Steady-state neuron-predominant LINE-1 encoded ORF1p protein and LINE-1 RNA increase with aging in the mouse and human brain

Reviewer #1 (Public review):

Summary:

In this study, Bonnifet et al. profile the presence of L1 ORF1p in the mouse and human brain and report that ORF1p is expressed in the human and mouse brain specifically in neurons at steady state and that there is an age-dependent increase in expression. This is a timely report as two recent papers have extensively documented the presence of full-length L1 transcripts in the mouse and human brain (PMID: 38773348 & PMID: 37910626). Thus, the finding that L1 ORF1p is consistently expressed in the brain is important to document and will be of value to the field.

Strengths:

Several parts of this manuscript appear to be well done and include the necessary controls. In particular, the documentation of neuron-specific expression of ORF1p in the mouse brain is an interesting finding with nice documentation. This will be very useful information for the field.

Weaknesses:

Several parts of the manuscript appear to be more preliminary and need further experiments to validate their claims. In particular, the data suggesting expression of L1 ORF1p in the human brain and the data suggesting increased expression in the aged brain need further validation. Detailed comments:

(1) The expression of ORF1p in the human brain shown in Fig. 1j is puzzling. Why are there two strong bands in the WB? How can the authors be sure that this signal represents ORF1p expression and not non-specific labelling? While the authors discuss that others have found double bands when examining human ORF1p, there are also several labs that report only one band. This discrepancy in the field should at least be discussed and the uncertainties with their findings should be acknowledged.

(2) The data showing a reduction in ORF1p expression in the aged mouse brain is an interesting observation, but the effect magnitude of effect is very limited and somewhat difficult to interpret. This finding should be supported by orthogonal methods to strengthen this conclusion. For example, by WB and by RNA-seq (to verify that the increase in protein is due to an increase in transcription).

(3) The transcriptomic data using human postmortem tissue presented in Figure 4 and Figure 5 are not convincing. Quantification of transposon expression on short read sequencing has important limitations. Longer reads and complementary approaches are needed to study the expression of evolutionarily young L1s (see PMID: 38773348 & PMID: 37910626 for examples of the current state of the art). As presented, the human RNA data is inconclusive due to the short read length and small sample size. The value of including an inconclusive analysis in the manuscript is difficult to understand. With this data set, the authors cannot investigate age-related changes in L1 expression in human neurons.

(4) In line with these comments, the title should be changed to better reflect the findings in the manuscript. A title that does not mention "L1 increase with aging" would be better.

Reviewer #2 (Public review):

Summary:

Bonnifet et al. sought to characterize the expression pattern of L1 ORF1p expression across the entire mouse brain, in young and aged animals and to corroborate their characterization with Western blotting for L1 ORF1p and L1 RNA expression data from human samples. They also queried L1 ORF1p interacting partners in the mouse brain by IP-MS.

Strengths:

A major strength of the study is the use of two approaches: a deep-learning detection method to distinguish neuronal vs. non-neuronal cells and ORF1p+ cells vs. ORF1p- cells across large-scale images encompassing multiple brain regions mapped by comparison to the Allen Brain Atlas, and confocal imaging to give higher resolution on specific brain regions. These results are also corroborated by Western blotting on six mouse brain regions. Extension of their analysis to post-mortem human samples, to the extent possible, is another strength of the paper. The identification of novel ORF1p interactors in brain is also a strength in that it provides a novel dataset for future studies.

Weaknesses:

The main weakness of the study is that cell type specificity of ORF1p expression was not examined beyond neuron (NeuN+) vs non-neuron (NeuN-). Indeed, a recent study (Bodea et al. 2024, Nature Neuroscience) found that ORF1p expression is characteristic of parvalbumin-positive interneurons, and it would be very interesting to query whether other neuronal subtypes in different brain regions are distinguished by ORF1p expression. The data suggesting that ORF1p expression is increased in aged mouse brains is intriguing, although it seems to be based upon modestly (up to 27%, dependent on brain region) higher intensity of ORF1p staining rather than a higher proportion of ORF1+ neurons. Indeed, the proportion of NeuN+/Orf1p+ cells actually decreased in aged animals. It is difficult to interpret the significance and validity of the increase in intensity, as Hoechst staining of DNA, rather than immunostaining for a protein known to be stably expressed in young and aged neurons, was used as a control for staining intensity. The main weakness of the IP-MS portion of the study is that none of the interactors were individually validated or subjected to follow-up analyses. The list of interactors was compared to previously published datasets, but not to ORF1p interactors in any other mouse tissue.

The authors achieved the goals of broadly characterizing ORF1p expression across different regions of the mouse brain, and identifying putative ORF1p interactors in the mouse brain. However, findings from both parts of the study are somewhat superficial in depth.

This provides a useful dataset to the field, which likely will be used to justify and support numerous future studies into L1 activity in the aging mammalian brain and in neurodegenerative disease. Similarly, the list of ORF1p interacting proteins in the brain will likely be taken up and studied in greater depth.

Comments on revisions:

The co-staining of Orf1p with Parvalbumin (PV) presented in Supplemental Figure S5 is a welcome addition exploring the cell type-specificity of Orf1p staining, and broadly corroborates the work of Bodea et al. while revealing that Orf1p also is expressed in non-PV+ cells, consistent with L1 activity across a range of neuronal subtypes. The authors also have strengthened their findings regarding the increased intensity of ORF1p staining in aged compared to young animals, and the newly presented results are indeed more convincing. The prospect of increased neuronal L1 activity with age is exciting, and the results in this paper have provided the groundwork for ongoing discoveries in this area. While it is disappointing that no Orf1p interactors were followed up, this is understandable and the data are nonetheless valuable and will likely prove useful to future studies.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Bonnifet et al. profile the presence of L1 ORF1p in the mouse and human brain. They claim that ORF1p is expressed in the human and mouse brain at a steady state and that there is an age-dependent increase in expression. This is a timely report as two recent papers have extensively documented the presence of full-length L1 transcripts in the mouse and human brain (PMID: 38773348 & PMID: 37910626). Thus, the finding that L1 ORF1p is consistently expressed in the brain is not surprising, but important to document.

Thank you for recognizing the importance of this study. The two cited papers have indeed reported the presence of full-length transcripts in the mouse and human brain. However, the first (PMID: 38773348) report has shown evidence of full-length LINE-1 RNA and ORF1 protein expression in the mouse hippocampus (but not elsewhere) and the second (PMID: 37910626) shows full-length LINE-1 RNA expression and H3K4me3-ChIP data in the frontal and temporal lobe of the human brain, but not protein expression.

Strengths:

Several parts of this manuscript appear to be well done and include the necessary controls. In particular, the evidence for steady-state expression of ORF1p in the mouse brain appears robust.

Weaknesses:

Several parts of the manuscript appear to be more preliminary and need further experiments to validate their claims. In particular, the data suggesting expression of L1 ORF1p in the human brain and the data suggesting increased expression in the aged brain need further validation. Detailed comments:

(1) The expression of ORF1p in the human brain shown in Figure 1j is not convincing. Why are there two strong bands in the WB? How can the authors be sure that this signal represents ORF1p expression and not nonspecific labelling? Additional validations and controls are needed to verify the specificity of this signal.

We have validated the antibody against human ORF1p (Abcam 245249-> https://www.abcam.com/enus/products/primary-antibodies/line-1-orf1p-antibody-epr22227-6-ab245249), which we use for Western blotting experiments (please see Fig1J and new Suppl Fig.2A,B and C), by several means.

