Slc22a23 Proficiency Influences Rat Behavioral Responses After Lysophosphatidylcholine C20:4n6 Administration

Round 1

Reviewer 1 Report (Previous Reviewer 2)

Comments and Suggestions for Authors

I thank the authors for their detailed responses and the added experiments, in particular, the time-course metabolomics and the additional metrics for the MWM. The revisions to the figures have substantially improved their readability. I have some remaining concerns regarding the analysis and the conclusions drawn from that.

 

1. I have noted the BH correction for the mass spectrometry, the Dunnett's comparisons for the open field, and the nonparametric tests for the water maze. However, the NOR, SI and MWM treatment contrasts are still uncorrected t-tests run multiple times, e.g. across age and test day, with no correction. This inflates type 1 error rate substantially and it matters here because the effect sizes are marginal and may not support the conclusions drawn.

I would also note that the repeated-measures structure is only partly handled. Paired t-tests address two timepoints at a time and Dunnett's covers the open field, but the design as a whole is not modelled.

I suggest that the authors apply the appropriate correction across the behavioural tests or to temper the conclusions.

2. For the social interaction test, my concern remains that sequential presentation of the partner rats confounds social novelty with habituation and fatigue of the test animal, and is not a choice-based novelty preference. Genuine social recognition would be shown by a preference for the novel rat over the familiar rat presented simultaneously. As run, the test does not support the social novelty claim.
3. For the novel object recognition and object complexity, thank you for relabling the panels and the move to absolute time spent with the novel objects. However, this does not address the confounds that come about with differing complexity of the objects. I understand that it would be difficult to rerun the test, however the limitation with the object complexity should be stated as a caveat.
4. For the MWM and repeated testing, my concern remains. My original point, that the reversal curves at 13 weeks were faster than at 9 weeks, is itself the repeated-testing effect appearing in the data, and the authors' own admission of a ceiling effect from day 4 onward confirms that task difficulty degraded across exposures. The response to this comment did not change the text or add analysis.

Given that the treatment is given during the reversal phases, the acquisition phases can be used as a within-animal check for carryover effects. Hence, presenting and analysing the acquisition performance (training days) can gauge the size of the repeated-testing effect. Any finding of carryover effects should be addressed in the discussion.

