Dissecting the heterogeneity of DENV vaccine-elicited cellular immunity using single-cell RNA sequencing and metabolic profiling

Generating effective and durable T cell immunity is a critical prerequisite for vaccination against dengue virus (DENV) and other viral diseases. However, understanding the molecular mechanisms of vaccine-elicited T cell immunity remains a critical knowledge gap in vaccinology. In this study, we utilize single-cell RNA sequencing (scRNAseq) and longitudinal TCR clonotype analysis to identify a unique transcriptional signature present in acutely activated and clonally-expanded T cells that become committed to the memory repertoire. This effector/memory-associated transcriptional signature is dominated by a robust metabolic transcriptional program. Based on this transcriptional signature, we are able to define a set of markers that identify the most durable vaccine-reactive memory-precursor CD8+ T cells. This study illustrates the power of scRNAseq as an analytical tool to assess the molecular mechanisms of host control and vaccine modality in determining the magnitude, diversity and persistence of vaccine-elicited cell-mediated immunity.

• The single cell RNAseq experiments have been designed in a way that I find hard to follow. Day 14 is about active T cells CD38+ HLA DR+, compared to double negative. But the scRNAseq for the control has not been used.
• For day 120, as memory cells have been first stimulated it is very difficult to interpret scRNAseq data (which have not been shown, only TCR). Did the authors consider the analysis of these cells without stimulation, maybe with tetramers? • Can the authors explain whether Day 14 TCR repertoire from CD38+ and CD38-subset overlap? • It is unclear whether scRNASeq have evidence of CD71 expression • At day 14 scRNAseq, I would suggest a more detailed analysis of the gene expression data, Not only testing the expression level of CD71 and other markers that have been associated to metabolic activities, but also to investigate whether or not specific subset of T cells exists. One way would be to test the presence of memory precursor versus effector cells, • In general, I would carefully analysis the scRNAseq data and not simply use cellRanger. There is a lot out there, in terms of software tools that have been shown to be more effective in detecting signals, and also to analysis drop out., Is CD71 affected by drop out? • Also, I was expecting some analysis that compare scRNaseq data from Day 14 and later time point. Interesting the later time point has been analysis only for TCR, what about the genes? • Why the authors have analysed only CD38+ cells in the gene expression analysis? Why not the CD38-population? What gene signatures these have and how they differ from the CD38 +? Did the metabolic pathways differ? Again, the gene expression analysis is very poor, with only a clustering analysis. • It would be interesting to look at the evolutionary dynamics by comparing scRNAseq at day 14 and day 120. A pseudo time analysis would be probably helpful. • Regarding peptide stimulation and ELISPOT, would be helpful to clarify whether specific peptides could be tested for each region and have a map against serotype? • On this matter, the data show NS3 and NS1 reactive memory but not NS5, which is also a known highly immunogenic region of the virus. ELISPOT in Fig 2 show (Subject 30), Are these data on other subjects, consistent with these? Perhaps other subjects have a broader and stronger NS5 restricted response? • On the message "". Interesting conclusion. Have the authors considered to test for specific property of long-term memory? Vaccine studies have been recently showing the presence of these precursor memory, see Rafi Ahmed paper in Nature on YFV and memory stem cells. This approach will allow investigation of activation but not memory. • The authors should clarify the message of this work. I found the discovery of a subset of precursor memory that could potentially be present already at day 14 the most interesting finding. Can the author retrospectively analyse the earliest time points? • Is there data before day 14? • The introduction of the work on CD71 CD98 comes a bit out of the blue. I see the point that gene expression suggests metabolic changes between the populations of T cells, But why these two markers? Gene expression didn't suggest these but an overall metabolic evolution. There are many other ways to investigate metabolic activities and also different pathways to be investigated, for instance, gene expression seems to suggest overexpression of MTOR and OHPHOS in some clusters (Cluster 1). Then point I am making is that this approach was not driven by the data but decided a priori as a hypothesis. This may not reflect the heterogeneity observed from the single cell data. Also, unclear whether this is the right mechanism that distinguish memory precursor from the rest of the memory cells. • For Figure 4, why the authors have not performed the experiment on specific memory and effector subsets rather than total CD4 or CD8?