(1) We have done immunoprecipitations and co-immunoprecipitations followed by quantitative mass spectrometry (LC-MS/MS; data not shown as they are part of a different study). We efficiently detect ORF1p in IPs (Western blot now added in Suppl Fig2B) and by quantitative mass spectrometry (5 independent samples per IP-ORF1p and IP-IgG: ORF1p/IgG ratio: 40.86; adj p-value 8.7e-07; human neurons in culture; data not shown as they are part of a different study). We also did co-IPs followed by Western blot using two different antibodies, either the Millipore clone 4H1 (https://www.merckmillipore.com/CH/en/product/Anti-LINE-1-ORF1p-Antibody-clone-4H1,MM_NF-MABC1152?ReferrerURL=https%3A%2F%2Fwww.google.com%2F) or the Abcam antibody to immunoprecipitate and the Abcam antibody for Western blotting on human brain samples. Indeed, the Millipore antibody does not work well on Western Blots in our hands. We consistently revealed a double band indicating that both bands are ORF1p-derived. We have added an ORF1p IP-Western blot as Suppl Fig. 2B which clearly shows the immunoprecipitation of both bands by the Abcam antibody. Abcam also reports a double band, and they suspect that the lower band is a truncated form (see the link to their website above). ORF1p Western blots done by other labs with different antibodies have detected a second band in human samples

• Sato, S. et al. LINE-1 ORF1p as a candidate biomarker in high grade serous ovarian carcinoma. Sci Rep 13, 1537 (2023) in Figure 1D

• McKerrow, W. et al. LINE-1 expression in cancer correlates with p53 mutation, copy number alteration, and S phase checkpoint. Proc. Natl. Acad. Sci. U.S.A. 119, e2115999119 (2022)) showing a Western blot of an inducible LINE-1 (ORFeus) detected by the MABC1152 ORF1p antibody from Millipore Sigma in Figure 7 - Walter et al. eLife 2016;5:e11418. (DOI: 10.7554/eLife.11418) in mouse ES cells with an antibody made inhouse (gift from another lab; in Figure 2B)

The lower band might thus be a truncated form of ORF1p or a degradation product which appears to be shared by mouse and human ORF1p. We have now mentioned this in the revised version of the paper (lines 183-189).

(2) We have used the very well characterized antibody from Millipore ((https://www.merckmillipore.com/CH/en/product/Anti-LINE-1-ORF1p-Antibody-clone-4H1,MM_NFMABC1152?ReferrerURL=https%3A%2F%2Fwww.google.com%2F)) for immunostainings and detect ORF1p staining in human neurons in the very same brain regions (Fig 2H, new Suppl Fig. 2E) including the cerebellum in the human brain. We added a 2nd antibody-only control (Suppl Fig. 2E).

(3) We also did antibody validation by siRNA knock-down. However, it is important to note, that these experiments were done in LUHMES cells, a neuronal cell line which we differentiated into human dopaminergic neurons. In these cells, we only occasionally detect a double band on Western blots, but mostly only reveal the upper band at ≈ 40kD. The results of the knockdown are now added as Suppl Fig. 2C.

Altogether, based on our experimental validations and evidence from the literature, we are very confident that it is indeed ORF1p that we detect on the blots and by immmunostainings in the human brain.

(2) The data shown in Figure 2g are not convincing. How can the authors be sure that this signal controls are needed to verify the specificity of this signal. represents ORF1p expression and not non-specific labelling? Extensive additional validations and

In line 117-123 of the manuscript, we had specified “Importantly, the specificity of the ORF1p antibody, a widely used, commercially available antibody [18,34–38], was confirmed by blocking the ORF1p antibody with purified mouse ORF1p protein resulting in the complete absence of immunofluorescence staining (Suppl Fig. 1A), by using an inhouse antibody against mouse ORF1p[17] which colocalized with the anti-ORF1p antibody used (Suppl Fig. 1B, quantified in Suppl Fig. 1C), and by immunoprecipitation and mass spectrometry used in this study (see Author response image 1)”.

Figure 2G shows a Western blot using an extensively used and well characterized ORF1p antibody from abcam (mouse ORF1p, Rabbit Recombinant Monoclonal LINE-1 ORF1p antibody-> (https://www.abcam.com/enus/products/primary-antibodies/line-1-orf1p-antibody-epr21844-108-ab216324; cited in at least 11 publications) after FACS-sorting of neurons (NeuN+) of the mouse brain. We have validated this ORF1p antibody ourselves in IPs (please see Fig 6A) and co-IP followed by mass spectrometry (LC/MS-MS; see Fig 6, where we detect ORF1p exclusively in the 5 independent ORF1p-IP samples and not at all in 5 independent IgG-IP control samples, please also see Suppl Table 2). In this analysis, we detect ORF1p with a ratio and log2fold of ∞ , indicating that this proteins only found in IP-ORF1p samples (5/5) and not in the IP-control samples ((not allowing for the calculation of a ratio with p-value), please see Suppl Table 2)

Author response image 1.

In addition, we have added new data showing the entire membrane of the Western blot in Fig1H (now Suppl Fig.1E) and a knock-down experiment using siRNA against ORF1p or control siRNA in mouse dopaminergic neurons in culture (MN9D; new Suppl Fig.1D). This together makes us very confident that we are looking at a specific ORF1p signal. The band in Figure 2G is at the same height as the input and there are no other bands visible (except the heavy chain of the NeuN antibody, which at the same time is a control for the sorting). We added some explanatory text to the revised version of the manuscript in lines 120-124 and lines 253-256).

Please note that in the IP of ORF1p shown in Fig6A, there is a double band as well, strongly suggesting that the lower band might be a truncated or processed form of ORF1p. As stated above, this double band has been detected in other studies (Walter et al. eLife 2016;5:e11418. DOI: 10.7554/eLife.11418) in mouse ES cells using an in-house generated antibody against mouse ORF1p. Thus, with either commercial or in-house generated antibodies in some mouse and human samples, there is a double band corresponding to full-length ORF1p and a truncated or processed version of it.

We noticed that we have not added the references of the primary antibodies used in Western blot experiments in the manuscript, which was now corrected in the revised version.

(3) The data showing a reduction in ORF1p expression in the aged mouse brain is confusing and maybe even misleading. Although there is an increase in the intensity of the ORF1p signal in ORF1p+ cells, the data clearly shows that fewer cells express ORF1p in the aged brain. If these changes indicate an overall loss or gain of ORF1p, expression in the aged brain is not resolved. Thus, conclusions should be more carefully phrased in this section. It is important to show the quantification of NeuN+ and NeuN- cells in young vs aged (not only the proportions as shown in Figure 3b) to determine if the difference in the number of ORF1p+ cells is due to loss of neurons or perhaps a sampling issue. More so, it would be essential to perform WB and/or proteomics experiments to complement the IHC data for the aged mouse samples.

We thank the reviewer for this comment and we agree that the representation has been confusing, which is why we added data to Suppl Fig.5 (F-K) using a different representation. As suggested by the reviewer, in new Suppl Fig. 5F-K, we now show the number of ORF1p+, NeuN+ or NeuN- cells per mm2. These graphs indicate that the number per mm2 of ORF1p+ cells overall do not decrease significantly (with the dorsal striatum as an exception, but possibly due to technical limitations which we now discuss in the results section, line 332-335). Globally, there is thus no loss of ORF1p+ expressing cells. There is also no global nor region-specific decrease in the number of neuronal cells (NeuN+ per mm2) although proportions change (Suppl Fig 2E, confocal acquisitions), thus most likely due to a gain of non-neuronal cells in this region. Concerning Western blots on mouse brain tissues from young and aged individuals, we unfortunately ran into limits regarding tissue availability of aged mice.

(4) The transcriptomic data presented in Figure 4 and Figure 5 are not convincing. Quantification of transposon expression on short read sequencing has important limitations. Longer reads and complementary approaches are needed to study the expression of evolutionarily young L1s (see PMID: 38773348 & PMID: 37910626 for examples of the current state of the art). Given the read length and the unstranded sequencing approach, I would at least ask the authors to add genome browser tracks of the upregulated loci so that we can properly assess the clarity of the results. I would also suggest adding the mappability profile of the elements in question. In addition, since this manuscript focuses on ORF1p, it would be essential to document changes in protein levels (and not just transcripts) in the ageing human brain.

We agree that there are limitations to the analysis of TEs with short read sequencing and we have added more text on this aspect in the revised version (results section) and highlighted the problem of limited and disequilibrated sample size in the discussion (line 638-644). The approaches shown in PMID: 38773348 & PMID: 37910626 or even a combination of them, would be ideal of course. However, here we re-analyzed a unique preexisting dataset (Dong et al, Nature Neuroscience, 2018; http://dx.doi.org/10.1038/s41593-018-0223-0), which contains RNA-seq data of human post-mortem dopaminergic neurons in a relatively high number of brain-healthy individuals of a wide age range including some “young” individuals which is rare in post-mortem studies. Such data is unfortunately not available with long read sequencing or any other more appropriate approach yet. Limitations are evident, but all limitations will apply equally to both groups of individuals that we compare. The general mappability profile of the full-length LINE-1 “UIDs” was shown in old Suppl Fig 6A. We have colorhighlighted now in new Suppl Fig 8C the specific elements in this graph. Most importantly, we have now used, as a condensate of suggestions by all reviewers, a combination of mappability score, post-hoc power calculation, visualization and correlation with adjacent gene expression in order to retain a specific locus with confidence or not. Using these criteria, we retained UID-68 (Fig 5D) which has a relatively high mappability score (Suppl Fig.8C) plus an overlap of umap 50 mappability peaks and read mapping when visualizing the locus in IGV (new Fig. 5E), very high post-hoc power (96.6%; continuous endpoint, two independent samples, alpha 0.05) and no correlation with adjacent gene expression per individual (Fig. 5F, G). Based on these criteria, we had to exclude UID-129, UID-37, UID-127 and UID-137, reinforcing the notion that a combination of quality control criteria might be crucial to retain a specific locus with confidence. This is now mentioned in the manuscript in the discussion in line 427430).

