Interstitial Ion Regulation in Cognitive Fatigability and Delayed Recovery: A Hypothesis-Driven Critical Review

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript entitled “Interstitial Ion Regulation in Cognitive Fatigability and Delayed Recovery: A Hypothesis-Driven Critical Review” aims to discuss the hypothesis that sustained cognitive demand progressively constrains the capacity to maintain and subsequently reconfigure the extracellular milieu. The manuscript is within the scope of the journal, and it is generally well prepared. The idea behind the paper is really interesting and important, but there are some issues that need to be clarified before the paper could be published. My specific comments are given below.

Although the central hypothesis is interesting and potentially significant, it seems a bit complex and not well supported by evidence in the literature in all its parts. The relationship between extracellular ionic milieu and cognitive fatigability is mainly derived from very different experimental models. The author should mark more clearly which evidence is directly demonstrated and which is hypothetical. To some extent, the author already does this, but it looks like there is a lot of inductive reasoning. It is important to avoid all formulations suggesting that the hypothesis has already been experimentally tested.

The manuscript would be easier to read if the propositions on the role of extracellular milieu in the development of cognitive fatigability during prolonged cognitive tasks and its potential role in delayed neurophysiological recovery were separated more clearly.

Some newer studies could be included in the manuscript, like https://doi.org/10.3390/jcm14103271 .

The authors should discuss more explicitly what differentiates the proposed extracellular-milieu framework from the existing alternative hypothesis.

The value of this manuscript lies in the fact that it proposes a testable hypothesis. That part could be further improved with more precise suggestions on which physiological parameters should be checked during prolonged cognitive tasks and recovery, what outcomes could be expected, and which results would support the proposed hypothesis.  

It is important that the author consistently uses the terms subjective fatigue, cognitive fatigability, neurophysiological recovery, and brain fatigue in order to clearly understand which model he is trying to explain.

Author Response

I thank the reviewer for recognizing the conceptual interest and potential significance of the manuscript. The revision preserves the proposed framework as a working hypothesis while making the distinction between direct evidence, mechanistic inference, and the integrated model more visible.

Comment 1

Although the central hypothesis is interesting and potentially significant, it seems a bit complex and not well supported by evidence in the literature in all its parts. The relationship between extracellular ionic milieu and cognitive fatigability is mainly derived from very different experimental models. The author should mark more clearly which evidence is directly demonstrated and which is hypothetical. To some extent, the author already does this, but it looks like there is a lot of inductive reasoning. It is important to avoid all formulations suggesting that the hypothesis has already been experimentally tested.

 

Response: I agree that the inferential boundary of the integrated hypothesis needed to be more visible. The revised manuscript now identifies the article as a non-systematic, hypothesis-driven Review; places the search scope and evidence hierarchy before the mechanistic argument; limits sleep–wake, movement, slice, genetic, and pathological studies to their appropriate evidence levels; and states explicitly in the Abstract and Conclusions that no direct test of the integrated demand–recovery–renewed-demand hypothesis under ordinary sustained cognitive demand was identified. Table 1 remains an evidence hierarchy rather than a list of studies that directly prove the hypothesis, and the working-hypothesis row carries no supporting citation. I also audited pivotal verbs and retained conditional language at the transitions from component mechanisms to cognitive fatigability.

Changes in the manuscript: “Within the literature examined, no direct test of this integrated hypothesis under ordinary sustained cognitive demand was identified.”

“Table 1 organizes the evidence by inferential distance and does not imply that the integrated hypothesis has already been tested.”

Location: Abstract, p. 1, lines 10–28; Section 1.1, p. 2, lines 8–27; Table 1, pp. 17–19; Section 7, p. 24, lines 31–49.

 

Comment 2

The manuscript would be easier to read if the propositions on the role of extracellular milieu in the development of cognitive fatigability during prolonged cognitive tasks and its potential role in delayed neurophysiological recovery were separated more clearly.

 

Response: I agree. The central hypothesis is now stated as two related but distinct propositions. The first concerns maintenance of an extracellular milieu that supports information processing during sustained demand. The second concerns delayed reconfiguration of that milieu after demand. Section 5.1 further separates extracellular-milieu reconfiguration from recovery of cellular responsiveness, functional recovery, and subjective recovery. The two routes remain connected within one temporal model but are not treated as the same phenomenon or measurement target.

Changes in the manuscript: “On this basis, this Review proposes that sustained cognitive demand progressively constrains the capacity to maintain an extracellular milieu that supports information processing during demand. A related but distinct proposition concerns delayed reconfiguration of that milieu afterward for rest, sleep, or renewed demand.”

Location: Section 1.2, p. 3, lines 20–33; Section 5.1, p. 12, lines 20–37; Section 5.6, p. 15, lines 47–50 and p. 16, lines 1–18; Figures 1 and 2, pp. 17 and 20.

 

Comment 3

Some newer studies could be included in the manuscript, like https://doi.org/10.3390/jcm14103271.

 

Response: Thank you for this recommendation. Johansson and Rönnbäck (2025) has been added as revised Reference 62. I use it as a recent clinical Brain Fatigue Syndrome framework and explicitly distinguish its focus on persistent symptoms in disease or injury contexts from the present Review’s focus on objective task-evoked cognitive fatigability and neurophysiological recovery over minutes to hours. It is therefore used for scope and framework comparison, not as direct evidence for ordinary-demand extracellular ionic mechanisms.

