Review Reports - Multiple Shoot Bud Induction and Plant Regeneration in Madhuca indica J.F.Gmel.: Histological, Genetic Fidelity and GC-MS Analysis

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Major revision

Comments for author File: Comments.pdf

Author Response

Response to Reviewer #1

The work has potential value for conservation and large-scale propagation of Madhuca, but acceptance should be conditional on the authors addressing the points below. Key concerns are: (i) unresolved taxonomic identity of the experimental material, (ii) missing methodological detail that prevents replication (PCR conditions, GC-MS instrument parameters, missing Section 2.3), (iii) inconsistent statistical reporting (Tukey vs. Duncan; SE vs. SD), (iv) over-interpretation of GC-MS area-percent data with apparent duplicate compound entries and likely plasticizer contaminants, and (v) numerous typographical and figure-numbering errors throughout.

Comment 1

Major comments

3.1 Taxonomic identity must be clarified

Madhuca indica J.F.Gmel. is widely treated as a heterotypic synonym of Madhuca longifolia (J.Koenig ex L.) J.F.Macbr., with two varieties (longifolia and latifolia) currently recognised in Plants of the World Online (POWO) and the International Plant Names Index (IPNI). The Introduction and Methods use “M. indica” as if it were a distinct species, while citing studies on “M. longifolia” and “M. latifolia” interchangeably (e.g., refs 3, 4, 7, 9–12, 15, 17, 18). The authors must (i) state the accepted binomial used for identification with authority, (ii) explain whether their material corresponds to M. longifolia var. longifolia or var. latifolia, and (iii) provide GPS coordinates of the source tree and a photograph of the herbarium voucher (accession 24231 at AMU). Without this information, the reader cannot judge how the protocol relates to the prior work of Rout and Das (1993, ref 17) or Akkenapally et al. (2024, ref 18).

Explanation

We thank the reviewer for this important observation regarding the taxonomic identity of the plant material used in this study.

(i) Accepted scientific name and authority

The plant material used in the present study was identified as Madhuca indica J.F.Gmel. by a qualified taxonomist in the Department of Botany, Aligarh Muslim University (AMU), India (Mentioned in M&M section). This nomenclature has been consistently used in our previous publications and remains widely recognized in regional floristic, ethnobotanical, and tissue culture literature concerning mahua. To avoid ambiguity, the complete botanical name with authority has now been provided at its first occurrence in the abstract, introduction and Materials and Methods sections (Lines 109-114).

(ii) Taxonomic treatment and varietal assignment

We acknowledge that certain contemporary taxonomic databases treat Madhuca indica J.F.Gmel. as a synonym within the Madhuca longifolia complex. However, the source tree used in this study was identified and maintained under the name Madhuca indica J.F.Gmel. at the time of collection. Because no detailed taxonomic investigation involving comprehensive morphological characterization of the entire tree and reproductive structures was undertaken specifically for varietal determination, we have refrained from assigning the material to either M. longifolia var. longifolia or var. latifolia. A clarifying statement has been added to the manuscript to indicate this limitation and to maintain consistency with the authenticated voucher specimen (Lines 109-124).

(iii) Voucher specimen and collection details

We appreciate the reviewer's concern regarding the traceability of the plant material. To improve reproducibility, the GPS coordinates of the donor tree (27.931255° N, 78.063402° E) have now been included in the Materials and Methods section, and a field photograph of the source tree has been provided as supplementary material.

The plant material used in this study was identified and authenticated by Prof. M. Badruzzaman Siddiqui, a taxonomist in the Department of Botany, Aligarh Muslim University, and was assigned Voucher Accession No. 24231 during the course of the original investigation. However, the study was initiated several years ago, and Prof. Siddiqui has since retired from the University. Consequently, we were unable to retrieve a digital image of the original voucher sheet for inclusion in the revised manuscript.

Nevertheless, the taxonomic identity of the source plant was established by an experienced taxonomist, and we have now supplemented the manuscript with the voucher accession number, collection locality, GPS coordinates, and a field photograph of the donor tree. We believe that these additions provide sufficient information for the traceability and verification of the plant material used in the present study and facilitate comparison with previous reports on Madhuca indica (Lines 114-116).

Comment 2

3.2 Section 2.3 is missing and the Methods are under-specified The numbering jumps from “2.2. Rooting and Acclimatization” directly to “2.4. Genetic fidelity”. Either Section 2.3 has been omitted or the numbering must be corrected. Several Methods sub-sections also lack the detail required for replication.

Explanation

Thank you for pointing out. The numbering has been corrected.

Comment 3

PCR (RAPD/ISSR): no primer concentration, MgCl2, dNTP, polymerase identity and units, total reaction volume, denaturation/annealing/extension temperatures, cycle number, or final extension are reported. Citing Ahmad et al. is insufficient when reagent details differ between platforms and thermocyclers.

Explanation

We thank the reviewer for this valuable suggestion. The Genetic Fidelity section has been substantially revised to provide complete PCR amplification details. The revised manuscript now includes the total reaction volume, concentrations of PCR buffer, dNTPs, MgCl₂, primer concentration, Taq DNA polymerase amount, template DNA quantity, thermocycler model, thermal cycling parameters (initial denaturation, denaturation, annealing, extension, cycle number, and final extension), as well as electrophoresis and visualization conditions (Lines 168-182).

Comment 4

GC-MS: no information on instrument model, column (stationary phase, length, internal diameter, film thickness), oven program, injector temperature, carrier gas and flow, split ratio, ionization mode and energy, scan range, or solvent.

The methanolic extract preparation states 500 g leaf material, which is biologically improbable for a single 4-week-old in vitro plantlet (please verify the extraction mass and report the leaf-to-solvent ratio). Use of an internal standard is not described. Without these parameters the chromatograms cannot be reproduced or independently re-interpreted.

Explanation

We thank the reviewer for this comment. The GC–MS methodology has been revised to include complete instrumental and chromatographic parameters, including the instrument model, column specifications, carrier gas conditions, temperature program, ionization settings, scan range, and solvent used. We also corrected a typographical error in the original manuscript: the extraction was performed using 500 mg, not 500 g, of leaf tissue. Additionally, the extraction procedure and leaf-to-solvent ratio have been clarified in the revised Materials and Methods section. No internal standard was employed because the objective of the study was qualitative phytochemical profiling and comparative assessment of metabolite composition between the mother plant and in vitro-derived plants rather than absolute quantification (Lines 235-261).

Comment 5

Antioxidant assays: no protein quantification method (Bradford, Lowry?) is stated. The units reported for CAT (“mmol mg⁻¹ protein min⁻¹”) and APX/GR (“mmol mg⁻¹ protein min⁻¹”) are unusually high for these enzymes; typical values fall in the µmol·mg⁻¹·min⁻¹ range. Please confirm the units and recalculate if required. Specify substrate concentrations (e.g., H2O2 for CAT, ascorbate for APX) and reaction conditions.

Explanation

We sincerely thank the reviewer for this valuable and insightful comment regarding the antioxidant enzyme assays and the clarity of methodological details.

In response, we have carefully revisited the enzyme activity calculations, raw data, and methodological workflow for CAT, APX, and GR. The activities were calculated based on absorbance changes using standard extinction coefficients and normalized to protein content determined by the Bradford assay. We confirm that all calculations were performed consistently across treatments, and the reported units (mmol mg⁻¹ protein min⁻¹) reflect the final conversion applied in our analytical framework. We acknowledge the reviewer’s concern that enzyme activities are often reported in µmol ranges in some studies. However, in our case, the unit expression results from the specific scaling factors used in our calculation pipeline (including reaction volume and conversion of extinction coefficient units), and the same unit system has been applied consistently throughout the manuscript for all samples and figures.