We will not be able to document changes in protein levels in aged human dopaminergic neurons as we do not have access to this material. We have tried to obtain human substantia nigra tissues but were not able to get sufficient amounts to do laser-capture microdissection or FACS analyses, especially of young individuals. There are still important limitations to tissue availability, especially of young individuals, and even more so of specific regions of interest like the substantia nigra pars compacta affected in Parkinson disease.

(5) More information is needed on RNAseq of microdissections of dopaminergic neurons from 'healthy' postmortem samples of different ages. No further information on these samples is provided. I would suggest adding a table with the clinical information of these samples (especially age, sex, and cause of death). The authors should also discuss whether this experiment has sufficient power. The human ageing cohort seems very small to me.

This is a re-analysis of a published dataset (Dong et al, Nat Neurosci, 2018; doi:10.1038/s41593-018-0223-0), available through dbgap (phs001556.v1.p1). In this original article, the criteria for inclusion as a brain-healthy control were as follows:

“…Subjects… were without clinicopathological diagnosis of a neurodegenerative disease meeting the following stringent inclusion and exclusion criteria. Inclusion criteria: (i) absence of clinical or neuropathological diagnosis of a neurodegenerative disease, for example, PD according to the UKPDBB criteria[47], Alzheimer’s disease according to NIA-Reagan criteria[48], or dementia with Lewy bodies by revised consensus criteria[49]; for the purpose of this analysis incidental Lewy body cases (not meeting clinicopathological diagnostic criteria for PD or other neurodegenerative disease) were accepted for inclusion; (ii) PMI ≤ 48 h; (iii) RIN[50] ≥ 6.0 by Agilent Bioanalyzer (good RNA integrity); and (iv) visible ribosomal peaks on the electropherogram. Exclusion criteria were: (i) a primary intracerebral event as the cause of death; (2) brain tumor (except incidental meningiomas); (3) systemic disorders likely to cause chronic brain damage.”

We do not have access to the cause of death, but we have added available metadata as Suppl_Table 5 to the manuscript.

We have performed a post-hoc power analysis (using the “Post-hoc Power Calculator” https://clincalc.com/stats/Power.aspx, which evaluates the statistical power of an existing study and added the results to the revision. Due to this analysis, we have indeed taken out Suppl Fig 7 as a whole which had shown data of three full-length LINE-1 loci (UID-37, UID-127 and UID-137) with low power (between 17-66% power). The locus shown in Fig. 5D of the UID-68) had a post-hoc power score of 96.6% which increases our confidence in this full-length LINE-1 element being upregulated in aged dopaminergic neurons. UID-129 had a post-hoc power score of 97%. However, visualization and mappability analysis of the UID-129 locus led us to exclude this UID.

The post-hoc power analysis for L1HS and L1PA2 revealed a low power (28.4% and 32.8% respectively). We have added these results to the manuscript (line 359-362), but decided to keep the data in as this will hopefully be a motivation for future confirmation studies knowing that the availability of similar data from brain-healthy human dopaminergic neurons especially of young individuals will be low.

(6) The findings in this manuscript apply to both human and mouse brains. However, the landscape of the evolutionarily young L1 subfamilies between these two species is very different and should be part of the discussion. For example, the regulatory sequences that drive L1 expression are quite different in human and mouse L1s. This should be discussed.

Indeed, they are different. We have added a paragraph to the discussion (lines 539-548).

(7) On page 3 the authors write: "generally accepted that TE activation can be both, a cause and consequence of aging". This statement does not reflect the current state of the field. On the contrary, this is still an area of extensive investigation and many of the findings supporting this hypothesis need to be confirmed in independent studies. This statement should be revised to reflect this reality.

We agree, this is overstated, we have changed this sentence accordingly to:

“It is now, 31 years after the initial proposition of the “transposon theory of aging” by Driver and McKechnie [14], still a matter of debate whether TE activation can be both, a cause and a consequence of aging [15,16].”

Reviewer #2 (Public Review):

Summary:

Bonnifet et al. sought to characterize the expression pattern of L1 ORF1p expression across the entire mouse brain, in young and aged animals, and to corroborate their characterization with Western blotting for L1 ORF1p and L1 RNA expression data from human samples. They also queried L1 ORF1p interacting partners in the mouse brain by IP-MS.

Strengths:

A major strength of the study is the use of two approaches: a deep-learning detection method to distinguish neuronal vs. non-neuronal cells and ORF1p+ cells vs. ORF1p- cells across large-scale images encompassing multiple brain regions mapped by comparison to the Allen Brain Atlas, and confocal imaging to give higher resolution on specific brain regions. These results are also corroborated by Western blotting on six mouse brain regions. Extension of their analysis to post-mortem human samples, to the extent possible, is another strength of the paper. The identification of novel ORF1p interactors in the brain is also a strength in that it provides a novel dataset for future studies.

Thank you for highlighting the strength of our study.

Weaknesses:

The main weakness of the study is that cell type specificity of ORF1p expression was not examined beyond neuron (NeuN+) vs non-neuron (NeuN-). Indeed, a recent study (Bodea et al. 2024, Nature Neuroscience) found that ORF1p expression is characteristic of parvalbumin-positive interneurons, and it would be very interesting to query whether other neuronal subtypes in different brain regions are distinguished by ORF1p expression.

We agree that this point is important to address. We have mentioned in the manuscript our previous work, which showed that in the mouse ventral midbrain, dopaminergic neurons (TH+/NeuN+) express ORF1p and that these neurons express higher levels of ORF1p than adjacent non-dopaminergic neurons (TH-/NeuN+; Blaudin de Thé et al, EMBO J, 2018). Others have shown evidence of full-length L1 RNA expression in both excitatory and inhibitory neurons but much less expression in non-neuronal cells (Garza et al, SciAdv, 2023). Further, ORF1p expression was documented in excitatory (CamKIIa-positive) and CamKIIa-negative neurons in the mouse frontal cortex (Zhang et al, Cell Res, 2022, doi.org/10.1038/s41422-022-00719-6). We do detect ORF1p staining in mouse (Fig. 1B, panel 10) and human Purkinje cells (based on morphology and in accordance with data from Takahashi et al, Neuron, 2022; DOI: 10.1016/j.neuron.2022.08.011) and most probably basket cells (based on anatomical location in the molecular layer near Purkinje cells) of the cerebellum (Suppl Fig.4). Some Purkinje cells express PV in mice (https://doi.org/10.1016/j.mcn.2021.103650 and 10.1523/JNEUROSCI.22-1607055.2002), as do stellate and basket cells of the molecular layer (10.1523/JNEUROSCI.22-16-07055.2002). While ORF1p is expressed in PV cells of the hippocampus (Bodea et al, Nat Neurosci, 2024) and in the human and mouse cerebellum in PV-expressing neurons, it does not seem as if ORF1p expression is restricted to PV cells overall. To adress this question experimentally, we have now performed ORF1p stainings in different brain regions (hippocampus, cortex, hindbrain, thalamus, ventral midbrain and cerebellum) together with parvalbumin (PV) stainings and in some cases including the lectin WFA (Wisteria floribunda agglutinin, which specifically stains glycoproteins surrounding PV+ neurons). We have added this data to the manuscript as Suppl Fig.4. While PV-positive neurons often co-stain with ORF1p, not all ORF1p positive cells are PV-positive. We have also deepened the discussion of this aspect in the revised manuscript (line 579-599).

The data suggesting that ORF1p expression is increased in aged mouse brains is intriguing, although it seems to be based upon modestly (up to 27%, dependent on brain region) higher intensity of ORF1p staining rather than a higher proportion of ORF1+ neurons. Indeed, the proportion of NeuN+/Orf1p+ cells actually decreased in aged animals. It is difficult to interpret the significance and validity of the increase in intensity, as Hoechst staining of DNA, rather than immunostaining for a protein known to be stably expressed in young and aged neurons, was used as a control for staining intensity.