Changes in the manuscript: “The scope also differs from the clinical Brain Fatigue Syndrome framework proposed by Johansson and Rönnbäck [62], which addresses persistent symptoms in disease or injury contexts rather than objective task-evoked fatigability and neurophysiological recovery over minutes to hours.”

Location: Section 6.4, p. 23, lines 45–51 and p. 24, lines 1–4; Reference 62, p. 28, lines 15–16.

 

Comment 4

The authors should discuss more explicitly what differentiates the proposed extracellular-milieu framework from the existing alternative hypothesis.

 

Response: I agree. Section 6.4 now states explicitly what the present Review adds to the prior state-dependent interstitial-ion framework of Rasmussen et al., and how it differs in scope from the clinical framework of Johansson and Rönnbäck. It also compares the extracellular-milieu account with intracellular Cl⁻ regulation, adenosine signaling, local sleep, and synaptic homeostasis without subsuming those processes into the core ionic state. The distinguishing features of the present framework are the temporal connection between objective cognitive fatigability and delayed neurophysiological recovery, the separation of extracellular reconfiguration from cellular responsiveness, and prespecified predictive and causal outcomes during renewed demand.

Changes in the manuscript: “The present Review does not claim novelty for that physiological premise; it extends the framework to the temporal relation among objective cognitive fatigability during sustained demand, post-demand reconfiguration of the extracellular milieu, recovery of cellular responsiveness, and performance during renewed demand.”

Location: Section 5.4, p. 14, lines 16–50 and p. 15, lines 1–11; Section 6.4, p. 23, lines 45–51 and p. 24, lines 1–12; References 46–51, 60, and 62, pp. 27–28.

 

Comment 5

The value of this manuscript lies in the fact that it proposes a testable hypothesis. That part could be further improved with more precise suggestions on which physiological parameters should be checked during prolonged cognitive tasks and recovery, what outcomes could be expected, and which results would support the proposed hypothesis.

 

Response: I agree. The three core predictions have been retained, but their operational content has been strengthened. Section 6.2.2 now defines predictive “outperformance” using prespecified held-out or prospective evaluation with complexity control. Table 2 has been expanded from three to four columns by adding “Measurements and Prespecified Analysis,” which specifies measurement phases, trajectory features, comparison models, target engagement, and non-target monitoring. Section 6.3 now adds a compact discussion of ion-selective electrodes, real-time iontophoresis, optical K⁺ indicators, and the present limits of astrocytic voltage and Na⁺ measurements. The outcomes that would support or weaken each prediction remain specified in advance.

Changes in the manuscript: “Here, ‘outperform’ means a prespecified improvement in predictive performance in held-out or prospectively collected data after accounting for model complexity.”

Location: Section 6.2, p. 20, lines 14–37 and p. 21, lines 1–41; Table 2, p. 22; Section 6.3, pp. 22–23.

 

Comment 6

It is important that the author consistently uses the terms subjective fatigue, cognitive fatigability, neurophysiological recovery, and brain fatigue in order to clearly understand which model he is trying to explain.

 

Response: I agree. I completed a terminology audit across the manuscript. Cognitive fatigability remains the objectively measured time-dependent change during sustained demand; subjective fatigue remains a distinct experience; delayed neurophysiological recovery is now explicitly defined as persistent post-demand effects on brain dynamics, the extracellular milieu, or cellular responsiveness; and brain fatigue is explicitly retained as a broader umbrella term rather than a synonym for cognitive fatigability. In Section 5.1, physiological recovery, functional recovery, and subjective recovery are distinguished explicitly. The phrase “within-demand behavioral recovery” was changed to “within-demand behavioral rebound,” and the residual phrase “behavioral recovery” in the same discussion was changed to “behavioral improvement,” so that transient improvement during continuing demand is not confused with post-demand recovery.

Changes in the manuscript: “Here, delayed neurophysiological recovery refers to persistent post-demand effects on brain dynamics, the extracellular milieu, or cellular responsiveness. Brain fatigue is used only as a broader umbrella term, not as a synonym for cognitive fatigability.”

“Subjective recovery refers to a reduction in the experienced feeling of fatigue and should be distinguished from both physiological and functional recovery.”

Location: Abstract, p. 1, lines 10–28; Section 1.2, p. 3, lines 28–33; Section 5.1, p. 12, lines 6–37; Section 6.4, p. 24, lines 13–16; Section 7, p. 24, lines 31–49.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

I thank the author for a manuscript that I found genuinely engaging to read. Hypothesis reviews are difficult to write well, since the temptation is either to overstate the case until the hypothesis reads as an established mechanism, or to hedge so thoroughly that nothing testable survives. This manuscript largely avoids both failures. It develops a coherent argument that runs from sleep-wake ionic physiology, through K⁺-dependent membrane effects and astrocytic transport, to a temporal model of demand, recovery and renewed demand, and it closes with predictions that specify in advance what would count as evidence against it. The comments below are offered with a single aim: to help the author defend that argument before the referees and readers who will press it hardest.

