Emergence of ion-channel mediated electrical oscillations in Escherichia coli biofilms

  1. Emmanuel U. Akabuogu
  2. Victor Martorelli
  3. Rok Krašovec
  4. Ian S. Roberts
  5. Thomas A. Waigh

  • Curated by eLife

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    This manuscript claims to have found evidence for coordinated membrane potential oscillations in E. coli biofilms that can be linked to a putative K+ channel and that may serve to enhance photo-protection. The finding of waves of membrane potential would be of interest to a wide audience from molecular biology to microbiology and physical biology. Unfortunately, a major issue with the experimental technique affects the interpretation of the observations: the dye used has been previously shown not to report membrane potential, leaving the evidence inadequate.

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Abstract

Bacterial biofilms are communities of bacteria usually attached to solid strata and often differentiated into complex structures. Communication across biofilms has been shown to involve chemical signaling and, more recently, electrical signaling in Gram positive biofilms. We report for the first time, community-level synchronized membrane potential dynamics in three-dimensional E. coli biofilms. Two hyperpolarization events are observed in response to light stress. The first requires mechanically sensitive ion channels (MscK, MscL and MscS) and the second needs the Kch-potassium channel. The channels mediated both local spiking of single E. coli biofilms and long-range coordinated electrical signaling in E. coli biofilms. The electrical phenomena are explained using Hodgkin-Huxley and 3D fire-diffuse-fire agent-based models. These data demonstrate that electrical wavefronts based on potassium ions are a mechanism by which signaling occurs in Gram negative biofilms and as such may represent a conserved mechanism for communication across biofilms.

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  1. Version published to 10.1101/2022.11.09.515771v3 on bioRxiv
  2. Version published to 10.7554/elife.92525.1 on eLife
  3. Version published to 10.7554/elife.92525 on eLife
  4. eLife

    Author Response:

    We would like to sincerely thank the referees and the editor for their time in considering our manuscript. The electrophysiology of bacteria is a fast-moving complex

    field and is proving contentious in places. We believe the peer review process of eLife provides an ideal mechanism to address the issues raised on our manuscript in an open and transparent manner. Hopefully we will encourage some more consensus in the field and help understand some of the inconsistencies in the current literature that are

    hampering progress.

    The editors stress the main issue raised was a single referee questioning the use of ThT as an indicator of membrane potential. We are well aware of the articles by the Pilizota group and we believe them to be scientifically flawed. The authors assume there are no voltage-gated ion channels in E. coli and then attempt to explain motility

    data based on a simple Nernstian battery model (they assume E. coli are unexcitable matter). This in turn leads them to conclude the membrane dye ThT is faulty, when in

    fact it is a problem with their simple battery model.

    In terms of the previous microbiology literature, the assumption of no voltage-gated ion channels in E. coli suggested by referee 2 is a highly contentious niche ideology. The majority of gene databases for E. coli have a number of ion-channels annotated as voltage sensitive due to comparative genetics studies e.g. try the https://bacteria.ensembl.org/ database (the search terms ‘voltage-gated coli’ give 2521 hits for genes, similarly you could check www.uniprot.org or www.biocyc.org) and M.M.Kuo, Y.Saimi, C.Kung, ‘Gain of function mutation indicate that E. coli Kch form a functional K + conduit in vivo’, EMBO Journal, 2003, 22, 16, 4049. Furthermore, recent microbiology reviews all agree that E. coli has a number of voltage-gated ion channels S.D.Beagle, S.W.Lockless, ‘Unappreciated roles for K + channels in bacterial physiology’,Trends in microbiology, 2021, 29, 10, 942-950. More emphatic experimental data is seen in spiking potentials that have been observed by many groups for E. coli, both directly using microelectrodes and indirectly using genetically expressed fluorophores, ‘Electrical spiking in bacterial biofilms’ E.Masi et al, Journal of the Royal Society Interface, 2015, 12, 102, ‘Electrical spiking in E. coli probed with a fluorescent voltage-indicating protein’, J.M.Kralj, et al, Science, 2011, 333, 6040, 345 and ‘Sensitive bacterial Vm sensors revealed the excitability of bacterial Vm and its role in antibiotic tolerance’, X.Jin et al, PNAS, 2023, 120, 3, e2208348120. The only mechanism currently known to cause spiking potentials in cells is due to positive feedback from voltage-gated ion channels (you need a mechanism to induce the oscillations). Indeed, people are starting to investigate the specific voltage-gated ion channels in E. coli and a role is emerging for calcium in addition to potassium e.g. ‘Genome-wide functional screen for calcium transients in E. coli identifies increased membrane potential adaptation to persistent DNA damage’, R.Luder, et al, J.Bacteriology, 2021, 203, 3, e00509.

    In terms of recent data from our own group, electrical impedance spectroscopy (EIS) experiments from E. coli indicate there are large conductivity changes associated with the Kch ion channels (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior',

    E.Akabuogu et al, ACS Nanoletters, 2024, in print). EIS experiments pr be the electrical phenomena of bacterial biofilms directly and do not depend on fluorophores i.e. they can’t be affected by ThT.

    Attempts to disprove the use of ThT to measure hyperpolarisation phenomena in E. coli using fluorescence microscopy also seem doomed to failure based on comparative control experiments. A wide range of other cationic fluorophores show similar behaviour to ThT e.g. the potassium sensitive dye used in our eLife article. Thus the behaviour of ThT appears to be generic for a range of cationic dyes and it implies a simple physical mechanism i.e. the positively charged dyes enter cells at low potentials. The elaborate photobleaching mechanism postulated by referee 2 seems most unlikely and is unable to explain our data (see below). ThT is photostable and chemically well- defined and it is therefore used almost universally in fluorescence assays for amyloids.

    A challenge with trying to use flagellar motility to measure intracellular potentials in live bacteria, as per referee 2’s many publications, is that a clutch is known to occur with E. coli e.g. ‘Flagellar brake protein YcgR interacts with motor proteins MotA and FliG to regulate the flagellar rotation speed and direction’, Q.Han et al, Frontiers in Microbiology, 2023, 14. Thus bacteria with high membrane potentials can have low motility when their clutch is engaged. This makes sense, since otherwise bacterial motility would be enslaved to their membrane potentials, greatly restricting their ability to react to their environmental conditions. Without quantifying the dynamics of the clutch (e.g. the gene circuit) it seems challenging to deduce how the motor reacts to Nernstian potentials in vivo. As a result we are not convinced by any of the Pilizota group articles. The quantitative connection between motility and membrane potential is too tenuous.

    In conclusion, the articles questioning the use of ThT are scientifically flawed and based on a niche ideology that E. coli do not contain voltage-gated ion channels. The current work disproves the simple Nernstian battery (SNB) model expounded by Pilizota et al, unpersuasively represented in multiple publications by this one group in the literature (see below for critical synopses) and demonstrates the SNB models needs to be replaced by a model that includes excitability (demonstrating hyperpolarization of the membrane potential).

    In the language of physics, a non-linear oscillator model is needed to explain spiking potentials in bacteria and the simple battery models presented by Pilizota et al do not have the required non-linearities to oscillate (‘Nonlinear dynamics and chaos’, Steve Strogatz, Westview Press, 2014). Such non-linear models are the foundation for describing eukaryotic electrophysiology, e.g. Hodgkin and Huxley’s Nobel prize winning research (1963), but also the vast majority of modern extensions (‘Mathematical physiology’, J.Keener, J.Sneyd, Springer, 2009, ‘Cellular biophysis and modelling: a primer on the computational biology of excitable cells’, G.C.Smith, 2019, CUP, ‘Dynamical systems in neuroscience: the geometry of excitability and bursting’, E.M.Izhikevich, 2006, MIT and ‘Neuronal dynamics: from single neurons to networks and models of cognition’, W.Gerstner et al, 2014, CUP). The Pilizota group is using modelling tools from the 1930s that quickly were shown to be inadequate to describe eukaryotic cellular electrophysiology and the same is true for bacterial electrophysiology (see the ground breaking work of A.Prindle et al, ‘Ion channels enable electrical communication in bacterial communities’, Nature, 2015, 527, 7576, 59 for the use of Hodgkin-Huxley models with bacterial biofilms). Below we describe a critical synopsis of the articles cited by referee 2 and we then directly answer the specific points all the

    referees raise.

    Critical synopsis of the articles cited by referee 2:

    1. ‘Generalized workflow for characterization of Nernstian dyes and their effects on bacterial physiology’, L.Mancini et al, Biophysical Journal, 2020, 118, 1, 4-14.

    This is the central article used by referee 2 to argue that there are issues with the calibration of ThT for the measurement of membrane potentials. The authors use a simple Nernstian battery (SNB) model and unfortunately it is wrong when voltage-gated ion channels occur. Huge oscillations occur in the membrane potentials of E. coli that cannot be described by the SNB model. Instead a Hodgkin Huxley model is needed, as shown in our eLife manuscript and multiple other studies (see above). Arrhenius kinetics are assumed in the SNB model for pumping with no real evidence and the generalized workflow involves ripping the flagella off the bacteria! The authors construct an elaborate ‘work flow’ to insure their ThT results can be interpreted using their erroneous SNB model over a limited range of parameters.

    1. ‘Non-equivalence of membrane voltage and ion-gradient as driving forces for the bacterial flagellar motor at low load’, C.J.Lo, et al, Biophysical Journal, 2007, 93, 1, 294.

    An odd de novo chimeric species is developed using an E. coli chassis which uses Na + instead of H + for the motility of its flagellar motor. It is not clear the relevance to wild type E. coli, due to the massive physiological perturbations involved. A SNB model is using to fit the data over a very limited parameter range with all the concomitant errors.

    1. Single-cell bacterial electrophysiology reveals mechanisms of stress-induced damage’, E.Krasnopeeva, et al, Biophysical Journal, 2019, 116, 2390.

    The abstract says ‘PMF defines the physiological state of the cell’. This statement is hyperbolic. An extremely wide range of molecules contribute to the physiological state of a cell. PMF does not even define the electrophysiology of the cell e.g. via the membrane potential. There are 0.2 M of K + compared with 0.0000001 M of H + in E. coli, so K + is arguably a million times more important for the membrane potential than H + and thus the electrophysiology! Equation (1) in the manuscript assumes no other ions are exchanged during the experiments other than H + . This is a very bad approximation when voltage-gated potassium ion channels move the majority ion (K + ) around! In our model Figure 4A is better explained by depolarisation due to K + channels closing than direct irreversible photodamage. Why does the THT fluorescence increase again for the second hyperpolarization event if the THT is supposed to be damaged? It does not make sense.

    1. ‘The proton motive force determines E. coli robustness to extracellular pH’, G.Terradot et al, 2024, preprint.

    This article expounds the SNB model once more. It still ignores the voltage-gated ion channels. Furthermore, it ignores the effect of the dominant ion in E. coli, K + . The manuscript is incorrect as a result and I would not recommend publication. In general, an important problem is being researched i.e. how the membrane potential of E. coli is related to motility, but there are serious flaws in the SNB approach and the experimental methodology appears tenuous.

    Answers to specific questions raised by the referees:

    Reviewer #1:

    Summary:
    Cell-to-cell communication is essential for higher functions in bacterial biofilms. Electrical signals have proven effective in transmitting signals across biofilms. These signals are then used to coordinate cellular metabolisms or to increase antibiotic tolerance. Here, the authors have reported for the first time coordinated oscillation of membrane potential in E. coli biofilms that may have a functional role in photoprotection.

    Strengths:
    - The authors report original data.
    - For the first time, they showed that coordinated oscillations in membrane potential occur in E. Coli biofilms.
    - The authors revealed a complex two-phase dynamic involving distinct molecular response mechanisms.
    - The authors developed two rigorous models inspired by 1) Hodgkin-Huxley model for the temporal dynamics of membrane potential and 2) Fire-Diffuse-Fire model for the propagation of the electric signal.
    - Since its discovery by comparative genomics, the Kch ion channel has not been associated with any specific phenotype in E. coli. Here, the authors proposed a functional role for the putative K+ Kch channel : enhancing survival under photo-toxic conditions.

    We thank the referee for their positive evaluations and agree with these statements.

    Weaknesses:
    - Since the flow of fresh medium is stopped at the beginning of the acquisition, environmental parameters such as pH and RedOx potential are likely to vary significantly during the experiment. It is therefore important to exclude the contributions of these variations to ensure that the electrical response is only induced by light stimulation. Unfortunately, no control experiments were carried out to address this issue.

    The electrical responses occur almost instantaneously when the stimulation with blue light begins i.e. it is too fast to be a build of pH. We are not sure what the referee means by

    Redox potential since it is an attribute of all chemicals that are able to donate/receive electrons. The electrical response to stress appears to be caused by ROS, since when ROS scavengers are added the electrical response is removed i.e. pH plays a very small minority role if any.

    - Furthermore, the control parameter of the experiment (light stimulation) is the same as that used to measure the electrical response, i.e. through fluorescence excitation. The use of the PROPS system could solve this problem.

    We were enthusiastic at the start of the project to use the PROPs system in E. coli as presented by J.M.Krajl et al,‘Electrical spiking in E. coli probed with a fluorescent voltage-indicating protein’, Science, 2011, 333, 6040, 345. However, the people we contacted in the microbiology community said that it had some technical issues and there have been no subsequent studies using PROPs in bacteria after the initial promising study. The fluorescent protein system recently presented in PNAS seems more promising, ‘Sensitive bacterial Vm sensors revealed the excitability of bacterial Vm and its role in antibiotic tolerance’, X.Jin et al, PNAS, 120, 3, e2208348120.

    - Electrical signal propagation is an important aspect of the manuscript. However, a detailed quantitative analysis of the spatial dynamics within the biofilm is lacking. In addition, it is unclear if the electrical signal propagates within the biofilm during the second peak regime, which is mediated by the Kch channel. This is an important question, given that the fire-diffuse-fire model is presented with emphasis on the role of K+ ions.

    We have presented a more detailed account of the electrical wavefront modelling work and it is currently under review in a physical journal, ‘Electrical signalling in three dimensional bacterial biofilms using an agent based fire-diffuse-fire model’, V.Martorelli, et al, 2024 https://www.biorxiv.org/content/10.1101/2023.11.17.567515v1

    - Since deletion of the kch gene inhibits the long-term electrical response to light stimulation (regime II), the authors concluded that K+ ions play a role in the habituation response. However, Kch is a putative K+ ion channel. The use of specific drugs could help to clarify the role of K+ ions.

