Melatonin Targets Mitochondrial Redox Homeostasis: Optimizing the Intracellular Microenvironment

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Comments on Reiter et al.

Given the significance of melatonin, and its relationship with mitochondrial redox biology, oxidative stress, and disease relevance, this review article is broad, timely, and of clear interest to IJMS readers. The manuscript also attempts to tackle a specific controversy regarding the function of melatonin as a direct radical scavenger and its mitochondrial synthesis. This gives the review a sharper purpose than a generic narrative overview. The manuscript further includes mechanistic discussion spanning chemical scavenging assays, mitochondrial localization, metabolites, lipid microdomains, and biomolecular condensates, so the scope is ambitious and potentially valuable across various fields.

 

A few comments are as below.

 

1. The central thesis is strongly stated from the abstract, throughout the main text, and the conclusion again emphasizes majority of evidence in favor of direct antioxidant actions. However, the manuscript does not distinguish between what is firmly established, what is strongly suggestive, and what remains inferential or controversial. Simply relying on the majority of studies supporting one aspect is not reliable. It requires critical analysis (see comment 7 below). This is the main weakness in its current form.
2. The overall flow of the article is understandable but not fully optimized. The review moves from mitochondrial ROS generation to direct radical scavenging chemistry, to metabolites, to quantum calculations, then to biomolecular condensates, lipid rafts, and finally mitochondrial synthesis/uptake and conclusion. On paper, that sequence is reasonable. In practice, the narrative often feels cumulative rather than analytical. A stronger structure would separate the review into clearer sections guiding the central thesis. For example: a distinct section on evidence of direct radical scavenging, emerging controversial/speculative mechanisms, indirect redox-modulating actions, evidence of mitochondrial synthesis/localization of melatonin, therapeutic implications and future directions/open questions. This is just a suggestion if the authors are willing to consider.
3. At present, the sections on lipid rafts and biomolecular condensates feel abrupt and disconnected from the central theme. The condensate section in particular introduces dense biophysical language and claims about viscosity, ergodic assemblies, and rheological transitions, but the transition into that topic is abrupt and the direct causal link to melatonin is not developed with the same rigor as the earlier chemistry sections.
4. The early sections summarizing ESR, pulse radiolysis, spin trapping, and related chemistry are useful and likely valid as a historical direct radical scavenging evidence. It also shows the direct receptor-independent chemistry can occur in cell-free systems. That point is legitimate and important. But the manuscript too often moves from “chemical plausibility” to “physiological importance” without sufficient critical qualification. For example:
   a. The authors acknowledge that some early studies found limited efficacy against superoxide, yet the discussion still trends toward a one-sided rehabilitation of melatonin’s in vivo antioxidant relevance.
   b. The authors repeatedly assert high intramitochondrial melatonin concentrations and broad mitochondrial synthesis in peripheral cells, but such claims require tighter discussion of methodological limitations, cell-type specificity, and competing interpretations.
   c. Computational and docking-based sections are presented as supportive, but these methods should be framed as hypothesis-supporting rather than confirmatory evidence for biological function.

5. The tone of claims needs moderation. For example, the phrases aimed at “dispelling” opposing views by the “sheer volume and uniformity” of evidence, are not appropriate for a high-level review. A review should synthesize and critically evaluate. The current tone risks undermining credibility, especially for readers who are not already aligned with the authors’ position.
6. The manuscript should separate direct radical scavenging from indirect redox regulation through enzymes, signaling, mitochondrial efficiency, and receptor-dependent pathways. In its current form there is no proper segregation which oftentimes deviates the article from its central theme.
7. A final summary table would help greatly: assay type, radical species, model system, main finding, physiological relevance, and limitations.

Overall, this review addresses a significant and timely topic and contains a substantial amount of potentially valuable information for the readers. However, in its current form the manuscript is not sufficiently balanced or critical for a review article. The manuscript would be much stronger if it were reorganized around levels of evidence, revised to adopt a more objective tone, and expanded to address key limitations, unresolved controversies, and physiological constraints.

Comments for author File: Comments.pdf

Author Response

The authors commend the reviewers on their insightful and comprehensive review of the paper.  Their comments are generally pointed and thoughtful and suggest caution in the interpretation of some of the data.  This is always a worthy suggestion, since scientific techniques are not necessarily infallible.  In consideration of the constructive comments that were made, the manuscript has been revised on the basis of their recommendations. 