Major concerns

1. Lines 271 to 276 correctly frame the mismatch between ionic processes operating on a millisecond-to-second scale and fatigability that develops over hours as the central unresolved problem and then leave it unresolved. Activity-dependent regulation of intracellular chloride is a use-dependent ionic mechanism that operates precisely on the intermediate timescale at issue (Alfonsa et al., Nat Neurosci 2023;26:64-78; Pracucci et al., Nat Commun 2023;14:7108; Alfonsa et al., Curr Biol 2025). Equally absent are the local sleep literature, extracellular adenosine as a sleep-pressure signal, and the synaptic homeostasis framework, even though Section 5.4 argues explicitly about sleep. I recommend a dedicated subsection on candidate temporal integrators, stating how the present framework relates to each, and naming at least one measurement capable of discriminating an extracellular-milieu account from a chloride-based or a local-sleep account.

 

2. Chloride is excluded without comment, which is difficult to sustain considering the preceding concern. Sodium is excluded as an extracellular variable, yet intracellular astrocytic Na⁺ becomes central both to Section 4.2 and to the two routes depicted in Figure 1. Brain temperature is treated as a confound to be monitored (line 841) rather than as a determinant of the milieu. Glutamate is formally excluded (line 388) and nonetheless receives subsections of its own. A short paragraph placed immediately after the definition, listing each exclusion together with its rationale, would resolve the inconsistency.

 

3. Section 6.3 outlines a staged design but does not link variables to techniques, nor does it acknowledge the limits of those techniques across a session lasting tens of minutes to hours: drift and point sampling in ion-selective microelectrode recordings; calibration of genetically encoded K⁺ indicators; the compatibility of real-time iontophoresis for extracellular space volume with a behaving animal; and the fact that astrocytic voltage and Na⁺ indicators have been applied in vivo largely under anesthesia. A paragraph, or a compact third table, would address this. The section should also state explicitly that the ionic predictions are rodent predictions and specify their human counterpart, given that references 3 and 40 concern brain dynamics and EEG rather than ionic composition.
4. Rasmussen, O'Donnell, Ding and Nedergaard (Prog Neurobiol, 2020) reviewed interstitial ions as regulators of state-dependent neural activity and is not cited, although several of its primary sources are. The reference should be included, accompanied by an explicit statement of what the present Review adds to it.

Minor concerns

1. The chain from Kir4.1 to membrane potential to EAAT driving force is presented twice in near-identical terms (lines 304 to 308 and 388 to 393); I suggest consolidating it in one location and cross-referencing the other. The locomotion-associated K⁺ rise of 0.6 to 1.0 mM is likewise introduced as a new finding on two separate occasions (lines 111 to 113 and 235 to 237).
2. This section would be better positioned earlier, ideally as Section 1.1, so that the reader encounters the non-systematic framing before the negative claims begin to do their work.
3. Abstract. A single clause should be added stating that this is a non-systematic hypothesis review for which no direct test has yet been identified. The Abstract should also carry the recommendation that astrocyte involvement be assessed through transport and extracellular variables rather than through Ca²⁺ alone, which at present appears nowhere in it.
4. The manuscript is single-authored yet uses "we" throughout, while the Author Contributions statement uses the singular. The plural sits particularly oddly on the sentences that advance negative claims.
5. Table 1. Supporting reference numbers should be added to each row. Several compound terms have lost hyphens or spaces in the proof ("statelinked", "firinghistory-dependent", "postdemand", "EAATdependent"); this appears to be a production artefact and should be checked at the proof stage.
6. Table 2. A third column naming the measurement and the analysis that would generate each outcome would considerably increase the table's usefulness.
7. Figure 1. The "altered" connector should be labelled with what is altered. The four-state timeline in panel A encodes state by color alone and would be uninterpretable in greyscale.
8. Lines 145 to 151.The tetrodotoxin result carries much of the weight of the bidirectional argument, and the text should state what it does not exclude, namely action-potential-independent transmitter release.
9. Lines 437 to 443. The BaCl₂ concentration should be given explicitly rather than described as "low-concentration".

Author Response

I am grateful to the reviewer for the generous assessment of the manuscript and for identifying the intermediate-timescale problem, the need for explicit operational boundaries, and the limitations of currently available measurements. The revision addresses these concerns while keeping the five-variable interstitial ionic state bounded and the integrated model explicitly hypothetical.

Major Comment 1

Lines 271 to 276 correctly frame the mismatch between ionic processes operating on a millisecond-to-second scale and fatigability that develops over hours as the central unresolved problem and then leave it unresolved. Activity-dependent regulation of intracellular chloride is a use-dependent ionic mechanism that operates precisely on the intermediate timescale at issue (Alfonsa et al., Nat Neurosci 2023;26:64-78; Pracucci et al., Nat Commun 2023;14:7108; Alfonsa et al., Curr Biol 2025). Equally absent are the local sleep literature, extracellular adenosine as a sleep-pressure signal, and the synaptic homeostasis framework, even though Section 5.4 argues explicitly about sleep. I recommend a dedicated subsection on candidate temporal integrators, stating how the present framework relates to each, and naming at least one measurement capable of discriminating an extracellular-milieu account from a chloride-based or a local-sleep account.

