Parallel expansion and divergence of an adhesin family in pathogenic yeasts

  1. Rachel A Smoak
  2. Lindsey F Snyder
  3. Jan S Fassler
  4. Bin Z He

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Abstract

Opportunistic yeast pathogens arose multiple times in the Saccharomycetes class, including the recently emerged, multidrug-resistant (MDR) Candida auris. We show that homologs of a known yeast adhesin family in Candida albicans, the Hyr/Iff-like (Hil) family, are enriched in distinct clades of Candida species as a result of multiple, independent expansions. Following gene duplication, the tandem repeat–rich region in these proteins diverged extremely rapidly and generated large variations in length and β-aggregation potential, both of which are known to directly affect adhesion. The conserved N-terminal effector domain was predicted to adopt a β-helical fold followed by an α-crystallin domain, making it structurally similar to a group of unrelated bacterial adhesins. Evolutionary analyses of the effector domain in C. auris revealed relaxed selective constraint combined with signatures of positive selection, suggesting functional diversification after gene duplication. Lastly, we found the Hil family genes to be enriched at chromosomal ends, which likely contributed to their expansion via ectopic recombination and break-induced replication. Combined, these results suggest that the expansion and diversification of adhesin families generate variation in adhesion and virulence within and between species and are a key step toward the emergence of fungal pathogens.

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  1. Version published to 10.1093/genetics/iyad024
  2. Version published to 10.1101/2022.02.09.479577v3 on bioRxiv
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    Reviewer #1

    SUMMARY

    The manuscript by Smoak et al., provides an analysis of the Hyr/Iff-like (Hil) genes in Candida species with a strong focus on C. auris. The authors demonstrate a repeated expansion of these genes in unique lineages of fungal species, many of which are associated with stronger clinical disease. There is evidence of selection operating on the gene family in the primary domain used for identification. These genes include a repeat just downstream of that core domain that changes frequently in copy number and composition. The location of these genes tends to cluster at chromosome ends, which may explain some aspects of their expansion. The study is entirely in silico in nature and does not include experimental data.

    MAJOR POINTS

    Altogether, many of the general findings could be convincing but there are some aspects of the analysis that need further explanation to ensure they were performed correctly. To start, a single Hil protein from C. auris was used as bait in the query to find all Hil proteins in yeast pathogens. Would you get the same outcome if you started with a different Hil protein? What is the basis for using Hil1 as the starting point? It also doesn't make sense to me to remove species just because there are already related species in the list. This may exclude certain evolutionary trends. Furthermore, it would be helpful to know how using domain presence and the conservation of position changes the abundance of the gene family across species? (beginning of results).

    We appreciate the reviewer’s criticisms on our strategy for identifying Hil proteins. In response, we have significantly revised our pipeline. In particular, we now combine the search results from three queries: in addition to C. auris Hil1’s Hyphal_reg_CWP domain (XP_028889033), we added the Hyphal_reg_CWP sequences from C. albicans Hyr1 and C. glabrata Hyr1. They were chosen as representatives in the two phylogenetic groups distinct from the one containing C. auris in order to avoid the bias due to the query’s phylogenetic position. Using the same criteria as we did for the original search, we identified three additional hits compared with the original 104 homologs list. In response to the criticism of the arbitrary exclusion of some species, we now include any species from the BLASTP search results as long as it is part of the 332 yeast species studied by Shen et al. 2018 (PMID: 30415838). The reason for this criterion is so that we can use the high-quality species phylogeny generated by Shen et al. 2018 to properly study the gene family evolution by reconciling the gene tree with the species tree. We additionally include the species in the MDR clade closely related to C. auris and used Muñoz et al. 2018 (PMID: 30559369) as the basis for the species phylogeny in the clade. Lastly, we no longer require the particular domain organization in classifying Hil family members. All BLASTP hits satisfying the E-value cutoff of 1x10-5 and query coverage > 50% are included.

    A major challenge in the analysis like this one is in dealing with repetitive sequences present in amplified gene families. For example, testing modes of selection on non-conserved sites is fraught. It's not clear if all sites used for these tests are positionally conserved and this should be clarified. Alignments at repeat edges will need to maintain this conservation and relatively good alignments as stated in lines 241-242 are concerning that this includes sequence that does not retain this structure necessary for making predictions of selection.

    We appreciate the reviewer’s comment. In the original manuscript, we performed two different types of analyses, one on the conserved and well-aligned Hyphal_reg_CWP domain and another on the rapidly evolving repeat region. For the former, we performed phylogenetic dN/dS analyses using maximum-likelihood, for which a reliable alignment is crucial and is the case here. The Hyphal_reg_CWP domain alignment for C. auris Hil1-Hil8 is shown below and also included as Fig. S7 in the revised manuscript: (figure in the response file)

    In the text, we added this sentence to emphasize this point: “We chose to focus on the Hyphal_reg_CWP domain because of its potential importance in mediating adhesion and also because the high-quality alignment in this domain allowed us to confidently infer the evolutionary rates (Fig. S7).”

    For the repeat domain, what we did in the original version was to calculate the pairwise dN/dS between individual repeat units found in Hil1 and Hil2. This didn’t require aligning the entire repeat regions in the two proteins, but instead relied on the alignment of the individual ~44 aa repeat units, which were highly conserved (see below). In the revised manuscript, however, we decided to focus our analyses on the Hyphal_reg_CWP domain because of a different concern, namely gene conversions between paralogs could distort the evolutionary history of the repeats (the same concern was addressed for the effector domain using an additional step of detecting recombination breakpoints, but the same analysis would be challenging for the repeat region due to alignment issues).

    (figure in the response file)

    It's also unclear to me why Figure S12 is here. The parameters for this analysis should be tested ahead of building models so only one set of parameters should be necessary to run the test. The evolutionary tests within single genes and across strains is really nice!

    We appreciate the reviewer’s suggestion. Based on the reviewer’s suggestion, we removed Fig. S12 and describe the model set up in the Materials and Methods section. We were not sure if the last point was a comment or a suggestion. We didn’t perform a population level selective sweep scan in C. auris. Such an analysis has in fact been attempted by Muñoz et al. 2021, who identified several members of the Hil family as the top candidates for positive selection (PMID: 33769478). We cited this in our Discussion:

    “Lastly, scans for selective sweep in C. auris identified Hil and Als family members as being among the top 5% of all genes, suggesting that adhesins are targets of natural selection in the recent evolutionary history of this newly emerged pathogen (Muñoz et al. 2021).”

    A major challenge for expanded gene families is rooting based on the inability to identify a strong similarity match for the full length sequence. The full alignment mentioned would certainly include significant gaps. If those gaps are removed and conserved sites only are used, does it produce the same tree? Inclusion of unalignable sequences would be expected to significantly alter the outcomes of those analysis and may produce some spurious relationships in reconciling with the species trees. Whether or not there are similar issues in the alignment of PF11765 need to be addressed as well. There's nothing in the methods that clarifies site selection.

    We appreciate reviewer’s comment and agree with the concern about alignment quality affecting phylogenetic reconstruction. To clarify, all phylogenetic analyses in this work are based on the alignment of the Hyphal_reg_CWP domain, which is well aligned (shown above for the subset of eight homologs in C. auris). Alignment of all 215 homologs is provided for readers to review (shorturl.at/kDEJ3). To clarify this choice, we now include the following in Results:

    “To further characterize the evolutionary history of the Hil family, including among closely related Candida lineages, we reconstructed a species tree-aware maximum likelihood phylogeny for the Hil family based on the Hyphal_reg_CWP domain alignment (Fig. 1C, Fig. S2).”

    We also included detailed steps for reconstructing the gene tree in Materials and Methods.

    To test the effect of gaps in the alignment on phylogenetic tree inference, we used two trimming programs, ClipKit (PMID: 33264284) and BMGE (PMID: 20626897), with author-recommended modes. They resulted in consistent gene tree results. We present the tree based on the ClipKit trimmed alignment in the main results. The root of the gene tree was inferred by jointly maximizing the likelihood scores for the gene tree based on the alignment and the evolution of the gene family within the species tree, using GeneRax (Morel et al. 2020, PMID: 32502238).

    Figure 1A: the placement of evolved pathogenesis is a little arbitrary. It's just as feasible that a single event increased pathogenesis in the LCA of C. albicans and C. parapsilosis that was subsequently lost in L. elongisporus. These should be justified or I'd suggest removing. The assignment of Candida species here also seems incomplete. The Butler paper notes both D. hansineii and C. lusitaniae as Candida species whereas they are excluded here.

    We removed Figure 1 entirely based on this and another reviewer’s comment. We note that there is broad consensus that opportunistic yeast pathogens have independently arisen multiple times, such as C. auris, C. albicans and C. glabrata. Whether Candida pathogens that are more closely related evolved separately or not are subjects of ongoing research (PMID: 24034898).

    It is tricky to include scaffolds in analysis of chromosomal location of the HIL genes. The break in the scaffold may be due to the assc repeats of these proteins alone or other, nearby repeats. Any statistics would be best done to include only known chromosomes or those that are strongly inferred by Munoz, 2021. This will change the display of Figure 7, but is unlikely to change the take home message.

    We agree with the reviewer’s concern. In the revised manuscript and with more species included, we now only analyze genomes assembled to a chromosomal level, with the exception of C. auris B8441, which is supported by Muñoz et al. 2021 as having chromosome-length sequences. The revised Figure 7 now only includes these results. We also removed the accompanying supplementary figure that showed results based on scaffold-level assemblies.

    MINOR POINTS

    Line 18: "spp." Should be "spps."

    Addressed throughout the revised manuscript.

    Line 41: I might rephrase this as "how pathogenesis arose in yeast..."

    Accepted (line 43 in revised manuscript).

    I might use a yeast-centric example around line 40 for duplication and divergence. This could include genes for metabolism of different carbon sources in S. cerevisiae.

    Accepted (lines 47-48)

    The Butler paper referenced on line 51 compared seven Candida species and 9 Saccharomyces species

    Changed (line 48)

    The autors state no other evolutionary analysis of adhesins has been performed but do not acknowledge this study: https://academic.oup.com/mbe/article/28/11/3127/1047032

    We appreciate the reviewer pointing this important reference to us. We now cite it in the introduction (line 64) and discussion (line 340)

    The first paragraph of the Results could be condensed

    Addressed.