1. The central thesis is strongly stated from the abstract, throughout the main text, and the conclusion again emphasizes majority of evidence in favor of direct antioxidant actions. However, the manuscript does not distinguish between what is firmly established, what is strongly suggestive, and what remains inferential or controversial. Simply relying on the majority of studies supporting one aspect is not reliable. It requires critical analysis (see comment 7 below). This is the main weakness in its current form.

Classifying data according to its strength is inherently a difficult task and surely “not everything the glitters is gold”.  The final judgement related to the validity of a claim is usually based on the collective data rather than on a few potential reports that are outliers.  In the current review the authors attempt to summarize the bulk of the published data to make their point.  However, in consideration of the reviewer’s concern, we have re-examined the data and attempted to be more critical of some findings. The changes are identified in the abstract as well as throughout the revised manuscript.

2. The overall flow of the article is understandable but not fully optimized. The review moves from mitochondrial ROS generation to direct radical scavenging chemistry, to metabolites, to quantum calculations, then to biomolecular condensates, lipid rafts, and finally mitochondrial synthesis/uptake and conclusion. On paper, that sequence is reasonable. In practice, the narrative often feels cumulative rather than analytical. A stronger structure would separate the review into clearer sections guiding the central thesis. For example: a distinct section on evidence of direct radical scavenging, emerging controversial/speculative mechanisms, indirect redox-modulating actions, evidence of mitochondrial synthesis/localization of melatonin, therapeutic implications and future directions/open questions. This is just a suggestion if the authors are willing to consider.

Indeed, the authors are definitely willing to consider this suggestion.

3. At present, the sections on lipid rafts and biomolecular condensates feel abrupt and disconnected from the central theme. The condensate section in particular introduces dense biophysical language and claims about viscosity, ergodic assemblies, and rheological transitions, but the transition into that topic is abrupt and the direct causal link to melatonin is not developed with the same rigor as the earlier chemistry sections.

To make the transition into liquid-liquid phase separation more clear, we have added the following sentences and reference to introduce the topic. “Liquid-liquid phase separation (LLPS) is a rapidly emerging subject of interest in free radical biology as well as in melatonin’s involvement in processes related to formation of membrane lipid rafts and cytosolic biomolecular condensates (BCs) [97,98]. The process of LLPS modulates free radicals and has potential clinical applications [99].” To the end of that section, we also added the following: “Since melatonin modulates LLPS resulting in changes in the redox environment, its antioxidant actions may be essential agent to support and maintain this process in both the membranes and cytosol.”

Also, the reviewer may want to examine Section 7. Melatonin, Oxidative Load, Lipid Rafts and Mitochondrial Lipid Microdomains for additional information related to melatonin, LLPS, and mitochondrial physiology.

4. The early sections summarizing ESR, pulse radiolysis, spin trapping, and related chemistry are useful and likely valid as historical direct radical scavenging evidence. It also shows direct receptor-independent chemistry can occur in cell-free systems. That point is legitimate and important. But the manuscript too often moves from “chemical plausibility” to “physiological importance” without sufficient critical qualification. For example:
The authors acknowledge that some early studies found limited efficacy against superoxide, yet the discussion still trends toward a one-sided rehabilitation of melatonin’s in vivo antioxidant relevance.
b. The authors repeatedly assert high intramitochondrial melatonin concentrations and broad mitochondrial synthesis in peripheral cells, but such claims require tighter discussion of methodological limitations, cell-type specificity, and competing interpretations.
c. Computational and docking-based sections are presented as supportive, but these methods should be framed as hypothesis-supporting rather than confirmatory evidence for biological function.

The reviewer introduces an important caution due to a chronic problem in free radical biology, i.e., proving specific reactions occur in vivo.  In response to these issues the authors have made changes (identified in the text) and have included the following paragraph. "Although the published reports leave little doubt that melatonin directly neutralizes a number of radical species under the conditions of the studies, proving these reactions occur in vivo is far more difficult.  This is an issue with all radical scavengers. Generally, their efficacy in vivo is determined by biochemical footprints that are formed such as for vitamin C, the oxidized product dehydroascorbic acid. For melatonin, the biochemical footprints are cyclic 3-hydroxy melatonin, AMK and AFMK. This evidence provides chemical plausibility but does not definitively establish physiological relevance. "  

5. The tone of claims needs moderation. For example, the phrases aimed at “dispelling” opposing views by the “sheer volume and uniformity” of evidence, are not appropriate for a high-level review. A review should synthesize and critically evaluate. The current tone risks undermining credibility, especially for readers who are not already aligned with the authors’ position.

