Peer review of: Image polaritons in boron nitride for extreme polariton confinement with low losses (2020)

Reviewers' comments: 
 
Reviewer #1 (Remarks to the Author): 
 
The authors present an interesting device based on hybrid hBN-metal nanostructures featuring 
extremely confined electromagnetic modes with high quality factors of up to 500 at mid -infrared 
frequencies. 
This is a record for nanophotonic devices at MIR frequencies. Their design goes beyond existing 
platforms using highly confined plasmons in graphene coupled to metallic surfaces. In their device, 
they used hyperbolic phonon polaritons (HPhP) in hBN coupled to their image polaritons in metallic 
ribbons. The phononic nature of the HPhP enables highly confined modes that are not limited by 
Landau damping. They further demonstrate by comparing their experimental data with their 
theoretical model that the losses of this new design are solely limited by surface scattering losses. 
This is a new  and highly interesting device that could unlock potential applications at MIR 
frequencies such as single molecule spectroscopy and sensing applications. 
Overall the paper is w ell written and goes straight to the point without lengthy explanations. 
I recommend this paper for publication in Nature Communications . 
I have added a few comments that the authors are welcome to take into account in order to 
improve the quality and readability of the  paper. 

1. In the paragraph “Gap dependence and dispersion” it w as unclear to me which type of hBN you 
used. Is it the h10BN or the naturally abundant hBN? In the paragraph “Naturally abundant vs. 
isotopically enriched hBN” you ananlyse the differences in your reflectance measurements of 
naturally abundant hBN and h10BN. You clearly demonstrate that the antisymmetric mode is only 
visible in samples with the h10BN. I therefore suppose that the devices presented in the “Gap 
dependence and dispersion” are fabricated from h10BN. For clarity, I would suggest the authors to 
start first to present their results with different isotopically enriched hBN, show that anti-
symmetric modes are only visible in h10BN and then discuss the dispersion properties of the 
symmetric and anti-symmetric modes in h10BN. I think that it will increase the clarity of the text . 
2. The definition of the symmetric and antisymmetric modes should be sharpened. In general the 
definition of the antisymmetric and symmetric modes is given by the symmetry of the tangential 
(here in your case Ex) of the electric field in the hBN slab. In Figure 1b, it is unclear to me w hat 
component of the E field is plotted. Is it Ex(y)? If so, please indicate it more clearly. 
3. The authors mention that the inhomo geneities and defects in the hBN film  are responsible for 
the decreased absorption observed in the reflectance. They mention also in the method that they 
have measured the thickness to the hBN flakes with AFM. An AFM image in the supplementary 
would be useful for the readers to assess the homogeneity of the thickness throughout the hBN 
flakes. If you could extract an RMS of the roughness that would even be better. 
4. Minor typos: 
- “While these performance metrics are already impressive, their ultimate limit has yet NOT been 
experimentally probed and understood” 
- Legend with gaps in Figure 2g. 
- “…w here t12 and t12 represents the modal transmission coefficients of the HPhPs” should be 
changed to “… w here t12 and t21 represent…” 
 
 
 
Reviewer #2 (Remarks to the Author): 
 
1. General comments 
In this manuscript, the authors achieved the highly confined polariton w ith high Q -factor, together 
with the high coupling efficiency. Not only the geometry is fully optimized w ith the image polariton 
scheme pioneered by the authors, the isotopically pure hBN sample w as employed to further 
suppress the loss. This leads to this extremely thin layer of hBN/metasurface system absorbing 
~90% of the light with extremely high Q-factor beyond >>200, w hich is simply stunning. I firmly 
believe that the manuscript merits the publication in Nature Communications . 
How ever, before further consideration for publication, I w ould like the authors to address the 
follow ing technical comments below, and I w ould like to review  the manuscript again w ith the 
authors’ updates. 
 
