The present study reports on improved glyoxal simulations by updated secondary production pathways and by the introduction of an artificial marine glyoxal source. It is well written and easy to follow and the figures are well-chosen. I have to apologize that I am not a chemist, such that many of my questions might be fully attributed to missing knowledge from my side. My major concern relates to the proposed artificial marine glyoxal source. While other model updates to the glyoxal production chain are explained, quantified and discussed in great detail, the suggested artificial marine glyoxal source remains poorly justified in terms of realistic chemical candidates and potential real-world equivalents. At the same time, it has significant impact and causes an increase in the global glyoxal burden of over 100%. Do the authors assume this proposed marine glyoxal precursor to be uniformly distributed in the global marine surface? Where could it originate from and how realistic is it? The authors mention that previous literature suggested e.g. DOM as potential marine glyoxal source, but the study does not debate how their proposed artificial source relates to these findings. Further, the impact of the proposed marine glyoxal source on related tropospheric tracers could be evaluated better. It is not clear to me how this new glyoxal chemistry impacts e.g. tropospheric CO or SOA formation and whether its impact on surface ozone is an improvement or degradation with respect to observations.

Other comments:

1. Section 3: The evaluation of the simulations with respect to surface and airborne observations remains a bit unclear. I suggest to name and discuss potential biases introduced by missing spatial and timely correlation between the observations and the simulations. It is not clear from the text whether the comparison to ground- and airborne observations considers any time correlation or, instead, is performed using the previously discussed yearly averaged simulations (which would introduce systematic biases that might cause part of the negative model bias). It is also unclear how the altitudinal resolution of the simulations impacts the comparison to airborne observations. I understand that the comparison only considers observations at the surface and within the PBL. However, the vertical bVOC profile has a very pronounced vertical gradient in particular in the lowermost troposphere. Or is the model bias constant throughout the PBL and the same for ground and airborne observations? Since the study concludes on missing (marine) surface sources, I would expect the model bias to be somewhat altitude dependent. The analysis might benefit from 1. clearly discussing the underlying methodology and potential thereoff resulting systematic biases 2. differentiating ground and airborne observations to enable a discussion of the altitudinal dependence of the model bias. For the latter, I suggest to add a figure with a comparison of glyoxal vertical profiles.
2. Section 8: This discussion might benefit from an evaluation with respect to observations. Without, the results are a bit difficult to interpret. Is there any impact on tropospheric CO? Does the updated glyoxal burden only reflect on surface concentrations, or is there any impact in the free and upper troposphere? For all key tropospheric species, do the updated simulations improve or degrade the model bias with respect to observations? For example, what does the observed increase in surface ozone mean in terms of validation vs. observations? The resulting increase in SOA that the abstract reports on is not discussed. How does this relate to other studies and observations?

Minor comments:

Lines 9-10: I imagine the increase in ozone and SOA must be significantly larger than the global mean over some regions. How does this compare to observations?

Line 24: column concentrations -> is this supposed to be slant column density or vertical column density? I suggest to use the common scientific term throughout the manuscript

Line 25: missing space

Line 35: I suggest to include more recent studies, e.g. using TROPOMI observations

Line 151: This is probably explained in detail in the respective references, but since the present study explicitly explores the impact of updated glyoxal production on e.g. surface ozone, I wonder about the assumptions made regarding the a priori glyoxal profiles in the satellite retrievals. This is even more crucial with respect to the discussed marine surface glyoxal production and resulting concentrations, since in particular the marine glyoxal profiles are quite uncertain over many regions.

Line 176: It is not clear how the yearly average is computed. I assume only simulations from the local satellite overpass time are used? This could be mentioned in the text, since otherwise the pronounced diurnal cycle of glyoxal might introduce systematic biases in the comparison. Also, for a species of such low optical density, the satellite must observe a significant fraction of negative retrievals. How are these taken into account in the comparison to a deterministic model?  

Table S1. Without clarification of the measurements altitudes, the given glyoxal concentrations are difficult to interpret. The first column sometimes mentions a geographic region and sometimes what appears to be measurement campaign acronyms. It might help the reader to be concise. Also, please carefully check the literature references. Wendisch et al., (2016) does not at all report on glyoxal.

Figure 2: Please add the respective references for the observations.

Line 202: This is not directly intuitive, considering that the model underestimates glyoxal in these bVOC source regions. How do you interpret an isoprene overestimation while at the same time glyoxal underestimation over regions clearly dominated by biogenic emissions? Is the model bias larger or smaller over bVOC source regions compared to other latitudes?

Line 227: I am aware that isoprene observations are globally sparse and not routinely available, but how does this scaling approach impact the comparison to independent isoprene measurements? How does it compare to results from TROPOMI-based isoprene inversion approaches?

Line 276: two-stages -> two stages

Line 280: ... and undergo rapid... ?

Line 281: fragments

Line 380: As above, considering this elevated isoprene-glyoxal yield in low NOx/high HOx environments, how do you interpret the model overestimation of isoprene coinciding with an underestimation of glyoxal in these regions?

Line 475: though a global bias

Line 526: were -> was

Line 591: the Amazonian rainforest

Zhang et al present work investigating the atmospheric glyoxal budget using a combination of satellite data and GEOS-Chem modeling. This topic is important and addressing issues with modern understanding in this domain is a worthwhile effort. While the authors present a thorough analysis, I believe there are several key pitfalls in this work that warrant further attention before this manuscript should be accepted for publication. They are highlighted below.

Model resolution

4˚x5˚ is very coarse spatial resolution and not at all state of the art. Existing work in GEOS-Chem routinely uses 2˚x2.5˚ or higher and has for the past several decades. Given that many of the spatial gradients in glyoxal concentrations are on the order of 10s of km or smaller, the authors need to justify why this resolution was chosen. The authors should explicitly discuss how and where a 4x5 degree simulation would be useful to modern atmospheric chemistry understanding, and consider of completing new simulations at 2˚x2.5˚.  

Data-model agreement

GEOS-Chem and the satellite retrieval disagree by quite a lot in this work. The authors do highlight this. However given the enormous uncertainties in both the simulation and the satellite data, it is difficult to know what to take away from this work as a reader. Can you tell if the model right? Are the satellite data to be trusted? Is an NMB of 60% even high at all given the coarse resolution and huge observational uncertainty?

More detailed statistical treatment of the role of uncertainty in the satellite retrievals would strengthen this work substantially.

Hypothetical Ocean Source

The GC-TM-EC simulation and related discussion is missing a very important caveat. Namely that according to equation 3, the authors specifically scaled an ocean emissions term such that the model and satellite data agreed. Once this was done, the paper discusses how well the concentrations agree in Section 6. This is a circular argument.

Further, glyoxal retrievals over oceans often have quite large per-retrieval errors, the statistical implications of which are not discussed in nearly enough detail in this manuscript. There is deep literature discussing robust emissions estimation from uncertain satellite observations. Incorporation of that kind of work would strengthen this paper.

There may well be missing emissions of glyoxal from oceans in current models. This work does not provide particularly strong evidence in that direction. Instead, this work demonstrates that adding a hypothetical source of glyoxal over oceans based on extremely noisy satellite data does improve agreement with observations. A variety of prior papers have suggested as much. While that may be true, there are many other potential issues with the simulation of photooxidants that could lead to similar changes in concentrations.