We have changed the words/phrases in question and tempered other statements that may be interpreted as being too strong. (identified in the text).

6. The manuscript should separate direct radical scavenging from indirect redox regulation through enzymes, signaling, mitochondrial efficiency, and receptor-dependent pathways. In its current form there is no proper segregation which oftentimes deviates the article from its central theme.

This is certainly an important point.  The direct free radical scavenging actions are receptor independent processes, while the promotion of antioxidative enzymes is likely receptor mediated.  This has now been re-emphasized in the report by changes in the Conclusion section. To emphasize this, we included the following sentence: “For example, the upregulation of antioxidative enzymes as well as the promotion of glutathione production are believed to follow melatonin’s interaction with membrane and/or nuclear receptors.”

7. A final summary table would help greatly: assay type, radical species, model system, main finding, physiological relevance, and limitations.

The mechanisms, etc., are summarized in detail in 3. Melatonin: Silence of the Radicals and, including a table containing the same information would, we feel, be redundant.

Reviewer 2 Report

Comments and Suggestions for Authors

 

The review by Reiter et al is a new review on melatonin and mitochondria.

This review follows the last one, by  Tavartkiladze and Reiter (DOI: https://dx.doi.org/10.21275/SR251217152341) on a similar subject, entitled “Melatonin and Human Mitochondria: Physiology, Pathochemistry, and Immunogenetics” and dated December 2025. It covered the pathological aspects of melatonin in mitochondria, following recent works from that group. The basic claim of Prof Reiter has been “bacteria are full of melatonin”. They originated the mitochondria some billion years ago, and thus mitochondria are full of melatonin. This is Nature best invention to prevent mitochondria from oxidative stress. Now, the present review examines how melatonin are located in mitochondria.

Interestingly, in the introduction, Prof. Reiter writes (lines 77 to 80) : “In these publications, the authors claim the ability of melatonin to limit oxidative stress is merely a result of the promotion of antioxidative enzymes via actions that also involve its engagement with membrane receptors (so-called MT1 and MT2) or with quinone reductase 2 in the cytosol, an alleged melatonin binding site [6-10]”.

These sentences are not correct. These authors claim that melatonin is a scavenger, but that scavengers do not work in a living system, according to the 3 decades worth of scientifical publications of HJ Forman’s group. Please, refer to these works to explain how melatonin can be an exception.

Furthermore, these authors ‘individuals’ do not claim that melatonin actions are all melatonin receptors mediated. In fact, they claim that melatonin, as a proven antioxidant is an inducer of the enzymatic defenses against oxidation. It is my understanding that they also wrote a review on the subject (“Does Biochemical Life Exist for a Receptor Agonist Outside Its Receptor? The Case of Melatonin”).

These authors also claimed that melatonin inductive capacities, although perfectly demonstrated in living systems, are due to a potential binding of it with a potential NUCLEAR factor (receptor) that has escaped the findings of dozens of laboratories these 3 to 4 last decades.

What these authors also wrote is that at the concentrations used in all the preclinical models and in most of the animal models, the melatonin receptors are desensitize. Which means that they are NOT active. A general feature of all GPCRs.

1/ This said, the review surveys the evidence that mitochondria are full of melatonin. Unfortunately, these claims are for the most part indirect. We are still waiting for experiments demonstrating that pure mitochondria contains melatonin. The Authors claim that because the Suofu paper (ref 57) shows the presence of AANAT in mitochondria, it means that mitochondria is full of melatonin. But the presence of melatonin in the same mitochondria is not reported in this publication. Furthermore, the presence of MT receptors in mitochondria preparation is weakened by the fact that the preparation of brain mitochondria were not claimed to be pure, and that mitochondria from brain are extremely difficult to obtain free of brain membrane contaminant – that could contain… MT receptors.

2/ Prof Reiter’s group hypothesized, in 1993 that melatonin travels freely through biological membranes. This was proven very elegantly by Yu et al, in 2014. This particular paper pointed out that the free traveling through the membranes concerns ALL the biological membranes. And thus, that no subcellular compartment(s) could retain/trap melatonin within them.

3/ According to the previous point, melatonin cannot stay in mitochondria. The Authors should experimentally show, as a start, that melatonin is indeed trapped in pure mitochondria prepared from an abundant tissue (like muscles).

