Polyfunctionalized N-Arylsulfonyl Indoles: Identification of (E)-N-Hydroxy-3-{3-[(5-(3-(piperidin-1-yl)propoxy]-1H-indol-1-yl)sulfonyl]phenyl}acrylamide (MTP150) for the Epigenetic-Based Therapy of Parkinson’s Disease

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript presents the synthesis and in vitro evaluation of a new series of multitarget small molecules (MSMs), especially MTP150. While the chemical characterization and enzymatic assays are well-documented, the biological validation in in vivo and in vitro models of neurodegenerative diseases (AD, PD, HD) is highly superficial and lacks the necessary mechanistic depth. There are significant logical gaps between the claims made in the Abstract and the actual data provided in the Results section.

1. Major Concern: The title identifies MTP150 as a "5HT6R multitarget small molecule", yet the manuscript provides no experimental evidence to confirm that this receptor contributes to the observed therapeutic effects in any biological model:

• The affinity for 5HT6R is much weaker than the potency for HDAC1, indicating that the observed phenotypic rescue (e.g., locomotor activity in worms or viability in cells) is more likely to be driven by the inhibition of HDACs rather than 5HT6R.
• The manuscript fails to demonstrate target engagement for 5HT6R in vivo. None of the biological models used (C. elegans, Drosophila, or SH-SY5Y cells) are genetically or pharmacologically 5HT6R -relevant models.

2. The Abstract claims that MTP150 is effective in "reducing protein aggregation, modulating matrix metalloproteinase activity, mitigating neuroinflammation, and enhancing DNA damage repair pathways" in C. elegans models. However, Figure 4 only provide "Activity counts". There is no experimental evidence (imaging or biochemical assays) to support the claims of “reduced protein aggregation, MMP modulation, or DNA repair in the worm models”.
3. The strains, CL2006 (AD), BR3579 (PD), and EAK103 (HD), are specifically designed to express Aβ, α-syn, and PolyQ accumulation. Relying solely on locomotor activity is insufficient to distinguish between a symptomatic effect (possibly due to AChE/5-HT6R/HDAC6 modulation) and a true disease-modifying effect. The authors failed to use target-specific controls, such as target-null mutants or RNAi-treated worms (e.g., hda-6 knockdown), to prove that the observed efficacy is target-dependent. And α-tubulin acetylation should be observed.
4. In DJ-1β Drosophila PD Model, the gold standard for neuroprotection is the survival of dopaminergic neurons. The authors only report climbing ability and ATP levels, which does not constitute proof of neuroprotection. TH-staining of fly brains may be necessary.
5. For DJ-1β deficiency SH-SY5Y model, mitochondrial functional markers, such as mitochondrial membrane potential, mtROS, etc., were omitted in favor of simple MTT viability assays.
6. Figure 7B shows that MTP150 has no effect on control (pLKO.1) cells under oxidative stress. If the drug acts through general pathways like HDAC inhibition or DNA repair, a baseline protective effect in control cells would be expected.

Author Response

The manuscript presents the synthesis and in vitro evaluation of a new series of multitarget small molecules (MSMs), especially MTP150. While the chemical characterization and enzymatic assays are well-documented, the biological validation in in vivo and in vitro models of neurodegenerative diseases (AD, PD, HD) is highly superficial and lacks the necessary mechanistic depth. There are significant logical gaps between the claims made in the Abstract and the actual data provided in the Results section.

1. Major Concern: The title identifies MTP150 as a "5HT6R multitarget small molecule", yet the manuscript provides no experimental evidence to confirm that this receptor contributes to the observed therapeutic effects in any biological model: Reviewer is right. This is why we have corrected the title of the article.

• The affinity for 5HT6R is much weaker than the potency for HDAC1, indicating that the observed phenotypic rescue (e.g., locomotor activity in worms or viability in cells) is more likely to be driven by the inhibition of HDACs rather than 5HT6R: Reviewer is right. This is why we have corrected the title of the article, and retained the mention to “…for the epigenetically-based therapy…”, in the title.
• The manuscript fails to demonstrate target engagement for 5HT6R in vivo. None of the biological models used (C. elegans, Drosophila, or SH-SY5Y cells) are genetically or pharmacologically 5HT6R -relevant models: Reviewer is right, but as molecule MTP150 is multitarget, it han been imposible to focus in a genetically or pharmacologically 5HT6R -relevant model. This is why we have chosen a more general in vivo suitable model.

