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Letter to the editor from Edna Grünblatt and Prof. Manfred Gerlach

Posted by PLOS_ONE_Group on 04 Sep 2012 at 11:01 GMT

We would like to press our concern in regard to a manuscript published recently in PLoS One Vol.7 issue 3 March 2012 “Methylphenidate exposure induces dopamine neuron loss and activation of microglia in the basal ganglia of mice” by Sadasivan et al.

The paper describes experimental studies looking for the chronic treatment effect of methylphenidate (MPH) in mice, in which the authors claimed to find that chronic MPH treatment causes degeneration of dopaminergic neurons in the substantia nigra and increase of activated microglia / inflammation. Such information, and claim is of great importance since, if these claims are correct, it might cause panic in many who treat children with attention-deficit hyperactivity disorder (ADHD) and other psychiatric disorders with MPH. Therefore, we wish to stress our concerns in regard to many facts and data that are not clearly reported in this manuscript, as well as points to the fact that they have interpreted the results in a very controversy way. We believe that such findings are very important, but in order to interpret them in a more objective perspective, we would appreciate if the authors could present all data, or add some experiments to make all aspects clear.

To be more concrete these are the details of the points we specifically think should be addressed. We tried to list them all in a form one would do if we would have been the reviewers of this manuscript before publication.
The first message coming from the title of the manuscript, which is “Methylphenidate exposure induces dopamine neuron loss and activation of microglia in the basal ganglia of mice”, is not accurate as the authors themselves present only 20% loss of TH-positive neurons with the highest dose of MPH treatment, which is actually in terms of dopaminergic loss usually have no consequence. In particularly, since the authors could not show any loss of dopamine in the striatum which would be more relevant. In addition, the authors did not conduct Nissl staining of the cells in order to analyze the loss of cells. It is well known that TH-staining of cells does not indicate necessarily for dopaminergic cell loss, as sometimes TH may just change in expression. Such knowledge was published in many publications using MPTP treatments. Therefore, such claim in the title is not accurate.

In the introduction, the authors claim that MPH was previously shown to produce superoxide in the brain: “In fact, both acute and chronic treatment with MPH has been shown to result in superoxide production in the brain (19, 20, 21, 22, 23).” Actually, only reference 21 mentions these findings, while the other references do not mention this fact. On the contrary, only the reference from Gomes (21), describes alteration in the superoxide levels due to MPH treatment, but only in acute treatment and not in the chronic treatment. Moreover, chronic treatment decreased the production of superoxides. Recently, Schmitz et al (Mol Cell Biochem. 2012 Feb;361 (1-2):281-8) described that chronic MPH treatment in rats actually decreased the oxidative stress parameters.

Coming to the methods description, there are many points missing or not clearly described, that makes it difficult for the reader to interpret correctly. First, it is not clear why the authors decided using three weeks old Swiss Webster mice for the experiments. For one, it is well known that different strains react differently to assaults, therefore it would be even better to compare the treatments with MPH in different strains, and second, postnatal day 28 correspond to around 2 years in human, which is an extremely early time point to start MPH treatment. As much as we know, MPH is never given to any child before the age of 6 years, and even further no “control” human takes MPH so early in life. Therefore, the authors should be aware that at such an early stage of life there is great brain developmental effects in comparison to later time points in life. Also the end point after the 12 weeks treatment the mice were corresponding to a human 9 year old person, which is again rather young.

In regard to the choice of MPH doses, the 1mg/kg and 10mg/kg are rather still very high in correspondence to clinical treatments that use usually maximum of 30 mg per ca. 30-40 kg child weight (which would be max. 1-0.75 mg/kg MPH; and usually even lower). Therefore, again here the interpretation of the results should be careful.
One more point associated with MPH delivery. The authors delivered MPH i.p. to the mice, which points to several differences in delivery and pharmacokinetics of MPH in humans. First, the delivery in humans is orally, which is than metabolised and therefore plasma levels are not as high as it would be when MPH would be delivered systemic. Second, it is well known that the metabolic capacity of rodents is different than in humans. Since the authors administered MPH systemically, it would be assumed that the plasma levels of MPH has been much higher (also at the lower doses) as the ones known to have therapeutic range in humans. Therefore it would have been very much helpful if the authors have measured the plasma levels of MPH after MPH administrations.

The method described for measuring microglia and activated microglia should have used a non-bias method, such as double labelling and automatic counting via computer software. The authors used only one antibody Iba-1 (which by the way is not demonstrated in the results of at least in a supplementary data). Usually, GFAP should be used as well as an additional cross test for glial cell detection, than it would have been expected to use antibody for resting microglia, and a double staining for the activated microglia. See, also the publications: Berg et al. J Neural Transm (2010) 117:1287–1292; and Halliday et al. Movement Disorders, Vol. 26, No. 1, 2011.

The method describing the MPTP treatment is not stated clearly enough for the reader, and only after searching for information (we found it at the end in one of the figures), the reader can find out at what time point MPTP was given to the animals. It would be helpful, when the authors will indicate exactly when MPH was given- before or after MPTP? And is there a control treatment with MPTP alone without MPH to compare with the combination of MPTP and MPH?

The authors did not mention at all the neurotransmitter measurement method used. We assume they were using HPLC methodology. But, still it should be described and indicated how many samples per group were used for the analysis. In addition, it is a bit questionable why the authors measured only dopamine and DOPAC and not HVA which is also a metabolite of dopamine. It is actually important since the dopamine metabolism rate is calculated as DOPAC+HVA/ dopamine, and not just DOPAC/dopamine.

