In vitro culture of freshly isolated Trypanosoma brucei brucei bloodstream forms results in gene copy-number changes

  1. Julius Mulindwa
  2. Geofrey Ssentamu
  3. Enock Matovu
  4. Kevin Kamanyi Marucha
  5. Francisco Aresta-Branco
  6. Claudia Helbig
  7. Christine Clayton

Reviewed by

Read the full article See related articles

Listed in

Log in to save this article

Abstract

Most researchers who study unicellular eukaryotes work with an extremely limited number of laboratory-adapted isolates that were obtained from the field decades ago, but the effects of passage in laboratory rodents, and adaptation to in vitro culture, have been little studied. For example, the vast majority of studies of Trypanosoma brucei biology have concentrated on just two strains, Lister 427 and EATRO1125, which were taken from the field over half a century ago and have since have undergone innumerable passages in rodents and culture. We here describe two new Trypanosoma brucei brucei strains. MAK65 and MAK98, which have undergone only 3 rodent passages since isolation from Ugandan cattle. High-coverage sequencing revealed that adaptation of the parasites to culture was accompanied by changes in gene copy numbers. T . brucei has so far been considered to be uniformly diploid, but we also found trisomy of chromosome 5 not only in one Lister 427 culture, but also in the MAK98 field isolate. Trisomy of chromosome 6, and increased copies of other chromosome segments, were also seen in established cultured lines. The two new T . brucei strains should be useful to researchers interested in trypanosome differentiation and pathogenicity. Initial results suggested that the two strains have differing infection patterns in rodents. MAK65 is uniformly diploid and grew more reproducibly in bloodstream-form culture than MAK98.

Article activity feed

  1. Version published to 10.1371/journal.pntd.0009738
  2. Version published to 10.1101/2021.06.10.446608v2 on bioRxiv
  3. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #4

    Evidence, reproducibility and clarity

    Summary:

    In this study, the investigators describe two new Trypanosoma brucei brucei strains wheich have been subjected to minimal passage in rodents or in culture. In addition to characterizing some of the phenotypic and genetic characteristics of these isolates and lines derived from them the authors also characterize the changes in gene copy numbers occurring during in vitro passage. While this study illuminated the impact of in vitro culturing for adaptation that might have been overlooked for years in unicellular eukaryotes, the experimental design and method description make their conclusions less convincing.

    Major comments:

    My main discomfort with this work is that it provides just enough information to be interesting and perhaps important, but not enough to be definitive. Part of this is not the fault of the authors - especially in dealing with various "lab" strains and their genomes - over which they have no control in terms of where and how they were isolated, maintained and investigated. But the authors seem to add to this problem by not determining the clonality of their new strains, failing to provide a full genome sequence (although they seem to have the data they need - including long-read sequencing - to do so), and with often vague descriptions of the analyses they performed as part of this report. My biggest concern has to do with the population structure of the beginning parasites set and to what extent the cultivation - even though limited - is selecting for variants within an existing non-clonal population rather than showing evidence of evolution of a (mostly"??) clonal population. The authors note that they have not cloned so as to "minimize manipulation" - which is sensible. But the provided references (particularly Ref 21) use microsatellite markers to establish wide clonality in populations in individuals. Although the authors have not indicated it here, one would presume that that "evolution" being observed in their lines over time (in animal or in culture) have not altered the microsatellite signature of the lines (thus are still clonal based upon standards of Ref 21), but has resulted in genetically and biologically altered lines - i.e. clonal variants. It seems without knowing the complexity of the beginning populations (granted - not easy), it is hard to say whether the changes over time are due to selection of a subset of the initial population, genetic changes in an initially clonal population, or a combination of the two. Indeed, a selection process would explain the unexpected differences found in early sampled (low parasitemic but high stumpy) and late sampled (high parasitemic but low stumpy) lines as well as the erratic growth in culture. The authors seem to go back and forth on this issue but the key problem is that there is not enough information here to understand this clearly, and for that reason, the work, although considerable, adds mostly anecdotal observations but relatively little definitively. The authors attribute gene/chromosome ploidy changes under in vitro culturing as adaptation of parasites due to chromosome replication and/or segregation. But this conclusion can not be reached unless the populations were clonal at the beginning. Related to this point, it is surprising that there is not a comparison between the A and B lines of each isolate to each other (e.g. 65A/65B). If the isolates are clonal to begin with then one would expect little difference between the 2 harvested 1 day apart from different rats.