We have now separated the analysis of NeuN+, ORF1p+ and NeuN- cells (please see new Suppl Fig5F-K) which highlights the fact that there is indeed no change in the number of ORF1p+ cells in the young compared to the aged mouse brain. However, while neuronal cell numbers throughout the brain do not change significantly (new Suppl Fig.5F), while cell proportions in the ventral midbrain (confocal microscopy based quantifications) change, possibly due to a combination of a slight loss in neurons and a gain in non-neuronal cell numbers (Suppl Fig3E). Please also keep in mind that the ventral midbrain region on images taken on a confocal microscope are a much smaller region than the midbrain motor region as specified by ABBA on images taken by the slide scanner. A different marker than DNA as a control requires the use of a protein that is stably expressed throughout the brain and throughout age. We are not aware of a protein for which this has been established. To nevertheless try to address this issue, we used whole-brain imaging intensity data for the protein Rbfox3 (NeuN) which we originally used as a marker for cell identity. We have now added the quantifications of the protein Rbfox3 (NeuN) to Fig3 (new Fig3B). As shown in this figure, NeuN intensity is not stable from one individual to another, neither in control mice nor in the aged control group. Most importantly, NeuN staining intensity does not increase in aged mice. As we did not use NeuN intensity but presence or absence of NeuN as a marker for cell identity, the instability of NeuN intensity from one individual mouse to another does not have an influence on the data presented in this manuscript. It does indicate however, that the overall increase of ORF1p in aged mice is not a mere reflection of a general decrease in protein turnover. As stated above, the DNA staining with Hoechst controls for technical artefacts. Using Hoechst and NeuN as control, we have thus provided evidence for the fact that the increase in ORF1p intensity per cell is indeed specific for ORF1p. This is now added to the results section (line 299-301).

The main weakness of the IP-MS portion of the study is that none of the interactors were individually validated or subjected to follow-up analyses. The list of interactors was compared to previously published datasets, but not to ORF1p interactors in any other mouse tissue.

As stated in the manuscript, the list of previously published datasets does include a mouse dataset with ORF1p interacting proteins in mouse spermatocytes (please see line 479-480: “ORF1p interactors found in mouse spermatocytes were also present in our analysis including CNOT10, CNOT11, PRKRA and FXR2 among others (Suppl_Table4).”) -> De Luca, C., Gupta, A. & Bortvin, A. Retrotransposon LINE-1 bodies in the cytoplasm of piRNA-deficient mouse spermatocytes: Ribonucleoproteins overcoming the integrated stress response. PLoS Genet 19, e1010797 (2023)). We indeed did not validate any interactors for several reasons (economic reasons and time constraints (post-doc leaving)). However, we feel that the significant overlap with previously published interactors highlights the validity of our data and we anticipate that this list of ORF1p protein interactors in the mouse brain will be of further use for the community.

The authors achieved the goals of broadly characterizing ORF1p expression across different regions of the mouse brain, and identifying putative ORF1p interactors in the mouse brain. However, findings from both parts of the study are somewhat superficial in depth.

This provides a useful dataset to the field, which likely will be used to justify and support numerous future studies into L1 activity in the aging mammalian brain and in neurodegenerative disease. Similarly, the list of ORF1p interacting proteins in the brain will likely be taken up and studied in greater depth.

Reviewer #3 (Public Review):

The question about whether L1 exhibits normal/homeostatic expression in the brain (and in general) is interesting and important. L1 is thought to be repressed in most somatic cells (with the exception of some stem/progenitor compartments). However, to our knowledge, this has not been authoritatively / systematically examined and the literature is still developing with respect to this topic. The full gamut of biological and pathobiological roles of L1 remains to be shown and elucidated and this area has garnered rapidly increasing interest, year-by-year. With respect to the brain, L1 (and repeat sequences in general) have been linked with neurodegeneration, and this is thought to be an aging-related consequence or contributor (or both) of inflammation. This study provides an impressive and apparently comprehensive imaging analysis of differential L1 ORF1p expression in mouse brain (with some supporting analysis of the human brain), compatible with a narrative of non-pathological expression of retrotransposition-competent L1 sequences. We believe this will encourage and support further research into the functional roles of L1 in normal brain function and how this may give way to pathological consequences in concert with aging. However, we have concerns with conclusions drawn, in some cases regardless of the lack of statistical support from the data. We note a lack of clarity about how the 3rd party pre-trained machine learning models perform on the authors' imaging data (validation/monitoring tests are not reported), as well as issues (among others) with the particular implementation of co-immunoprecipitation (ORF1p is not among the highly enriched proteins and apparently does not reach statistical significance for the comparison) - neither of which may be sufficiently rigorous.

Thank you for your comments on our manuscript.

We have addressed the concerns about the machine learning paradigm (see Author response image 1). Concerning the co-IP-MS, we can confirm that ORF1p is among the highly enriched proteins as it was not found in the IgG control (in 5 independent samples), only in the ORF1p-IP (in 5 out of 5 independent samples). This is what the infinite sign in Suppl Table 2 indicates and this is why there is no p-value assigned as infinite/0 doesn’t allow to calculate a pvalue. We have made this clearer in the revised version of the manuscript and added a legend to Suppl Table 2.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I would recommend the authors remove the human data and expand the analysis of the aged mice. This would most likely result in a much stronger manuscript.

We do think that the imaging data and the Western blots are convincing (please also see our detailed response above to the criticism concerning the antibody we used and the newly added data) and very much reflects what we find in the mouse brain, i.e. concerning the percentage of neurons expressing ORF1p and the percentage of ORF1p+ cells being neuronal. When it comes to the transcriptomic data on aged dopaminergic neurons, we have further discussed the limitations of this study in the revised manuscript and hope that the findings inspire others in the field to redo these types of analyses using the now state-of-the-art NGS technologies to address the question and validate what we have found.

Reviewer #2 (Recommendations For The Authors):

The characterization of ORF1p expression across the mouse brain would be vastly more informative if cell identity was established beyond NeuN+/NeuN---the neuronal predominance of L1 activity in the brain has long been observed. Indeed, even corroboration of the PV+ interneuron signature previously reported would both lend credence to the present study and provide valuable confirmation to the field.

We agree. Please see our response above as well as the new experimental data we added (Suppl Fig5.F-K).

The increased intensity (but not prevalence in terms of % of Orf1p positive cells) of Orf1p expression in aged mouse brains would be more convincing with further context and perhaps better controls. Is overall protein turnover in aged neurons simply slower than in neurons from younger brains? Immunostaining with another protein marker, rather than Hoescht staining of DNA, to demonstrate that increased staining intensity is unique to Orf1p, would make this result more compelling.

To address this question, we have now added the quantifications of the protein Rbfox3 (NeuN) to Fig3 (Fig. 3B). As shown in this figure, NeuN intensity is not stable from one individual to another, neither in control mice nor in the aged control group. As we did not use NeuN intensity but presence or absence of NeuN as a marker for cell identity, this does not have any influence on the data presented in this manuscript. It does indicate however, that the overall increase of ORF1p in aged mice is not a mere reflection of a general decrease in protein turnover. As stated above, the DNA staining with Hoechst controls for technical artefacts. Using Hoechst and NeuN as control, we have thus provided evidence for the fact that the increase in ORF1p intensity per cell is indeed specific for ORF1p.

Western blotting on cell lysates from aged vs young NeunN+ sorted cells would also strengthen this conclusion, although I appreciate the technical challenge of physically isolating whole mature neuronal cells.

Indeed, this would be feasible but only after FACS sorting, which is technically challenging on whole brain cells (less so on nuclei). We unfortunately do not have the possibility to embark on this right now.

Concerning data presentation, Figure 3A would be much more informative if the graph was broken down to show the proportion of ORF1p+ and ORF1p- cells, regardless of NeuN status, and the proportion of NeuN+ and NeuN- cells shown independently of Orf1p status. It is difficult to ascertain the relationship of either of these variables to age, as the graph is presented now.

