General comments:

Wang and co-workers address in their paper "Sensitivity of asymmetric Oxygen Minimum Zones to remineralization rate and mixing intensity in the tropical Pacific using a basin-scale model (OGCM-DMEC V1.2)" one of the still open issues on understanding the interplay between the physical ocean and the marine biogeochemistry in shaping OMZs. Based on a basin-scale model with a high horizontal resolution they perform sensitivity studies with a set of vertical mixing parameters and a reduced DON remineralisation rate. With the final parameter set they state that the model successfully reproduces the observed asymmetric OMZ.

Unfortunately, there is no new scientific finding in this paper. The results are very descriptive without any critical assessment.  Furthermore, the “improved model” setup is only evaluated wrt. oxygen distributions. Potential effects on other biological components and/or processes due to the new parametrisation are not analysed, even so, changes in the OMZ might feedback onto the net community production. The authors state in their conclusion that a “reduced remineralization rate leads to remarkable decrease of biological consumption over 200- 400 m”. This is a rather trivial finding.   

The physical and biological component of the applied OGCM are not sufficiently introduced.  Only after reading previous papers of the authors I could gain a rudimentary understanding of the physical model setup. It would be useful to describe at least the major characteristics of the physical model. I also find that it is not a sufficient introduction of the biogeochemical component to only provide its equations in an Appendix.  A more detailed description might be “boring” to the authors but it is very useful for the readers to get the basic concept of their model assumptions.

Moreover the oxygen cycle, the core topic of this paper, seems to be newly implemented into the biogeochemical module. However, a comprehensive introduction is missing. It would be interesting to know:  1) how is guaranteed that oxygen consumption does not exceed available oxygen?  2) are there any restrictions to remineralization depending on oxygen levels?  Oxygen consumption from NH4 oxidation seems to be missing or is neglected.  Oxygen production/consumption is calculated with a fixed ratio from NCP. However, photosynthesis based on nitrate produces a higher amount of oxygen than on NH4. Similarily, remineralization to NH4 needs less O2.   

Furthermore, there is no sentence on nitrogen reduction processes such as denitrification, whose activity is highly correlated with export production in the ETSP (Kalvelage etal, 2013).  As no values are given for NCP, export production, and also the distributions of nutrients or detritus are not provided it is impossible for the reader to judge the quality of the model performance.  As far as I know, there has been previously no assessment of their biological component for the depth range below 200m.  

In view of the extensive degree of revision, I refrain from specific and technical comments.   

The manuscript, “Sensitivity of asymmetric Oxygen Minimum Zones to remineralization rate and mixing intensity in the tropical Pacific using a basin-scale model (OGCM-DMEC V1.2)” by Wang et al. conduct a suite of model parameter sensitivity experiments with a very old, coarse resolution regional physical ocean model.  While using an older model is not necessarily a disadvantage, it is only an advantage is the relative strengths and weaknesses of the model are provided such that the reader can integrate the current analysis to other current understanding.  That context is not currently provided.  For example, focusing on this region has the advantage that the sponge resets the source O2 (a major weakness of global models) to observations (the authors should note this strength of the current approach).  Unfortunately, the comparability of the physical formulation to other models is missing.   For example, it is unclear whether the Indonesian Throughflow is represented which is an important part of the advective ventilation in the Western part of the basin and the partitioning of lateral oxygen source waters into the Eastern part of the basin.  The analysis uses an inappropriate definition of “suboxic” (see below).  Throughout the manuscript the word “rates” is used when “rate constant” is intended (e.g. on line 204 “Reducing remineralization rate by 50% (Cd0.5 minus reference) leads to large decrease…”) making it difficult to interpret the result since it is unclear whether the “rate” is proportionally reduced by 50% with fixed concentration or whether there are compensating responses/increases in concentration that result in a change in the remineralization locations.  While the result of the combined need to reduce the remineralization rate constant and increase the vertical diffusivity to better match oxygen distributions is encouraging, the manuscript oddly stops there without coming to any implications of the work for our understanding of the oxygen and nitrogen cycles or the past or future of the OMZ.  What was learned that wasn’t known before?  Most importantly, the final sentence of the conclusions, “Future studies utilizing advanced models are needed to better understand the impacts of physical and biological interactions on the variability and drivers of the tropical OMZs.” Suggests the authors themselves are unclear as to the significance of the present work to current ocean biogeochemical modeling.  As such, I recommend the authors work to clarify there descriptions and the implications and limitations of the current work in revision.

