The transpeptidase PBP2 governs initial localization and activity of the major cell-wall synthesis machinery in E. coli

Acceptance summary:

This article provides high-quality measurements that challenge an existing model proposing that cell wall synthesis is spatially controlled by MreB polymers assembling in negatively curved regions of the cytoplasmic membrane. Instead, the positional cue appears to be located on the peptidoglycan side, signaled by the recruitment of the major transpeptidase PBP2, which then provokes assembly of the cell wall synthesis machinery. In the future, it will be important to determine the exact spatial landmark that initiates this cascade.

Decision letter after peer review:

Thank you for submitting your article "Transpeptidase PBP2 governs initial localization and activity of major cell-wall synthesis machinery in Escherichia coli" for consideration by eLife. Your article has been reviewed by two peer reviewers, and the evaluation has been overseen by a Reviewing Editor and Gisela Storz as the Senior Editor. The reviewers have opted to remain anonymous.

The reviewers have discussed the reviews with one another and the Reviewing Editor has drafted this decision to help you prepare a revised submission.

In this report the authors use different fluorescent fusions to track PBP2 localization. They find two main states: diffusive and bound (immobile) when imaging at high frequency. However, lower frequency imaging revealed that the bound fraction consists of both immobile and persistently moving particles, with the persistently moving particles traveling circumferentially as observed previously. The key observation is that the fraction of bound PBP2 particles remains constant over a roughly 3-6 fold range of PBP2 protein levels. This finding indicates that PBP2 is likely to be limiting for the formation of active Rod complexes. In characterizing this motion, the authors present evidence that other components of the rod machinery are not necessary for PBP2 to adopt its bound state, suggesting it is recognizing a partner outside of the complex, which very likely may be the cell wall itself. Importantly, a series of papers have been published that highlight the preference of MreB to localize at sites of negative cell curvature, leading to a model where MreB brings the machinery to these sites to correct aberrant curvature and maintain rod shape. The authors also present data that the prior analysis of MreB curvature preference was dominated by the curvature of the polar regions. When these cellular regions are excluded, the preference is minimal and can be explained by MreB persistent motion. In total, the authors present a convincing case that PBP2 is limiting for Rod system activation, thus nicely complementing the recent report of an activated PBP2 mutant that stimulates Rod system activity in vivo and in vitro. These findings are changing the paradigm of Rod system regulation and will be of interest to a broad audience.

Major changes that must be made to the manuscript before it can be accepted:

1) The data are rigorously collected, assembled and analysed, and the findings are in general appropriately discussed in the context of the data obtained and of the existing literature. However, the paper is currently not written for a sufficiently broad audience. The text is too long, not very well structured and sometimes not an easy read. The figures could be more concise and require the reader to continuously go back and forward. Rewriting in a more concise manner (without sacrificing information), would significantly streamline the paper and convey the logic and connections more efficiently. Ways to clarify confusing presentation of the data are further proposed below.

2) With the present data, the authors cannot strongly conclude that the formation of the bound PBP2 state is independent of Rod system components other than MreB. The data for MreB are convincing due to the use of A22 and its known ability from Park's labeling studies to block PG synthesis by the Rod complex. However, the dependence of the PBP2 bound state on the other components was based on the use of depletion strains. It is therefore entirely possible that the residual bound and persistently moving states observed following depletion reflect the activity of remaining molecules of the depleted proteins. This possibility is especially true for the MreCD and RodZ experiments since they were produced and depleted from multicopy plasmids. The magnitude of depletion observed is significant, but how the final level of protein compares to the native levels is not presented. Also, even if the depletion is significant relative to native levels, it may be that very small amounts of these proteins are sufficient. In absence of additional controls, this section of the results and the associated discussion (and comments in the Introduction) requires significant revision to soften the conclusions and address the possibility that residual Rod components may underly some of the observed phenomena. In fact, reworking this section will help address the first requirement, because the text of this Results section is quite confusing. Also, Figure 3 and 6 might be somehow combined for them to be compared easily, the reader needs to refer to each back and forth (and the multiple supplementary figures) to follow the text.

3) The explanation given to the FRAP experiment of A22-untreated cells is not satisfying. The authors see no recovery of the bound fraction and indicate that this is presumably because bound molecules left the field of view through persistent motion. It is not clear why this would prevent diffusive molecules to transit to the bound state (immobile included) if the binding sites are not saturated and the average lifetime of a bound molecule is about 1 min.

