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PLOS ONE

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Additional Editor Comments (if provided):

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. Is the manuscript technically sound, and do the data support the conclusions?

Reviewer #1: Partly

Reviewer #2: No

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2. Has the statistical analysis been performed appropriately and rigorously? -->?>

Reviewer #1: No

Reviewer #2: No

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3. Have the authors made all data underlying the findings in their manuscript fully available??>

The PLOS Data policy

Reviewer #1: No

Reviewer #2: Yes

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4. Is the manuscript presented in an intelligible fashion and written in standard English??>

Reviewer #1: Yes

Reviewer #2: Yes

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Reviewer #1: Marquez et al. examined the membrane and synaptic characteristics of a few pyramidal neurons that were recorded from tissue taken from patients with epilepsy after the suspected seizure origin was surgically removed. According to the results, the primary change that can account for the tissue's hyperexcitability occurs at the synapse level rather than the somatic level.

Given the lack of information on the electrophysiology of neurons from the human brain, especially in diseased situations, the study may be relevant. However, the manuscript requires a significant change before it is ready for publication.

Major:

The location of the tissue of origin must be specified, if it can be found in the surgical data. For instance, whether or not the tissue is hippocampus-derived greatly alters a placement in the temporal lobe. The extent to which the tissue is solely inside the seizure onset zone or includes adjacent tissue that is likely less impacted by the clinical history must also be determined. In this context, the available surgical outcome must also be described in the table of affected individuals. This aids in determining the actual contribution of the excised tissue to each patient's network hyperexcitability.

There are too many details missing to fully comprehend the dataset's nature. For each patient, how many slices were taken? It is necessary to provide further details on the patient from whom the (few) recorded cells originate. For instance, one patient may have had four of the six temporal lobe cells recorded, while the other two patients may have just had one cell.

The statistics are presented in a too careless manner. The authors must try to justify the validity of applying their tests to such small samples for each dataset. The number (n) of measurements from which each reported mean value is derived must be included, particularly when using a repeated measures approach. Even if the result is not significant, it still needs to be reported together with the relevant p-value and other information. To clearly identify which factors were taken into account between-subjects and which were evaluated within-subjects, the mixed-effects ANOVA analysis has to be more thorough.

From what is said in the abstract, the focus on the cell morphology results, which are based on just (!) four cells, must be reduced.

Reviewer #2: 1. Is the manuscript technically sound, and do the data support the conclusions?

The manuscript presents original research on the electrophysiological and morphological properties of human Layer 5 (L5) pyramidal neurons (PCs) from different cortical regions, obtained from surgical resections of drug-resistant epilepsy (DRE) patients. The study addresses a relevant and timely topic in human neurophysiology. However, several technical and interpretative issues need to be addressed:

• Methods: Important experimental details are missing, including the osmolarity of all solutions and the rationale for using an unusual transport solution (320 mM sucrose, 1 mM EDTA, 5 mM Tris-HCl), which could affect neuronal viability and physiology due for example to a poor ion balance given by the absence of most of the ions needed to mimic the CSF and so maintain physiological conditions.

The unusually low biocytin concentration (0.04%) is concerning, as it may limit dendritic and axonal filling. The methods section does not specify the number of cells analyzed for dendritic complexity, nor the criteria used for their selection. However, based on the results, it appears that only four cells were included in this analysis. This raises concerns regarding the representativeness and robustness of the findings, as such a small sample size limits the ability to draw meaningful conclusions. Similarly, the small sample size used for the classification of L5 PCs across the different cortices makes generalization difficult.

• Data quantification: Several claims are not adequately supported by quantified data or statistical tests (e.g. lines 287, 296, 300-311). Notably, parameters such as action potential (AP) firing rates, adaptation, and afterhyperpolarization are mentioned but not systematically quantified or statistically compared.

• Neuron classification: The classification of L5 PCs based solely on spike frequency adaptation and firing rate is oversimplified. Extensive literature demonstrates the existence of well-defined subpopulations (ET vs. IT; for human temporal cortex gyrus see for example Kalmbach et al., 2021; for rodent neocortex see Moberg and Takahashi, 2022). These cells have distinct morphological and electrophysiological features that must be taken into account while attempting to classify L5 PCs in human cortex. The authors should revisit their classification strategy in light of established frameworks.

• Results interpretation: The interpretation of the FV-fEPSP relationship and the claim of synaptic imbalance in DRE lacks proper statistical comparison (e.g., regression slopes) and validation against healthy tissue or additional rodent data. Several passages are speculative and need either experimental evidence (e.g., recordings with synaptic blockers) or should be moved to the discussion.