We followed the suggestions of the reviewer agreeing that breaking down this figure into either ORF1p+ or NeuN+ or NeuN- cells without double attribution is easier to interpret. However, we also chose to use cell densities (cell numbers/ per mm2) to represent the data (new Suppl Fig.5F-K) which is even more precise while proportions are now shown in Suppl Fig.3A-E. Indeed, while it is important to realize that the variables ORF1p+/- or NeuN+/- are not completely independent of each other (as shown in proportions of old Fig4A and B, new Suppl Fig3A and B) as they form four categories (NeuN+/ORF1p+; NeuN+/ORF1p-. NeuN-/ORF1p+, NeuN-/ORF1p-), we can see from the data that there is no overall change in neuron number in the mouse brain between 3 month and 16 months of age. There isn’t an overall change of the density of ORF1p+ cells nor NeuN- cells in the mouse brain with the exception of a decrease in cell density of ORF1p-positive cells in the dorsal striatum accompanied by an increase in non-neuronal cell density (but as discussed above and in the manuscript (line 332-337), this might be due to technical limitations). Thus, while ORF1p intensities per cell increase significantly in older mice, here is no significant change in ORF1p+ cell number.

Reviewer #3 (Recommendations For The Authors):

(1) According to the description in Materials and Methods on the analysis of the confocal images (lines 731-743) the authors used Cell-Pose for both the nuclei and cell segmentation tasks, using model=cyto and diameter=30 for the first (nuclei) and model=cyto2 and diameter=40 for the second (cell). Description of analysis of sagittal brain regions (lines 746-764) indicates the pre-trained model DSB2018 from StarDist 2D was used for nuclei detection, and Cell-Pose using model cyto2 and diameter=30 for cell segmentation. Detected nuclei were then matched to segmented cell areas based on overlap criteria and each nucleus was labeled as 'positive' or 'negative' for either OFR1P or NEU-N.

As described in its three publications (1, 2, 3), Cell-Pose as a segmentation tool is trained in different datasets, with cyto2 being trained on a more varied dataset than cyto. In their library they also offer a model specific for nuclei2. Some description and explanation on the reasons two different models were used for nuclei detection and not choosing the offered specific pre-trained model by Cell-Pose in either case.

According to the cellpose library documentation "Changing the diameter will change the results that the algorithm outputs. When the diameter is set smaller than the true size then cellpose may over-split cells. Similarly, if the diameter is set too big then cellpose may over-merge cells.". It would be useful to offer the justification of the pixels chosen for the analysis (possibly average pixel counts in a subsample of Hoechst images).

Answers to questions 1-5:

Regarding ABBA, slices were first positioned and oriented manually along the Z-axis, without using DeepSlice. Automated affine registration was then applied in the XY plane, followed by manual refinement. 1 slice per mouse brain, 4 mouse brains per condition.

Regarding the gradient heatmap, as stated in the figure legend of Fig3F; Represented is the fold-change in percent (aged vs young) of the “mean of the mean” ORF1p expression per ORF1p+ cell quantified mapped onto the nine different regions analyzed. More precisely, the heatmap shows the percentage increase in the mean of all mean cell intensities in the aged condition, normalized to the mean of all mean cell intensities in the young condition. The pre-trained models and hyperparameters were selected based on their optimal performance across our image datasets. For slide scanner images, the StarDist DSB 2018 model was chosen over a Cellpose model because it more effectively avoided detecting out-of-focus nuclei, which were common in slide scanner images due to the lack of optical sectioning. This issue was not present in confocal images, where Cellpose cyto model was used instead. To assess the performance of each model and diameter setting, we computed the average precision (AP) metric, which is defined as AP = TP/(TP+FP+FN), where TP = true positives, FP = false positives, and FN = false negatives. The AP was calculated at the commonly used Intersection over Union (IoU) threshold of 0.5. For confocal images, Cellpose models and hyperparameters were evaluated on eight images per channel, capturing intensity variability across different mouse ages and brain regions. A total of approximately 2,000 nuclei and 1,000 NeuN and ORF1p cells were manually annotated. The AP values at an IoU threshold of 0.5 were: 0.995 for nuclei, 0.960 for NeuN, and 0.974 for ORF1p cells. These high AP values confirm that the selected models and diameter settings were well-suited for analyzing the entire dataset. For slide scanner images, nuclei and cell detection were evaluated on 14 images per channel, with approximately 800 nuclei and 400 NeuN and ORF1p cells manually annotated. The AP values were lower compared to confocal images, mainly due to a lower signal-to-noise ratio, which led to an increased number of false positives and false negatives: 0.806 for nuclei, 0.675 for NeuN, and 0.695 for ORF1p cells. This decline in performance was expected given the challenges posed by slide scanner images, including background noise and out-of-focus objects. Notably, the observed false positives primarily correspond to small-sized nuclei/cells or those with low intensity, which evade the stringent filters that were applied. While fine-tuning the models could further enhance detection robustness, we considered that the selected models and diameter settings were suitable for processing the entire dataset.

We added a paragraph to the materials & methods section with this new information; for confocal images (line 847-855), slide scanner images (line 878-885).

Author response table 1.

(2) Next to no information is offered regarding the brain segment registration and how the results were analyzed: The ABBA plug-in has two modules manual and automatic, via a DL pre-trained model called DeepSlice. The authors should report which mode of ABBA they used, how many slices per mouse brain, and how many brains. Moreover, there is no explanation of how the gradient heatmap of the brain regions (Figure 3G) was calculated.

Please see above

(3) Even the best algorithms produce some False predictions. In this application of the (3rd party) cellpose, StarDist, and ABBA pre-trained models, such cases of wrong predictions would have amplified downstream effects on the analysis e.g., wrongly characterizing certain cells as 'negative' (falsely not detected cell, falsely detected nucleus), or worse, biasing against certain cell subgroups (falsely not detected 'type' of nuclei). This is even more troubling with the variety of models used for the nuclei segmentation task, and the parameters in each. It is possible the authors performed optimizations and reported exactly such optimized values for their dataset, they should however still explicitly offer these detailed validation and optimization processes. The low statistical significance throughout the quantified results from these IF experiments (Figures 1-3) is also a cause for needing an explicit description of how these algorithms perform on the authors' data.

It is good practice that a pre-trained model when applied to a new dataset like the one that the authors produced for this work, would require basic monitoring for how it performs in the new, previously unseen dataset, even when the model's generalizability has been reported previously as great. It would be best if the authors had handannotated a few images as the validation set and produced some model performance metrics as a supplemental table for all pre-trained models they used, in the datasets they used them at. Alternatively, the authors are offered the ability by the cellpose team to fine-tune the model for their data, and this could be used to perform the experiments for this work instead if the performance metrics of the used cellpose (cyto and cyto2) models prove to be poor.

Please see above

(4) The legend for Figure 1A indicates that Cell-Pose was used for cell detection and StarDist for nuclei detection in the confocal images (line 960). This needs clarification and correction.

Please see above

(5) Some explanation of why the models used were changed when using confocal or the slide scanner microscope would be nice.

Please see above

(6) The legend title of Figure 3 (line 1040) "Fig. 3: ORF1p expression is increased throughout the whole mouse brain in the context of aging" is misleading as half the panels in the figure demonstrate a decrease in ORF1pexpressing cells. The two can be both true, but in a more nuanced relationship. A more modest representation of the data in the title is also warranted by the unimpressive statistical significance achieved (notably with no correction for multiple testing, which would further inflate them).

We have toned down the tile of Fig. 3 to “ORF1p expression is increased in some regions of the aged mouse brain” while leaving its meaning as globally. There is indeed no significant loss of ORF1p expressing cells (Suppl Fig. 5F; except in the dorsal striatum (Supl Fig. 5I, please see also discussion above), but there is a significant increase in ORF1p intensity per cell overall (Fig. 3A,C,F) and in several regions of the mouse brain (Fig E, G and H).

(7) Figure 4 suffers for significance. For example in panel A, the few genes with the highest -log10P value, ie above 1.3 (p-value of ~0.05) have a log2-fold change of 0.2-0.3 (fold change 1.14-1.23). There are no hits with even the modest log2-fold change of 0.5 (fold-change 1.4). The big imbalance between young/old samples for these RNA seq experiments (6 vs 36 mice) could be an issue here too.

