The submitted manuscript 'The new plant functional diversity model JeDi-BACH (version 1.0) in the ICON Earth System Model (version 1.0)' describes a new land surface model that merges functionality of the JSBACH model, which is the standard land surface scheme of the ICON ESM, with a more complex representation of terrestrial vegetation, based on the JeDi model, thereby replacing the plant functional type (PFT) approach with a higher resolution of functional traits.

The idea behind this manuscript is interesting and relevant, as effects of biodiversity on climate have rarely been studied so far. However, the manuscript has several substantial deficiencies (see also detailed comments):

  1) The text is overly long, most of the methods and the description of the extended analyses should be moved to the appendix. Apart from that, the text is mostly well written.

  2) The study substantially lacks validation. It is heavily based on the work by Pavlick et al. (2013), but, unlike Pavlick et al., the authors omit evaluation of global patterns of vegetation properties (e.g. NPP, Biomass). At least it should be demonstrated that the model is able to predict a realistic distribution of vegetation cover and spatial pattern of trees and grasses. It would be straightforward to add a stand-alone simulation to compare JeDi-BACH to the original JeDi model.

  3) The conclusions of the study are not supported by the outcomes of the model experiments. Specifically, the 'stabilization' of climate at higher values of initialized functional types (higher potential diversity) is, in my opinion, rather a statistical effect and not the result of an ecological mechanism (see detailed comments below).

L30     It would be good to clearly define 'diversity' from the start.

L126    Describing leaves of temperate trees as low-cost is questionable. Also, following this argument, there should be no needle-leaf trees at high latitudes. Usually, leaf traits follow a trade-off between long-lived but slowly growing and short-lived but fast growing (the "leaf economic spectrum", which is mentioned later in the manuscript). This should be clarified here.

L136    This makes no sense to me: The PGS are defined as differing in at least one trait value, albeit by a small amount. How can they be functionally redundant when they differ in a functional trait? 

L138    How is 'sufficiently complex' defined? Trade-offs should limit the number of PGS, so increasing the number or complexity of trade-offs should reduce the number of strategies, not increase them.

L140    It is unclear why the distinction between grasses and trees is given so much weight here. There are many more possible categorizations of plants, e.g. shrubs, which do not have a stem, in contrast to trees, but do have woody roots. What about different photosynthesis pathways, leaf phenology etc.? This focus on woody tissue seems arbitrary to me.

Tab.1 I suggest to remove the term "suck up water" for root water transport, and replace it by an appropriate wording, throughout the text.

L151 It is unclear what a conceptual parameter is and how it differs from an actual plant trait.

L156 'five traits t1 to t4' ?

L159 Above, the authors write that survival is determined by the carbon storage level, here a trade-off to reproduction and growth is mentioned. This seems to be inconsistent.

L156-164 The description of the trade-offs is not well justified. Why were these trade-offs chosen, is there a body of literature to support their relevance over others, and how are they parametrized?

L230    It is not clear in which way the biomass is computed, such that it can be compared among the PGS. Is it estimated per m2 ground covered by a PGS, i.e. specific biomass? The term 'biomass density' sounds like it, but a unit for M should be provided. Without a common reference unit, summing up biomass values per grid cell makes no sense. If it is biomass per area of ground, the biomass ratio hypothesis as implemented in JeDi-BACH may lead to biased estimates in ecosystems that consist of a mixture of trees and grasses. In Savannas, trees may have a high specific biomass but low abundance in the ecosystem. Thus, the biomass ratio hypothesis would predict a large share on ecosystem biomass and productivity, but this is not consistent with observations.

L467   C4 grasses are common, but C3 grasses, too, in many regions of the world. The exclusion of C3 grasses seems arbitrary to me, and needs to be justified. From a conceptual viewpoint, this introduces a systematic bias in the prediction of PGS, since the growth form grass/tree is linked without need to photosynthesis pathways.

L482-487        This sounds as if the model was not able to simulate self-shading, so introduction of fapar_max is necessary. However, JSBACH includes canopy layers, so LAI values larger that 10 should already lead to no further gain in light. Even in a big leaf approach, high LAI values lead to very small additional carbon gain due to the exponential extinction. I do not see why fapar_max is necessary, unless the leaf construction costs are generally too low in JeDi-BACH. This needs to be better explained.

L520    The well-documented value of 2.1 (Wullschleger, 2013) could be used, or it should be justified why 1.9 is more appropriate here.

L527    This further increases the bias in tree vs. grass PGS. I suggest to make either the grasses C3 or at least test the sensitivity of the model to this setup, i.e. use the C3 photosynthesis scheme for the grasses, too, and test to what extent this affects global biomass distribution and NPP.

L540    This statement definitely needs to backed up with appropriate references and discussion. The alternative view is that plants thrive as long as leaf water potential does not drop to critical levels. In that case, low transpiration does not matter, since stomata can simply remain open for diffusion of CO2. It has even been argued that the water transport from the roots to the leaves is not essential for the provision of nutrients, hence further reducing potentially negative impacts of saturated air.

L645    This is a relatively arbitrary choice and the sensitivity of the global biomass distribution and NPP to this choice needs to be tested.