Author Response

Response to Reviewer 2 Comments
1. Summary
Thank you very much for taking the time to review this manuscript. Please find the detailed responses below and the corresponding revisions in track changes in the re-submitted files.
2. Questions for General Evaluation	Reviewer’s Evaluation	Response and Revisions
Does the introduction provide sufficient background and include all relevant references?	Yes
Is the research design appropriate?	Can be improved
Are the methods adequately described?	Can be improved
Are the results clearly presented?	Can be improved
Are the conclusions supported by the results?	Can be improved
Are all figures and tables clear and well-presented?	Yes
3. Point-by-point response to Comments and Suggestions for Authors
Comments 1: I thank the authors for their detailed responses and the added experiments, in particular, the time-course metabolomics and the additional metrics for the MWM. The revisions to the figures have substantially improved their readability. I have some remaining concerns regarding the analysis and the conclusions drawn from that.   I have noted the BH correction for the mass spectrometry, the Dunnett's comparisons for the open field, and the nonparametric tests for the water maze. However, the NOR, SI and MWM treatment contrasts are still uncorrected t-tests run multiple times, e.g. across age and test day, with no correction. This inflates type 1 error rate substantially and it matters here because the effect sizes are marginal and may not support the conclusions drawn.   I would also note that the repeated-measures structure is only partly handled. Paired t-tests address two timepoints at a time and Dunnett's covers the open field, but the design as a whole is not modelled.   I suggest that the authors apply the appropriate correction across the behavioural tests or to temper the conclusions.   Response 1: Thank you very much for pointing this out. In this study, our primary aim was to determine whether LPC(20:4) administration have any effect within each genotype under each condition. Therefore, we performed t-test within each genotype for each condition.   We did not perform comparisons across genotype or other conditions (e.g. across age or test day). In our previous report (Uchimura et al., PLOS One 2024), we instead analyzed the effect of genotype (specifically WT vs. KO).   We have clarified this point in the revised manuscript at Line 339: “the present study focused on the differences between saline and lysophosphatidylcholine a C20:4n6 (LPC(20:4)) administration within each genotype. Specifically, we examined whether LPC(20:4) exerts an effect by comparing LPC(20:4) injection with saline injection in each genotype.”   Therefore, we used t-test for the statistical analysis.   For the social interaction test, my concern remains that sequential presentation of the partner rats confounds social novelty with habituation and fatigue of the test animal, and is not a choice-based novelty preference. Genuine social recognition would be shown by a preference for the novel rat over the familiar rat presented simultaneously. As run, the test does not support the social novelty claim.   Response 2: Thank you very much for pointing this out.   We did not claim that any social novelty was observed in our study. As stated in the manuscript starting at Line 2028: “However, no statistically significant difference was observed in our social novelty assay toward rat B (the novel rat) compared to rat A (the familiar rat) when rat B was presented 4 hours after rat A on day 3 (Figure 8C).”   To clarify this point further, we have revised the manuscript at Line 2030: “Social novelty might show differences when the familiar rat and the stranger rat were presented simultaneously [25].”   For the novel object recognition and object complexity, thank you for relabling the panels and the move to absolute time spent with the novel objects. However, this does not address the confounds that come about with differing complexity of the objects. I understand that it would be difficult to rerun the test, however the limitation with the object complexity should be stated as a caveat.   Response 3: Thank you very much for pointing this out. We added a sentence at Line 1773: “, and this is a potential caveat of this assay.”   For the MWM and repeated testing, my concern remains. My original point, that the reversal curves at 13 weeks were faster than at 9 weeks, is itself the repeated-testing effect appearing in the data, and the authors' own admission of a ceiling effect from day 4 onward confirms that task difficulty degraded across exposures. The response to this comment did not change the text or add analysis.   Given that the treatment is given during the reversal phases, the acquisition phases can be used as a within-animal check for carryover effects. Hence, presenting and analysing the acquisition performance (training days) can gauge the size of the repeated-testing effect. Any finding of carryover effects should be addressed in the discussion.   Response 4: Thank you very much for pointing this out. We conduced analysis of acquisition phase of the MWM tests and added Figure S1, S2 and S3.   We added a sentence at Line 3150: “Notably, in the acquisition phase of the MWM test at 8 weeks of age, randomly separated naïve rats exhibited significant differences. For example, trial 1 of the acquisition phase in Slc22a23+/+ rats differed significantly between naïve (C) and naïve (L) groups (Figure S1C). Significant differences were also observed in swim speed on day 1 (Figure S3AE). These results suggest the potential for false positives in the MWM analysis. Regarding the carryover effect of LPC(20:4) administration at 9 weeks of age, no significant differences were observed on day 1 of the acquisition phase at 12 weeks of age (Figure S1B, S2B, S3B), suggesting that the carryover effect from LPC(20:4) administration is likely to be minor. However, Slc22a23-/- rats in the acquisition phase at 12 weeks of age showed shorter latencies to the target in trials 2-4 on day 3 (Figure S1F) and faster swim speeds on days 2 and 5 (Figure S3BDF). Thus, carryover effects potentially may exist, particularly in Slc22a23-/- rats. Furthermore, this study was not conducted in a blinded manner and may therefore potentially contain sources of bias.”

 

 

Author Response File: Author Response.pdf

Reviewer 2 Report (Previous Reviewer 3)

Comments and Suggestions for Authors

The manuscript "pharmaceutics-4406881" by Yasuhiro Uchimura and co-authors has been substantially revised, additional experiments were made. Current version of the manuscript requires a correction of the corresponding paragraph in the Discussion, which is written rather awkwardly. There is still an option for an additional experiment, which could support currently proposed hypothesis, but I believe, the choice should be made by the authors, whose work and efforts are highly respected.

In my opinion, the research is planned and conducted very well. 

The requested details on statistics has been clarified upon resubmission.

The choice of animals' sex for the experiments has also been described.
Table 1 caption was clarified. 

Thus, here are the details on the remaining comment mentioned above:
 
The experiments on supplementation of LPC 20:4 and assessment of its blood plasma levels resulted in a rather surprising data (Fig. 4A). The result is only minimally discussed, with a hypothesis on urea excretion. However, the sentence "These findings suggest that Slc22a23 knockout may impair the reabsorption of LPC(20:4) from primary urine." requires a correction and probably more speculative remarks, because the proposed effect was not estimated. In other words, either supporting data on LPC 20:4 in urine should be clearly provided or other possible mechanisms which could lead to the absence of LPC 20:4 increase in blood just 30 minutes after its administration through the tail vein should be discussed with references to such mechanisms or similar examples.