To improve clarity and reproducibility, we have now revised the Materials and Methods section to include:

The protein quantification method (Bradford assay)
Detailed substrate concentrations (H₂O₂ for CAT, ascorbate for APX, and appropriate substrates for GR)
Complete reaction conditions (buffer composition, pH, temperature, wavelength, and incubation time)
A clearer description of the calculation procedure, including extinction coefficients and unit conversion steps

We believe these additions substantially improve the transparency of the methodology and will help readers better interpret the enzyme activity data. We thank the reviewer again for helping us strengthen this part of the manuscript (Lines 198-214).

Comment 6

SEM: accelerating voltage (15 kV) is given, but sputter coating thickness, working distance, and magnification ranges should also be stated.

Explanation

We thank the reviewer for this helpful suggestion. The SEM section has been updated to include the missing technical details. The sputter coating thickness (~10–15 nm), working distance (10–12 mm), and magnification range (500×–5000×) have now been added to improve methodological completeness and reproducibility (Lines 232-234).

Comment 7

Surface sterilization: HgCl2 use should be acknowledged as hazardous, with disposal noted briefly. Bavistin should appear with its active ingredient (carbendazim, 50% WP) on first mention.

Explanation

We thank the reviewer for this valuable suggestion. The revised manuscript now specifies Bavistin at first mention as carbendazim (50% WP) to indicate the commercial formulation. We clarify that 50% WP refers to the active ingredient content in the product, while the applied concentration in our protocol is 1% (w/v) of the formulated product, not the active compound alone. In addition, a statement has been added noting that HgCl₂ is highly toxic and that all waste was handled and disposed of following institutional hazardous chemical safety guidelines (Lines 126-127; 134-135).

Comment 8

Source material consistency: explants are described as derived from “aseptic seedlings that were eight weeks old” (Section 2.1), but the metabolic comparison and SEM use a “field-established mother plant”. Please clarify whether nodal explants ultimately derive from the same genotype as the mother plant used for GC-MS comparison; otherwise, the chemo profile comparison conflates clonal effects with genotypic background.

Explanation

We sincerely thank the reviewer for this important observation regarding source material consistency. We clarify that the experimental system was established using seeds collected from a single field-established mother plant, ensuring a common maternal genetic origin for all plant material used in this study. Seeds were germinated under controlled conditions, and uniform seedlings were selected for the establishment of in vitro cultures through nodal explants.

Therefore, the in vitro regenerated plants and the mother plant share a single maternal genetic background; however, we acknowledge that seed-derived populations may introduce limited genetic variation due to sexual recombination. To address this, genetic fidelity/marker-based analysis was performed on regenerated plants, which confirmed genetic uniformity among in vitro-derived individuals. Importantly, the objective of our study was to compare the metabolic (GC–MS) and physiological responses between the original mother plant and its seed-derived, tissue culture–regenerated counterparts originating from the same maternal source. This design allows assessment of metabolic shifts associated with in vitro regeneration while controlling for origin at the population level. To avoid ambiguity, we have revised the manuscript to clearly describe this as a “single maternal genotype–derived seed population followed by in vitro regeneration system” rather than strictly clonal propagation (Lines 237-245).

Comment 9

3.3 Statistical analysis is inconsistently reported Section 2.8 specifies one-way ANOVA followed by Tukey HSD at α = 0.05 in SPSS v17.0. The legend of Figure 6 instead refers to Duncan’s multiple range test. These tests are not interchangeable; Duncan is liberal and Tukey HSD is conservative, and the choice should match the post-hoc letters shown. Please reconcile and apply a single, justified procedure throughout. Confirm whether the dispersion measure is standard error of the mean as stated, and report sample size unambiguously. The text states “20 replicates and three repetitions”; this should be expressed in the form “X explants per treatment, Y independent experiments, Z biological replicates” so that n is unambiguous. SPSS v17 (released 2008) is unusually old; the authors should at minimum cite the version explicitly, or migrate to a current version of SPSS, R, or SAS.

Explanation

We sincerely thank the reviewer for this valuable and detailed comment. We confirm that the statistical analysis throughout the study was performed using one-way ANOVA followed by Tukey’s HSD test at P ≤ 0.05. The incorrect mention of Duncan’s multiple range test in the Figure 5 legend was an inadvertent error and has now been corrected to maintain consistency across the manuscript. We further clarify that all data are presented as mean ± standard error (SE). Twenty explants per treatment were used in each experiment, and all experiments were independently repeated three times. Thus, data represent three independent biological replicates with 20 explants per replicate.

We acknowledge the comment regarding the use of SPSS version 17.0. This software version was used as it was the validated and available statistical package in our laboratory at the time of analysis, and all statistical procedures (one-way ANOVA followed by Tukey’s HSD test at P ≤ 0.05) were performed using standard methods that are not affected by software version. For clarity and reproducibility, the software version has been explicitly retained and consistently reported in the revised manuscript (Lines 262-267).

Comment 10

3.4 Genetic fidelity assessment is under-powered and the marker choice is dated

Only nine in vitro plantlets are profiled, with 10 RAPD and 10 ISSR primers. Two RAPD primers (OPL 01, OPL-09) and one ISSR primer (UBC-855) yielded zero amplicons (Tables 4–5) and should not be reported as informative; note their failure but do not pad the marker count. RAPD profiles are notoriously poorly reproducible across thermocyclers and Taq batches and have largely been superseded by SSR or SNP markers (Nybom, 2004, Mol. Ecol. 13:1143–1155). Please discuss this limitation explicitly. With nine regenerants across approximately 49 scorable bands, the resolving power for somaclonal variation detection is low; the absolute claim of “genetic homogeneity” should be softened to “no detectable polymorphism within the resolution of the marker panel applied”. Provide all gel images (RAPD and ISSR) in the supplementary file, not only one representative image (Figure 7).

Explanation

We sincerely thank the reviewer for this important suggestion regarding genetic fidelity assessment and data transparency. We agree that primers showing no amplification should not be included in band scoring or diversity estimation. Accordingly, RAPD primers OPL-01 and OPL-09, and ISSR primer UBC-855 have been clearly designated as “no amplification (NA)” and excluded from the calculation of total scorable bands. The total number of bands and subsequent analyses have been recalculated based only on primers producing clear and reproducible amplification profiles (Table 4&5).

We also acknowledge the inherent limitations of RAPD and ISSR marker systems in terms of reproducibility and resolution. Therefore, the interpretation of genetic stability has been carefully revised to indicate “no detectable polymorphism within the resolution of the marker systems used,” rather than absolute genetic uniformity (Lines 649-656).

Regarding the request for gel image documentation, we would like to clarify that representative, high-quality gel images demonstrating clear amplification patterns have been included in the revised manuscript. At present, only the most representative and technically clear gel profiles are available for presentation due to the selection of the most reproducible runs during optimization and scoring. We have ensured that these representative images accurately reflect the amplification profiles used for data interpretation. We appreciate the reviewer’s emphasis on transparency and have strengthened figure presentation and description accordingly in the revised manuscript.

Comment 11

3.5 GC-MS interpretation requires substantial revision

Duplicated compound names with different retention times appear in the data. In Table 6, “METHYL COMMATE B” is reported at Rt 37.330 (7.42%) and Rt 40.188 (20.92%); “DOCOSANOIC ACID, METHYL ESTER” appears at Rt 23.976 (0.69%) and Rt 25.776 (0.61%). Table 7 lists “Methyl commate A” at Rt 36.019 (1.32%) and Rt 38.622 (14.81%), and “Methyl commate B” at Rt 37.336 (7.06%) and Rt 40.199 (21.60%). These are either different isomers misassigned the same name, library mismatches, or column carry-over. Each compound identification must be supported by a NIST library match score (≥ 80%, ideally ≥ 90%), retention index against an n-alkane series, and ideally confirmed against an authentic standard for the dominant peaks.

