I greatly appreciate the considerable efforts that the authors have spent to deal with my review comments. Their responses and the corresponding changes to the text are very good and convincing. Some issues will always remain, both with the model as well as with the data (we never have the "ideal" model, and data have their own pitfalls), but the authors have done a very good job clarifying what they have done, and in many instances even changing their approach (e.g. re. LAI). I think the manuscript is ready to go now. Congratulations! :-)

I thank the authors for the detailed replies and have no further questions or comments on the manuscript.

General comments

In this manuscript, the authors develop the well-known physiological model CASTANEA/PDG further to be able to evaluate tree mixtures and the impacts of this diversity on productivity. The resulting model is called PDG-Arena (note that it is not explained anywhere why this is "Arena"). The authors are using this model to simulate 39 forest plots (r = 10 m, i.e. merely 314 m2 each) from three sites that feature different mixtures (as well as monospecific plots). They use a smart design to "regularize" the measured plots towards uniform distributions of trees in horizontal space as well as mimicking single-species plots where in reality there are mixed-species plots; this allows them to disentangle the diversity effects nicely.

The results suggest that (1) PDG-Arena performs somewhat better than CASTANEA for these plots, and (2) that there is a small positive biodiversity effect indeed.

The development of PDG-Arena is described coherently and in a transparent manner. Yet, there is some discrepany between the plea of the authors that mechanistic, ecophysiologically-based formulations need to be sought, and the fact that multiple simplifying assumptions are made that are countering this endeavor somewhat; for example that truncs are ignored for the calculation of radiation although it is known that they can absorb a considerable fraction of the sunlight, and are also important for backscattering; or the assumption that there is no differentation between trees (in terms of sizes or species) regarding rooting behavior, which likely has strong implications for water competition in real stands. Undoubtedly any model needs to be based on simplifying assumptions. Some of them are addressed in the Discussion section (e.g. the rooting problem), but they are not put in context with the results of the study, unfortunately. Others are not addressed at all.

There are larger worries regarding the data used for benchmarking the simulations. The description of the data is not very clear. I presume that an initial inventory of the 39 plots was made in 1996 (this is why the simulations are starting in 1996), but no further inventories were executed (this is not clarified anywhere). It then appears that the growth of the trees was analyzed using dendrochronology (l. 213). It would be important to know whether all 1177 stems (l. 277) were cored indeed (this would be a huge amount of work!), or whether this was done only for a subset of the trees; but this is not stated anywhere. More importantly, tree height was assumed to be constant (l. 208), i.e. no height increment was simulated over 17 years (1996-2013), whereas growth was assumed to be BAI times tree height, which induces a strong bias in the simulation results as well as in the data (assuming that woody increment was calculated from the data using the same assumption - this is not stated anywhere, though). But if height was constant indeed, why not compare BAI (obs) against BAI (sim)? This would be a much more straightforward comparison (let's not even think about issues such as form factors etc.).

The simulation results nicely show the patterns hypothesized by the authors. Yet, they left me concerned. On the one hand, the effects induced by moving from CASTANEA to the three simulation studies with PDG-Arena (using three assumptions re. stand structure) are really very minor (Tab. 3 of the manuscript), with the r2 always being >0.965. Hence we are talking about minute effects here. On the other hand, the performance of any of the simulations appears poor to very poor (Tab. 4 of the manuscript) compared to measured (?; cf. above - what was actually measured, and how?) wood volume increment. Clearly PDG-Arena has the best performance, but this does not exceed an r2 of 0.5 and does not go below an error of 34%, which is clearly not satisfactory. Thus, the question arises whether these results can actually be trusted. It appears that both models would need to undergo additional development to be able to represent stand growth over a period of 17 years accurately, particularly since the initial situation was taken exactly from the measurements (inventory).

In that same context, the authors mention that LAI data are from the recent drought period (l. 216 and 418) whereas the inventory data are from nearly 30 yrs ago. This may explain the divergence between LAI values of ca. 3 (single-sided, I presume) and the very high BA values (ca. 50-60 m2/ha), which are hard to reconcile and may lead to strong inconsistencies in a model that is driven by radiation, and thus LAI. It is not clear whether LAI was set to a constant across the simulation time, using the 2022/2023 values. This would be a highly debatable assumption.

Importantly, one aspect that would be key for simulations across multiple years with a dynamic model is not addressed in the results shown in this study at all: it appears that all that is tested is diameter increment (and indirectly, volume increment using a static tree height), but not the development of any other tree characteristics such as height, the height of the crown base, leaf mass or leaf area, let alone allocation to belowground compartments (for which admittedly there would most likely not be any data). It would have been highly insightful to compare the simulated stands at the end of the inventory period (2013 - was there really no inventory carried out at that point in time?) against measurements. Focusing the comparison on simulated GPP among models and woody increment between models and a tree ring reconstruction leaves many questions unanswered. The inference drawn in this manuscript re. biodiversity effects is only believable if PDG-Arena is shown to realistically reflect the dynamics of these 39 plots, but the manuscript falls short in this regard, I am sorry to say.

The Discussion is relatively short and not structured very well. This should be reconsidered.

Detailed comments (by line numbers of the manuscript)

Abstract: is basically fine, but contains a few typos. Pls check (I cannot refer to line numbers here).

9: replace "if" by "even though".

119: "dynamic" -> "dynamics".

127: excess comma after "multi-layer".

138f.: cumbersome wording; better "are expressed on a per area basis, e.g. gross primary production is expressed as gC/m2". The use of "soil" and "surface" is confusing in this context.

