Peer review of: Aβ(1-42) tetramer and octamer structures reveal edge conductivity pores as a mechanism (2020)

Reviewers' comments first round: Reviewer #1 (Remarks to the Author):
Carulla and co-workers employed various biophysical techniques - NMR, SEC/IM-MS (size exclusion
chromatography coupled with ion-mobility mass spectrometry), MALDI-MS, electrical recordings,
as well as MD (molecular dynamics) simulations - to determine a structure of micelle-bound
Abeta(1-42) tetramers and octamers, which in case of the tetramer was submitted to the Protein
Data Bank.
 This work is of high importance and novelty as in the amyloid field structural information on Abeta
 oligomers (in solution and membrane-bound) is currently still missing. Such information is of
 importance as Abeta oligomers are thought to play a key role in the development of Alzheimer's
 disease.
 While the importance of the current work is without doubt, some concerns have to be addressed
 before the manuscript may become publishable:
1) The authors need to mention that pH values between 8.5 and 9.5 are anything but
physiological. It is known that the structures of monomeric and aggregated Abeta is highly
susceptible to pH. Thus, the structures reported here might be of no relevance at all at
physiological pH. Though having said this, it should also be mentioned that others publish Abeta
fibril structures determined at a non-physiological pH of 2 in a solution incolving 30% acetonitril
(doi: 10.1126/science.aao2825). Thus, when such a fibril structure can be published in Science, it
should also be warranted to publish an amyloid oligomer structure at pH 9 in Nature Commun. But
the pH issue must be openly discussed.
2) When discussing the pH problem, the most likely protonation states of the amino acids at pH 9
should be given. For sure, histidines will be neutral (unlike what the authors state on pp. 7 and 8).
But also the lysines may become neutral at such high pH, also considering that a hydrophobic
environment reduces the pKa auf lysine. In the Methods regarding the MD simulations the chosen
protonation states of titratable amino acids need to be given.
3) It should be further stated that the current structures determined from the co-assembly of
Abeta and DPC into micelles containing Abeta are not necessarily those which one might find in
lipid bilayers (biomembranes). With the suggested structure (Fig. 1d), the N-terminus of two of
the peptides, with all its charged residues, would need to traverse through the hydrophobic core of
the bilayer. The authors need to state how likely this event would be, e.g., how much energy it
would take for this process to happen, or whether this could be enabled by transporters.
4) The MD simulations do not fully support that the suggested structures would be likely in a lipid
bilayer environment. Fig. S14 shows that DPC assembles with its headgroup region around beta1,
i.e., this strand prefers a polar environment and therefore draws water into the bilayer as Fig. 5
shows. As the simulations were only conducted for 100 ns, which is too short for a system of that
size and needs to be extended to 1 microscond or longer, it remains open how stable the
suggested transmembrane tetramer structure indeed is. More analysis of the MD simulations
needs to be done: RMSD/F, number of water molecules traversed, secondary structure per residue
are some quantities that would be helpful.
5) While it is always expected that simulation scientists compare their results to existing
experimental observations, it seems that the opposite is usually not expected. But almost 10 years
ago models for transmembrane Abeta oligomers were published and their stability tested in MD
simulations (doi: 10.1021/ja103725c; doi: 10.1016/j.bbamem.2012.09.001). Interestingly, later a
very similar structure per Abeta peptide was determined by solid-state NMR as building block for
Abeta hexamers: doi: 10.1002/anie.201406357. The authors should include a comparison of their
structure model of membrane-bound Abeta oligomers with those previously published.
 6) The CCS results in Fig. 4e and f are anything but convincing. Cutting off the flexible N-terminal
 ends to obtain agreemt between structure model and actual CCS results does not increase the
 trust in the suggested tetramer and octamer models. However, it is anyhow questionable whether
 the ionized oligomers in the gas phase are structurally similar to the Abeta structures in DPC
 micelles. The authors should do more to convince this reviewer of this correspondance. As some of
 the authors are simulation scientists, one approach could be to simulate the oligomers in the
 proper ionization state in the gas phase to see how they evolve. The current approach (ignoring
 some of the residues to obtain the experimental CCS results) is below the standard expected for a
 publication in Nat. Commun.
 Reviewer #2 (Remarks to the Author):
 The manuscript by Ciudad et al. describes the structural characterization of Abeta(1-42) tetrameric
 and octameric structures. The structure of the tetramer is derived from NMR measurements.
 Cross-linking and SEC/IM-MS corroborate the findings of an Abeta tetramer, octamer, and other
 species. The study brings a 3D structure of an Abeta tetramer to the fore.
 The introduction is composed of only two paragraphs and lacking background on Abeta or other
 oligomers that have been either modelled or determined experimentally. In short, the introduction
 would benefit from more background and context.