Minor point I would specify in the abstract what metabolic programs determine T cell generation during early phase.
Reviewer #2: Remarks to the Author: I have looked at the paper and realise that part of it is outside my area of expertise. I am not familiar with single cell RNA sequencing data so cannot comment on that. I am also not familiar with work looking at human T cell responses to vaccines so that I do hope you have got an 'expert vaccine immunologist looking at this paper.
In terms of importance of the subject matter then I do feel that understanding the responses triggered by vaccines is well worth analysing and hence this paper addresses an important area of immunology and science.
The part of the work I am familiar with is the metabolic profiling assays. Here the authors use a number of tools to examine how a Dengue virus stimulates T cell metabolism. They use CD71 and CD98 antibodies which detect respectively the transferrin receptor and the heavy subunit of system L amino acid transporters. These are well validated tools and the data here should be robust.
The in vitro validation of these markers was good to see but not particularly novel. However it was very interesting to see that one could use CD71 to 'sense' a good vaccine response in T cells isolated from immunised individuals ex vivo . It was also interesting to see that it could be uses as an assay to monitor T cell activation in for ex vivo T cells stimulated in vitro with various antigen combinations.
Here I was surprised that this had not been done before. CD71 and CD98 are common markers for activated T cells that have been in existence since the 1980s? They are known to identify transformed and activated lymphocytes. None the less this is interesting to see these responses although I was not really convinced that CD71 and CD98 were any more sensitive that some of the other activation markers.
The authors also use two fluorescent dyes 2NPDG and BODIPY FL-C in credible attempts to monitor glucose uptake and fatty acid uptake. The problem with these experiments is that these tool compounds need to be used very carefully with carefully conceived controls to avoid problems with non specific binding to large cells versus small cells. These controls are not used in the paper or discussed. The controls are easy to do and simply require that the authors show that the binding of NPDG can be competed with excess glucose. ie cold competition of the glucose transporters -other wise there is no way to tell if this uptake is via a transporter of not or what it measures . Similarly with the fatty acid dye-Can a non fluorescent analogue'compete? The authors conclude that the data they show reflect changes in expression of fatty acid transporters and glucose transporters -it does not. The assay they use is simply not robust enough. The controls need to be done before these data can be cited to reflect transport.
However, given that the best correlation is with iron transport then the CD71 data is perhaps enough? A simple story based on CD71 is interesting given that we know how important iron metabolism is for cells.
Here other assays the authors might like to consider in future in terms of in vitro re-challenge would be to assess if the uptake of fluorescent transferin gave more sensitivity? As well, single cell assays for ERK1/2 phosphorylation and S6 phosphorylation can be very useful readouts of T cell activation in vitro and extremely sensitive. Moreover, antigen receptor engagement activates Erks1/2 with a couple of minutes and even S6 phosphorylation takes only 30 minutes. No need to do the long time point restimulation.
Reviewer #3: Remarks to the Author: The major claim from this study is that a unique transcriptional signature in a subset of the T-cell effectors expanding in response to dengue TAK-003 vaccination identifies them as memory precursors. CD71 is a major phenotypic marker for this subset.
This reviewer appreciates the excellent quality of the work, the extensive characterization of the T-cell expansion in dengue vaccine recipients using RNA-seq, clonotypic analysis, and flow cytometry methods. The resultant information that will be of great use to the field. However, the conclusion that CD71 (or other metabolic signatures) identifies the memory precursors, although has merit, is not convincing enough, with the data in its present form. The reasons are the following: 1. The authors sorted memory cells based on their functional specificity (i.e., ability to respond to NS1 or NS3 peptides by up-regulating CD69 and CD25), identified TCR clonotypes and examined the representation of these similar clonotypes in effector cells. However, the effector cells were sorted solely based on the expression of activation markers (CD38, HA-DR and or CD71) rather than functional specificity. In the absence of the information on specificity of these effector cells, it is difficult for this reviewer to be convinced of this major conclusion.
