General comments

This manuscript tackles the considerable challenge of parameterizing a highly detailed, process-based model of forest dynamics for 217 taxa towards an application at the regional scale (ca. 30'000 km2; Catalonia, Spain). It is a methodologically interesting and valuable contribution that I think should be published, notwithstanding my concerns detailed in the paragraphs below.

First, the manuscript tries to make the point that highly detailed models that distinguish a very large number of very detailed ecophysiological processes are useful (or perhaps even needed?) for faithful assessments of climate change impacts on forest dynamics. I am hesitant to accept this. The description of MEDFATE in this paper shows that it is based on multiple assumptions that are highly uncertain. Hence, different assumptions (i.e., different formulations) could have been chosen, leading on the one hand to different parameter requirements and on the other hand to different model behavior at least at some 'intermediate' level (i.e., between the ecophysiological processes and what is ultimately shown in Fig. 3, i.e. ecosystem-level NPP and wood volume). Thus, we cannot really tell whether the model is getting the right answer for the right reasons, or whether errors are compensating each other internally, thus actually enhancing the uncertainty in future projections rather than decreasing them. In this context, it is somewhat marring that the simpler variant of the model is generally closer to the measurements in what the authors call model "evaluation" (although the data are not independent of those used for the parameterization; more on that under the "Specific comments" below). I would have appreciated if the authors had used both model variants for the future projections - they mention computational reasons for not doing so, but even a 1728 h (= 72 days) simulation effort might be undertaken as a "production run" for such a paper. It would be quite instructive to see whether the two variants agree under future conditions.

Second, while I admire the effort and creativity employed by the authors to come up with parameter values (a total of ca. 25'000 parameter values had to be estimated!), I am concerned about the vast number of parameters that had to be estimated by imputation based on partly shaky assumptions (cf. below). And using a default value across all taxa is a somewhat desperate assumption to begin with. Such things induce a lot of uncertainty in the model on top of those mentioned above re. process formulations. So how much signal is actually gained by using a highly resolved approach when the projections are blurred by uncertainties in both process formulations and parameter estimates? It would appear to me (but this is not coming as a surprise) that going to this level of detail is not appropriate, and simpler models (such as the IPM...) should be used.

Third, I think for the manuscript to be more convincing, the authors would need to do a better job re. model validation, particularly regarding the "intermediate" levels in the model, to show that it does capture ecosystem structure and function and their dynamics reasonably well. It is only then that we could "trust" the regional-scale projections. In the current stetup, the manuscript does not provide any model validation in the strict sense, which I think is unfortunate.

Specific comments (referred to by line number)

65: It would be relevant to expand a little bit on what "sufficient" actually is - in the present sentence, this is a claim whose scope is hard to assess. It appears that the starting point for the authors is that a detailed treatment of the energy, water and carbon balance is a pre-requisite for any vegetation model, and demography is "nice to have". One could view things exactly the other way around when focusing on the regional scale (cf. the statements on l. 50-51, and the application of the model to project wood volume).

72-74: The nature of "trait-enabled" should be phrased in a more comprehensible manner for readers who are not familiar with the concept. I would write something like "...are 'trait-enabled', in the sense that their parameters can be linked quantiatively to easily measurable plant traits for which large-scale data bases exist." - and if you should disagree with such formulation, you would need to explain even better because I wouldn't have understood either...

87: I think it is not quite fair to state that "all these approaches ignore taxonomic information". I think all of them do consider them, although in widely different form. Your approach differs from these other approaches by being much more consistent in linking species parameters to plant traits at different levels of taxonomic resolution, rather than to impose one level of resolution across the model (as e.g. the 'classical' DGVMs with their PFTs are doing).

90-91: "trait coordination" and later also "trait syndromes" or "functional syndromes": I presume your are referring to "trade-offs" between traits here? If so, pls use this more common term. And if you mean something else, pls explain better.