Additionally, the morphological analysis in this study raises concerns about the representativeness and robustness of the findings, as the small sample size and large neuronal heterogeneity in human L5 (e.g., Kalbach et al, 2021) limit meaningful conclusions. Reported values, such as a total dendritic length of ~100 μm and an average of 1.5 branches, are unusually low compared to published data (e.g., >10 mm dendritic length and >60 apical branches in Mohan et al., 2015; Kalbach et al., 2021). These discrepancies may result from technical issues, including low biocytin concentration (0.04%?) or tissue damage during slicing. While the authors briefly mention some limitations, they still draw conclusions as if these morphological parameters were fully representative. Given the small sample size, possible artifacts, and inconsistencies with previous literature, these findings should be interpreted with caution, and further validation with larger, methodologically optimized datasets is strongly recommended.

• Figures: Several figures lack error bars, sample size annotations, and statistical comparisons. Some traces are presented without supporting quantification and should be either properly quantified or removed. Additionally, certain visualizations are unnecessarily complicated. For example, in Fig. 1B, expressing the number of cells as percentages makes the information less accessible than it needs to be, and the actual numbers should be reported directly. In Fig. 5C, D, and F, the heatmaps could be replaced with simple numeric values, as only four cells were analyzed.

In summary, while this study explores an important and promising area, substantial revisions are required to ensure that the conclusions are rigorously and appropriately supported by complete, quantified, and statistically tested data.

2. Has the statistical analysis been performed appropriately and rigorously?

Statistical analyses are generally described but are not always rigorously applied:

• Missing analyses: Many important comparisons (e.g., between cortical regions, between firing pattern types) lack proper statistical testing or explicit reporting of sample sizes. For example, in lines 430-438, the description of spontaneous synaptic events following train stimulation requires clarification. It is unclear whether these events represent recurrent excitation, asynchronous release, or another process. The claim that the number of these events “tended to be higher” in the temporal cortex lacks statistical validation. Further analysis is needed to determine whether this facilitation reflects pathological hyperexcitability or normal synaptic dynamics.

• Choice of error metrics: The use of the standard error of the mean (SEM) rather than standard deviation (SD) with such small sample sizes can give a misleading impression of data variability. SD would be more appropriate to accurately reflect the dispersion within the sample, particularly in cases where individual variability is of interest.

• Linear regression analyses: The interpretation of r² values in the FV-fEPSP relationship needs to be more cautious (lines 399-406). Perfect or near-perfect r² values (such as an r² = 1 in the frontal cortex data) may indicate overfitting that might be given by some issues in the data such as limited data points. Additionally, the phrase “theoretical consistency and proportionality” is vague and should be explicitly defined how the FV-fEPSP relationship in DRE in altered by comparing it with “healthy” tissue (i.e. non-epileptic, for example access tissue from tumor resections) or more rodent data. The least squares method quantifies the strenght of a linear relationship, but it does not inherently substantiate or prove synaptic imbalance. A statistical comparison of regression slopes across conditions is needed to support this claim. Finally, the claim that the proportionality is "disrupted" in DRE should be backed by statistical evidence.

• Assumptions and justifications: The rationale behind choosing specific current injection ranges and classification criteria is unclear and requires clarification. For example, was the range 90-210 pA empirically chosen, or was the firing linear without any adaptation, or was there the absence of significant variability in firing rates?

3. Have the authors made all data underlying the findings in their manuscript fully available?

The data availability is generally acceptable but lacks clarity in several areas:

• The number of cells analyzed for dendritic complexity is not specified in the methods, though results suggest only four were used, raising concerns about representativeness.

• The availability of raw electrophysiological data (e.g., individual firing frequencies, membrane properties, and fEPSP measurements) is not explicitly confirmed.

• Data supporting several figure panels (e.g., spontaneous postsynaptic potentials, firing rates) are either missing or insufficiently described.

The authors should ensure that all underlying data points (not only summary values) are made available.

4. Is the manuscript presented in an intelligible fashion and written in standard English?

The manuscript is generally intelligible and written in acceptable English, but several issues of clarity, consistency, and terminology need to be addressed:

• Abbreviation consistency: All abbreviations must be defined at first appearance and used consistently throughout the text.

• Sentence clarity: Several sentences in the Introduction and Methods are overly long or ambiguous (e.g., lines 69-73 and 74-79). These should be split and clarified.

