Tracking of Neuroinflammation Dynamics During Combined Anti-β-Amyloid Therapy (AAT) and Immunomodulation in a Preclinical Alzheimer’s Disease Model

Round 1

Reviewer 1 Report (New Reviewer)

Comments and Suggestions for Authors

In this study, the effect of combined treatment in transgenic mice modeling human Alzheimer's disease was evaluated using anti-Aβ antibodies and pioglitazone, assessed via various PET imaging approaches measuring amyloid burden and neuroinflammation, along with additional behavioral tests and biochemical analyses.

The experiments were carefully designed and described. I have only a few minor comments.
It is possible that in earlier versions of the manuscript the Methods section preceded the Results section, and many abbreviations were defined in Methods. Please define these abbreviations in the main text of the Results section at their first mention, in accordance with https://www.mdpi.com/journal/biomedicines/instructions (acronyms/abbreviations/initialisms should be defined the first time they appear in each of three sections: the abstract; the main text; the first figure or table). For example, this applies to [18F]FBB in line 80, [18F]GE-180 in line 104, %ID in line 101, DEA in line 196, RIPA in line 198, LMEM in line 231, EHA in line 276. Additionally, VOI in line 618 remains undefined.

In lines 193-194, it is unclear which specific method was used to analyze Aβ40 and Aβ42 levels without referring to the Methods section (blood, brain, ELISA, or western blot). Please clarify this in the text for the readers' convenience.

Author Response

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Reviewer 2 Report (New Reviewer)

Comments and Suggestions for Authors

This manuscript presents a valuable preclinical imaging study. In my view it is suitable for publication after minor revision. The longitudinal combination of TSPO-PET and Aβ-PET across multiple treatment arms, together with behavioral and biochemical follow-up, gives the work clear value and makes it a meaningful contribution to the field. Few points would benefit from clarification, particularly slightly softer wording where treatment effects are inferred, clearer reporting of the most relevant between-group contrasts, a more cautious interpretation of baseline-versus-change analyses, and brief clarification of how sex and missing data may have influenced the results. These are relatively modest issues of presentation and interpretation, and they do not diminish the overall  relevance, and potential impact of the study. 

Author Response

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Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

 

Thank you for the opportunity to review this manuscript. The study addresses a highly relevant and timely question in Alzheimer’s disease research, namely the interaction between anti-β-amyloid immunotherapy and neuroinflammatory dynamics, and how these processes may be modulated by adjunctive treatment with pioglitazone.

Overall, the manuscript presents a well-designed and technically solid study. The longitudinal design, the inclusion of multiple treatment arms, and the integration of TSPO-PET, Aβ-PET, biochemical analyses, and behavioral outcomes are clear strengths. The topic is of significant interest, particularly in light of the increasing clinical use of anti-Aβ monoclonal antibodies and the need to better understand treatment-associated inflammatory responses.

However, despite these strengths, there are several important issues that need to be addressed before the manuscript can be considered for publication. In its current form, the manuscript tends to overinterpret certain findings, and some of the central conclusions are not fully supported by the data. In addition, key limitations—particularly related to biomarker interpretation and mechanistic validation—require a more explicit and balanced discussion.

Below, I provide detailed comments aimed at strengthening the manuscript.

 

Major Comments

1. Overinterpretation of non-significant findings

A central concern relates to the interpretation of treatment effects on neuroinflammation, particularly in the global TSPO-PET analysis. While the manuscript suggests that pioglitazone attenuates the neuroinflammatory response associated with anti-Aβ monoclonal antibody treatment, the relevant comparisons do not remain statistically significant after false-discovery-rate correction and are appropriately described as exploratory. However, this limitation is not consistently reflected in the narrative. In several sections of the Results and Discussion, these findings are still interpreted in a manner that suggests a more definitive biological effect.

 

2. Interpretation of TSPO-PET signal

The manuscript largely interprets TSPO-PET as a marker of microglial activation. While this is a common approach, it is also well established that TSPO expression is not specific to microglia and may include contributions from astrocytes and vascular elements. Although this limitation is briefly acknowledged, it is not sufficiently integrated into the interpretation of the findings.

 

3. Interpretation of Aβ-PET signal

The manuscript appropriately notes that increases in Aβ-PET signal may reflect multiple factors, including changes in plaque composition, fibrillarity, tracer accessibility, or vascular amyloid deposition. However, despite this important caveat, some sections of the manuscript still lean toward relatively specific interpretations (e.g., increased plaque compactness or fibrillarity) without direct validation.

