Isolation and characterization of a covalent CeIV-Aryl complex with an anomalous 13C chemical shift

The synthesis of bona fide organometallic CeIV complexes is a formidable challenge given the typically oxidizing properties of the CeIV cation and reducing tendencies of carbanions. Herein, we report a pair of compounds comprising a CeIV − Caryl bond [Li(THF)4][CeIV(κ2-ortho-oxa)(MBP)2] (3-THF) and [Li(DME)3][CeIV(κ2-ortho-oxa)(MBP)2] (3-DME), ortho-oxa = dihydro-dimethyl-2-[4-(trifluoromethyl)phenyl]-oxazolide, MBP2– = 2,2′-methylenebis(6-tert-butyl-4-methylphenolate), which exhibit CeIV − Caryl bond lengths of 2.571(7) – 2.5806(19) Å and strongly-deshielded, CeIV − Cipso 13C{1H} NMR resonances at 255.6 ppm. Computational analyses reveal the Ce contribution to the CeIV − Caryl bond of 3-THF is ~12%, indicating appreciable metal-ligand covalency. Computations also reproduce the characteristic 13C{1H} resonance, and show a strong influence from spin-orbit coupling (SOC) effects on the chemical shift. The results demonstrate that SOC-driven deshielding is present for CeIV − Cipso 13C{1H} resonances and not just for diamagnetic actinide compounds.

The authors report the first Ce-Caryl bonded complex, [Li(THF)4][Ce IV (κ 2 -ortho-oxa)(MBP)2] and interrogate its bonding interactions through NMR spectroscopy and DFT calculations. The complex's uniquely downfield shifted Caryl 13 C{ 1 H} NMR shift and calculations suggest a significantly covalent Ce-Caryl interaction and that the downfield shift is driven by the significant SOC of Ce IV . The NMR work presented in this study is fantastic.
The synthetic chemistry, NMR spectroscopy, and non-trivial computational analysis are important benchmarks for the field, and certainly will generate significant excitement. However, there are a few key issues that must be addressed to secure these claims.
While I agree that the interrogation of multiconfigurational behavior in high-valent lanthanides is potentially an important aspect of this work, none of the data presented here, including the computational analysis, addresses this aspect and these conclusions are not supported.
I would suggest that if the key comments are addressed, this paper would be appropriate for a highprofile field journal (JACS, ACIE, Chem. Sci.). Since Nature Communications is committed to publishing results of significance to specialists within each broad field, Nature Communications would be an appropriate forum for a revised version of this manuscript. This paper would be substantially more impactful if it reported experimental data that could address multiconfigurational behavior in 3. However, this would require significant further experimentation including synchrotron studies, magnetometry, and/or CASSCF calculations. I would suggest that the synthetic and theoretical efforts described here be published as one complete story and the further necessary spectroscopic, magnetometry, and theoretical studies be published separately. These concerns are described below.
Key comments: 1) The authors state their hypothesis for the stabilization of a Ce-Caryl bond as "Considering strategies to stabilize a Ce 4+ -C aryl bond, we hypothesized that tethering the aryl group to the Ce center would kinetically inhibit homolysis of the Ce-C bond." a. This is quite reasonable but leaves unstated the other significant contribution to the redox stability of this system -the supporting aryloxide ligand framework which significantly stabilizes the tetravalent cerium center. In fact, the authors have demonstrated this stabilization in their prior work. This should also be clearly stated here, and, at a minimum, a few references to the use aryloxide ligand frameworks for the stabilization of reactive high-valent, organometallic early transition metal complexes should be included. I realize this is a bit of rabbit-hole, but the complexes and reactivity reported here have significant similarity to the work of Ian Rothwell and Hiroyuki Kawaguchi. 2) There is clearly unmodeled residual electron density in the structural model of the singlecrystal diffraction data of 3. Given that this complex is the centerpiece of this study, I would have liked more attention paid to this issue beyond the annotated CIF file. The authors claim that this unmodeled electron density is due to incompletely modeled whole molecule disorder in which only the Ce atoms of the two independent molecules in the asymmetric unit for the minor component can be identified.
