The following document contains the comments received from reviewers and our responses for sc-2017-036524.
Reviewer: 1
Comments: This manuscript reports an analysis of the free energy diagrams for photocatalytic conversion of dinitrogen to ammonia over rutile (110) model surface. The results indicate that nitrogen reduction is improbable, but the N-N bond cleavage is thermodynamically facile on rutile (110) through an oxidative pathway with the strong oxidative driving force provided by photogenerated holes. This manuscript may be published in ACS Sustainable Chemistry & Engineering after revisions after addressing the following issues.
We appreciate the positive perspective, and the detailed and thoughtful comments below. We have addressed each comment point-by-point and now feel that the manuscript is significantly stronger. 1. Abstract should be improved to emphasis the importance of the study.
Thank you for this suggestion. We have added two phrases to the abstract to highlight the novelty and importance of this study: “This is the first application of computational techniques to photocatalytic nitrogen fixation” and “This work provides strong evidence against the most commonly reported experimental hypotheses”. We hope that this helps potential readers recognize the significance of the work. 2. I am curious how the authors have hypothesized that rutile (110) is active surface for nitrogen fixation. Please describe the reason in details.
The rutile (110) is the lowest-energy surface of rutile, and has been previously hypothesized by other groups. We have added a discussion of this in the introduction:
“The rutile (110) surface is hypothesized to be the active surface for due to the fact that photocatalytic nitrogen fixation rates have been observed to correlate with the amount of rutile in TiO$_2$ samples; the (110) surface is the lowest energy surface on rutile and is likely to provide a model for other rutile surfaces. Furthermore, the rutile (110) surface has been explicitly hypothesized to be the active surface in recent experimental work.” 3. Band edges of rutile TiO2 and redox potentials are shown in Figure 3, but there is no citation. Necessary citations are suggested to be added in the manuscript.
The reviewer is correct that these citations should appear in the caption, and they have now been added. We note that they previously appeared in the methods section, but realize that this is inconvenient. 4. The band gap shown in Figure 3 is much larger than 3.0 eV, which is usually reported optical band gap of rutile TiO2.
We thank the reviewer for their astuteness in recognizing this issue. It seems that the band gap was 3.2 eV, consistent with anatase (rather than rutile). Fortunately this mistake was isolated to Fig. 3, and we confirmed that the oxidative potentials in free energy diagrams were computed using the correct band gap of 3 eV. 5. It is well known that pristine rutile is not active for hydrogen evolution reaction. Therefore, selective reduction of nitrogen to ammonia over pristine TiO2 may not be challenging even though the redox potential is near SHE.
We agree with the reviewer, though we have been unable to find an experimental study of hydrogen evolution on pristine rutile (likely due to its low activity). The fact that seems most surprising is that TiO2 is capable of dissociating the strong N-N bond more easily than it can dissociate the much weaker H-H bond. This is at the heart of the selectivity challenge, and we would argue that finding a catalyst with a high H2 evolution overpotential only solves the easy part of the challenge. We have tried to clarify this with the following addition to the introduction:
“...indicating that TiO$_2$ is capable of dissociating the strong N-N bond more easily than the much weaker H-H bond”. **6. The first step for dissociative nitrogen reduction is scission of the N-N bond. This step is not photoexcited process of TiO2. Therefore, the reviewer thinks that the high energy barrier is routinely accepted. Are there any pathway for the activation of nitrogen by photoexcited electrons? For example, N2*
- * + H+ + e- NH* + N*.**
The reviewer is correct that the chemical nature of the N-N scission suggests that a photon/electron mediated process would be needed to exploit the photocatalytic driving force, although we point out that this has not stopped other authors from hypothesizing the direct dissociation pathway. Specifically, we chose to address the direct dissociation pathway because it has been explicitly hypothesized by Hirakawa et. al., and because it represents one “extreme” of the reaction mechanism. Clearly, there is potential for “mixed” mechanisms with dissociation of N2Hx species. However, these mechanisms still lead to the formation of N* or NH* which are exceedingly unstable on the pristine and Fe-doped surfaces, and hence can be ruled out even with the modest 0.15 V overpotential. The exception is the oxygen defect, where NHx species are much more stabile; however, N* is still very unstable, indicating that formation of HNNH is still required. Since this is the potential-limiting step for the associative mechanism we suggest that there is little advantage to showing the thermodynamics of the mixed mechanisms, though these should certainly be considered in more advanced studies with kinetics included.
We have addressed this possibility with two comments:
“The same stabilization would be required for NH* species, effectively eliminating any pathway involving NH* (e.g. dissociation of NNH). Adsorbed NH$_2$ species are somewhat more stable, and may exist under solvated conditions, opening the possibility of mechanisms involving dissociation of N2Hx>2 species, similar to the associative mechanism that will be discussed subsequently.”