1. The Abstract claims that MTP150 is effective in "reducing protein aggregation, modulating matrix metalloproteinase activity, mitigating neuroinflammation, and enhancing DNA damage repair pathways" in C. elegans models. However, Figure 4 only provide "Activity counts". There is no experimental evidence (imaging or biochemical assays) to support the claims of “reduced protein aggregation, MMP modulation, or DNA repair in the worm models”: Please se below (response to point 3).
2. The strains, CL2006 (AD), BR3579 (PD), and EAK103 (HD), are specifically designed to express Aβ, α-syn, and PolyQ accumulation. Relying solely on locomotor activity is insufficient to distinguish between a symptomatic effect (possibly due to AChE/5-HT6R/HDAC6 modulation) and a true disease-modifying effect. The authors failed to use target-specific controls, such as target-null mutants or RNAi-treated worms (e.g., hda-6 knockdown), to prove that the observed efficacy is target-dependent. And α-tubulin acetylation should be observed: These C. elegans experiments were conducted as a proof of concept to evaluate the overall neuroprotective ability of MTP150 across various neurodegenerative models. They were not intended to explore target dependence in detail or to definitively classify the effects as strictly disease-modifying. While demonstrating target specificity in vivo—such as using target-null mutants or RNAi techniques like hda-6 knockdown and directly assessing α-tubulin acetylation—would be valuable, a comprehensive mechanistic analysis of each target’s role was beyond this study's scope. Such investigations will be pursued in future dedicated research.
3. In DJ-1β Drosophila PD Model, the gold standard for neuroprotection is the survival of dopaminergic neurons. The authors only report climbing ability and ATP levels, which does not constitute proof of neuroprotection. TH-staining of fly brains may be necessary: While we cannot fully exclude the possibility that DJ-1β mutant flies exhibit functional alterations in dopaminergic (DA) neurons, both our previous work and independent studies have consistently demonstrated the absence of detectable DA neurodegeneration in DJ-1β mutant brains (Lavara-Culebras and Paricio, 2007; Park et al., 2005). Therefore, DA neuron loss is not an expected or defining feature of this Drosophila PD model, and neuronal survival cannot be used as a primary readout of neuroprotection in this context. Instead, DJ-1β mutants are well known to display robust PD-relevant phenotypes including locomotor impairment, oxidative stress, and mitochondrial dysfunction. Accordingly, we assessed climbing performance, and protein carbonylation levels (as a validated marker of oxidative stress), since increased protein carbonylation has previously been shown to play a causal role in the motor deficits of PD model flies (Sanz et al., 2017). We additionally measured ATP levels as a functional indicator of mitochondrial status. Our results demonstrate that MTP150 supplementation significantly improves climbing ability, reduces oxidative damage, and restores mitochondrial function, all of them being PD-relevant phenotypes in this model.
4. For DJ-1β deficiency SH-SY5Y model, mitochondrial functional markers, such as mitochondrial membrane potential, mtROS, etc., were omitted in favor of simple MTT viability assays: In this experiment, our objective was specifically to demonstrate the neuroprotective effect of MTP150 in DJ-1-deficient human cells, thereby providing complementary support for the results obtained in the Drosophila PD model. Accordingly, we employed a viability-based assay as a direct and robust readout of overall cellular protection, rather than performing an extensive characterization of mitochondrial functional parameters, which was beyond the primary scope of this validation experiment.
5. Figure 7B shows that MTP150 has no effect on control (pLKO.1) cells under oxidative stress. If the drug acts through general pathways like HDAC inhibition or DNA repair, a baseline protective effect in control cells would be expected: While we acknowledge the reviewer’s comment, our results clearly demonstrate that MTP150 exerts a protective effect in DJ-1–deficient human PD model cells, which was the primary objective of this experiment. In this context, the absence of a significant effect in control (pLKO.1) cells under oxidative stress does not contradict our conclusions; it rather suggests that the compound preferentially rescues disease-related vulnerability instead of producing a nonspecific protective effect in otherwise normal cells. This disease-selective protection is, in fact, more relevant for therapeutic purposes than a generalized cytoprotective action in control cells.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript entitled “Polyfunctionalized N-arylsulfonyl indoles as 5-HT6R multitarget small molecules: Identification of (E)-N-Hydroxy-2-{3-[(5-(3-(piperidin-1-yl)propoxy)]-1H-indol-1-yl)sulfonyl]phenyl}acrylamide (MTP150) for the epigenetically based therapy of Parkinson’s disease” presents an interesting and well-designed study. The topic is clearly within the scope of the International Journal of Molecular Sciences, and the work makes a valuable contribution to the field of multitarget drug design for neurodegenerative diseases.

The manuscript is generally well written and scientifically sound. I therefore recommend publication after minor revision, mainly aimed at improving clarity, consistency, and presentation.

Minor comments and suggestions:

There is a notable inconsistency in compound numbering throughout the manuscript, which reduces readability and overall clarity. Some previously synthesized compounds are assigned numbers in Figure 2 (e.g., MTP150 (12), APP19 (13)), but these numbers are not consistently used in Tables 1, 2, or 5. It is unclear why certain compounds receive numbers while others do not. Newly synthesized derivatives are often presented with both code names and numbers, while in the discussion of results only numbers are used. I recommend establishing a clear and consistent numbering scheme for all compounds and applying it uniformly across figures, tables, and text.

Figure 2: The chemical structures are not consistently formatted; bond thicknesses and drawing styles vary. I recommend standardizing all structures for visual consistency.

Figure 3: Some compounds are not properly aligned with their corresponding substituents. Adjusting the layout would improve clarity and interpretation.

The presentation of results in Table 1 is not sufficiently clear, making it difficult to follow structure - activity relationships. For example, the piperazinyl derivative MTP100 is listed at the end of the table, separated from its related analogs. To improve clarity, I suggest including a general scaffold above the table and organizing the data to clearly display substituent variations (at the two modified positions) alongside the corresponding Kᵢ values.

Additionally, chemical structures within the table are consistent in style but vary in size. The same issue is observed in Table 2. I recommend standardizing structure sizes and improving the overall presentation of the results. For compounds whose Kᵢ values were previously reported, references are not consistently indicated. Citations should follow the journal style (e.g., as superscripts) and should be corrected throughout.

Scheme 1 is difficult to follow due to its complexity. I recommend splitting it into two separate schemes or panels and presenting the reactions in a more linear fashion to improve readability.

The β symbol in Aβ₁–₄₂ appears to be incorrectly rendered in the manuscript, likely due to font or encoding issues. Similar problems are observed for other symbols, including the σ symbol in hσ₁R and concentration units (e.g., HDAC6 IC₅₀ = 0.017 μM). Please carefully check the font/encoding and correct all affected symbols consistently throughout the text.