Author Response

Response to Reviewer 1 Comments
1. Summary
Thank you very much for taking the time to review this manuscript. Please find the detailed responses below and the corresponding revisions in track changes in the re-submitted files.
2. Questions for General Evaluation	Reviewer’s Evaluation	Response and Revisions
Does the introduction provide sufficient background and include all relevant references?	Yes
Is the research design appropriate?	Yes
Are the methods adequately described?	Yes
Are the results clearly presented?	Yes
Are the conclusions supported by the results?	Must be improved
Are all figures and tables clear and well-presented?	Yes
3. Point-by-point response to Comments and Suggestions for Authors
Comments 1: The manuscript "pharmaceutics-4406881" by Yasuhiro Uchimura and co-authors has been substantially revised, additional experiments were made. Current version of the manuscript requires a correction of the corresponding paragraph in the Discussion, which is written rather awkwardly. There is still an option for an additional experiment, which could support currently proposed hypothesis, but I believe, the choice should be made by the authors, whose work and efforts are highly respected.   In my opinion, the research is planned and conducted very well. The requested details on statistics has been clarified upon resubmission. The choice of animals' sex for the experiments has also been described. Table 1 caption was clarified.   Thus, here are the details on the remaining comment mentioned above: The experiments on supplementation of LPC 20:4 and assessment of its blood plasma levels resulted in a rather surprising data (Fig. 4A). The result is only minimally discussed, with a hypothesis on urea excretion. However, the sentence "These findings suggest that Slc22a23 knockout may impair the reabsorption of LPC(20:4) from primary urine." requires a correction and probably more speculative remarks, because the proposed effect was not estimated. In other words, either supporting data on LPC 20:4 in urine should be clearly provided or other possible mechanisms which could lead to the absence of LPC 20:4 increase in blood just 30 minutes after its administration through the tail vein should be discussed with references to such mechanisms or similar examples.
Response 1: Thank you very much for pointing this out. We agree with this comment. Therefore, we have revised the paragraph starting from Line 2771 “Although plasma LPC(20:4) levels increased after tail-vein administration in WT rats, the levels in Slc22a23 knockout rats did not increase and were constantly and significantly lower (Figure 4A), which was unexpected. At least three possible molecular mechanisms could explain the lack of increase and the constantly low plasma LPC(20:4) levels after intravenous administration: (1) increased uptake of LPC(20:4) by hepatocytes and enhanced biliary secretion, (2) increased lysophospholipase activity in plasma, and (3) increased renal excretion of LPC(20:4). Regarding (1) increased uptake of LPC(20:4) by hepatocytes and enhanced biliary secretion, it is widely recognized that the liver plays a major role in the removal of plasma LPC [39], and biliary secretion of LPC has been demonstrated in rat liver [40]. However, if the lower plasma level of LPC(20:4) is due to more efficient uptake into hepatocytes, why would LPC(20:4) be taken up more efficiently by hepatocytes in Slc22a23 knockout rats? A specific transporter is required for the cellular uptake of LPC, such as MFSD2A (SLC59A1) for LPC(22:6) (lysophosphatidylcholine a C22:6n3) [15]. Although it is difficult to explain how the absence of a transporter (Slc22a23 knockout) would lead to increased uptake of LPC(20:4) into hepatocytes, hepatic AA levels in Slc22a23 knockout rats were significantly higher than those in WT rats 2 hours after intravenous administration (Figure 4E). This result supports the idea of increased hepatic uptake of LPC(20:4) and subsequent AA production in Slc22a23 knockout rats. Regarding (2) increased lysophospholipase activity in plasma, LPC(20:4) can be degraded in the circulation by lysophospholipases, including lysophospholipase A1 and lysophospholipase D [41]. However, if the lower plasma level of LPC(20:4) is due to more efficient degradation in plasma, why would lysophospholipase activity be enhanced in the absence of a transporter (Slc22a23 knockout)? It is difficult to explain how the loss of a transporter (Slc22a23 knockout) would result in increased lysophospholipase activity in plasma. Furthermore, plasma AA levels in Slc22a23 knockout rats were significantly lower than those in WT rats 0.5 hours after intravenous administration (Figure 4D), suggesting that efficient degradation of LPC(20:4) in plasma is unlikely. Lastly, regarding (3) increased renal excretion of LPC(20:4), the kidney, alongside the liver, is one of the most important organs for the excretion of drugs and metabolites: the liver excretes compounds into bile, whereas the kidney excretes compounds into urine [42]. Renal excretion of drugs and metabolites involves three distinct processes: glomerular filtration, active tubular secretion, and passive tubular reabsorption [42]. SLC22A23 belongs to the SLC22 family of membrane transporters, which facilitate substrate movement across membranes through passive transport or secondary active transport driven by concentration gradients [43]. Therefore, SLC22A23 could be involved in the passive tubular reabsorption of LPC(20:4), although there are currently no supporting data for this possibility. If the SLC22A23 functions in the passive tubular reabsorption of LPC(20:4) in the distal renal tubule, the reduced plasma levels observed in Slc22a23 knockout could be simply explained by decreased reabsorption and increased urinary loss. The Slc22a23 gene is expressed in the mammalian/rodent renal system, as indicated by the gene expression databases (https://www.bgee.org/gene/ENSMUSG00000038267). Slc22a17, which shares the highest homology with Slc22a23, is expressed in the distal nephron [11] and is proposed to function as a receptor that reabsorbs proteins (ex. metallothionein) via receptor-mediated endocytosis [11]. Similar to SLC22A17, SLC22A23 may mediate the reabsorption of LPC(20:4) in the distal renal tubule. Therefore, possible mechanisms could include (1) increased uptake of LPC(20:4) by hepatocytes and enhanced biliary secretion, and/or (3) increased renal excretion of LPC(20:4). Further studies are warranted to elucidate the precise molecular mechanism.”