In regard to the microarray analysis it is not clear from the method description how many arrays were used for the analysis. Is it 3 per study, or less, and whether the RNA used for the analysis was pooled for the microarray or each animal SN sample was hybridized to one array? As much as we understood, the authors actually had only 3 animals per group for the expression analysis. This might be understandable since the microarray analysis is not that cheap, and probably because of budget reasons the authors used such a small sample size (which of course has very low power), but it should be specifically indicated that the authors are aware that it is definitely not statistically powerful enough for any conclusions. Actually, we would have expected that at least the confirmatory analysis that was used doing quantitative real-time RT-PCR (qPCR) would have used many more animals per group in order to reach statistical power. But as it seems the authors did not do this.

Regarding the use of the two reference genes ribosomal 18S and beta-actin, it is not described how the authors used these two genes for the normalization. Did they use the Genorm method or other? Also it should be pointed out that it is well known nowadays that these two reference genes are usually very unstable and therefore, one should have used many more, and other, reference genes to normalize the results.

The authors did some confirmation analysis of genes found to alter their expression on the microarray analysis, but on the other hand they chose 4 genes (IL-6, IL-1beta, TNF-alpha and Cox-2) that did not alter their expression at all on the microarray analysis. How do they comment on this fact?

Now, in general, in the methods, it is very hard to understand the number of animals used for each experiment and whether there is a reason why 1) not for all groups analysis was conducted for all parameters and 2) not all results are reported later (at least in the supplementary data).

Now, commenting to the results of the study. Since the authors present the dopaminergic neuron counts for control, MPTP alone, 1mg/kg MPH, 1mg/kg MPH+MPTP, 10mg/kg MPH and 10 mg/kg MPH+MPTP we would have expected that they will present the same data for the resting microglia and activated microglia in figure 2 as well as the ratio of activated / resting microglia, so that all data will be transparent. Unfortunately this was not done.

In the results, the authors reason “Since the cellular changes, both in SNpc dopaminergic neuron number and microglia, were observed primarily at the 10mg/kg MPH dose, we used qPCR to further examine and validate the expression of genes in animals exposed to only this dose”. It should be stressed that this is not a very convincing reason not to look at the other doses as well as the different treatment patterns (chronic vs. acute and with and without MPTP and the dose 1 and 10 mg/kg).

The reader actually would expect to have a look at these as well, especially when the authors later suggest that MPH treatment affects dopaminergic neurons and cause neurodegeneration. It is very important to look at all groups, and not only in 3 animals per group, but rather again at least 10 per group.

In a similar way, as mentioned above, the reader would have expected the authors to present in figure 3 all effects of MPH treatments, in all the different combinations as well as the effect of MPTP alone. This is, unfortunately not the case. This continues in the figures 4 and 5 that present the qPCR results, that should have been done for all the different groups as well as for more than 3 animals.

Coming to the discussion part, when we refer to all comments above, actually the discussion has to be adjusted to all bias and new data. Specifically, authors have to refer to the fact that they studied only one animal strain that might behave differently than other strains. Then also comment to the fact that they chose very early stages to treat animals with MPH, and not start at a corresponding age of 6 years old children and may be also look at lower dose of MPH that correspond more realistic to treatment in children. As well as, discuss the fact that MPH was administered systemically and not as in humans orally.

In the paragraph starting with “MPH´s mechanism of action is to increase the availability of....” the authors’ present data that were not mentioned in the results and claim that when they compared the ratio of striatal dopamine to SNpc dopaminergic neurons it was significantly altered. But, 1) no results are presented, and 2) the statistic is not presented. In general, it is very confusing when suddenly striatum comes in play when all results were regarded to SN. It would be rather important, if authors wish to present both SN and striatum results, than they should present for these two brain regions, ALL results of neurotransmitter, gene expression, etc. And not each time only part of the results.

Finally, in the discussion the authors claim that epidemiological study with amphetamine point to the fact of it to cause risk for Parkinson´s disease (PD). This might be correct, although there are no conclusive results in the literature. But it should be mentioned that amphetamine, not like MPH, not only inhibit the dopamine transporter but also cause dopamine release from the vesicles which in regard to MPH is known not to be the case. In addition, in regard to MPH, there are reports actually of MPH having protective effects in PD and show beneficial treatment effects (Fleming et al. (Behavioural Brain Research 156 (2005) 201-213). In addition, no association between PD and exposure to MPH or ADHD in childhood were found to exist in PD patients (Walitza et al. J Neural Transm Suppl. 2007; (72):311-5.).

In addition, Levi et al. (Neurotoxicology and Teratology 34(2012) 253-262), describe toxicity study comparing MPH with amphetamine and methamphetamine induced hyperthermia and neurotoxicity in male rats during waking time period. In this study, even the very high doses of MPH 4x 22mg/kg did not cause lethal hyperthermia or neurotoxicity as the other two did. Therefore, it could be concluded that the effects caused by MPH cannot be compared to the two drugs as actually done in the current manuscript.

We would very much appreciate it, when the authors could respond to these points, and hopefully could also present all results coming from this very interesting study, and discuss the results more critically.
We thank you in advance for your attention, and hope to hear from you soon.

Sincerely yours

PD Dr. Edna Grünblatt
Child and Adolescent Psychiatry,
University of Zurich,
Thurgauerstr. 39
8050 Zurich, Switzerland

Prof. Dr. Manfred Gerlach
Department of Child and Adolescent Psychiatry and Psychotherapy, University of Würzburg,
Füchsleinstr. 15
97080 Würzburg, Germany

Competing interests declared: PLOS ONE Staff

RE: Letter to the editor from Edna Grünblatt and Prof. Manfred Gerlach

rsmeyne replied to PLOS_ONE_Group on 05 Sep 2012 at 22:05 GMT

One of the advantages of publishing in PLoS One is the ability for other scientists to comment on papers, as well as providing the authors a chance to respond. As such, the authors of this paper would like to respond to the comments of Drs. Grunblatt and Gerlach, regarding our paper entitled “Methylphenidate exposure induces dopamine neuron loss and activation of microglia in the basal ganglia of mice”. Since the comments from Drs. Grunblatt and Gerlach were made in the form of a reviewer’s comments, we are responding in a similar vein; where we will highlight and address individual points. Although our responses to these comments are provided at some length (and are in bold), the authors feel the need to fully address each of these comments.