    How was the species tree in Figure 1A obtained?

    The previous figure 1 is now removed. The species tree used throughout the manuscript is based on Shen et al. 2018 with MDR clade species added, based on Muñoz et al. 2018.

    Figure 2: In panel A, "DH" and "SS" are not defined. I'd be careful with use of "non-albicans Candida" in Figure 2B. This usually includes C. tropicalis and C. dubliniensis and may confuse the reader.

    We removed the DH and SS labels. Instead, we highlighted three clades, which were defined in previous studies. These are the Candida/Lodderomyces clade (based on NCBI taxonomy database), the MDR clade (e.g., Muñoz et al. 2018, PMID: 30559369) and the glabrata clade (e.g., Gabaldón et al. 2013, PMID: 24034898).

    How was the binding domain defined to extract those sequences are produce a phylogeny? In building a ML model, how were parameters chosen?

    We now provide the following details in the Materials and Methods section:

    “To infer the evolutionary history of the Hil family, we reconstructed a maximum-likelihood tree based on the alignment of the conserved Hyphal_reg_CWP domain. First, we used hmmscan (HmmerWeb version 2.41.2) to identify the location of the Hyphal_reg_CWP domain in each Hil homolog. We used the “envelope boundaries” to define the domain in each sequence, and then aligned their amino acid sequences using Clustal Omega with the parameter {--iter=5}. We then trimmed the alignment using ClipKit with its default smart-gap trimming mode (Steenwyk et al. 2020). RAxML-NG v1.1.0 was compiled and run on the University of Iowa ARGON server with the following parameters on the alignment: raxml-ng-mpi --all --msa $align --model LG+G --seed 123 --bs-trees autoMRE.”

    The parameters for the ML tree reconstruction is listed on the last line above. The main parameter was the evolutionary model (LG+G), which accounts for rate variations using a gamma distribution. Other protein evolution models, e.g., VT+I+G, were tested and resulted in nearly identical tree topologies.

    Figure 3C/D could be just one panel.

    The structure predictions are now reorganized and presented on their own in the new Figure 3.

    Can you relate more the fungal hit to the Hil proteins conveyed in lines 152-154?

    We appreciate the reviewer’s comment, which referred to CgAwp1 and CgAwp3, whose effector domain structures were reported in a recent study (Reithofer et al. 2021, PMID: 34962966). We now discuss them in relation to the predicted Hyphal_reg_CWP structure, by showing them in Figure 3 and describing them in the Results (lines 181) “crystal structures for the effector domains of two Adhesin-like Wall Proteins (Awp1 and Awp3b) in C. glabrata, which are distantly related to those in the Hil family were recently reported, and the predicted structure of one of C. glabrata’s Hil family members (Awp2) was found to be highly similar to the two solved structures (Reithofer et al. 2021)”

    Line 168: Should read "Hence, ..."

    The original sentence was removed, but this grammatical error was checked for and corrected.

    Label proteins along the top of Figure 4 too.

    Accepted (in new Figure 4).

    Figure 5: for tests of selection, were sites conserved across the group? What does the black number at each node indicate? Dn and Ds are given as decimals. This is based on what attribute? For panel B, it is unclear what each tip denotes i.e., Hil1_tr6. Hil1 is the gene but what is "tr6"?

    In the revised manuscript, we provide the multiple sequence alignment for the Hyphal_reg_CWP domain used for the selection analysis as Fig. S7 to illustrate the level of conservation. The black numbers at the internal nodes are numeric indices used to refer to those nodes. In the revised manuscript, we use some of them to refer to the internal branches, e.g., 12…14 in the legend. In the new Figure 5, we do not list the numeric values of Dn and Ds (aka Ka, Ks). Instead, we use a color gradient to represent the estimated dN/dS ratios. The raw estimates are available in the project github repository. Panel B in the original Figure 5 and other panels related to the evolution of the repeats are now removed.

    It's unclear why comparison of the PF11765 domain includes the MRD proteins when those aren't included in the comparison to the repeats alone. Could that skew the comparison due to unequal sample numbers or changed variation frequencies in MDR relative to the other two groups?

    These results pertaining to the evolution of the repeats are now removed.

    Table 2 doesn't add much. This section could probably be reduced to a few sentences since it's highly speculative (intraspecies variation).

    Table 2 is now Table S5. We also simplified the result section in the revised version. While the functional implications of the intraspecific variable number of tandem repeats (VNTR) is speculative, it is founded on two bases: 1) the identification of the VNTR is credible, as the copy number variation is consistent within clades but differ between clades, which is not expected if they are caused by assembly errors; 2) experimental studies in S. cerevisiae for the Flo family strongly supported a direct impact of adhesin length on the adhesive phenotype of the cells (PMID: 16086015).

    Table 3 is not needed.

    Table 3 is now removed.

    Figure 6 - color coding in 6A needs to be explained. I'm assuming this is a taxonomical coding.

    In the revised Figure 6A, the coloring scheme is consistent with what we used in Figure 1 based on the three clades, and a legend is provided.

    Figure 1B is unnecessary. A Model of the protein indicating domains is sufficient here. Figure 1C needs labels for all termini, not just the pathogenic red branches. The figure doesn't provide clear association between adhesin families and the associated species. This could be omitted, especially since Flo is often associated with Saccharomyces species. Figure 1D is unnecessary.

    We have removed the original Figure 1.

    SIGNIFICANCE

    The work here is sorely needed in expanded gene families and in fungi specifically. No analysis at this level has been performed, to the best of my knowledge, in any fungal associated gene family and certainly not in relationship to pathogenic potential. The authors do a good job in citing the foundational literature upon which their study builds in most cases (one exception is noted above). It would be of general interest to those interested in the evolution of virulence, but the analysis is tricky. This is the biggest drawback I currently have as some of the information to assess the results is missing.

    We really appreciate the reviewer's positive comments. We agree and plan to explore the relationship between the adhesin family evolution and virulence phenotypes.

    Expertise: gene families, evolution dynamics, human fungal pathogens

    Reviewer #2

    SUMMARY

    Gene duplication and divergence of adhesin proteins are hypothesized to be linked with the emergence of pathogenic yeasts during evolution; however, evidence supporting this hypothesis is limited. Smoak et al. study the evolutionary history of Hil genes and show that expansion of this gene family is restricted to C. auris and other pathogenic yeasts. They identified eight paralogous Hil proteins in C. auris. All these proteins share characteristic domains of adhesin, and the structural prediction supports that their tertiary structures are adhesin-like. Evolutionary analysis of protein domains finds weak evidence of positive selection in the ligand-binding domain, and the central domain showed rapid changes in repeat copy number. However, performed tests cannot unambiguously distinguish between positive selection and relaxed selection of paralogs after gene duplication. Some alternative tests are suggested that may be able to provide more unambiguous evidence. Together with these additional tests, the detailed phylogenetic analyses of Hil genes in C. auris might be able to better support the hypothesis that the expansion and diversification of adhesin proteins could contribute to the evolution of pathogenicity in yeasts.

    We appreciate the reviewer’s comments and will address specific points below.

    MAJOR COMMENTS

    The authors present extensive analyses on the evolution of Hil genes in C. auris. There is significant merit in these analyses. However, the analyses conducted so far are incomplete, lacking proper consideration of other confounding factors. Detailed explanations of our major comments are listed below.

    1. First, the authors restricted genes in the Hil family to those only containing the Hyphal_reg_CWP domain. Yet, previous work included genes containing the ligand-binding domain or the repeat domain as Hil genes. More justification is needed whether the author's choice represents the natural evolutionary history of Hil genes appropriately. For instance, are the genes only containing the ligand-binding domain monophyletic or polyphyletic? We recommend including the phylogeny of all the Hil candidate genes, to discern whether evolutionary histories of the repeat domain and ligand-binding domain are congruent. Authors can use this phylogeny as justification to focus only on the ligand-binding domain containing genes.

    Butler et al. 2009 (PMID: 19465905) defined the Als family and the Hyr/Iff family as having either the N-terminal effector domain or the intragenic tandem repeats (ITR). Their rationale for the latter was that the ITS sequences were often conserved across species. Upon close inspection (Fig. S19,20 in that paper), however, we found that the ITS tend to be conserved in closely related species, but diverged among more distantly related species. Moreover, proteins in those figures that only contain the ITS and not the ligand-binding domains are all missing either the signal peptide, the GPI-anchor or both. This raises questions as to whether these proteins sharing the ITS sequence alone act as adhesins.

    More generally, defining the evolutionary history of proteins with multiple domains is complicated by recombination, which causes different parts (e.g., domains) of the protein to have distinct evolutionary histories. In fact, our study and others show that there exist “chimeras” that combine the effector domain from one adhesin family and the repeat sequence found in another (Zhao et al. 2011, PMID: 21208290, Oh et al. 2019, PMID: 31105652). In these cases, one phylogenetic tree is insufficient to describe the evolutionary history of the whole protein. We chose to define the Hil family by the Hyphal_reg_CWP domain and thus focus on the evolutionary history of this region because 1) while tandem repeat regions also contribute to adhesion in yeasts (Rauceo et al. 2006, PMID: 16936142), the effector domain likely plays a more important role in ligand binding and specificity. Therefore, we believe using the effector domain to define a protein family is more likely to group proteins with similar functional properties than if the repeat sequences were used. Also, while putative fungal adhesins lacking a recognizable ligand-binding domain exist, they are rare (Lipke 2018, PMID: 29772751); 2) The repeat region evolved much more rapidly than the effector domain, as we illustrate in Figures 2, 4 and 6 in our revised manuscript. While some repeat units are highly conserved, e.g., the ~44 aa unit found in Hil1-4 in C. auris and close relatives in the MDR clade, many others are short and degenerate, making it difficult to reliably identify homologs sharing the repeat. Besides, since each protein could contain many distinct repeats, it is not clear how one defines two sequences as belonging to the same family if they share one out of six types of repeats. We acknowledge that this definition leaves out the evolutionary history defined by the tandem repeats, which may reveal intriguing evolutionary dynamics, with functional implications. A recent review for the Als family discussed similar definition challenges and partly supported our choice (Hoyer and Cota, 2016, PMID: 27014205).