2. Many studies, including this study, suggests that CD71 is robustly expressed on proliferating cells. It is conceivable that these proliferating cells could have been highly enriched for non-structural protein specific cells, potentially due to higher abundance of these NS protein derived peptides; and as a result, could give an impression that these are memory precursors. 3) There was a typo in L134 "Tome point" shoudl be time point 4) The term "Matrixed elispot" is a bit unclear, perhaps matrix-based ELISPOT may be more accurate 5) The authors has not clearly explained the differential expression analysis performed in cell ranger What parameter have been used for thresholds? 2-fold? what was used as cut off for the gene expression showed in the tables?

Reviewers' Comments
Reviewer #2: Remarks to the Author: The authors have done some of the modifications I requested, but they still have one what overstate some aspects of the metabolic data I will only comment about this.
1) The authors state that they see changes in the amino acid transporter LAT1 by flow cytometry (fig  4). They do not measure LAT1 they measure its chaperone CD98. The text should be modified to say that they measure CD98. This does not necessarily mean LAT1 is expressed as CD98 can partner with other system L transporters and with integrins. In this context the authors in their rebuttal that the metabolites transported by CD98 fuel oxidative phosphorylation. CD98 is not a transporter but it can partner system L amino acid transporters that transport large neutral amino acids. However these do not fuel oxidative phosphorylation.
2) To validate that they were measuring glucose transporters they were asked to do a cold competition assay in their 2NPDG binding experiments. This did not work well and rather than accept that this means that their assay is not measuring a glucose transporter they claim this is an affinity problem. This is tiresome and not good science. If one cannot do the experiment properly then one does not assume that the data are valid one. Should rather be more questioning. However this could easily be overcome if the authors are open and honest about their data. Eg they should discuss the issues with cold competition in the paper. This would be simple to do. Readers can then make their own mind up Reviewer #3: Remarks to the Author: I read the revision with great interest.
In contrast to the interpretations presented here, what I can conclude from the data presented in the revised manuscript is: after vaccination the authors are identifying a set of highly activated effector cells. These cells, although highly activated based on activated profiles as well as metabolic indicators, completely fail to produce IFN-g when stimulated with peptides.
This phenotype is similar to what has been reported in dengue natural infection in humans, including robust up-reguation of CD71 , massive proliferation and inability to produce IFN-g when stimulated with dengue peptides (see: It is anticipated that some, but not all, of these cells are likely to survive to differentiate into memory cells that would regain ability to produce cytokines. These memory cells will obviously share the TCRs of the initial effector cells.
So, I do not think the authors are identifying "memory precursors".
The appropriate interpretation is that: Dengue vaccination leads to a robust expansion of effector cell populations that fail to produce IFN-g, similar to what has been seen in dengue natural infection, but the memory cells generated from these clonotypes later produce IFN-g.

If possible I would suggest to move in the main Suppl. Fig 4 as it clearly shows the difference with the CD38population.
While we agree with the reviewer that the data shown in Supplemental Figure  We are very familiar with the manuscript mentioned by the reviewer, as it has provided inspiration for some of our own work presented in this manuscript. However, we observe minimal overlap between the differentially-expressed gene products highlighted in the Wang et al study and those emphasized in our work. This is attributable to the fact that Wang et al were assessing differential gene expression between putatively pathogenic and non-pathogenic populations of influenza-reactive CD38 + HLA-DR + CD8 + T cells, while we are assessing differential gene expression within a population of CD38 + HLA-DR + CD8 + T cells in individual subjects. The gene signatures presented in the Wang et al manuscript includes many differentially-expressed interferon-associated factors, which we do not observe in our dataset.
However, many of the gene products and surface markers that we have highlighted in our study associated with T cell proliferation and effector function have been observed to be expressed in CD8 + T cells responding to natural viral infections. We have updated our manuscript to highlight these conserved transcriptional signatures.
There was a typo in L134 "Tome point" shoudl be time point We have corrected this typo in the revised manuscript The term "Matrixed elispot" is a bit unclear, perhaps matrix-based ELISPOT may be more accurate We agree with the reviewer that our description of this technique was confusing. We have clarified the description of the matrix-based ELISPOT in our revised manuscript.