    Overall the manuscript is difficult to follow and interpret, very light on details and Figure 2 is very confusing and is not particularly helped by the author's summary of them. A little more detail on how the experiment was done might help. It should be made clear and explicitly stated that the cultures were split (by how much/to what level - seems like it is 0.5 x 10e6?) once cultures reached what level (there doesn't appear to be any pattern there - so are they split every 24hrs unless they have declined?). Readers should not have to go to a previous publication to find these types of details needed to interpret the results. The text refers to "diluting them" but presumably a portion of the culture was reseeded/cultured - or was there a constant dilution of the culture over time? The authors refer to a "slowed growth" after 1-2 days, but 3 of the 4 cultures also declined again between 6 and 11 days. This is not consistent with the hypothesis that the rebound after 2-3 days was the result of an adaptation to a depleted component (if so, why would an additional "adaptation" be necessary?). 2E seems to have been handled differently from A-D. The growth curves in S2 fig do not exhibit the same drops as evident in the Fig 2 cultures.

    A fundamental finding of this research is detecting the gene copy number variation from the sequencing results of the strains after in vitro passages. However, the description of how to processing the sequencing reads was used to determine the gene copy number is vague. The description lacks basic information like the analysis workflow, software packages, parameters, and other important details. These details are the keys to support their conclusion.

    According to the authors, only one representative was considered for multicopy genes. But what is the criteria to call 'multicopy genes' here? How homologous these multicopy genes are set to be? The authors also mentioned that reads may also map to homologous genes, how is this issue dealt with during the analysis?

    Overall, the study seems rushed and too preliminary; much of the writing is loose and lacking in details. The authors mention that they have long read nanopore sequence but don't appear to use it to appropriately address some of the questions (e.g. Line 195 "In the meantime..."). As a result, although the results are intriguing (but not totally surprising - this work uncovers a bit of the dirty little secret most scientist realize underlies the pathogen strains that we often present as stable entities while knowing that they have and are changing over time), the study presents more questions than it answers - as the authors seem to acknowledge in their final paragraph.

    Minor comments:

    Line 79-83 - statements require some references The strain "A/B" nomenclature comes into use in the manuscript (line 129 and Fig 1 legend) without defining what the difference between A and B is (apparently this is the samples from 2 different cultures (Line 187) or from different rats - but it takes a bit of work to figure that out. - 1C could be interpreted to mean that the 2 rats got infected by either the A or B lines - or that the resulting lines were named based on the rat they came from, or they are just different cultures of the same stabilate).

    Line 141 "firmly confirmed" sounds a bit off - just "confirmed" or "firmly supported", perhaps better. Line 140/141 - S fig 2 a bit hard to understand - as is the remaining paragraphs on culture outcomes. As this is expressed as a ratio, could it not be argued that polyA+ enriches for (or ribo-minus "depletes" - using the author's treminology) short RNAs (or that ribo-minus enriches for longer)? It does seem likely that the relatively rare extra-long RNAs are underrepresented in the poly A+ method but not clear that this shows anything other than that the different techniques have different strengths/weaknesses.

    Line 156 ."... had run out of a nutrient..."

    Line 170: "several additional attempts ..." these were from the mouse blood "stabilates"?

    Line 188 and 189, figure S1 is figure S2, not S1.

    Line 192, comma is in the wrong place.

    Line 225: do you mean 'figure 4E' instead of 'figure 4B'. It would be informative if the authors could provide a statistic comparison of frequency of copy number alteration between tandem repeated genes and those that are not in tandem to support their statement in line 293-294.

    For the figures with chromosomes displayed, are these data points from the copy number of each unique gene? Or are they the average gene copy number per region? The chromosome number should be in order, Chr10 and Chr11 should be after Chr9, not the Chr1.

    Significance

    There is a lot of good information here, but it could be more clearly presented and better detailed. Placement in the literature is fine - although comparison to long-read sequenced T. brucei or T. cruzi genomes might deserve mention.

  4. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #3

    Evidence, reproducibility and clarity

    Summary

    Most laboratory research using T. b. brucei has made use of two strains, the monomorphic Lister 427 strain and the pleomorphic EATRO1125 strain. These strains have been passaged in vitro for decades in separate laboratories, thus selecting for populations that differ from both the original isolate and between laboratories.

