Peer review of: Generation, localization and functions of macrophages during the development of testis (2020)

Reviewers' comments: 

Reviewer #1 (Hematopoiesis, tissue-resident macrophage)(Remarks to the Author): 

Lokka et al. present data on the heterogeneity and origin of testes-resident macrophages and their 
role in spermatogenesis. Using high dimensional single cell mass cytometry, alterations in macrophage 
populations from the embryo to adult mice are determined, thereby defining new macrophage subsets. 
Lineage-tracing and macrophage-depletion studies substantiate the interpretation of the mass 
cytometry data and the manuscript elegantly bridges descriptive high-dimension mass-cytometry with 
functional in vivo approaches. The key messages are new and unprecedented to the field, making this 
a potentially high impact publication. All experiments are well thought through, presented and 
described. However, a few points need to be addressed to substantiate the strong and important 
conclusions drawn from the data provided: 

1) The mass cytometry data is very fascinating and a lot can be learned about macrophage 
heterogeneity in the testes. However, the authors need to state that any conclusion on precursor-
product relationships based on bioinformatic analysis remains a hypothesis until verified by actual in 
vivo lineage-tracing experiments shown later in the manuscript. The term ‘in silico lineage tracing’ or 
alike may work. This referee also suggests consolidation of this part of the manuscript. It would be 
great if the data can be provided to the readers by a publicly accessible database to provide the 
immense information to the field? 
2) Experiments testing the scavenging function are interesting (Figure 4c-g) and – to the opinion of 
this referee – crucial for the definition of a mature macrophage. However, it remains unclear whether 
dextran particles are engulfed or bound (the term used by the authors) – one is an active process, the 
other one may be a passive mechanism explaining the observed co-localization. Also, the authors may 
want to consider using the functional test as baseline for the definition of mature macrophages and, 
correspondingly, ‘label’ all other subsets ‘non-phagocytic macrophages’ (precursors?). The histological 
analysis needs to be quantified to allow any conclusion to be drawn. Finally, the authors state that 
MHCII+ cells do not ‘bind’ dextran, but the picture shows adjacent signals for dextran and MHCII 
(Figure 4g) – please specify and explain. 
3) The in vivo lineage-tracing experiments are very elegant and informative. Even though the 
embryonic origin of CD206+ MHCII- macrophages is shown, the extent of the contribution of embryo-
derived macrophages in this population is most likely underestimated. Tissue-specific lineage-tracing 
cre-transgenic mouse lines are available that exclusively and uniformly label embryo-derived 
macrophages. The authors could use one of these models or estimate the extent of contribution of 
embryonic cells to CD206+ MHCII- macrophages by applying TAM pulses at earlier time points 
(embryonic macrophage progenitors emerge around E8.5). How do the authors exclude the labeling of 
postnatal CXCR1+ cells through prolonged bioavailability of TAM? 
4) To show lack of contribution from postnatal definitive HSC-derived cells to testes macrophages the 
authors should use available lineage-tracing mouse models to substantiate their findings. 
5) Functional importance of embryonic macrophages for spermatogenesis. The authors deplete 
macrophages with anti-Csf1r Abs in newborn mice (efficient but transient for CD206+ MHCII- Mp, 
Figure 8 b-d,f) or use Ccr2-/- mice (inefficient, Figure 6d) and find no effect on spermatogenesis. The 
time point of macrophage depletion may be too late (NB), and or the depletion not complete 
preventing a potential role for embryonic macrophages on spermatogenesis to become evident by 
these assays. A genetic model targeting embryonic macrophages before birth or any other definitive 
experimental approach would be much more convincing. 
6) Overall, the manuscript is lengthy and would benefit greatly from consolidation into fewer figures 
focusing on the crucial experiments. 

Minors: 

Editorial Note: Parts of this peer review file have been redacted as indicated to remove third-party material where no permission to publish could be obtained.Figure 1a. Insert information on the pregating of the cells (same throughout Figure 2). 
Figure 4 a vs b. How do the authors explain the discrepancy of frequencies of CD206- MHCII- Mps in 
the testes of 5 week-old mice between mass and flow cytometry? 

Reviewer #2 (Immune metabolism, tissue-resident macrophage)(Remarks to the Author): 

Here the authors use a combination of high dimension flow cytometry, fate mapping and depletion 
studies to examine in detail the origin and phenotypes of macrophages in the testis. They identify 
CD206 and MHC-II as two key markers for the discrimination of macrophage populations. The analysis 
is extensive and well presented. The conclusions, however, are largely descriptive. It is of note that 
they are challenging current dogma and they propose an interesting hypothesis that CD206-MHC-II- 
cells give rise sequentially to CD206+MHC II- then CD206-MHC-II+ populations. They fairly note that, 
“These data are compatible with” such a scenario but this is based largely on trajectory analysis of the 
flow data. Although these analyses have hypothesis generating power, in my opinion this must be 
further confirmed with transfers, tight fate mapping or other means. Lastly, the fact that depletion of 
these populations seems to have little if any effect is disappointing. Together with the fact that the 
only functional assessment is uptake of dextran, Ig complexes or LDL, leaves one thinking that this 
report is better suited to a highly specialized venue where it will be seen by aficionados of 
hematopoiesis. 