Compound numbers are inconsistently formatted (bold vs. non-bold) in different sections. The formatting of hAChE is inconsistent (italic vs. non-italic “h”). Units are not consistently written (e.g., mL vs. ml). All formatting should be standardized according to journal style.There are several instances where the “=” sign is inconsistently spaced or formatted (e.g., Ki for MTP100 = 3392 nM). This issue may also occur for other numerical values. Please standardize numerical formatting throughout the manuscript.

 

There are minor typographical errors, such as 13NME instead of 13CNMR.

In the Experimental section, KOH is reported as "with KOH (2 mL, 4.34 mmol)". Since KOH is a solid, either the mass should be reported or, if a solution was used, the concentration (e.g., 2M KOH) should be specified. Please verify and correct accordingly.

Minor discrepancies in reagent calculations were also noted (e.g., benzenesulfonyl chloride (0.33 mL, 2.61 mmol) should correspond to 2.58 mmol). I recommend carefully checking all reagent amounts and calculations for consistency and accuracy.

The formatting of page numbers in the reference list should be standardized, as different conventions are currently used (first page only vs. page range).

Overall, the work is interesting, clearly written, and well aligned with the journal’s scope. After addressing the above minor issues related to consistency, formatting, and presentation, the manuscript will be significantly improved. I therefore recommend publication after minor revision.

 

 

Author Response

The manuscript entitled “Polyfunctionalized N-arylsulfonyl indoles as 5-HT6R multitarget small molecules: Identification of (E)-N-Hydroxy-2-{3-[(5-(3-(piperidin-1-yl)propoxy)]-1H-indol-1-yl)sulfonyl]phenyl}acrylamide (MTP150) for the epigenetically based therapy of Parkinson’s disease” presents an interesting and well-designed study. The topic is clearly within the scope of the International Journal of Molecular Sciences, and the work makes a valuable contribution to the field of multitarget drug design for neurodegenerative diseases.

The manuscript is generally well written and scientifically sound. I therefore recommend publication after minor revision, mainly aimed at improving clarity, consistency, and presentation.

Minor comments and suggestions:

There is a notable inconsistency in compound numbering throughout the manuscript, which reduces readability and overall clarity. Some previously synthesized compounds are assigned numbers in Figure 2 (e.g., MTP150 (12), APP19 (13)), but these numbers are not consistently used in Tables 1, 2, or 5. It is unclear why certain compounds receive numbers while others do not. Newly synthesized derivatives are often presented with both code names and numbers, while in the discussion of results only numbers are used. I recommend establishing a clear and consistent numbering scheme for all compounds and applying it uniformly across figures, tables, and text Thanks and corrected.The compounds have been re-numbered.

Figure 2: The chemical structures are not consistently formatted; bond thicknesses and drawing styles vary. I recommend standardizing all structures for visual consistency: Thanks and corrected.

Figure 3: Some compounds are not properly aligned with their corresponding substituents. Adjusting the layout would improve clarity and interpretation Thanks and corrected.

The presentation of results in Table 1 is not sufficiently clear, making it difficult to follow structure - activity relationships. For example, the piperazinyl derivative MTP100 is listed at the end of the table, separated from its related analogs. To improve clarity, I suggest including a general scaffold above the table and organizing the data to clearly display substituent variations (at the two modified positions) alongside the corresponding Kᵢ values Thanks and corrected..

Additionally, chemical structures within the table are consistent in style but vary in size. The same issue is observed in Table 2. I recommend standardizing structure sizes and improving the overall presentation of the results. For compounds whose Kᵢ values were previously reported, references are not consistently indicated. Citations should follow the journal style (e.g., as superscripts) and should be corrected throughout Thanks and corrected..

Scheme 1 is difficult to follow due to its complexity. I recommend splitting it into two separate schemes or panels and presenting the reactions in a more linear fashion to improve readability Thanks and corrected as suggested, incorporating three schemes.

The β symbol in Aβ₁–₄₂ appears to be incorrectly rendered in the manuscript, likely due to font or encoding issues. Similar problems are observed for other symbols, including the σ symbol in hσ₁R and concentration units (e.g., HDAC6 IC₅₀ = 0.017 μM). Please carefully check the font/encoding and correct all affected symbols consistently throughout the text. Thanks and corrected.

Compound numbers are inconsistently formatted (bold vs. non-bold) in different sections. The formatting of hAChE is inconsistent (italic vs. non-italic “h”). Units are not consistently written (e.g., mL vs. ml). All formatting should be standardized according to journal style.There are several instances where the “=” sign is inconsistently spaced or formatted (e.g., Ki for MTP100 = 3392 nM). This issue may also occur for other numerical values. Please standardize numerical formatting throughout the manuscript Thanks and corrected.

 

There are minor typographical errors, such as 13NME instead of 13CNMR: Thanks and corrected.

In the Experimental section, KOH is reported as "with KOH (2 mL, 4.34 mmol)". Since KOH is a solid, either the mass should be reported or, if a solution was used, the concentration (e.g., 2M KOH) should be specified. Please verify and correct accordingly Thanks and corrected.

Minor discrepancies in reagent calculations were also noted (e.g., benzenesulfonyl chloride (0.33 mL, 2.61 mmol) should correspond to 2.58 mmol). I recommend carefully checking all reagent amounts and calculations for consistency and accuracy: Thanks and corrected.

The formatting of page numbers in the reference list should be standardized, as different conventions are currently used (first page only vs. page range): Thanks. Nowadays, it depends on the Journal.