    Our recent electrical impedance spectroscopy publication provides further evidence that Kch is associated with large changes in conductivity as expected for a voltage-gated ion channel (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior', E.Akabuogu et al, ACS Nanoletters, 2024, in print.

    - The manuscript as such does not allow us to properly conclude on the photo-protective role of the Kch ion channel.

    That Kch has a photoprotective role is our current working hypothesis. The hypothesis fits with the data, but we are not saying we have proven it beyond all possible doubt.

    - The link between membrane potential dynamics and mechanosensitivity is not captured in the equation for the Q-channel opening dynamics in the Hodgkin-Huxley model (Supp Eq 2).

    Our model is agnostic with respect to the mechanosensitivity of the ion channels, although we deduce that mechanosensitive ion channels contribute to ion channel Q.

    - Given the large number of parameters used in the models, it is hard to distinguish between prediction and fitting.

    This is always an issue with electrophysiological modelling (compared with most heart and brain modelling studies we are very conservative in the choice of parameters for the bacteria). In terms of predicting the different phenomena observed, we believe the model is very successful.

    Reviewer #2:

    Summary of what the authors were trying to achieve:
    The authors thought they studied membrane potential dynamics in E.coli biofilms. They thought so because they were unaware that the dye they used to report that membrane potential in E.coli, has been previously shown not to report it. Because of this, the interpretation of the authors' results is not accurate.

    We believe the Pilizota work is scientifically flawed.

    Major strengths and weaknesses of the methods and results:
    The strength of this work is that all the data is presented clearly, and accurately, as far as I can tell.

    The major critical weakness of this paper is the use of ThT dye as a membrane potential dye in E.coli. The work is unaware of a publication from 2020 https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] that demonstrates that ThT is not a membrane potential dye in E. coli. Therefore I think the results of this paper are misinterpreted. The same publication I reference above presents a protocol on how to carefully calibrate any candidate membrane potential dye in any given condition.

    We are aware of this study, but believe it to be scientifically flawed. We do not cite the article because we do not think it is a particularly useful contribution to the literature.

    I now go over each results section in the manuscript.

    Result section 1: Blue light triggers electrical spiking in single E. coli cells

    I do not think the title of the result section is correct for the following reasons. The above-referenced work demonstrates the loading profile one should expect from a Nernstian dye (Figure 1). It also demonstrates that ThT does not show that profile and explains why is this so. ThT only permeates the membrane under light exposure (Figure 5). This finding is consistent with blue light peroxidising the membrane (see also following work Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com] on light-induced damage to the electrochemical gradient of protons-I am sure there are more references for this).

    The Pilizota group invokes some elaborate artefacts to explain the lack of agreement with a simple Nernstian battery model. The model is incorrect not the fluorophore.

    Please note that the loading profile (only observed under light) in the current manuscript in Figure 1B as well as in the video S1 is identical to that in Figure 3 from the above-referenced paper (i.e. https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com]), and corresponding videos S3 and S4. This kind of profile is exactly what one would expect theoretically if the light is simultaneously lowering the membrane potential as the ThT is equilibrating, see Figure S12 of that previous work. There, it is also demonstrated by the means of monitoring the speed of bacterial flagellar motor that the electrochemical gradient of protons is being lowered by the light. The authors state that applying the blue light for different time periods and over different time scales did not change the peak profile. This is expected if the light is lowering the electrochemical gradient of protons. But, in Figure S1, it is clear that it affected the timing of the peak, which is again expected, because the light affects the timing of the decay, and thus of the decay profile of the electrochemical gradient of protons (Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com]).

    We think the proton effect is a million times weaker than that due to potasium i.e. 0.2 M K+ versus 10-7 M H+. We can comfortably neglect the influx of H+ in our experiments.

    If find Figure S1D interesting. There authors load TMRM, which is a membrane voltage dye that has been used extensively (as far as I am aware this is the first reference for that and it has not been cited https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1914430 [ncbi.nlm.nih.gov]/). As visible from the last TMRM reference I give, TMRM will only load the cells in Potassium Phosphate buffer with NaCl (and often we used EDTA to permeabilise the membrane). It is not fully clear (to me) whether here TMRM was prepared in rich media (it explicitly says so for ThT in Methods but not for TMRM), but it seems so. If this is the case, it likely also loads because of the damage to the membrane done with light, and therefore I am not surprised that the profiles are similar.

    The vast majority of cells continue to be viable. We do not think membrane damage is dominating.

    The authors then use CCCP. First, a small correction, as the authors state that it quenches membrane potential. CCCP is a protonophore (https://pubmed.ncbi.nlm.nih.gov/4962086 [pubmed.ncbi.nlm.nih.gov]/), so it collapses electrochemical gradient of protons. This means that it is possible, and this will depend on the type of pumps present in the cell, that CCCP collapses electrochemical gradient of protons, but the membrane potential is equal and opposite in sign to the DeltapH. So using CCCP does not automatically mean membrane potential will collapse (e.g. in some mammalian cells it does not need to be the case, but in E.coli it is https://www.biorxiv.org/content/10.1101/2021.11.19.469321v2 [biorxiv.org]). CCCP has also been recently found to be a substrate for TolC (https://journals.asm.org/doi/10.1128/mbio.00676-21 [journals.asm.org]), but at the concentrations the authors are using CCCP (100uM) that should not affect the results. However, the authors then state because they observed, in Figure S1E, a fast efflux of ions in all cells and no spiking dynamics this confirms that observed dynamics are membrane potential related. I do not agree that it does. First, Figure S1E, does not appear to show transients, instead, it is visible that after 50min treatment with 100uM CCCP, ThT dye shows no dynamics. The action of a Nernstian dye is defined. It is not sufficient that a charged molecule is affected in some way by electrical potential, this needs to be in a very specific way to be a Nernstian dye. Part of the profile of ThT loading observed in https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] is membrane potential related, but not in a way that is characteristic of Nernstian dye.

    Our understanding of the literature is CCCP poisons the whole metabolism of the bacterial cells. The ATP driven K+channels will stop functioning and this is the dominant contributor to membrane potential.

    Result section 2: Membrane potential dynamics depend on the intercellular distance

    In this chapter, the authors report that the time to reach the first intensity peak during ThT loading is different when cells are in microclusters. They interpret this as electrical signalling in clusters because the peak is reached faster in microclusters (as opposed to slower because intuitively in these clusters cells could be shielded from light). However, shielding is one possibility. The other is that the membrane has changed in composition and/or the effective light power the cells can tolerate (with mechanisms to handle light-induced damage, some of which authors mention later in the paper) is lower. Given that these cells were left in a microfluidic chamber for 2h hours to attach in growth media according to Methods, there is sufficient time for that to happen. In Figure S12 C and D of that same paper from my group (https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf [ars.els-cdn.com]) one can see the effects of peak intensity and timing of the peak on the permeability of the membrane. Therefore I do not think the distance is the explanation for what authors observe.

    Shielding would provide the reverse effect, since hyperpolarization begins in the dense centres of the biofilms. For the initial 2 hours the cells receive negligible blue light. Neither of the referee’s comments thus seem tenable.

    Result section 3: Emergence of synchronized global wavefronts in E. coli biofilms

    In this section, the authors exposed a mature biofilm to blue light. They observe that the intensity peak is reached faster in the cells in the middle. They interpret this as the ion-channel-mediated wavefronts moved from the center of the biofilm. As above, cells in the middle can have different membrane permeability to those at the periphery, and probably even more importantly, there is no light profile shown anywhere in SI/Methods. I could be wrong, but the SI3 A profile is consistent with a potential Gaussian beam profile visible in the field of view. In Methods, I find the light source for the blue light and the type of microscope but no comments on how 'flat' the illumination is across their field of view. This is critical to assess what they are observing in this result section. I do find it interesting that the ThT intensity collapsed from the edges of the biofilms. In the publication I mentioned https://www.sciencedirect.com/science/article/pii/S0006349519308793#app2 [sciencedirect.com], the collapse of fluorescence was not understood (other than it is not membrane potential related). It was observed in Figure 5A, C, and F, that at the point of peak, electrochemical gradient of protons is already collapsed, and that at the point of peak cell expands and cytoplasmic content leaks out. This means that this part of the ThT curve is not membrane potential related. The authors see that after the first peak collapsed there is a period of time where ThT does not stain the cells and then it starts again. If after the first peak the cellular content leaks, as we have observed, then staining that occurs much later could be simply staining of cytoplasmic positively charged content, and the timing of that depends on the dynamics of cytoplasmic content leakage (we observed this to be happening over 2h in individual cells). ThT is also a non-specific amyloid dye, and in starving E. coli cells formation of protein clusters has been observed (https://pubmed.ncbi.nlm.nih.gov/30472191 [pubmed.ncbi.nlm.nih.gov]/), so such cytoplasmic staining seems possible.

    It is very easy to see if the illumination is flat (Köhler illumination) by comparing the intensity of background pixels on the detector. It was flat in our case. Protons have little to do with our work for reasons highlighted before. Differential membrane permittivity is a speculative phenomenon not well supported by any evidence and with no clear molecular mechanism.

    Finally, I note that authors observe biofilms of different shapes and sizes and state that they observe similar intensity profiles, which could mean that my comment on 'flatness' of the field of view above is not a concern. However, the scale bar in Figure 2A is not legible, so I can't compare it to the variation of sizes of the biofilms in Figure 2C (67 to 280um). Based on this, I think that the illumination profile is still a concern.

    The referee now contradicts themselves and wants a scale bar to be more visible. We have changed the scale bar.

    Result section 4: Voltage-gated Kch potassium channels mediate ion-channel electrical oscillations in E. coli

    First I note at this point, given that I disagree that the data presented thus 'suggest that E. coli biofilms use electrical signaling to coordinate long-range responses to light stress' as the authors state, it gets harder to comment on the rest of the results.

    In this result section the authors look at the effect of Kch, a putative voltage-gated potassium channel, on ThT profile in E. coli cells. And they see a difference. It is worth noting that in the publication https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] it is found that ThT is also likely a substrate for TolC (Figure 4), but that scenario could not be distinguished from the one where TolC mutant has a different membrane permeability (and there is a publication that suggests the latter is happening https://onlinelibrary.wiley.com/doi/10.1111/j.1365-2958.2010.07245.x [onlinelibrary.wiley.com]). Given this, it is also possible that Kch deletion affects the membrane permeability. I do note that in video S4 I seem to see more of, what appear to be, plasmolysed cells. The authors do not see the ThT intensity with this mutant that appears long after the initial peak has disappeared, as they see in WT. It is not clear how long they waited for this, as from Figure S3C it could simply be that the dynamics of this is a lot slower, e.g. Kch deletion changes membrane permeability.

    The work that TolC provides a possible passive pathway for ThT to leave cells seems slightly niche. It just demonstrates another mechanism for the cells to equilibriate the concentrations of ThT in a Nernstian manner i.e. driven by the membrane voltage.

    The authors themselves state that the evidence for Kch being a voltage-gated channel is indirect (line 54). I do not think there is a need to claim function from a ThT profile of E. coli mutants (nor do I believe it's good practice), given how accurate single-channel recordings are currently. To know the exact dependency on the membrane potential, ion channel recordings on this protein are needed first.

    We have good evidence form electrical impedance spectroscopy experiments that Kch increases the conductivity of biofilms (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior', E.Akabuogu et al, ACS Nanoletters, 2024, in print.

    Result section 5: Blue light influences ion-channel mediated membrane potential events in E. coli

    In this chapter the authors vary the light intensity and stain the cells with PI (this dye gets into the cells when the membrane becomes very permeable), and the extracellular environment with K+ dye (I have not yet worked carefully with this dye). They find that different amounts of light influence ThT dynamics. This is in line with previous literature (both papers I have been mentioning: Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com] and https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf [ars.els-cdn.com] especially SI12), but does not add anything new. I think the results presented here can be explained with previously published theory and do not indicate that the ion-channel mediated membrane potential dynamics is a light stress relief process.

    The simple Nernstian battery model proposed by Pilizota et al is erroneous in our opinion for reasons outlined above. We believe it will prove to be a dead end for bacterial electrophysiology studies.

    Result section 6: Development of a Hodgkin-Huxley model for the observed membrane potential dynamics

    This results section starts with the authors stating: 'our data provide evidence that E. coli manages light stress through well-controlled modulation of its membrane potential dynamics'. As stated above, I think they are instead observing the process of ThT loading while the light is damaging the membrane and thus simultaneously collapsing the electrochemical gradient of protons. As stated above, this has been modelled before. And then, they observe a ThT staining that is independent from membrane potential.

    This is an erroneous niche opinion. Protons have little say in the membrane potential since there are so few of them. The membrane potential is mostly determined by K+.

    I will briefly comment on the Hodgkin Huxley (HH) based model. First, I think there is no evidence for two channels with different activation profiles as authors propose. But also, the HH model has been developed for neurons. There, the leakage and the pumping fluxes are both described by a constant representing conductivity, times the difference between the membrane potential and Nernst potential for the given ion. The conductivity in the model is given as gK*n^4 for potassium, gNa*m^3*h sodium, and gL for leakage, where gK, gNa and gL were measured experimentally for neurons. And, n, m, and h are variables that describe the experimentally observed voltage-gated mechanism of neuronal sodium and potassium channels. (Please see Hodgkin AL, Huxley AF. 1952. Currents carried by sodium and potassium ions through the membrane of the giant axon of Loligo. J. Physiol. 116:449-72 and Hodgkin AL, Huxley AF. 1952. A quantitative description of membrane current and its application to conduction and excitation in nerve. J. Physiol. 117:500-44).

    In the 70 years since Hodgkin and Huxley first presented their model, a huge number of similar models have been proposed to describe cellular electrophysiology. We are not being hyperbolic when we state that the HH models for excitable cells are like the Schrödinger equation for molecules. We carefully adapted our HH model to reflect the currently understood electrophysiology of E. coli.

    Thus, in applying the model to describe bacterial electrophysiology one should ensure near equilibrium requirement holds (so that (V-VQ) etc terms in authors' equation Figure 5 B hold), and potassium and other channels in a given bacterium have similar gating properties to those found in neurons. I am not aware of such measurements in any bacteria, and therefore think the pump leak model of the electrophysiology of bacteria needs to start with fluxes that are more general (for example Keener JP, Sneyd J. 2009. Mathematical physiology: I: Cellular physiology. New York: Springer or https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0000144 [journals.plos.org])

    The reference is to a slightly more modern version of a simple Nernstian battery model. The model will not oscillate and thus will not help modelling membrane potentials in bacteria. We are unsure where the equilibrium requirement comes from (inadequate modelling of the dynamics?)

