Peer review of: Mantle data imply a decline of oxidizable volcanic gases could have triggered the Great (2020)

Reviewers' comments:
Reviewer #1 (Remarks to the Author):
In this study the authors aimed to improve the knowledge of an important and long-standing
enigma regarding the link between mantle oxidation state and atmospheric composition, more
specifically why the GOE appears slightly shifted with respect to the first recorded oxygen whiffs.
The authors performed calculations that allow to estimated the balance between reduced gas
species vs oxygenated species and related this to volcanism intended as redox carrier from the
Earth's mantle to the atmosphere. By analogy, the mantle-atmosphere system can be extended to
other planets and provide insights on the origin of life.
the paper is certainly well written, but any calculation performed relies on correct and sometimes
wrong intepretation of data from literature whose uncertainties are not taken into account at all.
Figure 1, the motivation for this study, shows an increase of fo2 relative to few mantle and
orogenic eclogites that are assumed to reflect the fo2 of Archaean MORBs without taken into
consideration possible degassing processes. Wrongly, the authors here put the mantle fo2 being
equal to the magma fo2 and the emitted gas fo2. But this is not the case as discussed by few
authors recently (Stagno et al.2019 CUP; Sorbadere et al GCA; Mooussallam et al EPSL, etc).
There is not evidence that an fo2 equilibrium exists between these three phases. In addition, data
from Nicklas are wrongly interpreted being the difference from Aulbach and Stagno (2016) be due
to the fact that the fo2 is not determined at mantle source P-T conditions. For some reason the
authors apply an arbitrary correction of Nicklas data to make the conciding with the present-day
MORB fo2. But, again, Aulbacj and Stagno results can merely be extended to the whole mantle.
Those are few sparse data. When extrapolating to the entire globe, things become highly
speculative. Again, it is not clear how uncertainties derived from fo2, gas chemistry, mantle P-T
regime, atmospheric T, CO2/SO2 gas ratio ultimately affect this model.
However, i admit that the paper is precious in defining processes of oxidation and reduction
 through gas/mineral reactions even better than done so far. But, quantities are not well
 constrained. So, I am sorry to not give the expected credit to this work. It is a great excercise,
 but, as said, highly speculative.
 Best regards
 Reviewer #2 (Remarks to the Author):
This is an interesting contribution on the causes of oxygenation of Earth’s atmosphere. The paper
is very clearly written, listing and explaining every step of the calculations performed as well as
the assumptions behind the equations. The authors show how every parameter affects oxygen
production, under the fundamental assumption that what is the ultimate driver or responsible of
atmosphere redox change is the secular oxidation of the mantle. I think this is very good
illustrative and informative paper that merits being published in Nature Communications.
My main comment is the lack of consideration given to recent findings showing how volcanic gas
temperature changes with time (owing to secular Earth cooling) may have affected atmosphere
oxygenation. We have shown that there is a decoupling between magma redox state and that of
its gases when released in open atmosphere and prior to mixing with it (Oppenheimer et al., 2018,
Nature Geosciences). This observation, first made on Kilauea, has been generalised by Moussallam
et al (2019, EPSL) and proposed as one (one more..) contributing factor to the GOE. In short,
colder gases are more oxidised than those hotter, regardless of the source's redox state. I think
that for completeness this mechanism should be quoted as well in this review type paper.
Apart from that missing information, the paper is technically ok and could be published in its
 present form.
 
Other comments are listed below keyed to line numbers of the main text.
155. For detailed information ?
210. I beg to disagree with this statement. See Moussallam et al 2019, EPSL
257. Perhaps say : The oxic transition time is older (larger)...
Bruno Scaillet
Reviewer #3 (Remarks to the Author):
 126-129. It is true that degassing affects magma redox state, but if the Hawaiian case holds true
 for Archean times, then we should see the reverse, ie the Aulbachs and Stagno trend should be
 more oxidised than the one of Nicklas et al. In general, the evidence point to a reducing effect on
 melt arising from volatile release during magma decompression.
  208. I dont think this statement is entirely correct. Serpentinisation is driven, by definition, by the
 alteration of olivine. Nowadays, ocean floor is covered mostly by basalt with little olivine (relative
 to mantle). H2 rich fluids are produced when mantle is the altered rock, not basalt, outcropping on
 seafloor. During the Archean, perhaps there was more extensive melting but the question is
 whether the produced crust was mafic or ultramafic. If it was basalt, even a more mafic than
 nowadays, then its alteration by seawater circulation is unlikely to have produced significant H2.
  221. This temperature is equivalent to assume that only basalts at ridges produce volcanic gases,
 an unlikely scenario. What about volcanic gases emitted at subduction zones, which are colder by
 200-300°C ? Or do you assume that subduction was not operating on a large scale prior to GOE ?
 Please clarify.
 226. I dont know this paper but the available evidence tells rather the opposite (See Moussallam
 et al., 2019)
  360-361. This is what the vast majority believes which I also beg to disagree with. The fact that
 the redox state of magma source(s) is equal to that of the magma itself is an implicit yet
 debatable assumption (see Burgisser and Scaillet, 2007, Nature).
   The model presented here aims at evaluating quantitatively as to whether or not the oxidation of
 the mantle during the Hadean and the Archean may have caused the GOE. This is an important
 step forward that is appropriate for publication in Nature Communications. I have several point of
 criticisms that need to be addressed before the paper can be accepted for publication.
 The model relies on two main variables. The temporal change in the mantle fO2 and the organic
 burial fraction (forg) estimated from the mass balance of the carbon isotope record. Figure 2b
 shows that the inferred threshold of Koxy = 1 above which the atmosphere becomes permanently
 oxidized intercept the 95% confidence interval at about 2.5 Ga. However, this is critically
 dependent of the shape of the undulating curve, with an inflexion point located at Koxy ~ 0.85 and
 ~ 2.65 Ga. Because this undulation is dependent on the temporal changes in forg , this inflexion
 point should be linked to a change in forg . As shown by Krissansen-Totton et al. (2015), however,
 there is no statistically significant difference between the pre-GOE and post-GOE forg. Rather,
 there is a statistically significant increase in ε (d13Ccarb-d13Corg), which is linked to the decrease
 in d13Corg in the late Archean, possibly due to methanotrophic-recycling. This is in contrast with
 the transition from the Proterozoic to the Phanerozoic, which is characterized by a well-constrained
 
increase in forg. How do these results fits with the curve shown in Figure 2b? Were both variables
(forg and ε) implemented and tested in the calculation of Koxy ? How sensitive are these 2
variables on the location of the inflexion point at ~2.65 Ga ? In the discussion section (lines 300-
312), it is stressed that the uncertainty envelope allows an oxic regime before 2.4 Ga, which was
not advocated in previous studies. Can be appropriate to refer to the study of Philippot et al.
(2018, Nature Communications) who recently showed that the GOE initiated at least at ~ 2.45 Ga
and most likely earlier.
The notion that the GOE may be the result of convection-induced homogenization of a redox-
stratified mantle inherited from the disproportionation of Fe2+ into a Fe3+ rich phase stored in the
lower mantle and metallic Fe0 drained into the core has been proposed by Andrault et al., (2017,
Geochim. Persp. Let.; missing reference to be added here). Their synchrotron-based experiments
indicate a primordial Fe3+ excess of ~20 % for the mantle iron, which would correspond to 500–
1000 times the O2 content in the present day Earth’s atmosphere. How this estimate fits with the
model presented here? Considering the quantitative approach proposed, it would be of major
interest to develop on the total flux of free oxygen release to the atmosphere during the Archean-
Proterozoic transition.