Overall, the work is interesting, clearly written, and well aligned with the journal’s scope. After addressing the above minor issues related to consistency, formatting, and presentation, the manuscript will be significantly improved. I therefore recommend publication after minor revision.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript describes the extensive medicinal chemistry optimization and biological characterization of MTP150, a polyfunctionalized N-arylsulfonyl indole derivative emerging as a lead multitarget small molecule for Parkinson’s disease. The authors demonstrate that MTP150 exhibits balanced in vitro activities against HDAC1/6, cholinesterases, MAO-B, and 5-HT6R, favorable BBB permeability, and in vivo efficacy in both C. elegans (AD, PD, HD) and DJ-1β Drosophila models, along with neuroprotective effects in human SH-SY5Y cells. However, despite the impressive scope and interdisciplinary nature of the work, several critical issues regarding experimental design, data interpretation, inconsistencies between main text and supplementary materials, SAR rationale, and statistical rigor need to be addressed before the manuscript can be considered for publication.

1. The most significant concern is the pharmacological relevance of the claimed 5-HT6R activity. According to Table 2, MTP150 has a Ki of 13,580 nM (13.58 µM) for 5-HT6R. This is conventionally considered very weak or inactive for a receptor target. How can such micromolar affinity be mechanistically linked to the observed in vivo efficacy, especially when brain exposure of unbound drug is likely orders of magnitude lower?
2. There is a clear discrepancy between the main text and the supplementary materials regarding MTP150’s HDAC6 activity. The manuscript states MTP150 is a potent HDAC6 inhibitor (IC50 = 0.040 µM), yet the supplementary docking section explicitly states that "docking models indicate that the interactions of the cap group with the surface of HDAC6 hinder the proper approach of the metal-binding moiety to the zinc ion, predicting limited biological activity for compound MTP150 with HDAC6." Please explain this fundamental contradiction between experimental data and computational prediction.
3. The reported Ki values for 5-HT6R binding assays (Tables 1 and 2) show very large standard deviations in several cases (e.g., MTP155: 57,960 ± 13,135; MTP86: 6,770 ± 1,471). These represent relative errors of 20–30%. Given that each compound was tested in only two technical replicates (no mention of biological replicates in the legend), how was assay reproducibility and statistical significance ensured?
4. The decision-making process for compound selection appears circular. The authors state that compounds of type III (14-20) were designed based on results from type I and II, yet these new compounds (with the exception of 19 for BuChE) show universally poor or no activity. The authors then state "we have reconsidered the Contilisant hybrids of type I and II for further investigation." This suggests the rational design of type III failed. What specific SAR lessons were learned from this negative dataset, and how will this inform future design?
5. Regarding the synthesis: the yield for hydroxamate 14 is only 6%, yet the compound was carried forward for biological testing. What was done to confirm the purity and correct identity of this batch, given that typical purity criteria is ≥95%? Was the low yield reproducible, or is this an isolated result that raises concerns about the reliability of this synthetic route?
6. The PAMPA-BBB data (Table 4 and 5) show MTP100 is "poorly dissolved, turbid at 50% in DMSO" and is classified as CNS-. However, the experimental permeability value for MTP100 is 1.6 ± 0.3, while Vorinostat is 1.8 ± 0.25 and is also CNS-. Given the standard deviations, these values are statistically indistinguishable. What is the justification for using a hard threshold (5.050 for CNS+) when the assay shows such variability, and why was MTP100 excluded while borderline compounds were retained?
7. In Figure 4, the C. elegans locomotor activity data shows significance at non-monotonic doses (e.g., PD model: significant at 0.01 µM and 1 µM, but not at 0.1 µM and 10 µM). This inverted U-shaped curve is not discussed. Was this observed consistently across replicates? How do the authors interpret this lack of clear dose-response?
8. The SH-SY5Y cytotoxicity data (Figure 6) indicates that MTP150 significantly reduces viability at concentrations >1 µM, yet the neuroprotection experiments (Figure 7A) were conducted using concentrations up to 0.1 µM well below this threshold. However, the Drosophila in vivo studies used 1 µM and 10 µM doses. Given that the fly food contains the compound throughout larval development, how do the authors reconcile the fact that 10 µM is clearly cytotoxic in human cells but is the most effective dose in flies? Was compound bioaccumulation or metabolic activation/deactivation considered?
9. In the HDAC inhibition methods, it is noted that for HDAC1, "inhibitor and enzyme were preincubated at 25 °C for 60 min." No such preincubation is mentioned for HDAC6. Since HDAC1 and HDAC6 inhibition potencies are directly compared to support the claim of balanced inhibition, why were different preincubation conditions used? Could the longer preincubation for HDAC1 artificially increase the apparent potency against this isoform?
10. The supplementary molecular docking for compound 15 (Figures 3S and 4S) shows the ligand "remains at the entrance" of HDAC1 and HDAC6. However, the method section states that "flexible residues" were used, including catalytic channel residues. If the docking protocol correctly models flexibility, why does the ligand not sample deeper binding poses? Was an induced-fit docking or molecular dynamics simulation considered to validate that this truly reflects an inability to bind, rather than a limitation of rigid or semi-flexible docking?
11. Regarding the claimed "epigenetically-based therapy": the manuscript demonstrates that MTP150 inhibits HDAC1 and HDAC6 in vitro and has phenotypic effects in disease models. However, there is no direct evidence presented that these phenotypic effects are actually mediated by HDAC inhibition (e.g., measurement of histone acetylation levels, target engagement studies, or rescue experiments with HDAC overexpression). Given the compound is multitarget, how can the authors confidently attribute the in vivo efficacy specifically to epigenetic mechanisms?
12. In the ADME section (Supplementary Materials, Table S1), the authors report that the compound violates no Lipinski rules, yet the accptHB (estimated number of hydrogen bonds accepted) is 11.45, which is far above the typical QikProp recommended maximum of 6.0. The authors acknowledge this but do not discuss its potential impact on permeability or efflux. Given that the compound shows only moderate predicted oral absorption (65.8%), isn’t this high polar surface area and HB acceptor count a significant liability for a CNS drug?
13. The manuscript repeatedly refers to "Contilisant" and "Contilistat" interchangeably and inconsistently across text and figures (e.g., Figure 1 labels 3 as "Contilistat", but text describes "Contilisant (1)" and "Contilistat (3)"). This is confusing for readers not intimately familiar with the authors' previous work. Please standardize nomenclature.
14. Regarding statistical analysis: for the C. elegans studies, the authors used one-way ANOVA with Dunnett’s post-hoc test for multiple comparisons against a single control. This is appropriate. However, for the Drosophila studies (Figure 5), one-way ANOVA with Tukey’s test was used to compare all groups. Given that there are only three groups (vehicle, 1 µM, 10 µM), and the comparison of interest is each dose vs. vehicle, Dunnett’s test would be more statistically powerful. Why was Tukey’s chosen? Additionally, no correction for multiple testing (e.g., Bonferroni) is mentioned for the numerous comparisons in Tables 1,2,4,5. Was any multiplicity adjustment applied?