Comment 1: We would like to press our concern in regard to a manuscript published recently in PLoS One Vol.7 issue 3 March 2012 “Methylphenidate exposure induces dopamine neuron loss and activation of microglia in the basal ganglia of mice” by Sadasivan et al.The paper describes experimental studies looking for the chronic treatment effect of methylphenidate (MPH) in mice, in which the authors claimed to find that chronic MPH causes degeneration of dopaminergic neurons in the substantia nigra and increase of activated microglia / inflammation. Such information, and claim is of great importance since, if these claims are correct, it might cause panic in many who treat children with attention-deficit hyperactivity disorder (ADHD) and other psychiatric disorders with Ritalin (MPH). Therefore, we wish to stress our concerns in regard to many facts and data that are not clearly reported in this manuscript, as well as points to the fact that they have interpreted the results in a very controversy way. We believe that such findings are very important, but in order to interpret them in a more objective perspective, we would appreciate if the authors could present all data, or add some experiments to make all aspects clear.

Response 1: As Drs. Gerlach and Grunblatt point out, we agree that this work has the potential to show that use of methylphenidate, in normal brains, may have unanticipated effects, including a small but significant loss of substantia nigra dopaminergic neurons. We are very clear and circumspect that these studies were done in mice and only looked at normal brains. We are overly careful to say that implications in regard to ADHD cannot necessarily be made since there is no experimental model that totally recapitulates the disorder.

To highlight his concept, we say in the final paragraph of our discussion “Taken together, our results suggest that chronic administration of methylphenidate in mice, at doses that approximate those at the higher therapeutic range in humans, results in a reduced expression of neurotrophic factors, increased neuroinflammation, and a small, but significant loss of SNpc dopamine neurons. These results can only be interpreted in the context of normal brain structure and function, and thus would have direct implications for the illicit/neurocognitive use of MPH.”

Comment 2: The first message coming from the title of the manuscript, which is “Methylphenidate exposure induces dopamine neuron loss and activation of microglia in the basal ganglia of mice”, is not accurate as the authors themselves present only 20% loss of TH-positive neurons with the highest dose of MPH treatment, which is actually in terms of dopaminergic loss usually have no consequence. In particularly, since the authors could not show any loss of dopamine in the striatum which would be more relevant. In addition, the authors did not conduct Nissl staining of the cells in order to analyze the loss of cells. It is well known that TH-staining of cells does not indicate necessarily for dopaminergic cell loss, as sometimes TH may just change in expression. Such knowledge was published in many publications using MPTP treatments. Therefore, such claim in the title is not accurate.

Response 2: The authors strongly disagree with this comment. Our title actually clearly and without bias accurately states what is in the paper. We report a small, but statistically significant (20%) loss of SNpc DA neurons (see later comments regarding methods of stereology). The authors of the letter are correct that we did not find a loss of striatal dopamine, but this in no way makes the loss of SNpc DA neurons any less significant. In terms of Drs. Gerlach and Grunblatt’s comments that this is of no significance, we disagree. Although this small loss did not affect striatal dopamine, our findings show that in mice, after 90 days of MPH, the SNpc is left with only 80% of its normal number of DA neurons. This small loss, in and of itself, may not have direct implications for the health of the animal; however, it is well known that a number of movement disorders, including Parkinson’s disease, can occur when one loses approximately 70% of their SNpc DA neurons. If MPH reduces the number of SNpc DA neurons by 20%, it could be suggested that there is a lesser “buffer” of these neurons, making the SNpc more vulnerable to further insults.

In terms of the methodology, Drs. Gerlach and Grunblatt state “the authors did not conduct Nissl staining of the cells in order to analyze the loss of cells. It is well known that TH-staining of cells does not indicate necessarily for dopaminergic cell loss, as sometimes TH may just change in expression. Such knowledge was published in many publications using MPTP treatments.”. As experts in quantitative assessment of SNpc DA neurons, which our lab has been conducting for 16 years (see also Baquet ZC, Williams D, Brody J, Smeyne RJ (2009) A comparison of model-based (2D) and design-based (3D) stereological methods for estimating cell number in the substantia nigra pars compacta (SNpc) of the C57BL/6J Mouse. Neuroscience 161: 1082-1090), we are aware of the potential for any number of exogenous compounds to reduce the levels of the surrogate dopamine marker tyrosine hydroxylase (TH), without actual cell loss. For this reason, we always counterstain TH with Nissl markers and then count all DA cells. In fact, this fact was included in our paper, which was missed. In the paper we specifically state “Briefly, for neuronal counts, brains were blocked and serially-sectioned at 10µm from the rostral hippocampus to the cerebellar-midbrain junction. Serial sections were mounted 5 sections per slide onto polyionic slides. TH-positive neurons and TH-negative, Nissl-positive cells within the SNpc that had the characteristics of dopaminergic neurons were counted using a 40X objective (total magnification 400x)”.

Comment 3: In the introduction, the authors claim that MPH was previously shown to produce superoxide in the brain: “In fact, both acute and chronic treatment with MPH has been shown to result in superoxide production in the brain (19, 20, 21, 22, 23).” Actually, looking into the references cited only reference 21 mention these findings, while the other references are not mentioning this fact. On the contrary, only the reference from Gomes (21), describes alteration in the superoxide levels due to MPH treatment, but only in acute treatment and not in the chronic treatment. Moreover, chronic treatment decreased the production of superoxides. Recently, Schmitz et al (Mol Cell Biochem. 2012 Feb;361 (1-2):281-8) described that chronic MPH treatment in rats actually decreased the oxidative stress parameters.