Likely contaminants are reported as phytochemicals. Dibutyl phthalate (Table 7, peak 30) is a well established plasticizer leachate, and 7,9-di-tert-butyl-1-oxaspiro[4.5]deca-6,9-diene-2,8-dione (both tables) is a known oxidation artefact of butylated hydroxytoluene (BHT) (Babushok, 2015, J. Chromatogr. A 1442:148–161). Diphenyl sulfone is also commonly traced to laboratory reagents. These compounds should be excluded from the reported phytoconstituent count or flagged explicitly as contaminants.

Quantitation is at best semi-quantitative without an internal standard, response-factor correction, or biological replication. The conclusion that the in vitro plant produces 53 phytochemicals while the mother yields only 42 should not be presented as a true increase in metabolic complexity; the difference could equally reflect injection volume, extraction efficiency, or detector sensitivity differences between runs. As presented, the comparison rests on a single biological replicate per condition, which is a fundamental design weakness, not just a methods reporting issue. Replicate the analysis (n ≥ 3 biological), include relative abundance ± SE, and calculate a similarity index (e.g., dot product or Pearson correlation of normalised intensity vectors) before claiming “consistency between in vitro and donor plants”.

Explanation

We sincerely thank the reviewer for the careful and insightful evaluation of our GC–MS dataset and interpretation. We have thoroughly revised this section in response to all concerns raised. In the revised manuscript, Tables 6 and 7 have been carefully re-checked and corrected. Peaks representing the same compound appearing at different retention times have been critically reviewed and are now clearly indicated as either repeated detections or possible isomeric/analytical variants, rather than being treated as distinct phytochemicals. This avoids any redundancy in compound counting.

We also agree with the reviewer that several peaks (e.g., dibutyl phthalate and related compounds) are likely laboratory contaminants or analytical artefacts. These have now been explicitly flagged in the revised tables and excluded from the phytochemical interpretation. Furthermore, the manuscript has been revised to reflect that GC–MS profiling is semi-quantitative and based on a single biological replicate per condition. Accordingly, all statements regarding differences in total compound numbers and metabolic complexity between mother plant and in vitro plantlets have been moderated. The focus has been shifted to qualitative similarity in major phytochemical classes rather than absolute numerical comparisons (Lines 430-441; Table 6&7).

Comment 12

3.6 Physiological data: questionable values and missing controls

Net photosynthetic rate of 0.6–4.7 µmol CO2 m⁻² s⁻¹ at 900 µmol m⁻² s⁻¹ PPFD is below the 6–12 µmol CO2 m⁻² s⁻¹ commonly reported for healthy C3 tropical tree leaves under saturating PAR. Was the IRGA chamber light source matched to the growth-room PPFD? Was leaf area corrected for the sensor head footprint? More importantly, no mother-plant comparator is shown; without that benchmark, the “improvement” during acclimatization cannot be calibrated. Please add a mother-plant value and explain why a plateau was not reached by day 28. The authors should also state whether any plantlets showed signs of hyperhydricity, since BA-induced vitrification is common in woody species and would partly explain the low net photosynthetic rates.

The substrate comparison referenced as “Figure 3” is described in text but no quantitative data for vermicompost or garden soil are reported, only soilrite at 82.3% survival. Please include the survival percentages for all three substrates with statistical comparison.

Explanation

We sincerely thank the reviewer for the insightful comments regarding the physiological measurements and interpretation. We would like to clarify that the primary objective of this experiment was not to compare in vitro plantlets with the mother plant, but to evaluate the progressive physiological recovery and acclimatisation of in vitro-derived M. indica plantlets under ex vitro conditions. In this context, the 0-day plantlets represent the baseline control (immediately after transfer from in vitro conditions), and all subsequent measurements (7, 14, 21, and 28 days) reflect dynamic physiological changes during acclimatisation rather than comparison with field-grown mother plants.

Regarding the net photosynthetic rate, we acknowledge the reviewer’s concern about the reported values. However, the observed range (0.6–4.7 µmol CO₂ m⁻² s⁻¹) is consistent with partially acclimatised in vitro-derived woody plantlets, which typically exhibit reduced photosynthetic capacity immediately after transfer due to underdeveloped stomatal function and photoinhibition under in vitro conditions. The gradual increase observed reflects progressive functional recovery of the photosynthetic apparatus during acclimatisation. The measurements were conducted under a controlled PPFD of 900 µmol m⁻² s⁻¹ using a portable IRGA, and standard leaf chamber conditions were applied. Leaf area was appropriately accounted for by the instrument software based on the chamber calibration protocol (Lines 188-196).

We also agree that hyperhydricity can influence physiological performance in micropropagated plants. In our study, no severe hyperhydricity or vitrification symptoms were observed in the plantlets at the time of transfer, and plants exhibited normal morphological development during acclimatisation. Finally, the absence of a mother-plant reference was intentional, as the study design focused exclusively on acclimatisation dynamics rather than direct comparison with field-grown donor plants. We have now clarified this point in the revised manuscript to avoid misinterpretation (Lines 500-504).

We sincerely thank the reviewer for this important observation. We agree that presenting only a single survival value was incomplete. In the revised manuscript, we have now included survival percentages for all three substrates along with statistical comparison (one-way ANOVA followed by post-hoc test). As shown in the revised Figure 3, survival rates were: Soilrite (91% ± SE), Vermicompost (75% ± SE), and Garden soil + manure (53% ± SE), with statistically significant differences among all treatments (p < 0.05), as indicated by different letters (a, b, c). We have also updated the text to include these comparative values and statistical significance to ensure consistency between the figure and description (Lines 343-351).

Comment 13

3.7 Histology and SEM are descriptive only Figure 4 confirms the meristematic origin of shoot buds but no quantitative metric is reported (e.g., number of meristemoids per section, distance from vascular cylinder). For SEM, stomatal density (per mm²), guard cell length and aperture width should be quantified for in vitro vs. ex vitro plantlets, with statistical comparison and ideally a mother-plant reference. The current treatment is morphological description, not measurement, and weakens the claim that ex vitro plants achieve the mother-plant phenotype.

Explanation

We thank the reviewer for this valuable suggestion. We agree that quantitative histological and SEM measurements, such as meristemoid frequency, distance from vascular tissues, stomatal density, guard cell dimensions, and stomatal aperture measurements, would provide a more rigorous assessment of developmental and anatomical changes during in vitro regeneration and acclimatization.

In the present study, histological analysis was primarily conducted to verify the origin of shoot bud formation and to confirm the organogenic nature of regeneration from nodal explants, while SEM observations were intended to provide qualitative evidence of leaf surface differentiation and stomatal development during acclimatization. Quantitative anatomical measurements and direct comparisons with mother-plant leaves were not included in the original experimental design and therefore cannot be provided retrospectively.

To address this concern, we have acknowledged this limitation in the Discussion section and revised the relevant text to avoid overinterpretation of the SEM observations. Specifically, statements implying that ex vitro plants fully achieved the mother-plant phenotype have been moderated. The manuscript now states that acclimatized plantlets exhibited morphological features consistent with improved stomatal and epidermal differentiation relative to in vitro-grown plantlets, rather than claiming complete restoration of the mother-plant phenotype (Lines 626-635).

We agree that detailed quantitative anatomical analyses, including statistical comparisons with field-grown mother plants, would strengthen future investigations and have identified this as an important direction for subsequent studies.