4/ For the scavenging capacity of melatonin, the Authors show a very nice figure of the “catabolism” of melatonin by ROS. This picture lacks 2 things: 1/ AFMK leads indeed to AMK by losing formic acid, an extremely toxic compound. This means that toxicity of ROS via melatonin would lead at least in part to acidosis in the mitochondria. And 2/ the quantity notion should be call in again. How much melatonin would be required to scavenge the continuous mitochondria production of ROS? According to the figure of lines 272, melatonin is able to scavenge ROS at a rate of 1.3 X 10¹⁰ M^-1s^-1. It would be helpful to the general reader to transform this constant in actual numbers. Why? Because, if the concentration of melatonin is so important in mitochondria, melatonin should be seen constantly in the cell (Melatonin travels freely though biological membranes). Now, if the amount of melatonin to counteract the ROS production is constant, it means that the source of serotonin in mitochondria should be quite gigantic as well. Furthermore, as known by The Authors, serotonin does not travel freely though the membranes. On the other hand, the compounds issued from the attacks of ROS onto melatonin should either accumulate in mitochondria - if they do not travel though the membranes – or be excreted from the mitochondria into the cells. I don’t think either of these hypotheses have been experimentally seen.

Of course, if the review is a global hypothesis, the title should clearly translate this fact, and researchers could start to experimentally address these questions.

5/ Concerning the expression of ANNAT in mitochondria, I have a bad time trying to find genetic evidence that mitoDNA encodes for AANAT, and as pointed out by the Individuals of references 7-10, and that this putative gene would be completely differently regulated than the pineal one. That is active at night, inactive during the day.

6/ As a last point, the innocuity of melatonin is still debated. I am very surprised that concerned Scientists working in Health area can claim that 1 gram (!!) of melatonin for 30 days is safe!!! (line 994 Melatonin has been given at a dose of 1,000 mg daily for 30 days with no evidence of toxicity [209]). In the meantime, the Authors cannot ignore publications on the possible link between melatonin and toddler sudden death, the link between cardiac problems and melatonin, and finally that some national agencies published warning on the use of over-the-counter melatonin (Australia, France, UK).

7/ The dose question remains also an open one. How much melatonin can circulate, how is the safety profile over the whole population, as well as for patients with severe health conditions (remember that melatonin is claimed to be effective as an adjuvant in most of the human diseases).

I read recently – in a paper by those Individuals (7-10) - that none of the 400 (ish) clinical trials implying melatonin treatment led to a clear effective conclusion. This should be also recalled along the recommendations of the present review (chapter 10:  “Conclusion: Final Thoughts Distilled”…)

Overall, I regret that the beliefs of Prof Reiter, that are fully respectable, could not be treated experimentally one by one, leading to a clear picture of the question: “Is there high concentrations of melatonin inside mitochondria? Where it come from? What is used to?

I am amazed that this is the 1350^th paper by Prof Reiter [since 1969, and according to the count in PubMed (“REITER RJ + melatonin“)] and that those questions are still open.

 

Author Response

We are grateful for the reviewer’s time taken to review this paper.  Input from any scientist even peripherally related to the subject is always important, especially when those individuals are doubtful about the value of melatonin.  Your comments certainly identified some possible weaknesses which we and many other scientists around the world are working on. We understand the resistance to melatonin since we have faced these headwinds for years. We feel the very large number of reports in both animals and plants that illustrate melatonin’s ability to reduce oxidative stress supports its antioxidant actions, be they due to direct scavenging or to indirect actions.  We have not made a large number of changes to the manuscript based on your review since they were primarily comments and are important for further consideration. Clearly, as a reviewer, you were providing us with valuable advice and points to consider as we move forward, and we accept them as serious comments.  It is always important to consider advice of experts in the field.  This is fair and we will surely take all your suggestions into consideration in our ongoing research.  We thank you for your comments and welcome them.  We are hopeful our explanations will satisfy you. 

The review by Reiter et al is a new review on melatonin and mitochondria. 

This review follows the last one, by  Tavartkiladze and Reiter (DOI: https://dx.doi.org/10.21275/SR251217152341) on a similar subject, entitled “Melatonin and Human Mitochondria: Physiology, Pathochemistry, and Immunogenetics” and dated December 2025. It covered the pathological aspects of melatonin in mitochondria, following recent works from that group. The basic claim of Prof Reiter has been “bacteria are full of melatonin”. They originated the mitochondria some billion years ago, and thus mitochondria are full of melatonin. This is Nature best invention to prevent mitochondria from oxidative stress. Now, the present review examines how melatonin are located in mitochondria.

