The manuscript describes the BORIS-2 model, a benthic ecosystem model based on class size that builds on a previous version that simulated ecosystems with a smaller size range and different representation of physiological processes. It describes a steady state solution used to test and evaluate the model and compare it to data from five different sites with a range of depths and overlying pelagic environments.

The authors did an excellent job organizing the manuscript; the explanation on the model itself, the validation and choice of coefficients, and the differences between the current version and BORIS-1 are well written and well linked when necessary. The arguments justifying the choices that need to be made to choose general coefficients and forcings to represent the different sites are well argued and informative for users that may want to run a transient version.  

The figures and tables are clear and contain all the necessary information. In my view the paper is suitable for publication, although I do have a few of suggestions on the text:

Line 289-291: It seems reasonable to me to use the sediment traps at 3000 m, but out of curiosity, how much to they diverge? Thinking of future exercises linking ecosystem to sediment diagenetic processes, information of resuspension/sedimentation is always useful

Line 304-307: these sentences could be linked better

Line 519-521: The global estimate of carbon burial also shows spatial variation, thought to be much higher in shelf environments. I would assume there could be differences between the shallower and deeper sites chosen for model validation that could be mentioned or briefly discussed here.

In this manuscript Martin et al. provide a model description and evaluation of an updated benthic community model, BORIS2. This model is a size based model of benthic heterotrophs / detritivores and extends the size range of the previous BORIS model both on the lower and upper ranges. Compared with the previous BORIS model, this second version also makes a number of improvements on the assumptions around metabolism and ingestion. This model is evaluated against 5 sites, including abyssal sites at the Porcupine abyssal plain and clarion clipperton zone. The inclusion of these two deep sites makes it so that this model is much more readily applicable for regional or other large-scale domains.

Main comments

My primary concern in this manuscript surrounds the introduction of the interference parameter, a_i. This parameter is described as the competitive interference between other scavengers, and shows up in the growth/feeding equation as modifying the biomass B. My concern about this primarily is because the size scaling parameters for the other processes are all identical (see next paragraph) – the entirety of the emergent structure of the community relies on this single parameter, which is very poorly understood and is not common to other ecosystem models. The functional form of the feeding relationship changes such that if you were to rewrite it to an equivalent Monod-like relationship, it would be g*f(R,B) = gR/(R+aB) but instead of a fixed half-saturation constant, aB varies with mass. So then the initial slope becomes R/aB. While I am not doubting that the introduction of a size-dependent scaling for Biomass in this feeding relationship could be useful, unfortunately I am also not convinced of the need for it either. Perhaps it is because I am not familiar with DeAngelis et al. 1975. To convince readers, perhaps the authors could show plots of this functional form (at a minimum), and ideally some more plots showing the authors’ central claim here, that you cannot achieve an emergent community structure in this model that matches observations without this parameter included. Personally, I think that it may be possible to achieve reasonable matches with the observations with more parsimonious parameterizations, if the scaling exponents for the other processes were allowed to vary.

The scaling exponents for growth, respiration, and mortality are all the same and set to -0.1. It is not the most common practice amongst community/ecosystem models to set all of the biomass scaling exponents to be the same value. As the authors state in section 2.7, a more common scaling for growth and respiration would be around -0.2 or -0.25 (I think the theoretical prediction would be -0.25 but realistic values may vary). However, mortality is often assumed to have a different scaling than growth and respiration. Here, in this model, there is no representation of predators of these organisms (i.e., demersal fish) so I was a little surprised that the authors removed the quadratic loss term, and did not tune the mortality scaling to implicitly represent the role of predators within the ecosystem. In this case the emergent community structure then arises from the relationship between growth-respiration and mortality.  

Can you describe a bit more what ends up being the closure term in the model, and if not – whether the lack of a closure term ends up constraining your parameter space so that bottom-up control can be the dominant control for the ecosystem?

Finally, for the benthos, the authors use the scaling exponent of the biomass size spectrum to constrain the model. I completely understand that these are very poorly observed systems and that available observational constraints are few and far in between. However, the danger in using the biomass size spectrum slope to validate the model is that very small variations in the size spectrum slope can have large implications for the total biomass. From a quick calculation, a 10% variation in the (normalized) biomass size spectrum slope (from -0.5 to -0.55) for a community that spans 10 orders of magnitude in size (e.g. 1 to 1e10 micrograms C) would result in a 3-fold difference in total community biomass. (This is using the fact that the normalized biomass size spectrum is integrable). Ecosystem modelers would certainly consider a 10% difference from an observed quantity to be an absolutely excellent match – but here the implications for total community biomass become quite large when the observed quantity used for model validation is a scaling exponent.

What would enhance this manuscript would be a series of sensitivity studies showing focused (generally) on the range of parameter space for this model. I appreciated that the authors included section 2.7 but I found it difficult to follow without some examples in the manuscript. Ideally, it would be great to see what the model results are when interference pre-factor were set to low values and the interference exponent was set to 0, combined with allowing beta of mortality to vary relative to the beta of growth and respiration, but I leave it up to the authors to decide what would be most appropriate.

Lastly – it would be remis for me to write all this without noting that it is extremely difficult to model a system that is as poorly observed and understood as the benthos. All model representations of a new system must start somewhere and BORIS1/BORIS2 is notable as the first of its kind.  I apologize for the somewhat rambling paragraphs above – but in my mind, all these model and parameter choices are all highly connected with each other.

Minor comments

Lines 112-113, I think fg should be kg, right?

Line 260, I found it confusing that the biomass scaling (alpha) was defined as a negative, resulting in values that are negative. I look into the benthos observations literature specifically and did not get the sense that this was common practice. If not common practice can you just use the raw values, allowing alpha to be positive?

Section 2.7, lines 385-384, 406-425. I overall like this discussion but found it hard to follow without some more concrete examples.