A light carbon isotope composition for the Sun

Measurements by the Genesis mission have shown that solar wind oxygen is depleted in the rare isotopes, 17O and 18O, by approximately 80 and 100‰, respectively, relative to Earth’s oceans, with inferred photospheric values of about −60‰ for both isotopes. Direct astronomical measurements of CO absorption lines in the solar photosphere have previously yielded a wide range of O isotope ratios. Here, we reanalyze the line strengths for high-temperature rovibrational transitions in photospheric CO from ATMOS FTS data, and obtain an 18O depletion of δ18O = −50 ± 11‰ (1σ). From the same analysis we find a carbon isotope ratio of δ13C = −48 ± 7‰ (1σ) for the photosphere. This implies that the primary reservoirs of carbon on the terrestrial planets are enriched in 13C relative to the bulk material from which the solar system formed, possibly as a result of CO self-shielding or inheritance from the parent cloud.

In my opinion, these shortcomings can be readily addressed by some rewriting or some modest additions in the text or the supplementary material.
The paper is very well written, but I did manage to find a few typos and places where some clarification of the prose should be considered. line 16: consider putting a negative sign in front of 60 line 38: change meteorite to meteorites line 138: change would to could line 230,232 and figure legend(s): "v" is used but I think it should be ν ("nu") lines 238, 240: same comment figure 3: several terms on the figure are not explained (CAIs, CC, OC, terrestrial fractionation line). Note that hibonite is misspelled. figure 4: there are several puzzling aspects of this figure and some improvements can be made. First, how is it known what heliocentric distance is appropriate for: EC, OC, CC, IDPs (inside of Jupiter?), 81P?. Second, how is the carbon isotope composition of Earth's core known? Third, it would be good to indicate the terrestrial mantle. line 263: typo: change "form" to "from" line 433: are there words missing after "mean molecular" ? line 533: "Modeling C loss from grains...... chemical reactions." This is not a complete sentence. line 641: "formation of" is repeated finally, consider changing the title to "A light carbon isotope composition of the Sun" rather than "...for the Sun".
Reviewer #2 (Remarks to the Author): I read with interest the new work by Lyons et al aimed at determining the carbon isotope composition of the solar photosphere. The stable isotope composition of the Sun is an important piece of cosmochemical information because the Sun represents the best available analogue of the composition of the protosolar nebula from which the planets formed. The stable isotopes of the light elements, H, C, N, O, present significant, sometimes extreme, variations among solar system objects and reservoirs. Understanding the causes of these variations may permit insight into cosmochemical components and processes that contributed and shaped the protosolar nebula.
Because the solar matter cannot be sampled directly, our knowledge of the elemental and isotopic composition of the Sun relies mainly on two different approaches. On the one hand, the spectroscopic analysis of the photosphere permitted to determine the elemental composition of many solar elements, but barely of the isotope compositions. On the other hand, the analysis of the solar wind (SW) gives insight into the isotopic composition of the major solar elements. The latter was the main scientific target of the Genesis mission, which collected SW ions during 27 months. The analysis of collected material permitted the determination of SW oxygen, nitrogen, and noble gas isotope compositions.
Carbon, the major forming element of organics, does not show large isotope variations in the solar system as do H and N, for reasons that remain to be determined. Nevertheless, given the astrophysical importance of this element and the fact that its two isotopes, 12C and 13C, show significant variations in the solar system, the determination of the solar C isotope composition is most welcome. So far, the only measurement of SW carbon isotope composition is that of Hashizume et al (2004) who proposed based on the analysis of lunar soil grains by ion probe that SW C has a d13C of ~ -100 permil. In passing this measurement should be clearly cited in the introduction of the present paper given its uniqueness. Thus this estimate supports enrichments of solar system objects and reservoirs in the heavy isotope 13C, in parallel to those of N, H and O which also require contribution/fractionation enriching most reservoirs in the heavy and rare isotopes 2H, 15N, 17O and 18O. However, the Hashizume et al's result was for SW and not for the Sun itself, thus requiring to correct for SW fractionation, a process that is almost not known.
Lyons et al propose here another approach, based on the analysis of the photospheric emission (data obtained in previous experiments and available in the literature) using new deconvolution techniques that permit to identify O and C isotopes. Being not familiar with solar spectroscopy and its latest developments, I cannot comment on the techniques used here, except that one of the authors has published well received papers on the field.
The authors report their determination of the photospheric 18O/16O ratio which value of -50±11 permil is consistent with what we know from Genesis. This is a good step to give confidence in their approach. They then get a d13C value of -48±7 permil for the photosphere. They suggest that this value is representative of the Sun and of the protosolar nebula, arguing that other fractionation processes such as gravitational settling are not significant. They use the so called Coulomb drag model (which is challenged, but there is not much model available either) to estimate a SW range of -75 to -95 permil, consistent with the range of -90 to -120 permil determined by Hashizume et al for SW implanted in lunar soils. Finally the authors attempt to discuss the cosmochemical implications of their determination.
Overall this ia an interesting piece of work and I recommend publication in Nature Comm, provided that experts in the field validate the photospheric deconvolution, and pending on significant improvement of the ms.
The ms. is not well prepared and suffers from several problems. Nature Comm allows full papers but this ms. seems to be a sequel submitted to a letters journal having drastic constraints on the length. Part of the interesting information on the used techniques is relegated in a Supplementary, as usual for letter journals, but not necessary here. Large pieces of information are somewhat hidden or not clearly expressed. For instance, in the Discussion section processes other than self shielding and presently shown into the Supplemenary should be discussed in the main text. The discussion of these possible processes is oriented towards a public already aware of the positions and controversies in the field. Concerning the possibility of isotope fractionation in ice, could the authors precise what kind of fractionation process they expect, and what would be the direction of fractionation ? If this fractionation also affected O as proposed, it should be mass-dependent according to the authors and therefore could not account for the 3-isotope O data. It seems that Lyons et al now prefer an origin of fractionation in the parent cloud. They should explain why the effect would be so large for N compared to C. I have also a difficulty with the Rayleigh distillation model applied to grain erosion. Grains are solid particles. When there is erosion, I doubt that the entire carbon of the grains would be in equilibrium with the fraction of lost C. I may have missed the nature of the process the authors propose, and I strongy suggest that they reformulate their discussion, by first clearly stating the stqarting processes and hypotheses for each case.