 

4. Lack of mechanistic validation

The study proposes that pioglitazone modulates neuroinflammatory responses and may shift microglia toward a more favorable phenotype. However, there is no direct experimental validation of these mechanisms. While the biochemical analyses are valuable, they do not fully support the proposed mechanistic interpretation.

 

5. Desynchronization Index (DI)

The use of the microglial desynchronization index is an interesting and potentially innovative aspect of the study. However, its biological interpretation remains relatively specialized and not widely established. At present, the manuscript gives this metric substantial interpretive weight, including its association with behavioral outcomes.

 

6. Statistical considerations

The manuscript employs appropriate statistical methods (e.g., LMEM), but there are several aspects that require clearer communication: Moderate and variable sample sizes across groups and time points, multiple comparisons, and reliance on trends that do not reach statistical significance.

 

7. Discussion structure and balance

The Discussion is well informed and demonstrates strong familiarity with the literature. However, it is somewhat lengthy and occasionally repetitive, and in some sections the interpretation extends beyond what is directly supported by the data.

 

8. Graphical model

 

You may consider including a final schematic figure summarizing the main findings and their conceptual implications for Alzheimer’s disease. Given the complexity of the study design and the multiple layers of data (TSPO-PET, Aβ-PET, biochemical markers, and behavioral outcomes), a visual summary would greatly enhance the clarity and overall impact of the manuscript.

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 3 Report (New Reviewer)

Comments and Suggestions for Authors

Thank you for the detailed and thoughtful responses to my previous comments. I am pleased to see that the manuscript has been significantly strengthened. The moderation of the language regarding exploratory findings and the inclusion of the graphical summary provide a much clearer and more scientifically rigorous narrative.

All major and minor points have been addressed to my satisfaction. My only remaining suggestion is to perform a final, thorough grammatical and stylistic review of the entire text (especially the new sections) to improve the overall flow and ensure the highest professional standard. I have no further concerns regarding the scientific content and believe this work will be a valuable contribution to the field

Author Response

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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

Dear authors, thank you for writing a paper about such an interestic topic. I slightly have my doubts about the title as in my opinion it is not really vaccination what you do but this is a minor concern. Same is true for the introduction, the experimental setup doesn't click naturally. You have to read it twice to understand why you use both TSPO and FBB imaging.

Major concerns came when I start reading the results and had a look at Figure 1. First all the abbreviations mentioned in the figure should be in the figure legend too. More important it is not clear what am I looking at? Is this the average signal of all animals within one group (how representative is this), or is it one representative animal of each group (and than the same for each timepoint to overcome individual differences as the quantification is already showed in the graphs)? While it is unusual to pool all the different treatmentgroups in one graph (as you did in D and E) without showing the differences as your aim is too show differences between the treatment groups.

In line 489 you mention that you obtained 165 scans but in Figure 1 I only count 164 scans. How are the animals divided over the groups (becasue table S7 is challenging to interpret)? Another point, there is a large difference between the number of scans per timepoint. If I understand it correctly on the 7.5M timepoint 40 scans were obtained while 27 failed? How do you explain this? This is not only scientifical but also ethical a red flag.

Another thing which is missing is the explanation regarding the scanning timepoints; 5M is baseline but in line 412 you mention that already from 2M on Abeta deposition is detectable and from approximately 6M memory impairments are measurable. Which means that for some of the animals at 5M this will be the case. It is in that regard also challenging to understand why you only used the 10M timepoint to perform behavioral testing. It would be in line with the 3Rs to use each animal as its own control and perform a baseline test too. 

You mention under 4.1.1 that all animals are randomly assigned to treatment groups, so I assume that also not all animals from one group are housed together in one cage? How do you do this with the Pioglitazone treatment (line 430) which was given into the regular mouse chow diet, also here how do you account for the differences in uptake? There will be heterogeneity within the uptake how do you correlate this with your results. Kind of same problem which is not clear for the ip injections (line 421 and 434) did the control groups get an injection with NaCl?

Last thing, in 4.1.2 you mention blinding but how is blinding of one experimenter possible at all? 

Author Response

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Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript presents a longitudinal multimodal imaging study investigating neuroinflammation and amyloid pathology in AppNL-G-F knock-in mice during chronic anti-Aβ monoclonal antibody treatment, with and without co-administration of the PPAR-γ agonist pioglitazone. The integration of TSPO-PET, Aβ-PET, biochemical analyses, and behavioral testing is a clear strength. The introduction of a PET-based microglial desynchronization index (DI) is innovative and potentially impactful.

The topic is timely and highly relevant, particularly in the context of emerging anti-Aβ immunotherapies and increasing recognition of neuroinflammation as a modulator of therapeutic response and adverse events.