Author Response

This manuscript describes the extensive medicinal chemistry optimization and biological characterization of MTP150, a polyfunctionalized N-arylsulfonyl indole derivative emerging as a lead multitarget small molecule for Parkinson’s disease. The authors demonstrate that MTP150 exhibits balanced in vitro activities against HDAC1/6, cholinesterases, MAO-B, and 5-HT6R, favorable BBB permeability, and in vivo efficacy in both C. elegans (AD, PD, HD) and DJ-1β Drosophila models, along with neuroprotective effects in human SH-SY5Y cells. However, despite the impressive scope and interdisciplinary nature of the work, several critical issues regarding experimental design, data interpretation, inconsistencies between main text and supplementary materials, SAR rationale, and statistical rigor need to be addressed before the manuscript can be considered for publication.

1. The most significant concern is the pharmacological relevance of the claimed 5-HT6R activity. According to Table 2, MTP150 has a Ki of 13,580 nM (13.58 µM) for 5-HT6R. This is conventionally considered very weak or inactive for a receptor target. How can such micromolar affinity be mechanistically linked to the observed in vivo efficacy, especially when brain exposure of unbound drug is likely orders of magnitude lower?: MTP150 is a multitarget compound being active in other biological targets as demonstrated, and possibly in other ones not investigated by us; so, the whole pharmacological power of MTP150 should be considered.

 

1. There is a clear discrepancy between the main text and the supplementary materials regarding MTP150’s HDAC6 activity. The manuscript states MTP150 is a potent HDAC6 inhibitor (IC50 = 0.040 µM), yet the supplementary docking section explicitly states that "docking models indicate that the interactions of the cap group with the surface of HDAC6 hinder the proper approach of the metal-binding moiety to the zinc ion, predicting limited biological activity for compound MTP150 with HDAC6." Please explain this fundamental contradiction between experimental data and computational prediction: We thank the reviewer for this observation. There is no actual discrepancy between the experimental and computational data, although the wording in the supplementary section may not have been fully clear. What we intended to convey is that the zinc coordination mode differs between HDAC1 and HDAC6. In HDAC1, the interaction is bidentate, whereas in HDAC6 it is monodentate. Consequently, the statement that “the interactions of the cap group with the surface of HDAC6 hinder the proper approach of the metal-binding moiety to the zinc ion” reflects the fact that MTP150 does not form a bidentate interaction with HDAC6, which is consistent with the lower inhibitory activity observed for HDAC6 compared to HDAC1. To clarify this point, an explanatory statement has been added in the revised Supplementary Materials text, as follows: “Docking models indicate that in HDAC6, the interactions of the cap group with the enzyme surface hinder the proper approach of the metal-binding moiety to the zinc ion preventing bidentate coordination, resulting in a monodentate interaction which explains the lower inhibitory activity of MTP150 against HDAC6 compared to HDAC1”.

 

 

1. The reported Ki values for 5-HT6R binding assays (Tables 1 and 2) show very large standard deviations in several cases (e.g., MTP155: 57,960 ± 13,135; MTP86: 6,770 ± 1,471). These represent relative errors of 20–30%. Given that each compound was tested in only two technical replicates (no mention of biological replicates in the legend), how was assay reproducibility and statistical significance ensured?>: Thank you for the comment. Ki values are reported as mean ± SD of two technical replicates (duplicate 8-point concentration-response curves). Ki is derived from one-site curve fitting and then calculated via the Cheng-Prusoff equation, so variability reflects replicate curve-fitting uncertainty and its propagation to Ki. Moreover, for some weaker ligands the bottom plateau was not fully constrained within the tested range and was partially estimated, which increases SD. Because the inhibition curves are fitted on a log10 concentration axis, the IC50 is obtained by back-transformation (antilog) of the fitted parameter and then converted to Ki using the Cheng-Prusoff equation. Therefore, modest differences between duplicate fits can appear amplified when Ki is reported in linear nM units.
   
   Importantly, reported SD is smaller on a logarithmic scale. For example, MTP86: 6,770 ± 1,471 nM corresponds (for n = 2) to ~5,730 and ~7,810 nM, i.e. only 0.13 log10 units. Assay reproducibility was monitored by including olanzapine on each plate (Ki 7 ± 2 nM), consistent with literature reported values

 

 

1. The decision-making process for compound selection appears circular. The authors state that compounds of type III (14-20) were designed based on results from type I and II, yet these new compounds (with the exception of 19 for BuChE) show universally poor or no activity. The authors then state "we have reconsidered the Contilisant hybrids of type I and II for further investigation." This suggests the rational design of type III failed. What specific SAR lessons were learned from this negative dataset, and how will this inform future design?: Thanks for this appropriate comment. We just considered new compounds bearing the HDAC pharmacophore installed at C2 at the índole heterocyclic ring system, leading to simple, new and easily available ligands. It’s clear that our previous design for compounds of type I and II was corrrect, and that this last option failed, and should be not be considered in future developments.

