Peer review of: Sub-picosecond thermalization dynamics in condensation of strongly coupled lattice plasmons (2020)

Reviewers' comments: 
Reviewer #1 (Remarks to the Author): 

Dear editor and authors, 
 
the article ‘sub-ps thermalization dynamics in lattice plasmons’ by Väkeväinen and co -authors 
reports on studies of a plasmonic system coupled to dye molecules, w ith a focus on the 
thermalization dynamics. I think the results and the experimental technique  that allows to 
investigate extremely fast thermalization and condensation dynamics are interesting, and the 
results obtained in the thermal regime (a Boltzmann behaviour for 2 k_B T) is quite impressive . 
 
I also think that the central questions the paper tries to address are interesting, such as the 
mechanism behind the thermalisation processes and the formation of the condensate. However, 
the discussion is not very clear for the most part, and surely not suitable for the broad readership 
of nature communications. Additionally, many interesting data that help understanding the details 
are only found in the supplementary, so some restructuring of the manuscript might be in order. 
 
Let me address a few  of the points that should be explained in more detail: 
 
i) The dye molecules have an upper state lifetime of a few  nanosecond, w hich means that 
spontaneous emission can be neglected completely, and stimulated emission will only become 
relevant for highly populated modes. Correspndingly, the thermalization must b e at least partly 
driven by the polariton-polariton interaction, especially in the thermal cloud w here the population 
density is low . As the very fast dynamics of the thermalisation in itself is very interesting and I 
think it w ould help if the physical me chanisms are discussed with more detail. For example, w hat 
are estimated time scales that affect the thermalisation time? Or are the dye molecules in this 
system only relevant to shape the dispersion relation, such that propagation speed, thermalization 
time, loss rates etc. are in the correct regime ? 
 
In the same line of reasoning: The TE-mode is not confined, i.e. serves as a loss channel. If 
thermalization proceeds via the dye molecules, w hich do not discriminate between TE and TM, 
then w hy does this loss channel still allow  for a condensate? This goes along w ith the photon 
number: The condensate contains roughly 10^9 photons, w hile the pump pulse delivers (at the 
conensation threshold) roughly 10^12 photons to the sample. First, can the authors give 
estimates of the expected threshold, assuming this w ould be an equilibrium system? Second, can 
the ratio of pump to condensate photons be used to extract some information on the losses? 
 
ii) The fact that for longer pump pulses no condensate is achieved does n ot seem surprising to me: 
The existing loss mechanisms lead to a reduction of the number of polaritons in the system, and 
for pulses longer than the typical loss rate the average polariton number w ill be below the critical 
polariton number. Thus, by increa sing the pump fluence one should see a condensate again. I 
assume experimentally this is not feasible? How ever, by observing the fluence required for 
condensation for different pulse length (as is done in Fig. S10 for one fluence) one should be able 
to extract information on the loss rates in the system. At the same time, one should check if the 
number of polaritons at the condensation threshold is a constant, w hich I w ould expect for a close -
to-equilibrium system, or if there is some dependence on the external parameters. 
 
iii)  The observed thresholds seem a bit ambiguous, as they are only valid for this exact system. As 
it is already shown that changing the pump pulse duration affect the observations (lasing or 
condensation) greatly, it w ould also help if the dependence of the observed double threshold 
behaviour to other experimental parameters such as pump geometry or lattice size is discussed. 
 
iv) I am not convinced if distinguishing the stimulated thermalization regime so strongly is 
justified. From the observed energy distributions, this regime seems to be a regime of imperfect 
thermalisation prior to condensation? Or more concretely, w hat (experimental) criterion is used to 
call a spectrum thermalized? One could e.g. look at the deviation from a Boltzmann distribution 
and constrain this somehow to have a quantitative measure. 
 
v) In the previous experiments of the research group a single-mode condensate w as achieved. 
Thus, more discussion on the multimode behaviour in the condensed regime is also necessary. 
There is some information about possible explanations of this in the supporting file. How ever, the 
discussion w ill be much more clear if the simulated mode structure of the lattice is plotted beside 
the observed spectra. Also, are there any other poss ible explanations for the observed multimode 
behaviour? Why is it not simply multi-mode lasing? The definition of a multimode condensate is 
anyw ay to be taken w ith a grain of salt, as most people take macroscopic population of the ground 
state as "the condensate", thus multimode condensates in itself are not governed by this 
Definition, so some discussion is required. 
 