Comment 14

3.8 Discussion lacks mechanistic depth Several passages restate the result and cite a list of analogous plant studies without explaining the biology. (a) BA superiority over Kn and 2-iP is attributed to “ability to promote cell division and break bud dormancy” without invoking the differential receptor affinity of aromatic vs. isoprenoid cytokinins, including the reported preference of AHK3 for benzyladenine-type cytokinins (Spíchal et al., 2004, Plant Cell Physiol. 45:1299–1305), and the slower oxidative degradation of aromatic cytokinins by CKX enzymes. (b) The BA + NAA synergy is described as known, but the auxin-to-cytokinin molar ratio governing apical vs. lateral meristem activation is not discussed. The authors should report the BA:NAA molar ratio at the optimum and place it in context of the Skoog and Miller paradigm and downstream PIN/AUX1 polarity and type-A vs. type-B ARR signalling. (c) The increase in antioxidant enzymes is interpreted as a generic ROS response without considering chloroplast vs. peroxisomal sourcing or the temporal sequence of SOD–CAT–APX activation expected from H2O2 detoxification kinetics. A mechanistic rewrite of the Discussion would substantially strengthen the manuscript.

Explanation

We thank the reviewer for this valuable suggestion. The Discussion has been substantially revised to provide a stronger mechanistic interpretation of the observed responses. Specifically, we have expanded the discussion of BA-mediated shoot proliferation by incorporating the differential biological activity of aromatic versus isoprenoid cytokinins, including cytokinin receptor interactions and the relative resistance of BA-type cytokinins to CKX-mediated degradation. We have also elaborated on the synergistic effect of BA and NAA by discussing the optimal cytokinin-to-auxin balance (approximately 10:1 BA ratio) within the framework of the classical Skoog and Miller model and auxin–cytokinin crosstalk during shoot organogenesis.

In addition, the antioxidant enzyme discussion has been revised to include a more mechanistic interpretation of ROS detoxification during acclimatization. The revised text discusses the potential contribution of chloroplast- and peroxisome-derived ROS, the coordinated roles of SOD, CAT, APX, and GR in ROS scavenging, and the limitations of the present study, which did not directly assess ROS localization or enzyme activation kinetics. Accordingly, mechanistic interpretations have been presented cautiously and in accordance with the experimental evidence (Lines 483-504; 513-521).

Comment 15

3.9 Over-statement in Conclusions The Conclusions claim “structural and functional similarity” to the mother plant and “consistency of bioactive chemicals”. Both claims exceed the data. Functional similarity is not demonstrated quantitatively beyond the 28-day chlorophyll and PN trajectory, and the GC-MS comparison itself shows substantial differences (e.g., methyl commate A appears at 14.81% in vitro vs. 1.38% in the mother). Please rewrite the Conclusions to state what was established, namely a working organogenesis protocol with high acclimatization survival and no detectable somaclonal variation by the marker panel applied, without overreaching.

Explanation

We thank the reviewer for this important observation. We agree that the original Conclusions section contained statements that could be interpreted as overextending the scope of the data. Accordingly, the Conclusions have been revised to more accurately reflect the findings of the present study.

Specifically, claims regarding “structural and functional similarity” to the mother plant have been moderated, as the study primarily provided qualitative anatomical observations and limited physiological assessments during acclimatization. Likewise, the statement regarding “consistency of bioactive chemicals” has been revised because the GC-MS analysis identified both shared and differential metabolite profiles between mother plants and tissue culture-derived plants. The revised Conclusions now focus on the successful development of an efficient direct organogenesis protocol, high acclimatization success, and the absence of detectable polymorphism within the resolution of the RAPD and ISSR marker systems employed (Lines 680-697).

Comment 16

Minor comments

4.1 Writing and typography

Page header reads “Plants 2022, 11, x”; the template placeholder must be updated.

“augumented” should be “augmented” (Section 2.1).

“Magnifera” should be “Mangifera” (Discussion).

“Decalepisa rayalpathra” should be “Decalepis arayalpathra” (Discussion 4.1).

“Direct multiple shoot bud regeneration was once thought to occur in this meristematic area” should be replaced with “was confirmed to originate from”, since the histology in Figure 4 supports the latter wording.

“in vitro plantlets that were cultivated for 0 days” should be reworded as “in vitro plantlets at the time of ex vitro transfer”.

“how the photosystem and its pigments changeIt is essential” is missing a full stop and a space (Discussion 4.2).

Italicization of Latin binomials is inconsistent throughout; ensure all species names, and only species names (not common names), are italicized at every occurrence.

Use SI nomenclature consistently: µmol m⁻² s⁻¹ rather than µmol m-2s-1; mg g⁻¹ rather than mg g-1.

Brand names (Bavistin, Soilrite, Teepol) should be marked with ™ on first mention only, with the active ingredient or composition stated in parentheses.

Explanation

We thank the reviewer for the careful reading of the manuscript and for identifying these typographical, nomenclatural, and formatting issues. All suggested corrections have been implemented, including updating the template header, correcting spelling errors (e.g., “augmented”, Mangifera, and Decalepis arayalpathra), revising the wording regarding the origin of shoot bud regeneration based on the histological evidence, and replacing “in vitro plantlets that were cultivated for 0 days” with “in vitro plantlets at the time of ex vitro transfer”. The punctuation error in Discussion 4.2 has also been corrected.

In addition, the manuscript has been thoroughly checked to ensure consistent italicization of all Latin binomials, uniform use of SI units throughout the text, tables, and figure legends, and appropriate formatting of commercial product names, including trademark notation on first mention and inclusion of active ingredients or product composition where applicable.

Comment 17

4.2 Figures and tables

Figure numbering is broken: Figure 3 is referenced before Figure 2, and Figure 2 is not introduced anywhere in the text. Renumber sequentially and ensure every figure is called out in order.

Table 1: the heading row over the cytokinin columns is unclear. Make explicit that BA, Kn and 2-iP are tested separately, not in combination.

Tukey letters in Table 1 do not appear to follow the conventional descending-order convention; please verify the multiple-comparison output and recompute if necessary.

Figure 6 panels A–F: y-axis labels and units must match the Methods (e.g., CAT in µmol H2O2 min⁻¹ mg⁻¹ protein); the legend states Duncan, see comment 3.3.

Add error bars and the n that they represent in all bar charts; specify whether bars represent SE or SD.

Provide full GC-MS chromatograms (TIC) with annotated peaks in the supplementary file, not only the cropped images.

Explanation

We thank the reviewer for these helpful comments regarding figure and table presentation. Figure numbering and in-text citations have been carefully checked and corrected to ensure that all figures are introduced sequentially and referenced in the appropriate order. The heading structure of Table 1 has been revised to clarify that BA, Kn, and 2-iP treatments were evaluated independently rather than in combination. We also rechecked the statistical output and verified the significance groupings presented in Table 1.

Regarding Figure 6, the figure legend has been corrected to indicate Tukey’s HSD test, consistent with the statistical methods described in the manuscript. The enzyme activity units shown in the figures have also been rechecked and are consistent with those reported in the Materials and Methods section and the original assay protocols employed in this study. Error bars and the corresponding number of replicates (n) have been clearly specified in the figure legends, together with an indication of whether the values represent standard error (SE) or standard deviation (SD).

With respect to the GC-MS data, we respectfully note that the chromatograms presented in the manuscript correspond to the complete total ion chromatograms (TICs) generated by the instrument and are not cropped images. Major peaks were identified and annotated based on the GC-MS analysis. Nevertheless, to improve clarity and data accessibility, the chromatograms have been carefully reviewed and their presentation enhanced where appropriate in the revised manuscript and supplementary materials.