a. This may be the best model possible, however, the authors should include further details on the refinement in the SI about how this model was determined and what other models were tested. For example, what about lower symmetry with twinning? Or a modulated supercell? I would suggest that the authors also provide the SCXRD derived precession images in the SI in order to rule out the presence of a supercell or undiagnosed twinning. b. Ideally, a non-problematic crystal would be identified. Have the authors tried to resolve the issues with this structure chemically? The supporting Li cation is supported by four THFs. These could be readily substituted by DME, TMEDA, or 12-c-4 in order to modify the crystal in order to get higher quality data. The authors could also consider metathesis with PPN or PPh4 cations or their derivatives to help template the structure.
3) The authors provide no proof-of-purity for any of the new complexes reported in this study.
This omission makes the reported yields somewhat unreliable. In the case of organometallic complexes, elemental analyses (EA, CHN) are standard. I expect that it is probably difficult obtain EAs that match the expected values for several of these complexes. However, the discrepancies could be reasonably explained. The authors must report their EA values for their complexes. 4) There is some confusion introduced in the text with the authors' inconsistent use of mixedvalent and multiconfigurational. Additionally, the relationship of these phenomena to canonical oxidation states is not presented in a clear and consistent manner. The confusion or conflation of terms is common in the literature. This paper would benefit from clarification of how these authors are using the terms. I would suggest that mixed-valent is best used to 1) refer to complexes, co-crystals, or materials in which the same metal-ion exists in two or more canonical oxidation states, or 2) to refer a complex of an f-element or a main group element that has a ground state electronic structure that has mixed-quantum numbers (e.g. 4f n 5d 1 ). None of the complexes in this study (nor any of the tetravalent Ce complexes cited by the authors) fall into either definition. All tetravalent Ce complexes and materials that have been interrogated by L3-edge XANES to-date can be described as multiconfigurational (by the definition in refs 6 and 33 in this manuscript). While there are several new inorganic tetravalent cerium complexes that present challenges for the current understanding of the phenomenon, the dichotomy presented in line 143-144, "common feature for CeIV compounds as well as for mixed-valence CeIV/CeIII species," has not been demonstrated to exist. a. The authors present a Ce configuration retrieved from NBO analysis for 3 (4f 0.76 d 0.60 ) as evidence for the partial f character in 3 and imply, without any comment or support, that this f character (0.76) is an equivalent observable to that extracted from the fit of L3-edge XANES spectra of tetravalent cerium materials and complexes (the authors choose the nf values of CeO2 (0.58) and cerocene (0.80) for comparison). i. If this DFT derived value corresponds to the nf values derived from L3-XANES spectra, then it would be a landmark result. Several groups have tried to construct a theoretical model of multiconfigurational behaviour that is correlated with experimental observables, and have not yet been successful.
1. However, in the absence of experimental data such as transmission L3-edge XANES spectra, HERFD XANES spectra, or even dc susceptibility for 3, this analysis of the NBO results is unsubstantiated and should be removed or softened (specifically the two sentences in lines 170-174).
a. I would expect the NBO derived configuration to be sensitive to method (not unlike the calculated NMR shift). The development of this analysis must be paired with experimental observables. b. The proposed d 0.60 character goes undescribed -this presents significant challenge theoretically and experimentally. What would the comparable CASSCF calculations show? dc susceptibility and RIXS experiments would be informative for future studies. b. To be clear, I am excited that the authors are trying to make this connection.
However, I believe substantial evidence required to establish this model and would need to be addressed in a separate manuscript on the development and analysis of this theoretical model and its correspondence to the reported L3-edge XAS data in the literature.