Response 3: The authors are correct here. This is a mistake in the placement of the references, where references 19, 20, 22, and 23 should have been placed prior to this sentence, after the line “Additionally, excess dopamine has been shown to be toxic both in vitro and in vivo due to the production of superoxide, hydrogen peroxide, and the dopamine quinone [16,17,18]. We would be glad to place a note of this effect within the article. The reference for Gomes should stay where it is. As stated in the abstract from this paper, Gomes and colleagues state, “The results showed that the acute administration of MPH in all doses in young rats increased the production of superoxide in the cerebellum and only in the high dose (10mg/kg) in the hippocampus, while chronic treatment had no effect. However, acute treatment in adult rats had no effect on production of superoxide, but chronic treatment decreased the production of superoxide in the cerebellum at the lower doses. Our data suggest that the MPH treatment can influence on production of superoxide in some brain areas, but this effect depends on age of animals and treatment regime with MPH.” While we did misplace these references in the text, there are also a number of other published papers that show changes in oxidative stress in brain following exposure to MPH. These include:
1) Martins MR, Reinke A, Petronilho FC, Gomes KM, Dal-Pizzol F, Quevedo J. Methylphenidate treatment induces oxidative stress in young rat brain. Brain Res. 2006 Mar 17;1078(1):189-97.
2) Fagundes AO, Rezin GT, Zanette F, Grandi E, Assis LC, Dal-Pizzol F, Quevedo J, Streck EL. Chronic administration of methylphenidate activates mitochondrial respiratory chain in brain of young rats. Int J Dev Neurosci. 2007 Feb;25(1):47-51.
3) Fagundes AO, Scaini G, Santos PM, Sachet MU, Bernhardt NM, Rezin GT, Valvassori SS, Schuck PF, Quevedo J, Streck EL. Inhibition of mitochondrial respiratory chain in the brain of adult rats after acute and chronic administration of methylphenidate. Neurochem Res. 2010 Mar;35(3):405-11.

Drs. Gerlach and Grunblatt also bring to our attention a paper by Schmitz. In this paper, Schmitz et al state “Rats received intraperitoneal injections of MPH (2.0 mg/kg) once a day, from the 15th to the 45th day of age or an equivalent volume of 0.9% saline solution (controls). Two hours after the last injection, animals were euthanized, and blood was collected. Results demonstrated that MPH did not alter the dichlorofluorescein formed, decreased both thiobarbituric acid reactive substances and total non-enzymatic radical-trapping antioxidant, and increased superoxide dismutase and catalase activities, suggesting that this psychostimulant may alter antioxidant defenses”.

Unlike the previous paper, this study examined antioxidant changes in blood, while we only reference papers discussing changes in brain, since this is the focus of our study.

Comment 4: Coming to the methods description, there are many points missing or not clearly described that makes it difficult for the reader to interpret correctly. First, it is not clear why the authors decided using three weeks old Swiss Webster mice for the experiments. For one, it is well known that different strains react differently to assaults, therefore it would be even better to compare the treatments with MPH in different strains, and second, postnatal day 28 correspond to around 2 years in human, which is extremely early time point to start MPH treatment. As much as we know, MPH is never given to any child before the age of 6 years, and even further no “control” human takes MPH so early in life. Therefore, the authors should be aware that at such an early stage of life there is great brain developmental effects in comparison to later time points in life. Also the end point after the 12 weeks treatment the mice were corresponding to a human 9 year old person, which is again rather young.

Response 4: Drs. Gerlach and Grunblatt make several points that we will address. First, they want to know why we use Swiss-Webster animals. A Pubmed search of papers from our lab shows our long standing interest and appreciation for strain differences in response to exogenous compounds. This includes the 2 papers cited:

1. Hamre K, Tharp R, Poon K, Xiong X, Smeyne, RJ. Differential strain susceptibility following 1-methyl-4-phenyl-1,2,3,6-tetrahydropyridine (MPTP) administration acts in an autosomal dominant fashion: quantitative analysis in seven strains of Mus musculus. Brain Res 1999. 828:91-103. PMID: 10320728
2. Boyd JD, Jang H, Shepherd KR, Faherty C, Slack S, Jiao Y, Smeyne RJ. Response to 1-methyl-4-phenyl-1,2,3,6-tetrahydropyridine (MPTP) differs in mouse strains and reveals a divergence in JNK signaling and COX-2 induction prior to loss of neurons in the substantia nigra pars compacta. Brain Res. 2007. 1175:107-16. PMID: 17884023

But see also:

3. Smeyne RJ and Jackson-Lewis V. The MPTP model of Parkinson’s disease. Mol Brain Res 2005. 134: 57-66. PMID: 15790530
4. Cook R, Lu L, Gu J, Williams RW, Smeyne RJ. Identification of a single QTL, Mptp1, for susceptibility to MPTP-induced substantia nigra pars compacta neuron loss in mice. Mol Brain Res 2003. 110:279-288. PMID: 12591164
5. Smeyne M, Jiao Y, Shepherd KR and Smeyne RJ. Glia cell number modulates sensitivity to MPTP in mice. Glia 2005. 52:144-152. PMID: 15920722
6. Jiao, Y., Lu, L., Williams, RW, and Smeyne, RJ. Genetic dissection of strain dependent paraquat-induced neurodegeneration in the substantia nigra pars compacta. PLoS ONE. 2012. 7: e29447. PMID: 22291891

In the Results section, we state “In terms of SNpc dopaminergic neuron loss, we have previously shown that the Swiss-Webster strain is resistant to MPTP-induced neuron loss [28,29].”; this is the “raison d’etre” for use of this strain, since we were examining if MPH could alter sensitivity to MPTP. The resistance to MPTP in Swiss Mice is also highlighted again in the discussion, where we state “In this study, we administered an acute regimen of MPTP (4x20mg/kg), an agent that is known to induce oxidative stress [48,49,50], to MPTP-resistant Swiss-Webster mice [28] treated with a chronic regimen of 1 or 10 mg/kg MPH.”