4) Subsection “PBP2 determines the location of new Rod complexes”: In addition to the two possibilities considered by the authors, there is potentially a third possibility: an MreB filament could be present at the PBP2-binding site prior to PBP2 but this filament would not be required for PBP2 recruitment. This could happen if PBP2 and MreB get there independently of each other, recruited by, for ex a third protein. In absence of data showing that PBP2 determines MreB localization this cannot be completely excluded.

Reviewer #1:

This very nice paper from Wollrab and co-workers describes an imaging analysis aimed at understanding how the cell elongation system of E. coli is controlled. This system inserts new peptidoglycan (PG) along the cell cylinder and is often called the Rod system or elongasome. Components of the complex include MreB, RodA, PBP2, MreC, MreD, and RodZ. Fluorescent fusions to members of this complex have previously been shown to form foci that rotate around the cell cylinder in a circumferential motion that depends on cell wall synthesis. Therefore, this persistent motion is thought to reflect the active machinery working to insert new PG into the existing cell wall matrix.

Prior work investigating the factors that control Rod system activation has focused on the actin-like MreB protein. A series of papers have been published that highlight the preference of MreB to localize at sites of negative cell curvature, leading to a model where MreB brings the machinery to these sites to correct aberrant curvature and maintain rod shape. This paper, along with a recently published genetic analysis of Rod system function, strongly suggest that rather than MreB, it is the crosslinking enzyme PBP2 that plays the major role in governing Rod system activity.

In this report the authors use different fluorescent fusions to track PBP2 localization. They find two main states: diffusive and bound (immobile) when imaging at high frequency. However, lower frequency imaging revealed that the bound fraction consists of both immobile and persistently moving particles, with the persistently moving particles traveling circumferentially as observed previously. The key observation is that the fraction of bound PBP2 particles remains constant over a roughly 3-6 fold range of PBP2 protein levels. This finding indicates that PBP2 is likely to be limiting for the formation of active Rod complexes. In characterizing this motion, the authors present evidence that other components of the rod machinery are not necessary for PBP2 to adopt its bound state, suggesting it is recognizing a partner outside of the complex, which very likely may be the cell wall itself. Importantly, the authors also present data that the prior analysis of MreB curvature preference was dominated by the curvature of the polar regions. When these cellular regions are excluded, the preference is minimal and can be explained by MreB persistent motion. In total, the authors present a convincing case that PBP2 is limiting for Rod system activation, thus nicely complementing the recent report of an activated PBP2 mutant that stimulates Rod system activity in vivo and in vitro. These findings are changing the paradigm of Rod system regulation and will be of interest to a broad audience.

The paper is clearly written and the data well presented. The experiments and analyses also appear well done, although I am not an expert in single particle tracking and will therefore leave commentary on this aspect of the paper to other more expert reviewers.

I have one major disagreement with the conclusions made by the authors that I think could largely be handled with changes to the text.

Major point:

1) I do not think the authors can strongly conclude that the formation of the bound PBP2 state is independent of Rod system components other than MreB. The data for MreB are convincing due to the use of A22 and its known ability from Park's labeling studies to block PG synthesis by the Rod complex. However, the dependence of the PBP2 bound state on the other components was based on the use of depletion strains. It is therefore entirely possible that the residual bound and persistently moving states observed following depletion reflect the activity of remaining molecules of the depleted proteins. This possibility is especially true for the MreCD and RodZ experiments since they were produced and depleted from multicopy plasmids. The magnitude of depletion observed is significant, but how the final level of protein compares to the native levels is not presented. Also, even if the depletion is significant relative to native levels, it may be that very small amounts of these proteins are sufficient.

Based on ribosomal profiling, E. coli cells in defined complete medium are predicted to produce 324 molecules of PBP2. Thus, in the minimal medium used for the microscopy experiments described, it is safe to assume roughly 200-400 PBP2 molecules/cell. According to the data in this report, only 20% of these are bound, and of these only 40% are persistently moving. This would equate to roughly 20-40 active PBP2 molecules/cell at any given time. With the exception of MreB, all the other Rod system components are predicted to be produced at the same level (RodA and MreD), or at twice (MreC) or 3-4x the level of PBP2 (RodZ). If it is true that there are only 20-40 active PBP2 molecules/cell, one can imagine a scenario where the other Rod components could be depleted to levels at or below detection limits, yet still promote the formation of the bound states of PBP2 and play a required role in the activation of the Rod complex. This scenario seems much more likely to me than postulating that WT PBP2 works without the other Rod components and that it may even partner with other PG polymerases to maintain persistent motion upon depletion of RodA. This section of the results and the associated discussion (and comments in the Introduction) requires significant revision to soften the conclusions and address the possibility that residual Rod components may underly some of the observed phenomena.