Fig. 1: The caption needs to be re-worked. The use of "hold" (and "held") should be replaced by verbs such as "calculate" or "perform"; si en français on peut dire "tenir/tenu" (honnêtement, je ne sais pas), ça ne se traduit pas en "hold/held". Also, "a trees crowns" is not correct grammar. Either "a tree's crown", or "the trees' crowns", or something similar.

142: wording issue - "the projected area of the individual crowns" (again, avoid "surface" here). I think this would say it all, and the comparison to the stand area is simply not needed.

159: omit second occurrence of "water" (not needed).

186: "operates two executions" is cumbersome wording. Replace by something like "evaluates light conditions using SamsaraLight in two steps for every simulation year".

188: "radiations" -> "radiation" (twice). This is probably the same thing as "les précipitations", which is simply "precipitation" in English. No plural possible here.

189: omit "every year".

193: "a" -> "the" (it is not a model, but "the model" here).

197: I was confused by the word "parameter" here. These are variables that should change dynamically in the model, right? A parameter is a constant. I appreciate that later we are told that h and hcb are held constant in the simulations, but here they should still be called "variables".

273: "at plot" -> "at the plot".

277: were indeed all 1177 trees cored? Was this done in 2014, and this is the reason why the time series extends to 2013 only? Or was a second (?) inventory done in 2013 (cf. l. 281)? This should be clarified. If the reader does not understand the data, the benchmarking cannot be understood fully either.

279: so was tree height kept constant across time? This is not clear either.

281: How many field inventories have been made? Just one in 1996? If more are available, why weren't they used for the benchmarking of the models (cf. General comments)?

289: Although I am intrigued by the approach taken here to generate synthetic stands that systematically miss certain aspects (compared to reality) such as species or species interactions, I found the description very difficult to follow and am not really sure I have understood. The setup O is straightforward, and in the setup RS tree positions were "regularized" (not sure this is a proper English term, but I understand). But what is the essence of the difference between RS and RN? This remains elusive to me, even after repeated reading of l. 293-297. Pls re-consider.

333: "informs" -> "inform".

334: it is not about the "presence" of physiological processes, but their importance. Pls adjust.

344: not clear what "modalities" is referring to here - the different sets of simulations, I guess? The term has not been used before, I think, and therefore should be avoided.

349-351: yes I agree, but the differences are really minute (cf. General comments).

352: "Modeling" -> "Model" ("modeling" refers to the process of developing the model).

398: "of" -> "or".

404-407: yes I agree, but on a (very) low level. Are the differences trustworthy if model performance is so low (cf. General comments)?

417: why is Bauges singled out here? cf. l. 217.

432: fix reference (parenthesis issue).

445: excess comma after "fluxes".

448-450: this is - theoretically - possible; however I have the strong feeling that the smallest fraction of the poor model performance is due to the climate interpolation. I am not convinced that this has deserved such prominence here.

466: perhaps have a separate section "Conclusions"?

467: "accurately simulate"... based on this study? I think this is an overstatement.

The authors built a new model by introducing tree species interaction into CASTANEA. Trees compete for water and light. Models with and without interaction are tested against each other for several sites with beech and fir. Including interaction between trees improved the performance of the model when compared with measurements.

Interaction between trees, of the same or different species, is an area where we have little knowledge. At the same time it is the belief that mixing tree species is a way to increase the resilience of forest ecosystems. Having a model that can reliably represent tree interaction is therefore very valuable, especially since there are not many of these models. Hence, the presented model and the promising results of this paper add an important tool to the toolbox of forest resilience researchers.

Some questions/remarks, in no particular order:

1) Competition for water and light is implemented, but there is no competition for nutrients, even if the authors themselves mention it in the introduction as being important (line 45). Shortly mentioning why this has not been done (and maybe possible consequences?) would be helpful. Maybe either in relation to mentioning ‚limiting resources‘ (line 436), or when discussing possible improvements of the model (lines 451-465)?

2) What is meant by global change? (e.g. line 49)

3) If there is limited water available, is all water divided equally among the trees? Or is water uptake connected to transpiration? In other words, how does competition for water take place? (section 2.1.2)

4) There is no vertical or horizontal differentation of soil water availability (lines 160-164). For the lack of horizontal differentation an explanation is added, but not for the lack of vertical differentation (although it is discussed in the discussion). I suggest either discussing/mentioning both here (lines 163-164), or neither (and discuss both in the discussion).

5) Calling mixing two different tree species „biodiversity“ is a bit of a stretch. After all, one can think of many more factors being of importance for biodiversity that all contribute to „mantaining key ecosystem services“ (line 5-6). I’m fully aware that it is difficult to quantify biodiversity or to somehow distill it out of model results and I agree that using the number of different tree species is a good first step/approximation, but I would be careful with the terminology. I propose to change the ‚net biodiversity effect (NBE)‘ to net mixing effect, or something along those lines, or otherwise clearly state that number of tree species is used as a proxy for biodiversity.

6) Since the paper introduces a new model, I think it would be nice to shortly discuss the limits/opportunities of the model. For what kind of setups can it be used? What are the size limitations of the plots? Can it be used for more than two different tree species? Can trees completely cover each other (undergrowth)? Etcetera

I didn’t specifically check for typos/grammar, but here are the ones I came across:

Abstract: the model builds upon a validated…

Line 31: „different nature“, different than what?

Line 52: confounding factorS

Line 56: To what does „this approach“ refer? I assume a modelling approach or something like that?

Line 62: community compositionS

Line 74: When it comes to simulatING

Line 218: proportional

Line 333: to inform us 

Line 398: more OR less

Line 562: attenuation coefficientS

Line 570: through the canopy