vi) It is interesting that by tuning the pump pulse duration and the lattice size, a spectral 
distribution that very closely matches Maxwell-Boltzmann distribution can be attained. I think the 
fact that this equilibrium distribution is achieved outside a steady state deserves more discussion, 
apart from the short discussing on page 14 and in the supplementary S5. While in a thermal 
equilibrium system the condensate is alw ays achieved, here it seems more like an interplay 
betw een losses and gain, similar to the experiments on classical condensation by e.g. Baruch 
Fischer, and thus I w ould hope for a longer discussion on the physics. Additionally, some 
comments on w hich thermodynamic quantities are expected to follow  predictions for thermal 
equilibrium in such a case apart from the spectrum w ould help . 
 
vii) The conclusions contain claims that are not supported I believe: The authors make several 
claims that hav e already been addressed for photon condensates, mostly by the Weitz group : 
-"What is the nature of the energy relaxation, how does the condensate form" -> Ref. 32 
- "What are the quantum statistical properties" -> Ref. 21 and Nature communications 7, 11340 
(2016) 
- "long-range coherence properties" -> PRL 116, 033604 (2016), Nature communications 8 (1), 
158 (2017) 
Thus, these claims are not really supported in general. Of course they are still true for the 
polariton-dye system, but not for photonic BECs per se. 
 
viii)  The abstract contains the claim "Our results give us direct access to spatiotemporal control 
and monitoring of thermalization processes...". While I agree w ith the control, w hich is here 
obtained by changing the pulse length, the "monitoring" part is to my opinion not shown in the 
paper. While for the propagating system as in previous w ork of the Törmä group a direct matching 
betw een position and time can be made, here a temporal monitoring w ould require a very 
sophisticated solution. There are streak cameras w ith 100 fs resolution available, but even this 
resolution obviously does not suffice . 
 
Thus, in general I think the results of the paper are very interesting and deserve publication. 
How ever, in the current version of the manuscript the quite general claims made are not 
supported by the data, or not explained such that the reader could easily connect the data to the 
claims. Correspondingly, for publication in nature communications major revisions are needed to 
my belief. Most importantly, a clear explanation of the thermalization process, see my point (i),  is 
required, as only then the reader can understand the interplay of the different mechanisms 
involved. 
 
Correspondingly, the paper can only be accepted after major revisio ns, or should be sent to a 
more specialized Journal after revisions are made. 
 
 

Review er #2 (Remarks to the Author): 
 
The manuscript "Sub-picosecond thermalization dynamics in condensation o f 
strongly coupled lattice plasmons" by Väkeväinen et al. demonstrates ultrafast 
thermalization dynamics of polariton lasing and condensation in a plasmonic 
nanoparticle array with strong light-matter coupling. In particular, the authors 
find three distinct regimes of light emission separated by tw o thresholds, w it h 
the first threshold corresponding to a one -dimensional lasing regime and the 
second threshold, which is only observed for short enough pulse durations, 
assigned to a two-dimensional multimode condensation regime including 
thermalization. These results are very interesting and present a novel 
phenomenon that to my know ledge has not been observed in these or similar 
systems before. The work thoroughly explores the different regimes and provides 
rich insight into the properties and dynamics of the emitted light. I thus 
wholeheartedly recommend publication in Nature Communications, provided the 
following comments are addressed: 
 
1) The authors mention that they achieve a signal that is 5 orders of magnitude 
larger than in their previous Nature Physics paper (ref. 28), which enables the 
observation of a thermal tail after condensation. How ever, it is not clear to me 
how  or why this is achieved and w hat is the crucial difference with respect t o 
the previous setup. 
 
2) It is also not fully explained why the authors refer to the regime reached 
after the first threshold as lasing and after the second as condensation - this 
seems to the rely on the observation of a thermalized tail after the second 
threshold, but the reasoning behind this should be clarified . 
 