    Result section 7: Mechanosensitive ion channels (MS) are vital for the first hyperpolarization event in E. coli.

    The results that Mcs channels affect the profile of ThT dye are interesting. It is again possible that the membrane permeability of these mutants has changed and therefore the dynamics have changed, so this needs to be checked first. I also note that our results show that the peak of ThT coincides with cell expansion. For this to be understood a model is needed that also takes into account the link between maintenance of electrochemical gradients of ions in the cell and osmotic pressure.

    The evidence for permeability changes in the membranes seems to be tenuous.

    A side note is that the authors state that the Msc responds to stress-related voltage changes. I think this is an overstatement. Mscs respond to predominantly membrane tension and are mostly nonspecific (see how their action recovers cellular volume in this publication https://www.pnas.org/doi/full/10.1073/pnas.1522185113 [pnas.org]). Authors cite references 35-39 to support this statement. These publications still state that these channels are predominantly membrane tension-gated. Some of the references state that the presence of external ions is important for tension-related gating but sometimes they gate spontaneously in the presence of certain ions. Other publications cited don't really look at gating with respect to ions (39 is on clustering). This is why I think the statement is somewhat misleading.

    We have reworded the discussion of Mscs since the literature appears to be ambiguous. We will try to run some electrical impedance spectroscopy experiments on the Msc mutants in the future to attempt to remove the ambiguity.

    Result section 8: Anomalous ion-channel-mediated wavefronts propagate light stress signals in 3D E. coli biofilms.

    I am not commenting on this result section, as it would only be applicable if ThT was membrane potential dye in E. coli.

    Ok, but we disagree on the use of ThT.

    Aims achieved/results support their conclusions:

    The authors clearly present their data. I am convinced that they have accurately presented everything they observed. However, I think their interpretation of the data and conclusions is inaccurate in line with the discussion I provided above.

    Likely impact of the work on the field, and the utility of the methods and data to the community:

    I do not think this publication should be published in its current format. It should be revised in light of the previous literature as discussed in detail above. I believe presenting it in it's current form on eLife pages would create unnecessary confusion.

    We believe many of the Pilizota group articles are scientifically flawed and are causing the confusion in the literature.

    Any other comments:

    I note, that while this work studies E. coli, it references papers in other bacteria using ThT. For example, in lines 35-36 authors state that bacteria (Bacillus subtilis in this case) in biofilms have been recently found to modulate membrane potential citing the relevant literature from 2015. It is worth noting that the most recent paper https://journals.asm.org/doi/10.1128/mbio.02220-23 [journals.asm.org] found that ThT binds to one or more proteins in the spore coat, suggesting that it does not act as a membrane potential in Bacillus spores. It is possible that it still reports membrane potential in Bacillus cells and the recent results are strictly spore-specific, but these should be kept in mind when using ThT with Bacillus.

    ThT was used successfully in previous studies of normal B. subtilis cells (by our own group and A.Prindle, ‘Spatial propagation of electrical signal in circular biofilms’, J.A.Blee et al, Physical Review E, 2019, 100, 052401, J.A.Blee et al, ‘Membrane potentials, oxidative stress and the dispersal response of bacterial biofilms to 405 nm light’, Physical Biology, 2020, 17, 2, 036001, A.Prindle et al, ‘Ion channels enable electrical communication in bacterial communities’, Nature, 2015, 527, 59-63). The connection to low metabolism pore research seems speculative.

    Reviewer #3:

    It has recently been demonstrated that bacteria in biofilms show changes in membrane potential in response to changes in their environment, and that these can propagate signals through the biofilm to coordinate bacterial behavior. Akabuogu et al. contribute to this exciting research area with a study of blue light-induced membrane potential dynamics in E. coli biofilms. They demonstrate that Thioflavin-T (ThT) intensity (a proxy for membrane potential) displays multiphasic dynamics in response to blue light treatment. They additionally use genetic manipulations to implicate the potassium channel Kch in the latter part of these dynamics. Mechanosensitive ion channels may also be involved, although these channels seem to have blue light-independent effects on membrane potential as well. In addition, there are challenges to the quantitative interpretation of ThT microscopy data which require consideration. The authors then explore whether these dynamics are involved in signaling at the community level. The authors suggest that cell firing is both more coordinated when cells are clustered and happens in waves in larger, 3D biofilms; however, in both cases evidence for these claims is incomplete. The authors present two simulations to describe the ThT data. The first of these simulations, a Hodgkin-Huxley model, indicates that the data are consistent with the activity of two ion channels with different kinetics; the Kch channel mutant, which ablates a specific portion of the response curve, is consistent with this. The second model is a fire-diffuse-fire model to describe wavefront propagation of membrane potential changes in a 3D biofilm; because the wavefront data are not presented clearly, the results of this model are difficult to interpret. Finally, the authors discuss whether these membrane potential changes could be involved in generating a protective response to blue light exposure; increased death in a Kch ion channel mutant upon blue light exposure suggests that this may be the case, but a no-light control is needed to clarify this.

    In a few instances, the paper is missing key control experiments that are important to the interpretation of the data. This makes it difficult to judge the meaning of some of the presented experiments.

    1. An additional control for the effects of autofluorescence is very important. The authors conduct an experiment where they treat cells with CCCP and see that Thioflavin-T (ThT) dynamics do not change over the course of the experiment. They suggest that this demonstrates that autofluorescence does not impact their measurements. However, cellular autofluorescence depends on the physiological state of the cell, which is impacted by CCCP treatment. A much simpler and more direct experiment would be to repeat the measurement in the absence of ThT or any other stain. This experiment should be performed both in the wild-type strain and in the ∆kch mutant.

    ThT is a very bright fluorophore (much brighter than a GFP). It is clear from the images of non-stained samples that autofluorescence provides a negligible contribution to the fluorescence intensity in an image.

    2. The effects of photobleaching should be considered. Of course, the intensity varies a lot over the course of the experiment in a way that photobleaching alone cannot explain. However, photobleaching can still contribute to the kinetics observed. Photobleaching can be assessed by changing the intensity, duration, or frequency of exposure to excitation light during the experiment. Considerations about photobleaching become particularly important when considering the effect of catalase on ThT intensity. The authors find that the decrease in ThT signal after the initial "spike" is attenuated by the addition of catalase; this is what would be predicted by catalase protecting ThT from photobleaching (indeed, catalase can be used to reduce photobleaching in time lapse imaging).

    Photobleaching was negligible over the course of the experiments. We employed techniques such as reducing sample exposure time and using the appropriate light intensity to minimize photobleaching.

    3. It would be helpful to have a baseline of membrane potential fluctuations in the absence of the proposed stimulus (in this case, blue light). Including traces of membrane potential recorded without light present would help support the claim that these changes in membrane potential represent a blue light-specific stress response, as the authors suggest. Of course, ThT is blue, so if the excitation light for ThT is problematic for this experiment the alternative dye tetramethylrhodamine methyl ester perchlorate (TMRM) can be used instead.

    Unfortunately the fluorescent baseline is too weak to measure cleanly in this experiment. It appears the collective response of all the bacteria hyperpolarization at the same time appears to dominate the signal (measurements in the eLife article and new potentiometry measurements).

    4. The effects of ThT in combination with blue light should be more carefully considered. In mitochondria, a combination of high concentrations of blue light and ThT leads to disruption of the PMF (Skates et al. 2021 BioRXiv), and similarly, ThT treatment enhances the photodynamic effects of blue light in E. coli (Bondia et al. 2021 Chemical Communications). If present in this experiment, this effect could confound the interpretation of the PMF dynamics reported in the paper.

    We think the PMF plays a minority role in determining the membrane potential in E. coli. For reasons outlined before (H+ is a minority ion in E. coli compared with K+).

    5. Figures 4D - E indicate that a ∆kch mutant has increased propidium iodide (PI) staining in the presence of blue light; this is interpreted to mean that Kch-mediated membrane potential dynamics help protect cells from blue light. However, Live/Dead staining results in these strains in the absence of blue light are not reported. This means that the possibility that the ∆kch mutant has a general decrease in survival (independent of any effects of blue light) cannot be ruled out.

    Both strains of bacterial has similar growth curve and also engaged in membrane potential dynamics for the duration of the experiment. We were interested in bacterial cells that observed membrane potential dynamics in the presence of the stress. Bacterial cells need to be alive to engage in membrane potential dynamics (hyperpolarize) under stress conditions. Cells that engaged in membrane potential dynamics and later stained red were only counted after the entire duration. We believe that the wildtype handles the light stress better than the ∆kch mutant as measured with the PI.

    6. Additionally in Figures 4D - E, the interpretation of this experiment can be confounded by the fact that PI uptake can sometimes be seen in bacterial cells with high membrane potential (Kirchhoff & Cypionka 2017 J Microbial Methods); the interpretation is that high membrane potential can lead to increased PI permeability. Because the membrane potential is largely higher throughout blue light treatment in the ∆kch mutant (Fig. 3AB), this complicates the interpretation of this experiment.

    Kirchhoff & Cypionka 2017 J Microbial Methods, using fluorescence microscopy, suggested that changes in membrane potential dynamics can introduce experimental bias when propidium iodide is used to confirm the viability of tge bacterial strains, B subtilis (DSM-10) and Dinoroseobacter shibae, that are starved of oxygen (via N2 gassing) for 2 hours. They attempted to support their findings by using CCCP in stopping the membrane potential dynamics (but never showed any pictoral or plotted data for this confirmatory experiment). In our experiment methodology, cell death was not forced on the cells by introducing an extra burden or via anoxia. We believe that the accumulation of PI in ∆kch mutant is not due to high membrane potential dynamics but is attributed to the PI, unbiasedly showing damaged/dead cells. We think that propidium iodide is good for this experiment. Propidium iodide is a dye that is extensively used in life sciences. PI has also been used in the study of bacterial electrophysiology (https://pubmed.ncbi.nlm.nih.gov/32343961/, ) and no membrane potential related bias was reported.

    Throughout the paper, many ThT intensity traces are compared, and described as "similar" or "dissimilar", without detailed discussion or a clear standard for comparison. For example, the two membrane potential curves in Fig. S1C are described as "similar" although they have very different shapes, whereas the curves in Fig. 1B and 1D are discussed in terms of their differences although they are evidently much more similar to one another. Without metrics or statistics to compare these curves, it is hard to interpret these claims. These comparative interpretations are additionally challenging because many of the figures in which average trace data are presented do not indicate standard deviation.

    Comparison of small changes in the absolute intensities is problematic in such fluorescence experiments. We mean the shape of the traces is similar and they can be modelled using a HH model with similar parameters.

    The differences between the TMRM and ThT curves that the authors show in Fig. S1C warrant further consideration. Some of the key features of the response in the ThT curve (on which much of the modeling work in the paper relies) are not very apparent in the TMRM data. It is not obvious to me which of these traces will be more representative of the actual underlying membrane potential dynamics.

    In our experiment, TMRM was used to confirm the dynamics observed using ThT. However, ThT appear to be more photostable than TMRM (especially towars the 2nd peak). The most interesting observation is that with both dyes, all phases of the membrane potential dynamics were conspicuous (the first peak, the quiescent period and the second peak). The time periods for these three episodes were also similar.

    A key claim in this paper (that dynamics of firing differ depending on whether cells are alone or in a colony) is underpinned by "time-to-first peak" analysis, but there are some challenges in interpreting these results. The authors report an average time-to-first peak of 7.34 min for the data in Figure 1B, but the average curve in Figure 1B peaks earlier than this. In Figure 1E, it appears that there are a handful of outliers in the "sparse cell" condition that likely explain this discrepancy. Either an outlier analysis should be done and the mean recomputed accordingly, or a more outlier-robust method like the median should be used instead. Then, a statistical comparison of these results will indicate whether there is a significant difference between them.

    The key point is the comparison of standard errors on the standard deviation.

    In two different 3D biofilm experiments, the authors report the propagation of wavefronts of membrane potential; I am unable to discern these wavefronts in the imaging data, and they are not clearly demonstrated by analysis.

    The first data set is presented in Figures 2A, 2B, and Video S3. The images and video are very difficult to interpret because of how the images have been scaled: the center of the biofilm is highly saturated, and the zero value has also been set too high to consistently observe the single cells surrounding the biofilm. With the images scaled this way, it is very difficult to assess dynamics. The time stamps in Video S3 and on the panels in Figure 2A also do not correspond to one another although the same biofilm is shown (and the time course in 2B is also different from what is indicated in 2B). In either case, it appears that the center of the biofilm is consistently brighter than the edges, and the intensity of all cells in the biofilm increases in tandem; by eye, propagating wavefronts (either directed toward the edge or the center) are not evident to me. Increased brightness at the center of the biofilm could be explained by increased cell thickness there (as is typical in this type of biofilm). From the image legend, it is not clear whether the image presented is a single confocal slice or a projection. Even if this is a single confocal slice, in both Video S3 and Figure 2A there are regions of "haze" from out-of-focus light evident, suggesting that light from other focal planes is nonetheless present. This seems to me to be a simpler explanation for the fluorescence dynamics observed in this experiment: cells are all following the same trajectory that corresponds to that seen for single cells, and the center is brighter because of increased biofilm thickness.

    We appreciate the reviewer for this important observation. We have made changes to the figures to address this confusion. The cell cover has no influence on the observed membrane potential dynamics. The entire biofilm was exposed to the same blue light at each time. Therefore all parts of the biofilm received equal amounts of the blue light intensity. The membrane potential dynamics was not influenced by cell density (see Fig 2C).

    The second data set is presented in Video S6B; I am similarly unable to see any wave propagation in this video. I observe only a consistent decrease in fluorescence intensity throughout the experiment that is spatially uniform (except for the bright, dynamic cells near the top; these presumably represent cells that are floating in the microfluidic and have newly arrived to the imaging region).

    A visual inspection of Video S6B shows a fast rise, a decrease in fluorescence and a second rise (supplementary figure 4B). The data for the fluorescence was carefully obtained using the imaris software. We created a curved geometry on each slice of the confocal stack. We analyzed the surfaces of this curved plane along the z-axis. This was carried out in imaris.

    3D imaging data can be difficult to interpret by eye, so it would perhaps be more helpful to demonstrate these propagating wavefronts by analysis; however, such analysis is not presented in a clear way. The legend in Figure 2B mentions a "wavefront trace", but there is no position information included - this trace instead seems to represent the average intensity trace of all cells. To demonstrate the propagation of a wavefront, this analysis should be shown for different subpopulations of cells at different positions from the center of the biofilm. Data is shown in Figure 8 that reflects the velocity of the wavefront as a function of biofilm position; however, because the wavefronts themselves are not evident in the data, it is difficult to interpret this analysis. The methods section additionally does not contain sufficient information about what these velocities represent and how they are calculated. Because of this, it is difficult for me to evaluate the section of the paper pertaining to wave propagation and the predicted biofilm critical size.