 

Response: I agree that the original manuscript identified the timescale gap without adequately examining candidate processes that could retain recent history over minutes to hours. Section 5.4 has therefore been expanded and retitled “Sleep and Candidate Temporal Integrators.” It now discusses neuronal intracellular Cl⁻/E_GABAA, extracellular adenosine, local neuronal OFF periods, and sleep-dependent synaptic homeostasis using the recommended primary studies. These processes are assigned distinct explanatory levels rather than being inserted into the core interstitial ionic state: intracellular Cl⁻ is treated as a cellular-responsiveness variable; adenosine as an upstream or parallel extracellular signal; local sleep as a network phenotype; and synaptic homeostasis as a parallel sleep-dependent reorganization mechanism. The section also proposes a discriminating design that compares the incremental predictive value of extracellular trajectories, intracellular Cl⁻, and local OFF periods, followed where feasible by selective recovery-phase manipulation.

Changes in the manuscript: “Here, candidate temporal integrator denotes a variable or process whose present state reflects recent activity over a longer interval and alters subsequent cellular or network responsiveness; it does not imply a single accumulating substance or an additional coordinate of the interstitial ionic state.”

Location: Section 3.2, p. 7, lines 13–22; Sections 5.3–5.4, p. 13, lines 34–51, p. 14, lines 1–50, and p. 15, lines 1–11; Section 5.6, p. 16, lines 8–18; Section 6.2.3, p. 21, lines 27–40; Section 6.4, p. 24, lines 5–12; References 46–51, p. 27, lines 31–42.

 

Major Comment 2

Chloride is excluded without comment, which is difficult to sustain considering the preceding concern. Sodium is excluded as an extracellular variable, yet intracellular astrocytic Na⁺ becomes central both to Section 4.2 and to the two routes depicted in Figure 1. Brain temperature is treated as a confound to be monitored (line 841) rather than as a determinant of the milieu. Glutamate is formally excluded (line 388) and nonetheless receives subsections of its own. A short paragraph placed immediately after the definition, listing each exclusion together with its rationale, would resolve the inconsistency.

 

Response: I agree that the original definition did not explain the selection and exclusion rules clearly enough. Immediately after the definition, the revised manuscript now states that the interstitial ionic state is an operational construct rather than an established physiological classification and gives the selection rationale for extracellular K⁺, Ca²⁺, Mg²⁺, pH, and extracellular space volume. It then distinguishes the broader extracellular milieu from this bounded state vector. Extracellular Na⁺, Cl⁻, glutamate, adenosine, metabolites, oxygen, and inflammatory mediators remain part of the broader milieu but are outside the selected core set; temperature and osmolarity are identified as physical determinants; and intracellular Na⁺ and Cl⁻ are classified as cellular-state variables. This resolves the category issue without implying that the excluded variables are unimportant or adding intracellular Cl⁻ to an extracellular construct.

Changes in the manuscript: “This is an operational construct, not an established physiological classification.”

“Other extracellular constituents … remain part of the broader extracellular milieu but are outside this selected core set. Temperature and osmolarity are additional physical determinants of that milieu. Intracellular Na⁺ and Cl⁻ are cellular-state variables rather than extracellular coordinates.”

Location: Section 1.2, p. 3, lines 1–14; Section 4.2, pp. 9–10; Section 5.3, p. 13, lines 29–42; Section 5.4, p. 14, lines 16–33.

 

Major Comment 3

Section 6.3 outlines a staged design but does not link variables to techniques, nor does it acknowledge the limits of those techniques across a session lasting tens of minutes to hours: drift and point sampling in ion-selective microelectrode recordings; calibration of genetically encoded K⁺ indicators; the compatibility of real-time iontophoresis for extracellular space volume with a behaving animal; and the fact that astrocytic voltage and Na⁺ indicators have been applied in vivo largely under anesthesia. A paragraph, or a compact third table, would address this. The section should also state explicitly that the ionic predictions are rodent predictions and specify their human counterpart, given that references 3 and 40 concern brain dynamics and EEG rather than ionic composition.

 

Response: I agree. Section 6.3 now links the principal variables to candidate methods and states the limitations most relevant to prolonged recordings: drift, reference instability, tissue disturbance, and point sampling for ion-selective electrodes; stable source–sensor geometry for real-time iontophoresis; in situ calibration, pH sensitivity, movement, photobleaching, and long-term stability for optical K⁺ indicators; and the fact that the cited astrocytic voltage measurements were obtained mainly in slices whereas the cited in vivo astrocytic Na⁺ measurements were obtained under anesthesia. RGEPO1 is cited as a promising awake-compatible optical method, but the text explicitly limits its demonstrated validity to seizure-related K⁺ transients rather than ordinary cognitive demand. The section now states directly that the ionic predictions are currently most feasible in rodents and that human behavioral, EEG, MEG, and magnetic-resonance trajectories are systems- or tissue-level counterparts rather than direct measures of local cortical interstitial ionic composition. A separate Table 3 was not added because the requested acquisition and analysis information could be accommodated in Section 6.3 and the expanded Table 2 without further expanding the manuscript.

Changes in the manuscript: “The astrocytic voltage measurements cited here were obtained mainly in slices, whereas the cited in vivo astrocytic Na⁺ measurements were obtained under anesthesia [35,36]; both therefore require separate validation for prolonged awake cognitive sessions.”