 

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report (Previous Reviewer 2)

Comments and Suggestions for Authors

I thank the authors for the acquisition phase analysis and the textual caveats added to the paper. 

I would like to clarify my original comment on the statistical analysis. I have no issues with the two-group comparison and I take the authors' point that the study is designed around the effect of LPC(20:4) within each genotype. My concern is with the number of contrasts. Within a single behavioural test, the same two-group contrast is repeated many times. For example, the NOR analysis comprises of 8 contrasts, with two genotypes, two ages and two injection timings. Restricting comparisons to within genotype does not reduce the contrast counts. If the authors want to retain the current analyses, I would suggest to state in section 2.7 that the behavioural comparisons are unadjusted for multiplicity. The caveats that the authors have added in the main text largely address my concern. However, the abstract does not reflect these caveats. I would also note that "consistently" at line 2651 now contradicts the caveat added at lines 2662 to 2665.

 

There are also some textual errors in the paper, including:

Line 1961 - Slc22a22 proficient and deficient should be Slc22a23.

Slc22s23 instead of Slc22a23 appears in several places as well, e.g. line 228, line 2315. 

Please check the citations for Figure 11D and 11F around Line 2200 to 2300. Are those meant to be 12D and 12F?

Figure legend for figure 6 has errors, as there is no panel F.

Author Response

Response to Reviewer 2 Comments
1. Summary
Thank you very much for taking the time to review this manuscript. Please find the detailed responses below and the corresponding revisions in track changes in the re-submitted files.
2. Questions for General Evaluation	Reviewer’s Evaluation	Response and Revisions
Does the introduction provide sufficient background and include all relevant references?	Yes
Is the research design appropriate?	Can be improved
Are the methods adequately described?	Can be improved
Are the results clearly presented?	Can be improved
Are the conclusions supported by the results?	Can be improved
Are all figures and tables clear and well-presented?	Yes
3. Point-by-point response to Comments and Suggestions for Authors
Comments 1: I thank the authors for the acquisition phase analysis and the textual caveats added to the paper.    I would like to clarify my original comment on the statistical analysis. I have no issues with the two-group comparison and I take the authors' point that the study is designed around the effect of LPC(20:4) within each genotype. My concern is with the number of contrasts. Within a single behavioural test, the same two-group contrast is repeated many times. For example, the NOR analysis comprises of 8 contrasts, with two genotypes, two ages and two injection timings. Restricting comparisons to within genotype does not reduce the contrast counts. If the authors want to retain the current analyses, I would suggest to state in section 2.7 that the behavioural comparisons are unadjusted for multiplicity. Response 1: Thank you very much for pointing this out. I added a sentence at Line 1069 (Line 438): “The behavioral comparisons are unadjusted for multiplicity.”   The caveats that the authors have added in the main text largely address my concern. However, the abstract does not reflect these caveats. I would also note that "consistently" at line 2651 now contradicts the caveat added at lines 2662 to 2665. Response 1: Thank you very much for pointing this out. I removed “consistently” at Line 3220 (Line 1040).   There are also some textual errors in the paper, including: Line 1961 - Slc22a22 proficient and deficient should be Slc22a23. Slc22s23 instead of Slc22a23 appears in several places as well, e.g. line 228, line 2315.  Response 2: Thank you very much for pointing this out. I fixed them.   Please check the citations for Figure 11D and 11F around Line 2200 to 2300. Are those meant to be 12D and 12F? Response 3: Thank you very much for pointing this out. I fixed them.   Figure legend for figure 6 has errors, as there is no panel F. Response 4: Thank you very much for pointing this out. I fixed them.”