Reviewer #2:

This manuscript from the van Teeffelen lab is a potentially important contribution to the cell wall biogenesis field. Using single molecule localization and computational simulations, the authors quantify the dynamic behaviours of the essential PBP2 transpeptidase and revisit the prevailing model according to which recruitment of MreB filaments to sites of negative curvature in the membrane initiate Rod complex formation in E coli. Based on their findings, the authors conclude that such model is incorrect and that, instead, Rod complex formation is initiated upon binding of PBP2 to an unknown substrate that is different to MreB and probably a local feature of the cell wall (although no real experimental evidence is provided to support this).

Overall the paper is well presented although the text is too long, not very well structured and quite indigestible to read, and the figures (too many, with too much data that are not always presented in a concise way and require the reader to continuously go back and forward) are also overloaded in my opinion. The data were nevertheless rigorously collected, assembled and analysed, and findings are in general appropriately discussed in the context of the data obtained and of the existing literature. I am not a physicist and thus will not review/comment on the methodological details behind their single molecule tracking/image analysis and simulations (which are about 4/5th of the Materials and methods) – I leave that to the specialists and will focus my comments in the biological part, data interpretation and impact.

I believe that this is an interesting study for the cell wall morphogenesis field. For this work to be highly influential research some mechanistic insight or experimental evidence about the substrate to which PBP2 binds to should be provided (it is speculated that it is some local cell wall feature but no data are provided to directly support this claim), and/or showing that initial localization of the Rod complex depends on PBP2 binding to such peptidoglycan cue and not on other proteins acting upstream PBP2. Along these lines, I am not completely convinced about the RodZ depletion and RodZ-PBP2 co-localization experiments presented and the conclusions that the authors draw from them and I would need them to address this point. This said, the data presented are in general very solid and the conclusions and discussions sound, and to my knowledge accurate quantification of the transitions between dynamic states in single trajectories was not done previously in the field. All in all, I believe that this study is significant enough for publication in eLife, and that no significant new work is required if the authors answer to the main points raised by the reviewers. The manuscript requires, however, some work – figures and text should be simplified/shorten for clarity, data of the wild-type strain should be included in the figures for reference, and some parts included in the results could be moved to the discussion.

Most substantial comments

– The explanation given to the FRAP experiment of A22-untreated cells is not satisfying. The authors see no recovery of the bound fraction and indicate that this is presumably because bound molecules left the field of view through persistent motion. I do not see why this would prevent diffusive molecules to transit to the bound state (immobile included) if the binding sites are not saturated and the average lifetime of a bound molecule is about 1 min. Could the authors please comment on this and maybe clarify their explanation in the text?

– Subsection “PBP2 determines the location of new Rod complexes”: In addition to the two possibilities considered by the authors, couldn't an MreB filament be present at the PBP2-binding site prior to PBP2 but not required for its recruitment? Could PBP2 and MreB get there independently of each other, recruited by, for ex a third protein? Why not? Why only the two possibilities indicated? Unless I missed something here or it is conclusively shown that MreB localization is dependent on PBP2 their hypothesis are incomplete and their conclusion biased.

– The entire depletion section should be reworked for the sake of clarity. There is too much information in the figures and often not described in the text. The depletion strains display levels (of MreCD in particular but also of RodZ) well above the native levels at the time of “induction” to start with. Since the bound fraction is increased in the rodZ induced condition and decreased in the RodZ depletion, this suggest that RodZ may recruit PBP2. The authors then exclude this possibility by showing that upon a longer depletion the bound fraction increases again. Yet they need to show that depletion is still working.g – only t6 and t9 are shown. And RodZ levels seem higher at 9h than at 6h (and data are probably from different cells relative to the data shown in Figure 5 supplements). RodZ levels at all the depletion points shown in Figure 5—S4 need to be shown to demonstrate that the depletion is still operating and progressing after 2h and to thus to exclude RodZ as binding cue. Also, the colocalisation experiments RodZ-PBP2 do not add much the way they are presented. Why weren't these done by TIRF? In any case, there is sufficient overlay for a RodZ-dependent binding not to be completely excluded. Overall the text of this Results section is quite confusing and does not convincingly support the strong conclusion of the authors that PBP2 substrate is the cell wall. Also, Figure 3 and 6 might be somehow combined for them to be compared easily, the reader needs to jungle between the two (and the multiple supplementary figures) to follow the text.