2. Major comments 

(1) The role of the periodic metallic ribbons 
As the conduction plane, the authors use the periodic metallic ribbons w ith some periodicity (p), 
w hile some of the simulations (e.g. Fig. S1) appear to have been  done assuming an extended 
conducting plane. Within the manuscript, the role of the periodic metal array w as indeed unclear. 
Do I correctly understand that the periodicity is essentially adding a kick to the in -plane 
momentum as typically done w ith a grating to launch a surface plasmon polariton (SPP)? The 
authors should clarify the role of this somew here early in the manuscript, as w ell as mentioning at 
the SI note 1 how  does the (lateral) gap in the conducting plane potentially affect the dispersion 
curve. 
 
(2) The estimation of the Purcell facto r 
At conclusion section, the authors estimate the Purcell factor of the polariton -based resonator to 
be exceeding 107, based on the quality factor and effective refractive index for the symmetric 
mode. How ever, the Purcell factor also depends on the mode volume – the highly confined nature 
of the polariton mode w as discussed throughout the manuscript, w hile the quantitative value of 
the mode volume w as never discussed, as long as I am aw are of. As the gigantic Purce ll factor is 
one of the signatures of this resonator, the authors should clarify the quantification of the mode 
volume. 
Also, in the end it w as unclear w hether the symmetric mode or the anti-symmetric mode is more 
beneficial for any further applications. At least for the Purcell factor, the anti-symmetric mode 
seems to be more advantageous, as it has higher Q -factor as w ell as mode-confinement (see my 
comment below ). One of the unique natures of the use of h10BN is also in that the anti-symmetric 
mode is observable. Letting aside the lower coupling efficiency for this mode, the authors should 
compute the Purcell factor for the anti-symmetric mode as w ell. 
 
(3) Confinement of the anti-symmetric mode 
I found the authors’ claim on the confinement and gap-size dependence of the anti-symmetric 
mode to be confusing. The authors claim at the early stage of the manuscript that the mode 
confinement for the AS mode is stronger than the S mode based on the cartoon in Fig. 1c (p.3: 
Due to the out-of-phase charge oscillation,… leading to stronger polariton confinement than for the 
symmetric mode). If the field is confined at the gap between the hBN and conducting plane, I 
w ould expect the momentum, Q-factor, loss etc. to be highly dependent on the gap . 
How ever, in contrary, the authors find that the reflection spectra and loss mechanism to be 
insensitive to the gap, w hich is against the intuition. (p.4: Such spatial distributions also explain 
w hy the anti-symmetric mode is less sensitive to the gap size; p.6: … w hich show s the anti-
symmetric mode is less sensitive to the gap size). At pg. 4, the authors attempt to give some 
explanations based on Fig. 2f, merely based on which the mechanism of the insensitivity is 
honestly unclear. If the calculations in Fig. 2e and 2f are re peated for another gap and 
demonstrate how the field profiles are altered, it may be more convincing . 
The authors should strengthen the discussion on this aspect. 
 
3. Minor comments 
(1) The role of objective lens 
The authors use FTIR microscope. Clearly this is necessary to observe the region w here 
hBN/metrasurface is formed, but is this also important to launch the polariton by adding some in -
plane momentum? 
 
(2) h10BN 
In Figure 1 and 2, the authors should clearly indicate they measure h10BN, not the natural one. I 
was confused for a while on which sample the authors are measuring. 

(3) Fig. 1a 
Is this mainly for the symmetric mode? Do I correctly understand the profile is dominated by the 
symmetric mode because the symmetric mode has less momentum mismatch ? If you plot the field 
amplitude with log scale for example, can you also see the anti-symmetric mode? 
 
(4) Fig. 2g 
The y-axis should be scaled from 0 – 100%. 
 
(5) Fig. 3 
The labels are missing. In Fig. 3a, I believe the left one is for the symmetric mode  and the right 
one is for the anti-symmetric mode. If so, the curves need to be clearly labeled and clarified in the 
caption. 
The three curves, I believe, correspond to g = 20 nm, 8 nm, 3 nm, from top to bottom. Again, this 
needs to be clearly labeled in the figure. 
 