 

 

Author Response File: Author Response.pdf

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

 

This study investigates the role of the orphan membrane transporter SLC22A23 in brain metabolism and neurodevelopment, focusing on its potential function through LPC 20:4. Using Slc22a23 knockout and wild-type rats, the authors identify reduced plasma LPC 20:4 levels in the knockout animals and evaluate the behavioral effects of LPC 20:4 administration to both control and knockout animals through several standard paradigms (open field, novel object recognition, social interaction, and Morris water maze tests). The findings suggest that LPC 20:4 supplementation enhances memory acquisition for Slc22a23+/+ and Slc22a23-/- animals. Thus, it indicated that SLC22A23 may participate in LPC 20:4 transport, although additional mechanisms are likely involved.

 

The work addresses an intriguing question regarding the physiological substrates of orphan transporters and their links to neurobehavioral phenotypes. The approach combining metabolomic profiling with behavioral assays is conceptually sound. The manuscript presents a potentially novel link between SLC22A23 and LPC 20:4–related metabolic and behavioral phenotypes. The proposed conclusions are well supported by experimental design and data interpretation.

Minor Comments:

1. The introduction could be improved by elaborating more on prior knowledge of SLC22A23, its relationship to the broader SLC22 family, and how it is linked to DoHaD hypothesis
2. The metabolomic screen likely identified multiple differential metabolites. It seems that LPC 20:4 was prioritized as a candidate substrate mainly based on the most significant change of levels in Slc22a23 knockout plasma. However, other less altered lipids might also play important biological roles. It might be more insightful to elaborate on other altered lipids and their potential roles in the discussion session. For example, whether other LPC species (e.g., LPC 16:0, LPC 18:1) were altered would help determine if the effect is selective or reflects a general disruption of phospholipid metabolism.
3. For all the statistics, it would be informative to also compare the two groups of (+/+) Naïve (C) and (-/-) Naïve (L), to evaluate how much the exogenous supplied LPC 20:4 would compensate the loss of SLC22A23. The analysis might shed light on whether SLC22A23 function as a transporter exclusively or with other roles, and whether other transporters for LPC 20:4 exist and co-play with SLC22A23.
4. Typo in line 527 “linoleic and” should be “linoleic and”

Additional comments: It would be very informative to conduct spatial metabolomics study of Slc22a23 knockout animals (brain, liver and other organs) to better understand where and how the various lipids were affected. Also how the injection of LPC 20:4 enhances its level in the brain. However, this set of experiments would be beyond the scope of current study but would be interesting to follow up for better mechanistic understanding.

Reviewer 2 Report

Comments and Suggestions for Authors

In this study, the authors are trying to identify the potential substrates of the SLC22A23 transporter, so they carried out a mass spectrometry of rat plasma and found two compounds (lysophosphatidylcholine C20:4 (LPC 20:4) and phosphatidylcholine ae C40:1 (PC O-C40:1) with an alkyl-ether bond) to be significantly different in proficient and deficient rats. From there, they synthesized LPC 20:4 for their subsequent experiments.

 

The introduction adequately covers the DOHaD background and the Slc22a23 characterisation.

 

Comments on materials and methods, and experimental design:

The authors did not check how much LPC 20:4 enters the plasma, how quickly it is cleared from the plasma, and whether the synthesized LPC 20:4 reaches the brain after administration. The last point is very important given that the authors are making conclusions that LPC 20:4 has central nervous system effects, and they noted that LPC 20:4 is more effective in proficient than deficient rats.

 

The presentation of figure 1 could use improvement. The treatment that the mice are receiving in each group and the number of mice per group is more important information than the period when the experiments are carried out. It would be helpful if the authors explain what the arrows indicate – black arrows are testing days, green arrows are treatment timepoints. The authors can also consider removing some of the text in the figure e.g. i.v., since all the mice are treated via that route and describe in the figure legend that the green arrows represent i.v. treatment. They can also remove the 24hr labels, especially for the watermaze, since they have the days labeled. They can then use different coloured arrows to represent 2hr treatment and 6 hr treatment. This will make figure 1 les cluttered and easier for the reader to understand.