[Editors' note: further revisions were suggested prior to acceptance, as described below.]

Thank you for resubmitting your work entitled "Transpeptidase PBP2 governs initial localization and activity of major cell-wall synthesis machinery in Escherichia coli" for further consideration by eLife. Your revised article has been evaluated by Gisela Storz (Senior Editor), a Reviewing Editor (Tâm Mignot) and one of the previous reviewers.

The manuscript has been improved but there are some remaining issues that need to be addressed before acceptance, as outlined below:

The authors have gone through a large number of experiments, analysis and revisions that make this a better paper. They have done a very good job in addressing most of the reviewers comments. Additionally, reinvestigation of new and old high frequency acquisition data of PBP2 revealed that a 3-state diffusion model (instead of a 2-state diffusion model) was a better fit for their dataset, so they reanalysed their data using a published tool instead of the custom approach (of fitting to a 2-state model) used in the previous version of the manuscript. While the outcome of the 2- and 3- state model were similar for wild-type levels of PBP2 fusions, the outcome for the overexpression of PBP2 was different: the fraction of bound PBP2 particles no longer remained constant (i.e. the number of bound PBP2 increased in direct proportion to total PBP2 levels) but decreased when the levels of PBP2 increased. Thus, the new fitting and analysis affected one of the main messages of the paper: the authors previously claimed that PBP2 was the limiting factor for rod-complex activity and the new results indicate that this is not the case. PBP2 is still important (since the number of active PBP2 molecules still rises, although not in direct proportion, with PBP2 levels) but is not the only limiting factor for Rod activity. The authors have adjusted their manuscript accordingly and provide the comparison of the 2- and 3- state model in their rebuttal letter and in Figure 1—figure supplement 1. I salute them for their in depth analysis and for revisiting their data and conclusions accordingly.

The paper is now clearer (the authors made an effort to shorten the text; discussion is also more structured and sharper) and convincing. The authors have made a clear effort to tone down their claims and indicate that a number of key questions remain to be addressed. The supplementary figures are helpful and improve the manuscript.

Some finals points that need to be addressed prior to publication are:

1) No evidence is provided to make the claim that the cell wall itself is the partner that PBP2 is recognizing outside the Rod complex, other than the slow diffusion coefficient of PBP2. The authors should either give more direct evidence that supports this or else rephrase their sentences to clearly indicate that this is speculation. The authors show that MreB is not the binding substrate of PBP2, and that none of the other Rod components provides the sole substrate for PBP2 binding… but no data are provided to directly support that a local cell wall feature binds PBP2 and initiates Rod complex formation. The authors should tone down this conclusion in the Abstract and as a main conclusion from the results reported.

2) The arguments given to exclude RodZ as PBP2 recruiting factor are not fully convincing on the basis of the data presented. The fraction of bound PBP2 decreases sharply and then progressively increases again (but remains lower than wt levels) during RodZ depletion (from t8). As pointed out during the first round of review, the authors do not show if depletion of RodZ is still operating at later times (the levels of RodZ in the depletion strain are not shown, the text suggests that this is shown in Figure 5—figure supplement 2F but this is not the case). The dCas9 data only shows t3 and t6, while the increase of bound PBP2 fraction operates after t8 in their depletion strain. This point is therefore not fully demonstrated and the conclusion should be toned-down.

3) The explanation that the diffusion constant of the diffusive population of PBP2 decreases significantly upon PBP2 overexpression (“perturbations in the stoichiometry.…. might lead to alternations of the cell wall structure”) is also pure speculation.

4) Title: please correct "Tranpeptidase PBP2 governs initial localization and activity of major cell-wall synthesis machinery in Escherichia coli" to"THE transpeptidase PBP2 governs initial localization and activity of THE major cell-wall synthesis machinery in Escherichia coli"?