“An alternative possibility is a mixed mechanism proceeding through dissociaton of partially hydrogenated species, since the NHx species are stable at the O-br vacancy; however, this would still necessitate the formation of the potential-limiting HNNH* species from the associative mechanism and would be thermodynamically (though not kinetically) equivalent.” (page 17)
7. Equations 7–12 are incorrect.
Again, we thank the reviewer for astuteness. The prior version listed the dissociative mechanism twice due to an error, which has now been rectified. 8. In the caption of Figure 9, “the conduction band edge” may be “the valence band edge”.
Thanks to the reviewer for catching this typo, we have corrected it in the current version. 9. Figure 10 was not referred in the manuscript.
Thanks for catching another oversight; we have fixed this. We discussed the general idea in the original text but never referred to the figure. A more detailed discussion of these results has been added along with a reference to the figure. 10. It is suggested that nitrogen is first oxidized to nitric oxide and subsequently reduced to ammonia. If so, there are reduction pathways of NO into N2 and N2O in addition to NH3. Detailed discussions are necessary since the proposed mechanism is speculative.
The reviewer is correct regarding the possibility of back-reactions. This has been observed experimentally by Yates and colleagues in UHV conditions (see C. N. Rusu and J. T. Yates, J. Phys. Chem. B, 104, p. 1729, 2000 and C. N. Rusu and J. T. Yates, J. Phys. Chem. B, 105, p. 2596, 2001 – both cited in the manuscript). A detailed investigation of this is beyond the scope of this paper, but we have now pointed out this challenge and added some additional discussion:
“However, reduction of nitrogen oxides is a complex process that can also form partially reduced species such as N$_2$O or N$_2$. In particular, the reaction of NO to N$_2$O and the reaction of N$_2$O to N$_2$ has been observed under UHV conditions by Yates and colleagues. Fully understanding the selectivity of photocatalytic NO reduction on TiO$_2$ is beyond the scope of this work, but selectivity should be considered in future studies of NO reduction.”
11. There are typo, for example, “the the” in Line 2 on page 6.
Thank you for catching this typo. We have proof-read the manuscript for others and hope that none are remaining. 12. Abbreviation should be explained when it first appears in the text.
We thank the reviewer for catching this oversight. The manuscript has been changed to explain each abbreviation when it is introduced. 13. The format of the references should be unified according to the requirements of this journal.
Thanks for catching this, we have modified the reference formatting to be consistent with the journal requirements.
Reviewer: 2
Comments: I understand that the authors have chosen to remove the experimental data which was superfluous due to already published data by others as pointed out by one of the reviewers. As it stands, I do not recommend this paper for publication in EES since it only presents computational data that does not explain the experimental findings nor suggests a reaction mechanism instead it focuses on excluding a number of reaction mechanisms. Therefore, I think this manuscript would be better suited in a more technical computational journal.
We respectfully disagree with this reviewer’s assessment, and feel that the work addresses a number of specific hypotheses that appear in the experimental literature, while also suggesting others for future testing. This should make the manuscript accessible to experimentalists, and also provide experimentalists with ideas for additional studies. Contrary to the reviewer’s comment, we explicitly propose a reaction mechanism (indirect reduction) that is thermodynamically plausible and does not appear elsewhere in the literature. We believe that this hypothesis-driven approach is an efficient way to communicate knowledge between experimental and computational studies. The goal of the scientific method is to test hypotheses, and we feel that conclusively disproving a hypothesis is of similar value to proving one. Given the nature of the work we feel that EES is an appropriate outlet. The more technical journals suggested tend to focus more heavily on method verification or development rather than hypothesis testing.
Reviewer: 3
Comments: This study applies density functional theory
calculations to examine the elementary reaction free energies associated
with nitrogen reduction on the rutile TiO2 (110) surface. The results
presented illustrate well that the reduction of nitrogen to ammonia is
not energetically feasible on the pristine, stoichiometric surface. Some
consideration of oxygen vacancies and doped Fe looks promising and is
considered at a relatively basic level, as well as potential other
conversion routes that include first oxidation followed by reduction.
The overall conclusions are interesting, and the resulted are presented
with limitations clearly highlighted. The limitations in the analysis
are quite severe, as there is no direct consideration of elementary
kinetics (ie, barriers), and catalytic kinetics are, of course,
generally dictated by barriers and not reaction energies. However, in
this study, large differences in reaction energies are sufficient to
make some interesting qualitative conclusions. Other major limitations
in the modeling approach include the lack of consideration of
interfacial solvation and charging in the photoelectrocatalytic system.