    In the analysis of positive selection, the authors do not adequately control for the effect of recombination on the evolutionary histories of protein sequences, especially given that Hil genes are rich in repetitive sequences. To account for recombination, GARD, an algorithm detecting recombination, should be performed to detect any recombination breakpoints within a protein domain. If recombination did occur within a protein domain, the authors should treat the unrecombined part as a single unit and use the phylogenetic information of this part to proceed with PAML analysis, instead of using the phylogeny of the entire protein domain. The authors should consider doing GARD analysis for the ligand-binding and repeat domains. For the repeat domain, low BS values in Fig. 5C indicate recombination between repeat units. Thus, the authors should analyze each repeat unit with GARD and re-analyze dN/dS.

    We deeply appreciate the reviewers’ criticism here. In the revised manuscript, we removed the analysis of the repeat units and followed the reviewers’ suggestion to carry out GARD analysis on the effector domain, which we now show reveals evidence of intra-domain recombination. Using the inferred breakpoints (Fig. S8), we identified two putatively non-recombining partitions and performed all downstream phylogenetic analyses on them separately. The results are presented in Fig. 5 and Table S6. Compared with the previous result based on the entire Hyphal_reg_CWP domain alignment, the new results reveal clearer patterns, including significantly elevated dN/dS on a subset of the branches. Newly added branch-site test results support a role of positive selection on the effector domain during the expansion of the Hil family in C. auris, suggesting functional diversification following gene duplications.

    The authors concluded positive selection in the ligand-binding domain based on the branch-wise model of PAML. Yet, w values were not higher than one, and it's unclear whether the difference in selective pressures the authors claimed here is biologically significant. Overall, what the authors present so far seems to be weak evidence of positive selection but is much more consistent with variation in the degree of purifying selection or evolutionary constraint. Using the site-wise model (m7 vs. m8) in PAML would allow the authors to detect which residues of the ligand-binding domain underwent recurrent positive selection. Combining the evolutionary information of protein residues and the predicted 3D structure will provide molecular insights into the biological impact of rapidly evolving residues. This would be a significant addition and raise the significance of the study, besides providing potentially stronger evidence of positive selection.

    We appreciate the reviewers’ criticism and suggestions. In the revised manuscript, we performed site tests comparing models M2a vs M1a, M8 vs M7 and M8a vs M8. For partition 1 (P1-414), all three tests were insignificant. For partition 2 (P697-987), the M2a vs M1a test was insignificant (P > 0.05) but M8 vs M7 and M8a vs M7a were both significant at a 0.01 level, and the omega estimate for the positively selected category was estimated to be ~15. The site tests require all branches to evolve under the same selection regime. To relax this constraint, we performed additional branch-site tests by designating the branches with an estimated dN/dS > 10 as the foreground (based on the free-ratio model estimates). This test was significant for both branches at a 0.01 level and the Bayes Empirical Bayes (BEB) procedure identified a total of 5 residues as having been under positive selection. Although three of the five residues, located in the C-terminus of the Hyphal_reg_CWP domain, are part of the α-crystallin domain, we refrain from drawing any functional conclusions because 1) the BEB procedure is known to be lacking power in identifying positively selected residues and 2) we still lack structure-function relationship for the α-crystallin domain. But we agree and believe that this line of analysis is promising in yielding functional insight into the evolution of the effector domain in the family.

    MINOR COMMENTS

    In Fig 1c, the figure legend should include more specific details: which adhesin proteins are shown here? Please specify species names on the species tree

    Figure 1 is removed in the revised manuscript

    In Fig 3E, secondary structures are labeled with the wrong colors. Sheet: purple, helix: yellow

    In the revised manuscript, the structures of SRRP-BR (original 3E) is now colored in a single color.

    What's the ligand-binding activity of the b-solenoid fold? How structurally similar are C. auris PF 11765 domains compared to C. glabrata Awp domains? This information will support the role of adhesin for the ligand-binding domain of Hil genes.

    We discuss the ligand-binding activity of the β-solenoid as follows in Discussion:

    “The elongated shape and rigid structure of the β-helix are consistent with the functional requirements of adhesins, including the need to protrude from the cell surface and the capacity for multiple binding sites along its length that facilitate adhesion. In some bacterial adhesins, such as the serine rich repeat protein (SRRP) from the Gram-positive bacterium, L. reuterii, a protruding, flexible loop in the β-helix was proposed to serve as a binding pocket for its ligand (Sequeira et al. 2018). Such a feature is not apparent in the predicted structure of the Hyphal_reg_CWP domain. Further studies are needed to elucidate the potential substrate for this domain and its mechanism of adhesion.”

    We also compare the structures of the C. auris Hil1/Hil7 Hyphal_reg_CWP domain and the CgAwp1/3 in Figure 3, with this in the legend “(C) Crystal structure of the C. glabrata Awp1 effector domain, which is highly similar to C. auris Hil1 and Hil7, but with the disulfide bond in a different location.”

    We added a section in the Discussion to comment on the structure-function relationship based on known β-helix (aka β-solenoid) structures. The main insight comes from similar structures identified through DALI searches, many of which are bacterial and viral surface proteins mediating adhesion. The ligand binding pocket and specificity would require additional structural studies to elucidate.

    In lines 248-249, the authors should also consider the influence of evolutionary history. For instance, repeats within the same Hil protein appeared later in evolution, compared to Hil gene duplication, and therefore these repeats experience less time for sequence divergence.

    In the revised manuscript, we removed the analyses pertaining to the evolution of the repeat regions due to multiple challenges including alignment, potential of gene conversion and recombination. This is an important and intriguing aspect of adhesin family evolution that we plan to follow up in future work.

    Although the bioinformatic evidence of C. auris Hil genes acting as adhesins is strong, it is still worthwhile to discuss the experiments of confirming the function of adhesins.

    We agree with the reviewer and acknowledge in the revised manuscript the limitation of our work:

    “Future experimental tests of these hypotheses will be important biologically for improving our understanding of the fungal adhesin repertoire, important biotechnologically for inspiring additional nanomaterials, and important biomedically for advancing the development of C. auris-directed therapeutics.”

    SIGNIFICANCE

    Overall, this study is interesting to investigate the evolutionary history of a crucial virulent gene in C. auris. Such evolutionary understanding will help us identify critical molecular changes associated with the pathogenicity of an organism during evolution, providing insights into the emergence of pathogens and novel strategies to cure fungal infections. The research question is important; however, the current analyses on the positive selection are incomplete, so the conclusion is modest so far. We recommend that the authors re-do the PAML analysis with the above considerations. This work will bring more significance to the mycology field if the functional impact of rapid evolution in protein domains can be supported or inferred.

    This manuscript is well-written, and the authors also did a great job specifying all the necessary details in the M&M.

    We appreciate the reviewers’ positive comments.

    Reviewer #3

    Summary:

    The manuscript by Smoak et al. provides considerable information gleaned from analysis of HYR/IFF genes in 19 fungal species. A specific focus is on Candida auris. The main conclusion is that this gene family repeatedly expanded in divergent pathogenic Candida lineages including C. auris. Analyses focus on the sequences encoding the protein's N-terminal domain and tracts of repeated sequences that follow. The authors conclude with the hypothesis that expansion and diversification of adhesin gene families underpin fungal pathogen evolution and that the variation among adhesin-encoding genes affects adhesion and virulence within and between species. The paper is easy to read, includes clear and attractive graphics, as well as a considerable number of supplementary data files that provide thorough documentation of the sources of information and their analysis.

    We appreciate the positive comment.

    MAJOR COMMENTS:

    • Are the key conclusions convincing?

    Overall, the authors' conclusions are supported by the information they present. However, the overall conclusion is stated as a hypothesis and that hypothesis is not particularly novel. The idea that expansion of gene families associated with pathogenesis occurs in the pathogenic species dates back at least to Butler et al. 2009, who first presented the genome sequences for many of the species considered here.

    We appreciate the reviewer’s comment. Our main conclusions are 1) the Hil family is strongly enriched in distinct clades of pathogenic yeasts after accounting for phylogenetic relatedness. This enrichment results from independent duplications, which is ongoing between closely related species; 2) the protein sequence of the Hil family homologs diverged rapidly following gene duplication, driven largely by the evolution of the tandem repeat content, generating large variation in protein length and β-aggregation potentials; 3) there is strong evidence for varying levels of selective constraint and moderate evidence for positive selection acting on the N-terminal effector domain during the expansion of the family in C. auris as our focal species. Based on these observations, we propose that expansion of adhesin gene families is a key preliminary step towards the emergence of fungal pathogenesis.

    Indeed, some version of this hypothesis has been proposed by several groups before us. We fully acknowledged this in our previous as well as the revised manuscript, by citing Butler et al. 2009 (PMID: 19465905), Gabaldón et al. 2013, 2016 (PMID: 24034898, 27493146). Our study built on these earlier efforts and extended them by addressing several limitations. First, we performed phylogenetic regression to test for the association between gene family size and the life history trait (pathogen or not) in order to properly account for the phylogenetic relatedness. This was not done in previous studies. Second, most earlier studies didn’t construct a family-wide gene tree to fully investigate the evolutionary history of the family. Gabaldón et al. 2013 did a phylogenetic analysis for the Epa family and a few others within the Nakaseomycetes, revealing highly dynamic expansions. In the present study, we expanded this effort by comprehensively identifying homologs within the Hil family in all yeasts and beyond. Third and perhaps the most important novelty in our study is our detailed analysis of sequence divergence and role of natural selection during the evolution of the family post duplication. This allowed us to present a complete picture of the family’s evolution, not just in its increase in copy number but also its diversification after the duplications, which is a key part of how gene duplications contribute to the evolution of novel traits. As such, we believe our study provides strong support for the above hypothesis.