Minor points: Line 38: "cyclopentadieninde" should be "cyclopentadienide" Line 96: This should be Epc not Epa : "The Epa of 3, -1.67 V versus Fc/Fc+, shifts by -0.72 V relative to the E1/2 of 1 (-0.94 V vs. Fc/Fc+), indicating that the ortho-oxa-moiety significantly stabilizes the CeIV couple in THF." Line 98: Epc should be Epa here since you say oxidation: The reduction of 3 is not reversible under the electrochemical conditions, although the event precedes a reversible oxidation at E1/2 = -0.94 V versus Fc/Fc+ and an irreversible oxidation at Epc = -0.43 V.
Line 109: Again, "Epc" should be "Epa" since it is an anodic scan. "Indeed, the return anodic scan comprises waves at E1/2 = -0.94 V versus Fc/Fc+ and Epc = -0.43 V respectively, consistent with previous assignments for compounds 1 and 2 ( Figure 4)." Line 110: An event at -0.43 V is not actually shown in Figure 4 as mentioned in line 110. Has this Epc value been reported in error? Or is it not shown and the reader should be directed to an SI figure such as S4b where there does seem to be an Epa around -0.5 V? Additionally, if these are from previous assignments as stated, please add references to the end of this sentence.
Line 124: "13C{1H} shift at ~213 ppm for a the CeIV-NHC" remove "a" Line 155: I believe there should be a "two" between "are" and "two-center" "There are two-center two-electron σ bonds describing the donation bonding between the aryl carbon and oxazolinide nitrogen and Ce" Is Fig. 3 an ORTEP or is it really a Mercury plot with a partial thermal ellipsoids? Either way, the crystallographic section of the SI or the main text should have the appropriate reference for the graphic generation. Values in Figure 4 caption and two separate places in the text (line 100 and 109) text do not match.
-0.94 vs -0.95 V. Please clarify the correct value or if these are in reference to different scan rates.

Responses to the Reviewer Comments (NCOMMS-20-25277;)
Note, changes in response to the reviewers are highlighted with blue text.

Reviewer #1 (Remarks to the Author):
Organocerium complexes of Ce(IV) are rare due to Ce(IV) being a powerful oxidant and the reductive C-C bond coupling with accompanying reduction to Ce(III) is more likely. The Schelter group has had a long standing presence in cerium chemistry and, in this report, they detail the synthesis and characterization of a Ce(IV) complex with a Ce-C(aryl) bond. The reaction of a bis(phenol) ligand with Ce(OtBu)4(THF)2 forms the previously reported Ce(IV) starting material more effectively, followed by reaction with an oxazolide to make the 'ate' product. The Ce-C bond has a highly shifted 13C NMR resonance at 255-256 ppm, which is ~50 ppm from the lithium shift, and far removed from the normal aryl region. Electronic structure and NMR calculations are employed to examine the Ce-Aryl complex in more detail.
Minor stuff: In the introduction, 13C NMR resonances have been correlated to electronic structure in a couple other cases: Organometallics 2017, 36, 4519 and Organometallics 2018, 37, 1884. These should be cited due to their relation to this manuscript. In addition, Inorganics 2015, 3, 589 describes the synthesis of Ce(IV) Cp derivatives and should be added to those in references 15-18.
Response: The three requested references have been added.
On page 4, line 82, pentamethylcyclopentadiene should be dienyl since the anion is what is being referenced.
Response: "pentamethylcyclopentadiene" has been changed to "pentamethylcyclopentadienyl" The heading Discussion should be Conclusion, right?
In the experimental, for the 1H and 13C NMR data, the 8 in d8-THF is superscripted, but subscripted in 19F and 7Li NMR data. All should be subscripted.