 

From the experimental design, I see that the authors have chosen to manipulate the length of time of treatment prior to the training or acquisition part of the novel object test and the social interaction test. However, I do not see the explanation for why they only chose the 6hr timepoint for the reversal day 1 and 2 of watermaze.

 

For day 2 of the social interaction test, a better control would be to put an object in the cup, instead of leaving it as an empty cup, as that serves as a non-social stimulus to be compared against the social stimulus. Leaving the cup empty will not give information for a general preference for an object or a social object.

For day 3 of the social interaction test, the authors assessed the interaction times with rat A and rat B across different test sessions to get a measurement of social novelty. However,  if the authors were assessing social memory, they should have put rat A in one cage and rat B in the other cage, and a preference for rat B  over rat A in the same testing session would be a more accurate measurement of the test rats preferring to explore rat B because it is the novel social stimulus compared to rat A.

It is unclear what statistical tests were used for the behavioural dataset, as the authors only stated that the JMP statistical software is used. However, this statistical software can run different types of statistical tests. Hence, I am unable to evaluate whether the statistical tests used to analyse the behavioural data are appropriate.

 

General comments for the results:

In the results, it would be helpful if the authors explain in 3.3 what naïve(C) and naïve(L) are in line 343, instead of stating it only in the figure legend of 4A.

As a general comment for all the results figures, I suggest removing the averages of the data along the x axes from all the figures and putting this information in tables with the SEM instead. A figure key for the symbols and arrows would also be helpful. The figure legends can be streamlined and be more descriptive of the figures. For example:

• in Figure 7, the methods can be left out or moved to the methods to avoid repetition,
• the statistical test should not be in the figure legend for figure 4. Rather it should be in the materials and methods.
• Some of the information in the figure legend, e.g. figure 4b “placed in a circular chamber (100cm diameter, 45cm height)” should go to the materials and methods, and instead, the figure legend should have a brief description of the data, e.g. deficient rats had increased distance traveled compared to WT (p=0.0391), with no significant differences between the rats allocated to the control and treatment groups.

 

 

Comments on Open field results:

Given that the authors tested the animals across multiple timepoints in the open field, they should be running a mixed-design anova with repeated measures and Bonferroni-corrected posthoc tests, rather than doing a difference in distance between 8weeks and 7 weeks, and 12 weeks and 7 weeks, because the exposure in the 8^th week would influence the 12^th week.

It is also strange that at baseline, before treatment, the naïve -/- rats showed increased distance traveled compared to +/+ in the group that are allocated to the 6hrs treatment time, whereas no increased in distance traveled is shown in the naïve rats allocated to the 2hrs treatment time. However, the authors only described the results for the baseline for the 6hr treatment time group, ignoring the 2hr treatment time group (line 344 to 347). If baseline genotype differences are inconsistent between cohorts, how are the authors able to compare treatment effects across cohorts?

After treatment, the use of two-tailed t tests here is inappropriate. As mentioned earlier, the authors should use a mixed-design anova, main effects would be genotype (between), treatment type (between), treatment time (between), Oft exposure (within, repeated measures at 7, 8 and 12). If they have a reason now to compare between 6hr and 2hr, then they do not need to include the treatment time and acknowledge that these are separate experiments. The significant main effects and interactions should be reported. If there are significant interactions, then they should do a Bonferroni-corrected, posthoc comparison. If the authors do this, then calculating the difference in locomotor activity from 7 weeks will not be necessary, and figure 5D and E will not be needed.

Figure 4 is rather confusing because it at first looks like the animals have been treated, because the figure legend stats “Control and LPC 20:4 injection group in each genotype”. However, the data that they are showing are animals from the two genotypes at baseline. The representation of these results could be made clearer. I do not think that the date when the animals are run is necessary here, because the more important information is the timepoint for the injection.

 

Comments on NOR results:

The authors state that the novel objects had holes in the caps, resulting in a preference for the novel object. However, the title for panels 6B and 6C is “Day 1 acclimation”, which should be when the animal is seeing the same familiar object (black circles). There should not be a preference for either black circle during the acclimation, or rather, the period when the animal is being trained to recognize the familiar object. Or perhaps the authors mean “Day 2 NOR”.

