Peer review of: Labeled oxytocin administered via the intranasal route reaches the brain in rhesus (2020)

Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

The study of Lee and co-authors, addressing permeability of neuropeptide oxytocin to the brain tissue of 
monkeys, is very timely and important for translational application of OT in human.  Furthermore, the 
strength of the study is that it goes beyond oxytocin.  With the intravenous condition as a control, the 
authors obtained two very valuable findings:  1) intranasal d5OT delivery bypasses the  blood brain 
barrier; 2) intranasal drug delivery (at least of a small peptide, such as 9-aminoacid OT) holds promise 
for targeted drug delivery to specific brain sites that are in the trajectory of the olfactory and trigeminal 
nerves while limiting systemic exposure to the peptide.  

The authors used a unique approach applying d5OT to detect it in plasma, CSF and brain tissue. 

The work performed correctly, although the limited number of animals was employed. However, I have 
few concerns to discuss with the authors: 

1. I guess, there is an error in Figure 1:  there should be no label “INTRANASAL” in that figure. 

2. What t=0 means? If this is the time point before d5OT injection, it should be clearly stated. 

3. Would it be reasonable to add control group with saline injections? 

4. It is surprising that no CSF d5 OT was detected at 60 or 120 minutes in CSF after IN administration. 
How the authors interpret these results in comparison to previous author’s data and also work on 
human performed by Rene Hurlemann’s group? 

5. Why the authors did not measure OT in such important structures as the amygdala and insular? If you 
the authors did not measure OT or due to a detection, why these structures are listed it in the Table? 

In general, more clear explanations of experimental design and results will straighten the manuscript. 
Indeed, the more details in the text will be profitable for easier reading and understanding the 
importance of author’s findings. 

Reviewer #2 (Remarks to the Author): 

In this study, Lee et al administered intranasally as well as intravenously deuterated oxytocin (d5OT) to 
rhesus macaques and measured concentrations of exogenous and endogenous oxytocin (OT) in CSF, 
plasma, and most importantly 12 different brain regions. The authors reported that, after intranasal but 
not intravenous delivery, exogenous OT (d5OT) was found in a number of cortical and subcortical areas. 
In addition, intranasally delivered d5OT also persisted for a longer period of time in plasma. As the 

authors correctly pointed out, despite the large number of acute OT administration studies in humans, 
in laboratory as well as clinical trials, little is known about the actual biochemical and neuronal 
mechanisms through which OT alters primate behavior. We commend the authors for making a very 
strong effort to bridge this critical gap in the OT literature. Nevertheless, we feel quite strongly that the 
scientific findings are not presented in a clear and effective manner, which limits its appeal to the broad 
readership of Nature Communications. We make several suggestions to improve the clarity of the 
manuscript. 

Concerns with the clarity of the text: 

Line 71-73: “Notwithstanding this action, clear evidence of the location and extent of brain parenchyma 
penetrance of OT after intranasal (IN) or intravenous (IV) administration remains unclear.” 
--What “action”? And how can “clear evidence” be “unclear”? 

Line 93 misses a closing bracket. 

Line 93-95: “these regions were chosen as they are important in mediating social cognition in primate 
species and because they reflect regions associated with the mesolimbic social decision-making network 
in primate species.” 
--I am not sure what the authors meant by saying areas such as the cerebellum and brainstem 
contribute to “social cognition” in primates, especially since the only relevant literate cited here is 
“Prefrontal Cortex and Social Cognition in Mouse and Man” (Bicks et al. 2015). 