    In this study, Mulindwa et al. describe the isolation of two new T. b. brucei strains from cattle in Uganda, MAK65 and MAK98, which show differences in virulence and propensity for stumpy form differentiation in rodents. To assess the effect of culture adaptation on trypanosomes, the researchers compared the gene copy number of the MAK65 and MAK98 isolates before and after culture adaptation. The study found that isolates cultured for as little as a week already demonstrated a broader gene copy number distribution than those that were not culture adapted. Broader gene copy number distributions, compared to the non-culture-adapted isolates, were also observed for a number of routinely-passaged Lister 427 and EATRO1125 cultures. The researchers observed reproducible increases in copy number for certain genes, such as those encoding histones, HSP70 and PFR proteins. The study postulated that changes in gene copy number observed across the genome increased bias towards rapid proliferation and stress tolerance upon culture adaptation.

    Major comments

    I have some concerns about the method that was used for the copy-number calculations. Firstly, I can imagine that a non-uniform distribution of the reads across the genome for any of the datasets could influence the results. Was this checked? Secondly, in the methods section lines 394/395 it is said that the modal RPKM for each dataset was 'adjusted slightly' to get a symmetrical distribution. Upon checking the modal RPKMs and the adjusted values used for the calculations, the adjusted values appear to have been adjusted to different extents between the different datasets to fit the authors assumptions. Do the authors believe that this could perhaps account for some of the subtle gene copy number changes observed (as is discussed in lines 287-290)? Next, why were the reads aligned 20 times? I think in general the method needs to be explained far more clearly so that the audience can understand what you did.

    Minor comments

    Additional experiments:

    Would it be possible to generate a phylogenetic tree comparing these new isolates with the Lister 427, TREU927 and EATRO1125 isolates in circulation to get an idea of how these strains may have evolved? I this could add to the strength of the manuscript.

    Title: Since no other unicellular eukaryotes are mentioned throughout the text, I think a more appropriate title for this study might be 'Adaptation of Trypanosoma brucei brucei bloodstream forms to in vitro culture results in gene copy-number changes.'

    Line 59: There have been more recent studies than the referenced paper (Cross et al., 2014) that quote far higher numbers of alternative VSG genes or pseudogenes in the Lister 427 strain. In Müller et al (2018, doi: 10.1038/s41586-018-0619-8) over 2500 VSGs are quoted and in Cosentino et al (2021, doi: 10.1101/2021.04.13.439624) 2872 VSGs are identified.

    Line 109/110: The dates of isolation written here, Feb 1st and July 30th 2016, are different to what is written under the Date of Isolation column in Supplementary text 1, table 1- 25/5/2016 and 30/7/2017. Do these two dates represent different things?

    Line 233: Should Figure 5 A, B, C and E (rather than A, B, D and E) be referenced here to show all the initial, not cultured results?

    Line 270/271: PIP39 does not promote differentiation to stumpy forms, but instead contributes towards the efficient differentiation of stumpies to procyclic forms (Szoor et al, 2010, doi: 10.1101/gad.570310).

    Discussion:

    It should be discussed in the text that changes in gene copy number have also been observed upon Leishmania culture adaptation (see, for e.g., Gerald Späth's work). This will strengthen the authors' conclusions. Furthermore, similar observations of aneuploidy and triploidy in some T. brucei Lister 427 strains have recently been reported in Cosentino et al (2021, doi: 10.1101/2021.04.13.439624). This could also be referenced somewhere in the text.

    Line 364: I think the Nijuru et al (2005, doi: 10.1007/s00436-004-1267-5) paper would be the correct reference here since it describes the use of the ITS-1 PCR. Reference 13 is actually referring to another paper, I cannot find Nijuru et al in the references list.

    Line 379: PAD staining should be referenced to be more informative and allow reproducibility.

    Figure 1, Line 580: How many cells were counted for determining the % PAD positivity?

    Figure 1, Line 581: Scale bar should be included in D.

    Supplement Text 1:

    I found Supplement Text 1 a little confusing for two reasons. Firstly, I was never sure if the tables or references being referenced were from the main text or from the supplement text 1, perhaps this could be made a little clearer to aid the reader. Secondly, the names of the isolates switched between, for e.g., MAK 65 and Tb065. For simplicity it could help to try and stick to one naming system.

    It might be worth adding a sentence about why Tb236B was not followed up. Was this because it could not easily be distinguished from MAK65 by microsatellite analysis?

    S3 Figure: Legend describes red bars but there are none in the figure.

    Table 2: In the legend for Sheet 2, the cut-off for the increase is missing.