Technical comments:

26 –“which made significant progresses” needs rephrasing.

40 – The authors are misinformed as to the definition of “suboxic”, quoting a value of 20 mmol m-3… suboxia is defined as an oxygen level at or below the detection limit, typically 2-10 mmol m-3 where interesting nitrogen  redox chemistry such as N2O production, denitrification and annamox occur.  The current definition of <20 is rather “strongly hypoxic” as it is well within the detectible range and well above the region of interesting redox chemistry.  I would note that the reference the authors cite, Paulmier and Ruiz-Pinu (2009), use a suboxic level of 4.5 umol/kg. Also, if the authors want to describe the truly “suboxic” volume, they should be aware that while Table 3 notes a volume of “suboxic” waters from WOA13, it has been demonstrated that these mapped products strongly underestimate the volume of suboxia at the <5 mmol/m3 definition (Bianchi et al., 2012; https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2011GB004209)

45-47 – There is an underlying assertion here that data alone provides understanding, and that more availability of data will resolve the underlying mechanisms.  This is a false premise.  Only by contextualizing the observations in a theoretical framework can mechanistic understanding be achieved.  Also, “our understanding is uncompleted in terms” should be rephrased.

54 – “often” seems unnecessary here given that if the OMZ stretches across the equator it would seem to always lead to an overestimate of the OMZ area… unless there is a concomitant decline in area elsewhere in some models.  If the latter is indeed the case, it would be worth mentioning.  If the intent is just to point out the overestimate, then remove “often”.

57 – “Apparently, it’s necessary to…” this is an odd way of saying this, making it sound like the authors are annoyed at the idea.

73 – This is a really old, coarse resolution model.  A lot of advance has occurred over the last 25 years.

74-75 – What is the vertical grid?  The stated 10-50m +20*10m layers = 210-250 m… this is not deep enough to represent the OMZ…? 

75 – What is the longitudinal grid?  150W-80E? Are the walls open to admit the Indonesian throughflow?  This would seem critical for representation of O2 ventilation flow into the domain (e.g. Rodgers et al, 1999; https://agupubs.onlinelibrary.wiley.com/doi/abs/10.1029/1998JC900094).  Is the Indonesian throughflow prescribed?  Both factors should also be explicit.

96 – the parameters here described as “rates” are actually “rate constants”, e.g. r is the rate constant for zooplankton respiration.

116 – What does “DON poor” mean?

128 – This implies that the model domain extends to 1000m or more, suggesting line 74-75 is incorrect.

140 – It is important to note that “underestimation of supply” is complex and can be from either O2 being too low in the waters that supply or the physical supply mechanisms being either too sluggish or out of balance (e.g. lateral versus vertical and advective versus diffusive”

145-149 – How did these perturbations influence the fidelity of T and S?

152 – What is the reference value of Cd?  What does it do?  There is no parameter called “Cd” is the appendix, only “CDON0” the remineralization rate constant at 10 C, but it’s reference value, 0.001, is very different from 0.5.  Looking at Table 1, I see that “Cd05” is actually “CDON0*0.5”.  However, it is not clear what the 100-600 m range of “0.0005-0.00025” means… is this the role of temperature on CDON0? This parameter needs a sentence or two of introduction, definition, and contextualization here to avoid confusion.

204 - the word “rates” is used when “rate constant” is intended (e.g. on line 204 “Reducing remineralization rate by 50% (Cd0.5 minus reference) leads to large decrease…”) making it difficult to interpret the result since it is unclear whether the “rate” is proportionally reduced by 50% with fixed concentration or whether there are compensating responses/increases in concentration that result in a change in the remineralization locations.

211 – “there is somehow a small decrease…” The use of “somehow” is an insufficient explanation… what is causing this decrease?  Is it a response to the remineralization constant decrease?

224 – Only here is it explained that there was no response in temperature to the diffusivity change.  This should have been noted earlier in the results as requested above, as well as the salinity response.

228 – “Limited field studies” – why is the defining feature of these studies that they were “limited”?  Is the evidence derived from them inconclusive?  More explanation of context would be helpful.