The reviewer refers to mouse samples (“6 to 36 mice”), but this is data of human post-mortem dopaminergic neurons from brain-healthy individuals which were laser-captured and sequenced as reported by Dong et al, Nat Neurosci, 2018. There is indeed a big imbalance between young and old samples which are linked to the difficulties in availability of brain-healthy post-mortem tissues from young individuals which are obviously much rarer than from older people. We agree that the fold-enrichment are modest and p-values rather high, but we argue to keep this data in as it is based on rare post-mortem human brain tissues which were difficult to obtain and will be very difficult to obtain in sufficient number in future studies. We hope however, that these results will encourage such studies in the future and motivate researchers to further look into the expression of TEs in aging brain tissues with higher sample sizes and more suitable sequencing techniques. We have now in the revised version toned down some sentences (i.e. line 359: modest, but significant increase in several young…) and have now also added a post-hoc power analysis (results section line 359-362: “There was a modest but significant increase in several younger LINE-1 elements including L1HS and L1PA2 at the “name” level (Fig. 4A, B), an analysis which was however underpowered (post-hoc power calculation; L1HS: 28.4%; L1PA2: 32.8%) and thus awaits further confirmation in independent studies.”)

(8) Figure legend 4C (line 1088) should offer more explanation on what is compared for these correlations: the young vs old results, all intensities of all experiments, and intensities separately for each sample.

We have added the missing information to Figure legend 4C (line 1209-1215): “Correlation of the RNA expression levels of LINE-1 elements with known transposable element regulators in human dopaminergic neurons (all ages included). What was compared are the expression levels of LINE-1 elements with known regulators of TEs for each individual sample, all ages included.”

(9) Figure 5, panel D. The regressions are all driven by 1-2 outliers. Should be removed as they don't add anything.

We agree and therefore have performed an outlier test (ROUT (Q=1%) and identified outliers (1 in each graph) have been taken out from the analysis. We argue that the information of a non-correlation of UID-68 and adjacent gene expression is important as it rules out a dependency of expression of the full-length LINE-1 depending on neighboring gene expression (see new Fig5E-G).

(10) Figure 6 panel B. It is unexpected that the GO terms with the highest enrichment also show weak significance and vice-versa. Fold enrichment in the PANTHER tool is defined as the % of GO-term genes in the sample divided by the %GO-term genes in the background (organism).

This is not unexpected as GO terms contain different numbers of proteins. Indeed, the significance can be different if the GO term contains for example 3 or 300 proteins. A GO term containing only few proteins with a high fold change between the conditions (here: ORF1p-IP vs whole mouse genome) will lead to a rather low significance for example. If you look at the last 6 categories in Fig 6B, you can appreciate that they have very similar values for enrichment but very different significance levels (FDR).

(11) Many citations in the References sections are referred to by doi and "Published online" date. These should be corrected to include the citation in standard format (journal name, volume, issue, pages, etc).

We apologize for this and have corrected this in the revised version.

(12) (line 970) Legend of Figure 1 is missing label referencing panel C (ie (C) Bar plot showing the total....).

Thank you for pointing this out, this has been corrected.

(13) The bottom violin plot in Figure 1C lacks sufficient explanation (what are the M1-4 categories?). The same problem with panel G (same Figure 1).

This has now been better explained. The M1-M4 categories denominate individual mice numbered from 1 to 4 for (results are shown per individual).

-> specified in line 1098-1099 (Fig.1C) and new text (1117-1118: Fig.1G): Four three-month-old Swiss/ OF1 mice (labeled as M1 to M4) are represented each by a different color, the scattered line represents the median. ****p<0.0001, nested one-way ANOVA. Total cells analyzed = 4645

(14) Figure 1B; confocal image 2 (Hippocampus) does not seem to tell the same story as the main slide scanner image. Overall, more explicit phrasing regarding how the Images in Figure 1B are not blow-outs of the bigger one but different, confocal images of the same regions.

We have changed the sentence to: “Representative images acquired on a confocal microscope of immunostainings showing ORF1p expression (orange) in 10 different regions of the mouse brain.”, which hopefully helps to indicate that these images are indeed not blow-outs of the slide scanner image.

(15) Young are defined as 3 months and 'old' as 16 months mice. 16-month group name would be better as "adults". Example of age range considered 'old': "Young (3-6-month-old) and aged (18-27-month-old) male mice were age- and source-matched for each experiment." https://www.cell.com/cell-metabolism/fulltext/S1550-4131(23)00462X?_returnURL=https%3A%2F%2Flinkinghub.elsevier.com%2Fretrieve%2Fpii%2FS15504131230 0462X%3Fshowall%3Dtrue

This is true, but the 16-month age group does not have a designation when looking at Mouse Life history stages in C57Bl/6 mice from the Jackson laboratory (see https://www.jax.org/news-and-insights/jax-blog/2017/november/when-are-mice-considered-old#), they are neither middle-aged nor old. We therefore believe that the designation as “aged” still holds true.

(16) Lines 63-65 > To our understanding, both ORF1 and ORF2 proteins are thought to exhibit cis preference.

Yes, that is true, but the sentence as it is does not make a claim about ORF2p not having cis-preference.

(17) Figure 1I is only referred to as "Figure I". Twice. Page 8, line 173 & 176.

Thank you, has been corrected.

(18) Lines 178-182 >To investigate intra-individual expression patterns of ORF1p in the post-mortem human brain, we analyzed three brain regions of a neurologically healthy individual (Figure 1J) by Western blotting. ORF1p was expressed at different levels in the cingulate gyrus, the frontal cortex, and the cerebellum underscoring a widespread expression of human ORF1p across the human brain." > It is difficult for us to gauge how believable the blots are without knowing the amount of protein loaded.

We have loaded 10ug of tissue lysate per lane (tissue pulverized with a Covaris Cryoprep; amount now mentioned in the materials & methods section). We have added some more information on the antibody in the revised manuscript (line 183-194).

We say this from our experience conducting similar blots of anti-ORF1p IPs from human brain tissues using the same antibody (4H1) without successful detection of enriched protein by western blot (of course there can be many reasons for that, but knowing the amount of protein loaded is important for reproducibility). In addition, we find the "double" ORF1p bands they see in almost every blot atypical.

In our hands, the 4H1 antibody does not work well on Western blots, but it immunoprecipitates well and works very well on immunostainings. However, the abcam AB 245249 works well for Western blotting (and IPs) which is why we used this antibody for these applications, respectively. As described above, there is evidence that the double band is not atypical, but rather frequent, which we now also mention in the revised manuscript line 183191: “To investigate intra-individual expression patterns of ORF1p in the post-mortem human brain, we analyzed three brain regions of a neurologically-healthy individual (Fig. 1J, entire Western blot membrane in Suppl Fig. 2A) by Western blotting using a commercial and well characterized antibody which we further validated by several means. The double band pattern in Western blots has been observed in other studies for human ORF1p outside of the brain (Sato et al, SciRep, 2023, McKerrow et al, PNAS, 2022) as well as for mouse ORF1p (Walter et al, eLife, 2016). We also validated the antibody by immunoprecipitation and siRNA knock-down in human dopaminergic neurons in culture (differentiated LUHMES cells, Suppl Fig. 2B and 2C) where we detect however in most cases the upper band only. The nature of the lower band is unknown, but might be due to truncation, specific proteolysis or degradation. ORF1p was expressed at different levels in the human post-mortem cingulate gyrus, the frontal cortex and the cerebellum underscoring a widespread expression of human ORF1p across the human brain. This was in accordance with ORF1p immunostainings of the human post mortem cingulate gyrus (Fig. 2H and Suppl Fig. 2E) and frontal cortex (Suppl Fig. 2E), with an absence of ORF1p staining when using the secondary antibody only (Suppl Fig. 2E).”

In some images a band is labeled as IgG heavy chain (e.g. presumably from the FACS, Figure 2G, and IP, Figure 6A - which could contain residual antibody) - however, this is avoidable by using a different antibody for capture than detection - which also helps reduce false positive results.

Unfortunately, we have only an antibody raised in rabbit available to perform IPs and Western blots on mouse tissues and therefore cannot avoid the detection of the IgG heavy chain.

Aside from these, there seem to be persistent 'double bands' in the region of ORF1p. Generally, we are unaccustomed to seeing such 'double bands' in human anti-ORF1p western blots and IP-western blots, and since, in this study, this is seen in both mouse and human blots, it raises some doubts. Having the molecular mass ladder on each blot to at least allow for the assessment of migration consistency and would therefore be very helpful.

We have added the molecular weights on the Western blots (Fig.1H, Fig. 2G and Suppl Fig.1D and E). As discussed also above, there is accumulating evidence that in some tissues, there are persistent double bands detected using ORF1p antibodies in both, mouse and human tissues.

Human ORF1p detection:

We have validated the antibody against human ORF1p (Abcam 245249-> https://www.abcam.com/enus/products/primary-antibodies/line-1-orf1p-antibody-epr22227-6-ab245249), which we use for Western blotting experiments (please see Fig1J and new Suppl Fig.2A,B and C), by several means.