    Significance

    Though the T. b. brucei Lister 427 and EATRO1125 strains are used most commonly for laboratory-based research, they have been extensively passaged in vitro without characterisation of the changes that have occurred between them and the original isolate, or indeed, between laboratories.

    Mulindwa et al. demonstrated that changes to gene copy number occur rapidly upon adaptation to culture of field isolates, and that different cultures of the same isolate can furthermore have different ploidies. This is an important advance and raises awareness a) that trypanosomes undergo changes upon laboratory adaptation, b) of the nature of some of these changes and c) that the changes can occur rapidly. Changes to gene copy number have also been shown to effect Leishmania donovani upon culture adaptation (Prieto Barja et al, 2017, doi: 10.1038/s41559-017-0361-x).

    This study will be of interest to the trypanosome community in general, but particularly those who work on biology that we already know is impacted by prolonged in vitro passage-differentiation, virulence and antigenic variation.

    Reviewer expertise: BSF differentiation, antigenic variation

  5. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #2

    Evidence, reproducibility and clarity

    Summary:

    Trypanosoma brucei brucei is a protozoan parasite studied both because it is the cause of Human African Trypanosomiasis, and as a unicellular eukaryotic model organism. However, only few isolates are lab-adapted and most literature focuses on derivatives of Lister 427 and EATRO1125, which have both been cultured under in vitro conditions for several decades. In this manuscript, Mulindwa and colleagues describe and characterise two novel T. b. brucei strains (MAK65 and MAK98) isolated from the field with minimal passage through rodents. These new strains are clearly more closely related to trypanosomes in the field, compared to the aforementioned in vitro models. The authors investigate infection dynamics in murine models, in particular to assess differentiation capabilities of the parasites. Furthermore, optimisation of in vitro adaptation is also attempted successfully. Finally, the authors show, through genome sequencing, that adaptation of both strains to laboratory-based culture affects gene ploidy, and several examples of interest are discussed. A key conclusion is that cultured lines from the same original isolate can rapidly (in a matter of weeks) develop karyotype differences, which could carry implications for the study, as well as genetic manipulation of these organisms. The availability of novel laboratory strains for the study of T. b. brucei is a significant outcome for the trypanosome research community.

    Major comments:

    The key conclusions, in particular that adaptation to in vitro culture results in reproducible genomic alterations are convincing. In my opinion, this is a descriptive study, in that the underlying causes (and consequences) of the findings are not investigated further.

    The authors state several hypotheses based on their results in the 'Outlook' section. The majority of these hypotheses are valid points to make, but I feel the following should be toned down: Lines 321-323 - These hypotheses are speculative, based on available data, and should be revised. There are likely many factors that will impact parasite growth in initial stages of culture adaptation, but most commonly there is a selection bottleneck effect that will impact initial growth.

    Line 344 - With the data presented, it is difficult to say whether tissue distribution is different between the two trypanosome strains. I would suggest removing this claim, unless work was carried out to investigate differences in tissue distribution.

    Changes in gene copy number is discussed, but one interesting aspect is whether this translates to changes at the protein level (e.g. are there increases in HSP70 mRNA or protein levels after in vitro adaptation?). Whilst not essential, carrying out qPCRs or Western blots to confirm this would enhance the impact of this study. If these experiments are not carried out, this point should be added to the discussion.

    It would be very interesting to further analyse the genomics data to assess whether there are further changes to metabolic gene copy number, perhaps as a result of in vitro adaptation. These changes could be linked to the high levels of nutrients available in HMI-9 medium. Currently, only a pteridine transporter is mentioned, although the tables list several genes such as glycerol kinase and an arginine transporter. Are there changes in glucose transporter copy number after culturing these strains? Copy number of this array can often vary in field isolates.

    The arginine transporter, AAT5 was previously shown to be an essential transporter (PMID: 28045943). Loss of copy numbers could reflect reduced need in a nutrient-rich environment such as in vitro culture medium. I feel this may be worth mentioning, but not investigating further.

    More detail is required in the Materials and Methods section, in particular the "sequence analysis" section: Which Illumina kits were used? What tool/software was used for genome alignment? Which reference genome was used (if TREU 927, what version)? What parameters were used for tryprnaseq and DeSeqU1 (if default settings were used, please mention this)? What tool/software was used for gene copy analysis (i.e. the alignment that was restricted to 20 alignments)? How was modal RPKM value adjusted to obtain a symmetrical distribution? These details are essential for this work to be reproducible. In addition, they would help establish a pipeline that can be used to directly compare other novel field isolates.