3) The Michelson interferometer measurements seem very similar to those recently 
reported in reference 30, which also showed the stripes observed in the "1 D 
lasing" regime identified here. It would be helpful to a reader not familia r 
with the literature to mention this. Also, could further insight be provided 
into why these 1D stripes show up and full 2D coherence is not reached in this 
regime? 
 
4) The continuous redshift of the emission during the propagation implies a 
somewhat continous thermalization process, w hich seems slightly at odds w ith th e 
picture of (resonant) vibration-driven decay between states that is ofte n 
invoked in organic molecular polariton condensation. For example, this is 
identified in a very recent article (Ramezani et al, Nano Letters 2019, 
https://doi.org/10.1021/acs.nanolett.9b03139, w hich should probably be cited) a s 
the main pathway for polariton decay, also on ultrafast timescales. Can it b e 
understood w here this seeming difference between decay driven by discrete 
vibrational modes and continuous redshifting comes from? 
 
5) After the second threshold, the "condensate" peak has a multi-peak 
substructure in energy (see, e.g., Fig 3j, low est panel). This is explained in 
the supplemental (section 6) as due to an approximate degeneracy between 
different modes that is lifted for finite -sized nanoparticles. However, it did 
not become clear to me w hat these different modes correspond to, maybe this 
could be clarified? 
 
 


Review er #3 (Remarks to the Author): 
 The manuscript reports about an experimental observation of the sub-picosecond thermalization 
dynamics in the condensation formation of strongly coupled lattice plasmons. 
The high quality and the level of detail of the obtained results as w ell as their concise presentation 
justify that the manuscript is published at Nature Communications. How ever, 
prior to publication, the authors should respond to the following questions and comments : 
 
1) Is it possible to estimate the magnitude of the photon-photon interaction and to determine at 
least qualitatively how it depends upon the concentration of the dye molecules? 
 
2) Which criteria justify to choose the particular organic dye molecule IR-792? Which other dye 
solutions could, in principle, be used? 
 
3) On the one hand, at the beginning the authors mention the topic of Bose -Einstein condensation 
of photons, but then on page 7 they argue to have measured only a Maxw ell-Boltzmann 
distribution. 
Thus, the general question arises w hether the observed condensation of strongly cou pled lattice 
plasmons is a quantum or a classical effect. This question reminds one to a simila r 
situation, which occurs for the condensation of magnons, w here the original experimental 
publication 
 
Nature 443, 430 (2006) 
 
claims to have seen a Bose-Einstein condensation, but later on this w as more precisely identified 
to be just a Rayleigh-Jeans condensation in 
 
Phys. Rev. Lett. 115, 157203 (2015) 
 
4) Another question concerns symmetry arguments. From Fig. S1 the nanoparticle array is 
symmetric in x- and y-direction. On the other hand 
 
a) it is argued on page 9 that lasing exhibits confined luminescence along ky but spreads along kx 
 
b) Fig. 4 reveals that spatial coherence is asymmetric in x- and y-direction. 
 
What is the physical reason for that asymmetry? 
 
5) The authors should mention in the text the order of magnitude of the coherence length and how 
to explain at least the order of magnitude . 
 
6) On page 11 the authors mention their rate equations in Section S8 and emphasize that they are 
not sufficient for describing the condensate or lasing observations. This raises the questio n 
how  the rate equations w ould have to be extended to cover at least qualitiatively all the 
experimentally observed features. 
 
7) The authors mention on page 13 that the Kirton-Keeling dynamics in Section S9 is not sufficient 
to describe the observed quantum dynamics. And they attribute this to the high coherence of the 
thermalization 
due to the observed stimulated processes and due to strong light-matter coupling. Therefore I 
suggest that the authors apply an extension of the Kirton-Keeling dynamics to their system w hich 
takes into account 
self-consistently not only the dissipative but also the coherent dynamics : 
 
New  J. Phys. 20, 055014 (2018) 
 
8) At the end of their manuscript the authors discuss the effect of pulse duration. Here I suggest 
to make the manuscript more concise by producing and discussing a phase diagram, w here the 
pump fluence for the occurence of the 
first and second threshold are plotted versus the pump duration. Such a phase diagram w ould 
summarize w ithin one figure various experimental results, w hich are currently distributed in 
different figures.