 

1. Regarding the synthesis: the yield for hydroxamate 14 (now compound 1 after the suggested re-numbering) is only 6%, yet the compound was carried forward for biological testing. What was done to confirm the purity and correct identity of this batch, given that typical purity criteria is ≥95%? Was the low yield reproducible, or is this an isolated result that raises concerns about the reliability of this synthetic route?: Thanks for the observation. As shown in the Supplementary Material (page S3) the compound is pure by HPLC-MS analysis. The yield has not been optimized, as at this level what we needed is to have amounts to test it. In the case the compound would have been interesting, we would have tried to optimize the process to prepare it, no doubt.

 

1. The PAMPA-BBB data (Table 4 and 5) show MTP100 is "poorly dissolved, turbid at 50% in DMSO" and is classified as CNS-. However, the experimental permeability value for MTP100 is 1.6 ± 0.3, while Vorinostat is 1.8 ± 0.25 and is also CNS-. Given the standard deviations, these values are statistically indistinguishable. What is the justification for using a hard threshold (5.050 for CNS+) when the assay shows such variability, and why was MTP100 excluded while borderline compounds were retained?: We based our permeability cut-offs on those proposed and validated by Di et al. for the same PAMPA-BBB setup. These define three distinct categories (CNS+, CNS, CNS–), representing fixed thresholds rather than being statistically derived from our dataset. In our classification, compounds with Pe below the CNS– threshold were considered non-permeable, those well above as CNS+, and those in between as borderline CNS, regardless of minor numerical differences within each group. MTP100 was not excluded solely because its Pe (1.6 ± 0.3) is close to Vorinostat (1.8 ± 0.25), but because: (i) it falls below the CNS–cut-off in our validated calibration, (ii) it showed clear solubility issues (“poorly dissolved, turbid at 50% in DMSO”), which compromise the reliability and translational value of its permeability estimate, and (iii) it lacked the overall balance of pharmacological profile and developability compared with the compounds prioritized for in vivo work. In contrast, the retained “borderline” compounds had acceptable solubility and more favorable global profiles, so we considered their intermediate Pe values informative for decision-making despite the intrinsic variability of the assay.

 

1. In Figure 4, the C. elegans locomotor activity data shows significance at non-monotonic doses (e.g., PD model: significant at 0.01 µM and 1 µM, but not at 0.1 µM and 10 µM). This inverted U-shaped curve is not discussed. Was this observed consistently across replicates? How do the authors interpret this lack of clear dose-response? : Yes, the non-monotonic pattern was observed consistently across independent experiments: the lowest and some intermediate doses repeatedly showed the most robust improvement in locomotor activity, whereas intermediate doses fell within the assay's variability range and did not always reach significance.​ We interpret this as a plausible inverted U-shaped (hormetic) response, commonly observed for CNS-active and epigenetic modulators. This response indicates that optimal network modulation occurs within a narrow concentration window, with higher doses potentially activating compensatory or off-target mechanisms that reduce behavioral benefits. Additionally, since the assay measures activity from 25–35 worms per well and is subject to biological and technical variability, we did not attempt to determine a formal EC50. Instead, we used these data as a proof-of-concept showing that MTP150 can enhance locomotor function in vivo across a range of submaximal doses.

 

 

1. The SH-SY5Y cytotoxicity data (Figure 6) indicates that MTP150 significantly reduces viability at concentrations >1 µM, yet the neuroprotection experiments (Figure 7A) were conducted using concentrations up to 0.1 µM well below this threshold. However, the Drosophila in vivo studies used 1 µM and 10 µM doses. Given that the fly food contains the compound throughout larval development, how do the authors reconcile the fact that 10 µM is clearly cytotoxic in human cells but is the most effective dose in flies? Was compound bioaccumulation or metabolic activation/deactivation considered?: We thank the reviewer for this comment. The difference between the concentrations used in SH-SY5Y cells and in Drosophila reflects the intrinsic distinction between an in vitro system and a whole organism. In flies, the compound is administered through the food and therefore undergoes ingestion, absorption, distribution, metabolism, and excretion; consequently, the nominal dietary concentration does not correspond to the effective intracellular concentration in target tissues, which is expected to be substantially lower. For this reason, higher external concentrations are typically required in Drosophila to achieve biological effects. Importantly, no developmental toxicity or reduced viability was observed in flies at the tested doses, indicating that these concentrations are well tolerated in vivo. Thus, the apparent discrepancy is consistent with organism-level pharmacokinetic buffering rather than true cytotoxic equivalence.

 

 

1. In the HDAC inhibition methods, it is noted that for HDAC1, "inhibitor and enzyme were preincubated at 25 °C for 60 min." No such preincubation is mentioned for HDAC6. Since HDAC1 and HDAC6 inhibition potencies are directly compared to support the claim of balanced inhibition, why were different preincubation conditions used? Could the longer preincubation for HDAC1 artificially increase the apparent potency against this isoform?: This is an interesting question. However, preincubation time does not artificially increase the potency of an inhibitor, but rather helps to provide a more accurate estimate of its true potency. Our manuscript presents a diverse set of multitarget small molecules bearing various zinc-binding groups (ZBGs), including o-aminoanilides and propylhydrazides. These ZBGs are known for their slow-binding characteristics at HDAC1-3, causing a delay in enzyme-inhibitor equilibration. Consequently, the true potency of slow-binding inhibitors is usually underestimated in standard end-point assays. Therefore, we assessed these compounds with a pre-incubation time of 1 hour to determine their true potency. Similar slow-binding inhibition of HDAC6 has only previously been reported for compounds bearing a DFMO ZBG. Additionally, o-aminoanilides and propylhydrazides are inactive at HDAC6, and hydroxamic acids are considered to be fast-on/fast-off HDACi. Given the structures of our compounds, it was therefore unnecessary to include a pre-incubation time in the HDAC6 assay.  