    One key issue with a manuscript of this type is whether genome sequence data are accurate. The authors are not the first research group to take draft genome sequence data at face value and attempt to draw major conclusions from it. The accuracy of public genome data continues to improve, especially with the emergence of PacBio sequencing. Because the IFF/HYR genes contain long tracts of repeated sequences, genome assemblies from short-read data are frequently inaccurate. For example, is it reasonable to have confidence that the number of copies of a tandemly repeated sequence in a specific ORF is exactly 21 (an example taken from Table 2) when each repeat is 40+ amino acids long and highly conserved? Table S6 would benefit from inclusion of the type of sequence data used to construct each draft genome sequence. It is also reasonable to question whether the genome of the type strain is used as a template to construct the draft genomes of the other strains. If that was standard practice, conservation of the repeat copy number among strains might be an artefact. Conservation of repeat sequences to the degree shown is not a feature of the ALS family, a point of contrast between gene families that could be explored in the Discussion.

    We appreciate the reviewer’s comment and agree strongly that a key limitation in gene family evolution studies like ours is the quality of the genome assembly. In the original manuscript, we took several steps to ensure the completeness and accuracy of the Hil family homologs, primarily by basing our results on the high quality RefSeq collection of assemblies, and supplementing it with two fungi-specific databases. In the revised manuscript, we performed further quality analyses to assess and correct for inaccuracy in the BLASTP hits. Because RefSeq aims to provide a stable reference, it is often slow in replacing older assemblies with newer ones based on improved technologies. We thus compared the RefSeq hits for species in which a newer, long-read based assembly had become available. The results are documented in Text S1 and in summary, while we did find examples of missing homologs and inconsistent sequences, the problems were isolated to specific species and the inconsistency pertains only to the tandem repeat regions. Regarding the specific example of within-species variable number of tandem repeats (VNTR) in C. auris Hil1-Hil4, we are confident of both the copy number and the sequence variation for two reasons. First, all C. auris strain genomes analyzed in this study were assembled de novo rather than based on a reference genome, and all were long-read based (PacBio) (Table S4). Second, empirically, we found the VNTR identified in Hil1-Hil4 agree among strains within one of the four clades of C. auris while differing between clades (Table S5). Since assembly errors are not expected to produce clade-specific patterns, we believe this is strong evidence for the VNTR identified being real.

    We also appreciate the reviewer’s suggestion on discussing the conservation of the repeats as an interesting trait for a group of Hil proteins in comparison to the Als family. We now added a section in Discussion focusing on the special properties of this group of Hil proteins.

    • Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

    Due to the nature of my comments, this review will not be anonymous. I will include some of the data from my laboratory to further illustrate the point about the quality of draft genome sequences, especially for gene families that contain repeated sequences. My laboratory group has spent the past several years looking at the families of cell wall genes in these species and know that the C. tropicalis genome sequence used in the current analysis is highly flawed. There is even a manuscript from several years ago that documents problems in the assembly (doi: 10.1534/g3.115.017566). There is a new PacBio sequence available that has considerably improved data for this group of genes, but still is not perfect. We designed primers and amplified the various coding regions to verify whether the IFF/HYR were correct in the draft genome sequences. For C. tropicalis, we know that 7 of the genes listed in this paper are broken (i.e. prematurely terminated) giving a false impression of their construction. The current study did not verify any gene sequences, so broken/incomplete genes are a stumbling block for developing conclusions.

    We deeply appreciate the reviewer pointing out the flaws in the C. tropicalis genome. Using the PacBio sequence-based new assembly, we were able to confirm the reviewer’s comment on the sequence and annotation error in the RefSeq assembly for C. tropicalis. We listed the comparisons between the two assemblies in Table S8. Because the differences reside outside of the Hyphal_reg_CWP domain, they don’t impact our phylogenetic analyses, which are based on the effector domain alignment. To determine if this is a widespread issue affecting all genome assemblies based on older technologies, and in response to the reviewer’s criticism, we systematically checked the sequences of BLASTP hits based on the RefSeq assemblies against newer, long-read based ones when available. As detailed in Text S1 in the revised manuscript, the problems seen in C. tropicalis were not observed in four other species. While the sample size is small, we believe the issues with C. tropicalis are likely due to a combination of specific issues with the original assembly and special properties of the genome.

    Similarly, the recent work from Cormack's lab features a PacBio C. glabrata sequence (doi: 10.1111/mmi.14707). The paper details how the authors focused on accurate assembly of the types of genes studied here. Sequences from the current project should be compared to the PacBio assembly to determine if they provide the same results.

    We compared the sequences of the three C. glabrata Hil homologs identified in the RefSeq assembly (GCF_000002545.3) to the best BLAST hits in one of the new Cormack lab assemblies for (BG2 strain, GCA_014217725.1). Two of the three proteins showed identical sequences between the assemblies. One of them is longer in the new assembly than in the RefSeq (1861 vs 1771 aa, XP_447567.2, QHS67215.1). The main difference, however, was the number of hits recovered. Performing BLASTP searches in the new assembly recovered 13 hits vs 3 from the RefSeq assembly, of which 12 were in the subtelomeric region. For this reason, we used the new assembly as the basis for the Hil homologs in our subsequent analyses. To determine if we missed homologs in other genomes due to incomplete subtelomeric regions in the RefSeq assemblies, we repeated the BLASTP search in four other genomes (Text S1). In one of the four species, C. nivariensis, we recovered one more homolog than in the RefSeq. In all other three, we identified the same number (S. cerevisiae: 0, K. lactis: 1, C. albicans: 12), suggesting that the issues seen in C. glabrata is likely specific to this species and its RefSeq assembly.

    Another part of the study that deserves additional attention or perhaps altered presentation is the idea that the Iff/Hyr N-terminal domain binds ligands. The literature on the Iff/Hyr proteins is limited. In my opinion, though, the authors of this paper could more completely present the information that is known. The paper by Uppuluri et al. is cited (doi: 10.1371/journal.ppat.1007056), but I did not see any information about their data regarding interaction of C. albicans Hyr1 with bacterial proteins mentioned in the manuscript under review. It is formally possible that the N-terminal domain of Iff/Hyr proteins does not bind a ligand. The current manuscript includes a great deal of speculation on that point, suiting it better to a Hypothesis and Theory format rather than other types of publications.

    We appreciate the reviewer’s criticism and suggestion. We made two revisions based on the comments. First, we no longer refer to the Hyphal_reg_CWP domain as ligand-binding. Instead, we refer to it as the effector domain, following existing practices in the field (Lipke 2018, PMID: 29772751, de Groot et al. 2013, PMID: 23397570). Second, during the description of the predicted structure for the domain, we mentioned that it lacks an apparent binding pocket as suggested/identified in other β-solenoid proteins with carbohydrate binding abilities. Therefore, we suggest that the potential substrate and mechanism of binding by this domain remain to be determined with further experiments. We do, however, believe that there is strong evidence for the domain being involved in adhesion. A recent study (Reithofer et al. 2021) presented structural and phenotypic characterization of three Adhesin wall-like proteins (Awp1,2,3) in C. glabrata. In particular, experimental studies of CgAwp2, a Hil family protein, showed that its deletion resulted in the reversion of the hyperadhesive phenotype in one of the C. glabrata strains. Plastic was one of the substrates being evaluated, although, as the reviewer’s work pointed out, adhesion to plastics doesn’t indicate ligand binding, as it can be mediated by non-specific hydrophobic interactions (Hoyer and Cota 2016, PMID: 27014205). Nonetheless, the results presented in Reithofer et al. 2021 and other lines of evidence presented in the current work strongly supported adhesin functions of the Hil family.

    Table 1 attempts to offer evidence that the Iff/Hyr N-terminal domain has adhesive function but falls short of convincing the reader. One of the example structural templates is a sugar pyrophosphorylase that seems irrelevant to the current discussion. In the column called "Function", the word adhesin is found several times, but no detail is presented. The only entry that offers an example ligand indicates that the domain binds cellulose which is not likely relevant for mammalian pathogenesis, the main focus of the work. Other functions listed include self-association and cell aggregation--using the N-terminal domain. It is formally possible that Iff/Hyr proteins drive aggregation using the N-terminal domain and beta-aggregation sequences in the repeated region. The authors should develop these ideas further. Discussion of adhesive/aggregative function related to the ALS family can be found in Hoyer and Cota, 2016 (doi: 10.3389/fmicb.2016.00280).

    We appreciate the reviewer’s comments. In the revised manuscript, we removed Table 1, which was based on I-TASSER identified templates. Instead, we identified similar structures in the PDB50 database to the AlphaFold2 prediction for the Hyphal_reg_CWP domain in C. auris Hil1 using DALI (Table S3). We described the functional implications based on this list as follows:

    “We identified a number of bacterial adhesins with a highly similar β-helix fold but no α-crystallin domain (Table S3), e.g., Hmw1 from H. influenzae (PDB: 2ODL), Tāpirins from C. hydrothermalis (PDB: 6N2C), TibA from enterotoxigenic E. coli (PDB: 4Q1Q) and SRRP from L. reuteri (PDB: 5NY0). For comparison, the binding region of the Serine Rich Repeat Protein 100-23 (SRRP100-23) from L. reuteri was shown in Fig. 3F (Sequeira et al. 2018). Together, these results strongly suggest that the Hyphal_reg_CWP domain in the C. auris Hil family genes mediate adhesion.”

    One line of evidence that suggest the Hyphal_reg_CWP domain may have ligand-binding activity is from the L. reuteri SRRP-BR, which is one of the bacterial adhesins identified as having a highly similar β-helical structure (but missing the α-crystallin domain). In Sequeira et al. 2018 (PMID: 29507249), the authors showed via both in-vitro and in-vivo experiments that this domain “bound to host epithelial cells and DNA at neutral pH and recognized polygalacturonic acid (PGA), rhamnogalacturonan I, or chondroitin sulfate A at acidic pH”. However, the predicted structure for the Hyphal_reg_CWP domain in C. auris Hil1 and Hil7 lack a protruding, flexible loop in the β-helix, which was proposed to serve as a binding pocket for the ligand in SRRP-BR. We therefore commented in the text “Such a feature is not apparent in the predicted structure of the Hyphal_reg_CWP domain. Further studies are needed to elucidate the potential substrate for this domain and its mechanism of adhesion.”

    We also appreciate the reviewer’s suggestion to discuss the potential role of the Hil proteins in mediating adhesion vs cell aggregation. We now have a section in Discussion that focuses on the potential role of the β-aggregation sequences especially in the subset of Hil proteins led by C. auris Hil1-Hil4, which have an unusually large number of such sequences. We discuss the recent literature suggesting the potential of such features mediating cell-cell aggregation.