 Abeta oligomers were studied in dodecylphosphocholine (DPC), a detergent, and at non-
 physiological pH (8.5 and 9.5). The authors note in discussion that DPC is a membrane mimic and
 not a physiological environment. However, there is no mention in regards to pH. Would the
 proposed structures be stable at physiological pH?
 The 3D structure reveals an antiparallel arrangement with two of the three subunits exhibiting long
 flexible, solvent exposed N-termini. Given the structure, it would appear there would be large
 entropic barrier to insertion into the bilayer. Can the authors speculate on a plausible mechanism
 for insertion into the bilayer? Another issue not addressed, is the fact that charged and polar
 residues (such as His, Qln, and Lys) in their model (see Fig 1 and S17) are centrally located in the
 hydrophobic core of the bilayer. This simply does not make chemical sense and raises concerns to
 the validity of the proposed model. An explanation to rationalize exposure of such residues in the
 hydrophobic environment is warranted.
 In regards to the SEC/IM-MS measurements, increased activation conditions were used to disrupt
 the Ab complexes. The authors note tetramers broke into trimers and monomers, but this is not
 evident from the data presented (Fig S16 and S19). The assignment of oligomeric states by m/z
 and IM measurements is solid. The authors may consider isolating particular Ab species using the
 quadrupole prior to subjecting them to increased activation? This has been done before (see doi:
 10.1038/nature20820 and doi: 10.1007/s13361-016-1555-1), which would provide a more robust
 evaluation of complex gas-phase stability/dissociation.
 IM measurements (CCS values) were compared to a limited set of Ab models. The CCS values
 indicate a compact CCS value that agrees with models where the flexible loops have been removed
 from the structure prior to calculation. This approach raises significant concerns; deleting residues
 to match measured CCS values is not acceptable nor rigorous. First, flexible regions can lead to an
 increase in CCS values (see DOI: 10.1002/anie.201203047), which is not observed here. Does this
 imply that the N-termini are more ordered than flexible? Second, have other models been
 compared to the measured CCS values? Such as, a six-stranded cylindrin-like structure? Or other
 models? At present, additional models should be explored and also considering gas-phase
 minimization prior to CCS calculation.
 No controls for the electrical recordings using planar lipid bilayers are presented. DPC is a
 detergent, which could disrupt the integrity of the bilayer giving rise to background signals. Were
 measurements of DPC in the absence of Ab performed?
 The section titled “preparation of ... enriched in Ab(1-42) octamers” seems out of place. Suggest
 moving up and before the SEC-MS analysis section.
 The manuscript could be improved by merging some figures. For example, Fig S17 can be
 incorporated into Fig S7.
 For denatured and native MS measurements, the measured and theoretical masses should be
 reported along with error.
 Supplementary Fig. 18 is mislabelled. I presume the data shown is for PFOsHIGH not PFOsLOW. Pg 8, “... using DPC at natural abundance.” This is unclear as DPC is non-natural.
Pg 15, “.. we have precisely defined the structural ..” Remove precisely.
Reviewer #3 (Remarks to the Author):
   Although I am not able to expertly comment on the quality of the NMR data, the study seems well
 designed and executed.
  This is a very interesting paper that presents a startling structure for the micelle-inserted amyloid-
 beta-42 polypeptide (AB42). AB42 is, of course, generally thought to be associated with the
 etiology of Alzheimer's disease. There is a body of evidence in the literature that AB42 can adopt
 some sort of transmembrane oligomer, with additional evidence that it can act (aberrantly) as an
 ion channel, potentially a mechanism that contributes to how AB42 promotes Alzheimer's disease.
 In this paper the authors used NMR spectroscopy to document that AB42 in dodecylphosphocholine
 micelles can form two closely related oligomeric structures. In one structure 4 subunits come
 togehther to form a single sheet with two subunits forming trans-micelle beta hairpins flank the
 two other subunits central in the tetrameric sheet as a single beta strands. What is amazing is that
 the 6-stranded tetatrameric sheet does not form a closed barrel, but instead is an "open" sheet
 with solvent exposed edges for strands 1 and 6. The other structure is a dimer of tetramers where
 the 6-stranded sheets form a sandwich in the micelle interior, again with exposed edges. The
 authors also present electrophysiology measurements in which ion channel activity is documented,
 apparently for both monomer and dimers, with the channel activity apparently being associated
 with the exposed edges of the monomeric or dimeric sheets.
 The NMR studies of this work were meticulously carried out and documented-- very convincing.
 Moreover, one can imagine how these structures might be stable in micelles: the horizontal
 diameter of the sheet is on the same order as the diameter of the micelle it sits in, so the need to
 form transmicelle beta barrels is relieved by the fact that the exposed edges of strands 1 and 6 are
 not exposed to a bilayer interior, but instead to water outside of the micelle water at the micelle-
 water interface. So, these structures seem reasonable as micelle structures. However, it seems
 less clear that they could be energetically accommodated as transmembrane structures in a sealed
 lipid bilayer, where the exposed edges of strands 1 and 6 would be exposed only to lipid, resulting
 in burial backbone amide groups with unsatisfied H-bonding potential.