In terms of the ages chosen for this study (PD 28-125), we state that this corresponds to a developmental period of periadolesence to young adult rodents. This information is taken from a paper by Susan Andersen (Andersen SL (2002) Changes in the second messenger cyclic AMP during development may underlie motoric symptoms in attention deficit/hyperactivity disorder (ADHD). Behav Brain Res 130: 197-201.; see Figure 1 in paper, page 198).

Additionally, a number of papers examining developmental milestones in mice use postnatal day 21-28 mice as a period of periadolescence. These include, but are not limited to:

1) Gramage, E., Del Olmo, N., Fole, A., Martín, Y. B. and Herradón, G. (2011), Periadolescent amphetamine treatment causes transient cognitive disruptions and long-term changes in hippocampal LTP depending on the endogenous expression of pleiotrophin. Addiction Biology. doi: 10.1111/j.1369-1600.2011.00362.x

2) Unterwald EM, Ivkovic S, Cuntapay M, Stroppolo A, Guinea B, Ehrlich ME. Prenatal exposure to cocaine decreases adenylyl cyclase activity in embryonic mouse striatum. Dev Brain Res. 2003 Dec 30;147(1-2):67-75.

Comment 5: Furthermore, it is not correct that MPH is never given to children under the age of 6 years old. Although MPH is not approved for use in children under age 6, preschool-aged children have been identified as a group in which psychostimulant use is increasing. We have included only a few of the many references indicating this here (Ghuman JK, Byreddy S, Ghuman HS. Methylphenidate transdermal system in preschool children with attention-deficit/hyperactivity disorder. J Child Adolesc Psychopharmacol. 2011 Oct;21(5):495-8); Murray DW. Treatment of preschoolers with attention-deficit/hyperactivity disorder. Curr Psychiatry Rep. 2010 Oct;12(5):374-81.); Elder, T.E The importance of relative standards in ADHD diagnoses: Evidence based on exact birth dates. J Health Econ. 2010 Sep;29(5):641-56.)

In regard to the choice of MPH doses, the 1mg/kg and 10mg/kg are rather still very high in correspondence to clinical treatments that use usually maximum of 30 mg per ca. 30-40 kg child weight (which would be max. 1-0.75 mg/kg MPH; and usually even lower). Therefore, again here the interpretation of the results should be careful.

One more point associated with MPH delivery. The authors delivered MPH i.p. to the mice, which points to several differences in delivery and pharmacokinetics of MPH in humans. First, the delivery in humans is orally, which is than metabolised and therefore plasma levels are not as high as it would be when MPH would be delivered systemic. Second, it is well known that the metabolic capacity of rodents is different than in humans. Since the authors administered MPH systemically, it would be assumed that the plasma levels of MPH has been much higher (also at the lower doses) as the ones known to have therapeutic range in humans. Therefore it would have been very much helpful if the authors have measured the plasma levels of MPH after MPH administrations.

Response 5: We agree that one has to be careful when comparing doses of drugs and their subsequent effects when going between species. However, this is a necessary fact when using animal models. In our study, we used ip administration of 1 and 10 mg/kg MPH, which we state reproduces the therapeutic window in humans (treatment of ADHD and recreational use/narcolepsy, respectively). A paper by Balcioglu et al., entitled “Plasma and brain concentrations of oral therapeutic doses of methylphenidate and their impact on brain monoamine content in mice. Neuropharmacology. 2009 Dec;57(7-8):687-93” shows that 0.75-2.0 mg/kg administered orally in mice provided “plasma levels of d-methylphenidate that are comparable to those seen in ADHD patients taking oral therapeutic doses of methylphenidate”. Although not included in this paper, we did perform a pharmacokinetic study examining the levels of MPH in brain after 1 and 10 mg/kg ip MPH which showed that our 1 mg/kg doses recapitulated brain levels of MPH similar to that reported by Bhide’s group, and that 10 mg/kg MPH ip showed a linear increase in availability of MPH. This 1-10X MPH dosing range for treatment of ADHD through narcolepsy is what we examined in this study.
A somewhat similar comment was raised during the review process, where a reviewer wrote: “The authors indicate that the doses of methylphenidate used are at the higher end of those typically used in humans. I disagree with this given the max dose of methylphenidate used in children is typically 60 mg per day (usually in the 20-30 mg/day range), and on a mg/kg basis, a 30 kg child would have received 300 mg/day with the 10 mg/kg dose. This should be changed in the manuscript.”; and our response was: “The reviewer is correct that a typical dose of MPH in children is approximately 60 mg, which in a 30kg child would be approximately 2 mg/kg. However, we were discussing not only dosing in children with ADHD but also other conditions that MPH is used, including narcolepsy. In the paper by “Leonard BE, McCartan D, White J, King DJ. Methylphenidate: a review of its neuropharmacological, neuropsychological and adverse clinical effects. Hum Psychopharmacol. 2004 Apr;19(3):151-80, it is stated “Effective treatment of somnolence in narcoleptics may require remarkably high doses of methylphenidate. To investigate suggestions that high doses of methylphenidate might induce methylphenidate psychosis or affect the development of depressive symptoms, Pawluk et al. (1995) identified a group of 11 narcoleptic patients (six men and five women) treated at a sleep disorder centre who had received doses of methylphenidate in excess of 100 mg/day for at least the preceding 5 years. They found that five of these met DSM-III-R criteria for dysthymia and one for major depression but that there was nothing to suggest that the depressive disorders were due to the high dose of stimulant, the chronic stressors associated with their narcolepsy or the narcolepsy itself. Only two of the patients had symptoms of methylphenidate-induced psychosis or an incipient psychotic process and it appeared that certain predisposing factors, such as pre-treatment paranoid ideation, a family history of psychosis, significant head injury, or previous excessive use of stimulants, may have been required to trigger the psychosis. Those narcoleptics on a high dose of methylphenidate over a prolonged period who were free of these predisposing factors did not appear to be at increased risk of psychosis. Thus, one of the patients who exhibited psychotic symptoms was on the highest daily dose of methylphenidate (480 mg), but another patient had been on 400 mg daily for a much longer period and showed no evidence of stimulant psychosis. Interestingly, in the context of the commonly expressed concern that chronic use of stimulants may promote the development of hypertension, only 2 of these 11 patients were hypertensive, with one of these reporting a history of hypertension dating prior to the initiation of stimulants. Only one was being treated with antihypertensive medication. “ This high dose was also used in a study of narcoleptics: Pawluk LK, Hurwitz TD, Schluter JL, Ullevig C, Mahowald MW. Psychiatric morbidity in narcoleptics on chronic high dose methylphenidate therapy. J Nerv Ment Dis. 1995 Jan;183(1):45-8.
In the text this is summarized in the Introduction as “ In this study, we investigate whether long-term administration of MPH in mice at two doses (1mg/kg and 10mg/kg) that reproduce the therapeutic window in humans (treatment of ADHD and recreational use/narcolepsy, respectively)[25,26,27] can induce changes in the basal ganglia.”
Additionally, there is evidence for differential metabolism of MPH among different species based on the pharmacokinetic profiles found in Wargin et al., (Pharmacokinetics of methylphenidate in man, rat and monkey. J Pharmacol Exp Ther. 1983 Aug;226(2):382-6) . In the study, they observe a substantial increase in the systemic clearance of MPH in rats when compared to humans. Thus, due to high clearance of MPH, a 10mg/kg MPH dose in rodents may be in the therapeutic range of humans. Also, papers by Valvassori et al (Sensitization and cross-sensitization after chronic treatment with methylphenidate in adolescent Wistar rats. Behav Pharmacol. 2007 May;18(3):205-12) and Gerasimov et al (Synergistic interactions between nicotine and cocaine or methylphenidate depend on the dose of dopamine transporter inhibitor. Synapse. 2000 Dec 15;38(4):432-7) recommend 1-5 mg/kg and 10mg/kg for therapeutic use and recreational MPH/narcolepsy use, respectively.
We have added the following text to the Methods, “Starting at postnatal day PD28, mice were administered intraperitoneal (i.p.) injections of saline, 1mg/kg, or 10mg/kg methylphenidate hydrochloride (MPH, Cat # M2892 Sigma-Aldrich), once daily, 1 hour prior to the initiation of the animal’s active phase (18:00 hrs). The doses of MPH used in this study were chosen based on previous studies in rodents suggesting that MPH doses of less than 5 mg/kg i.p. mirror those that are used in clinical practice [58], whereas recreational use of MPH or its use in the treatment of narcolepsy would be reflected by a dose of 10 mg/kg [59].”