    The analysis is considered in more detail in a more expansive modelling article, currently under peer review in a physics journal, ‘Electrical signalling in three dimensional bacterial biofilms using an agent based fire-diffuse-fire model’, V.Martorelli, et al, 2024 https://www.biorxiv.org/content/10.1101/2023.11.17.567515v1

    There are some instances in the paper where claims are made that do not have data shown or are not evident in the cited data:

    1. In the first results section, "When CCCP was added, we observed a fast efflux of ions in all cells"- the data figure pertaining to this experiment is in Fig. S1E, which does not show any ion efflux. The methods section does not mention how ion efflux was measured during CCCP treatment.

    We have worded this differently to properly convey our results.

    2. In the discussion of voltage-gated calcium channels, the authors refer to "spiking events", but these are not obvious in Figure S3E. Although the fluorescence intensity changes over time, it's hard to distinguish these fluctuations from measurement noise; a no-light control could help clarify this.

    The calcium transients observed were not due to noise or artefacts.

    3. The authors state that the membrane potential dynamics simulated in Figure 7B are similar to those observed in 3D biofilms in Fig. S4B; however, the second peak is not clearly evident in Fig. S4B and it looks very different for the mature biofilm data reported in Fig. 2. I have some additional confusion about this data specifically: in the intensity trace shown in Fig. S4B, the intensity in the second frame is much higher than the first; this is not evident in Video S6B, in which the highest intensity is in the first frame at time 0. Similarly, the graph indicates that the intensity at 60 minutes is higher than the intensity at 4 minutes, but this is not the case in Fig. S4A or Video S6B.

    The confusion stated here has now been addressed. Also it should be noted that while Fig 2.1 was obtained with LED light source, Fig S4A was obtained using a laser light source. While obtaining the confocal images (for Fig S4A ), the light intensity was controlled to further minimize photobleaching. Most importantly, there is an evidence of slow rise to the 2nd peak in Fig S4B. The first peak, quiescence and slow rise to second peak are evident.

  5. eLife

    Author Response

    We would like to sincerely thank the referees and the editor for their time in considering our manuscript. The electrophysiology of bacteria is a fast-moving complex field and is proving contentious in places. We believe the peer review process of eLife provides an ideal mechanism to address the issues raised on our manuscript in an open and transparent manner. Hopefully we will encourage some more consensus in the field and help understand some of the inconsistencies in the current literature that are hampering progress.

    The editors stress the main issue raised was a single referee questioning the use of ThT as an indicator of membrane potential. We are well aware of the articles by the Pilizota group and we believe them to be scientifically flawed. The authors assume there are no voltage-gated ion channels in E. coli and then attempt to explain motility data based on a simple Nernstian battery model (they assume E. coli are unexcitable matter). This in turn leads them to conclude the membrane dye ThT is faulty, when in fact it is a problem with their simple battery model.

    In terms of the previous microbiology literature, the assumption of no voltage-gated ion channels in E. coli suggested by referee 2 is a highly contentious niche ideology. The majority of gene databases for E. coli have a number of ion-channels annotated as voltage sensitive due to comparative genetics studies e.g. try the https://bacteria.ensembl.org/ database (the search terms ‘voltage-gated coli’ give 2521 hits for genes, similarly you could check www.uniprot.org or www.biocyc.org) and M.M.Kuo, Y.Saimi, C.Kung, ‘Gain of function mutation indicate that E. coli Kch form a functional K+ conduit in vivo’, EMBO Journal, 2003, 22, 16, 4049. Furthermore, recent microbiology reviews all agree that E. coli has a number of voltage-gated ion channels S.D.Beagle, S.W.Lockless, ‘Unappreciated roles for K+ channels in bacterial physiology’, Trends in microbiology, 2021, 29, 10, 942-950. More emphatic experimental data is seen in spiking potentials that have been observed by many groups for E. coli, both directly using microelectrodes and indirectly using genetically expressed fluorophores, ‘Electrical spiking in bacterial biofilms’ E.Masi et al, Journal of the Royal Society Interface, 2015, 12, 102, ‘Electrical spiking in E. coli probed with a fluorescent voltage-indicating protein’, J.M.Kralj, et al, Science, 2011, 333, 6040, 345 and ‘Sensitive bacterial Vm sensors revealed the excitability of bacterial Vm and its role in antibiotic tolerance’, X.Jin et al, PNAS, 2023, 120, 3, e2208348120. The only mechanism currently known to cause spiking potentials in cells is due to positive feedback from voltage-gated ion channels (you need a mechanism to induce the oscillations). Indeed, people are starting to investigate the specific voltage-gated ion channels in E. coli and a role is emerging for calcium in addition to potassium e.g. ‘Genome-wide functional screen for calcium transients in E. coli identifies increased membrane potential adaptation to persistent DNA damage’, R.Luder, et al, J.Bacteriology, 2021, 203, 3, e00509.

    In terms of recent data from our own group, electrical impedance spectroscopy (EIS) experiments from E. coli indicate there are large conductivity changes associated with the Kch ion channels (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior', E.Akabuogu et al, ACS Nanoletters, 2024, in print). EIS experiments probe the electrical phenomena of bacterial biofilms directly and do not depend on fluorophores i.e. they can’t be affected by ThT.

    Attempts to disprove the use of ThT to measure hyperpolarisation phenomena in E. coli using fluorescence microscopy also seem doomed to failure based on comparative control experiments. A wide range of other cationic fluorophores show similar behaviour to ThT e.g. the potassium sensitive dye used in our eLife article. Thus the behaviour of ThT appears to be generic for a range of cationic dyes and it implies a simple physical mechanism i.e. the positively charged dyes enter cells at low potentials. The elaborate photobleaching mechanism postulated by referee 2 seems most unlikely and is unable to explain our data (see below). ThT is photostable and chemically well-defined and it is therefore used almost universally in fluorescence assays for amyloids.

    A challenge with trying to use flagellar motility to measure intracellular potentials in live bacteria, as per referee 2’s many publications, is that a clutch is known to occur with E. coli e.g. ‘Flagellar brake protein YcgR interacts with motor proteins MotA and FliG to regulate the flagellar rotation speed and direction’, Q.Han et al, Frontiers in Microbiology, 2023, 14. Thus bacteria with high membrane potentials can have low motility when their clutch is engaged. This makes sense, since otherwise bacterial motility would be enslaved to their membrane potentials, greatly restricting their ability to react to their environmental conditions. Without quantifying the dynamics of the clutch (e.g. the gene circuit) it seems challenging to deduce how the motor reacts to Nernstian potentials in vivo. As a result we are not convinced by any of the Pilizota group articles. The quantitative connection between motility and membrane potential is too tenuous.

    In conclusion, the articles questioning the use of ThT are scientifically flawed and based on a niche ideology that E. coli do not contain voltage-gated ion channels. The current work disproves the simple Nernstian battery (SNB) model expounded by Pilizota et al, unpersuasively represented in multiple publications by this one group in the literature (see below for critical synopses) and demonstrates the SNB models needs to be replaced by a model that includes excitability (demonstrating hyperpolarization of the membrane potential).

    In the language of physics, a non-linear oscillator model is needed to explain spiking potentials in bacteria and the simple battery models presented by Pilizota et al do not have the required non-linearities to oscillate (‘Nonlinear dynamics and chaos’, Steve Strogatz, Westview Press, 2014). Such non-linear models are the foundation for describing eukaryotic electrophysiology, e.g. Hodgkin and Huxley’s Nobel prize winning research (1963), but also the vast majority of modern extensions (‘Mathematical physiology’, J.Keener, J.Sneyd, Springer, 2009, ‘Cellular biophysics and modelling: a primer on the computational biology of excitable cells’, G.C.Smith, 2019, CUP, ‘Dynamical systems in neuroscience: the geometry of excitability and bursting’, E.M.Izhikevich, 2006, MIT and ‘Neuronal dynamics: from single neurons to networks and models of cognition’, W.Gerstner et al, 2014, CUP). The Pilizota group is using modelling tools from the 1930s that quickly were shown to be inadequate to describe eukaryotic cellular electrophysiology and the same is true for bacterial electrophysiology (see the ground breaking work of A.Prindle et al, ‘Ion channels enable electrical communication in bacterial communities’, Nature, 2015, 527, 7576, 59 for the use of Hodgkin-Huxley models with bacterial biofilms). Below we describe a critical synopsis of the articles cited by referee 2 and we then directly answer the specific points all the referees raise.

    Critical synopsis of the articles cited by referee 2:

    (1) ‘Generalized workflow for characterization of Nernstian dyes and their effects on bacterial physiology’, L.Mancini et al, Biophysical Journal, 2020, 118, 1, 4-14.

    This is the central article used by referee 2 to argue that there are issues with the calibration of ThT for the measurement of membrane potentials. The authors use a simple Nernstian battery (SNB) model and unfortunately it is wrong when voltage-gated ion channels occur. Huge oscillations occur in the membrane potentials of E. coli that cannot be described by the SNB model. Instead a Hodgkin Huxley model is needed, as shown in our eLife manuscript and multiple other studies (see above). Arrhenius kinetics are assumed in the SNB model for pumping with no real evidence and the generalized workflow involves ripping the flagella off the bacteria! The authors construct an elaborate ‘work flow’ to insure their ThT results can be interpreted using their erroneous SNB model over a limited range of parameters.

    (2) ‘Non-equivalence of membrane voltage and ion-gradient as driving forces for the bacterial flagellar motor at low load’, C.J.Lo, et al, Biophysical Journal, 2007, 93, 1, 294.

    An odd de novo chimeric species is developed using an E. coli chassis which uses Na+ instead of H+ for the motility of its flagellar motor. It is not clear the relevance to wild type E. coli, due to the massive physiological perturbations involved. A SNB model is using to fit the data over a very limited parameter range with all the concomitant errors.

    (3) Single-cell bacterial electrophysiology reveals mechanisms of stress-induced damage’, E.Krasnopeeva, et al, Biophysical Journal, 2019, 116, 2390.

    The abstract says ‘PMF defines the physiological state of the cell’. This statement is hyperbolic. An extremely wide range of molecules contribute to the physiological state of a cell. PMF does not even define the electrophysiology of the cell e.g. via the membrane potential. There are 0.2 M of K+ compared with 0.0000001 M of H+ in E. coli, so K+ is arguably a million times more important for the membrane potential than H+ and thus the electrophysiology!

    Equation (1) in the manuscript assumes no other ions are exchanged during the experiments other than H+. This is a very bad approximation when voltage-gated potassium ion channels move the majority ion (K+) around!

    In our model Figure 4A is better explained by depolarisation due to K+ channels closing than direct irreversible photodamage. Why does the THT fluorescence increase again for the second hyperpolarization event if the THT is supposed to be damaged? It does not make sense.

    (4) ‘The proton motive force determines E. coli robustness to extracellular pH’, G.Terradot et al, 2024, preprint.

    This article expounds the SNB model once more. It still ignores the voltage-gated ion channels. Furthermore, it ignores the effect of the dominant ion in E. coli, K+. The manuscript is incorrect as a result and I would not recommend publication. In general, an important problem is being researched i.e. how the membrane potential of E. coli is related to motility, but there are serious flaws in the SNB approach and the experimental methodology appears tenuous.

    Answers to specific questions raised by the referees

    Reviewer #1 (Public Review):

    Summary: Cell-to-cell communication is essential for higher functions in bacterial biofilms. Electrical signals have proven effective in transmitting signals across biofilms. These signals are then used to coordinate cellular metabolisms or to increase antibiotic tolerance. Here, the authors have reported for the first time coordinated oscillation of membrane potential in E. coli biofilms that may have a functional role in photoprotection.

    Strengths:

    • The authors report original data.
    • For the first time, they showed that coordinated oscillations in membrane potential occur in E. Coli biofilms.
    • The authors revealed a complex two-phase dynamic involving distinct molecular response mechanisms.
    • The authors developed two rigorous models inspired by 1) Hodgkin-Huxley model for the temporal dynamics of membrane potential and 2) Fire-Diffuse-Fire model for the propagation of the electric signal.
    • Since its discovery by comparative genomics, the Kch ion channel has not been associated with any specific phenotype in E. coli. Here, the authors proposed a functional role for the putative K+ Kch channel : enhancing survival under photo-toxic conditions.

    We thank the referee for their positive evaluations and agree with these statements.

    Weaknesses:

    • Since the flow of fresh medium is stopped at the beginning of the acquisition, environmental parameters such as pH and RedOx potential are likely to vary significantly during the experiment. It is therefore important to exclude the contributions of these variations to ensure that the electrical response is only induced by light stimulation. Unfortunately, no control experiments were carried out to address this issue.

    The electrical responses occur almost instantaneously when the stimulation with blue light begins i.e. it is too fast to be a build of pH. We are not sure what the referee means by Redox potential since it is an attribute of all chemicals that are able to donate/receive electrons. The electrical response to stress appears to be caused by ROS, since when ROS scavengers are added the electrical response is removed i.e. pH plays a very small minority role if any.

    • Furthermore, the control parameter of the experiment (light stimulation) is the same as that used to measure the electrical response, i.e. through fluorescence excitation. The use of the PROPS system could solve this problem.

    We were enthusiastic at the start of the project to use the PROPs system in E. coli as presented by J.M.Krajl et al, ‘Electrical spiking in E. coli probed with a fluorescent voltage-indicating protein’, Science, 2011, 333, 6040, 345. However, the people we contacted in the microbiology community said that it had some technical issues and there have been no subsequent studies using PROPs in bacteria after the initial promising study. The fluorescent protein system recently presented in PNAS seems more promising, ‘Sensitive bacterial Vm sensors revealed the excitability of bacterial Vm and its role in antibiotic tolerance’, X.Jin et al, PNAS, 120, 3, e2208348120.

    Electrical signal propagation is an important aspect of the manuscript. However, a detailed >quantitative analysis of the spatial dynamics within the biofilm is lacking. In addition, it is unclear if the electrical signal propagates within the biofilm during the second peak regime, which is mediated by the Kch channel. This is an important question, given that the fire-diffuse-fire model is presented with emphasis on the role of K+ ions.