• Technical terminology: Terms like “synaptic spontaneous activity” should be replaced by the more precise “spontaneous postsynaptic potentials.” In line 162, it is not clear what the authors mean with “interval’s latency”. If I understand Fig. 1 correctly, the latency refers to the time between the onset of the current injection and the occurrence of each evoked action potential within that step - is this what the authors meant? It should be also better clarified whether the authors refer to cytoarchitectonic subdivisions of Layer 5 (e.g., 5a vs. 5b) or a particular distance from the pia when they write “the middle region of layer V” (line 277) or “external region of layer V” (line 375).

• Consistency in tense and form: Active/passive forms should be harmonized, and descriptions of results made more precise.

• Figure labels: Some figure labels are misleading or incorrect (e.g., calling voltage traces “I-V curves” in Fig. 2B1-B3).

Overall, while the manuscript is understandable, careful editing for clarity, grammar, and terminology is needed.

Summary:

Major points

• Please add missing details in the Methods section, including osmolarity of solutions, rationale for transport medium, objective lenses, z-stack step size, and sample size criteria for morphology analysis.

• Reconsider the classification strategy for Layer 5 pyramidal neurons in light of established subtypes (ET/IT) as described in recent literature (e.g. Kalmbach et al., 2021; Moberg and Takahashi, 2022).

• Quantify all electrophysiological parameters discussed in the text (e.g., AP firing rates, spike adaptation, afterhyperpolarization), and report statistical analyses.

• Correct overinterpretations regarding synaptic influence on firing rates and the FV-fEPSP relationship. These claims should be either experimentally tested (e.g., with synaptic blockers) or restricted to the discussion.

• Review and improve figure presentations, i.e. add error bars, report the number of cells, perform statistical comparisons, and remove unsupported traces.

• Replace speculative interpretations with data-supported statements or move them to the discussion.

• Revise the language for clarity, consistency, and technical accuracy, addressing long or ambiguous sentences, terminology, and typographical errors.

Minor points

• Adjust terminology, e.g. “spontaneous postsynaptic potentials” instead of “synaptic spontaneous activity.”

• Clarify specific method descriptions (e.g., “Membrane capacitance was calculated as the ratio of the membrane time constant to the input resistance”).

• Correct typographical and figure annotation errors (e.g., r² values in line 398, significance asterisks in Fig. 3C).

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Reviewer #1: No

Reviewer #2: Yes: Laura Monni

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Dear Dr. Galvan,

Thank you for submitting your manuscript to PLOS ONE. After careful consideration, we feel that it has merit but does not fully meet PLOS ONE’s publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

Please submit your revised manuscript by Nov 18 2025 11:59PM. If you will need more time than this to complete your revisions, please reply to this message or contact the journal office at plosone@plos.org . When you're ready to submit your revision, log on to https://www.editorialmanager.com/pone/ and select the 'Submissions Needing Revision' folder to locate your manuscript file.

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We look forward to receiving your revised manuscript.

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Michele Giugliano

Academic Editor

PLOS ONE

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If the reviewer comments include a recommendation to cite specific previously published works, please review and evaluate these publications to determine whether they are relevant and should be cited. There is no requirement to cite these works unless the editor has indicated otherwise.

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

Reviewer #2: (No Response)

Reviewer #3: (No Response)

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2. Is the manuscript technically sound, and do the data support the conclusions??>

Reviewer #2: Partly

Reviewer #3: Partly

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3. Has the statistical analysis been performed appropriately and rigorously? -->?>

Reviewer #2: Yes

Reviewer #3: Yes

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4. Have the authors made all data underlying the findings in their manuscript fully available??>

The PLOS Data policy

Reviewer #2: Yes

Reviewer #3: Yes

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5. Is the manuscript presented in an intelligible fashion and written in standard English??>

Reviewer #2: Yes

Reviewer #3: Yes

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Reviewer #2:  I thank the authors for the thorough and thoughtful revisions to their manuscript. The new version is much improved in clarity and presentation, and several of the concerns I raised in my initial review have been well addressed. I appreciate the substantial improvements made in the revised manuscript, particularly the more careful interpretation of the data. This is a welcome change. While I fully understand the challenges involved in working with human cortical tissue - and I acknowledge the value of such data - I would still encourage the authors to frame their conclusions with appropriate caution given the sample size. The difficulty of the preparation is not in question, but ensuring careful interpretation remains important for the strength of the study.

Overall, I believe the manuscript is close to being suitable for publication pending minor revisions.

I do have a few additional comments and suggestions:

1) Thank you for adding the osmolarity value of the intracellular solution (315–325 mOsm/l). While this value is somewhat high compared to typical physiological intracellular osmolarities (~280–295 mOsm), I understand it may not have impacted the current dataset substantially. However, please report the osmolarity also of the other solutions used for transport, slicing, recovery and recording (extracellular aCSF) for completeness.