-In Figure 3, there are two data points with low error bars, labelled O7+ and O6+, that are not presented in the text (or that I missed as the text is unclear). I suppose that they correspond to different degrees of ionisation, but non of these are discussed. The way the O isotope composition is obtained is also mysterious for a public that has not followed closely the controversies on these topics in the last few years.
-In Figure 4, there are 3 data points pertaining to this study, one without label and the two others labelled with ionisation degrees. How is computed the non labeled ? what is its ionization degree ? -Errors (eg abstract) should be precised eg 1 or 2 sigmas, 95 CI etc.
Reviewer #3 (Remarks to the Author): This paper describes improved retrievals of the isotope ratios of oxygen and carbon in the Solar atmosphere as traced by archival high-resolution spectroscopy from the ATMOS experiment. While the data have previously been analyzed, this work presents a new retrieval using improved oscillator strengths for the rovibrational transitions of CO. The improved oscillator strengths remove, arguably, the dominant source of systematic uncertainty in the retrieved isotope abundance ratios of carbon and oxygen, and allows the authors to determine their values to greater accuracy than what was previously possible. It is important to note that it has been known for a long time that the CO oscillator strengths were uncertain, as different, independent (theoretical and measured) disagreed significantly, so this work addresses a long-standing problem by a timely application of these new oscillator strenghts.
The methods applied to derive isotope ratios are apparently adopted from existing literature, e.g., by Ayres et al. 2013. This is a strength of the study, as it is shown that the single change of updating oscillator strengths reconciles the Solar spectroscopy with independent estimates of the Solar isotope ratios. However, a criticism of the manuscript, is that the text remains unclear as to which degree the Ayres et al. method is adopted in detail, or whether there are any departures (see comments below).
The authors find that the Solar composition is isotopically light, and consistent with the solar isotope ratios inferred from Genesis measurements of the Solar wind. This follows expectations, but lends great confidence to any derived interpretaionts of the data.
The study also finds a depleted 12C/13C ratio in the Sun, which is a new result, potentially consistent with nebular selective photodissociation.
Consequently, I think this is an important development in our understanding of the formation of the Earth and other Solar System bodies. The decades-long uncertainty in the Solar carbon and oxygen ratios has put a limit on the confidence with which we have been able to constrain the fractionation processes taking place in the Solar nebula. This work makes great progress toward solving the question of the Solar composition and its relation to nebular fractionation. My main concern relates to how confident we can be that the reported error bars are correct, as the manuscript in its present form does not provide sufficient detail. I believe the authors likely did the necessary work on quantifying their errors, and so should be able to provide an error budget and respond to my questions below without too much trouble.
Detailed comments: -The study hinges on the claim that the errors on the inferred isotope ratios have been significantly decreased. However, I think that the derived errors are not sufficiently justified in the Supporting Material, mainly due to a relative lack of quantitative information about how they were derived. Specifically, the modeling procedure is very complex and will compound errors hierarchically. That is, there are data errors which lead to errors on the derived equivalent widths. The EWs are then used to compare to model with its own systematic errors, etc. While there is no doubt that the improved oscillator strengths will help, the manuscript does not make it clear how errors (statistical and systematic) are propagated. An approach such as described would likely lend itself well to a Bayesian approach, but that does not seem to be the case here.
What prior distributions were assumed for the error sources, and how were they propagated to arrive at the final posterior errors? Is it possible to report the full error budget that must have gone into calculating the reported errors? Can we reasonably assume that the posterior distributions are normally distributed (as suggested by the singular errors) and that there are no hidden degeneracies?
-The result appears to rely heavily on the spectroscopic methods described in great detail in Ayres et al. 2013. However, it is not clear from the text to which degree this work was exactly replicated, or whether there were any departures. Could the authors comment on that, so that the reader knows whether or not Ayres et al. 2013 is an appropriate reference for the methods in this workand specifically which parts of the analysis are relevant (the text indicates it is the "analysis of ATMOS solar spectra", but is it also the fit of the atmospheric models?) -It seems that the systematic error from the atmospheric model fit is based on the spread of inferred isotope ratios implied by different model assumptions. How do we know that the model grid reasonably samples the possible parameter space? Is the reader supposed to refer the discussion in Ayres et al. 2013 to justify the choice of model parameters?
-The C/O ratio is assumed to be exactly 0.5, but the referenced value (from Allende Prieto et al. 2002) has an uncertainty of 14%. How does this affect the error on the isotope ratios?
1 Replies to referees: A light C isotope composition for the Sun, by Lyons et al.
Before getting into the detailed replies, I would like to thank the 3 referees for their helpful reviews. I originally submitted this to Nature, and so the format was not appropriate for Nature Communications. The paper has been expanded, as per the Nature Communications format, and the points raised by the referees have been addressed. Figures have been added (there are now 9) to the main text, and the number of references has been increased. The Methods section contains most of the mathematical details.
Replies to the 3 referees are below, given in the order of the points raised.