    We have presented a more detailed account of the electrical wavefront modelling work and it is currently under review in a physical journal, ‘Electrical signalling in three dimensional bacterial biofilms using an agent based fire-diffuse-fire model’, V.Martorelli, et al, 2024 https://www.biorxiv.org/content/10.1101/2023.11.17.567515v1

    • Since deletion of the kch gene inhibits the long-term electrical response to light stimulation (regime II), the authors concluded that K+ ions play a role in the habituation response. However, Kch is a putative K+ ion channel. The use of specific drugs could help to clarify the role of K+ ions.

    Our recent electrical impedance spectroscopy publication provides further evidence that Kch is associated with large changes in conductivity as expected for a voltage-gated ion channel (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior', E.Akabuogu et al, ACS Nanoletters, 2024, in print.

    • The manuscript as such does not allow us to properly conclude on the photo-protective role of the Kch ion channel.

    That Kch has a photoprotective role is our current working hypothesis. The hypothesis fits with the data, but we are not saying we have proven it beyond all possible doubt.

    • The link between membrane potential dynamics and mechanosensitivity is not captured in the equation for the Q-channel opening dynamics in the Hodgkin-Huxley model (Supp Eq 2).

    Our model is agnostic with respect to the mechanosensitivity of the ion channels, although we deduce that mechanosensitive ion channels contribute to ion channel Q.

    • Given the large number of parameters used in the models, it is hard to distinguish between prediction and fitting.

    This is always an issue with electrophysiological modelling (compared with most heart and brain modelling studies we are very conservative in the choice of parameters for the bacteria). In terms of predicting the different phenomena observed, we believe the model is very successful.

    Reviewer #2 (Public Review):

    Summary of what the authors were trying to achieve:

    The authors thought they studied membrane potential dynamics in E.coli biofilms. They thought so because they were unaware that the dye they used to report that membrane potential in E.coli, has been previously shown not to report it. Because of this, the interpretation of the authors' results is not accurate.

    We believe the Pilizota work is scientifically flawed.

    Major strengths and weaknesses of the methods and results:

    The strength of this work is that all the data is presented clearly, and accurately, as far as I can tell.

    The major critical weakness of this paper is the use of ThT dye as a membrane potential dye in E.coli. The work is unaware of a publication from 2020 https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] that demonstrates that ThT is not a membrane potential dye in E. coli. Therefore I think the results of this paper are misinterpreted. The same publication I reference above presents a protocol on how to carefully calibrate any candidate membrane potential dye in any given condition.

    We are aware of this study, but believe it to be scientifically flawed. We do not cite the article because we do not think it is a particularly useful contribution to the literature.

    I now go over each results section in the manuscript.

    Result section 1: Blue light triggers electrical spiking in single E. coli cells

    I do not think the title of the result section is correct for the following reasons. The above-referenced work demonstrates the loading profile one should expect from a Nernstian dye (Figure 1). It also demonstrates that ThT does not show that profile and explains why is this so. ThT only permeates the membrane under light exposure (Figure 5). This finding is consistent with blue light peroxidising the membrane (see also following work Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com] on light-induced damage to the electrochemical gradient of protons-I am sure there are more references for this).

    The Pilizota group invokes some elaborate artefacts to explain the lack of agreement with a simple Nernstian battery model. The model is incorrect not the fluorophore.

    Please note that the loading profile (only observed under light) in the current manuscript in Figure 1B as well as in the video S1 is identical to that in Figure 3 from the above-referenced paper (i.e. https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com]), and corresponding videos S3 and S4. This kind of profile is exactly what one would expect theoretically if the light is simultaneously lowering the membrane potential as the ThT is equilibrating, see Figure S12 of that previous work. There, it is also demonstrated by the means of monitoring the speed of bacterial flagellar motor that the electrochemical gradient of protons is being lowered by the light. The authors state that applying the blue light for different time periods and over different time scales did not change the peak profile. This is expected if the light is lowering the electrochemical gradient of protons. But, in Figure S1, it is clear that it affected the timing of the peak, which is again expected, because the light affects the timing of the decay, and thus of the decay profile of the electrochemical gradient of protons (Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com]).

    We think the proton effect is a million times weaker than that due to potasium i.e. 0.2 M K+ versus 10-7 M H+. We can comfortably neglect the influx of H+ in our experiments.

    If find Figure S1D interesting. There authors load TMRM, which is a membrane voltage dye that has been used extensively (as far as I am aware this is the first reference for that and it has not been cited https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1914430 [ncbi.nlm.nih.gov]/). As visible from the last TMRM reference I give, TMRM will only load the cells in Potassium Phosphate buffer with NaCl (and often we used EDTA to permeabilise the membrane). It is not fully clear (to me) whether here TMRM was prepared in rich media (it explicitly says so for ThT in Methods but not for TMRM), but it seems so. If this is the case, it likely also loads because of the damage to the membrane done with light, and therefore I am not surprised that the profiles are similar.

    The vast majority of cells continue to be viable. We do not think membrane damage is dominating.

    The authors then use CCCP. First, a small correction, as the authors state that it quenches membrane potential. CCCP is a protonophore (https://pubmed.ncbi.nlm.nih.gov/4962086 [pubmed.ncbi.nlm.nih.gov]/), so it collapses electrochemical gradient of protons. This means that it is possible, and this will depend on the type of pumps present in the cell, that CCCP collapses electrochemical gradient of protons, but the membrane potential is equal and opposite in sign to the DeltapH. So using CCCP does not automatically mean membrane potential will collapse (e.g. in some mammalian cells it does not need to be the case, but in E.coli it is https://www.biorxiv.org/content/10.1101/2021.11.19.469321v2 [biorxiv.org]). CCCP has also been recently found to be a substrate for TolC (https://journals.asm.org/doi/10.1128/mbio.00676-21 [journals.asm.org]), but at the concentrations the authors are using CCCP (100uM) that should not affect the results. However, the authors then state because they observed, in Figure S1E, a fast efflux of ions in all cells and no spiking dynamics this confirms that observed dynamics are membrane potential related. I do not agree that it does. First, Figure S1E, does not appear to show transients, instead, it is visible that after 50min treatment with 100uM CCCP, ThT dye shows no dynamics. The action of a Nernstian dye is defined. It is not sufficient that a charged molecule is affected in some way by electrical potential, this needs to be in a very specific way to be a Nernstian dye. Part of the profile of ThT loading observed in https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] is membrane potential related, but not in a way that is characteristic of Nernstian dye.

    Our understanding of the literature is CCCP poisons the whole metabolism of the bacterial cells. The ATP driven K+ channels will stop functioning and this is the dominant contributor to membrane potential.

    Result section 2: Membrane potential dynamics depend on the intercellular distance

    In this chapter, the authors report that the time to reach the first intensity peak during ThT loading is different when cells are in microclusters. They interpret this as electrical signalling in clusters because the peak is reached faster in microclusters (as opposed to slower because intuitively in these clusters cells could be shielded from light). However, shielding is one possibility. The other is that the membrane has changed in composition and/or the effective light power the cells can tolerate (with mechanisms to handle light-induced damage, some of which authors mention later in the paper) is lower. Given that these cells were left in a microfluidic chamber for 2h hours to attach in growth media according to Methods, there is sufficient time for that to happen. In Figure S12 C and D of that same paper from my group (https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf [ars.els-cdn.com]) one can see the effects of peak intensity and timing of the peak on the permeability of the membrane. Therefore I do not think the distance is the explanation for what authors observe.

    Shielding would provide the reverse effect, since hyperpolarization begins in the dense centres of the biofilms. For the initial 2 hours the cells receive negligible blue light. Neither of the referee’s comments thus seem tenable.

    Result section 3: Emergence of synchronized global wavefronts in E. coli biofilms

    In this section, the authors exposed a mature biofilm to blue light. They observe that the intensity peak is reached faster in the cells in the middle. They interpret this as the ion-channel-mediated wavefronts moved from the center of the biofilm. As above, cells in the middle can have different membrane permeability to those at the periphery, and probably even more importantly, there is no light profile shown anywhere in SI/Methods. I could be wrong, but the SI3 A profile is consistent with a potential Gaussian beam profile visible in the field of view. In Methods, I find the light source for the blue light and the type of microscope but no comments on how 'flat' the illumination is across their field of view. This is critical to assess what they are observing in this result section. I do find it interesting that the ThT intensity collapsed from the edges of the biofilms. In the publication I mentioned https://www.sciencedirect.com/science/article/pii/S0006349519308793#app2 [sciencedirect.com], the collapse of fluorescence was not understood (other than it is not membrane potential related). It was observed in Figure 5A, C, and F, that at the point of peak, electrochemical gradient of protons is already collapsed, and that at the point of peak cell expands and cytoplasmic content leaks out. This means that this part of the ThT curve is not membrane potential related. The authors see that after the first peak collapsed there is a period of time where ThT does not stain the cells and then it starts again. If after the first peak the cellular content leaks, as we have observed, then staining that occurs much later could be simply staining of cytoplasmic positively charged content, and the timing of that depends on the dynamics of cytoplasmic content leakage (we observed this to be happening over 2h in individual cells). ThT is also a non-specific amyloid dye, and in starving E. coli cells formation of protein clusters has been observed (https://pubmed.ncbi.nlm.nih.gov/30472191 [pubmed.ncbi.nlm.nih.gov]/), so such cytoplasmic staining seems possible.

    It is very easy to see if the illumination is flat (Köhler illumination) by comparing the intensity of background pixels on the detector. It was flat in our case. Protons have little to do with our work for reasons highlighted before. Differential membrane permittivity is a speculative phenomenon not well supported by any evidence and with no clear molecular mechanism.

    Finally, I note that authors observe biofilms of different shapes and sizes and state that they observe similar intensity profiles, which could mean that my comment on 'flatness' of the field of view above is not a concern. However, the scale bar in Figure 2A is not legible, so I can't compare it to the variation of sizes of the biofilms in Figure 2C (67 to 280um). Based on this, I think that the illumination profile is still a concern.

    The referee now contradicts themselves and wants a scale bar to be more visible. We have changed the scale bar.

    Result section 4: Voltage-gated Kch potassium channels mediate ion-channel electrical oscillations in E. coli

    First I note at this point, given that I disagree that the data presented thus 'suggest that E. coli biofilms use electrical signaling to coordinate long-range responses to light stress' as the authors state, it gets harder to comment on the rest of the results.

    In this result section the authors look at the effect of Kch, a putative voltage-gated potassium channel, on ThT profile in E. coli cells. And they see a difference. It is worth noting that in the publication https://www.sciencedirect.com/science/article/pii/S0006349519308793 [sciencedirect.com] it is found that ThT is also likely a substrate for TolC (Figure 4), but that scenario could not be distinguished from the one where TolC mutant has a different membrane permeability (and there is a publication that suggests the latter is happening https://onlinelibrary.wiley.com/doi/10.1111/j.1365-2958.2010.07245.x [onlinelibrary.wiley.com]). Given this, it is also possible that Kch deletion affects the membrane permeability. I do note that in video S4 I seem to see more of, what appear to be, plasmolysed cells. The authors do not see the ThT intensity with this mutant that appears long after the initial peak has disappeared, as they see in WT. It is not clear how long they waited for this, as from Figure S3C it could simply be that the dynamics of this is a lot slower, e.g. Kch deletion changes membrane permeability.

    The work that TolC provides a possible passive pathway for ThT to leave cells seems slightly niche. It just demonstrates another mechanism for the cells to equilibriate the concentrations of ThT in a Nernstian manner i.e. driven by the membrane voltage.

    The authors themselves state that the evidence for Kch being a voltage-gated channel is indirect (line 54). I do not think there is a need to claim function from a ThT profile of E. coli mutants (nor do I believe it's good practice), given how accurate single-channel recordings are currently. To know the exact dependency on the membrane potential, ion channel recordings on this protein are needed first.

    We have good evidence form electrical impedance spectroscopy experiments that Kch increases the conductivity of biofilms (https://pubs.acs.org/doi/10.1021/acs.nanolett.3c04446, 'Electrical impedance spectroscopy with bacterial biofilms: neuronal-like behavior', E.Akabuogu et al, ACS Nanoletters, 2024, in print.

    Result section 5: Blue light influences ion-channel mediated membrane potential events in E. coli

    In this chapter the authors vary the light intensity and stain the cells with PI (this dye gets into the cells when the membrane becomes very permeable), and the extracellular environment with K+ dye (I have not yet worked carefully with this dye). They find that different amounts of light influence ThT dynamics. This is in line with previous literature (both papers I have been mentioning: Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 [sciencedirect.com] and https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf [ars.els-cdn.com] especially SI12), but does not add anything new. I think the results presented here can be explained with previously published theory and do not indicate that the ion-channel mediated membrane potential dynamics is a light stress relief process.

    The simple Nernstian battery model proposed by Pilizota et al is erroneous in our opinion for reasons outlined above. We believe it will prove to be a dead end for bacterial electrophysiology studies.

    Result section 6: Development of a Hodgkin-Huxley model for the observed membrane potential dynamics

    This results section starts with the authors stating: 'our data provide evidence that E. coli manages light stress through well-controlled modulation of its membrane potential dynamics'. As stated above, I think they are instead observing the process of ThT loading while the light is damaging the membrane and thus simultaneously collapsing the electrochemical gradient of protons. As stated above, this has been modelled before. And then, they observe a ThT staining that is independent from membrane potential.

    This is an erroneous niche opinion. Protons have little say in the membrane potential since there are so few of them. The membrane potential is mostly determined by K+.

    I will briefly comment on the Hodgkin Huxley (HH) based model. First, I think there is no evidence for two channels with different activation profiles as authors propose. But also, the HH model has been developed for neurons. There, the leakage and the pumping fluxes are both described by a constant representing conductivity, times the difference between the membrane potential and Nernst potential for the given ion. The conductivity in the model is given as gKn^4 for potassium, gNam^3*h sodium, and gL for leakage, where gK, gNa and gL were measured experimentally for neurons. And, n, m, and h are variables that describe the experimentally observed voltage-gated mechanism of neuronal sodium and potassium channels. (Please see Hodgkin AL, Huxley AF. 1952. Currents carried by sodium and potassium ions through the membrane of the giant axon of Loligo. J. Physiol. 116:449-72 and Hodgkin AL, Huxley AF. 1952. A quantitative description of membrane current and its application to conduction and excitation in nerve. J. Physiol. 117:500-44).

    In the 70 years since Hodgkin and Huxley first presented their model, a huge number of similar models have been proposed to describe cellular electrophysiology. We are not being hyperbolic when we state that the HH models for excitable cells are like the Schrödinger equation for molecules. We carefully adapted our HH model to reflect the currently understood electrophysiology of E. coli.

