Peer review of: Measurement of the spin-forbidden dark excitons in MoS2 and MoSe2 monolayers (2020)



RR2
REVIEWER COMMENTS
Reviewer #1 (Remarks to the Author)
I have thoroughly read the revised manuscript, SI, and authors’ responses to all the reviewers. The authors have addressed some of my questions. However, after careful reading, I believe that the revised manuscript still does not meet the standard of Nature Communications for the three major reasons.
1. First, this work does not have enough novelty, and the result is not significant enough. The authors applied an in-plane magnetic field to brighten the dark exciton in MoS2 and MoSe2, similar to what has been done previously on WSe2, WS2, and especially MoSe2. The work on MoSe2 is not significantly different from previous work. The author showed that the dark exciton is the ground state for MoS2. However, it is not clear why that would lead to new physics beyond what we have known for WSe2, WS2, and MoSe2.
2. The experimental data quality shown in this work does not fully support the four-band theory presented in this work and should be significantly improved. Considering the significant improved quality of BN encapsulated TMD devices, including the authors’ own efforts, the MoS2 PL shown in this work is simply too broad to extract fine features needed for the authors’ theory. The bright exciton PL does not even look like a single PL peak.
3. The results are inconsistent with what we know about MoS2. For example, it is inconsistent with the temperature dependence of PL from MoS2, including the authors’ previous work (PHYSICAL REVIEW X 7, 021026 (2017)). The authors spend some efforts to reconcile the discrepancy. However, these explanations are based on speculation and hypothesis that are not supported by experiments or quantitative analysis. Some are even incorrect.
I think the manuscript is better suited for a specialized journal such as 2D Materials for PRB after the improvement. I list specific questions below.
1. In response to the authors’ reply: “But none of them unambiguously solved the problem for MoS2 although this material is the most studied among the TMD family (for instance, ~1177 papers published in the past 12 months for MoS2, compared to only 118 for WSe2 or 94 for MoSe2 – Source : Topics inWOS).” The large number of papers on MoS2 is mostly because the MoS2 crystals are more abundant in nature and more accessible, which is also the reason why it was studied first among TMDs. This fact itself does not justify the novelty. The authors need to specify why the discovery of dark exciton in MoS2 leads to new discovery compared with what has been done in WSe2, WS2, and MoSe2.
2. Related to the authors’ reply about the linewidth of the MoS2, the PL spectra shown in Fig. 1 is quite broad and cannot even be described with a single Lorentzian peak at 0 T. There is at least one shoulder peak around ~1.94 eV (and even another one at ~ 1.95 eV). How do the authors determine the bright exciton peak position? Considering the

measured split is only on the order of 10 meV, accurate determination of the peak position and PL nature is critical.
3. Related to question (2), what is the doping of the MoS2 studied and did the authors measure the PL spectra as a function of carrier density? This information will be important to identify different peaks. For example, dark trions would have the same dependence on the in-plane B field and will also have the same g-factor.
4. The authors need to show the line traces of the color plot in Fig. 2, especially for B field close to 10 T. It is not clear how the author could extract the dark exciton peak position at the field around 8 T. Fig.2a reproduced previous results of MoSe2 (2D materials, 7 015017 2019), but the data is of lower quality. The dark exciton could not be seen until B field > 8 T (according to the authors), while it can be observed for the B field as low as 5 T in the previous work (2D materials, 7 015017 2019). The data extracted from Fig. 2a does not support the four-band theory developed by the authors. For example, the dark exciton behavior at the low B field transition to the grey exciton behavior at the high B field is a smooth change (Fig. 2b). At the intermediate B field, say 20 T, two PL peaks instead of one should be observed according to the four-band theory. However, this is not the case. Could the authors try to analyze the data from the previous work to see if that fits the authors’ theory? The current data does not support this theory.
5. Also related to the fitting in Fig. 2b, if the fitting is not sensitive for δ < 1 meV, why set it to be 0.6 meV instead of 0 meV? There is no guarantee that the value in WSe2 (PHYSICAL REVIEW B 96, 155423 (2017)) should be the same in MoSe2, considering the sample difference and even the doping difference. Could the authors show the fitting result of 0 meV, is it better than the fitting with δ =0.6 meV? Did the author fit the data with the two-level model (just bright exciton and dark exciton) instead? The two-level model would also give four PL peaks for the tilted B field. Is the four-band fitting quantitatively better? The current PL data does not seem to support that the four-band theory instead of the two-level theory.
6. For Fig.3, the authors should also show the PL line trace for the low B field. Can the authors fit the data with just the Zeeman splitting of the dark and bright exciton? It is not clear that the current data is fitted better with the four-band theory.
7. What is the doping of the MoSe2 studied here? Did the authors study the dependence on the carrier density, especially with an in-plane magnetic field, as shown in the previous work (2D materials, 7 015017 2019)?
8. Can the author show the PL line traces in Fig. 4 that shows peak 3 and 4? It is not clear how peak 4 can be extracted from the color plot. Again, can the authors fit the MoS2 data with only the Zeeman splitting of the dark exciton and bright exciton, which will also give 4 peaks? Would the fitting be quantitatively better or worse than the fitting by the four-band theory?