Reviewer #1
"Several points could be made clearer" 1. What is the "middle photosphere"? The profile of enhanced temperature is from ~ 10 to 10 4 dyne cm -2 , and is illustrated in Figure 3 of Ayres et al. 2013. The top of the photosphere occurs at ~ 0.87 mbar (= 870 dyne cm 2 ). So the range over which the temperature perturbation has been applied is from the 'middle photosphere' to the lower chromospheres. The text has been modified to indicate this (see p. 4 of revised text). Justification of this temperature perturbation comes from the requirement that 12 C 16 O abundances are the same for Δv = 1 and Δv = 2 transitions. The improvement in spectroscopic line strengths (i.e. f-values) makes this constraint possible. The magnitude of the isotope effect that accompanies this constraint is illustrated in Table 1, column 'Error 5'. Assuming that the revised f-values are correct, we get instead the errors indicated in '1-σ final' column of Table 1.

"
The computed O abundance is slightly low" compared to helioseismology. The error, if there is an error, in the elemental O abundance will have minimal impact on the derived isotope ratios. We have not quantitatively assessed this effect here. Is this reasonable? Yes, because all isotopologue abundances scale similarly, the change in isotopologue ratios is very small.
3. The difference in the f-values between Hure and Roueff 1996 (HR96) and Goorvitch 1994 (G94) is due to the different dipole moment functions assumed in these two papers. This is described in the 1 st paragraph of p 4 of the revised manuscript.
"Efficacy of Figures 1 and 2" Explanatory text has been added to the captions of both figures. Figure 1 is the raw observation data from ATMOS, but with some co-adding of lines. Figure 2 is the new oscillator strengths computed from Li et al., and is the basis for the new results reported in Figures 4 and 5. 'Typos and clarification' -note that nearly all line numbers have changed, but I will use the old line numbers given by the referee for the point raised.    Figure 5) -The heliocentric distances for ECs, OCs, CCs, IDPs, and 81P are meant to be illustrative only, and not precise determinations. A sentence to this effect has been added to the caption. The C isotope composition of Earth's core is an estimate from models by Horita and Pulyakov (2015) (ref. 67). This reference was inadvertently left out of the original submission, but has been added here in the caption to (the new) Figure 5. A reference to the estimated fraction of C in the core (up to 90% of total Earth C) has also been added. Terrestrial mantle values have been explicitly labeled in Figure 5. I thank the reviewer for these substantial improvements to Figure 5.
line 263 -typo -change form to from -done line 433 -change mean molecular to mean molecular mass. line 533 -"modeling C loss from grains…' -this sentence has been removed.
Title: We've decided to keep 'for' in the title, but we do appreciate the suggestion.