    Thus, in applying the model to describe bacterial electrophysiology one should ensure near equilibrium requirement holds (so that (V-VQ) etc terms in authors' equation Figure 5 B hold), and potassium and other channels in a given bacterium have similar gating properties to those found in neurons. I am not aware of such measurements in any bacteria, and therefore think the pump leak model of the electrophysiology of bacteria needs to start with fluxes that are more general (for example Keener JP, Sneyd J. 2009. Mathematical physiology: I: Cellular physiology. New York: Springer or https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0000144 [journals.plos.org])

    The reference is to a slightly more modern version of a simple Nernstian battery model. The model will not oscillate and thus will not help modelling membrane potentials in bacteria. We are unsure where the equilibrium requirement comes from (inadequate modelling of the dynamics?)

    Result section 7: Mechanosensitive ion channels (MS) are vital for the first hyperpolarization event in E. coli.

    The results that Mcs channels affect the profile of ThT dye are interesting. It is again possible that the membrane permeability of these mutants has changed and therefore the dynamics have changed, so this needs to be checked first. I also note that our results show that the peak of ThT coincides with cell expansion. For this to be understood a model is needed that also takes into account the link between maintenance of electrochemical gradients of ions in the cell and osmotic pressure.

    The evidence for permeability changes in the membranes seems to be tenuous.

    A side note is that the authors state that the Msc responds to stress-related voltage changes. I think this is an overstatement. Mscs respond to predominantly membrane tension and are mostly nonspecific (see how their action recovers cellular volume in this publication https://www.pnas.org/doi/full/10.1073/pnas.1522185113 [pnas.org]). Authors cite references 35-39 to support this statement. These publications still state that these channels are predominantly membrane tension-gated. Some of the references state that the presence of external ions is important for tension-related gating but sometimes they gate spontaneously in the presence of certain ions. Other publications cited don't really look at gating with respect to ions (39 is on clustering). This is why I think the statement is somewhat misleading.

    We have reworded the discussion of Mscs since the literature appears to be ambiguous. We will try to run some electrical impedance spectroscopy experiments on the Msc mutants in the future to attempt to remove the ambiguity.

    Result section 8: Anomalous ion-channel-mediated wavefronts propagate light stress signals in 3D E. coli biofilms.

    I am not commenting on this result section, as it would only be applicable if ThT was membrane potential dye in E. coli.

    Ok, but we disagree on the use of ThT.

    Aims achieved/results support their conclusions:

    The authors clearly present their data. I am convinced that they have accurately presented everything they observed. However, I think their interpretation of the data and conclusions is inaccurate in line with the discussion I provided above.

    Likely impact of the work on the field, and the utility of the methods and data to the community:

    I do not think this publication should be published in its current format. It should be revised in light of the previous literature as discussed in detail above. I believe presenting it in it's current form on eLife pages would create unnecessary confusion.

    We believe many of the Pilizota group articles are scientifically flawed and are causing the confusion in the literature.

    Any other comments:

    I note, that while this work studies E. coli, it references papers in other bacteria using ThT. For example, in lines 35-36 authors state that bacteria (Bacillus subtilis in this case) in biofilms have been recently found to modulate membrane potential citing the relevant literature from 2015. It is worth noting that the most recent paper https://journals.asm.org/doi/10.1128/mbio.02220-23 [journals.asm.org] found that ThT binds to one or more proteins in the spore coat, suggesting that it does not act as a membrane potential in Bacillus spores. It is possible that it still reports membrane potential in Bacillus cells and the recent results are strictly spore-specific, but these should be kept in mind when using ThT with Bacillus.

    ThT was used successfully in previous studies of normal B. subtilis cells (by our own group and A.Prindle, ‘Spatial propagation of electrical signal in circular biofilms’, J.A.Blee et al, Physical Review E, 2019, 100, 052401, J.A.Blee et al, ‘Membrane potentials, oxidative stress and the dispersal response of bacterial biofilms to 405 nm light’, Physical Biology, 2020, 17, 2, 036001, A.Prindle et al, ‘Ion channels enable electrical communication in bacterial communities’, Nature, 2015, 527, 59-63). The connection to low metabolism pore research seems speculative.

    Reviewer #3 (Public Review):

    It has recently been demonstrated that bacteria in biofilms show changes in membrane potential in response to changes in their environment, and that these can propagate signals through the biofilm to coordinate bacterial behavior. Akabuogu et al. contribute to this exciting research area with a study of blue light-induced membrane potential dynamics in E. coli biofilms. They demonstrate that Thioflavin-T (ThT) intensity (a proxy for membrane potential) displays multiphasic dynamics in response to blue light treatment. They additionally use genetic manipulations to implicate the potassium channel Kch in the latter part of these dynamics. Mechanosensitive ion channels may also be involved, although these channels seem to have blue light-independent effects on membrane potential as well. In addition, there are challenges to the quantitative interpretation of ThT microscopy data which require consideration. The authors then explore whether these dynamics are involved in signaling at the community level. The authors suggest that cell firing is both more coordinated when cells are clustered and happens in waves in larger, 3D biofilms; however, in both cases evidence for these claims is incomplete. The authors present two simulations to describe the ThT data. The first of these simulations, a Hodgkin-Huxley model, indicates that the data are consistent with the activity of two ion channels with different kinetics; the Kch channel mutant, which ablates a specific portion of the response curve, is consistent with this. The second model is a fire-diffuse-fire model to describe wavefront propagation of membrane potential changes in a 3D biofilm; because the wavefront data are not presented clearly, the results of this model are difficult to interpret. Finally, the authors discuss whether these membrane potential changes could be involved in generating a protective response to blue light exposure; increased death in a Kch ion channel mutant upon blue light exposure suggests that this may be the case, but a no-light control is needed to clarify this.

    In a few instances, the paper is missing key control experiments that are important to the interpretation of the data. This makes it difficult to judge the meaning of some of the presented experiments.

    (1) An additional control for the effects of autofluorescence is very important. The authors conduct an experiment where they treat cells with CCCP and see that Thioflavin-T (ThT) dynamics do not change over the course of the experiment. They suggest that this demonstrates that autofluorescence does not impact their measurements. However, cellular autofluorescence depends on the physiological state of the cell, which is impacted by CCCP treatment. A much simpler and more direct experiment would be to repeat the measurement in the absence of ThT or any other stain. This experiment should be performed both in the wild-type strain and in the ∆kch mutant.

    ThT is a very bright fluorophore (much brighter than a GFP). It is clear from the images of non-stained samples that autofluorescence provides a negligible contribution to the fluorescence intensity in an image.

    (2) The effects of photobleaching should be considered. Of course, the intensity varies a lot over the course of the experiment in a way that photobleaching alone cannot explain. However, photobleaching can still contribute to the kinetics observed. Photobleaching can be assessed by changing the intensity, duration, or frequency of exposure to excitation light during the experiment. Considerations about photobleaching become particularly important when considering the effect of catalase on ThT intensity. The authors find that the decrease in ThT signal after the initial "spike" is attenuated by the addition of catalase; this is what would be predicted by catalase protecting ThT from photobleaching (indeed, catalase can be used to reduce photobleaching in time lapse imaging).

    Photobleaching was negligible over the course of the experiments. We employed techniques such as reducing sample exposure time and using the appropriate light intensity to minimize photobleaching.

    (3) It would be helpful to have a baseline of membrane potential fluctuations in the absence of the proposed stimulus (in this case, blue light). Including traces of membrane potential recorded without light present would help support the claim that these changes in membrane potential represent a blue light-specific stress response, as the authors suggest. Of course, ThT is blue, so if the excitation light for ThT is problematic for this experiment the alternative dye tetramethylrhodamine methyl ester perchlorate (TMRM) can be used instead.

    Unfortunately the fluorescent baseline is too weak to measure cleanly in this experiment. It appears the collective response of all the bacteria hyperpolarization at the same time appears to dominate the signal (measurements in the eLife article and new potentiometry measurements).

    (4) The effects of ThT in combination with blue light should be more carefully considered. In mitochondria, a combination of high concentrations of blue light and ThT leads to disruption of the PMF (Skates et al. 2021 BioRXiv), and similarly, ThT treatment enhances the photodynamic effects of blue light in E. coli (Bondia et al. 2021 Chemical Communications). If present in this experiment, this effect could confound the interpretation of the PMF dynamics reported in the paper.

    We think the PMF plays a minority role in determining the membrane potential in E. coli. For reasons outlined before (H+ is a minority ion in E. coli compared with K+).

    (5) Figures 4D - E indicate that a ∆kch mutant has increased propidium iodide (PI) staining in the presence of blue light; this is interpreted to mean that Kch-mediated membrane potential dynamics help protect cells from blue light. However, Live/Dead staining results in these strains in the absence of blue light are not reported. This means that the possibility that the ∆kch mutant has a general decrease in survival (independent of any effects of blue light) cannot be ruled out.

    Both strains of bacterial has similar growth curve and also engaged in membrane potential dynamics for the duration of the experiment. We were interested in bacterial cells that observed membrane potential dynamics in the presence of the stress. Bacterial cells need to be alive to engage in membrane potential dynamics (hyperpolarize) under stress conditions. Cells that engaged in membrane potential dynamics and later stained red were only counted after the entire duration. We believe that the wildtype handles the light stress better than the ∆kch mutant as measured with the PI.

    (6) Additionally in Figures 4D - E, the interpretation of this experiment can be confounded by the fact that PI uptake can sometimes be seen in bacterial cells with high membrane potential (Kirchhoff & Cypionka 2017 J Microbial Methods); the interpretation is that high membrane potential can lead to increased PI permeability. Because the membrane potential is largely higher throughout blue light treatment in the ∆kch mutant (Fig. 3AB), this complicates the interpretation of this experiment.

    Kirchhoff & Cypionka 2017 J Microbial Methods, using fluorescence microscopy, suggested that changes in membrane potential dynamics can introduce experimental bias when propidium iodide is used to confirm the viability of tge bacterial strains, B subtilis (DSM-10) and Dinoroseobacter shibae, that are starved of oxygen (via N2 gassing) for 2 hours. They attempted to support their findings by using CCCP in stopping the membrane potential dynamics (but never showed any pictoral or plotted data for this confirmatory experiment). In our experiment methodology, cell death was not forced on the cells by introducing an extra burden or via anoxia. We believe that the accumulation of PI in ∆kch mutant is not due to high membrane potential dynamics but is attributed to the PI, unbiasedly showing damaged/dead cells. We think that propidium iodide is good for this experiment. Propidium iodide is a dye that is extensively used in life sciences. PI has also been used in the study of bacterial electrophysiology (https://pubmed.ncbi.nlm.nih.gov/32343961/, ) and no membrane potential related bias was reported.

    Throughout the paper, many ThT intensity traces are compared, and described as "similar" or "dissimilar", without detailed discussion or a clear standard for comparison. For example, the two membrane potential curves in Fig. S1C are described as "similar" although they have very different shapes, whereas the curves in Fig. 1B and 1D are discussed in terms of their differences although they are evidently much more similar to one another. Without metrics or statistics to compare these curves, it is hard to interpret these claims. These comparative interpretations are additionally challenging because many of the figures in which average trace data are presented do not indicate standard deviation.

    Comparison of small changes in the absolute intensities is problematic in such fluorescence experiments. We mean the shape of the traces is similar and they can be modelled using a HH model with similar parameters.

    The differences between the TMRM and ThT curves that the authors show in Fig. S1C warrant further consideration. Some of the key features of the response in the ThT curve (on which much of the modeling work in the paper relies) are not very apparent in the TMRM data. It is not obvious to me which of these traces will be more representative of the actual underlying membrane potential dynamics.

    In our experiment, TMRM was used to confirm the dynamics observed using ThT. However, ThT appear to be more photostable than TMRM (especially towars the 2nd peak). The most interesting observation is that with both dyes, all phases of the membrane potential dynamics were conspicuous (the first peak, the quiescent period and the second peak). The time periods for these three episodes were also similar.

    A key claim in this paper (that dynamics of firing differ depending on whether cells are alone or in a colony) is underpinned by "time-to-first peak" analysis, but there are some challenges in interpreting these results. The authors report an average time-to-first peak of 7.34 min for the data in Figure 1B, but the average curve in Figure 1B peaks earlier than this. In Figure 1E, it appears that there are a handful of outliers in the "sparse cell" condition that likely explain this discrepancy. Either an outlier analysis should be done and the mean recomputed accordingly, or a more outlier-robust method like the median should be used instead. Then, a statistical comparison of these results will indicate whether there is a significant difference between them.

    The key point is the comparison of standard errors on the standard deviation.

    In two different 3D biofilm experiments, the authors report the propagation of wavefronts of membrane potential; I am unable to discern these wavefronts in the imaging data, and they are not clearly demonstrated by analysis.

    The first data set is presented in Figures 2A, 2B, and Video S3. The images and video are very difficult to interpret because of how the images have been scaled: the center of the biofilm is highly saturated, and the zero value has also been set too high to consistently observe the single cells surrounding the biofilm. With the images scaled this way, it is very difficult to assess dynamics. The time stamps in Video S3 and on the panels in Figure 2A also do not correspond to one another although the same biofilm is shown (and the time course in 2B is also different from what is indicated in 2B). In either case, it appears that the center of the biofilm is consistently brighter than the edges, and the intensity of all cells in the biofilm increases in tandem; by eye, propagating wavefronts (either directed toward the edge or the center) are not evident to me. Increased brightness at the center of the biofilm could be explained by increased cell thickness there (as is typical in this type of biofilm). From the image legend, it is not clear whether the image presented is a single confocal slice or a projection. Even if this is a single confocal slice, in both Video S3 and Figure 2A there are regions of "haze" from out-of-focus light evident, suggesting that light from other focal planes is nonetheless present. This seems to me to be a simpler explanation for the fluorescence dynamics observed in this experiment: cells are all following the same trajectory that corresponds to that seen for single cells, and the center is brighter because of increased biofilm thickness.

    We appreciate the reviewer for this important observation. We have made changes to the figures to address this confusion. The cell cover has no influence on the observed membrane potential dynamics. The entire biofilm was exposed to the same blue light at each time. Therefore all parts of the biofilm received equal amounts of the blue light intensity. The membrane potential dynamics was not influenced by cell density (see Fig 2C).