    In the RNA preparation section (line 372), please indicate replicate number for each sample group used for transcriptomics analysis, as well as parasitaemia or cell number used for extractions. In addition, if RNA extraction was carried out according to the Trifast manual, please state this.

    The protocol for staining with PAD1 requires more detail (line 380). If this protocol is available in a previous study, it is sufficient to reference this.

    The study mentions attempts to adapt cells using methylcellulose (line 179). It would be helpful for the reader to know what percentage (w/v) was attempted. In addition, did the authors consider using serum supplements from different host sources (e.g. goat or adult bovine?). If only FBS supplementation was attempted, it would be worthwhile mentioning this.

    This reviewer is not an expert on statistical analysis of genomics data, but it may be of interest to carry out statistical analysis of the differences in copy number between non-culture-selected and culture-selected parasites (figure 6) to determine whether these differences are significant.

    In my opinion, experiments are adequately replicated.

    Minor comments:

    Line 136 - What is the rationale of calculating Log2 fold changes of 65A/98A to compare to log2 fold change of ST/SL? Given the authors are in possession of normalised read count data for all 4 sample groups, it would also be interesting to show correlation between the individual datasets (e.g. 65A vs 98A, 65A vs ST, 65A vs SL, etc). Perhaps this would be more informative, and give an idea whether, for example, 65A is more similar to previously published datasets derived from stumpy or slender parasites.

    Prior studies are referenced appropriately, with the following exception: Line 70 - note T. b. gambiense as an example of African trypanosome that does not undergo sexual recombination (reference PMID: 26809473)

    To make the text and legends clearer, it would be beneficial to add commas to numbers >1,000. In addition, text would be more legible if spaces are added between numbers and units (e.g. 480 bp, instead of 480bp), with the exception of temperature and percentages. There are also inconsistencies in spacing around the multiplication symbol when stating cell densities (line 170: 1.5 x106/ml; line 176: 5x 105/ml) - please add spacing on both sides.

    In figures 1A and 1B, y-axis numbering is not consistent (i.e. 1A is linear, 1B is logarithmic) I would recommend maintaining consistency between these two experiments.

    In figure 1C, the 'A' and 'B' variants of the MAK strains are not defined in the legend, nor main text. It would be helpful for the reader to know what is meant by'98A' vs '98B'.

    In figure 1E, statistical test used to generate R and R2 are not indicated.

    In figure 2, please make y-axis scale consistent (e.g. 2A consistent with 2B, 2C consistent with 2D) as this makes it much easier for the reader to compare and contrast the data2.

    In all figures showing gene copy number overviews (4, 5 and S3), the chromosomes not in order (i.e. chromosomes 10 and 11 should come after 9). I feel these figures would be improved by keeping chromosomes in increasing number, left to right.

    In figures 5A and 5B, does the 'c' refer to culture or clone? This should be clarified. In addition, it is difficult to tell which colour represents which culture/clone in panel A in particular.

    Line 308 - Could the authors explain why the translation factor eIF3c result (significant decrease in copy number) is an "odd" one?

    In the legends for Tables 1 and 2 it is worth mentioning that the "Tb927" prefix has been removed for legibility.

    Several genes/proteins are discussed in the study (e.g. HSP70, histones). However, the implications of these changes, and their potential significance, are not discussed. A paragraph on what these changes could mean for the biology of the parasite would be of interest.

    As mentioned above, lack of PAD1 staining in MAK98 does not necessarily mean differences in tissue distribution compared to MAK65 and this sentence should be revised.

    Can the authors comment on expected differences in drug sensitivity in these strains compared to Lister 427 and EATRO1125? For example, changes in pteridine transporter copy number, if reflected at the protein level, could impact anti-folate uptake.

    A previous study investigating transcriptomics of culture-derived vs. in vivo derived T. brucei concluded that in vitro-cultured cells can be used as alternatives to animal-derived parasites (PMID: 29606092). How do the results presented here impact the findings of this previous study?

    Significance

    The availability of new strains to study African trypanosomes is significant. Furthermore, low passage number means that these strains more accurately reflect naturally occurring strains in the field, compared to the commonly used EATRO1125 and Lister 427, both of which have been adapted for laboratory use for decades.

    The finding that adaptation to laboratory culture has a significant effect on gene copy number is also of importance, and suggests variation in karyotype between strains in different labs is common, even if they are derived from the same original isolate. The logical next step is to find out how these karyotype differences impact cell biology.