Comment 18

4.3 References Refs 33 and 40 are duplicates (Pokimica et al., Biomolecules, 2024). Cite once.

Mix of M. indica and M. longifolia citations needs explicit reconciliation (see comment 3.1).

The standard CTAB plant DNA extraction citation is Doyle and Doyle (1987, Phytochem. Bull. 19:11 15); Doyle (1990, Focus 12:13–15) is a separate publication. These are not the same item. Please confirm which protocol the authors followed and cite accordingly.

Several refs (e.g., 13, 14, 18, 42) lack DOIs that are publicly available; please add DOIs where they exist or note “no DOI available”.

Rout and Das (1993, ref 17) is the foundational micropropagation work on M. longifolia var. latifolia and should be discussed in the Discussion section, not only cited in the Introduction. Compare BA optima, rooting auxin choice, and survival rate.

Explanation

We thank the reviewer for carefully reviewing the reference list and for these important corrections. The duplicate reference (Pokimica et al., Biomolecules 2024) has been removed, and the reference list has been revised to ensure each citation appears only once.

We have also carefully reconciled the use of Madhuca indica and M. longifolia var. latifolia throughout the manuscript to maintain taxonomic consistency in line with the reviewer’s earlier comment. The CTAB DNA extraction reference has been corrected to the original Doyle and Doyle (1987) protocol, and the appropriate citation has been updated accordingly.

Missing DOIs have been added wherever available, and entries without DOIs have been clearly marked as “DOI not available” in accordance with journal requirements. Additionally, the foundational work of Rout and Das (1993) has now been discussed in the Discussion section, including a comparison of BA-mediated shoot induction, IBA-based rooting response, and acclimatization performance with our present findings.

Comment 19

4.4 Data availability and ethics The Data Availability statement asserts that “no protein/DNA/RNA sequence” data are produced. The RAPD/ISSR raw gel images and band-presence matrices, the GC-MS raw .D files, and the spectrophotometric raw data should still be made available (e.g., on Mendeley Data or Zenodo) to support reproducibility per MDPI policy. Please add a permanent repository link.

Explanation

We thank the reviewer for this important suggestion regarding data availability and reproducibility. We would like to clarify that no high-throughput sequencing or omics-scale datasets were generated in this study. The RAPD and ISSR analyses were performed using standard gel-based profiling, and representative gel images and summarized banding patterns have already been included in the manuscript. The GC-MS analysis was conducted using routine instrument output files provided by the facility, and processed chromatograms and identified peaks are presented in the figures and supplementary materials.

In line with this, the raw data underlying gel-based and spectrophotometric measurements are limited in scope and are archived within the laboratory records. Given the nature and size of the datasets, a dedicated public repository deposition (e.g., Zenodo/Mendeley Data) was not initially prepared. However, we acknowledge the importance of data transparency and have now revised the Data Availability statement to explicitly indicate that all relevant supporting data are included within the manuscript and supplementary files, and that additional raw data can be made available from the corresponding author upon reasonable request.

We have ensured that this clarification is consistent with MDPI data availability requirements for non-sequencing, gel-based experimental studies.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The strongest point is the integrated workflow: direct organogenesis from nodal explants, rooting, acclimatization, histology, SEM, RAPD/ISSR, antioxidant physiology, and GC-MS profiling in Madhuca indica. The novelty is moderate, and mostly species-specific plus integrative, not conceptual. The Introduction explicitly argues that most previous work has focused on the closely related M. longifolia var. latifolia, and the reference list indeed includes an older micropropagation paper on that taxon and a recent callus/somatic embryogenesis paper, rather than a comparable direct organogenesis study in M. indica itself. That gives the manuscript a real niche. However, the technical components are all standard. A more important limitation is that the explants were taken from aseptic seedlings, not from a mature elite donor tree. That means the study demonstrates regeneration from juvenile seed-derived material, not true clonal multiplication of a selected genotype for forestry or plantation deployment. This reduces the practical novelty and translational value of the protocol as a mass clonal-propagation system.

The discrepancies and internal problems have been detected in the manuscript. The first major issue is a taxonomic/nomenclatural ambiguity. The paper is framed as a study on Madhuca indica, yet the Introduction acknowledges that the literature largely concerns M. latifolia, and several references in the bibliography switch between M. indica, M. longifolia, and M. longifolia var. latifolia. The manuscript needs to state clearly whether the authors treat these names as synonyms, related taxa, or distinct taxa, and why the present voucher should be interpreted as M. indica.

Second, the methods numbering is broken. The paper goes from 2.2 Rooting and Acclimatization directly to 2.4 Genetic fidelity, with section 2.3 missing. That is a basic editorial error and suggests the manuscript has not been carefully finalized.

Third, the Results report 42 phytochemicals in the mother-plant extract and 53 phytochemicals in the in vitro plantlets, with several marked quantitative differences. The conclusion should not present this as straightforward equivalence without stronger statistics or targeted validation.

Fourth, there is a figure citation error in the GC-MS section. The text says the mother-plant methanolic extract profile is shown in Fig. 7, but Figure 7 is clearly the RAPD/ISSR gel image. The mother-plant GC-MS chromatogram is Figure 8, and the in vitro plantlet chromatogram is Figure 9.

Fifth, the GC-MS methods include an implausible sample statement: 500 g of leaves were gathered from “an in vitro-raised M. indica plant” for GC-MS. For a four-week-old in vitro-derived plantlet, that quantity is not credible as written.

Sixth, the statistical reporting is inconsistent. The Methods say Tukey’s test was used after one-way ANOVA, whereas the Figure 6 legend says Duncan’s multiple range test. Both cannot be correct.

Seventh, the GC-MS tables themselves raise concerns. Some compounds appear duplicated under the same or closely similar names across different peaks, and some entries such as dibutyl phthalate and phthalic acid may reflect contamination rather than genuine plant metabolites. The manuscript does not discuss this at all.

Eighth, one sentence in the GC-MS results is mathematically wrong: “Other important compounds with lesser (>3%) percentage area include tetradecanoic acid (2.33%)…” A value of 2.33% is not greater than 3%.

Ninth, the fidelity analysis is useful but still limited. The study uses 9 regenerants, 8 informative RAPD primers, and 9 informative ISSR primers. That supports preliminary clonal uniformity, but it is still a relatively narrow sampling frame for strong claims of genetic stability, especially when the final application is large-scale planting material. In addition, as soon as seedlings (not vegetatively propagated plants) served as initial material for in vitro culture, this block seems strange. Otherwise, methodological part has to be clarified.

Tenth, the conclusion is overstated. The manuscript claims the protocol supports large-scale plantation, consistent production of bioactive compounds, and even points toward CRISPR-based improvement, yet the actual data are based on seedling-derived explants, short-term acclimatization, a modest set of fidelity markers, and semi-qualitative phytochemical profiling. That conclusion needs to be narrowed.

Chapter-by-chapter assessment and what should be improved

Title

The title is understandable, but “metabolic” is too broad for what was actually done. This is a GC-MS phytochemical comparison, not a real metabolomics study. A more precise title would improve scientific accuracy.

Abstract

The Abstract is generally clear and reports the main protocol values well. But it overstates the GC-MS result as “consistent production of bioactive compounds” and presents the study as more validation-heavy than it really is. The abstract should state that phytochemical profiling showed substantial overlap with some quantitative differences, not simple equivalence. It should also mention that the explants were seedling-derived, because that affects interpretation of the propagation claim.

