Sex-biased regulatory changes in the placenta of native highlanders contribute to adaptive fetal development

Reviewer #1 (Public Review):

In this manuscript, the authors investigate differences between Tibetans and Han Chinese at altitude in terms of placental transcriptomes during full-term pregnancy. Most importantly, they found that the inter-population differentiation is mostly male-specific and the observed direction of transcriptional differentiation seems to be adaptive at high altitude. In general, it is of great importance and provides new insights into the functional basis of Tibetan high-altitude adaptations, which so far have been mostly studied via population genetic measures only. More specifically, I firmly believe that we need more phenotype data (including molecular phenotypes such as gene expression data) to fully understand Tibetan adaptations to high altitude, and this manuscript is a rare example of such a study. I have a few suggestions and/or questions with which I hope to improve the manuscript further, especially in terms of 1) testing if the observed DEG patterns are truly adaptive, and 2) how and whether the findings in this study can be linked to EPAS1 and EGLN1, the signature adaptation genes in Tibetans.

Major Comments:

1. The DEG analysis is the most central result in this manuscript, but the discrepancy between sex-combined and sex-specific DEGs is quite mind-boggling. For those that were differentially expressed in the sex-specific sets but not in the sex-combined one, the authors suggest an opposite direction of DE as an explanation (page 11, Figure S5). But Figure S5A does not show such a trend, showing that down-regulated genes in males are mostly not at all differentially expressed in females. Figure S6B does show such a trend, but it doesn't seem to be a dominant explanation. I would like to recommend the authors test alternative ways of analysis to boost statistical power for DEG detection other than simply splitting data into males and females and performing analysis in each subset. For example, the authors may consider utilizing gene-by-environment interaction analysis schemes here biological sex as an environmental factor.

2. Please clarify how the authors handled multiple testing correction of p-values.

3. The "natural selection acts on the placental DEGs ..." section is potentially misleading readers to assume that the manuscript reports evidence for positive selection on the observed DEG pattern between Tibetans and Han, which is not.
a) Currently the section simply describes an overlap between DEGs and a set of 192 genes likely under positive selection in Tibetans (TSNGs). The overlap is quite small, leading to only 13 genes in total (Figure 6). The authors are currently not providing any statistical measure of whether this overlap is significantly enriched or at the level expected for random sampling.
b) The authors are describing sets of DEGs that seem to affect important phenotypic changes in a consistent and adaptive direction. A relevant form of natural selection for this situation may be polygenic adaptation while the authors only consider strong positive selection at a single variant/gene level.
c) The manuscript is currently providing no eQTL information that can explain the differential expression of key genes. The authors can actually do this based on the genotype and expression data of the individuals in this study. Combining eQTL info, they can set up a test for polygenic adaptation (e.g. Berg and Coop; https://journals.plos.org/plosgenetics/article?id=10.1371/journal.pgen.1004412). This will provide a powerful and direct test for the adaptiveness of the observed DEG pattern.

4. The manuscript is currently only minimally discussing how findings are linked to EPAS1 and EGLN1 genes, which show the hallmark signature of positive selection in Tibetans. In fact, the authors' group previously reported male-specific association between EPAS1 SNPs and blood hemoglobin level. Many readers will be intrigued to see a discussion about this point.

Reviewer #2 (Public Review):

In this manuscript, the authors use newly-generated, large-scale transcriptomic data along with histological data to attempt to dissect the mechanisms by which individuals with Tibetan ancestry are able to mitigate the negative effects of high elevation on birth weight. They present detailed analyses of the transcriptomic data and find significant sex differences in the placenta transcriptome.

I have significant concerns about the conclusions that are presented. The analyses also lack the information necessary to evaluate their reliability.

The experimental design does not include a low elevation comparison and thus cannot be used to answer questions about how ancestry influences hypoxia responses and thus birthweight at high elevations. Importantly, because the placenta tissues (and trophoblasts specifically) are quickly evolving, there are a priori good reasons to expect to find population differences irrespective of adaptive evolution that might contribute to fetal growth protection. There are also significant details missing in the analyses that are necessary to substantiate and replicate the analyses presented.