Interestingly, in the introduction, Prof. Reiter writes (lines 77 to 80) : “In these publications, the authors claim the ability of melatonin to limit oxidative stress is merely a result of the promotion of antioxidative enzymes via actions that also involve its engagement with membrane receptors (so-called MT1 and MT2) or withquinone reductase 2 in the cytosol, an alleged melatonin binding site [6-10]”.

This sentence was not adequately specific and has been changed with the addition of information regarding melatonin’s stimulation of antioxidative enzymes.

These sentences are not correct. These authors claim that melatonin is a scavenger, but that scavengers do not work in a living system, according to the 3 decades worth of scientifical publications of HJ Forman’s group. Please, refer to these works to explain how melatonin can be an exception.

As covered in a recent survey by HJ Forman and H Zhang (Targeting oxidative stress in disease: promise and limitations of antioxidant therapy. Henry Jay Forman & Hongqiao Zhang), it is essentially impossible to definitively prove direct scavenging of ROS in vivo.  Thus, the reviewer points out that it is questionable to claim that melatonin is a direct radical scavenger in living systems. Proof of direct scavenging has not even been achieved for classic antioxidants such as vitamin C which have a much longer investigative history than melatonin. The best evidence for scavenging in vivo seems to be the footprint molecules that are identified, e.g., in the case of vitamin C, dehydroascorbic acid.  The footprint molecules for melatonin are cyclic 3-hydroxy melatonin, AK and AMFK.  But even this may not be absolute proof of scavenging. Melatonin is not an exception. With this in mind, we have changed phrases in the text to make the conclusion that melatonin is a direct scavenger in vivo less definitive.

Furthermore, these authors ‘individuals’ do not claim that melatonin actions are all melatonin receptors mediated. In fact, they claim that melatonin, as a proven antioxidant is an inducer of the enzymatic defenses against oxidation. It is my understanding that they also wrote a review on the subject (“Does Biochemical Life Exist for a Receptor Agonist Outside Its Receptor? The Case of Melatonin”).

The authors could not find the article identified.  We certainly do not disagree that melatonin, very likely via receptor mechanisms, upregulates antioxidant enzyme activities and glutathione synthesis.  Those actions are not the subject of the review.  We did add a statement at the end of the first paragraph of the Conclusions to cover this point.

These authors also claimed that melatonin inductive capacities, although perfectly demonstrated in living systems, are due to a potential binding of it with a potential NUCLEAR factor (receptor) that has escaped the findings of dozens of laboratories these 3 to 4 last decades.

We are not sure to who the reviewer is referring when he/she mentions “these authors” in the above sentence.  Certainly, melatonin has an orphan nuclear receptor, but we do not know the data that stimulating the nuclear receptor upregulates melatonin synthesis.  Perhaps we are misreading the statement made by the reviewer.  If he/she would be willing to identify the associated publications, the authors would be pleased to discuss them.

What these authors also wrote is that at the concentrations used in all the preclinical models and in most of the animal models, the melatonin receptors are desensitize. Which means that they are NOT active. A general feature of all GPCRs.

We do not disagree with this statement.

1/ This said, the review surveys the evidence that mitochondria are full of melatonin. Unfortunately, these claims are for the most part indirect. We are still waiting for experiments demonstrating that pure mitochondria contains melatonin. The Authors claim that because the Suofu paper (ref 57) shows the presence of AANAT in mitochondria, it means that mitochondria is full of melatonin. But the presence of melatonin in the same mitochondria is not reported in this publication. Furthermore, the presence of MT receptors in mitochondria preparation is weakened by the fact that the preparation of brain mitochondria were not claimed to be pure, and that mitochondria from brain are extremely difficult to obtain free of brain membrane contaminant – that could contain… MT receptors.