Response: This issue has been corrected in both the body of the manuscript and the Supporting Information. Response: While the reviewer is correct in noting the exceptional 13 C resonance for methanediide ligands bound to cerium, the statement that the cerium has little to do with the associated shift compared to the ligand, we feel is diminishing of the impact the alphaphosphorus atoms have on the interaction of the carbon atom. Referencing the Hayton/Hrobarik OM 2017 paper, the SOC effects from the interaction between the thorium and carbon atom, the methanediide ligand has a SOC effect of only 3 ppm, but simply removing one phosphorous increases the SOC effect increases by 50 ppm, so there is a big impact of the ortho-phosphorus. Unfortunately, there is no isolated analogous cerium compound to see if the SOC effects are analogous between cerium and thorium, nor have the methanediide-Ce SOC effects been evaluated. We hope to make more connections between thorium and cerium chemical shifts in future publications.
Overall, the rarity of Ce(IV) organometallic compounds makes this manuscript compelling, and brings about more questions for the f element community to debate. I support its publication in Nat. Commun. once comments/suggestions/concerns are addressed.
We thank the reviewer for their supportive assessment of our work.

Reviewer #2 (Remarks to the Author):
This manuscript details the synthesis and characterization of an interesting and novel Ce4+ organometallic compound and provides an in-depth investigation via NMR, X-ray diffraction, and computational models. The authors state that NMR spectroscopy finds evidence of spin-orbit coupling in Ce4+ for the first time, and computational models reproduce the observed chemical shift. The single crystal X-ray diffraction (SCXRD) determined crystal structure is then used as a confirmation of appropriate bond lengths and angles. The authors present their findings well and succinctly, and while I cannot expertly comment on the NMR spectroscopy, I do have some reservations about the SCXRD collection and data work-up.
Some might argue that the SCXRD data is not necessary, due to the in-depth NMR and accompanying computation models, yet I find that additional confirmation (e.g. bond distances) comforting when presenting new, unusual, or game-changing research. In this regard, the SCXRD has some issues that should not be ignored and should at least be commented on in the Supporting Information.
I believe an insufficient absorption correction was applied (or maybe unaccounted twinning).
Response: We have responded to these comments on the x-ray structural data for (previously 3 now) 3-THF individually, below. Additionally, for this revision, a second data set, comprising the DME solvate of the Li+ cation instead of the THF-solvate, complex 3-DME in the revised version, was obtained. The bond parameters in the title complex are nearly identical to the new one, and the new data set does not have these same issues with the single crystal x-ray data collected for 3-THF.
In the original structure of 3-THF that we presented, we did attempt to find a twin component, with no success. Indexing fit 87% of all peaks harvested (150000) and no reasonable twin matrix was found using CrysalisPro that fits the missed peaks.
The authors, within the CheckCIF, state that there is "minor Ce atom disorder", and thus twocomponent ligand (or solvent) disorder cannot be effectively modeled. Heavy metals often have significant residual electron density and can sometimes be handled with face indexing of the crystal. I do not see this as "Ce atom disorder", which would imply that accurate bond distances between Ce and other atoms would be difficult to arrive at. Using a Mo or Ag source could also help with this absorption issue.
Response: The use of face indexing and altering absorption correction values/variables did not resolve the issue of the large Q-peaks. When the Q-peaks are modeled as disordered Ce atoms, we get a 10% and 8% occupancy respectively. And the R factor drops to around 8.7%. We can see some evidence of a whole molecule disorder from Q-peaks that slightly resemble phenyl rings that correspond to the ligand, but the Q-peaks are too small (less than 0.8) and the amount of restraints/constraints needed would not benefit this structure and finding the entire second component of the light atoms is not plausible without using harsh constraints like SAME or EADP. In addition, the disordered component might be an enantiomer and that would make modeling it even more challenging without enough Q-peaks to find the orientation/position of the ligands. This structure was collected on Cu radiation due to the crystal being weakly diffracting with Mo and the long cell axes.
Additionally, there is an ISOR command present in the CIF and the authors have not provided which atom that the command was used on in the manuscript or SI (and the .res file is not imbedded in the CIF either). Briefly looking in the CIF, it seems that Ce1 might present as NPD… Response: Ce1 is not NPD and has no restraints/constraints in our model.