Review to: Sensitivity of asymmetric Oxygen Minimum Zones to remineralization rate and mixing intensity in the tropical Pacific using a basin-scale model (OGCM-DMEC V1.2) by Wang et. al

This paper examines the sensitivity of the oxygen minimum zones (OMZs) to a change in the remineralization rate and changes in the vertical diffusion coefficient in the tropical Pacific. The goal of this study is to present a calibrated model, to evaluate this model and to identify the mechanisms that explain the asymmetric shape of the OMZ in the tropical Pacific. 

Unfortunately this paper only shows the impact of two parameter changes, change in the remineralization rate and the vertical background diffusivity, mainly on the oxygen fields and DON distribution without providing an explanation about the driving mechanisms and a thorough discussion of the results. With this there is so far no scientifically new finding in the current state of the manuscript. In particular an explanation about the mechanisms that drive the asymmetric shape of the OMZs in the tropical Pacific, that is already present in the reference simulation, is missing due to the mainly descriptive nature of the paper. In addition the language that is used is in many places imprecise. E.g. there is no differentiation between vertical and horizontal transport processes as both are termed physical transport.

I think there is potential, that this model and the performed sensitivity simulations, could be used to explain the mechanisms that drive the asymmetry in the oxygen fields, although the current version leaves the reader with too many open questions. 

The model description is not sufficient. There is e.g. no information given about the biogeochemical boundary conditions. What does it mean: All biological components are computed in a manner similar to physical variables. What is the reason to average the model output for the period of 1981-2000 and do not include the last 18 years. Specially, as later in the manuscript some months of year 2009 are compared to some cruise data that are not introduced in the manuscript, they just appear. Are the model data detrended before averaging? Is there a remaining model drift? Why not simply using climatological simulations? What kind of inter-annual forcing is used? 

Although it is mentioned at several places (abstract and introduction) that the model is calibrated - there is no further information given how. Is it calibrated only against the oxygen fields? As the reference simulation already represents the asymmetric shape of OMZ, I assume that this is at least partly a result of the model calibration. The only information that is in the paper: Some parameters have been changed compared to an earlier version of the model. This is however not sufficient.

The model evaluation and validation is lacking. The oxygen fields look fine, but there is no information about, e.g. the circulation. How good is the current system represented in this model? What about nitrogen and phosphate - is there a bias in the east west gradient (one of the problems as shown e.g. by Dietze and Loeptien, 2013, doi:10.1002/gbc.20029) or is that reduced etc. 

Regarding the structure of the paper - I would suggest to reorganize the paper: There should be a clear separation between the model set up as well as the set up of the sensitivity simulations and the results. In addition, regarding the comparison with the cruise data - these simply appear, where do they come from? Same happens with the DON data from HOT. 

The sensitivity simulations show an improved representation of the OMZ in Fig4. The description of this improvement in the text is somewhat incorrect. The asymmetric shape is present in all simulations. It seems that the changes in the parameters result in an overall increase of DO and not necessarily an increase of the asymmetry. As at the southern hemisphere the DO concentrations are lower, one might get the impression that this increase might be slightly larger, but there is no evidence that this is the case at this stage. In addition, in the text it is stated that between 2°S-2°N the values of DO are relatively high (~30-40 mmol m-3) in Cd0.5Kb0.5. Fig 4f does not support this. Around 400m depth the DO concentrations are below 20 mmol m-3. 

Fig 10 clearly shows differences - but there is no explanation given about the choice of the region shown as well as what have been done with the data - I guess they have been averaged. As the vertical oxygen gradients are different in these two regions, I would have expected a difference in the oxygen response, as the vertical diffusive transport depends on the gradient. Unfortunately the explanation of the results are again left to the reader. 

In addition there is no clear explanation given about the choice of the parameter change for the sensitivity simulations and with this it seems rather arbitrary. Also why is an increase of the vertical background diffusivity of 0.5 cm2/s optimal, what about higher rates?

A thorough discussion of the results is missing. How are the results related to other modeling studies? The sensitivity studies show that the major changes occur along the equator - so this indicates that somehow the representation of the current system is important and needs to be shown and discussed. There are several physical processes in addition to the known impact of vertical mixing that seem to be capable to reduce the oxygen model bias along the equator, e.g. enhancing zonal diffusion or enhancing viscosity. Also, as the model is forced with an inter-annually varying forcing, what about the potential impact of El Nino events?

As the manuscript needs substantial revisions, I do not add any specific and/or technical comments at this stage of the review process.