On 2020-05-20 00:12:59, user A. Andreoni wrote:
This is definitely a really nice work, very comprehensive and providing insights from multiple points of view on a problem that has been puzzling researchers in this field for a while. Well done! I see that in the twitter feed many people are reporting: “When experiment and theory disagrees, it's not always the theory that's wrong”, and although I see where it’s coming from, I would suggest caution. I do not think that previous experiments were “wrong”: there might be the possibility that they were not interpreted correctly. And this pre-print shows, partly, why and how. On this topic, I have some commentary that I would like to share here below (apologies in advance for the length).
I understand that the article is trying to provide an accurate, unequivocal experimental response to what seem to be controversial findings from several research groups, in a field where experimental results often do not match the thermodynamic calculations on the system. It is also my understanding that, coming from the same research groups, this pre-print is trying to clarify the findings from their earlier publication, Riedel et al., 2015, Nature.<br />
The effort and amount of work presented here is impressive, and the results are quite compelling. In the big picture, this work is very important in the process of trying to solve the debate on whether diffusion is enhanced, or not during catalysis.<br />
However, what is presented here seems to somehow leave aside experimental evidence and knowledge on FCS and fluorescent dyes that were reported in the literature even before the previous paper (Riedel et al., 2015, Nature) was published. I will try to make my case here to the best of my knowledge, and I will be happy to discuss and revise any inaccuracies or anything that I might have missed and could help understanding the choices of the authors.<br />
This is the main concern that I bring forward: most of the field working on “catalysis enhanced diffusion” appears to be using Fluorescence Correlation Spectroscopy (FCS) to measure diffusion coefficients with a required accuracy that ignores the intrinsic flaws of the technique itself, which have been known for a (debatably) long number of years. Part of this concern is addressed in Gunther et al, 2018, AccChemRes, although not, in my view, to its full extent.
Is FCS accurate and precise enough for the task? My answer is: it depends on several considerations.<br />
1. Precision-wise that should be possible, as long as alignment of the setup is at its best (see: Enderlein et al, 2004, Current Pharmaceutical Biotechnologiy; Enderlein, 2005, Journal of Fluorescence) and care is taken to use high precision coverslips, properly set the correction collar of the objective, focus consistently at the same distance from the glass/buffer interface, use an appropriate combination of power and recording time, and perform well-designed controls.<br />
2. Point 1 holds if we assume that once the reaction is started (substrate is added), (almost) every single enzyme will be always caught in the act of catalysis while going through the confocal volume, however, what is most likely to happen is that only a fraction of the enzymes will be observed during catalysis and therefore with their diffusion coefficient enhanced. To analyze the data, two different scenarios might be faced:<br />
a. Try and use a two-components diffusion model to fit the data; this might work if the difference between the diffusion times/coefficients of the different species in solution is at least ~1.6-fold (see Ruttinger et al, 2010, Journal of Fluorescence; Meseth et al, 1999, <br />
Biophysical Journal)<br />
b. It could also be that only one decay will be discernible, where the time constant is the weighted average between the species involved (enzymes "caught" in catalysis and enzymes which aren’t). By increasing the substrate concentration, the contribution to the time constant of enzymes undergoing catalysis will increase and therefore the overall FCS decay will shift toward shorter times. This is what is observed in Riedel et al., 2015, Nature , as well as other similar publications investigating the same problem using the same technique.<br />
3. Point 2 would generate clean data to be analyzed in either of the two ways suggested if we were in an ideal world. That is, with an ideal fluorescent dye. However, this is (very) rarely the case, which brings me to my second main argument.