-and could be what the ISOR is used on -which should be refined in a more appropriate (and "less-hard") way. The identity of the ISOR should be provided regardless, along with a brief paragraph describing the data/refinement work-up to explain what was done to the data (as there seems to be a significant number of site occupancy changes for solvent and ligand moieties).
Response: ISOR and SIMU are used on the disordered THFs on the Li adduct, toluene solvent and bisphenol ligand with stretchy ellipsoids due to the presence of a whole molecule disorder.
I view these issues as quite minor when considering the scope of the manuscript (and believe the overall structure as presented), yet specific refinement treatment for the residual density, disorder, and use of ISOR should be investigated, applied, and provided before resubmission. Bond distances and angles may change slightly, though (hopefully) within error.
Response: Comparing the bond lengths with the Ce disorder modeled and without shows no significant change in bond distances, all changes within error.
To reiterate, a second structure, the DME solvate, complex 3-DME, was obtained and the bond parameters are very similar and it does not have these same issues with the SCXRD data of 3-THF.
We appreciate the reviewer's careful analysis of our SCXR data.

Reviewer 3:
The authors report the first Ce-Caryl bonded complex, [Li(THF)4][Ce IV (κ 2 -ortho-oxa)(MBP)2] and interrogate its bonding interactions through NMR spectroscopy and DFT calculations. The complex's uniquely downfield shifted Caryl 13 C{ 1 H} NMR shift and calculations suggest a significantly covalent Ce-Caryl interaction and that the downfield shift is driven by the significant SOC of Ce IV . The NMR work presented in this study is fantastic.
Response: We thank the reviewer for their enthusiastic response.
The synthetic chemistry, NMR spectroscopy, and non-trivial computational analysis are important benchmarks for the field, and certainly will generate significant excitement. However, there are a few key issues that must be addressed to secure these claims.
While I agree that the interrogation of multiconfigurational behavior in high-valent lanthanides is potentially an important aspect of this work, none of the data presented here, including the computational analysis, addresses this aspect and these conclusions are not supported.
I would suggest that if the key comments are addressed, this paper would be appropriate for a high-profile field journal (JACS, ACIE, Chem. Sci.). Since Nature Communications is committed to publishing results of significance to specialists within each broad field, Nature Communications would be an appropriate forum for a revised version of this manuscript. This paper would be substantially more impactful if it reported experimental data that could address multiconfigurational behavior in 3. However, this would require significant further experimentation including synchrotron studies, magnetometry, and/or CASSCF calculations. I would suggest that the synthetic and theoretical efforts described here be published as one complete story and the further necessary spectroscopic, magnetometry, and theoretical studies be published separately. These concerns are described below.
Response: We agree with the reviewer that there are further electronic structure studies to perform on this system. As a practical matter, it is not currently possible for us to collect the synchrotron data for such a study, due to COVID related restrictions of measurements at our preferred synchrotron, SSRL. As indicated by the reviewer, we prefer to report that work in a subsequent publication. We have initiated that work, however, and the results will be presented in due course.
Key comments: 1) The authors state their hypothesis for the stabilization of a Ce-Caryl bond as "Considering strategies to stabilize a Ce 4+ -Caryl bond, we hypothesized that tethering the aryl group to the Ce center would kinetically inhibit homolysis of the Ce-C bond." a. This is quite reasonable but leaves unstated the other significant contribution to the redox stability of this system -the supporting aryloxide ligand framework which significantly stabilizes the tetravalent cerium center. In fact, the authors have demonstrated this stabilization in their prior work. This should also be clearly stated here, and, at a minimum, a few references to the use aryloxide ligand frameworks for the stabilization of reactive high-valent, organometallic early transition metal complexes should be included. I realize this is a bit of rabbit-hole, but the complexes and reactivity reported here have significant similarity to the work of Ian Rothwell and Hiroyuki Kawaguchi.