In addition, if the animals a preferring the novel object due to the complexity of the object, rather than because it is novel, then the measurements obtained, regardless of whether the ratio or the absolute time is used, is not reflective of recognition memory in these animals. The authors should have ensured that the familiar and novel object are of similar complexity, to avoid confounding factors in the test. Looking at the time spent with the novel object as a measure of memory would not help, because each animal has different exploration levels and different motivation to explore. The evidence that the animals are spending less time to explore can be seen when you compare the general trend of time spent at 12 weeks versus 8 weeks. The time spent at 12 weeks is generally lower across genotypes and treatment groups, likely because the animals are less interested in exploring objects that they have seen at 8 weeks.  Given the confounding factor of object complexity and only using the time spent with novel object, the NOR results cannot be reliably interpreted as reflecting the treatment and genotype effects on recognition memory.

Additionally, please check the graph titles for panels D and E. These should say day 2, not day 1. For the statistical analysis, it is a similar comment to the OFT. It should be a mixed-design anova with between and repeated measures. The averages long the x axes should be put in table form to avoid cluttering your figure.

 

Comments on Social interaction test results:

As mentioned earlier, the social interaction test has a confound where the other cage is empty. In a standard SI test, one cage should have an inanimate and the other the partner animal. For a social novelty test, one cage should have the familiar partner and the other cage has the novel partner to give the animals a choice. In the current design, the authors are just comparing interaction times of partner rat versus empty cage in separate sessions. Exposing the test rat to one partner rat at a time rather than giving the test rat a choice between two partners simultaneously suggests that the absence of social novelty preference is likely due to a flawed test design rather than a lack of treatment or genotype effects.

 

Comments on Watermaze results:

For the watermaze, the animals are treated twice, at the start of day 1 and day 2 of the reversal phase. It would have been helpful if the authors explain why they only treated the animals for the reversal phase and not the acquisition phase.

 

Here, the authors show that while the animals spend significantly more time in the 40cm around the target zone than a 40cm area elsewhere in the pool (red numbers in the figure), there seems to be no significant genotype or treatment effects on spatial memory recall. For the statistical analysis here, it should be a two-way anova, with 2 genotypes and 2 treatments and a genotype by treatment interaction, then Bonferroni-corrected t tests, not a two-tailed t test. Additionally, upon noting that the animals had no treatment for the acquisition and treatment for the reversal, perhaps the authors should compare the acquisition versus reversal probes for 8 to 9 weeks, and 12 to 13 weeks, as a proxy measure for no treatment versus with treatment within the same animal.

 

The authors then looked at the effect of treatment on day 1 and day 2 of the reversal, which is an assessment of cognitive flexibility and relearning. The authors should do a repeated measures anova analysis for the learning curves of the reversal phase, rather than two-tailed t tests. From the first trial graph (panel C), it looks like the open triangles remain more spread out than the other groups across the days, so there may be a genotype x treatment interaction across the training days for trial 1 if the authors do an anova. The authors should explain why they treated before and after day 1 and justify their decision for analysing trial 1 separately from trials 2 to 4.

 

The authors could add in swim distance and swim speed to rule out differences in exploration levels due to repeated testing effects in the watermaze.

 

In figure 8, panel C, the Y axis states “within 20cm target zone”, but the methods, figure legends and text says “40cm of target zone”. Please check.

 

Comments on Statistical power:

This study is likely underpowered, because there are many comparisons being done – 2 genotypes, 2 treatments, 2 treatment periods, 2 ages, two timepoints for testing (for NOR and SI). However, the authors have only about 6 to 7 animals per group for the 6hr injection group, which is where they are noting most of their effects. This is generally lower than what most behavioural studies would have, which is 8 to 12 animals in each group. Paradoxically, the 2hr injection groups have more animals, up to 12 in some groups and thus providing better statistical power, but fewer significant effects were found. Their finding suggest some pharmacokinetic differences between the two injection timings, but these were not adequately addressed in this paper.

In addition, with multiple comparisons in this study design, the authors used two-tailed t-tests without correction. This inflates Type I error rate.

 

General comments for Discussion:

While I understand why the authors may have opted to only use male rats for this study (differing social behaviours and lipid profiles), a justification of why only male rats was should be included.

Additionally, the authors did not address why they chose LPC 20:4 instead of PCO-C40:1 for their subsequent experiments.

 

 

Discussion for NOR:

The authors stated that LPC 20:4 administration reduced time spent exploring the novel object in the latter half of the test, however they concluded that this represents memory enhancement without explaining how they came to this conclusion.