“The direct ionic predictions of this Review are presently most feasible in rodent models.”

Location: Table 2, p. 22; Section 6.3, p. 22, lines 3–20 and p. 23, lines 1–35; References 60 and 61, p. 28, lines 11–14.

 

Major Comment 4

Rasmussen, O'Donnell, Ding and Nedergaard (Prog Neurobiol, 2020) reviewed interstitial ions as regulators of state-dependent neural activity and is not cited, although several of its primary sources are. The reference should be included, accompanied by an explicit statement of what the present Review adds to it.

 

Response: Thank you for identifying this omission. Rasmussen et al. has been added as revised Reference 60 and is explicitly identified as the closest conceptual precedent for state-dependent interstitial-ion physiology. The revised manuscript does not claim novelty for the proposition that interstitial ions regulate brain state. It states that the present Review extends that premise to the temporal relation among objective cognitive fatigability during demand, post-demand extracellular reconfiguration, recovery of cellular responsiveness, and performance during renewed demand, with explicit supporting and weakening criteria.

Changes in the manuscript: “The present Review does not claim novelty for that physiological premise; it extends the framework to the temporal relation among objective cognitive fatigability during sustained demand, post-demand reconfiguration of the extracellular milieu, recovery of cellular responsiveness, and performance during renewed demand.”

Location: Section 6.4, p. 23, lines 45–51; Reference 60, p. 28, lines 11–12.

 

Minor Comment 1

The chain from Kir4.1 to membrane potential to EAAT driving force is presented twice in near-identical terms (lines 304 to 308 and 388 to 393); I suggest consolidating it in one location and cross-referencing the other. The locomotion-associated K⁺ rise of 0.6 to 1.0 mM is likewise introduced as a new finding on two separate occasions (lines 111 to 113 and 235 to 237).

 

Response: I agree. The detailed Kir4.1–membrane-potential–Na⁺-gradient–EAAT explanation is retained in Section 4.2. Section 3.4 now cross-references that location and focuses only on the reciprocal local coupling of K⁺ and glutamate release and clearance. Likewise, the quantitative 0.6–1.0 mM locomotion-associated K⁺ increase remains in Section 2.1; Section 3.1 now refers back to it rather than reintroducing it as a new result.

Changes in the manuscript: “As described in Section 2.1, the locomotion-associated cortical K⁺ rise began before movement onset.”

“The dependence of glutamate uptake on Kir4.1-supported astrocyte membrane potential and the transmembrane Na⁺ gradient is considered in Section 4.2.”

Location: Section 2.1, p. 4, lines 1–13; Section 3.1, p. 6, lines 24–39; Section 3.4, p. 8, lines 1–14; Section 4.2, p. 9, lines 31–50.

 

Minor Comment 2

This section would be better positioned earlier, ideally as Section 1.1, so that the reader encounters the non-systematic framing before the negative claims begin to do their work.

 

Response: I agree. The former unnumbered “Literature Search and Scope” section has been moved from the end of the manuscript to Section 1.1, immediately after the opening description of the two temporal phenomena. The search strategy, non-systematic framing, use of primary studies, evidence hierarchy, and scope of negative claims are therefore presented before the mechanistic argument. The detailed disclosure of how ChatGPT was used remains at the end of Section 1.1, which serves as the methods/scope section for this hypothesis-driven Review, while the product details remain in Acknowledgments. This two-part placement avoids duplicating the full statement while providing both the use details and product information.

Location: Section 1.1, p. 2, lines 8–27; Acknowledgments, p. 25, lines 10–13.

 

Minor Comment 3

Abstract. A single clause should be added stating that this is a non-systematic hypothesis review for which no direct test has yet been identified. The Abstract should also carry the recommendation that astrocyte involvement be assessed through transport and extracellular variables rather than through Ca²⁺ alone, which at present appears nowhere in it.

 

Response: I agree. The Abstract has been revised within the journal’s approximate 200-word limit. It now identifies the article as a non-systematic, hypothesis-driven Review, states that no direct test of the integrated hypothesis under ordinary sustained cognitive demand was identified, and states that astrocyte involvement should be assessed through transport and extracellular variables rather than Ca²⁺ alone.

Changes in the manuscript: “Astrocyte involvement should be assessed through transport and extracellular variables rather than Ca²⁺ alone.”

Location: Abstract, p. 1, lines 10–28.

 

Minor Comment 4

The manuscript is single-authored yet uses "we" throughout, while the Author Contributions statement uses the singular. The plural sits particularly oddly on the sentences that advance negative claims.

 

Response: I agree. All authorial first-person plural constructions have been removed from the manuscript. Depending on sentence function, they were replaced by “This Review,” “the hypothesis,” or an impersonal construction. A whole-document search confirmed that no authorial “we” remains. The response letter uses the first-person singular because it is written directly by the sole author.

Location: Global revision throughout the manuscript; no authorial first-person plural remains.

 

Minor Comment 5

Table 1. Supporting reference numbers should be added to each row. Several compound terms have lost hyphens or spaces in the proof ("statelinked", "firinghistory-dependent", "postdemand", "EAATdependent"); this appears to be a production artefact and should be checked at the proof stage.