 The text, figures, and supporting material are all very well written. I think this work is EXTREMELY
 interesting and should be published following revision, without any requirement for additional
 experiments. However, the authors should provide more detail on what evidence they have that
 the micellar structure they carefully document in this work is maintained in lipid vesicles. This
 closely relates to the question of whether the channel activity they document really stems from
 AB42 channels that resemble the micellar structures. Again, more textual justification seems
 needed.
 Finally, the sample composition, pH, and temperature need to be spelled out in detail in the
 caption to Figure 1.
 Reviewer #4 (Remarks to the Author): Review of NCOMMS-19-35967-T
  The manuscript by Ciudad et al deals with an important open question in our understanding of the
 Alzheimer’s Disease (AD) Pathology cascade: the mechanism by which amyloid-beta causes
 damages neurons. The authors cite the “amyloid hypothesis” in which Abeta is assumed to be the
 primary toxic agent in AD, and note that the mechanism of toxcity is unclear. They also cite works
 in which soluble forms of Abeta can induce pores of various sorts in membranes. This is the
 background for their basic hypothesis: that Abeta structures can form pores in planar lipid
 bilayers, and therefore can serve as a mechanism of neurotoxicity. The primary focus of the work
 is in establishing the feasibility of this idea, and the authors perform detailed work in establishing
 this to be the case. The evidence that Abeta structures can form pores in planar lipid bilayers, and
 that this is specific to certain forms of Abeta, seems to be well established by this study, and
 supported by beautiful and clear figures.
 I will address a different aspect of this study, which is the validity of their hypothesis: that Abeta
 can cause pores in the membranes of neurons adjacent to sufficient concentrations of Abeta, which
 will then disrupt neuronal activity. The principal evidence for that disruption is shown in
 Supplementary Figure 20, in which the membrane conductance is increased by the introduction of
 βPFOsAβ(1-42) into planar lipid bilayers.
 This makes a clear prediction of the effect of soluble Abeta on neuronal activity. The prediction is
 that the input conductance of these neurons will be increased. Intracellular recordings from several
 lines of APP+ transgenic mice (two of which are published) , in which both soluble Abeta and
 amyloid plaques are present in the surrounding neuropil, by measurement of average input
 resistance in the neurons, do not show the increase in RIN that would be expected to be
 associated with such a conductance increase (Stern et al, J. Neurosci 24, 4335-4340 (2004);
 Kellner et al, Neurobiology of Aging 35, 1982-1991 (2014)). I do not know of any studies which
 have shown different results. (In addition, measurement by several groups show hyperactivity in
 numerous lines of APP transgenic mice, which is the opposite effect that would be expected from a
 general conductance increase.) these are issues that should be addressd by the authors, if they
 wish to argue that increased membrane conductance is indeed a mechanism of neuronal disruption
 by Abeta.
 NOTE: This, however, is not necessarily evidence that the conductance increase does not occur.
 The direct measurements of input resistance are made using electrodes inserted into the soma. It
 may well be that the the toxic effects of Abeta on the membrane are local. Indeed, one study
 shows that there are specific effects on dendritic spines in proximity to plaques, where the
 concentrations of soluble Abeta are higher (Spires et al, J Neurosci. 25, 7278-7287 (2005)).
 This is an hypothesis which can be tested, using targeted patch recordings in slices of APP
 transgenic mouse cortex. The recordings would have to target dendrites in mice in which plaque
 aggregation is severe, so that dendrites would have a high probability of proximity to plaques.
 While difficult, targeted recordings are performed on a daily basis by numerous laboratories. If the
 input conductance is increased in these dendrites, compared to aged-match recordings in WT
 mice, it would indeed be strong evidence that the hypothesis proposed by the authors is correct.
 In many studies, including the one I cited, there is evidence for stripping of spines form these
 dendrites, which I would predict will show the opposite effect: raising the local dendritic input
 resistance.
 At present, however, there is no such evidence of which I am aware that the mechanism proposed
 by the authors disrupts neuronal activity in AD. And some evidence does exist that the overall
 conductance in the neuron is not raised in APP-transgenic mouse model neurons. The current
 study does show an interesting possible mechanism of action of one of the forms of Abeta: one
 interesting enough to be further investigated. Again, evidence for the specific mechanisms (note
 the plural) of the pathophysiological effects of Abeta is a “missing link” in our understanding of the
 cascade of effects of the Abeta in the disase process.
 Edward A. Stern
 Brain Research Center
 Bar Ilan University