However, several conceptual and methodological issues limit the strength of the conclusions. In particular, the functional interpretation of TSPO-PET, the framing of “beneficial vs harmful neuroinflammation,” and the mechanistic claims regarding pioglitazone require substantial revision. The manuscript would be suitable for publication after major revision addressing the concerns outlined below.

Major Comments

1. Overinterpretation of TSPO-PET

The manuscript frequently interprets TSPO-PET as a direct functional marker of microglial activation (e.g., enhanced phagocytosis, beneficial modulation, harmful inflammation). This interpretation is too strong.

TSPO is not microglia-specific and may reflect astrocytic or vascular contributions. Moreover, TSPO expression does not distinguish functional phenotypes of microglia. No functional assays (e.g., phagocytosis, DAM markers, CD68, Trem2 clustering) or histological validation are provided to confirm the cellular source of the signal.

Therefore, statements suggesting that treatments “improve microglial response” or “enhance phagocytic capacity” are not directly supported by the data. Mechanistic claims should be rephrased using more cautious language (e.g., “associated with,” “consistent with,” “suggests altered coupling”) and avoid causal interpretation.

2. Lack of Immunohistochemical Validation

Although acknowledged, the absence of immunohistochemistry represents a major limitation. The study makes central claims about microglial modulation without:

• validation of microglial density or morphology,
• confirmation of TSPO colocalization,
• assessment of plaque-associated microglia,
• quantification of CAA or vascular pathology, despite discussion of ARIA-like mechanisms.

This limits attribution of TSPO changes specifically to microglial biology and weakens the interpretation of increased Aβ-PET signal under pioglitazone as plaque compaction. The limitations section should be strengthened and mechanistic certainty reduced. Any available archival tissue validation would substantially enhance the manuscript.

3. Interpretation of Increased Aβ-PET Signal with Pioglitazone

A key finding is increased [18F]FBB SUVR with pioglitazone (alone or combined) despite reduced insoluble Aβ biochemically. The proposed explanation, plaque compaction with increased β-sheet content, is plausible but remains speculative. Alternative explanations include:redistribution toward vascular Aβ (CAA), altered tracer accessibility, treatment-related vascular remodeling or microhemorrhages.

Without histological confirmation, definitive conclusions about plaque compaction are premature. Alternative interpretations should be more explicitly discussed.

4. Statistical Interpretation

Several global TSPO-PET comparisons do not remain significant after FDR correction yet are narratively interpreted as supporting anti-inflammatory effects. While effect sizes are informative, trends should not be presented as confirmed findings.

The manuscript should clearly distinguish statistically significant results from exploratory observations and avoid overstating non-significant comparisons.

5. Microglial Desynchronization Index (DI)

The DI is an innovative component but requires further clarification regarding: sensitivity to global signal shifts, dependence on SUVR normalization, lack of validation against independent biological measures, behavioral correlations observed only in a specific subgroup.

It remains unclear whether DI reflects biologically meaningful network-level microglial dynamics or statistical covariance influenced by global signal variation.

Additional clarification on robustness and incremental value beyond conventional SUVR would strengthen this section.

6. Behavioral Correlations

The negative correlation between TSPO-PET and Morris water maze performance appears only in the anti-Aβ monotherapy group. The conclusion that pioglitazone prevents detrimental inflammation is plausible but not uniquely supported. Alternative explanations include reduced variance, ceiling/floor effects, or reduced dynamic range in treated groups. Formal comparison of regression slopes across groups would strengthen this analysis and causal interpretations should be tempered.

7. Translational Framing

The discussion proposes clinical exploration of anti-Aβ plus PPAR-γ agonist combination therapy. However, clinical trials of pioglitazone in AD have not demonstrated clear efficacy, safety considerations in elderly populations are not discussed, the antibody used differs from currently approved agents. Therefore, a more balanced discussion of translational limitations is recommended.

Minor Comments

1. Clarify stability of the brainstem reference region across genotype and treatment.
2. Provide explicit sample sizes per group and timepoint in figure legends.
3. Ensure consistent interpretation of %ID vs SUVR throughout the text.
4. Correct minor typographical and formatting issues.
5. Improve clarity of selected multi-panel figure descriptions.

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Dear authors, thank you very much for this fast reply and the alterations you made to the manuscript this definitely improved it. 