279-290: The assumptions about the causes of tree mortality (starvation and desiccation) are a bit shaky. Mortality formulations are highly likely to be pivotal for model behavior, and hence they require careful thought and parameterization. I am not convinced that the assumption of "30% of maximum" for both processes is appropriate. Furthermore, I was surprised to read that turgor loss (to 30% of max symplastic water content) is a key cause of mortality in MEDFATE - to the best of my knowledge, wilting is easily reversible, but plant hydraulic failure is a syndrome that is more difficult to overcome (although I disagree with the authors' interpretation of the Choat et al. 2018 paper in that regard, but this is not the major point here). So why should I trust these formulations and their parameterization?

315: The authors later (in the Discussion) acknowledge the problems with using the SoilGrids database. We have tried multiple times to use that database for estimating soil properties for simulation studies, and have always given up because of truly strange results, taking resort to other sources of data. Wouldn't there be a better data product for Catalonia?

338-341: So the SNFI data were used for model "tuning". This means that what is shown in section 5.1 is not a "model evaluation" in the sense of a validation. These results have been forced, which strongly reduces their usefulness for demonstrating the skill of the model. I think alternative model validation data would be needed. I am aware that this may be everything but easy. However, this is a major weakness of the manuscript.

362: I wouldn't use this example, as RGGS is not explained anywhere in the main paper. At the same time, however, I appreciated this very example because it shows how uncertain the parameterization procedures used here actually are: shade tolerance (sensu Niinemets & Valladares) is a highly aggregated concept that is pragmatically useful in some models, but probably not in highly detailed ones. Why should shade tolerance be related to these traits, and even in a linear manner? We have recently evaluated whether we can relate P88 (or P50) from the TRY database to the species' drought tolerance (according to Niinements & Valladares). The correlation is essentially non-existing, because the two concepts relate to vastly different levels of integration, and actually no relationship should be expected to begin with.

460 (Tab. 3): Why are there different entires under "Mean observed" for the basic vs. advanced model version (and again different for the IPM)? This is not explained anywhere, and the 'naïve' reader would expect the observations to be independent of the model resolution?!

578-580: This assertion is only valid if the processes are captured in the right way, which may not be the case (see general comments on structural uncertainties in the model). I suggest being more careful here.

599-600: Even if one follows this conclusion (which I do not really, for all the reasons mentioned above), one easily arrives at the question why a very complicated model like MEDFATE is actually used if the goal is indeed to "only" project regional standing timber volume. Simpler approaches would be equally suitable, would be inflicted with fewer uncertainties, and are even likely to provide more robust results. So why go with MEDFATE in this case? See also lines 635, where many more variables are mentioned that are of (potential) interest for forest management planning - but none of them are shown here, and the question arises how accurately they are projected by MEDFATE.

Technical comments

The manuscript is generally easy to read and understand, but it should still undergo a careful linguistic check before it is being published. I am pointing out examples of the kind of issues below, this is not a comprehensive list.

63: "impact these" -> "impact of these".

70: remove "into model parameters" (simply not needed). Then "while it is known that" -> "as".

83: "consists in" -> "consists of".

91: "within- and among-": remove dashes.

110: Not clear how one can add processes to TWO preceding models. Below, two different additions ("basic" and "advanced") are explained that relate to ONE preceding model version. Pls clarify (consider using the terms "version" or "variant" when refering to these entities, maybe this would help).

196: "conforms" -> "constitutes" ???

222: replace "and" by a comma (note that this is another documentation of high structural uncertainty in the model, cf. comments further above).

271, 272: "feedback" -> "feed back" (the verb is used here, not the noun).

272: add a comma before "and" (a full sentence = main clause is starting here).

292: remove "but" (grammatically incorrect, not needed).

303: "includes a strong" -> "includes strong".

309: remove "different" (simply not needed).

310: number of SNFI plots in inventory #2 is not given here. Why?

369: "aim make" -> "aim to make".

395: "found" -> "find".