    The incredibly large number of figures that focus on the repeated sequences in the genes does not appear to include mention of the idea that these regions are frequently highly glycosylated. Knowing how much carbohydrate is added to these sequences in the mature protein would also have bearing on whether the beta-aggregation potential is realized. The Iff/Hyr proteins could stick to other things based on ligand binding (adhesion), hydrophobicity, aggregative activity, etc. Not much is really known about protein function so the conclusions are only speculative. The authors are largely accurate in presenting their conclusions as speculative, but the conclusions are not developed fully and always land on the idea that the N-terminal domain has adhesive function when that aspect clearly is not known.

    We appreciate the reviewer’s comment. We have performed N- and O-glycosylataion predictions for the Hil family proteins in C. auris as a focal example and presented the results in Figure 2 of the revised manuscript. Briefly, we found that all eight proteins are predicted to be heavily O-glycosylated (Fig. 2C). N-glycosylation is rare except in Hil5 and Hil6, in regions with a low Ser/Thr content (Fig. 2C). We also deemphasized the ligand-binding ability of the effector domain and its importance in assessing the adhesin function of the Hil family proteins. At the same time, we highlighted other mechanisms as the reviewer pointed out, such as aggregative activities, in our discussion on the potential importance of the large number of β-aggregation motifs.

    Another aspect of the analysis that is not mentioned is that several of the species discussed are diploid. What effect does ploidy have on the conclusions? Most draft genomes for diploid species are presented in a haploid display, so are not completely representative of the species. Additionally, some species such as C. parapsilosis are known to vary between strains in their composition of gene families, with varying numbers of loci in different isolates.

    We appreciate the reviewer raising this issue. The potential impact of having diploid genomes represented as haploids is twofold. First, if the genome sequencing was performed on a diploid cell sample with some highly polymorphic regions, that would present difficulties to the assembly and could result in poorly assembled sections. Second, either because of the first issue, or because the researchers used the haploid phase of the organism for sequencing, the representative haploid genome will not be “completely representative of the species” as the reviewer suggested. The second problem is not specific to diploids – even for haploids, any single or collection of genomes would represent just a slice of the genetic diversity in the species. We did two things to look into this. First, we analyzed multiple strains in C. auris to reveal both Hil family size variation and also sequence polymorphism, particularly in the tandem repeat region. We also, as part of the quality control, compared and searched assemblies for different strains of some species when available. We agree that characterizing multiple genomes in a species is important for fully revealing the gene pool diversity and could have important consequences on our understanding of the emergence of novel yeast pathogens.

    Regarding the first issue, we checked the original publications for two large-scale yeast genome sequencing projects that included 10 of the 32 species in the present study (Dujon et al. 2004, PMID: 15229592 and Butler et al. 2009, PMID: 19465905). In Dujon et al. 2004, the authors stated that haploid cells were used in cases where the species has both haploid and diploid phases. In Butler et al. 2009, the authors said in the Methods that “for highly polymorphic regions of diploid genomes, initial sequence assemblies were iteratively re-assembled in regions of high polymorphism to minimize read disagreement from the two haplotypes while maximizing coverage.”. Therefore, the potential issue of heterozygosity is likely minimal. In addition, many diploid yeasts have large regions in their genomes being homozygous, both as a result of clonal expansion and also due to loss of heterozygosity (LOH), as documented in C. albicans and other Candida species (e.g., PMID: 28080987). Nonetheless, we acknowledge that this issue is yet another challenge to having high-quality, complete genome assemblies. In the discussion, we fully acknowledge the limitation of our study by genome assemblies, and believe that ongoing improvement thanks to the development of long-read technologies will allow more in-depth studies, particularly in the subtelomeric regions and for repeat-rich sequences.

    The manuscript concludes that having more genes is better, that the gene family represents diversification that must be driven by its importance to pathogenesis, without recognizing that some species evolve toward lower pathogenesis. This concept could be explored in the Discussion. …My own experience makes me wonder if the authors found any examples of species that provide an exception to the idea that having more genes is better and positively associated with pathogenesis. The parallel between IFF/HYR and ALS genes is made many times in the manuscript. Spathaspora passalidarum, a species that is not pathogenic in humans, but clearly within the phylogenetic group examined here, has 29 loci with sequence similarity to ALS genes. How many IFF/HYR genes are in S. passalidarum?

    We appreciate the reviewer’s comment. We will address the two comments above together as they are related. First of all, S. passalidarum is now included in our extended BLAST search list and we identified a total of 3 homologs in this species. When compared with the related Candida/Lodderomyces clade, which includes C. albicans, the Hil family in this species is relatively small (3 vs. >10). More generally, we observe a significant correlation between the Hil family size and the species’ pathogenic potential (Figure 1B and the phylogenetic regression result in the text).

    Regarding the first comment, we did identify two species that had a large Hil family (>8 based on C. auris) and yet were not known to infect humans. One of them, M. bicuspidata, has 29 Hil homologs and is interestingly a parasite for freshwater animals, such as Daphnia. The other species, K. africana, has 10 homologs and its ecology is not well described in the literature. With respect to the relationship between adhesin family and pathogenicity, we would like to make two points. First, as mentioned above, we observed a strong correlation between the Hil family size and the pathogen status, after correcting for phylogenetic relatedness, suggesting that expansion of the Hil family is a shared trait among pathogenic species. This doesn’t rule out the possibility that some species may have an expanded adhesin family, such as the example the reviewer mentioned, for reasons other than infecting a human host. Second, a key point in our work is that expansion of the adhesin family is only the first step – the crucial contribution of gene duplications to adaptation is not just in the increase in copy number, but also in providing the raw materials for selection to generate novel phenotypes. On that front, we documented the rapid divergence of the central domains both between and within species, as well as signatures of relaxed selective constraint and positive selection acting on the effector domain following gene duplications in C. auris, both of which support the above theme.

    There are several current taxonomies for the species in this region of the tree. The source of the names used in this paper could be specific more completely.

    We appreciate the reviewer’s comment. We now gave the complete Latin names for all species in Figure 1 and only use abbreviated names, e.g., C. auris, after the first occurrence. For species with multiple names in the literature, we followed the species name and phylogenetic placement in Shen et al. 2018 (PMID: 30415838).

    The Results and Discussion sections are largely redundant. The tone of the paper is conversational, making it easy to read, but there seems little left to say in the Discussion that has not already been mentioned as the background for the various types of analyses. The authors should revise the paper to eliminate discussions of published literature from the Results and expand the Discussion to include some of the themes that have not been mentioned yet.

    We appreciate the reviewer’s comment. In the revised manuscript, we have moved discussion points from the Result to the Discussion section. We also overhauled the Discussion to focus on the implications based on, but not already covered, in the Result part, including the points the reviewer suggested, e.g., the implications of the structure on adhesion mechanism.

    Another point that the authors do not mention is documented recombination between IFF and ALS genes (doi: 10.3389/fmicb.2019.00781) and the effect of that process on evolution among these gene families.

    We appreciate the reviewer’s comment. We now mention this and related observations in Discussion as part of the discussion on the mutational mechanisms for the evolution of the family:

    “Diversification of adhesin repertoire within a strain can arise from a variety of molecular mechanisms. For example, chimeric proteins generated through recombination between Als family members or between an Als protein’s N terminal effector domain and an Hyr/Iff protein’s repeat region have been shown (Butler et al. 2009; Zhao et al. 2011; Oh et al. 2019). Some of the adhesins with highly diverged central domains may have arisen in this manner (Fig. S10).”

    My reading of the work by Xu et al. 2021 (doi: 10.1111/mmi.14707) does not match the direction of its presentation in the current paper. Oh et al., 2021 (doi: 10.3389/fcimb.2021.794529) discussed that point recently, providing another point for the Discussion in the current paper.

    We appreciate the reviewer’s comment and agree that our original reading of Xu et al. 2021 was incorrect. Instead of suggesting a higher mutation rates in the subtelomeric region, the authors instead suggested the evolution of the Epa family in the subtelomere was driven by Break-Induced Replication. We now update our discussion in the following way, also citing Oh et al. 2021

    “Finally, as reported by (Muñoz et al. 2021), we found that the Hil family genes are preferentially located near chromosomal ends in C. auris and also in other species examined (Fig 7), similar to previous findings for the Flo and Epa families (Teunissen and Steensma 1995; De Las Peñas et al. 2003; Xu et al. 2020; Xu et al. 2021) as well as the Als genes in certain species (Oh et al. 2021). This location bias of the Hil and other adhesin families is likely a key mechanism for their dynamic expansion and sequence evolution, either via ectopic recombination (Anderson et al. 2015) or by Break-Induced Replication (Bosco and Haber 1998; Sakofsky and Malkova 2017; Xu et al. 2021). Another potential consequence of the subtelomeric location of Hil family members is that the genes may be subject to epigenetic silencing, which can be derepressed in response to stress (Ai et al. 2002). Such epigenetic regulation of the adhesin genes was found to generate cell surface heterogeneity in S. cerevisiae (Halme et al. 2004) and leads to hyperadherent phenotypes in C. glabrata (Castaño et al. 2005).”

    I might have missed it, but I could not find what constitutes a BLAST-excluded sequence (Table S7). Additional explanation (or making the explanation easier to find) would help the reader.

    We apologize for the inadvertent mistake of leaving out Table S7. In the revised manuscript, we include all hits from species that are part of the 322 species phylogeny in Shen et al. 2018. Thus, we removed the original Table S7.

    • Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.
    • Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

    Ideally, validation of all sequences would provide a stronger foundation for the work. However, that request is not realistic in terms of time or resources.

    We agree with the reviewer and appreciate the understanding. In the revised manuscript, we performed additional analyses to evaluate the accuracy and correct the sequences of the BLASTP hits from RefSeq database by comparing them to long-read based assemblies when possible. Please see previous replies to reviewers’ comments and Text S1 for details.

    • Are the data and the methods presented in such a way that they can be reproduced?