Line 98: “40 IU IN is the dose commonly used in human studies with OT.” 
--This is not entirely true. Single-dose human studies usually use 20-40IU of OT, and most OT studies in 
rhesus monkeys were within this range (for example, 25 IU in Chang et al. 2013, Ebitz et al. 2013, Jiang & 
Platt 2018, 24 IU in Modi et al. 2014, 48 IU in Dal Monte et al. 2014). By this standard, 40 IU and 
especially 80 IU are on the higher end in terms of dosage for macaques. More importantly, since 
macaques weigh much less than adult humans, the IU/kg dose is quite high in the aforementioned 
studies. These caveats need to be properly addressed (Freeman et al. 2016). 
Line 124-125: “This same device was used in similar previous nonhuman primate studies. Intranasal 
spray, anesthetized animals.” 
--Here the authors cited the same paper (Dal Monte et al. 2014) twice. Additionally, Dal Monte et al. 
2014 compared the effectiveness of intranasal spray and nebulization, but the authors failed to clarify 
that the method used in the current study was spray instead of nebulization. Furthermore, Dal Monte et 
al. reported that both delivery methods elevated OT level in CSF, while the changes in plasma OT were 
greater after nasal spray compared to nebulizer. Yet these findings (and other relevant studies such as 
Striepens et al. 2013, Modi et al. 2014) were never discussed. On a similar note, the CSF OT results 
presented here did not completely agree with the authors’ earlier paper (Lee et al. 2018), but this point 
was not sufficiently discussed either. 

Study design and results: 

My main concern is that too many statements seem redundant, self-contradictory, or simply call for 
further clarification. 

Line 314-316: “Concentrations of d5OT were quantified only after IN administration, not IV 
administration; the brain regions where these were quantified were OFC, striatum, thalamus, and 
brainstem.” 
--I think the authors meant they “analyzed” all 12 brain areas following both administration routes, but 
they only “identified”/“detected” d5OT in OFC, striatum, thalamus, and brainstem in the IN condition. 

Similarly, line 320-321: “D5OT in CSF was quantified only at time point 60…”. 
--I think the authors meant “detected” in this context, but please clarify. 

Line 321: “There was no d5OT detected in plasma or CSF at T=0, as expected.” 
--Why was plasma d5OT discussed at all under the subtitle “ CSF Concentrations of d5OT”? 

Line 330-348: This section of text on plasma concentrations of d5OT constantly jumped back and forth 
comparing different doses, routes and time points with a series of wilcoxon signed rank tests. It is very 
unclear which specific hypotheses were being tested here and therefore difficult to gauge whether more 
appropriate statistical methods exist. 

Line 347-348: “This difference indicates that IN delivery results in lower, but more sustained, plasma 
levels.” 
--The “lower” plasma OT concentration following IN delivery was not discussed in this section. 

Line 359-360: “Bivariate correlation between d0OT in the CSF and d5OT concentration in the plasma was 
not significant: Pearson correlation=0.07, p=0.655.” 
The authors need to justify why this Pearson correlation was run and why it was the only correlation 
reported, and conveyed by a single sentence not belonging to any paragraph. 

Line 448-450: “Decreasing concentrations, (~50%) over 2 hours, were observed in all 4 dose-route 
conditions, and this main effect of time does not support a feed forward effect of administered d5OT on 
endogenous levels.” 
--Why does this result not support a feed forward effect? Can the authors elaborate? 

Line 463-464: “Another limitation is the 2 hour interval between d5OT administration and necropsy.” 

And 

Line 467-472: “In addition, with the measurement of concomitant brain and CSF concentrations of d5OT, 
we can determine the extent to which IN administration results in brain concentrations of d5OT, in 
excess of that which crossed the blood brain barrier (i.e., IV route). This distinguishing feature is 
necessary, as the neurobehavioral effects of OT administered at peripheral sites, including IN, are most 

likely centrally mediated, with OT signaling in the brain required for the behavioral effect.” 
--These sentences seem to describe the strength of the current study but they lie within a paragraph 
dedicated to “limitations”. 

Finally, I think the authors need to defend the study design more forcefully. It is quite understandable 
that nonhuman primate studies, especially neuroanatomical ones, will be constrained by the number of 
animals available. Nevertheless, it important for researchers to define their hypotheses and complete 
the appropriate power analyses before conducting the experiment. For example, the authors 
acknowledged that, based on their prior study (Lee et al. 2018), they already knew some of the assay 
results could be “highly variable” across subjects (line 434). Despite this knowledge, they chose a mixed 
design with both males and females and 3 dose-route combinations, resulting in only two monkeys in 
each manipulation condition, and the only two male monkeys in the same condition (table 2). There are 
many potential problems with this design. First of all, the OT system is sexually dimorphic in a number of 
species (for example see Insel & Hulihan 1995; Dumais & Veenema 2016), and behavioral evidence 
suggests that male and female rhesus macaques respond to exogenous OT differently (Jiang & Platt 
2018 a,b). If there were a sex-specific effect present in the current study, it would have been obscured 
by the dose-route effect. 