432-433: Why not between the second and the fourth inventory? This would have provided a longer time series and thus better insights into model behavior. The shorter the 'evaluation' period (when the model is initialized with the data from the first inventory, and this is what was done here, I suppose), then the more difficult it is for any model to be wrong - because the initial data is most likely the strongest predictor of its skill, not the model-internal processes. Hence this 12-year (?) period is a really short snippet for a model test, on top of the non-independence of the data (cf. comments further above).

507: "First": there is no "second" further below. Re-consider the structure of this paragraph.

554: "account" -> "amount".

560: "intra-specific can" -> "intra-specific variation can" (?).

575: "focus" -> "foci".

596: "prediction forest" -> "prediction of forest".

599: "confidence on" -> "confidence in".

614: "this equations" -> "these equations".

615: "dessication" -> "desiccation" (also elsewhere).

623: "perform under" -> "perform well under".

650: "think MEDFATE can be" -> "think that MEDFATE is".

General Comments

The manuscript of De Cáceres and colleagues is an interesting study that describes the design of a forest dynamics model that is parameterised based on a diverse range of datasets from forest inventory to allometric and physiological datasets. In doing so the authors provide a systematic presentation of their methodology to derive the parameters needed to run the model at a regional scale. This study supports a model design that maintains the taxonomic resolution of species which is probably  more relevant for forest management simulations in contrast to other approaches that use traits distributions to incorporate the range of functional diversity.  

The ms is well structured and the methods employed are adequately described, taken into account the wide range of work that the authors put in this study. I believe that this study is an important step towards a better understanding and simulation of Mediterranean forest dynamics and should be published. However, I believe that the authors need to make clear that their approach essentially uses trait average values for parameterising a the species under study, thus it does not enable plastic responses especially under climate change conditions. Also I think that the authors should also expand their simulation outputs under climate change conditions in a more species specific rationale, as for example aggregating all simulations in figures like Figure 3 does not help the reader to evaluate the ability of the model to provide species specific responses (which is also one of the advantages of the MEDFATE).

Specific Comments

L54: year missing from first reference

L63: the impact +”of” these

L98-L101. Please rephrase, this sentence is not very clear

L108-109: You are not only illustrating the challenges that you encountered but also provide suggestions for solving them 😊

L124. Please explain a bit better what you mean by density variable? Is it just the number of individuals per area, per species per area? 

L221 “although”

L343 Does each tree species have a species-specific probability of ingrowth model based on the three bioclimatic variables?

L369 With the aim “to”

L383 the large amount “of”  

L388 “of” leaves and fine roots

5.1 Evaluation with SNFI data. I do not understand here why you do not compare the predicted BA changes of the different models with the actual observed BA from the plots data. Also why the mean observed BA is different for the two sub-models? This is what you compare against no?. Also shouldn’t the units be m2 ha-1 y-1 in Table 3?

L451 “…predictions we …” something is missing here (observed?)

L482  Predicted “from/by” the model

L493 “could/are predicted to” cause widespread drought-induced defoliation

L494. I think it would be good to present in separate figures the “evolution” of ingrowth and mortality for each species. You should expect some species to be show higher drought vulnerability based on the parameterisation of your drought response.

L507-509. Strange sentence, please rephrase

L512-514. Agree but also some might expect that the demographic parameters should emerge as properties of a fully developed trait-enabled model. The forest inventory data could then be used to validate the recruitment and mortality submodels?

L560 Second, intra-specific… something is missing

L611. Please provide year of publication

L638 “delete second “estimates”

L644 “an hybrid”?

Appendix C

C.1

Line 697, are the extinction coefficients the same for each taxon? If not please specify.

C.2 Details of the estimation of transpiration and photosynthesis parameters of the basic sub-model

The approach the authors follow here to infer the parameters of the basic submodel (meta-modelling) is interesting, but it assumes that the advanced model simulations are correct, no? Do you have any data to validate this, or at least show that is behaves relatively realistically?

Table C3.  I would make bold only the statistically significant correlation in the upper right part of the table.