(1) We have done immunoprecipitations and co-immunoprecipitations followed by quantitative mass spectrometry (LC-MS/MS; data not shown as they are part of a different study). We efficiently detect ORF1p in IPs (Western blot now added in Suppl Fig2B) and by quantitative mass spectrometry (5 independent samples per IP-ORF1p and IP-IgG: ORF1p/IgG ratio: 40.86; adj p-value 8.7e-07; human neurons in culture; data not shown as they are part of a different study). We also did co-IPs followed by Western blot using two different antibodies, either the Millipore clone 4H1 (https://www.merckmillipore.com/CH/en/product/Anti-LINE-1-ORF1p-Antibody-clone- 4H1,MM_NF-MABC1152?ReferrerURL=https%3A%2F%2Fwww.google.com%2F) or the Abcam antibody to immunoprecipitate and the Abcam antibody for Western blotting on human brain samples. Indeed, the Millipore antibody does not work well on Western Blots in our hands. We consistently revealed a double band indicating that both bands are ORF1p-derived. We have added an ORF1p IP-Western blot as Suppl Fig. 2B which clearly shows the immunoprecipitation of both bands by the Abcam antibody. Abcam also reports a double band, and they suspect that the lower band is a truncated form (see the link to their website above). ORF1p Western blots done by other labs with different antibodies have detected a second band in human samples

• Sato, S. et al. LINE-1 ORF1p as a candidate biomarker in high grade serous ovarian carcinoma. Sci Rep 13, 1537 (2023) in Figure 1D

• McKerrow, W. et al. LINE-1 expression in cancer correlates with p53 mutation, copy number alteration, and S phase checkpoint. Proc. Natl. Acad. Sci. U.S.A. 119, e2115999119 (2022)) showing a Western blot of an inducible LINE-1 (ORFeus) detected by the MABC1152 ORF1p antibody from Millipore Sigma in Figure 7 - Walter et al. eLife 2016;5:e11418. (DOI: 10.7554/eLife.11418) in mouse ES cells with an antibody made inhouse (gift from another lab; in Figure 2B)

The lower band might thus be a truncated form of ORF1p or a degradation product which appears to be shared by mouse and human ORF1p. We have now mentioned this in the revised version of the paper (lines 183-189).

(2) We have used the very well characterized antibody from Millipore ((https://www.merckmillipore.com/CH/en/product/Anti-LINE-1-ORF1p-Antibody-clone-4H1,MM_NF-MABC1152?ReferrerURL=https%3A%2F%2Fwww.google.com%2F)) for immunostainings and detect ORF1p staining in human neurons in the very same brain regions (Fig 2H, new Suppl Fig. 2E) including the cerebellum in the human brain. We added a 2nd antibody-only control (Suppl Fig. 2E).

(3) We also did antibody validation by siRNA knock-down. However, it is important to note, that these experiments were done in LUHMES cells, a neuronal cell line which we differentiated into human dopaminergic neurons. In these cells, we only occasionally detect a double band on Western blots, but mostly only reveal the upper band at ≈ 40kD. The results of the knockdown are now added as Suppl Fig. 2C.

Altogether, based on our experimental validations and evidence from the literature, we are very confident that it is indeed ORF1p that we detect on the blots and by immmunostainings in the human brain.

Mouse ORF1p detection: In line 117-123 of the manuscript, we had specified “Importantly, the specificity of the ORF1p antibody, a widely used, commercially available antibody [18,34–38], was confirmed by blocking the ORF1p antibody with purified mouse ORF1p protein resulting in the complete absence of immunofluorescence staining (Suppl Fig. 1A), by using an inhouse antibody against mouse ORF1p[17] which colocalized with the anti-ORF1p antibody used (Suppl Fig. 1B, quantified in Suppl Fig. 1C), and by immunoprecipitation and mass spectrometry used in this study (see Author response image 1)”.

Figure 2G shows a Western blot using an extensively used and well characterized ORF1p antibody from abcam (mouse ORF1p, Rabbit Recombinant Monoclonal LINE-1 ORF1p antibody-> (https://www.abcam.com/enus/products/primary-antibodies/line-1-orf1p-antibody-epr21844-108-ab216324; cited in at least 11 publications) after FACS-sorting of neurons (NeuN+) of the mouse brain. We have validated this ORF1p antibody ourselves in IPs (please see Fig 6A) and co-IP followed by mass spectrometry (LC/MS-MS; see Fig 6, where we detect ORF1p exclusively in the 5 independent ORF1p-IP samples and not at all in 5 independent IgG-IP control samples, please also see Suppl Table 2). In this analysis, we detect ORF1p with a ratio and log2fold of ∞ , indicating that this proteins only found in IP-ORF1p samples (5/5) and not in the IP-control samples ((not allowing for the calculation of a ratio with p-value), please see Suppl Table 2)

In addition, we have added new data showing the entire membrane of the Western blot in Fig1H (now Suppl Fig.1E) and a knock-down experiment using siRNA against ORF1p or control siRNA in mouse dopaminergic neurons in culture (MN9D; new Suppl Fig.1D). This together makes us very confident that we are looking at a specific ORF1p signal. The band in Figure 2G is at the same height as the input and there are no other bands visible (except the heavy chain of the NeuN antibody, which at the same time is a control for the sorting). We added some explanatory text to the revised version of the manuscript in lines 120-124 and lines 253-256).

Please note that in the IP of ORF1p shown in Fig6A, there is a double band as well, strongly suggesting that the lower band might be a truncated or processed form of ORF1p. As stated above, this double band has been detected in other studies (Walter et al. eLife 2016;5:e11418. DOI: 10.7554/eLife.11418) in mouse ES cells using an in-house generated antibody against mouse ORF1p. Thus, with either commercial or in-house generated antibodies in some mouse and human samples, there is a double band corresponding to full-length ORF1p and a truncated or processed version of it.

We noticed that we have not added the references of the primary antibodies used in Western blot experiments in the manuscript, which was now corrected in the revised version.

(19) Figure 1H, 1J, 6A: Show/indicate molecular weight marker.

The molecular weight markers were added (please see Fig.1H, Fig. 2G and Suppl Fig.1D and E).

(20) Page 10, line 223. " ...expressing ORF1p and ORF1p"?

Thank you, this was corrected.

(21) Lines 279-280 "An increase of ORF1p expression was also observed in three other regions albeit not significant." > This means it is not distinguishable as a change under the assumptions and framework of the analysis; please remove this statement.

We agree, we removed this sentence.

(22) Page 13, line 301. Labeling the group with a mean age of 57.5 as "young" might be a bit misleading.

This is why we put the “young” in quotation marks.

(23) Lines 309-311 "however there was a significant increase in several younger LINE-1 elements including L1HS and L1PA2 at the "name" level (Figure 4A, B)". > Effect size is tiny; is this really viable as biologically significant? Maybe just remove the volcano plot? Does panel A add anything not covered by B?

We would like to keep the Volcano plot, even though effect sizes are small (which we acknowledge in the manuscript line 359-362: “There was a modest but significant increase in several younger LINE-1 elements including L1HS and L1PA2 at the “name” level (Fig. 4A, B), an analysis which was however underpowered (posthoc power calculation; L1HS: 28.4%; L1PA2: 32.8%) and thus awaits further confirmation in independent studies.” The reason for this decision is to illustrate a general increase in expression (even with a small effect size) of several LINE-1 elements at the name level with the youngest LINE-1 elements being amongst those with the highest effect.

(24) Lines 327-328 "The transcripts of these genes showed, although not statistically significant, a trend for decreased expression in the elderly (Supplementary Figure 5D-G). > I do not recommend doing this.

We agree and take it out.

(25) Lines 339-342 "While several tools using expectation maximization algorithms in assigning multi-mapping reads have been developed and successfully tested in simulations 48,54, we used a different approach in mapping unique reads to the L1Base annotation of full-length LINE-1" > Generally, this section is not clear - what is the rationale for the approach (compared to the stated norms)? Ideally, justify this analytical choice and provide a basic comparison to other more standard approaches (even if briefly in a supplement).