Minor comments: 

In figure 1a the distinction seems to be on cd45 density rather than F4/80. In fact many of the assays 
show differences in CD45 density but this is not commented on in the text. 

In contrast to the statements it appears that a substantial number of the F4/80int cells are CD11c+ in 
the NB and there is a substantial population of eosinophils as well. 

Statements such as, “These data are compatible with a scenario that CD206−MHC II− cells infiltrate 
the testes during the fetal period (presumably as Ly6C+ monocytes) and first give rise to CD206+MHC 
II− cells in young mice and subsequently differentiate to CD206−MHC II+ macrophages during later 
postnatal life.” Are not sufficiently supported. 

The first 3 figures are purely descriptive and could be substantially condensed as in the later figures 
the populations are largely cooked down to those noted above. 

Figure 4 f clearly shows CD206+ cells with no dextran (more than are positive for dextran) yet the 
analysis seems to show nearly uniform labeling. 

Figure 5 is descriptive and needs some sort of quantification if possible. 

Reviewer #3 (Remarks to the Author): 

Thank you for the opportunity to review the manuscript by Lokka et al.: “Tissue-resident macrophages 
in the adult testis are of embryonic origin”. The authors used mass cytometry, depletion experiments, 
macrophage deficient mice and fluorescent imaging to investigate the developmental origin and 
turnover of tissue-resident macrophages in the testis of mice. They define new macrophage cell types, 

and show that testicular macrophages are fetal-derived, and are indispensable for spermatogenesis. 
This is an interesting article that brings new insight into the macrophage biology of the testis and 
argues against some previously established concepts. The use of mass cytometry and multiple 
experimental mouse models is a powerful approach. The manuscript could benefit from addressing the 
following comments. 

1. The mass cytometry approach of newborn and postnatal testis identified interesting new cell 
populations. From a technical standpoint, how did the authors account for sample to sample variability 
in staining. Were samples from various experimental groups barcoded together? Moreover, it appears 
that sample groups are being analyzed with different strategies. For example, what is the rationale 
behind analyzing the newborn data (fig 1f) separately from the postnatal data analysis (fig 2-3). 
Similarly, why FlowSOM ran only on the postnatal samples and not on the newborn samples? 

2. Fetal testis where only assessed in figure 1. All other figures are focused on newborn and/or 
postnatal testis. It doesn’t seem like the assessment of the fetal testis is crucial to the results and 
conclusions of this manuscript. If it is, this should be made clearer. Moreover, the flow cytometric 
approach and additional phenotypic assessment of CD115+, CD206+ and Ly6Clow expression seems 
rather redundant when they had the opportunity to run high-dimensional mass cytometry. Why was 
decided to not run mass cytometry on embryonic samples? 

3. To interrogate the yolk-sac origin of F4/80hi macrophages in fetal testis the authors used a 
depletion model that should selectively deplete yolk-sac derived macrophage. However, when looking 
at Suppl. Fig 2e., both F4/80hi and F4/80int cells are present in the brain of the isotype-treated group, 
with the F4/80int cells remaining after depletion. Why are F4/80int macrophages present in the brain 
when the authors say there should be solely yolk-sac derived macrophages? 

4. In the fate-mapping experiments on line 287-298, YPF-positivity was exclusively found in the 
CD206+MHCII- cells. However, results show only 1% of the CD206+MHCII- cells are YPF-positive. 
Consequently, if only 1% of the CD206+MHCII- cells are of yolk-sac origin, it doesn’t seem like a 
surprise that depletion of yolk-sac derived macrophages by anti-CSF1R antibody administration will 
have an impact on the macrophage populations. This should be discussed in the manuscript. 

5. The origin tracking results (Fig 6) show that yolk-sac and fetal-liver derived macrophages 
contribute to only a part of the tissue-resident macrophages observed in the testis (i.e. there are still 
macrophages populations present in both experimental models), while bone-marrow derived 
macrophages do not significantly contribute to the population under normal homeostatic conditions. 
The authors should speculate where the other tissue-resident macrophages observed in the testis 
might originate from. 

6. An explanation for why the tissue-resident depletion should also be done in newborns next to 10-
day-old mice is warranted. In addition, the authors should discuss the difference in obtained results 
between these 2 experimental models, i.e. recovery of macrophage populations in newborn model 
while no recovery in 10-day-old mice model.