We cannot comment on the statement that neural mitochondria are difficult to isolate in pure form. Suofu et al showed the presence of both AANAT and ASMT, the two enzymes required for the conversion of serotonin to melatonin, as well as the chaperone 14-3-3, in non-synaptosome neural mitochondria. They also showed the isolated mitochondria converted deuterated serotonin  to deuterated melatonin (Fig 1H) They were also convinced that their mitochondrial preparations were pure since there was an absence of actin, E-cadherin, calreticulin, syntaxin-6, and Rab1 (which ae located in other subcellular compartments) while the mitochondrial marker cytochrome c oxidase subunit IV was abundant in their preparation. (see Fig. 1A in their report). They also reported that the isolated mitochondria produce deuterated melatonin when they were incubated with deuterated serotonin (Fig 1H). This group also reported that knocking out AANAT led to damage of the mitochondria melatonin (Fig 1 D-E).  A later study by the same group reported that AANAT knock out negatively impacted mitochondrial physiology with the effects being reversed by exogenous melatonin (Jauhari A, Baranov SV, Suofu Y, Kim J, Singh T, Yablonska S, Li F, Wang X, Oberly P, Minnigh MB, Poloyac SM, Carlisle DL, Friedlander RM. Melatonin inhibits cytosolic mitochondrial DNA-induced neuroinflammatory signaling in accelerated aging and neurodegeneration.J Clin Invest. 2020 Jun 1;130(6):3124-3136. doi: 10.1172/JCI135026).

2/ Prof Reiter’s group hypothesized, in 1993 that melatonin travels freely through biological membranes. This was proven very elegantly by Yu et al, in 2014. This particular paper pointed out that the free traveling through the membranes concerns ALL the biological membranes. And thus, that no subcellular compartment(s) could retain/trap melatonin within them.

This is likely correct. We feel however, that melatonin is synthesized in mitochondria, perhaps induced by elevated oxidative stress, which means it may be in position when an excess of free radicals occurs. Suofu et al. also showed that melatonin from mitochondria is released from these organs, and we have also suggested this and proposed it may even have autocrine and paracrine actions when it escapes from the cell. Thus, we agree that melatonin moves throughout the cell.

3/ According to the previous point, melatonin cannot stay in mitochondria. The Authors should experimentally show, as a start, that melatonin is indeed trapped in pure mitochondria prepared from an abundant tissue (like muscles).

We agree that melatonin is not trapped in the mitochondria.  When it is synthesized in this organelle, possibly in response to locally generated free radicals, it is initially in greatest concentrations in mitochondria but with time it diffuses throughout the cell

4/ For the scavenging capacity of melatonin, the Authors show a very nice figure of the “catabolism” of melatonin by ROS. This picture lacks 2 things: 1/ AFMK leads indeed to AMK by losing formic acid, an extremely toxic compound. This means that toxicity of ROS via melatonin would lead at least in part to acidosis in the mitochondria. And 2/ the quantity notion should be call in again. How much melatonin would be required to scavenge the continuous mitochondria production of ROS? According to the figure of lines 272, melatonin is able to scavenge ROS at a rate of 1.3 X 10¹⁰ M^-1s^-1. It would be helpful to the general reader to transform this constant in actual numbers. Why? Because, if the concentration of melatonin is so important in mitochondria, melatonin should be seen constantly in the cell (Melatonin travels freely though biological membranes). Now, if the amount of melatonin to counteract the ROS production is constant, it means that the source of serotonin in mitochondria should be quite gigantic as well. Furthermore, as known by The Authors, serotonin does not travel freely though the membranes. On the other hand, the compounds issued from the attacks of ROS onto melatonin should either accumulate in mitochondria - if they do not travel though the membranes – or be excreted from the mitochondria into the cells. I don’t think either of these hypotheses have been experimentally seen.

We very much appreciate this information and are in essential agreement.  Regarding the availability of serotonin as a precursor, low serotonin levels have not heretofore been shown to rate limit melatonin synthesis even in the pineal gland of young animals at night when melatonin production is highly elevated.  It has been shown that a dramatic decrease in pineal melatonin synthesis in aged rats may relate to a deficiency of serotonin (Stokkan KA, Reiter RJ, Nonaka KO, Lerchl A, Yu BP, Vaughan MK. Food restriction retards aging of the pineal gland.Brain Res. 1991 Apr 5;545(1-2):66-72. doi: 10.1016/0006-8993(91)91270-b). However, this has not been examined in mitochondria of peripheral cells.

Of course, if the review is a global hypothesis, the title should clearly translate this fact, and researchers could start to experimentally address these questions.  of serotonin

Thanks for this comment.  We are very hopeful, as we always are, that the report will entice others to check melatonin in their experimental models, be they antioxidant of some other functions.  New imaginative investigators are important to the field.  That field is growing rapidly. e.g., plant biologists are heavily involved in melatonin’s role as an antioxidant and its many other functions.