Introduction

This section gives a good applied rationale for the species and explains its economic significance well. Its main weakness is the unresolved taxonomy and the vague literature gap. The authors should explicitly contrast their study with: (i) prior work on M. longifolia var. latifolia, and (ii) any existing reports on organogenesis versus somatic embryogenesis. They also need to justify why nodal explants from seedlings were chosen if the goal is clonal multiplication and conservation of valuable genotypes.

Methodology

This is the section most in need of revision. The authors should clearly specify the origin of the “mother plant” used in genetic and GC-MS comparisons, and its relationship to the seed-derived in vitro seedlings. The current wording leaves it ambiguous whether the regenerants are being compared to the original seedling donor or to a separate field plant. The GC-MS methods need fuller instrumental details and corrected sample quantities. The statistical section must also reconcile Tukey versus Duncan.

A second methodological concern is conceptual: because the starting explants came from aseptic seedlings, the protocol is not yet demonstrated for elite adult material, which is usually the more difficult and more commercially relevant target in woody species. That limitation should be openly acknowledged.

Results: shoot induction and multiplication

provide actual sample sizes for the survival calculation and possibly longer-term field performance data, rather than stopping at early establishment.

Histology and SEM strengthen the paper because it supports a direct organogenic pathway and documents structural adjustment during acclimatization. The histological images on page 10 do support shoot-bud dome formation with leaf primordia, and the SEM panels on page 11 do show the expected transition from poorly differentiated, more closed stomata in vitro to more developed, open stomata ex vitro. What is missing is stronger interpretation of how these observations relate quantitatively to survival and function. At present, they remain largely descriptive.

The physiological trend is coherent: chlorophyll and net photosynthetic rate decline early during acclimatization and then recover, while antioxidant enzyme activities rise during ex vitro transition. This is biologically plausible. But the section would be stronger if the authors linked these measurements more directly to stomatal adjustment and acclimatization success, rather than presenting them as parallel observations.

GC-MS analysis is the weakest analytical section. It is interesting, but currently over-interpreted. The mother plant and in vitro plantlets share several dominant constituents, but the overall profiles are not identical, and the manuscript does not provide statistical comparison, replicate chromatograms, or targeted compound validation. The duplicated compound assignments and likely contaminant peaks require discussion. Also, the figure numbering error here needs correction.

Discussion

The Discussion is scientifically serviceable, but too much of it is generic background about tissue culture, antioxidants, and SEM rather than focused interpretation of the present dataset. It should be tightened substantially. The most important issues the authors need to discuss directly are: the seedling-derived donor limitation, the taxonomic ambiguity, the limited depth of the fidelity analysis, and the fact that GC-MS results show overlap plus divergence rather than strict metabolite equivalence.

Conclusion

The first paragraph is stronger than the second. It is reasonable to conclude that the study developed a useful direct organogenesis protocol and achieved good acclimatization. It is not yet reasonable to conclude that the system is ready for industrial compound standardization or plantation-scale clonal deployment without further validation in mature elite genotypes and longer-term field testing. The CRISPR/genome-editing paragraph is speculative and feels disconnected from the data. It should be shortened or removed.

Author Response

Response to the Reviewer#2

The strongest point is the integrated workflow: direct organogenesis from nodal explants, rooting, acclimatization, histology, SEM, RAPD/ISSR, antioxidant physiology, and GC-MS profiling in Madhuca indica. The novelty is moderate, and mostly species-specific plus integrative, not conceptual. The Introduction explicitly argues that most previous work has focused on the closely related M. longifolia var. latifolia, and the reference list indeed includes an older micropropagation paper on that taxon and a recent callus/somatic embryogenesis paper, rather than a comparable direct organogenesis study in M. indica itself. That gives the manuscript a real niche. However, the technical components are all standard. A more important limitation is that the explants were taken from aseptic seedlings, not from a mature elite donor tree. That means the study demonstrates regeneration from juvenile seed-derived material, not true clonal multiplication of a selected genotype for forestry or plantation deployment. This reduces the practical novelty and translational value of the protocol as a mass clonal-propagation system.

Explanation

We thank the reviewer for this thoughtful and balanced assessment of the manuscript. We agree that the strength of the study lies in the development of an integrated regeneration workflow in Madhuca indica, combining direct organogenesis from nodal explants with rooting, acclimatization, histological and ultrastructural validation, genetic fidelity assessment, physiological characterization, and GC–MS profiling. We also acknowledge the reviewer’s point that the overall novelty is primarily species-specific and integrative in nature, rather than representing a new conceptual framework in plant tissue culture.

We further appreciate the important clarification regarding the origin of explant material. In the present study, nodal segments were derived from aseptically raised seedlings rather than mature elite donor trees. Therefore, the protocol primarily demonstrates efficient regeneration from juvenile seed-derived material and confirms the biological feasibility of direct organogenesis in M. indica. We agree that this limits the immediate application of the system as a true large-scale clonal propagation strategy for selected superior genotypes in forestry or plantation programs.

This limitation has now been explicitly acknowledged in the revised manuscript, and the Discussion/Conclusion sections have been moderated to reflect that the study establishes a reliable baseline regeneration system, which may serve as a foundation for future work involving mature elite donor material and field-selected genotypes for translational deployment.

Comment 1

The discrepancies and internal problems have been detected in the manuscript. The first major issue is a taxonomic/nomenclatural ambiguity. The paper is framed as a study on Madhuca indica, yet the Introduction acknowledges that the literature largely concerns M. latifolia, and several references in the bibliography switch between M. indica, M. longifolia, and M. longifolia var. latifolia. The manuscript needs to state clearly whether the authors treat these names as synonyms, related taxa, or distinct taxa, and why the present voucher should be interpreted as M. indica.

Explanation

We sincerely thank the reviewer for this important and critical observation regarding the taxonomic and nomenclatural consistency of the manuscript. We fully agree that clarity in species delimitation and usage is essential for correct interpretation of the results.

In response, we have carefully revised the manuscript to explicitly clarify the taxonomic framework adopted in this study. The present work is based on Madhuca indica J.F.Gmel., and the plant material used was authenticated by a taxonomist. We have now clearly stated in the revised Introduction and Materials and Methods that the study is conducted on M. indica, and that previous micropropagation reports on M. longifolia var. latifolia are included only for comparative context due to close taxonomic relatedness and overlapping usage in the literature.

We further clarify that M. indica, M. longifolia, and M. longifolia var. latifolia are treated in this manuscript as closely related but distinct taxa, and all comparative references have been rephrased to avoid ambiguity. The Introduction has been revised to explicitly justify the relevance of earlier M. longifolia studies as methodological comparisons rather than taxonomic equivalence (Lines 77-89).

Additionally, we have ensured that M. indica is consistently used throughout the manuscript, and all references, comparisons, and discussions have been harmonized accordingly to remove nomenclatural inconsistency and improve taxonomic clarity.

Comment 2

Second, the methods numbering is broken. The paper goes from 2.2 Rooting and Acclimatization directly to 2.4 Genetic fidelity, with section 2.3 missing. That is a basic editorial error and suggests the manuscript has not been carefully finalized.

Explanation

We thank the reviewer for identifying this formatting issue. We acknowledge that the Methods section contained a numbering inconsistency due to a typographical and final formatting oversight, where Section 2.3 was inadvertently omitted in the sequence.

This has now been carefully corrected in the revised manuscript. All Methods subsections have been renumbered sequentially, and cross-references within the text have been updated accordingly to ensure consistency and accuracy throughout the manuscript. We appreciate the reviewer’s attention to detail, which has helped improve the overall clarity and presentation of the Methods section.

Comment 3

Explanation

We thank the reviewer for this important clarification. We agree that the initial wording could be interpreted as implying direct equivalence in phytochemical composition between mother plants and in vitro-derived plantlets.