More importantly, because of the large cross-subject variability (for example, in table 2, OT brain 
concentrations differed not only between the IN 40 and IN 80 conditions, but also frequently between 
the two subjects within the same condition), the current study is severely under-powered to uncover 
any cross-condition differences. 

As the current manuscript stands, it fails to capture the interest of general readers because the specific 
questions, hypotheses, and motivation for each statistical test, and the greater impact of each finding, 
remain obscure. I think the manuscript would benefit significantly from extensive restructuring and 
rewriting to highlight the most important findings and implications for the field. 

Reviewer #3 (Remarks to the Author): 

In this paper, the authors examine accumulation of a labeled (deuterated) oxytocin in the brain 
following intranasal administration. This is a really important paper for several reasons, only one of 
which is the finding of brain penetration of exogenous oxytocin (d5OT). It also shows endogenous OT 
(d0OT) in areas of the brain that I am not aware of having been examined before in this manner in a 
primate (for example, the cerebellum). 

There are a number of improvements which could be made in the paper, however, some substantive 
and some minor. 

1) There should be details of the brain findings in the text of the results section. These findings are also 

not discussed very thoroughly in the discussion and the authors don’t make much of the novelty of their 
findings. 
2) The tables are not very effective presentations of the data, and their legends are completely 
insufficient. I don’t know if brain, CSF, and plasma are squished together this way because of figure 
limitations of the journal? But it makes it hard to read. 
3) The figures also could be more attractive and use larger print for readers over 40! 
4) For the d5OT, it appears that in some cases the compound was detectable at 40 IU IN but not at 80 IU 
IN (for example, in the striatum). This seems counter-intuitive…shouldn’t a larger amount of d5OT show 
up in the same area in which a smaller amount could be detected? The authors should at least address 
what the reason for this might be. 
5) There are a number of recent papers that are not cited here but are relevant, especially the following 
which posits a mechanism for OT to cross the blood-brain barrier: 
https://www.ncbi.nlm.nih.gov/pubmed/30820471 

But also the following which shows OTR binding in humans some of the areas examined: 
https://www.ncbi.nlm.nih.gov/pubmed/30514927 

And, since the authors are talking about neural OT in non-human primates and humans (and this paper 
includes data on OT fibers in rhesus monkeys); 
https://www.ncbi.nlm.nih.gov/pubmed/29797339 

Another important recent study on this topic: 
https://www.ncbi.nlm.nih.gov/pubmed/31238093 

6) The sentence beginning in line 309 is non-grammatical. 
7) Line 261: should be baseline blood “samples” 

Reviewer #4 (Remarks to the Author): 

The work presents an important study on the administration of oxytocin via intranasal route (IN) versus 
IV in the rhesus monkey. As strong positives, the work is important, clinically relevant and is technically 
well performed. 

The author’s prior study weakens novelty. They have already demonstrated the approach, validated the 
use of this specific isotopic tracer and detection via LC/MS, and compared the effectiveness of IV and IN 
for CSF =. The current study builds and expands on the prior work as they looked at multiple (important) 
brain regions; not surprisingly, the peptide, once it reaches a brain region, lasts longer than in CSF. 

An issue that is mentioned but not well addressed involves reproducibility of peptide delivery. The 
authors describe the large variability in the IN application. While the IV variability was 25-30% relative 

variability, for IN, this increased to almost 100%. Given the lower variability in the IV, this does not 
appear to be a technical/measurement issue but an issue related to the mode of delivery. In such a case, 
when the peptide is applied by an expert, the amount delivered through IN does not appear to be well 
controlled. If the reviewer is understanding this, wouldn’t this issue impact the clinical ability to deliver a 
specific amount of drug? Can the authors describe ways to reduce the individual to individual variability 
of peptides?