Although the datasets are ultimately valuable as reference sets, the absence of low elevation comparisons for Tibetans and Han Chinese individuals undermines the ability of the authors to assess whether differences observed between populations are linked to hypoxia responses or variation in the outcomes of interest (i.e., hypoxia-dependent fetal growth restriction).

The authors attempt to tackle this phenotypic association by looking for correlations between gene networks (WGCNA) and individual genes with birthweight and other measurements collected at birth. I have some reservations about this approach with only two groups (i.e., missing the lowland comparison), but it is further problematic that the authors do not present data demonstrating that there are differences in birthweight or any other traits between the populations in the samples they collected.

Throughout, I thus find conclusions about the adaptive value and hypoxia-responses made by the authors to be unsubstantiated and/or the data to be inadequate. There are also a gratuitous number of speculative statements about mechanisms by which differential gene expression leads to the protection of birthweight that are not evaluated and thus cannot be substantiated by the data presented.

As currently presented and discussed, these results thus can only be used to evaluate population differences and tissue-specific variation therein.

There is also some important methodological information missing that makes it difficult or impossible to assess the quality of the underlying data and/or reproduce the analyses, further limiting the potential impact of these data:
1. Transcriptome data processing and analyses: RNA quality information is not mentioned (i.e., RIN). What # of reads are mapped to annotated regions? How many genes were expressed in each tissue (important for contextualizing the # of DE genes reported - are these a significant proportion of expressed genes or just a small subset?).
2. The methods suggest that DE analyses were run using data that were normalized prior to reading them into DESeq2. DESeq2 has an internal normalization process and should not be used on data that was already normalized. Please clarify how and when normalization was performed.
3. For enrichment analyses, the background gene set (all expressed genes? all genes in the genome? or only genes expressed in the tissue of interest?) has deterministic effects on the outcomes. The background sets are not specified for any analyses.
4. In the WGCNA analysis, P-values for correlations of modules with phenotype data (birthweight etc.) should be corrected for multiple testing (i.e., running the module correlation for each outcome variables) and p.adjust used to evaluate associations to limit false positives given the large number of correlations being run.
6. The plots for umbilical histological data (Fig 5 C) contain more than 5 points, but the use of replicate sections is not specified. If replicate sections were used, the authors should control for non-independence of replicate sections in their analyses (i.e., random effects model).

On more minor notes:
There is significant and relevant published data on sex differences and hypoxia in rodents (see Cuffe et al 2014, "Mid- to late-term hypoxia in the mouse alters placental morphology, glucocorticoid regulatory pathways, and nutrient transporters in a sex-specific manner" and review by Siragher and Sferuzzi-Perro 2021, "Placental hypoxia: What have we learnt from small animal models?"), and historical work reporting sex differences in placental traits associated with high elevation adaptation in Andeans (series of publications by Moira Jackson in the late 1980s, reviewed in Wilsterman and Cheviron 2021, "Fetal growth, high altitude, and evolutionary adaptation: A new perspective").

Reviewer #3 (Public Review):

More than 80 million people live at high altitude. This impacts health outcomes, including those related to pregnancy. Longer-lived populations at high altitudes, such as the Tibetan and Andean populations show partial protection against the negative health effects of high altitude. The paper by Yue sought to determine the mechanisms by which the placenta of Tibetans may have adapted to minimise the negative effect of high altitude on fetal growth outcomes. It compared placentas from pregnancies from Tibetans to those from the Han Chinese. It employed RNAseq profiling of different regions of the placenta and fetal membranes, with some follow-up of histological changes in umbilical cord structure and placental structure. The study also explored the contribution of fetal sex in these phenotypic outcomes.

A key strength of the study is the large sample sizes for the RNAseq analysis, the analysis of different parts of the placenta and fetal membranes, and the assessment of fetal sex differences.

A main weakness is that this study, and its conclusions, largely rely on transcriptomic changes informed by RNAseq. Changes in genes and pathways identified through bioinformatic analysis were not verified by alternate methods, such as by western blotting, which would add weight to the strength of the data and its interpretations. There is also a lack of description of patient characteristics, so the reader is unable to make their own judgments on how placental changes may link to pregnancy outcomes. Another weakness is that the histological analyses were performed on n=5 per group and were rudimentary in nature.