The electroneutrality liberation front

Update #2

A concise letter summarising the most serious criticisms I make below has been published in Nature Reviews Neuroscience, alongside a final response from the referees. I make a few final remarks on the affair.


The Editor,
Nature Reviews Neuroscience

Dear Sir,

I write to alert you to several issues that may confuse readers and warrant your attention in a “perspective” that appeared in your journal:

Holcman, D and Yuste, R (2015) The new nanophysiology: regulation of ionic flow in neuronal subcompartments. Nat. Rev. Neurosci. 16/685–92. doi: 10.1038/nrn4022

I summarise for your convenience discussion that took place on PubMed Commons (after fruitless direct interaction with the authors), now only available through mirroring on PubPeer. It seems that you did not notice the discussion and the authors took no action to make even simple corrections or resolve ambiguities.

  1. The central aim of the perspective is to suggest that revolutionary ionic and electrical behaviour will be identified and understood if we no longer apply the classical constraint of electroneutrality when modelling electrodiffusion in neurones. However, the voltages available in vivo (~100 mV maximum) make it impossible to generate significant deviations from electroneutrality, at least in structures of the scale of spines. For a sphere delimited by typical membrane (with apparent specific capacitance of 1 µF cm-2) and typical spine radius (0.25 µm), we can calculate the number of electronic charges transferred when charging by 100 mV (~5000) and compare it to the number of charges contained in the sphere with 300 mM ions (~12 million). The ratio of net/total charges is thus ~0.0004. Furthermore, most of those excess charges will be largely neutralised as part of the membrane capacitance. This shows why, for spines and related structures, electroneutrality remains a very accurate approximation. A consequence of the difficulty of driving deviations from electroneutrality is that the net charges of Fig. 3b and c would be unattainable in real life.
  2. Both intracellular and extracellular solutions in mammals contain about 150 mM of both positive and negative charges. The presence of such huge numbers of positive and negative charges would greatly influence the behaviour of the small numbers of net charges, but the “background” ions have simply been omitted from the simulations in the article. The authors have in effect simulated a few charges moving within an insulator, instead of a conductor. The applicability of the insulator to real life is zero. Looked at another way, the high ionic strength of physiological solutions induces strong electrostatic screening on the scale of the Debye length, which is less than 1 nm under physiological conditions. This screening is completely absent from the simulations here.
  3. The concentrations in Fig. 3 are obviously incorrect, at least in panels 3b (where the mean concentration should be 40 µM) and 3c (where the mean concentration should be 400 µM). It is unclear how the red curves were calculated to fit these erroneous values.
  4. The simulations of Fig. 3 were carried out exclusively for the perspective, but several aspects are not specified or are ambiguous.
  5. Bizarrely, the boundary conditions of Box 1 imply strict electroneutrality.
  6. In Box 2, the boundary condition does imply a net charge (i.e. a deviation from electroneutrality), but appears to be incorrect. I believe it should contain R2 in the denominator (although the numerical value might be 1 µm, the units need to be compatible). The calculated voltage may therefore be incorrect.
  7. The ambiguity about the precise simulations being carried out in Fig. 3 and Box 2 should therefore be resolved.
  8. For completeness, the particle diffusion coefficient and the relative permittivity should be specified.
  9. The simulations in Fig. 3 and Box 2 (apparently) contain no membrane, so the title of Box 2 confuses by purporting to investigate the membrane capacitance.
  10. In Box 2, the authors describe an apparently new and exciting result regarding nonlinearity of the membrane capacitance in a nanocompartment. As already stated, there is no membrane in the simulation. Moreover, the behaviour is “non-classical” not because of the nanocompartment but because the authors have used a “non-classical” definition of the capacitance: measured from the centre of the sphere to its boundary, rather than to infinity. It is of no practical application. For instance, were it to be applied in electrostatics, the classic isolated sphere would have zero capacitance.

It is understood that “perspectives” may contain some speculation, but presumably the presentation should make clear to readers which parts are speculative and the likely applicability of the speculation? More fundamentally, what is your editorial policy on speculation without apparent relation to real life?

Yours faithfully,


I welcome discussion, here or on the PubPeer thread.

Update

It turns out that the authors have posted a reply that I only recently discovered. This pdf is linked on this news page. For now, I think their document can largely speak for itself, but I will highlight one characteristic part of the reply. In point 5 above, I mention that the equations in their Box 1 imply electroneutrality. In the reply, the authors make the fair point that “There cannot be electroneutrality … with a single positive ion [i.e. if the only species of ion present is positive].” Nevertheless, in the box text, the authors very clearly state, “At the boundary, there is no flux of the electric field”, which by Gauss’s law can only occur if the boundary encloses zero net charge. This electroneutrality condition is also expressed in mathematical form in equation 3. Thus, the boundary condition implies electroneutrality and is wholly inconsistent with the existence of positive ions only within the boundary. The authors have been modelling electroneutral positive charges.

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