Peer review of: Plasmon-driven synthesis of individual metal@semiconductor core@shell nanoparticles (2020)

Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

Baldi and coworkers report on the synthesis of semiconductor shells around gold nanoparticle cores 
enabled exclusively by the heat generated locally at the individual particle level upon illumination with 
532 nm laser light. The authors exclude the role of hot holes in this reaction and demonstrate that the 
proposed process affords the growth of uniform shells, which is not possible via regular heating of the 
reaction vessel. The study is interesting and extremely valuable at a time where the field is trying to 
unravel the interdependence of hot carriers and heat to carry out chemistry at the metal interface. 
However, in its current form it is still too preliminary for publication. I have explained my opinion in 
detail in the following: 

1. What do the authors mean when on page 3 they write “individual”? Does it mean that their method 
does not really illuminate individual particles? 
2. It is not clear to me if and how the temperature on the individual illuminated nanoparticles is 
measured. Also, it is not clear whether the neighboring particles are far enough on the substrate from 
the illuminated one to not experience heating due to heat transport from the illuminated particle. SEMs 
should be provided to show the actual particle to particle separation on the substrate. If particles are 
illuminated under a known sequence, is there a correlation between position and shell thickness/optical 
properties? Controls need to be set up to prove it. 
3. To prove that hot holes are not at play here, the authors point to the band alignment and the mean 
free path length of holes in these structures. However, because these studies are at the single particle 
level, an estimation of band alignment for the exact crystalline structure of ceria produced should be 
reported, along with HR-TEM characterization, for this hypothesis to be verified. 
4. All the thermal properties of the medium, substrate, etc. are calculated and not measured. While 
necessary, this calculation is however not sufficient, and local measurements need to be carried out. 
5. Details on the FDTD calculations employed and described on page 8 need to be provided in the SI, so 
that is possible to evaluate the validity of the approach and verify how the role of the substrate has 
been taken into account, importantly because at least two different types of substrates have been 
employed in these studies. 
6. A statistical assessment of optical and morphological properties of the nanoparticles at the population 
level (more than the 35 particles studied here) need to be reported to assess the validity of the 
approach and the analysis of the data. 
7. In various plots the authors report the data points with colored spheres. These are however 
misleading as it is not clear what the magnitude of the error is in these measurements and therefore 
how accurate the fit is. 
8. In equation 3 the authors propose a constant SERS response of the reactants on the nanoparticle 
surface. However, as the nanoparticle grows so does its surface area, which in turn affects the SERS 
signal. Furthermore, while the growing shell may impact the identity and intensity of the signal, this 
effect is in rapid evolution during the first growth stages. Even if we take into account only these two 
points, the equality assumed for the SERS term in Eq. 3 is not correct. 
9. The experiments on the nanorods need to be integrated with laser irradiation tuned with the 
longitudinal LSPR as controls, with experiments under polarized light, and with an explanation on why 
growth is (or not) isotropic around the nanorod. I am also curious why the spectra in figure 4 are cut at 
600 nm. TEM spectra for these additional nanostructures are needed. 
In conclusion, while the study is interesting, it still needs to be completed with additional experiments 
before becoming publishable. 



Reviewer #2 (Remarks to the Author): 