 

Response: I agree. Representative references have been added to each empirical row of Table 1. No reference was added to the working-hypothesis row because no single study tests the integrated sequence. I also audited the Word file and rendered PDF for the cited spacing and hyphenation artifacts; the affected terms now appear as “state-linked,” “firing-history-dependent,” “post-demand,” and “EAAT-dependent.”

Location: Table 1, pp. 17–19; global Word and rendered-PDF audit.

 

Minor Comment 6

Table 2. A third column naming the measurement and the analysis that would generate each outcome would considerably increase the table's usefulness.

 

Response: I agree. Table 2 has been expanded from three to four columns by adding “Measurements and Prespecified Analysis.” This column specifies the repeated measurement phases, candidate trajectory features, held-out or blocked cross-validation, endpoint-appropriate predictive metrics, physiological target engagement, and monitoring of non-target effects. Measurements and analysis were combined in one column to preserve readability at the journal’s page width.

Location: Section 6.2, pp. 20–21; Table 2, p. 22.

 

Minor Comment 7

Figure 1. The "altered" connector should be labelled with what is altered. The four-state timeline in panel A encodes state by color alone and would be uninterpretable in greyscale.

 

Response: I agree. The connector is now labelled “altered cellular response,” specifying that the output evoked by the standardized input is altered. The figure also carries the visible statement “Non-exclusive working hypotheses; both routes may coexist.” Numbered markers (1–4) have been added to the Panel A timeline so that the temporal sequence is interpretable independently of color. The legend has been updated accordingly.

Location: Figure 1 and its legend, p. 17.

 

Minor Comment 8

Lines 145 to 151. The tetrodotoxin result carries much of the weight of the bidirectional argument, and the text should state what it does not exclude, namely action-potential-independent transmitter release.

 

Response: I agree. A narrow caveat has been added immediately after the tetrodotoxin result. It preserves the demonstrated observation while preventing the experiment from being interpreted as evidence for a purely non-neuronal mechanism.

Changes in the manuscript: “The tetrodotoxin result does not exclude action-potential-independent transmitter release or identify the cellular source of the K⁺ change.”

Location: Section 2.3, p. 4, lines 38–45.

 

Minor Comment 9

Lines 437 to 443. The BaCl₂ concentration should be given explicitly rather than described as "low-concentration".

 

Response: I agree. The concentration is now specified as 100 μM BaCl₂ in the discussion of the Walch et al. experiment. The surrounding text continues to distinguish the pharmacological manipulation from AQP4 deletion and Na⁺/K⁺-ATPase inhibition and does not describe the study as a Kir4.1 knockout. The final search also added Bakketun et al. (2026) to show that AQP4 involvement in K⁺-evoked swelling depends on K⁺ concentration and protocol.

Changes in the manuscript: “The initial astrocyte swelling persisted in aquaporin-4-deficient tissue and was not clearly reduced by 100 μM BaCl₂-mediated inhibition of inwardly rectifying K⁺ channels, whereas Na⁺/K⁺-ATPase inhibition attenuated it [16].”

Location: Section 4.3, p. 10, lines 30–40; References 16 and 37, pp. 26–27.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript " Interstitial Ion Regulation in Cognitive Fatigability and Delayed Recovery: A Hypothesis-Driven Critical Review’’ is an ambitious and conceptually interesting review that attempts to integrate findings from human cognitive-fatigue studies, sleep–wake physiology, extracellular ion regulation, astrocytic biology, neuronal excitability, metabolism, and recovery after sustained demand.  After going through the manuscript, I have following comments/suggestions for the author:

1. The author defines the interstitial ionic state as comprising extracellular K⁺; Ca²⁺; Mg²⁺; extracellular pH; and extracellular-space volume. This is conceptually interesting, but the choice of these variables appears author-defined rather than established recognized physiological construct. Hence, I would recommend the author to explicitly explain why these five variables were selected and why other extracellular variables were excluded. In addition, the author should also explain whether neurotransmitters, adenosine, lactate, oxygen, glucose, inflammatory mediators, osmolarity, etc., should be considered part of the same physiological state and whether extracellular-space volume should be included in an “ionic state.”
2. The manuscript distinguishes cognitive fatigability during demand from delayed neurophysiological recovery after demand. This distinction is important. However, ‘recovery’ is used at several different levels. This needs to be separated and the proposed “recovery” mechanism needs a clearer operational definition
3. The manuscript recognizes that increased astrocytic Ca²⁺ after demand does not necessarily indicate dysfunction. This should be carried more consistently throughout the manuscript with greater caution.
4. The author should explicitly explain why sleep–wake findings are mechanistically informative but not direct evidence for the cognitive-fatigue hypothesis.
5. The manuscript argues that a multivariable extracellular model should outperform a K⁺-only model. This is an attractive prediction, but “outperform” needs to be operationalized. What does this exactly mean - higher explained variance? better cross-validated prediction? lower prediction error? …….
6. The manuscript is conceptually dense. I would suggest shorter paragraphs and clearer topic sentences.
7. Figure 1 is useful conceptually, but the distinction between the two proposed routes should be visually emphasized as non-exclusive hypotheses, rather than established mechanisms.