What about the photophysics of the dyes used? Fluorescent dyes are far from perfect, and even though amazing steps forward were made by organic chemists, there are still considerations to be made nevertheless. And it seemed that these were (point blank) ignored prior to the commentary of Gunther et al, 2018, AccChemRes about the use of FCS in this particular field. Here are some examples:<br />
1. Most dyes have complex photophysics occurring in the us to ms time scale (triplet states, blinking), and this has been amply and thoroughly documented since the resurgence of FCS in the modern microscopy era, and more so with the advent of super-resolution microscopy, which makes direct use of these properties in some of its implementations. Research groups that worked on this are Rigler, Schwille, Widengren, Eggeling, Tinnefeld, Sauer, Seidel, De Schryver, Hofkens, Enderlein just to name a few. Even the dye ATTO655 which seemed to be, at first, not plagued by triplet-state issues detectable in FCS, turned out not to be exempt from them, if proper conditions are not met (see Vogelsang et al, 2009, PNAS).<br />
2. The photophysics of a large number of fluorescent dyes often used in FCS experiments is affected by organic compounds in various way, especially so upon excitation to their first excited state, at which point they could be considered essentially radicals. Fluorophores are often subject to redox reactions and this has been documented (work from Rigler, Widengren, Schwille using FCS, and Tinnefeld, Sauer, among others, for single molecule super-resolution):<br />
a. An example is presented in Widengren et al, 2007, Journal of Phys Chem A, where the effect of a series of redox chemicals on the apparent diffusion time of dyes is shown. It’s worth noting that one of the chemicals, n-propyl-gallate, is chemically similar to pNPP, used in this pre-print, and in Riedel et al.<br />
b. In Vogelsang et al, 2008, Angewandte Chemie and Vogelsang et al, 2009, PNAS, ATTO dyes are investigated and it is quite clear from their findings that in one way or the other (depending on conditions) most of these dyes blink and some time-constants are provided in the papers.<br />
c. A side note: in Riedel et al, 2015, Nature, not all the substrates are potentially redox active, however there are other properties to be taken into account such as the changes in refractive index that some substrates (e.g.: urea) might cause and that will introduce artifacts that has to be corrected for (see Enderlein et al, 2005, ChemPhysChem).<br />
3. A few miscellaneous things: I was trying to find back papers where the triplet state (us region) of ATTO647N is discussed/observed in FCS but did not have any luck, however I recall using it myself for FCS measurements and it is quite clear that there is a triplet state to account for (~5-20 us region). On a different aspect, I understand that when looking at, for example Widengren et al, 2007, Journal of Phys Chem A one might argue that the changes in apparent diffusion time there work the opposite of what observed in the field of diffusion-enhanced catalysis, but it does make a point that intermolecular reactions that are not necessarily faster than diffusion do influence the observed diffusion coefficient. Furthermore, a more illustrative example might be found in Andreoni et al, 2017, Chemistry – A EurJ where redox chemicals do reduce the apparent diffusion time of a fluorescently labeled protein (Figure S6) and it is necessary to consider the redox nature of dye and reactants in order to find a physical explanation to the apparently odd phenomenon.
Provided all the considerations above, here is my last argument: data analysis. Although the focus might be on Riedel et al, 2015, Nature, I find this to be the most puzzling aspect in most of the publications that I looked at in the field of catalysis-enhance diffusion. Either because some authors do not show the data (e.g.: Muddana et al, 2010, JACS; Jee et al, 2018, PNAS; Illien et al, 2007, Nano Letters), or because when analyzing the data, it seems that the authors do not take into account the known literature on dyes photophysics and they claim that FCS data were analyzed “using a model accounting for diffusion only (Gdiff)”. Given the context, Riedel et al, 2015, Nature, probably provides for the first time a glance at how the data look like and here are some observations:<br />
1. In Figure 1 of the manuscript the data with their fit to a diffusion-only equation are presented. Although not strictly necessary to see what is going on, the residuals are also shown, and make further observations easier:<br />
a. It is clear that the residuals are not randomly distributed, and this should already raise questions. Even ignoring everything regarding the photophysical aspects of dyes during FCS experiments, there is evidence that the model does not describe the data.<br />
b. I understand that, supposedly, the diffusion time constant in FCS data might be described by the half-decay region of the curve and that is why close-ups of the plots on those areas are presented. However, this ignores completely the influence that other phenomena might have on the decay in a specific time region, and does not attempt to describe the phenomena occurring in the sample in a more comprehensive way.<br />
c. This is just a doubt: the data are presented here normalized, and I wonder if the fitting was performed on the normalized, or on the non-normalized data. Statistical weighing when fitting FCS data is very important (variance is not constant, see Wohland et al, 2001, Biophysical Journal; Saffarian, 2003, Biophysical Journal), and hopefully it was taken into account, because it would introduce bias if fitting was performed on normalized data.<br />
2. It is quite clear that to properly fit the data, addition of components to the fitting equation would have benefited the quality of the analysis, without necessarily incurring in a problem of overfitting (which I acknowledge might be an issue with FCS data). There are known and explainable physical phenomena underlying the need for multiple components (triplets, blinking, possibly multiple species?). Fitting of FCS data is indeed a controversial subject because overfitting is not uncommon, especially when not all the underlying processes are known and clearly explainable, or proper care is not take to ensure that the measuring setup is properly aligned and aberrations are minimized. However, achieving proper chi-square minimization would have cleared doubts on the reliability of the fitting:<br />
a. He et al, 2012, Analytical Chemistry provide a nice framework to use a Bayesian approach to fit the data with the statistically most likely model. Applications to “real world data” are presented in Guo et al, 2012, Analytical Chemistry and Sun et al, 2015, Analytical Chemistry<br />
b. Another possible approach would be to use the maximum entropy method proposed by Sengupta et al, 2003, Biophysical Journal, which would be very suitable here since the working hypothesis assumes distributions of diffusion times in the sample.