Reviewer #2
The manuscript has been rewritten to the larger format allowed by Nature Communications. Much of the discussion that was previously in the Supplementary section is now in the main text. A Methods sections now contains most of the mathematical details.
"Concerning the possibility of isotope fractionation in ice…" -A short, qualitative section on isotope fractionation due to CO ice formation has been added to the manuscript. The affect of CO ice formation on O isotopes is also discussed in a new figure (Figure 9). A more quantitative treatment of the expected mass-dependent isotope fractionation will be presented elsewhere.
"It seems that Lyons et al. now prefer an origin of fractionation in the parent cloud" -I have always considered the parent cloud to be a possible site for CO self-shielding (e.g., see Ref. 40,authors Lee,Bergin and Lyons). The timescale analysis presented here for C loss in the surface of the nebula suggests that the parent cloud may be a better location for the origin of a large C isotope fractionation. From a chemical standpoint, self-shielding in the nebula and parent cloud are very similar. However, the different number densities and pathlengths in the two environments mean that the preservation of photo-generated isotope affects can differ.
"why the effect would be so large for N compared to C" -This is a very important issue, but not one that we wish to address in this paper. To do so would require a detailed discussion of N 2 photolysis, which is difficult to do in a precise yet succinct manner.
"Rayleigh distillation" -We agree with the reviewer that the application of Rayleigh distillation to C grain erosion is not warranted. This text has been removed. Coulomb drag isotope fractionation is dependent on the charge state of the heavy ion (i.e., O + or C + ). A citation to key paper on this topic has been added to the caption. A more detailed discussion of coronal ions is given Coulomb drag section of Methods. Figure 5) -The unlabeled red point is CO in the solar photosphere, and is unionized. The red points labeled C 5+ and C 6+ are the charge states for C in the corona and solar wind. The figure caption has been modified to make these points more clear.

Figure 4 (now
"Errors" -Errors are 1-σ, which is now explicitly stated in the abstract. A sentence has been added to the text (2 nd paragraph) indicating that all errors are 1-σ unless stated otherwise.

Reviewer #3
"It has been know for a long time that the CO oscillator strengths were uncertain…" -Yes, I discovered this after giving a talk on this topic. E. Roueff was in the audience, and came up afterward to thank me for the work. The real credit goes to Li et al. (2015) for determining the new DMF.
The solar atmosphere and radiative transfer models closely follow Ayres et al. 2013. The principal departure in the modeling presented here is the new oscillator strengths. A statement to this effect has been added to the Methods, but this should be readily apparent from the citations to Ayres et al. (ref. 12). The interpretation of the new C isotope ratio for the solar system is new and has been brought into the main text.
"The study hinges on the claim…". The error analysis follows Ayres et al. 2013, but with a decrease in the error associated with the f-values. Table 1 has been added to list the various factors contributing errors. All errors are added in quadrature. Systematic errors are propagated in this error analysis only for the solar atmosphere temperature profile (see Fig. 3). Large systematic errors due to 12 C 16 O line tail overlap with minor isotopologue ( 13 C 16 O, 12 C 17 O, 12 C 18 O) peaks were eliminated in Ayres et al. 12 . A Bayesian error analysis may be performed in the future, but would impose a significant burden on the authors for the present work.
"What prior distributions…". The reviewer poses this question in terms of prior and posterior errors. We are not performing a Bayesian error analysis. All errors are assumed to be normally distributed.
"The result appears to rely heavily on…" As stated above, Ayres et al. 12 is an appropriate reference for the many of the methods in this work. That includes the solar atmosphere and radiative transfer models, but does not include the new f-values. Nor does it include the analysis of how this 13 C enrichment could arise from CO self-shielding or other processes.
"It seems that the systematic error from the atmosphere model fit…" The reviewer is welcome to refer to Ayres et al 12 for a discussion of the parameter space sampled by the atmospheric model. "The C/O ratio is assumed to be exactly 0.5…" Allende-Prieto et al. 2002 give a C/O value of 0.50 ± .07. We have not run models with different C/O ratios, but our expectation is that the isotopic ratios will be only weakly dependent on the elemental ratios.