Response: we agree with the reviewer and have added the statements: "Lastly, we sought a supporting ligand that would stabilize the Ce IV oxidation state to prevent charge transfer and subsequent Ce-C bond homolysis." And "Aryloxide ligands have been previously shown to both stabilize the Ce IV oxidation state and other high valent organometallic species." Which includes several references from the above listed authors.
2) There is clearly unmodeled residual electron density in the structural model of the single crystal diffraction data of 3. Given that this complex is the centerpiece of this study, I would have liked more attention paid to this issue beyond the annotated CIF file. The authors claim that this unmodeled electron density is due to incompletely modeled whole molecule disorder in which only the Ce atoms of the two independent molecules in the asymmetric unit for the minor component can be identified.
a. This may be the best model possible, however, the authors should include further details on the refinement in the SI about how this model was determined and what other models were tested. For example, what about lower symmetry with twinning? Or a modulated supercell? I would suggest that the authors also provide the SCXRD derived precession images in the SI in order to rule out the presence of a supercell or undiagnosed twinning.
Response: Thank you, reviewer, for the careful consideration of the crystal structure data. For the data set for 3-THF, we were not able to determine any reasonable twinning model (using CrysalisPro or Platon). The chosen cell indexed as 86.7% to 150000 reflections and no reliable twin orientation was able to cover the remaining 13% (see our response to the previous reviewer comment above). In addition, the histograms show no evidence of weak satellite peaks that would indicate a modulated cell. In our experience with modulated cells, multiple cell sizes can be indexed and weak in-between peaks can be identified, along with heavy disorder in several molecules in the asymmetric unit cell. No smaller cells can be identified, even by restricting cell lengths. In addition, the precession images look fine with no indication of twinning or modulation.
b. Ideally, a non-problematic crystal would be identified. Have the authors tried to resolve the issues with this structure chemically? The supporting Li cation is supported by four THFs. These could be readily substituted by DME, TMEDA, or 12-c-4 in order to modify the crystal in order to get higher quality data. The authors could also consider metathesis with PPN or PPh4 cations or their derivatives to help template the structure.
Response: Based on the reviewer's suggestion, we have investigated the recrystallization of the title compound from DME. Indeed, we have found that the recrystallization of the compound from DME afforded formation of the Li(DME)3 cation, which produced a much higher-quality crystal overall. We have fully characterized this new congener of the compound, 3-DME, and added it to the manuscript. This new congener has afforded better determination of important bond distances. We thank the reviewer for their suggestion.
3) The authors provide no proof-of-purity for any of the new complexes reported in this study. This omission makes the reported yields somewhat unreliable. In the case of organometallic complexes, elemental analyses (EA, CHN) are standard. I expect that it is probably difficult obtain EAs that match the expected values for several of these complexes. However, the discrepancies could be reasonably explained. The authors must report their EA values for their complexes.
Response: We agree with the reviewer and typically obtain and report these data as a matter of course. Our initial submission was limited in this manner by COVID-19-related suspension of research activities. We have now provided EA data for compounds 2, 3-THF, and 3-DME. We appreciate the reminder from the reviewer on this point. 4) There is some confusion introduced in the text with the authors' inconsistent use of mixedvalent and multiconfigurational. Additionally, the relationship of these phenomena to canonical oxidation states is not presented in a clear and consistent manner. The confusion or conflation of terms is common in the literature. This paper would benefit from clarification of how these authors are using the terms. I would suggest that mixed-valent is best used to 1) refer to complexes, co-crystals, or materials in which the same metal-ion exists in two or more canonical oxidation states, or 2) to refer a complex of an f-element or a main group element that has a ground state electronic structure that has mixed-quantum numbers (e.g. 4f n 5d 1 ). None of the complexes in this study (nor any of the tetravalent Ce complexes cited by the authors) fall into either definition. All tetravalent Ce complexes and materials that have been interrogated by L3edge XANES to-date can be described as multiconfigurational (by the definition in refs 6 and 33 in this manuscript). While there are several new inorganic tetravalent cerium complexes that present challenges for the current understanding of the phenomenon, the dichotomy presented in line 143-144, "common feature for CeIV compounds as well as for mixed-valence CeIV/CeIII species," has not been demonstrated to exist.