    The second data set is presented in Video S6B; I am similarly unable to see any wave propagation in this video. I observe only a consistent decrease in fluorescence intensity throughout the experiment that is spatially uniform (except for the bright, dynamic cells near the top; these presumably represent cells that are floating in the microfluidic and have newly arrived to the imaging region).

    A visual inspection of Video S6B shows a fast rise, a decrease in fluorescence and a second rise (supplementary figure 4B). The data for the fluorescence was carefully obtained using the imaris software. We created a curved geometry on each slice of the confocal stack. We analyzed the surfaces of this curved plane along the z-axis. This was carried out in imaris.

    3D imaging data can be difficult to interpret by eye, so it would perhaps be more helpful to demonstrate these propagating wavefronts by analysis; however, such analysis is not presented in a clear way. The legend in Figure 2B mentions a "wavefront trace", but there is no position information included - this trace instead seems to represent the average intensity trace of all cells. To demonstrate the propagation of a wavefront, this analysis should be shown for different subpopulations of cells at different positions from the center of the biofilm. Data is shown in Figure 8 that reflects the velocity of the wavefront as a function of biofilm position; however, because the wavefronts themselves are not evident in the data, it is difficult to interpret this analysis. The methods section additionally does not contain sufficient information about what these velocities represent and how they are calculated. Because of this, it is difficult for me to evaluate the section of the paper pertaining to wave propagation and the predicted biofilm critical size.

    The analysis is considered in more detail in a more expansive modelling article, currently under peer review in a physics journal, ‘Electrical signalling in three dimensional bacterial biofilms using an agent based fire-diffuse-fire model’, V.Martorelli, et al, 2024 https://www.biorxiv.org/content/10.1101/2023.11.17.567515v1

    There are some instances in the paper where claims are made that do not have data shown or are not evident in the cited data:

    (1) In the first results section, "When CCCP was added, we observed a fast efflux of ions in all cells"- the data figure pertaining to this experiment is in Fig. S1E, which does not show any ion efflux. The methods section does not mention how ion efflux was measured during CCCP treatment.

    We have worded this differently to properly convey our results.

    (2) In the discussion of voltage-gated calcium channels, the authors refer to "spiking events", but these are not obvious in Figure S3E. Although the fluorescence intensity changes over time, it's hard to distinguish these fluctuations from measurement noise; a no-light control could help clarify this.

    The calcium transients observed were not due to noise or artefacts.

    (3) The authors state that the membrane potential dynamics simulated in Figure 7B are similar to those observed in 3D biofilms in Fig. S4B; however, the second peak is not clearly evident in Fig. S4B and it looks very different for the mature biofilm data reported in Fig. 2. I have some additional confusion about this data specifically: in the intensity trace shown in Fig. S4B, the intensity in the second frame is much higher than the first; this is not evident in Video S6B, in which the highest intensity is in the first frame at time 0. Similarly, the graph indicates that the intensity at 60 minutes is higher than the intensity at 4 minutes, but this is not the case in Fig. S4A or Video S6B.

    The confusion stated here has now been addressed. Also it should be noted that while Fig 2.1 was obtained with LED light source, Fig S4A was obtained using a laser light source. While obtaining the confocal images (for Fig S4A ), the light intensity was controlled to further minimize photobleaching. Most importantly, there is an evidence of slow rise to the 2nd peak in Fig S4B. The first peak, quiescence and slow rise to second peak are evident.

  6. eLife

    eLife assessment

    This manuscript claims to have found evidence for coordinated membrane potential oscillations in E. coli biofilms that can be linked to a putative K+ channel and that may serve to enhance photo-protection. The finding of waves of membrane potential would be of interest to a wide audience from molecular biology to microbiology and physical biology. Unfortunately, a major issue with the experimental technique affects the interpretation of the observations: the dye used has been previously shown not to report membrane potential, leaving the evidence inadequate.

  7. eLife

    Reviewer #1 (Public Review):

    Summary:
    Cell-to-cell communication is essential for higher functions in bacterial biofilms. Electrical signals have proven effective in transmitting signals across biofilms. These signals are then used to coordinate cellular metabolisms or to increase antibiotic tolerance. Here, the authors have reported for the first time coordinated oscillation of membrane potential in E. coli biofilms that may have a functional role in photoprotection.

    Strengths:
    - The authors report original data.
    - For the first time, they showed that coordinated oscillations in membrane potential occur in E. Coli biofilms.
    - The authors revealed a complex two-phase dynamic involving distinct molecular response mechanisms.
    - The authors developed two rigorous models inspired by 1) Hodgkin-Huxley model for the temporal dynamics of membrane potential and 2) Fire-Diffuse-Fire model for the propagation of the electric signal.
    - Since its discovery by comparative genomics, the Kch ion channel has not been associated with any specific phenotype in E. coli. Here, the authors proposed a functional role for the putative K+ Kch channel : enhancing survival under photo-toxic conditions.

    Weaknesses:
    - Since the flow of fresh medium is stopped at the beginning of the acquisition, environmental parameters such as pH and RedOx potential are likely to vary significantly during the experiment. It is therefore important to exclude the contributions of these variations to ensure that the electrical response is only induced by light stimulation. Unfortunately, no control experiments were carried out to address this issue.
    - Furthermore, the control parameter of the experiment (light stimulation) is the same as that used to measure the electrical response, i.e. through fluorescence excitation. The use of the PROPS system could solve this problem.
    - Electrical signal propagation is an important aspect of the manuscript. However, a detailed quantitative analysis of the spatial dynamics within the biofilm is lacking. In addition, it is unclear if the electrical signal propagates within the biofilm during the second peak regime, which is mediated by the Kch channel. This is an important question, given that the fire-diffuse-fire model is presented with emphasis on the role of K+ ions.
    - Since deletion of the kch gene inhibits the long-term electrical response to light stimulation (regime II), the authors concluded that K+ ions play a role in the habituation response. However, Kch is a putative K+ ion channel. The use of specific drugs could help to clarify the role of K+ ions.
    - The manuscript as such does not allow us to properly conclude on the photo-protective role of the Kch ion channel.
    - The link between membrane potential dynamics and mechanosensitivity is not captured in the equation for the Q-channel opening dynamics in the Hodgkin-Huxley model (Supp Eq 2).
    - Given the large number of parameters used in the models, it is hard to distinguish between prediction and fitting.

  8. eLife

    Reviewer #2 (Public Review):

    Summary of what the authors were trying to achieve:
    The authors thought they studied membrane potential dynamics in E.coli biofilms. They thought so because they were unaware that the dye they used to report that membrane potential in E.coli, has been previously shown not to report it. Because of this, the interpretation of the authors' results is not accurate.

    Major strengths and weaknesses of the methods and results:
    The strength of this work is that all the data is presented clearly, and accurately, as far as I can tell.

    The major critical weakness of this paper is the use of ThT dye as a membrane potential dye in E.coli. The work is unaware of a publication from 2020 https://www.sciencedirect.com/science/article/pii/S0006349519308793 that demonstrates that ThT is not a membrane potential dye in E. coli. Therefore I think the results of this paper are misinterpreted. The same publication I reference above presents a protocol on how to carefully calibrate any candidate membrane potential dye in any given condition.

    I now go over each results section in the manuscript.

    Result section 1: Blue light triggers electrical spiking in single E. coli cells

    I do not think the title of the result section is correct for the following reasons. The above-referenced work demonstrates the loading profile one should expect from a Nernstian dye (Figure 1). It also demonstrates that ThT does not show that profile and explains why is this so. ThT only permeates the membrane under light exposure (Figure 5). This finding is consistent with blue light peroxidising the membrane (see also following work Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 on light-induced damage to the electrochemical gradient of protons-I am sure there are more references for this).

    Please note that the loading profile (only observed under light) in the current manuscript in Figure 1B as well as in the video S1 is identical to that in Figure 3 from the above-referenced paper (i.e. https://www.sciencedirect.com/science/article/pii/S0006349519308793), and corresponding videos S3 and S4. This kind of profile is exactly what one would expect theoretically if the light is simultaneously lowering the membrane potential as the ThT is equilibrating, see Figure S12 of that previous work. There, it is also demonstrated by the means of monitoring the speed of bacterial flagellar motor that the electrochemical gradient of protons is being lowered by the light. The authors state that applying the blue light for different time periods and over different time scales did not change the peak profile. This is expected if the light is lowering the electrochemical gradient of protons. But, in Figure S1, it is clear that it affected the timing of the peak, which is again expected, because the light affects the timing of the decay, and thus of the decay profile of the electrochemical gradient of protons (Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923).

    If find Figure S1D interesting. There authors load TMRM, which is a membrane voltage dye that has been used extensively (as far as I am aware this is the first reference for that and it has not been cited https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1914430/). As visible from the last TMRM reference I give, TMRM will only load the cells in Potassium Phosphate buffer with NaCl (and often we used EDTA to permeabilise the membrane). It is not fully clear (to me) whether here TMRM was prepared in rich media (it explicitly says so for ThT in Methods but not for TMRM), but it seems so. If this is the case, it likely also loads because of the damage to the membrane done with light, and therefore I am not surprised that the profiles are similar.

    The authors then use CCCP. First, a small correction, as the authors state that it quenches membrane potential. CCCP is a protonophore (https://pubmed.ncbi.nlm.nih.gov/4962086/), so it collapses electrochemical gradient of protons. This means that it is possible, and this will depend on the type of pumps present in the cell, that CCCP collapses electrochemical gradient of protons, but the membrane potential is equal and opposite in sign to the DeltapH. So using CCCP does not automatically mean membrane potential will collapse (e.g. in some mammalian cells it does not need to be the case, but in E.coli it is https://www.biorxiv.org/content/10.1101/2021.11.19.469321v2). CCCP has also been recently found to be a substrate for TolC (https://journals.asm.org/doi/10.1128/mbio.00676-21), but at the concentrations the authors are using CCCP (100uM) that should not affect the results. However, the authors then state because they observed, in Figure S1E, a fast efflux of ions in all cells and no spiking dynamics this confirms that observed dynamics are membrane potential related. I do not agree that it does. First, Figure S1E, does not appear to show transients, instead, it is visible that after 50min treatment with 100uM CCCP, ThT dye shows no dynamics. The action of a Nernstian dye is defined. It is not sufficient that a charged molecule is affected in some way by electrical potential, this needs to be in a very specific way to be a Nernstian dye. Part of the profile of ThT loading observed in https://www.sciencedirect.com/science/article/pii/S0006349519308793 is membrane potential related, but not in a way that is characteristic of Nernstian dye.

    Result section 2: Membrane potential dynamics depend on the intercellular distance

    In this chapter, the authors report that the time to reach the first intensity peak during ThT loading is different when cells are in microclusters. They interpret this as electrical signaling in clusters because the peak is reached faster in microclusters (as opposed to slower because intuitively in these clusters cells could be shielded from light). However, shielding is one possibility. The other is that the membrane has changed in composition and/or the effective light power the cells can tolerate (with mechanisms to handle light-induced damage, some of which authors mention later in the paper) is lower. Given that these cells were left in a microfluidic chamber for 2h hours to attach in growth media according to Methods, there is sufficient time for that to happen. In Figure S12 C and D of that same paper from my group (https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf) one can see the effects of peak intensity and timing of the peak on the permeability of the membrane. Therefore I do not think the distance is the explanation for what authors observe.

    Result section 3: Emergence of synchronized global wavefronts in E. coli biofilms

    In this section, the authors exposed a mature biofilm to blue light. They observe that the intensity peak is reached faster in the cells in the middle. They interpret this as the ion-channel-mediated wavefronts moved from the center of the biofilm. As above, cells in the middle can have different membrane permeability to those at the periphery, and probably even more importantly, there is no light profile shown anywhere in SI/Methods. I could be wrong, but the SI3 A profile is consistent with a potential Gaussian beam profile visible in the field of view. In Methods, I find the light source for the blue light and the type of microscope but no comments on how 'flat' the illumination is across their field of view. This is critical to assess what they are observing in this result section. I do find it interesting that the ThT intensity collapsed from the edges of the biofilms. In the publication I mentioned https://www.sciencedirect.com/science/article/pii/S0006349519308793#app2, the collapse of fluorescence was not understood (other than it is not membrane potential related). It was observed in Figure 5A, C, and F, that at the point of peak, electrochemical gradient of protons is already collapsed, and that at the point of peak cell expands and cytoplasmic content leaks out. This means that this part of the ThT curve is not membrane potential related. The authors see that after the first peak collapsed there is a period of time where ThT does not stain the cells and then it starts again. If after the first peak the cellular content leaks, as we have observed, then staining that occurs much later could be simply staining of cytoplasmic positively charged content, and the timing of that depends on the dynamics of cytoplasmic content leakage (we observed this to be happening over 2h in individual cells). ThT is also a non-specific amyloid dye, and in starving E. coli cells formation of protein clusters has been observed (https://pubmed.ncbi.nlm.nih.gov/30472191/), so such cytoplasmic staining seems possible.

    Finally, I note that authors observe biofilms of different shapes and sizes and state that they observe similar intensity profiles, which could mean that my comment on 'flatness' of the field of view above is not a concern. However, the scale bar in Figure 2A is not legible, so I can't compare it to the variation of sizes of the biofilms in Figure 2C (67 to 280um). Based on this, I think that the illumination profile is still a concern.

    Result section 4: Voltage-gated Kch potassium channels mediate ion-channel electrical oscillations in E. coli

    First I note at this point, given that I disagree that the data presented thus 'suggest that E. coli biofilms use electrical signaling to coordinate long-range responses to light stress' as the authors state, it gets harder to comment on the rest of the results.

    In this result section the authors look at the effect of Kch, a putative voltage-gated potassium channel, on ThT profile in E. coli cells. And they see a difference. It is worth noting that in the publication https://www.sciencedirect.com/science/article/pii/S0006349519308793 it is found that ThT is also likely a substrate for TolC (Figure 4), but that scenario could not be distinguished from the one where TolC mutant has a different membrane permeability (and there is a publication that suggests the latter is happening https://onlinelibrary.wiley.com/doi/10.1111/j.1365-2958.2010.07245.x). Given this, it is also possible that Kch deletion affects the membrane permeability. I do note that in video S4 I seem to see more of, what appear to be, plasmolysed cells. The authors do not see the ThT intensity with this mutant that appears long after the initial peak has disappeared, as they see in WT. It is not clear how long they waited for this, as from Figure S3C it could simply be that the dynamics of this is a lot slower, e.g. Kch deletion changes membrane permeability.

    The authors themselves state that the evidence for Kch being a voltage-gated channel is indirect (line 54). I do not think there is a need to claim function from a ThT profile of E. coli mutants (nor do I believe it's good practice), given how accurate single-channel recordings are currently. To know the exact dependency on the membrane potential, ion channel recordings on this protein are needed first.