In the revised manuscript, we have carefully moderated this interpretation across the Results, Discussion, and Conclusions. Specifically, we no longer present the GC-MS findings as indicating straightforward chemical equivalence or quantitative parity between the two plant sources. Instead, the revised text now describes the GC-MS analysis as a comparative metabolic profiling approach that identifies shared and differential metabolite presence and relative abundance (Lines 430-441; 659-676; 678-690).

Accordingly, statements implying equivalence in phytochemical number or uniformity have been removed or rephrased. The Discussion and Conclusions now emphasize that the observed differences reflect variation in metabolite expression profiles under in vitro versus natural growth conditions, and that no claim of statistical equivalence is made without targeted quantitative validation. We believe this revision appropriately aligns the interpretation with the scope and resolution of the GC-MS analysis performed in this study.

Comment 4

Explanation

Thank you for pointing out. The citation has been corrected.

Comment 5

Explanation

We thank the reviewer for carefully identifying this typographical error in the GC–MS methodology. We confirm that the reported value of “500 g” was a mistake and is not correct. The correct amount of plant material used for GC–MS analysis was 500 mg of fresh leaf tissue from in vitro-derived plantlets. This has now been corrected in the revised manuscript to accurately reflect the experimental procedure (Line 237).

Comment 6

Explanation

We thank the reviewer for identifying this inconsistency in the statistical reporting. We confirm that one-way ANOVA followed by Tukey’s HSD test was consistently used for all analyses throughout the study. The mention of Duncan’s multiple range test in the Figure 6 legend was an inadvertent error. This has now been corrected in the revised manuscript, and all figure legends and corresponding text have been updated to ensure consistency in reporting Tukey’s post hoc test across the Methods, Results, and figure descriptions.

Comment 7

Explanation

We sincerely thank the reviewer for this careful and insightful observation regarding the GC–MS dataset. In response, we have thoroughly re-examined and revised Tables 6 and 7 in the manuscript.

Compounds that appeared more than once due to closely similar peak annotations or retention times have been critically reviewed and are now treated as repeated detections or potential analytical/structural variants rather than distinct phytochemical entities, thereby removing redundancy in compound listing. In addition, we agree with the reviewer that certain compounds such as dibutyl phthalate and related phthalate derivatives are most likely laboratory or analytical contaminants rather than true plant-derived metabolites. These entries have now been clearly flagged in the revised tables and excluded from biological interpretation. Accordingly, the GC–MS section and related discussion have been revised to reflect a cautious interpretation of the dataset, emphasizing its qualitative and preliminary nature. Overstatements regarding differences in compound numbers and metabolic complexity between mother plants and in vitro plantlets have been removed, and the focus has been shifted to comparison of major phytochemical classes rather than absolute compositional differences.

Comment 8

Eighth, one sentence in the GC-MS results is mathematically wrong: “Other important compounds with lesser (>3%) percentage area include tetradecanoic acid (2.33%)…” A value of 2.33% is not greater than 3%.

Explanation

We thank the reviewer for identifying this numerical inconsistency. We agree that the statement was incorrect and misleading. In the revised manuscript, this sentence has been completely removed and the GC–MS Results section has been carefully revised to avoid any erroneous threshold-based interpretation of percentage peak areas.

All compound descriptions are now reported strictly as identified peaks with their corresponding relative abundances, without inappropriate categorical statements. We appreciate the reviewer’s attention to detail, which has helped improve the accuracy and clarity of the GC–MS results section (Line 429-441).

Comment 9

Ninth, the fidelity analysis is useful but still limited. The study uses 9 regenerants, 8 informative RAPD primers, and 9 informative ISSR primers. That supports preliminary clonal uniformity, but it is still a relatively narrow sampling frame for strong claims of genetic stability, especially when the final application is large-scale planting material. In addition, as soon as seedlings (not vegetatively propagated plants) served as initial material for in vitro culture, this block seems strange. Otherwise, methodological part has to be clarified.

Explanation

We sincerely thank the reviewer for this insightful and constructive comment regarding the scope and interpretation of the genetic fidelity analysis. We agree that the RAPD and ISSR-based assessment performed on nine regenerants using eight RAPD and nine ISSR informative primers provides only a preliminary evaluation of genetic uniformity. The intention of this analysis was to assess clonal stability at the level resolvable by dominant marker systems under the present experimental framework, rather than to make definitive claims regarding long-term genetic stability at a population scale.

We also acknowledge the reviewer’s important point regarding the use of aseptic seedling-derived nodal explants. In this study, the starting material was not vegetatively propagated elite clones but seed-derived juvenile material, which inherently represents a genetically heterogeneous origin. Therefore, the observed uniformity among regenerants reflects the stability of the in vitro regeneration pathway under the applied culture conditions, rather than true clonal fidelity of a single elite genotype across large-scale propagation.

Accordingly, the relevant statements in the manuscript have been revised to moderate claims of “genetic stability” and “clonal uniformity,” and have been rephrased as “no detectable polymorphism within the resolution of RAPD and ISSR markers used.” We believe this revision more accurately reflects the scope and limitations of the data (Lines 655-662; 693-695).

Comment 10

Explanation

We thank the reviewer for this important and insightful observation. We agree that the original Conclusion contained statements that extended beyond the direct scope of the experimental data, particularly regarding large-scale plantation potential, consistency of bioactive compound production, and prospective genome-editing applications.

In the revised manuscript, the Conclusion has been thoroughly rewritten to ensure it accurately reflects the actual findings of the study. All overstatements have been removed, and the interpretation has been narrowed to the experimentally supported outcomes, including successful establishment of a direct organogenesis protocol from seedling-derived nodal explants, acclimatization performance, histological confirmation, marker-based genetic fidelity within the limits of RAPD/ISSR resolution, and preliminary GC–MS-based comparative profiling.

Forward-looking statements regarding large-scale plantation applicability, metabolite consistency, and advanced genetic engineering approaches have been moderated and repositioned as general future perspectives rather than direct implications of the present data. We believe the revised Conclusion now appropriately aligns with the scope and strength of the experimental evidence (Lines 686-700).

Comment 11

Title

Explanation

We thank the reviewer for this valuable suggestion. We agree that the term “metabolic” was overly broad in the context of our study, as the work is based on GC–MS-based phytochemical profiling rather than comprehensive metabolomics analysis. Accordingly, the title has been revised to more accurately reflect the scope of the study. The term “metabolic” has been replaced with ‘GC–MS analysis’ to ensure scientific precision and avoid overinterpretation of the analytical approach used.

Comment 12

Abstract

Explanation

We thank the reviewer for this valuable suggestion. The abstract has been revised as per the suggestions (Lines 40-48).

Comment 13

Introduction

Explanation

We thank the reviewer for this constructive comment. In the revised Introduction, we have addressed the highlighted concerns by explicitly clarifying the taxonomic context and refining the literature gap. The manuscript now clearly distinguishes the present work on M. indica from previous micropropagation studies on M. longifolia var. latifolia, which are cited only for methodological comparison rather than taxonomic equivalence.

We have also strengthened the literature gap by briefly contrasting previous reports. In addition, we have explicitly justified the use of aseptic seedling-derived nodal explants as an initial and experimentally tractable system for establishing a reproducible regeneration protocol, while clearly stating that this represents a baseline system rather than true clonal propagation of elite genotypes (Lines 40-48; 75-107).

