more sound! This point is developed on line 848 by calling for an improvement in model validation/benchmarking. I don't follow this argument, to be honest. There is surely plenty of data available with which you could test core elements of the predictions of your model? For example, you could use the BAAD allometry databases, or similar, you need not just focus on CO2. Moreover, asserting that because your model predicts different responses over > 1000 years than those from short term experimental responses, and so, little can (may) be learned by tested against such data is ill thought through in my opinion. You are never going to have the types of data your model will need to "validate" it. The point of manipulation experiments, or comparisons across natural gradients (e.g. N availability, aridity, temperature), is to test core elements of (what should be emergent) model behaviour. In doing so, you are or trying to ensure that the underlying principles are sound. There are a number of studies that also have competition experiments (e.g. BIOCON, PHACE, etc) admittedly in grassland ecosystems, but there are data. It is, of course, true that simply assuming the response in a short term manipulation experiment is the "truth" would be fanciful, but these are one of our best ways to ground models in data. With this paragraph, why not think a bit more creatively about what kinds of existing datasets could be used to test elements of your model predictions? You will never have the data to replicate this experiment, so one either discusses the state of data, or one appreciates quite how much data we actually have and try to make use of it.
Specific things:
----------------
- In the methods, I do not really follow the simplification from LM3-PPA to BiomeE. After reading section 2.1, I'm really unclear what the key differences are, all that is presented for guidance is: "simplified the processes of energy transfer and soil water dynamics". This could mean a wide range of things! Does that mean otherwise the models are the same? So what is gained by this simplification? Does the model perform similarly? Could this be shown?
- Following on from this...the description of how water stress affects productivity is completely unclear to me, even after reading the text on lines 212-215. From digging through the supplementary, it seems like individuals could have different levels of water stress, but do they? Do you assume different slope terms "m" in your Leuning stomatal model? Do individuals have different rooting depths?
- Following up on this point, where would an interested reader find the equations? Does Weng et al. (2017) contain all the equations? If so, can the authors more clearly indicate this at the top? My understanding is that the code is freely available, why not tell the reader of this in the methods? I know if I was reading this paper in my free time that would immediately make me more interested...
- Eqn 3 ... could the authors provide rough ranges for the targets that emerge from these equations? I would have found this very helpful as I was reading the paper. I'm anticipating that the authors will respond by saying the range could be huge given the possible combinations, so consider this an optional request. I just wanted to get a sense of how much each target varied by and over what kinds of numbers.
- where does the empirical constant representing the ratio of sapwood cross-sectional area to target leaf area come from? Is this based on measurements in any way? It presumably comes by given that leaf area and sapwood cross-sectional area are measured.
- In instances where the plant doesn't have the resources to grow, if I follow the text, then C and N are returned to the storage pools for later. How large do these pools get? How much respiration takes place? In other models applied to eCO2 experiments (e.g. CABLE, CLM), the inability to grow in response to eCO2 led to a need to up-regulate respiration to make things balance (Zaehle et al. 2014, New Phyt). There is arguably very little experimental support for this kind of behaviour, in fact the data from the EucFACE experiment would show no support at all (paper in press). This could be a worthwhile thing to comment on in the discussion of the manuscript. Does the model assumptions lead to large builds up of these stores? If it doesn't, then can the models make a mechanistic link to explain how they achieve this seems more realistic behaviour compared to other models applied to eCO2 experiments...
- I note that the other reviewers mentioned it and it is a theme I've noticed across a few of the papers from this set of authors...there are datasets that are *freely* available to test the behaviour of this and other models from this group. I don't immediately see the what is stopping these authors testing their approaches on eCO2 data? Is it because those studies don't have competition (not true of all FACE sites), but then please say so. The lead author was involved in a number of these studies and so would have access to all the data required. I realise they've added a further paragraph about the broad responses being consistent, but I find this a bit unsatisfactory to be honest. For years, modelling groups have been able to pass off general statements that their models were consistent with eCO2 experiments when they were explicitly tested, this clearly wasn't the case! Despite my reservations on this issue, this isn't a sticking point for me, the authors designed their experiment and it is not my place to tell them the paper I would have written (even if I might just have done that :P). It would be great in future work if the authors found a way to make use of the experimental data.
- With the competition angle (this could be me not quite following), you effectively have 8 PFTs competing? But you've only tested one fairly specific ecosystem (i.e. the meteorology found at Harvard forest). Presumably, your results would vary with climate? If I've followed, then I'm somewhat surprised this wasn't also a consideration? At the very least, can this be explored as a discussion point? Temperature and changing water availability (if properly parameterised, see earlier question), could conceivably change your conclusions...
- With Fig 3, would it be useful to make the allocation changes relative? It is a little hard to see the changes because of the span of different fractions on the c and d panels. Similarly, instead of showing one of either GPP or NPP, why not show the response ratio?
- Is there a reason you don't show a figure more like Fig 3 for the polyculture simulations? You seem to jump straight to the changes for basal area, I was certainly expecting a similar plot first to orientate myself.
- In fig 4g, I don't follow why the orange (RL=2) ends up being succeeded by (RL=3) after 600 years? This seems pretty abrupt and I don't see it commented on. Could the mechanism be explained further in the text? In every other panel, there seems to be a clear winner and then that is it. Similarly, across all panels, the transition between the dominance of one strategy and replacement by another looks quite abrupt. My expectation was that this would be more gradual than these plots are showing? Could the authors explain why I've got this concept so wrong! Or perhaps it is the compression of time on the x-axis that makes it seem like this visually?
Small things:
-------------
- This could be my ignorance of the difference (or lack of) but when the authors refer to "vegetation demographic models" do they simply mean dynamic vegetation model (DVMs) or DGVMs (with "global" thrown in)? If they do, would it make sense to maintain the far more common (ubiquitous?) usage? I'm usually not pedantic over such things, but to be honest I didn't see the need to redefine a very common catch-all term. It is up to the authors what they do with this point.
- How many ESMs actually have VDMs in them? It would be good to cite a few if there are, I can't think of many off the top of my head! Aren't most run offline, rather than interactively with climate? The papers cited are certainly not examples of DGVMs embedded within ESMs.
- In the methods when the authors refer to "monoculture" runs as having allocation schemes as "analogous to the fixed allocation", I have a bit of trouble with this description. To me, this says fixed fraction, i.e. X, Y and Z% to difference plant pools. But, in which DGVM is that true? Some land surface models perhaps, but DGVMs? I feel like there is a lot of space for interpretation by the reader in with the authors mean here and the "see above" would send the reader back to ~line 60 from line 150. Why not be explicit in the methods exactly what is meant? I think the clarity will only help the readability of the paper.
- The CN target of leaves seems pretty high? Where do these targets come from? Table 1 would be great with an additional column with "references". If the value isn't literature based then that column should be left empty.
- "This range covers the soil nitrogen content at Harvard Forest" - in space (across the forest?)? In time (i.e. over what time periods?)? Could the authors attempt to characterise what this range reflects in terms of N availability in the wider context of availability found globally? I suspect this would be helpful for the general reader, I don't personally have an intuitive SOM value in my head and I would have found this helpful.
- Line 344: You said that the PFT was based on an evergreen needle-leaved tree, but you're modelling a deciduous ecosystem? Is this to avoid phenology issues, then why not pick a different ecosystem!?
- Line 547 - presumably you meant to replace "significantly" and forgot to, please check.
Martin De Kauwe |
- Printer-friendly version
- Supplement