To clarify this, we slightly modified the experimental section as follows:

 “In the case of o-aminoanilide and hydrazide-based inhibitors, which are known for their slow-binding characteristics at HDAC1-3 [43,44], inhibitor and enzyme (HDAC1) were preincubated at 25 °C for 60 min.”

 

1. The supplementary molecular docking for compound 15 (now compound 2 after the suggested re-numbering) (Figures 3S and 4S) shows the ligand "remains at the entrance" of HDAC1 and HDAC6. However, the method section states that "flexible residues" were used, including catalytic channel residues. If the docking protocol correctly models flexibility, why does the ligand not sample deeper binding poses? Was an induced-fit docking or molecular dynamics simulation considered to validate that this truly reflects an inability to bind, rather than a limitation of rigid or semi-flexible docking?: The docking protocol was performed using a flexible‐residue approach and, in order to ensure adequate conformational sampling, each docking calculation was repeated 50 independent runs. Across all generated poses, compound 15 (= 2) consistently remained located at the entrance of the catalytic tunnel, and none of the obtained solutions reached or properly occupied the catalytic zinc site. Importantly, the use of a flexible docking approach allows partial simulation of side-chain movements within the catalytic channel, thereby providing the ligand with a greater opportunity to adapt and accommodate within the pocket than would be possible under a fully rigid docking protocol. Despite this added flexibility, the ligand did not show deeper binding poses. This recurrent behaviour suggests that the observed binding mode is unlikely to be solely a methodological artifact, but rather reflects an intrinsic tendency of the molecule. The most plausible explanation is steric hindrance combined with strong stabilizing interactions established with amino acid residues at the tunnel entrance, which energetically favour a shallow binding orientation and prevent deeper penetration into the catalytic pocket. While induced-fit docking could allow additional conformational adjustment of the ligand, and molecular dynamics simulations could provide dynamic insight into ligand accommodation over time, the high reproducibility of the results across multiple runs supports the interpretation that compound 15 (= 2) has a limited ability to access the catalytic site under the modelled conditions.

 

 

1. Regarding the claimed "epigenetically-based therapy": the manuscript demonstrates that MTP150 inhibits HDAC1 and HDAC6 in vitro and has phenotypic effects in disease models. However, there is no direct evidence presented that these phenotypic effects are actually mediated by HDAC inhibition (e.g., measurement of histone acetylation levels, target engagement studies, or rescue experiments with HDAC overexpression). Given the compound is multitarget, how can the authors confidently attribute the in vivo efficacy specifically to epigenetic mechanisms?: Thanks for the point. As commented above, MTP150 is a multitarged compound, being active in diverse biological targets; so, not only the “epigenetically” factor is critical, but the whole pharmacological power should be considered for the observed in vivo response. As we have designed MTP150 by installing a well known HDAC phamacophoric group, we can reasonably retain this mention.

 

1. In the ADME section (Supplementary : tHASN, Table S1), the authors report that the compound violates no Lipinski rules, yet the accptHB (estimated number of hydrogen bonds accepted) is 11.45, which is far above the typical QikProp recommended maximum of 6.0. The authors acknowledge this but do not discuss its potential impact on permeability or efflux. Given that the compound shows only moderate predicted oral absorption (65.8%), isn’t this high polar surface area and HB acceptor count a significant liability for a CNS drug?: We thank the reviewer for this important observation. It is correct that the predicted number of hydrogen bond acceptors (accptHB = 11.45) exceeds the typical QikProp recommended threshold of 6.0. However, it is important to clarify that Lipinski’s Rule of Five defines the acceptable upper limit for hydrogen bond acceptors as ≤ 10, not 6. The compound does not violate Lipinski’s criteria, although it does exceed the more conservative QikProp recommendation. This relatively high polarity contributes to the predicted moderate oral absorption (65.8%), as reflected in the ADME analysis. Although the predicted accptHB value is 11.45, QikProp calculates Lipinski violations based on the structural count of nitrogen and oxygen atoms (N + O ≤ 10), rather than the predictive accptHB descriptor. Since the structural N + O count in this compound remains within the Lipinski threshold, QikProp reports zero Rule of Five violations. The accptHB parameter reflects an estimate of hydrogen bond accepting capacity and does not directly correspond to the discrete structural count used for Lipinski evaluation. As a result, accptHB values may be fractional (e.g., 11.45). Thus, the apparent discrepancy arises because these two parameters measure related but distinct concepts. An elevated hydrogen bond acceptor count and increased polarity may reduce passive membrane permeability and could potentially increase susceptibility to efflux transporters, factors that are particularly relevant for CNS-targeted drugs. However, CNS penetration is a multifactorial property that depends not only on hydrogen bond acceptor count and polar surface area, but also on lipophilicity, molecular flexibility, molecular weight, and potential interactions with active transport mechanisms. In this context, the predicted QPlogBB value for compound MTP150 is −2.075, which falls within the range reported by QikProp for brain/blood partitioning (see Table S1). Additionally, the polar surface area (PSA), which reflects the molecule’s hydrogen bonding capacity, is 113.587 Ų, which is within the acceptable range according to QikProp. Therefore, although the predicted accptHB value of compound MTP150 may represent a potential limitation for optimal BBB permeability, it does not necessarily preclude CNS exposure. Indeed, in the PAMPA-BBB assay, which predicts CNS penetration, the compound is predicted to effectively cross the blood–brain barrier, in agreement with the theoretical ADME predictions.