Comment 6: The method for measuring microglia and activated microglia should have used a non-bias method, such as double labeling and automatic counting via computer software. The authors used only one antibody Iba-1 (which by the way is not demonstrated in the results or at least in a supplementary data). Usually, GFAP should be used as well as an additional cross test for glial cell detection, than 3, it would have been expected to use antibody for resting microglia, and a double staining for the activated microglia. See, also the publications: Berg et al. J Neural Transm (2010) 117:1287–1292; and Halliday et al. Movement Disorders, Vol. 26, No. 1, 2011.

Response 6: Dr. Gerlach and Grunblatt state that microglia should be counted using non-biased methods. We agree, and in fact, that is what was done. As noted in the Methods, “Microglia were counted using the optical fractionator method [65] using Microbrightfield StereoInvestigator (MBF Biosciences, Williston, VT)… Based on cell size of the counting particle in 12 micron (empirically measured) sections, we used a high NA lens and a total magnification of 1000x in which we were able to clearly define approximately 18 focal planes within our section (1 focal plane equals approximately 0.54 mm).

In terms of using only 1ba-1, this antibody recognizes the 17-kDa EF hand protein that is specifically expressed in macrophages/microglia. This antibody recognizes both resting and activated microglia that can be distinguished by morphology. We discuss our methods for differentiating these two states in the Methods where we write, “Both Iba-1 resting and activated microglia were counted [66]. Stringent measures were adopted to classify Iba-1 positive microglia as resting or activated based on morphology based on the detailed description by Graeber and Streit [67]. Microglial cells would be deemed as resting if they contained a small oval Iba-1-positive cell body that averaged 3 microns in diameter with long slender processes. Microglia would be classified as activated when the cell body was slightly increased in size compared to resting microglia and had an irregular shape. The processes on the microglia were shorter and had thickened processes. The appearance of activated versus resting microglia is highlighted in Figure 1C,F,I.”

It is also suggested that we examine GFAP expression as a measure of microglia. GFAP recognizes a subpopulation of reactive astroglia, but does not recognize microglia (Esiri MM, McGee JO. Monoclonal antibody to macrophages (EMB/11) labels macrophages and microglial cells in human brain. J Clin Pathol. 1986 Jun;39(6):615-21; Baudry M, Yao Y, Simmons D, Liu J, Bi X. Postnatal development of inflammation in a murine model of Niemann-Pick type C disease: immunohistochemical observations of microglia and astroglia. Exp Neurol. 2003 Dec;184(2):887-903.);. Additionally, the data sheets for the antibody we use from Wako (http://www.wako-chem.co.j...) shows the absolute non-overlap of iba-1 and GFAP.

Comment 7: The method describing the MPTP treatment is not described clearly enough for the reader, and only after searching for information (we found it at the end in one of the figures), the reader can find out at what time point MPTP was given to the animals. It would be helpful, when the authors will indicate exactly when MPH was given- before or after MPTP? And is there a control treatment with MPTP alone without MPH to compare with the combination of MPTP and MPH?