We thank the reviewer for his comment. Indeed, randomly assigning multi-mapping reads is usually a good strategy to quantify the expression of repeats at the family level (Teissandier et al. 2019) which we did in the first part of the analysis (class, family and name level). However, our main goal was to focus on specific single fulllength LINE elements which can encode ORF1p. We therefore decided to only use uniquely mapped reads, which is by definition the only way to be sure that a sequencing read really comes from a specific genomic location, and which will to not over-estimate their expression level. In this sense, we have added some explanatory text to this specific section. We also added a section to the discussion (line 638-644): This analysis has technical limitations inherent to transcriptomic analysis of repeat elements especially as it is based on short-read sequences and on a limited and disequilibrated number of individuals in both groups. Nevertheless, we tried to rule out several biases by demonstrating that mappability did not correlate with expression overall and used a combination of visualization, post-hoc power analysis and analysis of the mappability profile of each differentially expressed fulllength LINE-1 locus.

(26) Page 16, line 389. The age span covered is 59 years although the difference in mean age between the two groups is only 25.5 years - please indicate both metrics.

We have added this additional metric in line 432.

(27) Lines 394-397 "Further, correlation analyses suggest that L1HS expression might possibly be controlled by the homeoprotein EN1, a protein specifically expressed in dopaminergic neurons in the ventral midbrain 50, the heterochromatin binding protein HP1, two known regulators of LINE-1, and the DNA repair proteins XRCC5/6." > This reads like a drastic reach unless framed explicitly as a 'tempting speculation' (or similar). I don't think this claim should be made as it is without further validation.

We believe to have used careful language (“correlation analysis suggests”.“might possibly be controlled”) in the results section as well as in the discussion (line 660-671): “Matrix correlation analysis of several known LINE-1 regulators, both positive and negative, revealed possible regulators of young LINE-1 sequences in human dopaminergic neurons. Despite known and most probable cell-type unspecific regulatory factors like the heterochromatin binding protein CBX5/HP1 [51] or the DNA repair proteins XRCC5 and XRCC6 [49], we identified the homeoprotein EN1 as negatively correlated with young LINE-1 elements including L1HS and L1PA2. EN1 is an essential protein for mouse dopaminergic neuronal survival [50] and binds, in its properties as a transcription factor, to the promoter of LINE-1 in mouse dopaminergic neurons [17]. As EN1 is specifically expressed in dopaminergic neurons in the ventral midbrain, our findings suggests that EN1 controls LINE-1 expression in human dopaminergic neurons as well and serves as an example for a neuronal sub-type specific regulation of LINE-1.” To this we added: “Although these proteins are known regulators of LINE-1, this correlative relationship awaits experimental validation.”

(28) Mouse protein/gene names are all capital letters on page 17/18. Changes on page 18/19. This should be consistent.

Thank you, this has been corrected (all capital).

(29) Page 23, line 559. The estimated ORF1p/ORF2p ratio referenced is based on an overexpression of L1 from a plasmid (ref87). > It should be made clear to the reader that it is still unknown whether such a ratio is representative of native conditions.

OK, this is indeed true. Thank you for pointing this out. (line 621-622)

(30) Lines 613-616 "Further, GO term analysis contained expected categories like "P-body", mRNA metabolism related categories, and "ribonucleoprotein granule". We also identified NXF1 as a protein partner of ORF1p, a protein found to interact with LINE-1 RNA related to its nuclear export 89." > There is no reason to speculate that the proteins in the pulldown are specific to L1 RNAs.

We did not speculate that the proteins in the pulldown are specific to LINE-1 RNA. We just mentioned that NXF1 was an ORF1p protein partner and that it had been found previously as a LINE-1 RNA interactor.

ORF1p is present in large heterogeneous assemblies - not every protein should be assigned an L1-related function and many proteins will be participating in general RNA-granule functions (given L1 ORFs are known to accumulate in such structures). Moreover, the granules are not the same in every cell type. IP is done in low salt and overnight incubation (poorly controlled for non-specific accumulation).

We state that these key interactors are “probably” essential for completing or repressing the LINE-1 life cycle. It is true that we cannot affirm this. We therefore added a sentence to the discussion (line 679): “This supports the validity of the list of ORF1p partners identified, although we cannot rule out the possibility that unspecific protein partners might be pulled down due to colocalization in the same subcellular compartment.”

(31) Lines 629-631" These results complete the picture of the post-transcriptional and translational control of ORF1p and suggest that these mechanisms, despite a steady-state expression, are operational in neurons." > Stating that these results complete the picture, which is still very much open for completion (granted, these results add to the picture), is an unneeded over-reach.

We agree. We changed “complete” to “add to “ the picture.

(32) Lines 641-644 "Finally, we found components of RNA polymerase II and the SWI/SNF complex as partners of ORF1p. This further indicates that ORF1p has access to the nucleus in mouse brain neurons as described for other cells 95,96, implying that ORF1p potentially has access to chromatin." > There is no way to know if this is a post-lysis effect - we have no real specificity information. The mock IP control is insufficient for this conclusion without further validation.

We added: “however a bias due to a post-lysis effect cannot be excluded.” Line 711

(33) ab216324 for IF and ab245122 for IP - why? What is the difference? Both are rated equally for IF and IP - please provide a rationale for reagent selection and use.

These two antibodies are the same except their storage buffer. ab245122 is azide and BSA-free, while ab216324 contains the preservative sodium azide (0.01%) and the following constituents: PBS, 40% Glycerol (glycerin, glycerine), 0.05% BSA. As azide and BSA can affect coupling of antibodies to beads, antibodies which do not contain these components in their buffer are preferred for IPs (but can be stored less long).

(34) Page 35, line 862. "1.3 x 105" should be "1.3 x 105".

We added a regular x but we are not sure if this is what the reviewer was referring to ?

(35) MS comparison in Figure 6. Why is the comparison not being made between young vs. old brain/neurons? This would be more informative instead of just showing what they IP over a mock IgG control and the comparison would track better with other experiments in the rest of the paper.

Yes, that is true. However, we did not do this at the time as we did not have old mouse brain tissue available. Services from official animal providers in France have unfortunately only recently expanded their offer with regard to the availability of aged animals.

(36) Supplementary Table 2 (MS data) is lacking information. How many peptides (unique/total) were discovered for each protein? Why are all ratios and p-values not listed for every protein in the table? LFQ protein intensity values should also be listed. Each supplementary table should have a legend as a separate tab in the document.

As stated in the SupplTable2 and now made clearer in an independent tab file in SupplTable2 which contains a legend to the table, some proteins do not have associated p values and ratios as these proteins are found only in the ORF1p IP and not in the IgG control. This is why these proteins have an indefinite sign instead of a foldenrichment and no p-value assigned as we cannot calculate a ratio with X/0 which again makes it impossible to obtain a p-value. Concerning the absence of LFQ protein intensity values, as stated in the materials & methods section, we did not use these values (linear model) but instead the intensity values of the peptides: “The label free quantification was performed by peptide Extracted Ion Chromatograms (XICs), reextracted by conditions and computed with MassChroQ version 2.2.21 109. For protein quantification, XICs from proteotypic peptides shared between compared conditions (TopN matching) with missed cleavages were used. Median and scale normalization at peptide level was applied on the total signal to correct the XICs for each biological replicate (n=5). To estimate the significance of the change in protein abundance, a linear model (adjusted on peptides and biological replicates) was performed, and p-values were adjusted using the Benjamini–Hochberg FDR procedure.”

The number of peptides unique/total for each protein has been added to Suppl_Table2 along other available information.

(37) Poor overlap in 6C could in part be explained by the use of different sample/tissue types, but more likely the big difference could come from the very different conditions at which the IPs were performed (buffers and incubation times etc.).

The overlap seems poor, but nevertheless is bigger as by chance (representation factor 2.6, p<5.4e-08). We agree that this can be in part explained by different experimental conditions which we now added to the discussion (line 478: “However, differences in experimental conditions could also influence this overlap.”)

(38) Figure 6D is a very uninspiring representation of the data. What is the point of showing several binary interactions? Was the IgG control proteome also analyzed? Have proteins displayed in Figure 6 been corrected for that?

The point of showing these interactions is that OFR1p interacts with clustered proteins. ORF1p interacts with proteins that belong to specific GO terms (Fig6b), but these proteins are also interacting with each other more than expected (Fig6C). This is the benefit of showing a STRING (Search Tool for the Retrieval of Interacting Genes/Proteins) representation, which is a database of known and predicted protein–protein interactions. Indeed, proteins in Fig6 have been corrected for the IgG proteome. We only show proteins that were enriched or uniquely present in the ORF1p IP condition compared to the IgG control (please see Suppl_Table2).