5/ Concerning the expression of ANNAT in mitochondria, I have a bad time trying to find genetic evidence that mitoDNA encodes for AANAT, and as pointed out by the Individuals of references 7-10, and that this putative gene would be completely differently regulated than the pineal one. That is active at night, inactive during the day.

AANAT is not encoded in the mitochondria; this is done in the nucleus. Pineal AANAT is a result of NE stimulation of the pinealocyte.  Mitochondrial melatonin in somatic cells is not under the influence of the sympathetic nervous system.

6/ As a last point, the innocuity of melatonin is still debated. I am very surprised that concerned Scientists working in Health area can claim that 1 gram (!!) of melatonin for 30 days is safe!!! (line 994 Melatonin has been given at a dose of 1,000 mg daily for 30 days with no evidence of toxicity [209]). In the meantime, the Authors cannot ignore publications on the possible link between melatonin and toddler sudden death, the link between cardiac problems and melatonin, and finally that some national agencies published warning on the use of over-the-counter melatonin (Australia, France, UK).

The paper related to administering 1,000 mg per day for a month with no side effects was published by Aaron Lerner, the individual who discovered melatonin.  Despite attempts to do so, no LD50 has been defined for melatonin. The most recent alleged cardiac problem was presented at the heart meeting in New Orleans.  It was an Abstract and even that was not peer-reviewed. The weakest aspect of this report is that the control subjects likely had a greater intake of melatonin than the so-called melatonin group. The author only considered patients who took melatonin as a prescription, which means they took 1 – 3 mg daily.  If they did not take prescription melatonin, they were placed in the control group and it was assumed they did not take melatonin.  However, in the US, many individuals take larger amounts of OTC melatonin daily, often up to 100 mg.  These individuals were all in the control group. So the results may have been in stark contrast to what the authors claimed.  This report and other such reports have similar flaws.  We have corresponded with the authors and they agree with this error; unfortunately, no steps have been taken to correct it. The sanctioned prescription dose of melatonin (1 – 3mg) in Australia, France and UK possibly relates to the pharmaceutical industry’s opposition to melatonin because of its high efficacy as well as its inexpensive and non-patentable nature. These same companies have developed analogues which are patentable and much more expensive. Most countries do not limit melatonin usage at higher doses.    

7/ The dose question remains also an open one. How much melatonin can circulate, how is the safety profile over the whole population, as well as for patients with severe health conditions (remember that melatonin is claimed to be effective as an adjuvant in most of the human diseases).

I read recently – in a paper by those Individuals (7-10) - that none of the 400 (ish) clinical trials implying melatonin treatment led to a clear effective conclusion. This should be also recalled along the recommendations of the present review (chapter 10:  “Conclusion: Final Thoughts Distilled”…) 

The problem with the failure of the clinical trials or only modest effects likely relates to the dosages used, usually 3 mg.  When it comes to other antioxidants, e.g., vitamin C, higher doses provided in grams are not uncommon (Linus Pauling suggested 4 grams for some cases).  Allometric calculation of human doses based on the outcomes of animal studies is 1.0 – 1.5 mg per kg body weight.  These are the doses we feel should be used in clinical trials.

Overall, I regret that the beliefs of Prof Reiter, that are fully respectable, could not be treated experimentally one by one, leading to a clear picture of the question: “Is there high concentrations of melatonin inside mitochondria? Where it come from? What is used to?

We know the mitochondrial melatonin in somatic cells does not come from the pineal gland; removal of the pineal gland in animals does not depress or change melatonin levels in the mitochondria of other cells.  Melatonin is an unusual molecule. In addition to its antioxidant actions, it is an anti-inflammatory molecule, anti-cancer agent, etc.  The reviewer could check PubMed to identify thousands of worthy publications on these and other subjects. 

I am amazed that this is the 1350^th paper by Prof Reiter [since 1969, and according to the count in PubMed (“REITER RJ + melatonin“)] and that those questions are still open.

Dr. Reiter has never had to defend his publication record in response to reviewer’s comments.  This is something new.  He has trained 148 postdocs, 32 Ph.D. students, has had countless visiting faculty train at his laboratory, and has collaborations throughout the world.   All these interactions have led to the publications referenced by the reviewer.  Regarding the comment about the “open question”, there are many molecules with a much longer investigative history where the mechanisms are not yet totally known. Such is the nature of science, as the reviewer is undoubtedly aware.