Our intention was to provide an overall visual impression of the treatment- and age-related signal distribution at the group level while avoiding potential bias from selecting one individual animal that may not be representative of the cohort. --> But now everything is averaged out and differences are more challenging to see. You have a group because you expect heterogeneity and this also makes the model a representative model as in humans the same heterogeneity is found. You now present it like this isn't good and that every mouse within a group should behave exactly the same.

to confirm that AppNL-G-F mice show higher TSPO-PET uptake than WT mice independent of
treatment arm. --> what is the scientific rationale behind this increase in uptake?

we indeed had 164 TSPO scans, as it is correctly reflected in Table S7. Additionally, we noticed a mismatch in the total number of all mice (73 in methods vs 72 in Table S7) and WT mice (17 in Methods vs 16 in Table S7). --> this is at least sloppy, how reliable are the other numbers in that regard? That same sloppyness is reflected in the current version of the paper where numbereus times: Error! Reference source not found is stated in the text.

The numbers per animal group are now clear though the rationale between the differences in group sizes are not discussed. The same is true for the number of scans per timepoint. It is now mentioned that this is limited due to logistics but numbers are not mentioned. Why not? While such explicitly asked I expect a number when this is not given this raises questions.

Mice assigned to pioglitazone treatment were distributed across multiple cages --> does this mean that not all the mice from this group are in one cage (which makes sense) but is does not read that they are in separated cages? How many animals were housed in one cages? How is compensated for the individual differences? Did you found differences in chow weight between the cages? Are these differences correlated with the results found in the other parameters?

 

Author Response

Dear authors, thank you very much for this fast reply and the alterations you made to the manuscript this definitely improved it. 

A: We thank the reviewer for the overall positive assessment of the revisions made

1) Our intention was to provide an overall visual impression of the treatment- and age-related signal distribution at the group level while avoiding potential bias from selecting one individual animal that may not be representative of the cohort. --> But now everything is averaged out and differences are more challenging to see. You have a group because you expect heterogeneity and this also makes the model a representative model as in humans the same heterogeneity is found. You now present it like this isn't good and that every mouse within a group should behave exactly the same.

A: We thank the reviewer for the critical note. First, group average images are considered as a gold standard in showing imaging results. We do not deem it appropriate to change the images of figure 1 to arbitrary images of individual mice. Second, we do understand that the reviewer would like to see the heterogeneity of treatment groups at a higher level (i.e. in the main figure versus in the supplemental figure). Therefore, we moved supplemental Figure S2 into the main Figure 1 and edited the text respectively. With this approach, the individual heterogeneity is more pronounced, which we deem also important.

2) to confirm that AppNL-G-F mice show higher TSPO-PET uptake than WT mice independent of
treatment arm. --> what is the scientific rationale behind this increase in uptake?

A: The rationale of panels D and E of Figure 1 is to show that microglial activation in response to amyloid accumulation can be measured with TSPO-PET in the amyloid mouse model used. This constitutes a prerequisite for the subsequent analyses and  we deemed it crucial to show that TSPO-PET can detect more signal in AppNL-G-F mice compared to WT mice. 

3) we indeed had 164 TSPO scans, as it is correctly reflected in Table S7. Additionally, we noticed a mismatch in the total number of all mice (73 in methods vs 72 in Table S7) and WT mice (17 in Methods vs 16 in Table S7). --> this is at least sloppy, how reliable are the other numbers in that regard? That same sloppyness is reflected in the current version of the paper where numbereus times: Error! Reference source not found is stated in the text.

A: In light of a constructive academic exchange, we would appreciate if the reviewer would also take into consideration that these “error!” messages can occur from manuscript conversion instead of sloppiness by the authors. All references are displayed appropriate in the *.doc version that we downloaded for the second round of revision as recommended by the journal. We sincerely apologize for the necessary correction mentioned above.

4) The numbers per animal group are now clear though the rationale between the differences in group sizes are not discussed. The same is true for the number of scans per timepoint. It is now mentioned that this is limited due to logistics but numbers are not mentioned. Why not? While such explicitly asked I expect a number when this is not given this raises questions.

A: We do not understand the reviewer's criticism in this regard since all numbers are mentioned in Supplemental Table 7.  

Mice assigned to pioglitazone treatment were distributed across multiple cages --> does this mean that not all the mice from this group are in one cage (which makes sense) but is does not read that they are in separated cages? How many animals were housed in one cages? How is compensated for the individual differences? Did you found differences in chow weight between the cages? Are these differences correlated with the results found in the other parameters?

A: We confirm that previous studies (Blume et al 2024, PMC9007038) showed equivalent food intake per mouse regardless of the number of mice housed in one cage. There was no difference in chow weight between cages and thus, no specific analysis was performed.

Round 3

Reviewer 1 Report

Comments and Suggestions for Authors

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