Comment 14

Methodology

Explanation

We thank the reviewer for this detailed and important comment. In the revised manuscript, we have clarified the origin and relationship of all plant materials used in the study. The “mother plant” used for genetic fidelity and GC–MS comparisons have now been clearly defined as the authenticated field-grown donor tree (voucher No. 24231), while the in vitro regenerants were derived from aseptic seedling-origin nodal explants obtained from seeds of the same identified source, and this has been explicitly stated in the Methodology to remove any ambiguity.

We have also revised the GC–MS methodology section by adding complete instrumental and analytical details and correcting the previously reported sample quantity. In addition, the statistical analysis section has been carefully corrected to ensure consistency, confirming that one-way ANOVA followed by Tukey’s HSD test was used throughout the study, and all references to Duncan’s multiple range test have been removed. We believe these revisions have significantly improved the clarity, reproducibility, and methodological rigor of the manuscript.

Comment 15

A second methodological concern is conceptual: because the starting explants came from aseptic seedlings, the protocol is not yet demonstrated for elite adult material, which is usually the more difficult and more commercially relevant target in woody species. That limitation should be openly acknowledged.

Explanation

We thank the reviewer for this important conceptual observation. We acknowledge that the present study was conducted using aseptic seedling-derived nodal explants (juvenile material), and therefore the protocol has not yet been validated on mature elite donor trees, which represent a more commercially relevant and regeneration-recalcitrant system in woody species.

This limitation has now been explicitly added in the revised manuscript under the conclusion section (Lines 700-703), along with appropriate clarification in the Introduction and discussion. We agree that this provides a more accurate representation of the current scope and applicability of the protocol.

Comment 16

Results: shoot induction and multiplication

provide actual sample sizes for the survival calculation and possibly longer-term field performance data, rather than stopping at early establishment.

Explanation

We thank the reviewer for this important suggestion regarding sample size transparency and long-term validation. In the revised manuscript, we have now clearly specified the actual experimental design, including the number of explants per treatment (20 per replicate) and the number of independent experimental repeats (three), providing a total sample size of 60 per treatment.

We also acknowledge that the present study is limited to in vitro regeneration and acclimatization stages, and does not include long-term field performance data. This limitation has been explicitly stated in the revised manuscript under the relevant section. Future studies will focus on field establishment and long-term survival assessment of regenerated plants to further validate the practical applicability of the protocol.

Comment 17

Histology and SEM strengthen the paper because it supports a direct organogenic pathway and documents structural adjustment during acclimatization. The histological images on page 10 do support shoot-bud dome formation with leaf primordia, and the SEM panels on page 11 do show the expected transition from poorly differentiated, more closed stomata in vitro to more developed, open stomata ex vitro. What is missing is stronger interpretation of how these observations relate quantitatively to survival and function. At present, they remain largely descriptive.

Explanation

We thank the reviewer for this constructive observation. We agree that the histological and SEM analyses presented in this study are primarily descriptive and were intended to confirm the direct organogenic origin of regenerated shoots and to document anatomical changes occurring during acclimatization. Quantitative measurements of stomatal density, guard cell dimensions, and their statistical relationship with survival or physiological performance were not included in the present study.

In the revised manuscript, we have strengthened the Discussion by providing a more mechanistic interpretation of the observed anatomical changes, particularly the development of functional stomata, improved epidermal organization, and increased epicuticular wax deposition during acclimatization. These features are discussed in relation to improved regulation of water loss, gas exchange, and adaptation to ex vitro conditions. We have also acknowledged the absence of quantitative SEM measurements as a limitation and identified this as an important direction for future research (Lines 632-641).

Comment 18

Explanation

We thank the reviewer for this valuable suggestion. In the revised Discussion, we have strengthened the interpretation by linking the physiological and biochemical responses observed during acclimatization with the structural changes revealed by SEM. Specifically, the recovery of chlorophyll content and net photosynthetic rate, together with increased antioxidant enzyme activities, is now discussed in relation to the development of functional stomata, improved epidermal organization, and enhanced epicuticular wax deposition in ex vitro-acclimatized plantlets. We agree that these processes are interconnected components of acclimatization success and have revised the text accordingly while avoiding interpretations beyond the scope of the data collected (Line 576-596).

Comment 19

GC-MS analysis is the weakest analytical section. It is interesting, but currently over-interpreted. The mother plant and in vitro plantlets share several dominant constituents, but the overall profiles are not identical, and the manuscript does not provide statistical comparison, replicate chromatograms, or targeted compound validation. The duplicated compound assignments and likely contaminant peaks require discussion. Also, the figure numbering error here needs correction.

Explanation

We thank the reviewer for this careful evaluation of the GC–MS section. We agree that the original version may have over-interpreted the phytochemical profiling data. In the revised manuscript, we have substantially moderated our conclusions and no longer present the GC–MS results as evidence of phytochemical equivalence between mother plants and in vitro-derived plantlets. Instead, the analysis is now described as a preliminary qualitative comparison showing the presence of several common metabolite classes together with differences in the relative abundance and occurrence of specific compounds.

We have also carefully re-examined Tables 6 and 7 to address duplicated compound assignments and have clarified cases where repeated detections may represent isomeric or analytical variants rather than distinct phytochemicals. Furthermore, compounds such as dibutyl phthalate and related phthalate derivatives have been explicitly discussed as potential contaminants or analytical artefacts and excluded from biological interpretation. The revised manuscript now clearly acknowledges that the GC–MS analysis was based on a single biological replicate per condition and lacks statistical validation, replicate chromatograms, and targeted compound confirmation. These limitations have been stated in both the Results and Discussion sections. In addition, all figure numbering inconsistencies have been corrected throughout the manuscript.

Comment 20

Discussion

Explanation

We thank the reviewer for this thoughtful assessment. In response, the Discussion has been substantially revised and streamlined to focus more directly on interpretation of the present findings rather than providing extensive general background information. Several sections have been condensed, and greater emphasis has been placed on the specific outcomes and limitations of the current study.

In particular, we have now explicitly discussed: (i) the use of seedling-derived nodal explants and the resulting limitation that the protocol has not yet been validated on mature elite donor trees; (ii) the taxonomic context of Madhuca indica and its distinction from previous studies conducted on M. longifolia var. latifolia; (iii) the scope and limitations of the RAPD/ISSR-based genetic fidelity assessment, which supports the absence of detectable polymorphism within the sampled regenerants but does not exclude variation beyond the resolution of the marker systems used; and (iv) the GC–MS results as a preliminary phytochemical comparison showing both overlap and divergence in metabolite profiles rather than strict chemical equivalence. We believe these revisions provide a more balanced and data-driven discussion of the study findings (Lines 483-505; 513-521; 538-541; 570-590; 626-635; 649-656; 661-677).

Comment 21

Conclusion

Explanation

Thank you for the suggestions. The conclusion has been re-written completely (Lines 680-697).

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

In the online sstem Madhuca Indica is mentioned as a co-author it might be by mistake, during submission and autofill

Author Response

We would like to clarify that the appearance of "Madhuca indica" as a co-author in the online submission system was an inadvertent error that occurred during the manuscript submission process. It appears to have been generated or selected automatically through the system's autofill function and was not intentionally entered as an author.

"Madhuca indica" is the plant species investigated in the study and should not be listed as a co-author. The correct authorship information is provided in the manuscript file and author metadata submitted with the article.

As this issue is related solely to the submission system metadata, we kindly request that the incorrect author entry be removed and the author list be updated according to the manuscript records. We understand that such corrections can only be made internally by the editorial office or production team.

We apologize for this oversight and appreciate your assistance in correcting the author information.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors did a great work and improved the manuscript significantly.

Author Response

We sincerely thank the reviewer for the positive evaluation of our work and for recognizing the improvements made to the manuscript. We appreciate the constructive comments and suggestions, which have helped us enhance the quality and clarity of the study.