Response 7: The authors are correct that we did not include this information directly in the Methods section, although it is clearly written in the legend to Figure 1 where we state “Stereological estimates of dopamine neuron number in substantia nigra pars compacta (SNpc) in animals administered saline (ctrl), saline+MPTP (ctrl+MPTP), 1mg/kg MPH, 1mg/kg MPH + MPTP, 10mg/kg MPH and 10mg/kg MPH + MPTP. Saline, 1mg/kg MPH and 10mg/kg were administered for 90 days following a one-week drug washout period before 4x20mg/kg MPTP was injected (n=10).” As you can see here, we clearly state that MPH was administered prior to MPTP. In terms of whether we show MPTP with or without MPH, this is clearly provided in Figures 1J and Figure 2.

Comment 8:The authors did not mention at all the neurotransmitter measurement method used. We assume they were using HPLC methodology. But, still it should be described and indicated how many samples per group were used for the analysis. In addition, it is a bit questionable why the authors measured only Dopamine and DOPAC and not HVA which is also a metabolite of dopamine. It is actually important since the dopamine metabolism rate is calculated as DOPAC+HVA/ dopamine, and not just DOPAC/dopamine.

Response 8: Drs. Gerlach and Grunblatt are correct in that we inadvertently did not include our methods for HPLC analysis of dopamine and its metabolites. We would be glad to include this as an added note to the paper.

Bilateral striata were dissected from mice and then homogenized in chilled 0.3M perchloric acid and centrifuged at 10,000g for 15 minutes at 4°C. Dopamine (DA), and its metabolite 3,4-dihydroxyphenylacetic acid (DOPAC) were analyzed using reverse-phase ion pairing HPLC combined with electrochemical (EC) detection under isocratic elution conditions. The amount of DA and DOPAC were determined by injecting known concentrations of these compounds and extrapolating from a standard curve. Statistical differences were determined using a one-way ANOVA followed by Bonferonni post hoc tests.

In terms of how we define dopamine turnover, numerous methods have been used. The use of DOPAC/DA has been used in a number of papers, including: Matsuda S, Matsuzawa D, Ishii D, Tomizawa H, Sutoh C, Nakazawa K, Amano K, Sajiki J, Shimizu E. Effects of perinatal exposure to low dose of bisphenol A on anxiety like behavior and dopamine metabolites in brain. Prog Neuropsychopharmacol Biol Psychiatry. 2012 Jul 1. [Epub ahead of print]; Bueno-Nava A, Gonzalez-Pina R, Alfaro-Rodriguez A, Avila-Luna A, Arch-Tirado E, Alonso-Spilsbury M. The selective inhibition of the d(1) dopamine receptor results in an increase of metabolized dopamine in the rat striatum. Neurochem Res. 2012 Aug;37(8):1783-9. Epub 2012 May 10; Davidson C, Coomber B, Gibson CL, Young AM. Effect of pre-ischaemic conditioning on hypoxic depolarization of dopamine efflux in the rat caudate brain slice measured in real-time with fast cyclic voltammetry. Neurochem Int. 2011 Oct;59(5):714-21. Epub 2011 Jul 5.; Shen H, Luo Y, Yu SJ, Wang Y. Enhanced neurodegeneration after a high dose of methamphetamine in adenosine A3 receptor null mutant mice. Neuroscience. 2011 Oct 27;194:170-80. Epub 2011 Aug 10.
We do have the data for both DOPAC and HVA and could, if required, provide this data.

Comment 9: In regard to the microarray analysis it is not clear from the method description how many arrays were used for the analysis. Is it 3 per study? or less? and whether the RNA used for the analysis was pooled for the microarray or each animal SN sample was hybridized to one array? As much as we understood, the authors actually had only 3 animals per group for the expression analysis. This might be understandable for the microarray analysis study which is not that cheap, and probably because of budget reasons the authors used such a small sample size (which of course has very low power), but it should be specifically indicated that the authors are aware that it is definitely not statistically enough for any results. Due to the small “n”, we do not make a big deal of all of the gene changes; however those that piqued our interest we did use qPCR for confirmation. Actually, we would have expected that at least the confirmatory analysis that was used doing quantitative real-time RT-PCR (qPCR) would have used many more animals per group in order to reach statistical power. But as it seems the authors did not do this.


Response 9: Drs. Gerlach and Grunblatt are correct that the “n” for each experiment is not in the Methods sections, although it is clearly stated in the legend to Figure 4, where we write “(A) Heat map representation of gene expression changes following chronic administration of either 1mg/kg MPH or 10mg/kg MPH in the SN (n=3)”. Although not specifically stated, we feel it is clear that the “n” represents individual animals rather than pooled data. In terms of statistics, we used an FDR-corrected p-value of 0.01(q value of ≤0.05) to identify genes that were changed. As required by PLoS One, all data are MIAME compliant, and the raw data were deposited in a MIAME compliant database (GEOID: GSE33619). A separate cohort of 3 mice was used to confirm the mRNA changes; but due to the small variability of our results, we were confident in calling something statistically different.


Comment 10: Regarding the use of the two reference genes ribosomal 18S and beta-actin, it is not described how the authors used these two genes for the normalization. Did they use the Genorm method or other? Also it should be pointed out that it is well known nowadays that these two reference genes are usually very unstable and therefore, one should have used many more, and other, reference genes to normalize the results.

Response 10: We did not use the Genorm method for comparisons using reference genes. Based on empirical experience on our lab, the 18S and b-actin are the least variable genes following treatment with MPTP, paraquat, and methylphenidate and have been a standard with the microarray papers in our lab.

Comment 11: The authors did some confirmation analysis of genes found to alter their expression on the microarray analysis, but on the other hand they chose 4 genes (IL-6, IL-1beta, TNF-alpha and Cox-2) that did not alter their expression at all on the microarray analysis. How do they comment on this fact?

Response 11: I am sure that Drs. Gerlach and Grunblatt recognize that microarray is only a semi-quantitative method, but helps to identify genes when looking at a large pool. Other methods, where one examines genes of interest, absent on the microarray but based on potential function (inflammation) are also valid. This is why, despite no changes in the microarray data, we examined these genes.