    Yes, the data and methods are documented clearly and perhaps too thoroughly in many places. A considerable amount of confidence is placed in sequences that might not be accurate and tracking details down to the amino acid residue may not be reasonable in this context. A disclaimer might help--everyone probably already knows that genome sequences are not perfect but stating that the analysis is only as good as the genome sequence acknowledges that fact.

    We appreciate the reviewer’s comment. In the revised manuscript, we tried to strike a balance between providing enough methodological details for the readers to assess the conclusions and yet also keeping the flow of the paper. We also accepted the reviewer’s suggestion by adding a disclaimer in the Discussion:

    “we acknowledge the possibility of missing homologs in some species and having inaccurate sequences in the tandem-repeat region. We believe the expected improvements in genome assemblies due to advances in long-read sequencing technologies will be crucial for future studies of the adhesin gene family in yeasts.”

    • Are the experiments adequately replicated and statistical analysis adequate?

    The idea of replicates does not really apply to this analysis. I think that the species sampled are reasonable to represent the region of the phylogenetic tree on which the analysis is focused. The authors clearly documented their computational methods in an admirable way.

    We appreciate the reviewer’s comment.

    MINOR COMMENTS:

    Figure 1 has elements that would make a nice graphical summary, but most of it should not be part of the final manuscript. For example, Panel A is repeated in Figure 2. It is not clear what Panel C means until the reader gets to Figure 2. Panel D is unnecessary. The image in Panel B is a good graphic. Endothelial adhesion is not mentioned, though. It is also debatable whether the proteins bind directly to plastic or to the body fluids that coat the plastic.

    Based on this and another reviewer’s comments, we removed Figure 1 from the revised manuscript.

    Compared to Figure 1, the information in Figure 3 is inconsistent. The "central domain" in Panel A is not central to anything as drawn, located at the end of the protein. The figure should be revised to be consistent with the majority of the authors' results.

    We appreciate the reviewer’s suggestion. The terminologies used to describe the different parts of a typical yeast adhesin vary in the literature. In the Als family literature, central domain refers to the region after the N-terminal effector domain and before the C-terminal Ser/Thr-rich stalk domain. In the Hil family proteins, there is not a clear distinction between a “central” and a “stalk” region. In Boisramé et al. 2011 (PMID: 21841123), the authors referred to the region between the Hyphal_reg_CWP domain and the GPI-anchor as the central domain. We adopted that use. We realize that this can lead to confusion especially for Als researchers. In some other literature, e.g., Reithofer et al. 2021, this part of the protein is referred to as the B-region. But we couldn’t find wide use of that term. We decided to stay with “central domain” in this work and hope that by defining the term in Figure 2A, we would avoid any confusion within the scope of this work.

    Are the low-complexity repeats mentioned in the Figure 4 legend present anywhere else in the C. auris genome or elsewhere among the species used in this study? The answer to that question may also provide evolutionary clues.

    We did find one other putative GPI-anchored cell wall protein containing this ~44aa repeat unit, but with a different effector domain (GLEYA, PF10528). This protein (PIS58185.1 in C. auris B8441), appears to be a hybrid between the repeat region of C. auris Hil1 and an N-terminal effector domain of a different family. This result fits the theme of the reviewer’s work in C. albicans and C. tropicalis on the chimeric adhesins formed between the Als and Hyr/Iff families. Due to the scope of the current work, we omitted this finding from the main result.

    Figure S1 legend. How was the distance to C. glabrata measured to call it equal?

    The original Figure S1 was removed in the revised manuscript. A consistent set of criteria was employed in deciding which BLASTP hits to include as Hil family members.

    Figure S4 could be presented better. Both diagonals have the same information. One could be emptied or could alternatively present nucleotide identity.

    The original Figure S4 was removed in the revised manuscript.

    Italicize the species names in Panel C of Figure S8.

    The original Figure S8C is now Figure S9 and we systematically checked to make sure that species Latin names are italicized. Thanks for pointing this out.

    Lines 256-257: The paper selectively samples the Iff/Hyr family and does not examine the "entire" family. Please revise.

    We appreciate the reviewer’s comment. In the revised manuscript, we no longer selectively sample species. Instead, we only exclude three species that are not part of the 322-yeast species phylogeny in Shen et al. 2018 and Muñoz et al. 2018, namely Diutina rugosa, *Kazachstania barnettii *and Artibeus jamaicensis. Our extensive BLASTP searches also indicated that the family as defined in this work is specific to the budding yeast subphylum. We therefore believe it is accurate to describe the work as examining the entire Hil family.

    • Are prior studies referenced appropriately?

    I was disappointed to see that the paper does not reference my laboratory's work at all. When ALS genes are featured so strongly in a report, it seems reasonable to include something we have done over 30+ years. Our most-recent ALS paper (Oh et al., 2021 doi: 10.3389/fcimb.2021.794529) would be a reasonable source for defending the gene numbers used in Figure 2A. Other examples of our work that directly relate to concepts in this paper were mentioned above.

    We sincerely apologize for our negligence. We are new to the fungal adhesin field through an accidental finding, and despite our effort to digest the relevant literature, we did unfortunately overlook the extensive work done on the Als family, much of which came from the reviewer’s lab. We have carefully read the papers suggested by the reviewer as well as others, and now have better incorporated prior foundational and insightful work into our result and discussion sections (see previous replies to the reviewer’s comments).

    • Are the text and figures clear and accurate?

    Suggestions for improvement are incorporated into the comments above.

    • Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

    Please present Methods and Results in the past tense. I still make the same mistake when I try to get my ideas on the page but proofread one more time and ensure the verb tenses are accurate.

    We appreciate the reviewer’s comments and have edited the Methods and Results sections accordingly.

    SIGNIFICANCE

    • Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

    The paper reads as if it is presenting preliminary data for a grant proposal. Perhaps Prof. He's lab wants to seek functional evidence for the role of the Iff/Hyr proteins. The current paper provides an exhaustive background for such a pursuit. As presented, there is little functional data for these proteins, genome sequences are not 100% accurate, but the trends noted are defendable.

    We appreciate the reviewer’s comments. We acknowledge that experimental studies will be needed to prove and further establish the functional importance of our findings. However, we believe our gene family evolutionary studies provided important novel insights and serve as an example for adhesin family evolution.

    • Place the work in the context of the existing literature (provide references, where appropriate).

    The ideas presented here are similar to those pioneered in the Butler et al. Nature paper in 2009 (doi: 10.1038/nature08064). We now have the benefit of more genome sequences so the analysis can encompass more species. C. auris adds a newer focus on part of the phylogenetic tree that was not previously emphasized. The idea of "more is better" is very simplistic, though. Parallel work for the ALS family shows complexity in gene expression levels, suggesting that some adhesins are poised to make a large contribution while others are likely to have a scant presence on the cell surface. Those concepts are not really explored in the current paper, either. See Hoyer and Cota 2016 (doi: 10.3389/fmicb.2016.00280); Oh et al. (doi: 10.3389/fmicb.2020.594531).

    We appreciate the reviewer’s comments and have included a discussion about the potential diversity of the duplicated Hil family proteins, in terms of function and their regulation in the Discussion. Also see our response to the first comment of the reviewer regarding the novelty of our hypothesis and the significance of our findings.

    • State what audience might be interested in and influenced by the reported findings.

    Potential readers would come from the fields of fungal adhesion and pathogenesis, as well as evolutionary biology.

    We appreciate the reviewer’s comments.

    • Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

    I discovered and named the ALS gene family in C. albicans and have spent 30+ years characterizing it. Most recently, my lab has focused on providing an accurate gene census and validated gene sequences for the cell wall "adhesinome" in the pathogenic Candida species. Some families are expanded and some are not. Some proteins appear only in a few species and demonstrate key roles in host-fungus interactions. There are many nuances to interpretation of what these fungi are doing from the standpoint of cell-surface adhesins and we look forward to exploring these ideas across many genomes, using validated gene sequences. We have a tremendous dataset that might make good fuel for a collaboration with Prof. He, given his enthusiasm for this area of study, as well as his outstanding expertise and perspectives on evolutionary analyses.

    We sincerely thank the reviewer for the critical analysis of our manuscript and appreciate the many suggestions for improving the manuscript.

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    Referee #3

    Evidence, reproducibility and clarity

    Summary:

    The manuscript by Smoak et al. provides considerable information gleaned from analysis of HYR/IFF genes in 19 fungal species. A specific focus is on Candida auris. The main conclusion is that this gene family repeatedly expanded in divergent pathogenic Candida lineages including C. auris. Analyses focus on the sequences encoding the protein's N-terminal domain and tracts of repeated sequences that follow. The authors conclude with the hypothesis that expansion and diversification of adhesin gene families underpin fungal pathogen evolution and that the variation among adhesin-encoding genes affects adhesion and virulence within and between species. The paper is easy to read, includes clear and attractive graphics, as well as a considerable number of supplementary data files that provide thorough documentation of the sources of information and their analysis.

    Major comments:

    • Are the key conclusions convincing?

    Overall, the authors' conclusions are supported by the information they present. However, the overall conclusion is stated as a hypothesis and that hypothesis is not particularly novel. The idea that expansion of gene families associated with pathogenesis occurs in the pathogenic species dates back at least to Butler et al. (2009; doi: 10.1038/nature08064) who first presented the genome sequences for many of the species considered here.

    One key issue with a manuscript of this type is whether genome sequence data are accurate. The authors are not the first research group to take draft genome sequence data at face value and attempt to draw major conclusions from it. The accuracy of public genome data continues to improve, especially with the emergence of PacBio sequencing. Because the IFF/HYR genes contain long tracts of repeated sequences, genome assemblies from short-read data are frequently inaccurate. For example, is it reasonable to have confidence that the number of copies of a tandemly repeated sequence in a specific ORF is exactly 21 (an example taken from Table 2) when each repeat is 40+ amino acids long and highly conserved? Table S6 would benefit from inclusion of the type of sequence data used to construct each draft genome sequence. It is also reasonable to question whether the genome of the type strain is used as a template to construct the draft genomes of the other strains. If that was standard practice, conservation of the repeat copy number among strains might be an artefact. Conservation of repeat sequences to the degree shown is not a feature of the ALS family, a point of contrast between gene families that could be explored in the Discussion.

    • Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

    Due to the nature of my comments, this review will not be anonymous. I will include some of the data from my laboratory to further illustrate the point about the quality of draft genome sequences, especially for gene families that contain repeated sequences. My laboratory group has spent the past several years looking at the families of cell wall genes in these species and know that the C. tropicalis genome sequence used in the current analysis is highly flawed. There is even a manuscript from several years ago that documents problems in the assembly (doi: 10.1534/g3.115.017566). There is a new PacBio sequence available that has considerably improved data for this group of genes, but still is not perfect. We designed primers and amplified the various coding regions to verify whether the IFF/HYR were correct in the draft genome sequences. For C. tropicalis, we know that 7 of the genes listed in this paper are broken (i.e. prematurely terminated) giving a false impression of their construction. The current study did not verify any gene sequences, so broken/incomplete genes are a stumbling block for developing conclusions.

    Similarly, the recent work from Cormack's lab features a PacBio C. glabrata sequence (doi: 10.1111/mmi.14707). The paper details how the authors focused on accurate assembly of the types of genes studied here. Sequences from the current project should be compared to the PacBio assembly to determine if they provide the same results.

    Another part of the study that deserves additional attention or perhaps altered presentation is the idea that the Iff/Hyr N-terminal domain binds ligands. The literature on the Iff/Hyr proteins is limited. In my opinion, though, the authors of this paper could more completely present the information that is known. The paper by Uppuluri et al. is cited (doi: 10.1371/journal.ppat.1007056), but I did not see any information about their data regarding interaction of C. albicans Hyr1 with bacterial proteins mentioned in the manuscript under review. It is formally possible that the N-terminal domain of Iff/Hyr proteins does not bind a ligand. The current manuscript includes a great deal of speculation on that point, suiting it better to a Hypothesis and Theory format rather than other types of publications.

    Table 1 attempts to offer evidence that the Iff/Hyr N-terminal domain has adhesive function but falls short of convincing the reader. One of the example structural templates is a sugar pyrophosphorylase that seems irrelevant to the current discussion. In the column called "Function", the word adhesin is found several times, but no detail is presented. The only entry that offers an example ligand indicates that the domain binds cellulose which is not likely relevant for mammalian pathogenesis, the main focus of the work. Other functions listed include self-association and cell aggregation--using the N-terminal domain. It is formally possible that Iff/Hyr proteins drive aggregation using the N-terminal domain and beta-aggregation sequences in the repeated region. The authors should develop these ideas further. Discussion of adhesive/aggregative function related to the ALS family can be found in Hoyer and Cota, 2016 (doi: 10.3389/fmicb.2016.00280).

    The incredibly large number of figures that focus on the repeated sequences in the genes does not appear to include mention of the idea that these regions are frequently highly glycosylated. Knowing how much carbohydrate is added to these sequences in the mature protein would also have bearing on whether the beta-aggregation potential is realized. The Iff/Hyr proteins could stick to other things based on ligand binding (adhesion), hydrophobicity, aggregative activity, etc. Not much is really known about protein function so the conclusions are only speculative. The authors are largely accurate in presenting their conclusions as speculative, but the conclusions are not developed fully and always land on the idea that the N-terminal domain has adhesive function when that aspect clearly is not known.

    Another aspect of the analysis that is not mentioned is that several of the species discussed are diploid. What effect does ploidy have on the conclusions? Most draft genomes for diploid species are presented in a haploid display, so are not completely representative of the species. Additionally, some species such as C. parapsilosis are known to vary between strains in their composition of gene families, with varying numbers of loci in different isolates.

    The manuscript concludes that having more genes is better, that the gene family represents diversification that must be driven by its importance to pathogenesis, without recognizing that some species evolve toward lower pathogenesis. This concept could be explored in the Discussion.

    The Results and Discussion sections are largely redundant. The tone of the paper is conversational, making it easy to read, but there seems little left to say in the Discussion that has not already been mentioned as the background for the various types of analyses. The authors should revise the paper to eliminate discussions of published literature from the Results and expand the Discussion to include some of the themes that have not been mentioned yet.

    My own experience makes me wonder if the authors found any examples of species that provide and exception to the idea that having more genes is better and positively associated with pathogenesis. The parallel between IFF/HYR and ALS genes is made many times in the manuscript. Spathaspora passalidarum, a species that is not pathogenic in humans, but clearly within the phylogenetic group examined here, has 29 loci with sequence similarity to ALS genes. How many IFF/HYR genes are in S. passalidarum?

    There are several current taxonomies for the species in this region of the tree. The source of the names used in this paper could be specific more completely.

    Another point that the authors do not mention is documented recombination between IFF and ALS genes (doi: 10.3389/fmicb.2019.00781) and the effect of that process on evolution among these gene families.

    My reading of the work by Xu et al. 2021 (doi: 10.1111/mmi.14707) does not match the direction of its presentation in the current paper. Oh et al., 2021 (doi: 10.3389/fcimb.2021.794529) discussed that point recently, providing another point for the Discussion in the current paper.

    I might have missed it, but I could not find what constitutes a BLAST-excluded sequence (Table S7). Additional explanation (or making the explanation easier to find) would help the reader.

    • Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.
    • Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

    Ideally, validation of all sequences would provide a stronger foundation for the work. However, that request is not realistic in terms of time or resources.

    • Are the data and the methods presented in such a way that they can be reproduced?

    Yes, the data and methods are documented clearly and perhaps too thoroughly in many places. A considerable amount of confidence is placed in sequences that might not be accurate and tracking details down to the amino acid residue may not be reasonable in this context. A disclaimer might help--everyone probably already knows that genome sequences are not perfect but stating that the analysis is only as good as the genome sequence acknowledges that fact.

    • Are the experiments adequately replicated and statistical analysis adequate?

    The idea of replicates does not really apply to this analysis. I think that the species sampled are reasonable to represent the region of the phylogenetic tree on which the analysis is focused. The authors clearly documented their computational methods in an admirable way.

    Minor comments:

    • Specific experimental issues that are easily addressable.

    Figure 1 has elements that would make a nice graphical summary, but most of it should not be part of the final manuscript. For example, Panel A is repeated in Figure 2. It is not clear what Panel C means until the reader gets to Figure 2. Panel D is unnecessary. The image in Panel B is a good graphic. Endothelial adhesion is not mentioned, though. It is also debatable whether the proteins bind directly to plastic or to the body fluids that coat the plastic.

    Compared to Figure 1, the information in Figure 3 is inconsistent. The "central domain" in Panel A is not central to anything as drawn, located at the end of the protein. The figure should be revised to be consistent with the majority of the authors' results. Structures in Panels C to E would benefit from the "through the spiral" view that is featured in Figure S9. What experimental technique was used to solve the structure in Panel E? Adding that information to the legend would be helpful to the reader. Also, the secondary structure colors seem to be reversed between the legend and domain structure. Adding the coordinates of the domains shown would help the reader to understand their location in the mature protein.

    Are the low-complexity repeats mentioned in the Figure 4 legend present anywhere else in the C. auris genome or elsewhere among the species used in this study? The answer to that question may also provide evolutionary clues.

    Figure S1 legend. How was the distance to C. glabrata measured to call it equal?

    Figure S4 could be presented better. Both diagonals have the same information. One could be emptied or could alternatively present nucleotide identity.

    Italicize the species names in Panel C of Figure S8.

    Lines 256-257: The paper selectively samples the Iff/Hyr family and does not examine the "entire" family. Please revise.

    • Are prior studies referenced appropriately?

    I was disappointed to see that the paper does not reference my laboratory's work at all. When ALS genes are featured so strongly in a report, it seems reasonable to include something we have done over 30+ years. Our most-recent ALS paper (Oh et al., 2021 doi: 10.3389/fcimb.2021.794529) would be a reasonable source for defending the gene numbers used in Figure 2A. Other examples of our work that directly relate to concepts in this paper were mentioned above.

    • Are the text and figures clear and accurate?

    Suggestions for improvement are incorporated into the comments above.

    • Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

    Please present Methods and Results in the past tense. I still make the same mistake when I try to get my ideas on the page but proofread one more time and ensure the verb tenses are accurate.

    Significance

    • Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

    The paper reads as if it is presenting preliminary data for a grant proposal. Perhaps Prof. He's lab wants to seek functional evidence for the role of the Iff/Hyr proteins. The current paper provides an exhaustive background for such a pursuit. As presented, there is little functional data for these proteins, genome sequences are not 100% accurate, but the trends noted are defendable.

    • Place the work in the context of the existing literature (provide references, where appropriate).

    The ideas presented here are similar to those pioneered in the Butler et al. Nature paper in 2009 (doi: 10.1038/nature08064). We now have the benefit of more genome sequences so the analysis can encompass more species. C. auris adds a newer focus on part of the phylogenetic tree that was not previously emphasized. The idea of "more is better" is very simplistic, though. Parallel work for the ALS family shows complexity in gene expression levels, suggesting that some adhesins are poised to make a large contribution while others are likely to have a scant presence on the cell surface. Those concepts are not really explored in the current paper, either. See Hoyer and Cota 2016 (doi: 10.3389/fmicb.2016.00280); Oh et al. (doi: 10.3389/fmicb.2020.594531).

    • State what audience might be interested in and influenced by the reported findings.

    Potential readers would come from the fields of fungal adhesion and pathogenesis, as well as evolutionary biology.

    • Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

    I discovered and named the ALS gene family in C. albicans and have spent 30+ years characterizing it. Most recently, my lab has focused on providing an accurate gene census and validated gene sequences for the cell wall "adhesinome" in the pathogenic Candida species. Some families are expanded and some are not. Some proteins appear only in a few species and demonstrate key roles in host-fungus interactions. There are many nuances to interpretation of what these fungi are doing from the standpoint of cell-surface adhesins and we look forward to exploring these ideas across many genomes, using validated gene sequences. We have a tremendous dataset that might make good fuel for a collaboration with Prof. He, given his enthusiasm for this area of study, as well as his outstanding expertise and perspectives on evolutionary analyses.