L794    While this adaptation saves computational time, it introduces an imbalance into the competition for water and light, if I understand correctly. There seems to be no impact of LAI of a PGS on the absorption of light by another PGS, but the root length of a PGS will affect water availability of other PGS through the shared soil water pool. This should at least be discussed.

L803    As the main outcome of this study is the effect of vegetation on the global water cycle, this is a substantial limitation regarding the interpretation of the model results. A stand-alone setup with prescribed meteorological fields is required and the simulated global distributions of biomass and NPP need to be compared to the coupled model run.

L808-836        This part is overly long and should be shortened by at least 50%.

L820    Better: 'To address this issue...'

L886    Indeed, it would be better to make this clear from the start of the manuscript, please change this.

L908    This distribution looks substantially different from Fig. 8a in Pavlick et al. (2013), and, more importantly, it does not show much similarity to the global species richness pattern of plants, in contrast to the original JeDi model. This needs to be addressed somewhere.

L919    I do not think that this pattern agrees well with Barthlott et al (1996), in particular since the stand-alone JeDi performed better.

L922    I strongly disagree with this statement. The value of actual diversity in this model is arbitrary, you only need to increase the number of initial PGS to increase absolute diversity. It is the pattern of relative diversity which is ecologically meaningful.

L926    I do not think that the higher vegetation coverage in the high diversity simulation is convincing in general. A relative diversity of up to 10% in the Sahara is highly unrealistic, even if these are all grass PFTs. There is no extensive vegetation cover in the Sahara. In contrast, no PGS seem to survive in Western Siberia, which is probably due to bias in the climate model. Again, I recommend to run at least one stand-alone simulation to test if these unrealistic patterns result from the uncalibrated climate model or from deficiencies in JeDi-BACH. 

L966    While the convergence is expected at a sufficient number of initialized PGS, what surprises me is the low standard deviation of the distribution. For the high initial diversity ensembles, it looks like more than 50% of all surviving PGS have a CWM value around 0.5, which means that there is little selection towards certain trait values happening in the model. It is clear that the variation of climate at the land surface likely covers a large part of the potential trait range, and summing up CWMs from different regions of the world will drive the distribution to the mean value. However, climate regions are not equally distributed, which means that CWMs from regions that contain many grid cells should have a larger influence on the distribution. I would like to see the global pattern of the CWM(t3).

L982-999        It is not clear to me why the idea of 'high biomass islands' is necessary here. For any given environment, there will be a certain number of locations in the multidimensional trait space that allow survival of the corresponding PGS. As soon as the number of initialized PGS is large enough to sample all these regions, the results of the ensemble simulations will converge, as a more frequent or 'dense' sampling of these regions will not result in further functional variation, but simply a higher number of similar PGS. If there is more to that model outcome than a purely statistical effect, it should be more clearly described.

L1016   I do not think that this conclusion is justified. The authors write above that trees have a lower chance of survival than grass PGS, and they also note that at low initial diversity a larger part of the global land surface remains free of vegetation. This alone would lead to lower evapotranspiration in the simulations with low initial diversity, as bare soil evaporation is lower than transpiration, and grasses on average are less efficient in accessing water in deeper soil layers. The other effects are simply the result of the well-known moisture recycling effect over the land surface (e.g. Zemp et al., 2017, Nat.Comm.). The term 'stabilization' is misleading here. As I wrote in the previous comment, the convergence of the diversity estimates and, consequently, the global vegetation properties, can be interpreted as outcome of a sufficient sampling of the trait space. Stabilization, however, suggests that there is some mechanism that leads to a certain value of a flux, such as evapotranspiration, at high diversity. If the authors identified such a mechanism, it should be better described.

L1029   In principle, I agree with the authors that the low number of PFTs used in many land surface models may promote the simulation of climatic conditions that are too sensitive to the parametrizations of the PFTs. However, an important detail is not mentioned here: Fig. 8 clearly shows that the majority of grid cells exhibits CWM values around 0.5 for trait t3. If this is the case for other traits, too, then the selection algorithm in JeDi-BACH mainly chooses 'average' PGS as survivors in most regions of the world. Otherwise, the frequency distributions of CWMs across all grid cells should be broader or more skewed. PFTs are typically parametrized according to 'average' plants, so the mismatch to the JeDi-BACH estimates and the consequences for simulated climate feedbacks may be much smaller than expected.

L1106   A Mann-Whitney-U test is used to check if values drawn from two distributions show a tendency to differ from each other. It is not clear to me how the presented sensitivity analysis justifies the application of such a test, since for each distribution (characterized by ctrl, increased, and decreased parameter value), only one sample is drawn, so there is no basis to characterize the distributions. This should be either removed from the manuscript or better explained.

L1190   I think the statistical basis for such a conclusion is not sufficient here (see previous comment). While it is logical that a strong change in vegetation structure may affect regional climate via impacts on transpiration and the hydrological cycle, Figs. 13 -15 show marked effects of the parameter variation in all regions of the world, also those with high diversity. Since I do not follow the explanation of the test for statistical significance, I also consider these regions affected by the parameter changes, meaning that high diversity may not necessarily promote a stabilization of regional climate.

I received the request to review the manuscript following minor revisions.

I read the manuscript with interest and don't have any concerns, objections or recommendations.

Therefore, I think, the manuscript can be published as is.

PS: Figure 12a: y-axis: "terrestrial" instead of "terrestrail"