2) Please include the quality criteria for inclusion of patch clamp recordings, including series resistance and the max % change of it at the end of the recording. Please also add the calculation of the liquid junction potential and if the RMP was corrected for it.

3) Please specify in the Methods section the membrane potential at which cells were held during current-clamp recordings. Additionally, indicate this value (i.e., the RMP) in the example traces in Figure 1D, both for the responses to current injections and for the spontaneous synaptic activity traces.

4) Line 423: the manuscript states that data from " a control rodent´s acute slice " were used for comparative purposes. However, it appears that the rodent dataset consists of only one slope value (n = 1). If so, this does not support statistical testing, as no variance can be estimated from a single observation - even if a standard deviation (SD = 5.68) is later reported. Unless multiple independent rodent data points are available, I recommend presenting this comparison descriptively, without inferential statistics. If instead this was a typo, please correct it and include also the sample size of rodent’s data in the figure legend.

Moreover, since the data were taken from a publication, please cite it also in the results section.

5) Line 427: minor typo in the value of r2.

6) Please review again the use of abbreviations for consistency. For example, the abbreviation “RS” (regular spiking) is used in the text but is not defined at first appearance (e.g., line 167). While it’s acceptable to remind the reader that IT-2 neurons are regular spiking, for clarity and consistency, please use either “IT-2 neurons” or “RS neurons/PCs” throughout. For instance, in the morphological analysis section, the term “RS PCs” appears, which may be confusing without consistent terminology.

7) Discussion: the authors compare RMP values across studies and relate it to the age limitation (range 2–30 years). However, such comparisons are inherently limited: RMP measurements in whole-cell patch clamp are strongly influenced by recording conditions, including pipette and bath solutions, series resistance, dialysis effects, and the often-uncompensated liquid junction potential. Without standardized protocols, direct comparisons of absolute RMP values between studies are not reliable. Furthermore, the cited age range may not represent a major limitation. Barzó et al. (2025, eLife) analyzed a large dataset of human L2/3 pyramidal neurons (from cortical tissue close to pathological lesion – but in line also with non-human primate and rodent studies) across the lifespan and showed that the most pronounced changes in passive properties, including RMP, occur early in life (before age 1), with relatively stable values beyond that. This suggests that developmental shifts in RMP are unlikely to confound comparisons within the 2–30-year range, provided the data were recorded consistently.

8) Please, be consistent also with citation style as sometimes (Last name et al, year) is provided instead of numbers.

Reviewer #3:  Review of “Layer V Neocortical Neurons From Individuals With Drug-Resistant Epilepsy Show Multiple Synaptic Alterations but Lack Somatic Hyperexcitability”

The authors performed whole-cell recordings from human layer-V pyramidal cells resected from the temporal, parietal, and frontal cortex in patients with drug-resistant epilepsy. Cells were classified as IT-2 (regular-spiking) and ET (intrinsic-bursting), with regional analyses primarily focused on IT-2 neurons. Using L I/II stimulation while recording in L Va, they measured presynaptic fiber volleys (FV) and field EPSPs. FV–fEPSP correlation was weak in human tissue but much stronger in a rodent control. A key finding is that 10-pulse, 30-Hz trains produced significant facilitation in the temporal cortex, whereas the frontal cortex showed only mild facilitation, and the parietal cortex showed none. These synaptic results were accompanied by more spontaneous postsynaptic events in the temporal cortex than in the other regions. In conclusion, the authors state that differences in synaptic properties, rather than cellular electrophysiology, underlie epilepsy.

The authors applied solid, classical methods and clearly state their aims. It is also important to enhance the human electrophysiological recording dataset, as done by the authors, rather than relying on a single dominant source of data. Nevertheless, several concerns arose during reading, some about the results themselves and others about the strength and framing of the conclusions. In some cases, the lack of proper control does not prevent publication but requires the authors to adjust their conclusion.

Major comments

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• SSA and time from resection (Figure 4G).

SSA appears highly related to elapsed time after surgery/slicing (larger immediately post-resection). Did the authors record the time from surgery to experiment for each neuron and analyze SSA versus this interval?

• Sag ratio (IT-2 vs ET).

Reported sag ratios (IT-2: 0.141 ± 0.072; ET: 0.164 ± 0.063) are smaller than expected from prior work and my own experience. Since rodents were also recorded, a rodent sag comparison could be informative. As it stands, the small difference raises concern that the ET vs IT-2 classification may be compromised.

• Input resistance of ET neurons.