Comments on the Quality of English Language

There are several grammatical, typographical and syntax issues in the manuscript.  The manuscript needs a thorough language correction.

Author Response

I thank the reviewer for the careful assessment of the manuscript’s conceptual boundaries and terminology. The revision makes the operational status of the five-variable state, the levels of recovery, and the predictive criteria more explicit without converting the Review into a systematic review or an all-inclusive model of brain fatigue.

Comment 1

The author defines the interstitial ionic state as comprising extracellular K⁺; Ca²⁺; Mg²⁺; extracellular pH; and extracellular-space volume. This is conceptually interesting, but the choice of these variables appears author-defined rather than established recognized physiological construct. Hence, I would recommend the author to explicitly explain why these five variables were selected and why other extracellular variables were excluded. In addition, the author should also explain whether neurotransmitters, adenosine, lactate, oxygen, glucose, inflammatory mediators, osmolarity, etc., should be considered part of the same physiological state and whether extracellular-space volume should be included in an “ionic state.”

 

Response: I agree. The revised definition now states explicitly that the interstitial ionic state is an operational construct and not an established physiological classification. The five variables were retained because they change coordinately across sleep–wake states, experimental manipulation of their composition alters local neural activity, and they directly shape excitability or the concentration change produced by ionic flux. Extracellular space volume remains included because it scales the concentration change produced by a given flux, although it is not itself an ion. The broader extracellular milieu now explicitly includes other ions, neurotransmitters, adenosine, metabolites, oxygen, and inflammatory mediators, while temperature and osmolarity are classified as physical determinants and intracellular Na⁺ and Cl⁻ as cellular-state variables.

Changes in the manuscript: “This is an operational construct, not an established physiological classification.”

Location: Section 1.2, p. 3, lines 1–14; Sections 4.2–4.4, pp. 9–11.

 

Comment 2

The manuscript distinguishes cognitive fatigability during demand from delayed neurophysiological recovery after demand. This distinction is important. However, ‘recovery’ is used at several different levels. This needs to be separated and the proposed “recovery” mechanism needs a clearer operational definition.

 

Response: I agree. Section 5.1 now distinguishes extracellular-milieu reconfiguration from recovery of cellular responsiveness to a standardized input under comparable extracellular conditions. It also separates physiological recovery from functional recovery and subjective recovery. A performance rebound observed while a task is still continuing is now described as a “within-demand behavioral rebound,” not as post-demand recovery. The manuscript further states that recovery need not mean return of every variable to a universal pre-demand point, because rest, sleep, and renewed demand may require different configurations.

Changes in the manuscript: “Within physiological recovery, this Review distinguishes reconfiguration of the extracellular milieu from recovery of cellular responsiveness to a standardized input under comparable extracellular conditions.”

Location: Section 5.1, p. 12, lines 6–37; Section 5.6, p. 15, lines 47–50 and p. 16, lines 1–18; Figure 1, p. 17.

 

Comment 3

The manuscript recognizes that increased astrocytic Ca²⁺ after demand does not necessarily indicate dysfunction. This should be carried more consistently throughout the manuscript with greater caution.

 

Response: I agree. The Ca²⁺ caution has been made explicit at the principal points where astrocytic Ca²⁺ is interpreted. The Abstract now states that astrocyte involvement should be assessed through transport and extracellular variables rather than Ca²⁺ alone. Section 2.3 now limits the noradrenaline result to modulation of astrocytic Ca²⁺ responses. Sections 4.2 and 5.2 state that Ca²⁺ or cAMP signals are not equivalent to preserved transport, dysfunction, or recovery, and Section 5.5 uses the boundary cases to show that Ca²⁺ magnitude does not map monotonically onto K⁺ clearance or neuronal recovery.

Changes in the manuscript: “Post-demand Ca²⁺ or cAMP persistence would therefore be a temporal signature rather than a direct measure of recovery or dysfunction.”

Location: Abstract, p. 1, lines 15–19; Section 2.3, p. 4, lines 46–48; Section 2.4, p. 5, lines 31–36; Section 4.2, p. 10, lines 12–19; Section 5.2, p. 13, lines 3–13; Section 5.5, p. 15, lines 13–32.

 

Comment 4

The author should explicitly explain why sleep–wake findings are mechanistically informative but not direct evidence for the cognitive-fatigue hypothesis.

 

Response: I agree. Section 2.2 now states directly that the cited studies examined sleep–wake transitions, movement, and sensory processing rather than cognitive fatigability during sustained demand or post-demand neurophysiological recovery. The following sentence preserves their proper role: they support the physiological principle that extracellular ionic changes can accompany brain states and alter subsequent neural activity. Section 5.4 retains the same boundary when discussing sleep-related candidate temporal integrators.

Changes in the manuscript: “These studies examined sleep–wake transitions, movement, and sensory processing rather than cognitive fatigability during sustained cognitive demand or post-demand neurophysiological recovery.”

Location: Section 2.2, p. 4, lines 31–35; Section 5.4, p. 14, lines 1–15.

 

Comment 5

The manuscript argues that a multivariable extracellular model should outperform a K⁺-only model. This is an attractive prediction, but “outperform” needs to be operationalized. What does this exactly mean - higher explained variance? better cross-validated prediction? lower prediction error? …….