In this paper the authors report an interesting approach to grow controlled composite nanoparticles 
using plasmonic photothermal effects. In particular, the authors demonstrate growth of CeO2, ZnO and 
ZnS shells over Au nanoparticles and Au nanorods. The major novelty aspect consists in the possibility of 
controlling with great accuracy the growth of the oxide shell on each individual nanoparticle potentially 
achieving much higher uniformities then in colloidal processes where temperature cannot be well 
controlled at the nanoscale. The authors clearly present their methodology and report a substantial 
amount of convincing data. Overall, I think this work is very interesting and worth of publication in 
Nature Communication. Indeed, it is of interest for a broad community as it could enable the realization 
of highly controlled optical and chemically active substrates (e.g. for sensing, photochemistry, material 
science etc.). Nonetheless, I think the authors should address these following major concerns before the 
paper can be accepted for publication. 
Major Points 
• One aspect that I find a bit surprising is that the authors did several TEM images but do not appear to 
use TEM to measure the thickness of the semiconductor shell grown around the Au nanoparticles. 
Instead they rely purely on FDTD simulations. Although the FDTD simulations can be a good tool for 
covering the wide range of thicknesses explored by the authors, from Fig. 1d it is clear that the shell is 
quite rough and far from an idealized perfectly spherical shell. It would be thus very helpful if the 
authors could show the correspondence between the calculated shell and measured (TEM) shell 
thickness for a one or two shell thicknesses (ideally a thin one and a thick one encompassing the range 
of thicknesses studied). In particular, the TEM images would allow to assess the quality of the shell and 
the statistic distribution of its thickness. If this is not feasible it would be helpful if the authors could 
explain the experimental constraints that limit them to using solely FDTD. 
• Related to the previous point, one of the major claims of the work is that this approach allows highly 
controlled growth of the semiconductor shell. In this respect, I think that the work would be greatly 
strengthened by showing some statistics on the reproducibility of the process. Indeed, it would be 
interesting to show that under XX mW/um2 laser irradiation for YY min the shell growth is ZZ+/-zz nm. It 
could then be very helpful to relate the uncertainty to the experimental conditions: does it originate 
from the size dispersion of the initial nanoparticle size? Does it originate from the uncertainty in the 
laser/nanoparticle overlap? What conditions have the largest impact and should be thus controlled with 
the greatest precision? Such discussion would be very instructive for other researchers interested in 
applying this method. 
• In the discussion of the plasmonic photothermal effect, the authors assume that convective heat 
removal is negligible for their problem (i.e. heat is removed solely by diffusion through water which has 
a low thermal conductivity). However, this assumption is reasonable only if the liquid surrounding the 
nanoparticles is highly confined so that convective motion cannot reach large velocities. However, the 
authors do not discuss at all the geometry of their test cell (apart from showing a schematic without 
dimensions in Fig.1). It is thus very important that the authors provide greater details about their test 
cell. Also, in the main text they should explicitly address the assumption of negligible convection. 
• Related to the previous point, the authors explain that the CeO2 shell growth is a very good test 
process because it does not occur below 90C. This means that there should be a laser threshold power 
below which irradiation does not lead to any shell growth. This laser threshold would also enable the 
authors to validate their thermal model. Indeed, they should find that for such laser power and laser 
position the temperature increase calculated with eqn. 2 or eqn S9, which neglect convection and 
assume an average thermal conductivity for the surrounding medium, is below 90C. Do the authors 
observe such threshold? If not, is there any experimental limitation that hinders such observation? The 
authors might want to discuss this point in the manuscript. 
• In Fig. 2e the authors show that the scattering signal is independent of polarization. However, they 
never discuss how sensitive is their scattering signal to the shell thickness. In fig. S6 they show the result 
of numerical calculations but what about the experimental result, which has a broader plasmon 
linewidth and a noisier signal? If the grown shell was differing by only a few nm, would they be able to 
distinguish it in the DF signal? What about the polarization dependent measurements for the Au 
nanorods? Connecting to my first point, TEM images might clarify this aspect. In particular, Au nanorods 
would be a better test because the asymmetry should be maximum if other effects (e.g. near field, hot 
carriers) were to play any role. 