(6) Introduction 
For the general readership of Nature Communications, it may help to clarify the potential broader 
applications of phonon/plasmon polaritons at the very beginning of the introduction w ith some 
citations, e.g. from Oh, Basov, and Hillenbrand group etc. 
 
 
 
Review er #3 (Remarks to the Author): 
 
“Pushing the Polariton Confinement Limits with Low Losses using Image Polaritons in Boron 
Nitride” by Li et al. demonstrates highly confined, low -loss modes associated with hexagonal boron 
nitride near metallic gratings, which serve not only to couple far-field light to the polaritons, but 
also change their dispersion w hen the gap is very small. By performing scattering experiments, the 
authors conclude to have observed both the symmetric low est-order metal-dielectric-hBN mode, 
as w ell as the antisymmetric mode, the latter of which w as concluded to have an effective index of 
130 and a quality factor of roughly 500. Their results w ere in part assisted by: not patterning the 
BN directly, and using isotopically enriched BN, similar to a previous work by some of the authors 
in Nature Materials. 
 
In general, the results seem correct and the platform is new  (in the context of phonon polaritons) 
and may enable advances in light-matter interactions as well as nanophotonics with phonon 
polaritonics. In my opinion, the  one of the strongest points is the simultaneous figures of merit 
achieved (confinement and loss). 
 
However, the manuscript needs to be clarified further. In particular: 
 
1. The authors compare their system to a somewhat similar system in graphene (Science  
360.6386 (2018): 291-295.). I w ould like to see a more in-depth discussion about the similarities 
and differences between the authors’ system and this one. In particular, tw o questions I have are : 
 
1a. In the graphene system, the dispersion is fundamentally altered by the metal (becoming 
linear), w hile according to Fig. 2i of the current manuscript (and Fig. 1b of the supplement), the 
dispersion is qualitatively similar, and simply pushed to larger momenta for smaller gaps. Could 
the authors comment on w hy their system is so different? 
 
1b. Could the authors also comment on w hat transverse confinement (e.g., the mode length) is in 
their system, as a function of gap size? How much of the energy resides in the gap? How does this 
compare to the analogous system in graphene? 
2. What is the origin of the critical gap parameter in the surface scattering model? 
 
3. Comparing the theoretical damping rate to the measured damping rates of the polaritons 
indicates considerable discrepancies. The authors attribute this  to the sensitive nature of the 
antisymmetric mode scattering to defects and other imperfections. Could the authors back this 
attribution up through some (simple) simulations including roughness or other defects (simply to 
show  sensitivity of the quality factor to realistic roughness, rather than to quantitatively account 
for the observations). Such considerations could also in principle determine how much variation in 
the quality factor is to be expected. Further complicating the authors claim is that even  for the 
symmetric case, the larger gap sizes (8 and 20 nm), the trend in the measurements seems to not 
follow  the predictions either. Generally, I w ould like to see the discussion of possible discrepancies 
expanded upon. 
 
4. Exactly w hich field is being plotted in Fig. 1a? 
 
5. Finally, some of the points made in the introduction/abstract need to be qualified, as they can 
potentially confuse a reader newer to the field. 
 
5a. For example, “Polaritons in tw o-dimensional (2D) materials provide extreme light co nfinement 
that is not possible w ith conventional metal plasmonics” needs to be toned -down, as metal 
nanogap structures enable much tighter confinement (though of course, in hBN, the losses are 
much better, and the spectral range w here confinement happens is different). 
 
5b. Furthermore, some statements, as w ritten, appear to not be correct. For example: “Recent 
w orks on PhPs in 2D materials such as hBN have reported effective indices of a few  tens - several 
times larger than values previously reported for plasmons in metallic nanostructures or graphene”. 
In graphene, effective indices of >100 are somew hat commonplace (as just tw o examples, take 
Nature materials 14.4 (2015): 421-425 or Nature 557.7706 (2018): 530-533).