I know all this was long, and mainly not focused on this pre-print, but this pre-print sparks one major question: were the data, in previous publications on catalysis-enhanced diffusion, treated differently, analyzed in a more suitable way, what would they tell us?<br />
It seems to me a non-trivial oversight to go the great length of using very complex measurements (ABEL trap, SPT) to verify previous findings, without addressing the analysis of previously published results. Furthermore, a review of the FCS literature would have already raised concerns on trying to use yet again the same technique as previously (as done in Riedel et al). Methodologies to mitigate the issues (dyes photophysics, other artifacts) preventing from measuring accurate diffusion coefficients by fluctuation spectroscopy were already proposed, most of them introducing an additional “ruler” in the system: 2-focus FCS (Schwille; Enderlein), scanning-FCS (Schwille), RICS (Gratton). They are also less cumbersome to realize and less “invasive” than the ABEL trap: could, for example, the introduction of the fairly intense external electric field influence the experiments in this case?
I am glad to see that in this pre-print controls were shown, which were not provided earlier, such as the effect of substrate on the apparent diffusion of the dye and other enzymes. Focusing on this pre-print there are still few questions that would be useful if they were addressed by the authors:<br />
• In the ABEL trap experiments, did they have to use viscosity-increasing additives, such as glycerol or PEG? If so, what’s the concentration and were the same conditions used for the FCS and the SPT experiments?<br />
• In Figure 2, the authors report the Ds extracted from one single, 300s long FCS experiment and show the standard deviation calculated from there. However, it would be more meaningful to obtain an error from repeated experiments, where a new sample is used each time. This would account for reproducibility of methodological variables, such as refocusing, coverslip-to-coverslip variations and so on.<br />
• In the FCS setup description, the pinhole used is 100 um but no indication is provided regarding the total magnification of the system (objective+tube lens): how many Airy units is the pinhole?<br />
• To verify the blinking behavior, the authors used Trolox + "oxygen removal" to reverse the effect of pNPP. I am not aware of photophysical studies on JF646, thus my questions are mainly focused on ATTO647N: this dye is known to blink in the absence of oxygen, but I cannot find any information on the blinking behavior in the presence of it. Now, introduction of pNPP in solution induces blinking, is this in oxygen-free environment? Or is it in the presence of oxygen? Did the author try to use Trolox without removing oxygen? Did they quantify the TX/TQ ratio (see Cordes et al, 2009, JACS)? Since we are talking photophysics here, is pNPP likely to behave as a reducing or oxidizing agent in this case? There should be a more clear presentation of the different conditions (similar to what is done for JF646 in Figure 5) to help the reader navigate through them.<br />
• It is nice to see that Monte-Carlo simulations were performed to study the effect of blinking on diffusion. However, I have two notes here:<br />
o Without the need of simulations, it would have been possible to simply produce FCS data from an autocorrelation function containing 2 terms (Gdiff*Gblink), maybe using local gaussian noise to emulate uncertainty, and see if the introduction of Gblink (~10ms) would affect the mean diffusion time observed, and how.<br />
o I notice in Figure S8 B that the fitting of the blue curve (+3mM pNPP) is not quite following the data above 7ms: is it reasonable to suspect that’s because the data actually should be described by two components (Gdiff*Gblink)? Did the authors try to simulate different % of blinking occurring, and then tried to retrieve both the blinking and the diffusion time constant? If this worked, it would make an intriguing case for re-visiting previous data in light of these new findings.
If anyone reads this, thanks for your attention and I hope this won’t be taken too harshly, I am just trying to use this space to share my view, and open a discussion about this in a constructive way.<br />
Best of luck to the authors if they already submitted the paper for publication, and thanks for sharing this on bioRxiv!