    Result section 5: Blue light influences ion-channel mediated membrane potential events in E. coli

    In this chapter the authors vary the light intensity and stain the cells with PI (this dye gets into the cells when the membrane becomes very permeable), and the extracellular environment with K+ dye (I have not yet worked carefully with this dye). They find that different amounts of light influence ThT dynamics. This is in line with previous literature (both papers I have been mentioning: Figure 4 https://www.sciencedirect.com/science/article/pii/S0006349519303923 and https://ars.els-cdn.com/content/image/1-s2.0-S0006349519308793-mmc6.pdf especially SI12), but does not add anything new. I think the results presented here can be explained with previously published theory and do not indicate that the ion-channel mediated membrane potential dynamics is a light stress relief process.

    Result section 6: Development of a Hodgkin-Huxley model for the observed membrane potential dynamics

    This results section starts with the authors stating: 'our data provide evidence that E. coli manages light stress through well-controlled modulation of its membrane potential dynamics'. As stated above, I think they are instead observing the process of ThT loading while the light is damaging the membrane and thus simultaneously collapsing the electrochemical gradient of protons. As stated above, this has been modelled before. And then, they observe a ThT staining that is independent from membrane potential.

    I will briefly comment on the Hodgkin Huxley (HH) based model. First, I think there is no evidence for two channels with different activation profiles as authors propose. But also, the HH model has been developed for neurons. There, the leakage and the pumping fluxes are both described by a constant representing conductivity, times the difference between the membrane potential and Nernst potential for the given ion. The conductivity in the model is given as gK*n^4 for potassium, gNa*m^3*h sodium, and gL for leakage, where gK, gNa and gL were measured experimentally for neurons. And, n, m, and h are variables that describe the experimentally observed voltage-gated mechanism of neuronal sodium and potassium channels. (Please see Hodgkin AL, Huxley AF. 1952. Currents carried by sodium and potassium ions through the membrane of the giant axon of Loligo. J. Physiol. 116:449-72 and Hodgkin AL, Huxley AF. 1952. A quantitative description of membrane current and its application to conduction and excitation in nerve. J. Physiol. 117:500-44).

    Thus, in applying the model to describe bacterial electrophysiology one should ensure near equilibrium requirement holds (so that (V-VQ) etc terms in authors' equation Figure 5 B hold), and potassium and other channels in a given bacterium have similar gating properties to those found in neurons. I am not aware of such measurements in any bacteria, and therefore think the pump leak model of the electrophysiology of bacteria needs to start with fluxes that are more general (for example Keener JP, Sneyd J. 2009. Mathematical physiology: I: Cellular physiology. New York: Springer or https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0000144)

    Result section 7: Mechanosensitive ion channels (MS) are vital for the first hyperpolarization event in E. coli.

    The results that Mcs channels affect the profile of ThT dye are interesting. It is again possible that the membrane permeability of these mutants has changed and therefore the dynamics have changed, so this needs to be checked first. I also note that our results show that the peak of ThT coincides with cell expansion. For this to be understood a model is needed that also takes into account the link between maintenance of electrochemical gradients of ions in the cell and osmotic pressure.

    A side note is that the authors state that the Msc responds to stress-related voltage changes. I think this is an overstatement. Mscs respond to predominantly membrane tension and are mostly nonspecific (see how their action recovers cellular volume in this publication https://www.pnas.org/doi/full/10.1073/pnas.1522185113). Authors cite references 35-39 to support this statement. These publications still state that these channels are predominantly membrane tension-gated. Some of the references state that the presence of external ions is important for tension-related gating but sometimes they gate spontaneously in the presence of certain ions. Other publications cited don't really look at gating with respect to ions (39 is on clustering). This is why I think the statement is somewhat misleading.

    Result section 8: Anomalous ion-channel-mediated wavefronts propagate light stress signals in 3D E. coli biofilms.

    I am not commenting on this result section, as it would only be applicable if ThT was membrane potential dye in E. coli.

    Aims achieved/results support their conclusions:

    The authors clearly present their data. I am convinced that they have accurately presented everything they observed. However, I think their interpretation of the data and conclusions is inaccurate in line with the discussion I provided above.

    Likely impact of the work on the field, and the utility of the methods and data to the community:

    Any other comments:

    I note, that while this work studies E. coli, it references papers in other bacteria using ThT. For example, in lines 35-36 authors state that bacteria (Bacillus subtilis in this case) in biofilms have been recently found to modulate membrane potential citing the relevant literature from 2015. It is worth noting that the most recent paper https://journals.asm.org/doi/10.1128/mbio.02220-23 found that ThT binds to one or more proteins in the spore coat, suggesting that it does not act as a membrane potential in Bacillus spores. It is possible that it still reports membrane potential in Bacillus cells and the recent results are strictly spore-specific, but these should be kept in mind when using ThT with Bacillus.

  9. eLife

    Reviewer #3 (Public Review):

    It has recently been demonstrated that bacteria in biofilms show changes in membrane potential in response to changes in their environment, and that these can propagate signals through the biofilm to coordinate bacterial behavior. Akabuogu et al. contribute to this exciting research area with a study of blue light-induced membrane potential dynamics in E. coli biofilms. They demonstrate that Thioflavin-T (ThT) intensity (a proxy for membrane potential) displays multiphasic dynamics in response to blue light treatment. They additionally use genetic manipulations to implicate the potassium channel Kch in the latter part of these dynamics. Mechanosensitive ion channels may also be involved, although these channels seem to have blue light-independent effects on membrane potential as well. In addition, there are challenges to the quantitative interpretation of ThT microscopy data which require consideration. The authors then explore whether these dynamics are involved in signaling at the community level. The authors suggest that cell firing is both more coordinated when cells are clustered and happens in waves in larger, 3D biofilms; however, in both cases evidence for these claims is incomplete. The authors present two simulations to describe the ThT data. The first of these simulations, a Hodgkin-Huxley model, indicates that the data are consistent with the activity of two ion channels with different kinetics; the Kch channel mutant, which ablates a specific portion of the response curve, is consistent with this. The second model is a fire-diffuse-fire model to describe wavefront propagation of membrane potential changes in a 3D biofilm; because the wavefront data are not presented clearly, the results of this model are difficult to interpret. Finally, the authors discuss whether these membrane potential changes could be involved in generating a protective response to blue light exposure; increased death in a Kch ion channel mutant upon blue light exposure suggests that this may be the case, but a no-light control is needed to clarify this.

    In a few instances, the paper is missing key control experiments that are important to the interpretation of the data. This makes it difficult to judge the meaning of some of the presented experiments.

    (1) An additional control for the effects of autofluorescence is very important. The authors conduct an experiment where they treat cells with CCCP and see that Thioflavin-T (ThT) dynamics do not change over the course of the experiment. They suggest that this demonstrates that autofluorescence does not impact their measurements. However, cellular autofluorescence depends on the physiological state of the cell, which is impacted by CCCP treatment. A much simpler and more direct experiment would be to repeat the measurement in the absence of ThT or any other stain. This experiment should be performed both in the wild-type strain and in the ∆kch mutant.

    (2) The effects of photobleaching should be considered. Of course, the intensity varies a lot over the course of the experiment in a way that photobleaching alone cannot explain. However, photobleaching can still contribute to the kinetics observed. Photobleaching can be assessed by changing the intensity, duration, or frequency of exposure to excitation light during the experiment. Considerations about photobleaching become particularly important when considering the effect of catalase on ThT intensity. The authors find that the decrease in ThT signal after the initial "spike" is attenuated by the addition of catalase; this is what would be predicted by catalase protecting ThT from photobleaching (indeed, catalase can be used to reduce photobleaching in time lapse imaging).

    (3) It would be helpful to have a baseline of membrane potential fluctuations in the absence of the proposed stimulus (in this case, blue light). Including traces of membrane potential recorded without light present would help support the claim that these changes in membrane potential represent a blue light-specific stress response, as the authors suggest. Of course, ThT is blue, so if the excitation light for ThT is problematic for this experiment the alternative dye tetramethylrhodamine methyl ester perchlorate (TMRM) can be used instead.

    (4) The effects of ThT in combination with blue light should be more carefully considered. In mitochondria, a combination of high concentrations of blue light and ThT leads to disruption of the PMF (Skates et al. 2021 BioRXiv), and similarly, ThT treatment enhances the photodynamic effects of blue light in E. coli (Bondia et al. 2021 Chemical Communications). If present in this experiment, this effect could confound the interpretation of the PMF dynamics reported in the paper.

    (5) Figures 4D - E indicate that a ∆kch mutant has increased propidium iodide (PI) staining in the presence of blue light; this is interpreted to mean that Kch-mediated membrane potential dynamics help protect cells from blue light. However, Live/Dead staining results in these strains in the absence of blue light are not reported. This means that the possibility that the ∆kch mutant has a general decrease in survival (independent of any effects of blue light) cannot be ruled out.

    (6) Additionally in Figures 4D - E, the interpretation of this experiment can be confounded by the fact that PI uptake can sometimes be seen in bacterial cells with high membrane potential (Kirchhoff & Cypionka 2017 J Microbial Methods); the interpretation is that high membrane potential can lead to increased PI permeability. Because the membrane potential is largely higher throughout blue light treatment in the ∆kch mutant (Fig. 3AB), this complicates the interpretation of this experiment.

    Throughout the paper, many ThT intensity traces are compared, and described as "similar" or "dissimilar", without detailed discussion or a clear standard for comparison. For example, the two membrane potential curves in Fig. S1C are described as "similar" although they have very different shapes, whereas the curves in Fig. 1B and 1D are discussed in terms of their differences although they are evidently much more similar to one another. Without metrics or statistics to compare these curves, it is hard to interpret these claims. These comparative interpretations are additionally challenging because many of the figures in which average trace data are presented do not indicate standard deviation.

    The differences between the TMRM and ThT curves that the authors show in Fig. S1C warrant further consideration. Some of the key features of the response in the ThT curve (on which much of the modeling work in the paper relies) are not very apparent in the TMRM data. It is not obvious to me which of these traces will be more representative of the actual underlying membrane potential dynamics.

    A key claim in this paper (that dynamics of firing differ depending on whether cells are alone or in a colony) is underpinned by "time-to-first peak" analysis, but there are some challenges in interpreting these results. The authors report an average time-to-first peak of 7.34 min for the data in Figure 1B, but the average curve in Figure 1B peaks earlier than this. In Figure 1E, it appears that there are a handful of outliers in the "sparse cell" condition that likely explain this discrepancy. Either an outlier analysis should be done and the mean recomputed accordingly, or a more outlier-robust method like the median should be used instead. Then, a statistical comparison of these results will indicate whether there is a significant difference between them.

    In two different 3D biofilm experiments, the authors report the propagation of wavefronts of membrane potential; I am unable to discern these wavefronts in the imaging data, and they are not clearly demonstrated by analysis.

    The first data set is presented in Figures 2A, 2B, and Video S3. The images and video are very difficult to interpret because of how the images have been scaled: the center of the biofilm is highly saturated, and the zero value has also been set too high to consistently observe the single cells surrounding the biofilm. With the images scaled this way, it is very difficult to assess dynamics. The time stamps in Video S3 and on the panels in Figure 2A also do not correspond to one another although the same biofilm is shown (and the time course in 2B is also different from what is indicated in 2B). In either case, it appears that the center of the biofilm is consistently brighter than the edges, and the intensity of all cells in the biofilm increases in tandem; by eye, propagating wavefronts (either directed toward the edge or the center) are not evident to me. Increased brightness at the center of the biofilm could be explained by increased cell thickness there (as is typical in this type of biofilm). From the image legend, it is not clear whether the image presented is a single confocal slice or a projection. Even if this is a single confocal slice, in both Video S3 and Figure 2A there are regions of "haze" from out-of-focus light evident, suggesting that light from other focal planes is nonetheless present. This seems to me to be a simpler explanation for the fluorescence dynamics observed in this experiment: cells are all following the same trajectory that corresponds to that seen for single cells, and the center is brighter because of increased biofilm thickness.

    The second data set is presented in Video S6B; I am similarly unable to see any wave propagation in this video. I observe only a consistent decrease in fluorescence intensity throughout the experiment that is spatially uniform (except for the bright, dynamic cells near the top; these presumably represent cells that are floating in the microfluidic and have newly arrived to the imaging region).

    3D imaging data can be difficult to interpret by eye, so it would perhaps be more helpful to demonstrate these propagating wavefronts by analysis; however, such analysis is not presented in a clear way. The legend in Figure 2B mentions a "wavefront trace", but there is no position information included - this trace instead seems to represent the average intensity trace of all cells. To demonstrate the propagation of a wavefront, this analysis should be shown for different subpopulations of cells at different positions from the center of the biofilm. Data is shown in Figure 8 that reflects the velocity of the wavefront as a function of biofilm position; however, because the wavefronts themselves are not evident in the data, it is difficult to interpret this analysis. The methods section additionally does not contain sufficient information about what these velocities represent and how they are calculated. Because of this, it is difficult for me to evaluate the section of the paper pertaining to wave propagation and the predicted biofilm critical size.

    There are some instances in the paper where claims are made that do not have data shown or are not evident in the cited data:

    (1) In the first results section, "When CCCP was added, we observed a fast efflux of ions in all cells"- the data figure pertaining to this experiment is in Fig. S1E, which does not show any ion efflux. The methods section does not mention how ion efflux was measured during CCCP treatment.

    (2) In the discussion of voltage-gated calcium channels, the authors refer to "spiking events", but these are not obvious in Figure S3E. Although the fluorescence intensity changes over time, it's hard to distinguish these fluctuations from measurement noise; a no-light control could help clarify this.

    (3) The authors state that the membrane potential dynamics simulated in Figure 7B are similar to those observed in 3D biofilms in Fig. S4B; however, the second peak is not clearly evident in Fig. S4B and it looks very different for the mature biofilm data reported in Fig. 2. I have some additional confusion about this data specifically: in the intensity trace shown in Fig. S4B, the intensity in the second frame is much higher than the first; this is not evident in Video S6B, in which the highest intensity is in the first frame at time 0. Similarly, the graph indicates that the intensity at 60 minutes is higher than the intensity at 4 minutes, but this is not the case in Fig. S4A or Video S6B.

  10. Version published to 10.1101/2022.11.09.515771v2 on bioRxiv
  11. Version published to 10.1101/2022.11.09.515771v1 on bioRxiv