 

Discussion for SI:

The authors mentioned reduced sociability, in lines 584-587, but did not discuss what their findings mean. It was not clear how their data for social interaction works into part of their “memory enhancement” claim. Perhaps they mean that the significantly reduced interaction times with rat 2 from day 2 to day 2 in LPC20:4 treated WT and -/- at 9 weeks suggest social memory. However, they did not discuss why the effect was absent in 13week-old rats.

 

Discussion for WM:

The authors treated prior to the first reversal training on day 1 – possibly affecting acquisition, and prior to day 2 – possibly affecting recall and subsequent acquisition. However, there is no discussion on how treatment on only Days 1-2 produces effects in Days 3 to 5. The authors should discuss whether this reflects persistent pharmacological effects due to improved learning or enhanced memory consolidation and recall.

In addition, with the effects observed during reversal training, the lack of treatment effects in the reversal probe is contradictory. Although this is not unusual (e.g. ceiling effect), it should be discussed.

The authors also did not discuss why the reversal training curves for the 13 weeks tend to 0 much faster than at 9 weeks. This is likely due to the repeated testing effects in the watermaze (as mentioned earlier), which are difficult to overcome even with different distal cues (there are several published reviews on the effects of repeated testing).

 

In general, given the confounds in the experimental protocols, the lack of explanation for some of the decisions made with treatment timepoints, underpowered study, it is not clear how the authors can "conclude that LPC 20:4 administration can enhance memory acquisition in both Slc22a23+/+ and Slc22a23-/- rats.”

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript by Yasuhiro Uchimura and colleagues is an example of a solid and well-planned research. The Authors have identified a number of potential targets for an orphan transporter using their knockout rat model. They synthesized the most potent target and used it both in control and knockout animals. Physiological effects are reported. The description of Methods and results is also on a high scientific level, although the choice for the statistical tests used should be described. Importantly, as the t-test was used, and a lot of groups were compared each time, the problem of multiple comparisons must be taken into account and a correction for multiple testing should be used. Probably is already was used, but there is no description in the manuscript, so please clarify.

There is no description of the choice of animals' sex for the experiments. Why weren't the females used?
Table 1 description should include abbreviations and the green color, if the latter is neсessary. 

Have you confirmed, that supplementation of LPC 20:4 to animals increase its level in blood of both control and knockout rats? Such an experiment would improve understanding of the obtained data, testing the ability of SLC22A23-/- rats to obtain LPC 20:4 when supplemented in extra quantities. Comparison with the behavioral data would be possible too.

 

Reviewer 4 Report

Comments and Suggestions for Authors

 

The study investigates an underexplored SLC22 family transporter, Slc22a23, using knockout rats and behavioral assays linked to lysophosphatidylcholine (LPC 20:4) metabolism. This is a significant step forward in understanding orphan transporter biology, particularly in the context of neurodevelopmental and behavioral regulation. The linkage between metabolomics (LPC 20:4) and behavioral outcomes is innovative.

 

The introduction successfully connects SLC22A23 regulation, and behavioral phenotypes. However, the mechanistic bridge between undernutrition, Slc22a23 upregulation, and LPC 20:4 function is weakly defined.

 

1. Clarify why LPC 20:4 was prioritized among hundreds of metabolites and please sufficiently discuss the prior paper, including neuroanatomic changes.
2. How SLC22A23 might mediate LPC transport mechanistically (e.g., similarity to other SLC22 transporters, membrane localization, charge-based transport feasibility).
3. Metabolomics has been performed in a large number of SLC22 transporter knockouts. These knockouts should be discussed. Is LPC altered in any of these knockouts? 
4. Discuss the OAT-related subgroup in the Intro referring to the various evolutionary classifications in original papers. This is a somewhat odd subgroup, and please better explain the relationships of SLC22A23 to more familiar SLC22 transporters such as OCTs, OATs, OCTNs. Is there some reason to expect a neurobehavioral phenotype with SLC22A23 based on this?
5. The metabolomic approach is robust for plasma analysis. However, given the extensive discussion of the neurological effects and hippocampal changes known in the knockout, metabolomic analysis of brain tissue – specifically the hippocampus- seems warranted. Did they try CNS metabolomics? 

 7. The discussion reiterates behavioral findings but doesn’t sufficiently connect them to SLC22A23 transporter biology or LPC 20:4 pharmacokinetics. The possibility that LPC 20:4 is a direct or indirect substrate is left unresolved. Again, it is very important to discuss metabolic changes in other SLC22 transporter knockouts. Why don't they have behavioral phenotypes? Maybe the authors can suggest which ones ought to be further investigated in this regard based on LPC?