9. The fact that the dark exciton is lower in energy than the bright exciton in MoS2 is not consistent with the temperature dependence of the MoS2, including the authors’ previous work (PHYSICAL REVIEW X 7, 021026 (2017)). The author should perform temperature-dependent PL of MoS2 in the presence of the in-plane B field. The PL intensity ratio between the dark exciton and bright exciton as a function of the temperature will tell the information about the energy difference between the dark exciton and bright exciton.
10. The authors claim that the reason they could observe dark exciton in MoS2 with large NA object might be “We can speculate that either the oscillator strength of grey exciton is much smaller than in WX2 and/or that their population remains weak despite lying at lower energy than the bright state.” Do the authors have an estimation of the oscillator strength of the grey exciton compared with that of the WSe2? Fine features of dark exciton such as dark trion and dark exciton phonon replica have been observed in WSe2 (Nature Communications volume 11, Article number: 618 (2020); Nature Communications volume 10, Article number: 2469 (2019); Phys. Rev. Lett. 123, 027401, (2019); Phys. Rev. Research 1, 032007(R), (2019)). These fine features are supposed to have much smaller oscillator strength than the dark exciton of WSe2 but still can be directly observed. Therefore, I am not convinced by the author’s speculation.
11. The authors also claim, “For the population issue, we can notice that contrary to WX2, the bright- dark exciton splitting in MoS2 ML is smaller than the optical phonon energies which can lead to inefficient relaxation between bright and dark excitons”. This speculation is incorrect. First of all, for non-resonant excitation, it is not correct to assume that the excited electron-hole pair to relax to the bright exciton state first. The exciton with excess energy can directly relax to the dark exciton state. Also, there is no guarantee the relaxation of the exciton to the dark exciton state is only via one particular optical phonon mode.
12. For the discussion of the g-factor of the dark exciton in MoS2: “The measurements in the tilted field geometry presented below yield 𝑔𝑧𝐷=-6.5 ; this large value is in good agreement with the predicted one in a simple model26 and the measured one in WSe2 MLs21,27 (see table I).” The authors should explicitly include the theoretically precited value here and compare it with the experimental data. Also, the authors should explain why the value of 6.5 for MoS2 is a good agreement with the value of 9.4 (experimentally obtained from WSe2).
13. Table I should include the previous results of MoSe2 for completeness.
14. The authors claim that their results will be important for understanding the “trion fine structure.” Could the authors elaborate on that, and why is it different from what we have known from WSe2?
15. Did the authors use the four-band theory to fit the data in Fig. 1? How does that compare with the fitting with the two-level model?

16. How does the dark exciton intensity of MoSe2 scale with B field? Can the authors analyze data from Fig. 2 similarly as Fig. 1?
17. I would hesitate to call the MoS2 device in this work “high quality”, considering the broad PL width and the shape of the PL. The authors claim that the bright exciton peak width is 7 meV in the reply. Could the author show the fitting of the data shown in Fig 1? It is not clear how could the MoS2 bright exciton PL at 0 T (Fig. 1) be fitted with a single peak. The author attributed the broad PL to inhomogeneity broadening, but it is simply too large for a 2-micrometer spot.

 Reviewer #2 (Remarks to the Author):
 The authors provided a detailed, comprehensive response to the previously raised questions and
 included appropriate changes to the manuscript and supplementary. I thus further emphasize the
 importance of the reported findings for the field and strongly recommend publication of this work
 in Nature Communications journal.
 (I apologize for not appending the following question/suggestion to the initial report. This should
 be thus considered as fully optional at this stage:
 - Considering intensity dependence of the XG/XB ratio for MoSe2 – is it correct that one would not
 expect the quadratic dependence with the magnetic field (compared to MoS2) due to the
 competition between field-induced brightening and changes in the population ratio due to the
 energy splitting? Can the extracted intensity ratio be reasonably modeled using the two
 components or may one observe non-equilibrium scenario in the experiment?)
 Reviewer #3 (Remarks to the Author):
 With the appropriate responses to the reviewers' reports and substantial improvements in the
 figures, model simulation, and data interpretations, I agree with the publication of the revised
 manuscript in Nature Communications.