Response: We agree with the reviewer confusion exists in the literature wherein terms: "mixedvalent" and "multiconfigurational" are used (erroneously) interchangably. And we agree with the reviewer on the definition of a mixed-valent state, and with the fact that its meaning differs from that of a multiconfigurational state. To clarify the text, we have removed all occurrences of "mixed-valent" where the intention was to describe a system as "multiconfigurational". Along the same lines, we changed the text: "The MOs with the most Ce 4f character remain largely metal-centered and span the seven lowest unoccupied molecular orbitals (LUMO to LUMO+6, Supplementary Figures 11-17) of the complex, a common feature for Ce IV compounds as well as for mixed-valence Ce IV /Ce III species." to "The MOs with the most Ce 4f character remain largely metal-centered and span the seven lowest unoccupied molecular orbitals (LUMO to LUMO+6, Supplementary Figures 13-19) of the complex, a common feature for Ce IV compounds as well as for cerium species with a debated Ce IV /Ce III oxidation state." a. The authors present a Ce configuration retrieved from NBO analysis for 3 (4f 0.76 d 0.60 ) as evidence for the partial f character in 3 and imply, without any comment or support, that this f character (0.76) is an equivalent observable to that extracted from the fit of L3-edge XANES spectra of tetravalent cerium materials and complexes (the authors choose the nf values of CeO2 (0.58) and cerocene (0.80) for comparison).
Response: The Ce natural configuration of 4f 0.76 5d 0.60 is a result of donation bonding involving cerium and the neighboring C, N and O atoms, as evidenced by the NLMO analysis presented in Table 1 of the manuscript. This configuration is indeed similar to that in CeO2 (4f 0.82 5d 1.05 ) calculated by Hay et al.[J. Chem. Phys. 125, 034712, 2006] and to that in cerocene (4f 0.98 5d 1.36 ) calculated by Moosen and Dolg [Chem. Phys. Lett. 594, 47-50, 2014], obtained via Mulliken population analyses of calculated ground state electron densities. Indeed, for both CeO2 and cerocene, the calculated Ce configuration agrees well with the configuration derived from the L3edge XAS (4f 0.58 for CeO2 and 4f 0.89 for cerocene, values quoted as "nf" in the XAS communitythe combined 4f shell occupation), as far as the 4f occupancy is concerned. We did not mean to say that the calculated Ce configuration for complex 3 is strictly equivalent to those derived experimentally for CeO2 and cerocene. To resolve this issue, the original sentence at lines 170, 171, now reads: "The large Ce 4f electron count of 3 (0.76), associated mainly with the sizable Ce-Caryl bonding, is comparable to the calculated and experimentally-determined Ce 4f electron counts in CeO2 and Ce(C8H8)2." i. If this DFT derived value corresponds to the nf values derived from L3-XANES spectra, then it would be a landmark result. Several groups have tried to construct a theoretical model of multiconfigurational behaviour that is correlated with experimental observables, and have not yet been successful.
Response: The nf value derived from peak-fitting an experimental L3 XAS spectrum is believed to give a measure of the 4f-shell population in the GS of the complex. Then, yes, our DFT/NBOderived Ce 4f 0.76 occupation, which is in fact the combined 4f-shell electron occupation, can be taken as a calculated analogue of nf, with the caveat that its accuracy connects to the chemical bonding in the complex as captured by the used approximation, i.e. DFT/B3LYP. However, in absence of the L3 XAS experiment we prefer not to overinterpret the calculations, and we refrain from identifying the DFT-calculated cerium 4f population of 0.76 with nf for the purpose of the