Again, though these are significant limitations, the large energetic
differences make qualitative conclusions still generally well supported
by the more simplistic analysis. As these limitations are highlighted
for the reader and discussed, I recommend publication following
consideration of the following significant comments.
We thank the reviewer for this positive assessment, and are grateful for
their ability to recognize the considerable value provided by the
relatively simple models employed. Further, the constructive criticism
provided is very useful and we have revised and improved the manuscript
accordingly. 1) I have a number of comments regarding the
consideration of the stable state of the surface under reaction
conditions, the first section of results.
a. It is unclear what the difference between the “gas” and “aqueous”
conditions are in the discussion of these results. The authors note that
the gas phase is humidified, and presuming 100% humidity, the chemical
potential of gas phase water and liquid water would be equivalent. The
chemical potential of water in the aqueous system is noted as being
calculated directly from the saturation pressure of water (ie, 100% RH),
and from what I can tell, the water chemical potential is the only thing
that could differentiate the two conditions in their modeling approach.
Did the authors consider the “gas” conditions as 0% relative humidity,
and the “aqueous” conditions as 100% relative humidity? If so, this
should be clarified, and discussed why 0% RH would be the relevant “gas”
phase conditions given this system would presumably be exposed to
ambient air.
The reviewer is correct, and we apologize for the previous ambiguity. The original figure had all values for chemical potential set to 1 atm except the value being modified. for Example in plot c, the chemical potential of N$_2$ and O$_2$ were set to 1 atm, while the chemical potential of water was modified. We realize this does not reflect experimental conditions, but was generated this way to get a general overview of coverages at low and high pressure. We have revised the figures to track more realistic chemical systems. Plots a-c have been revised such that the chemical potential of N$_2$ and O$_2$ have been set to 0.8 atm and 0.2 atm respectively as the chemical potential of water is modified, with zero representing liquid water. Plots d-f have the chemical potential of water set to 0.035 atm and O$_2$ set to 0.2 atm while N2 is moddified, with zero being set to 0.8 atm. The plots intersect at 0, reflecting the fact that the free energy of liquid water is equal to the free energy of water vapor at 100 % RH.
b. In Figure 2, to make the plots on the left (a, b, and c), I believe a constant value of the chemical potential of N2 must have been assumed. On the right (d-f), a constant chemical potential of water must have been assumed. The authors should clarify what values were used for these species in making these plots.
The reviewer is correct and we thank them for noting this, omitting this fact was an oversight. The main text has been clarified. The chemical potential of water is set to 100% relative humidity.
c. In making these plots, the authors have only considered adsorbed N2, whereas the steady state system operating photocatalytically would attain a surface potential, and formation of stable NxHy species would be possible. As the authors show, adsorbed NH3 (and other species under certain conditions) can be more stable than adsorbed N2 under operating conditions. The authors might consider making diagrams at a presumed operating potential to consider if the surface would attain (thermodynamically) a high coverage of NHx species. Similarly, operating conditions could cause the reduction of surface O atoms (ie, the adsorption of H or formation of surface O vacancies), and this was not considered.
The reviewer is correct that formation of NxHy species is possible, and a thermodynamic analysis of the process including all species would show high coverages of NHx species. However, we know that this process is kinetically slow in practice due to N-N bond scission. We suspect a high kinetic barrier to exist somewhere in the system, however our analysis is unable to display this. Because of this limitation, we have chosen to only use the reactants, as they are likely to dominate under real reaction conditions. In order to properly estimate the coverages of these species we would also need to include the concentration of ammonium ions, hydrazine, and nitrites/nitrates; however, these quantities are not well-known experimentally and would require a kinetic model to estimate. Nonetheless, we expect that the concentrations would all be relatively low, creating a driving force to remove NHx and NOx surface species. We have produced figures for this analysis under both oxidizing and reducing band edges and included it in the supplementary material.
2) I am a bit confused as to the distinction between routes that first undergo oxidation and those that initiate through reduction, given the surface of TiO2 has O atoms. It appears the difference between N2O* and N2* is that an excess O atom is present. However, presumably N2* could form by creating an O vacancy, appearing as “N2O* adsorbed with a vacancy nearby.” Or, wouldn’t N2 reduction occurring on a surface that had excess O* to begin with be mechanistically equivalent to the “NO” route? Presumably N2 would adsorb to an O rather than the Ti if the surface was overoxidized.
Regarding the first part of the comment, N2 does not adsorb at an O-br
site unless it is constrained, indicating that this is not a viable
route to formation of an oxygen vacancy. However, in the case of excess
O* the reviewer make a good point regarding direct adsorption of N2 to
a surface O*. Indeed this is (slightly) more energetically favorable
than independent adsorption, and hence we have changed the mechanism for
N2
This comment has been addressed by modifying the N2
3) The authors state in the conclusions “defects are not predicted to be thermodynamically stable under operating conditions.” The basis for this conclusion is unclear – I don’t see a consideration of the reduction of surface O atoms to form water and a vacancy considered in the paper.