 

Response: I agree. Section 6.2.2 now defines “outperform” as a prespecified improvement in predictive performance in held-out or prospectively collected data after accounting for model complexity. It provides endpoint-appropriate examples: lower root-mean-square error or mean absolute error, or higher out-of-sample R², for continuous outcomes, and lower log loss or Brier score for binary lapse outcomes. It also states that improved in-sample fit alone is insufficient. Table 2 applies the same criterion to the model-comparison prediction.

Changes in the manuscript: “Here, ‘outperform’ means a prespecified improvement in predictive performance in held-out or prospectively collected data after accounting for model complexity.”

Location: Section 6.2.2, p. 21, lines 1–15; Table 2, p. 22.

 

Comment 6

The manuscript is conceptually dense. I would suggest shorter paragraphs and clearer topic sentences.

 

Response: I agree with the need to reduce unnecessary conceptual density, but I addressed it selectively to avoid replacing a revision with a wholesale rewrite. The Introduction is now divided into “Literature Search and Scope” and “Rationale and Working Hypothesis.” Dense areas were separated by function, and the new material in Sections 5.4, 6.3, and 6.4 is organized into short paragraphs with explicit topic sentences. Existing paragraphs that already performed one scientific function were retained. Redundant descriptions of the locomotion-associated K⁺ rise and the Kir4.1–EAAT chain were removed rather than rewritten stylistically.

Location: Introduction, pp. 2–3; Sections 3.1 and 3.4, pp. 6 and 8; Section 5.4, pp. 13–15; Section 6.3, pp. 22–23; Section 6.4, pp. 23–24.

 

Comment 7

Figure 1 is useful conceptually, but the distinction between the two proposed routes should be visually emphasized as non-exclusive hypotheses, rather than established mechanisms.

 

Response: I agree. Figure 1 now states visibly, above both panels, “Non-exclusive working hypotheses; both routes may coexist.” The existing legend continues to state that the routes are working hypotheses and that the diagram does not imply causal ordering. The connector in Panel B has also been clarified as an “altered cellular response,” and the Panel A timeline is now numbered so that its sequence does not depend on color alone.

Location: Section 5.6, p. 15, lines 47–50 and p. 16, lines 1–18; Figure 1 and its legend, p. 17.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The author addressed all my comments. 

Author Response

I sincerely thank the reviewer for confirming that all previous comments have been satisfactorily addressed. No further scientific changes were required in response to this comment.

Reviewer 2 Report

Comments and Suggestions for Authors

Two items should be cleaned at proof stage. First, the Literature Search and Scope material now appears twice: as the new Section 1.1 and again as an unnumbered section immediately before Author Contributions. The two copies also carry different search cut-off dates, 6 September 2026 in Section 1.1 and 24 July 2026 in the duplicate. Please delete the duplicate and retain the later date. Second, the sentence in Section 1.2 beginning “A related but distinct proposition concerns delayed reconfiguration of and to reconfigure that milieu afterward for rest, sleep, or renewed demand” is ungrammatical, having retained fragments of both the original and the revised wording. Please restore it to a single clean sentence.

Section 6.4 lists reward valuation among the alternative mechanisms but does not engage it. Opportunity-cost and effort-based decision accounts predict the same behavioral signature the model predicts, namely increased reaction-time variability, lapses, and fluctuating accuracy, so a reader from that literature will not see where the two accounts part. One sentence naming an observation that would distinguish a capacity-constraint account from a cost-revaluation account is sufficient. Reference 58, already cited, supports the author's position and can carry the point. Once these two points are addressed, the manuscript is suitable for publication in its present form.

Author Response

Thank you for identifying these remaining points. I confirmed that the duplicate Literature Search and Scope material has been removed from the final manuscript and that the later search cut-off date of 6 September 2026 is retained. I also confirmed that the sentence in Section 1.2 now reads as a single grammatical sentence:

“A related but distinct proposition concerns delayed reconfiguration of that milieu afterward for rest, sleep, or renewed demand.”

I also agree that the distinction from opportunity-cost or effort-based decision accounts should be made explicit. I therefore added one sentence to Section 6.4 specifying a discriminating observation:

“A capacity-constraint account would be favored if time-on-task performance instability persisted despite preserved task engagement, as observed in the rodent continuous performance test [58], and tracked physiological recovery trajectories; by contrast, rapid normalization after changing reward or effort costs without corresponding physiological recovery would favor a cost-revaluation account.”

Reference 58 is used only to support the observation that time-on-task performance decrements can persist despite preserved task engagement; the contrast involving reward or effort manipulation is presented as a testable prediction rather than as a result already demonstrated by that study.

Reviewer 3 Report

Comments and Suggestions for Authors

Thank you for addressing my comments. I am happy with your review. However, I would suggest a thorough language check and formatting adjustment for better readeability of the manuscript.

Comments on the Quality of English Language

There are several grammatical, typographical and syntax issues in the manuscript.  The manuscript needs a thorough language correction.

Author Response

Thank you very much for your positive assessment. I performed a final language and formatting check throughout the manuscript, including grammar, sentence structure, terminology, hyphenation, table layout, figure legends, reference formatting, and paragraph/page layout. No substantive scientific changes were introduced during this final editorial pass.