 

 

1. The manuscript repeatedly refers to "Contilisant" and "Contilistat" interchangeably and inconsistently across text and figures (e.g., Figure 1 labels 3 as "Contilistat", but text describes "Contilisant (1)" and "Contilistat (3)"). This is confusing for readers not intimately familiar with the authors' previous work. Please standardize nomenclatura: Thank you very much for the observation. In the revised version of the manuscript we have re-numbered the compounds, and eliminated the structure and mention to Contilistat.

 

1. Regarding statistical analysis: for the C. elegans studies, the authors used one-way ANOVA with Dunnett’s post-hoc test for multiple comparisons against a single control. This is appropriate. However, for the Drosophila studies (Figure 5), one-way ANOVA with Tukey’s test was used to compare all groups. Given that there are only three groups (vehicle, 1 µM, 10 µM), and the comparison of interest is each dose vs. vehicle, Dunnett’s test would be more statistically powerful. Why was Tukey’s chosen? Additionally, no correction for multiple testing (e.g., Bonferroni) is mentioned for the numerous comparisons in Tables 1,2,4,5. Was any multiplicity adjustment applied?: Thank you for this comment. To ensure consistency across all analyses, we have now applied one-way ANOVA with Dunnett’s post-hoc test not only to the Drosophila experiments, as suggested, but also to the human cell studies. Accordingly, Figures 5, 6, and 7 have been revised. This change in the statistical approach did not alter the results or their interpretation.

 

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors appear to have addressed the reviewers' questions. I am in full support of publication.

Author Response

Thank you very much for your comment.

Reviewer 3 Report

Comments and Suggestions for Authors

I thank the authors for their detailed responses and for the revisions made to the manuscript. I acknowledge the renumbering of compounds, the correction of nomenclature, the adjustments to statistical analysis in the Drosophila studies, and the clarifications added to the Supplementary Materials regarding HDAC docking.
The manuscript has improved, and the extensive experimental work is commendable. However, several issues should still be addressed before publication:
1.    The Ki value of 13.58 µM for MTP150 is very modest. While the compound may act through other targets, the current title and narrative overemphasize 5-HT6R. I recommend softening these claims (e.g., removing "5-HT6R" from the title and toning down related statements).
2.    The contradiction between experimental potency (IC50 = 0.040 µM) and docking prediction ("limited biological activity") is now clarified in wording but not in substance. A brief comment in the Discussion acknowledging this limitation of the computational model would be helpful.
3.    The negative results are acknowledged but dismissed without SAR insights. Adding a short sentence on what was learned (e.g., "C2 substitution without the N-methylpropargyl motif is detrimental for activity") would strengthen the manuscript.
4.    The explanation for using 10 µM in flies versus ≤0.1 µM in cells is plausible but speculative. A note in the Discussion that this reflects typical in vivo/in vitro differences, without overinterpreting, would suffice.
These are minor revisions that do not require new experiments. With these adjustments, the manuscript would be suitable for publication.

Author Response

Reviewer 3

 

1. The Ki value of 13.58 µM for MTP150 is very modest. While the compound may act through other targets, the current title and narrative overemphasize 5-HT6R. I recommend softening these claims (e.g., removing "5-HT6R" from the title and toning down related statements): Yes, reviewer is right and we have removed this term from the title (“Polyfunctionalized N-arylsulfonyl indoles: Identification of (E)-N-Hydroxy-3-{3-[(5-(3-(piperidin-1-yl)propoxy]-1H-indol-1-yl)sulfonyl]phenyl}acrylamide (MTP150) for the epigenetically-based therapy of Parkinson’s disease”), and in the text when appropriate.
      The contradiction between experimental potency (IC50 = 0.040 µM) and docking prediction ("limited biological activity") is now clarified in wording but not in substance. A brief comment in the Discussion acknowledging this limitation of the computational model would be helpful: Thank you very much for your observation, that we accept. So, a brief comment on the limitation of the computational model has been added in the Supplementary Materials (Page 22S), as follows: “…Docking models indicate that, in HDAC6, the interactions of the cap group with the enzyme surface hinder the proper approach of the metal-binding moiety to the zinc ion, preventing bidentate coordination and resulting in a monodentate interaction, which explains the lower inhibitory activity of MTP150 against HDAC6 compared to HDAC1, while noting that docking provides a qualitative view of ligand–target interactions.”.
   3.    The negative results are acknowledged but dismissed without SAR insights. Adding a short sentence on what was learned (e.g., "C2 substitution without the N-methylpropargyl motif is detrimental for activity") would strengthen the manuscript: Thank you very much for this comment, that we incorporated in the Manuscript, in page 14 as follows: “…To sum up, and by comparison with Contilisant (Figure 1), it seems that in hybrids of type III, C2 substitution at the indole core without the N-methylpropargyl motif is detrimental for activity...”
   4.    The explanation for using 10 µM in flies versus ≤0.1 µM in cells is plausible but speculative. A note in the Discussion that this reflects typical in vivo/in vitro differences, without overinterpreting, would suffice: According to this comment, we have included the following sentence at the end of section 2.5: “The difference in beneficial MTP150 concentrations observed in human cells compared with those in Drosophila reflects the inherent distinction between an in vitro system and a whole organism.”

 

Author Response File: Author Response.pdf