Minor Points 
• I feel that the data repartition between the main text and the supplementary often does not reflect 
the really important points that the authors are trying to make in the manuscript. 
o For example, in Fig. 1 most of the space is taken by the optical set-up description and only a minor 
part is devoted to the data/TEM/EDX. Although in this work the simultaneous measurement of diverse 
optical signals is important, I find that the optical set-ups are not novel and could be very well described 
in detail in supplementary without loss of understanding from the reader. Instead, Fig. 1 has no clear 
sketch that explain the data shown in Fig1c-d and more broadly what the authors are doing. It is true 
that in the experimental set-up drawings (Fig1a-b) the authors have added a shell around an Au 
nanoparticle under laser irradiation but the detail is practically invisible for the reader. In fact, the 
attention is entirely focused on the large optical set-up schematic. I thus suggest that they zoom in onto 
the sample schematic to clearly show the nanoparticle without/with shell without/with irradiation, 
respectively. They can simply use some labels (e.g. Dark Field, PL) under such zoomed view to explain 
which optical signals they monitor, moving the detailed optical path to SI. This schematic would then 
make clear the data that are currently present in Fig.1 as well as the overall concept presented in this 
work. 
o Another example is Fig. 3. Most of the space is devoted to the analysis of the PL signal while very little 
space is given to the final result (panel d). Although I totally understand that the authors are using a 
novel approach to analyze the signal and thus want to clarify their process to the reader, I wonder 
whether the technical details might take less space in the manuscript figure in favor of fewer, clearer 
experimental results. In this respect, the long and complex time traces of PL could go to the SI while only 
a few time profiles (currently shown as tiny sketches in Fig. 3) could be shown in the manuscript with 
much greater clarity for the reader. 
Overall, these are just suggestions. Yet, I invite the authors to think carefully how their figures could be 
improved/restructured to avoid diluting their major experimental results among the description of 
smaller technical details that could be instead reported in the supplementary information. 



Reviewer #3 (Remarks to the Author): 

The reviewed manuscript presents a comprehensive experimental analysis of light-driven nanoparticle 
growth. Specifically, the authors investigate the growth of dielectric and semiconductor shells on 
metallic nanoparti- cles induced by the localized plasmon heating. Using dark field microscopy, the 
authors are able to address and characterize this phenomenon at the single particle level, being able, at 
the same time, to temporally fol- low the shell growth. Thanks to that, the authors present very clean 
and clear results that allow them to draw solid conclusions. In my opinion, the paper is very interesting 
for the broad community of nanophotonics, timely, and well-written, and thus merits publication. That 
said, I do have a few comments and suggestions that, once addressed, I believe can help to improve the 
manuscript: 

- At the very end of page 3, the authors mention “inelastic scattering.” Although later in the paper the 
meaning of this becomes clear, I think the authors should expand a bit more on what the mean by that 
on page 3. 

- On page 8 and Supplementary S9, the authors explain that they obtain an effective thermal 
conductivity by taken the average of the water and quartz thermal conductivities. However, it is not 
clear to me that this is justified. I believe that most of the surface of the nanoparticle should be cover by 
water, furthermore, the part that is in contact with the substrate should actually be experiencing a 
contact thermal resistance that may be very different from that predicted by the bulk thermal 
conductance, as shown in recent papers [1]. I recommend the authors to elaborate more on how the 
accuracy on the estimation of the thermal conductance can impact their results. 

- On page 11, the authors claim that the change on photoluminescence can be assumed to be propor- 
tional to the change on scattering cross-section. However, does the temperature change impact these 
two quantities in the same way? 

- The authors show that the growth of the different shells is independent of the polarization of light. This 
is consistent with the fact that the temperature in the nanoparticle is rather uniform due to the high 
thermal conductance of metals. Although an isotropic growth is probably very useful in many cases, 
sometimes a non-homogeneous growth may be desired. Could the authors envision any potential 
approach leading to a non-homogenous growth? Perhaps using ultrafast illumination? 

[1] P. Zolotavin, A. Alabastri, P. Nordlander and D. Natelson, Plasmonic Heating in Au Nanowires at Low 
Temperatures: The Role of Thermal Boundary Resistance, ACS Nano, 10(7), pp. 6972-6979, (2016).