The formation energy for oxygen defects discussed in the text (1.54 eV) is the energy required to reduce the surface oxygen atoms to form water. This was not stated explicitly which likely led to confusion. We have added the reactions of each defect formation energy in the supplementary information to clarify the reference states.
4) The consideration of Fe doping is rather basic, as the authors do not appear to have considered whether Fe doping would alter the stable state of the surface. Fe doping forces formation of a Fe4+ formal species, though reduction to Fe3+ or Fe2+ would be much more likely under N2 reduction conditions (see Fe Pourbaix diagram). A Fe2+ model would be relatively easy for the authors to consider, as this would likely form simply by having Fe doping occur together with an O vacancy formation. Fe3+ could be modeled with two Fe dopants and a vacancy. These would be much more realistic models of the Fe doped system. Some discussion of this large limitation in the Fe doping consideration should be added, or possibly the Fe doping analysis simply removed. In its current form, I would consider the Fe doping calculations done possibly misleading.
This is a very good suggestion. The iron site was added due to a request during the first round of revision, and the model in our paper was chosen for simplicity. However, the reviewer’s point regarding Fe formal oxidation states is a good one, and indicates that more realistic models can be created rather simply. We have tested the Fe3+ and Fe2+ sites suggested and found that an Fe2+ site is more stable than the original model. We have repeated the analysis on this site and replaced the free energy diagrams in the main text with these, and added a comparison of the two sites in the SI. The new results have not altered the main conclusions of the paper as the barrier to nitrogen dissociation and the first hydrogenation is still very large; however, the new site is more stable even than the O-br defect, and has an appreciable N2 binding energy, which could have implications in future studies. We have revised and expanded the discussion as follows:
“Two defects were considered, an Fe$^{4+}$ defect arising from direct substitution of the 5-fold Ti atom, and an Fe$^{2+}$ defect formed by substitution of a Ti atom beneath a bridging O and removal of the bridging O, effectively forming a O-br defect and Fe substitution (see the Supplementary Information for visualization of the slab). The Fe$^{2+}$ defect was found to be more stable, and Fig. 7 shows the energetics of the associative pathway with an iron-substituted rutile (110) surface (a comparison of the free energy path for the Fe$^{4+}$ defect is available in the Supplementary Information). This mechanism is very similar to the mechanism on the pristine and O-br vacancies, with the slight difference that N-NH$_2$ is more stable than HNNH on the Fe defect. The limiting potential of 2.2 eV is comparable to that of the defected surface in Fig. 6 (1.7 eV), but is slightly higher due to the stronger adsorption of N$_2$. The energetics of the associative pathway on Fe-substitution defects are compared directly to O-br defects and pristine rutile (110) in Fig. 8a, illustrating that the Fe-substitution defect has a similar effect to the O-br vacancy. The energy required to form this defect was calculated to be 1.1 eV relative to bulk rutile and BCC iron. This moderate formation energy is lower than that of the O-br defect, and N$_2$ adsorbs with a relatively strong binding energy of -0.5 eV. This suggests that Fe surface defects promote the formation of O-br vacancies and adsorption of N$_2$. Nonetheless, the high limiting potential of 2.2 V indicates that the Fe-substitution defect is not active for photocatalytic nitrogen reduction.”
a. In the Fe doped section, I did not understand the statement “The energy required to form this defect was calculated to be 2 eV relative to bulk rutile and BCC iron.” Such a consideration would require at least knowing the chemical potential of O (or that of water, protons, and an electrochemical potential), so it is unclear the basis on which it was concluded Fe doping was unstable.
We see now that this is ambiguous. For this energy, the iron reference is BCC iron, the proton and electron reference is set by the reversible hydrogen electrode at zero potential, the oxygen reference is set by gaseous water at saturation pressure at 300K and the titanium reference is set by the TiO$_2$ bulk calculation. We have clarified this by including the reaction for defect formation in the SI. 5) Bottom of page 22, “reference hydrogen electrode” should be “reversible hydrogen electrode.”
Thanks to the reviewer for catching this typo; we have corrected this in the manuscript. 6) Page 23 – The potentials given for holes and excited electrons should be clarified as to what is the reference scale.
The reviewer is correct that the approach used may be confusing, and we have clarified this in the methods section. We have chosen to treat holes/electron potentials in a way that absorbs DFT error into the equilibrium energy and hence preserves overpotentials that are consistent with the experimental values (otherwise overpotentials would be incorrect by an amount equal to the DFT error in the equilibrium potential). We tried to clearly state this in the captions, and have now elaborated in the methods section to clarify further.
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