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    Referee #2

    Evidence, reproducibility and clarity

    Summary

    Gene duplication and divergence of adhesin proteins are hypothesized to be linked with the emergence of pathogenic yeasts during evolution; however, evidence supporting this hypothesis is limited. Smoak et al. study the evolutionary history of Hil genes and show that expansion of this gene family is restricted to C. auris and other pathogenic yeasts. They identified eight paralogous Hil proteins in C. auris. All these proteins share characteristic domains of adhesin, and the structural prediction supports that their tertiary structures are adhesin-like. Evolutionary analysis of protein domains finds weak evidence of positive selection in the ligand-binding domain, and the central domain showed rapid changes in repeat copy number. However, performed tests cannot unambiguously distinguish between positive selection and relaxed selection of paralogs after gene duplication. Some alternative tests are suggested that may be able to provide more unambiguous evidence. Together with these additional tests, the detailed phylogenetic analyses of Hil genes in C. auris might be able to better support the hypothesis that the expansion and diversification of adhesin proteins could contribute to the evolution of pathogenicity in yeasts.

    Major Comments

    The authors present extensive analyses on the evolution of Hil genes in C. auris. There is significant merit in these analyses. However, the analyses conducted so far are incomplete, lacking proper consideration of other confounding factors. Detailed explanations of our major comments are listed below.

    1. First, the authors restricted genes in the Hil family to those only containing the Hyphal_reg_CWP domain. Yet, previous work included genes containing the ligand-binding domain or the repeat domain as Hil genes. More justification is needed whether the author's choice represents the natural evolutionary history of Hil genes appropriately. For instance, are the genes only containing the ligand-binding domain monophyletic or polyphyletic? We recommend including the phylogeny of all the Hil candidate genes, to discern whether evolutionary histories of the repeat domain and ligand-binding domain are congruent. Authors can use this phylogeny as justification to focus only on the ligand-binding domain containing genes.
    2. In the analysis of positive selection, the authors do not adequately control for the effect of recombination on the evolutionary histories of protein sequences, especially given that Hil genes are rich in repetitive sequences. To account for recombination, GARD, an algorithm detecting recombination, should be performed to detect any recombination breakpoints within a protein domain. If recombination did occur within a protein domain, the authors should treat the unrecombined part as a single unit and use the phylogenetic information of this part to proceed with PAML analysis, instead of using the phylogeny of the entire protein domain. The authors should consider doing GARD analysis for the ligand-binding and repeat domains. For the repeat domain, low BS values in Fig. 5C indicate recombination between repeat units. Thus, the authors should analyze each repeat unit with GARD and re-analyze dN/dS.
    3. The authors concluded positive selection in the ligand-binding domain based on the branch-wise model of PAML. Yet, w values were not higher than one, and it's unclear whether the difference in selective pressures the authors claimed here is biologically significant. Overall, what the authors present so far seems to be weak evidence of positive selection but is much more consistent with variation in the degree of purifying selection or evolutionary constraint. Using the site-wise model (m7 vs. m8) in PAML would allow the authors to detect which residues of the ligand-binding domain underwent recurrent positive selection. Combining the evolutionary information of protein residues and the predicted 3D structure will provide molecular insights into the biological impact of rapidly evolving residues. This would be a significant addition and raise the significance of the study, besides providing potentially stronger evidence of positive selection.

    Minor Comments

    1. In Fig 1c, the figure legend should include more specific details: which adhesin proteins are shown here? Please specify species names on the species tree
    2. In Fig 3E, secondary structures are labeled with the wrong colors. Sheet: purple, helix: yellow
    3. What's the ligand-binding activity of the b-solenoid fold? How structurally similar are C. auris PF 11765 domains compared to C. glabrata Awp domains? This information will support the role of adhesin for the ligand-binding domain of Hil genes.
    4. In lines 248-249, the authors should also consider the influence of evolutionary history. For instance, repeats within the same Hil protein appeared later in evolution, compared to Hil gene duplication, and therefore these repeats experience less time for sequence divergence.
    5. Although the bioinformatic evidence of C. auris Hil genes acting as adhesins is strong, it is still worthwhile to discuss the experiments of confirming the function of adhesins.

    Significance

    Overall, this study is interesting to investigate the evolutionary history of a crucial virulent gene in C. auris. Such evolutionary understanding will help us identify critical molecular changes associated with the pathogenicity of an organism during evolution, providing insights into the emergence of pathogens and novel strategies to cure fungal infections. The research question is important; however, the current analyses on the positive selection are incomplete, so the conclusion is modest so far. We recommend that the authors re-do the PAML analysis with the above considerations. This work will bring more significance to the mycology field if the functional impact of rapid evolution in protein domains can be supported or inferred.

    This manuscript is well-written, and the authors also did a great job specifying all the necessary details in the M&M.

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    Referee #1

    Evidence, reproducibility and clarity

    The manuscript by Smoak et al., provides an analysis of the Hyr/Iff-like (Hil) genes in Candida species with a strong focus on C. auris. The authors demonstrate a repeated expansion of these genes in unique lineages of fungal species, many of which are associated with stronger clinical disease. There is evidence of selection operating on the gene family in the primary domain used for identification. These genes include a repeat just downstream of that core domain that changes frequently in copy number and composition. The location of these genes tends to cluster at chromosome ends, which may explain some aspects of their expansion. The study is entirely in silico in nature and does not include experimental data.

    Major points

    Altogether, many of the general findings could be convincing but there are some aspects of the analysis that need further explanation to ensure they were performed correctly.

    To start, a single Hil protein from C. auris was used as bait in the query to find all Hil proteins in yeast pathogens. Would you get the same outcome if you started with a different Hil protein? What is the basis for using Hil1 as the starting point? It also doesn't make sense to me to remove species just because there are already related species in the list. This may exclude certain evolutionary trends. Furthermore, it would be helpful to know how using domain presence and the conservation of position changes the abundance of the gene family across species? (beginning of results).

    A major challenge in the analysis like this one is in dealing with repetitive sequences present in amplified gene families.

    • For example, testing modes of selection on non-conserved sites is fraught. It's not clear if all sites used for these tests are positionally conserved and this should be clarified. Alignments at repeat edges will need to maintain this conservation and relatively good alignments as stated in lines 241-242 are concerning that this includes sequence that does not retain this structure necessary for making predictions of selection.
    • It's also unclear to me why Figure S12 is here. The parameters for this analysis should be tested ahead of building models so only one set of parameters should be necessary to run the test. The evolutionary tests within single genes and across strains is really nice!
    • A major challenge for expanded gene families is rooting based on the inability to identify a strong similarity match for the full length sequence. The full alignment mentioned would certainly include significant gaps. If those gaps are removed and conserved sites only are used, does it produce the same tree? Inclusion of unalignable sequences would be expected to significantly alter the outcomes of those analysis and may produce some spurious relationships in reconciling with the species trees.
    • Whether or not there are similar issues in the alignment of PF11765 need to be addressed as well. There's nothing in the methods that clarifies site selection. Figure 1A: the placement of evolved pathogenesis is a little arbitrary. It's just as feasible that a single event increased pathogenesis in the LCA of C. albicans and C. parapsilosis that was subsequently lost in L. elongisporus. These should be justified or I'd suggest removing. The assignment of Candida species here also seems incomplete. The Butler paper notes both D. hansineii and C. lusitaniae as Candida species whereas they are excluded here. It is tricky to include scaffolds in analysis of chromosomal location of the HIL genes. The break in the scaffold may be due to the assc repeats of these proteins alone or other, nearby repeats. Any statistics would be best done to include only known chromosomes or those that are strongly inferred by Munoz, 2021. This will change the display of Figure 7, but is unlikely to change the take home message.

    Minor points

    Line 18: "spp." Should be "spps."

    Line 41: I might rephrase this as "how pathogenesis arose in yeast..."

    I might use a yeast-centric example around line 40 for duplication and divergence. This could include genes for metabolism of different carbon sources in S. cerevisiae.

    The Butler paper referenced on line 51 compared seven Candida species and 9 Saccharomyces species The autors state no other evolutionary analysis of adhesins has been performed but do not acknowledge this study: https://academic.oup.com/mbe/article/28/11/3127/1047032

    The first paragraph of the Results could be condensed

    How was the species tree in Figure 1A obtained?

    Figure 2: In panel A, "DH" and "SS" are not defined. I'd be careful with use of "non-albicans Candida" in Figure 2B. This usually includes C. tropicalis and C. dubliniensis and may confuse the reader. How was the binding domain defined to extract those sequences are produce a phylogeny? In building a ML model, how were parameters chosen?

    Figure 3C/D could be just one panel.

    Can you relate more the fungal hit to the Hil proteins conveyed in lines 152-154?

    Line 168: Should read "Hence, ..." Label proteins along the top of Figure 4 too.

    Figure 5: for tests of selection, were sites conserved across the group? What does the black number at each node indicate? Dn and Ds are given as decimals. This is based on what attribute? For panel B, it is unclear what each tip denotes i.e., Hil1_tr6. Hil1 is the gene but what is "tr6"?

    It's unclear why comparison of the PF11765 domain includes the MRD proteins when those aren't included in the comparison to the repeats alone. Could that skew the comparison due to unequal sample numbers or changed variation frequencies in MDR relative to the other two groups?

    Table 2 doesn't add much. This section could probably be reduced to a few sentences since it's highly speculative (intraspecies variation).

    Table 3 is not needed.

    Figure 6 - color coding in 6A needs to be explained. I'm assuming this is a taxonomical coding.

    Figure 1B is unnecessary. A Model of the protein indicating domains is sufficient here. Figure 1C needs labels for all termini, not just the pathogenic red branches. The figure doesn't provide clear association between adhesin families and the associated species. This could be omitted, especially since Flo is often associated with Saccharomyces species. Figure 1D is unnecessary.

    Significance

    The work here is sorely needed in expanded gene families and in fungi specifically. No analysis at this level has been performed, to the best of my knowledge, in any fungal associated gene family and certainly not in relationship to pathogenic potential. The authors do a good job in citing the foundational literature upon which their study builds in most cases (one exception is noted above). It would be of general interest to those interested in the evolution of virulence, but the analysis is tricky. This is the biggest drawback I currently have as some of the information to assess the results is missing. Expertise: gene families, evolution dynamics, human fungal pathogens

  7. Version published to 10.1101/2022.02.09.479577v1 on bioRxiv
  8. Version published to 10.1101/2022.02.09.479577v2 on bioRxiv