ET Rin of 122 ± 24.1 MΩ seems high relative to prior studies (around 50 MΩ). This calls into question the classification and could impact conclusions about IT-2 properties. Please reconcile with the literature and methods.

• Rheobase.

Figures 2F and 2I appear inconsistent regarding rheobase. In Fig. 2I, the fitted curves suggest the smallest rheobase in parietal, not frontal, cortex. Fits in Fig. 2I should correspond to measured rheobases in Fig. 2F; please reconcile this mismatch, as it affects a main conclusion.

• “Loss of STD”.

The statement “These data suggest that frequency-dependent synaptic facilitation or the loss of STD in epileptic neocortex favors excitatory synaptic activity.” is not supportable without a proper control to link these changes to disease. Therefore, the conclusion should be reframed to avoid implying pathological loss without a proper control. Nevertheless, as I understand the difficulty in getting control tissue, therefore, it is important to underline that the results themselves are valuable.

• Morphology sample size.

Only four biocytin-filled RS PCs (from parietal and frontal cortex) were analyzed. Given known variability with depth, cortical folding, and location within a slice, even within a small region, this is insufficient for strong conclusions. The authors already considered this issue for reviewers #1 and #2, but unfortunately, the issue still stands. Namely, the similarity between the cells could be either statistically significant or not.

Important points

--------------------

• External Ca²⁺.

Because [Ca²⁺]o critically sets release probability, it can strongly alter short-term plasticity. Please, either provide a control demonstrating that your [Ca²⁺]o choice does not change the qualitative outcome, or discuss how different [Ca²⁺]o would impact interpretation.

• “Barely exhibited SSA at RMP.”

If PCs “barely exhibited SSA at their RMP,” what are the consequences for analyses that use SSA as a readout? Please clarify how SSA was ultimately used in Figure 4G.

• Rheobase vs threshold.

If rheobase differs across regions while RMP and Rin are similar, this implies a lower voltage threshold for AP initiation in the frontal cortex (≈ 60% closer to rest than the temporal). Can this be confirmed directly from existing data?

• “Higher global Na⁺ conductance in frontal PCs.”

Could differences in Na⁺ channel kinetics or subtype expression also explain the observations, beyond “global conductance”? A more nuanced report on the observation would help.

• AP dV/dt variance.

Reported slopes (e.g., −83.9 ± 37.1 mV/ms temporal; −48.2 ± 1.96 mV/ms parietal; −77.5 ± 27.4 mV/ms frontal) show a strikingly smaller SD in parietal neurons. Please explain this disparity.

• Human vs rodent slope comparison.

The statement that slopes differ significantly from the rodent control and therefore indicate “altered synaptic response dynamics” is hard to interpret. Why would human microcircuits be expected to match rodent slopes, given anatomical differences (layers and size proportions of the different layers)? Please justify or reframe.

• Use of predicted values.

In figure 4, the authors plot the FV-fEPSP predicted values (from the fitted line). I have to admit that understanding the reasoning for this plotting is not easy. Please consider a clarification for this panel not to burden the reader

• AIS identification.

“The axon’s initial segment was visually identified.” How was the end of the AIS determined? Please reference standard criteria for AIS identification.

Minor points

--------------

• The Introduction mentions “different neuronal mechanisms at different organizational levels.” Please define these levels explicitly.

• “Glutamatergic strength, the synchronicity between presynaptic volleys and field EPSPs, and short-term, frequency-dependent plasticity were determined at the synaptic level.” Please clarify this phrasing; synaptic properties are, by definition, at the synaptic level.

• “To explore a possible desynchronization… FV vs fEPSP slopes were correlated.” How is “desynchronization” defined here? Do you mean reduced coupling or statistical independence between the two signals?

• “≈ 65% of the recorded neurons belong to the IT-2 neurons…” Consider: “≈ 65% of recorded neurons belong to the IT-2 class/ were IT-2.”

• “Extracellular recordings in independent slices.” Please define “independent” (e.g., different patients, different blocks, or non-overlapping sites?).

• “Strong linear correlation and slope recovery… despite disorganized or desynchronized conditions.” The terms “disorganized” and “desynchronized” are not clear in this context. Please clarify, define precisely, or revise.

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Reviewer #2: Yes: Laura Monni

Reviewer #3: No

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Layer V Neocortical Neurons From Individuals With Drug-Resistant Epilepsy Show Multiple Synaptic Alterations but Lack Somatic Hyperexcitability

PONE-D-25-08682R2

Dear Dr. Galvan,

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Reviewer #2: All comments have been addressed

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Reviewer #2: (No Response)

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Reviewer #2: Yes: Laura Monni

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