|Review of "Projections of oceanic N2O emissions in the 21st century using the IPSL Earth System Model" by Martinez-Rey et al.|
The Authors addressed most of my comments in the revised version of the manuscript, and I’m generally satisfied with the changes and additions. In particular, the discussion of the potential shortcomings of the IPSL model, and the implications for the analysis, have been substantially expanded in the revised manuscript. The description of the N2O production parameterizations, their origin and rationale have been also clarified, and references have been provided.
Among the conclusions of the paper, the suggested increase in subsurface inventories because of increased stratification (and despite reduced production) is novel and thought provoking. The decrease in interior N2O production as a response to decreased export and remineralization is also interesting, but more in line with our expectations. The role and importance of oxygen minimum zones and suboxic waters, and of the low-O2 production pathway, is still unclear, and perhaps leads to the least robust results of the paper. However, this reflects the uncertainty that still exists in our understanding of low-O2 processes, and the shortcomings of the 3D GCM utilized. These limitations have been now thoroughly acknowledged by the Authors.
I think that the manuscript will be a useful first reference for anyone interested in the future evolution of N2O emission under climate change. It also points to processes that should be robust and of first order importance in Earth System Models (and presumably in the real world), and it suggests several aspects of the N2O cycle where more work is needed.
I still have few concerns regarding the box model formulation. I realize this is not an essential part of the paper, although it is used to gain some insight to interpret the GCM model behavior. Also, my concerns might not change the final message. However, equations 2-3, with the parameters explained in the revised text and Table S1, seem wrong as a box model of the surface and deep ocean. My problems are:
To be dimensionally consistent, and obtain rates of change (as in the left hand sides), both the mixing coefficient and the gas exchange parameter should have units of (1/time). For example, a simple interpretation would hold if the mixing coefficient was a volume transport (m3/s) divided by the box volume (m3), and the gas exchange coefficient a piston velocity (m/s) multiplied by the box surface area (m2) and divided by the box volume (m3). As they are now, expressed as dimensional fractions, these coefficients do not allow to calculate time rates of changes, and the box model does not have a clear physical meaning.
Once one realizes that the mixing terms represent a volume transport divided by the volume of the box, the mixing coefficients (v) should not be the same for the surface and deep box - a given transport of water will have much smaller effects in the deep box because of the much larger volume - unless here the surface and deep volumes are equal, which I guess the Authors could have (somewhat oddly) assumed (in which case the surface gas exchange should be quite small, because of the thickness of the surface box).
Similarly the gas exchange term is puzzling - even after correcting for the units of k (or pi) (which dimensionally should not be a fraction), the atmospheric concentrations are missing - it looks like the surface box just outgasses N2O to an atmosphere with zero mixing ratio (not a big effect but physically odd).
I suggest that the authors check their model formulation, or at least provide a consistent physical interpretation and derivation of the equations.
l. 353: initialize (typo)
l. 385: decrease increase: awkward wording
l. 487: smaller instead of less