Comment 12: Now, in general, in the methods, it is very hard to understand the number of animals used for each experiment and whether there is a reason why 1) not for all groups analysis was conducted for all parameters and 2) not all results are reported later (at least in the supplementary data).

Response 12: We feel that the “n” of each experiment is clearly defined either in the Methods section or in the Figure legend.

Comment 13: Now, commenting to the results of the study. Since the authors present the dopaminergic neuron counts for control, MPTP alone, 1mg/kg MPH, 1mg/kg MPH+MPTP, 10mg/kg MPH and 10 mg/kg MPH+MPTP we would have expected that they will present the same data for the resting microglia and activated microglia in figure 2 as well as the ratio of activated / resting microglia, so that all data will be transparent. Unfortunately this was not done.

Response 13: The writers are correct that we did not include the 1 mg/kg MPH + MPTP microglia data. In terms of resting/activated microglia ratios, the necessary raw data is in the paper and can easily be extrapolated.

Comment 14: In the results, the authors reason “Since the cellular changes, both in SNpc DA neuron number and microglia, were observed primarily at the 10mg/kg MPH dose, we used qPCR to further examine and validate the expression of genes in animals exposed to only this dose”. It should be stressed that this is not a very convincing reason not to look at the other doses as well as the different treatment patterns (chronic vs. acute and with and without MPTP and the dose 1 and 10 mg/kg). The reader actually would expect to have a look at these as well, especially when the authors later suggest that MPH treatment affects dopaminergic neurons and cause neurodegeneration.

Response 14: Since we did not see any changes in microglia activation (as a marker for inflammation) at the low doses of MPH, we did not examine gene changes. We agree that this data would have added to the paper, but the tissue/RNA is no longer available to add this information. Additionally, this information was not requested during the review process.

Comment 15: Coming to the discussion part, when we refer to all comments above, actually the discussion has to be adjusted to all bias and new data. Specifically, authors have to refer to the fact that they studied only one animal strain that might behave differently than other strains. Then also comment to the fact that they chose very early stages to treat animals with MPH, and not start at a corresponding age of 6 years old children and may be also look at lower dose of MPH that correspond more realistic to treatment in children. As well as, discuss the fact that MPH was administered systemically and not as in humans orally.

Response 15: Most of these issues were addressed in response to previous comments. We do recognize, as would, I think, most readers that the results are specific for Swiss-Webster mice; although this strain is used in many studies. I do think that we are very circumspect in the Discussion on the implications of the paper, where we only discuss potential implications of chronic MPH use in normal brain as well as the fact that these studied are in mice.

Comment 16: In the paragraph starting with “MPH´s mechanism of action is to increase the availability of....” the authors’ present data that were not mentioned in the results and claim that when they compared the ratio of striatal dopamine to SNpc DA neurons it was significantly altered. But, 1) no results are presented, and 2) the statistic is not presented. In general, it is very confusing when suddenly striatum comes in play when all results were regarded to SN. It would be rather important, if authors wish to present both SN and striatum results, than they should present for these two brain regions, ALL results of neurotransmitter, gene expression, etc. And not each time only part of the results.

Response 16: The writers are correct that we do not present this data, although it can be extrapolated from the data presented. The point of this discussion was to show compensation of the dopamine produced in the SNpc and the neuron/dopamine ratio that has the potential to increase oxidative stress on the SNpc DA neurons. This is only a point of discussion and is not tested experimentally (thus its placement in the Discussion). Perhaps, we were too strong in saying we measured these differences when we only used extrapolated data from this study.

Comment 17: Finally, in the discussion the authors claim that epidemiological study with amphetamine point to the fact of it to be risk for Parkinson´s disease (PD). This might be correct, although there are no conclusive results in the literature. But it should be mentioned that amphetamine, not like MPH, not only inhibit the dopamine transporter but also cause dopamine release from the vesicles which in regard to MPH is known not to be the case. In addition, in regard to MPH, there are reports actually of MPH having protective effects in PD and show beneficial treatment effects (Fleming et al. (Behavioural Brain Research 156 (2005) 201-213). In addition, no association between PD and exposure to MPH or ADHD in childhood were found to exist in PD patients (Walitza et al. J Neural Transm Suppl. 2007; (72):311-5.). 5 In addition, Levi et al. (Neurotoxicology and Teratology 34(2012) 253-262), describe toxicity study comparing MPH with amphetamine and methamphetamine induced hyperthermia and neurotoxicity in male rats during waking time period. In this study, even the very high doses of MPH 4x 22mg/kg did not cause lethal hyperthermia or neurotoxicity as the other two did. Therefore, it could be concluded that the effects caused by MPH cannot be compared to the two drugs as actually done in the current manuscript.

Response 17: We are aware that the mechanism of action of the amphetamines versus that of methylphenidate is different, although both act to increase the availability of the monoamines in the synaptic cleft; thus, both drugs are psychostimulants used in the treatment of ADHD. However, the point of this is not to examine the increased risk for potential development of neurodegenerative disorders in persons with ADHD; but only point out the potential risk in those using these drugs for non-therapeutic purposes (recreation, cognitive enhancement). I think we are very clear that this data might or might not apply to persons/animals with known or unknown changes that are apparent in ADHD; and it would be very useful to reexamine these data if an appropriate model is developed. Nonetheless, given the very small number of studies that have been conducted, alterations at the cellular and anatomical levels from longer term use of this drug need to be in the literature, as noted by Drs. Gerlach and Grunblatt themselves.

We thank PLoS One and its editors for the opportunity to reply to these comments.

Respectfully,

Shankar Sadasivan, Ph.D.
Brooks Pond, Ph.D.
Amar Pani, Ph.D.
Chunxu Qu, Ph.D.
Yun Jiao, M.D.
Richard Smeyne, Ph.D.


No competing interests declared.