    Few trypanosome strains are routinely used in a laboratory setting, in particular the monomorphic Lister 427 and the pleomorphic EATRO1125 (AnTat1.1). The adaptation of two novel strains with minimal passage and differing virulence is a significant outcome. In the past, adaptation involved growing parasites on feeder layer cells but addition of cysteine removes this requirement (PMID: 4045385). Comparison of culture- and animal-derived T. brucei has been carried out before (for example, PMID 29606092), and in addition, genomic analysis has previously suggested aneuploidy does not occur (PMID: 30256189). Therefore, the finding that adaptation to in vitro culture can result in changes in gene copy number is novel, and significant. It is unknown whether these changes are reflected at the mRNA or protein level and this is an important next step.

    The main audience for these findings is the trypanosome research community, especially groups working on the genomics of African trypanosomes. In addition, the findings are of significance (as mentioned in the manuscript) to researchers designing genetic manipulation experiments with culture-derived trypanosomes.

    The background of this reviewer is in biochemical parasitology, with work focusing on livestock trypanosomes (Trypanosoma congolense, Trypanosoma vivax). Key words: Metabolism, Metabolomics, Transcriptomics, Drug mode of action, Drug resistance.

  6. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #1

    Evidence, reproducibility and clarity

    Summary:

    The authors present an analysis of gene copy number in Trypanosoma brucei lines based on resequencing. The analysis includes 2 strains isolated very recently, which are sequenced straight from passage in animals and following culture in flasks. They then compare gene copy number in these strains to T. brucei lines commonly used in the lab and reference DNA probably isolated after multiple passages through animals, concluding that there are some genes that consistently change copy number on adaptation to culture. There is some overlap with the authors' previous work [PMID: 26715446] comparing isolates of T. b. rhodesiense (data also included here), but here they have the addition of lines pre and post adaptation to culture, and focus more on gene copy number over transcriptomic changes.

    The question is a really interesting one: what are labs selecting for when they adapt these parasites to culture? The authors generate some useful data on this subject and suggest some of the additional analysis that could be done with these data in future in the Outlook section. However, I have 2 major comments about the analysis presented that I believe affect whether it can be used to support the conclusions made in this manuscript.

    Major comments:

    1. In the analysis, the authors' discuss variation in measured copy number as if representing genuine changes in gene number. However, variation can also result from differences in sequencing depth or be introduced during DNA isolation, processing, sequencing and/or mapping. In my opinion, this variation is not adequately dealt with in the analysis presented and as a result at least some of the subsequent interpretations are likely to be incorrect. While array copy numbers in particular would be expected to become more heterogeneous as a population ages, this is unlikely to affect the majority of diploid genes and should not greatly influence the distribution around copy number of 2. Moreover, where average diploid genes do change, they are expected to do so across whole chromosomes or large sections of chromosomes, which does not appear to be the pattern seen in S3 Fig. Moreover, heterogeneity in the population of chromosomes present in the culture resulting from changes in replication/segregation [as suggested in the text] would affect the spread of copy numbers between chromosomes, but not the distribution on each chromosome (as the genes are still linked even when the average chromosome copy number is non-integer). For example, for the distribution broadening seen in MAK98_cA (which appears to be broadening of the distribution at all positions on all chromosomes) to be the result of a biological process would require widespread and extreme fragmentation of the chromosomes. I would suggest this is very unlikely against the alternative of variation introduced during DNA processing, sequencing and/or mapping - and indeed, this is the likely the cause of for the majority of observed difference in the overall distribution around 2 copies.

    This source of variation in copy number estimates needs to be accounted for in testing for differences as the certainty for each estimate will vary with sample preparation and also gene length. In addition, the distributions for Lister427 1313 and MAK98_cA probably suggest that these should be removed from the analysis.

    1. The lines being analysed are not phylogenetically independent, meaning that similarity can reflect shared ancestry rather than selection. The 3 lines derived from Lister 427 are obviously expected to be very closely related, and the authors have previously shown that the 4 T. b. rhodesiense isolates are highly similar (suggesting recent common ancestor) [PMID: 26715446]. In addition, although EATRO1125 was derived independently, this too might be more closely related to 427 than to the new lines. As such, copy number in each cannot be taken as an independent measurement. I'm afraid I think this makes the statistical approach taken to identify 'reproducible' gene copy number changes invalid. For example, the monooxygenase Tb927.9.1400 in Fig. 6E is present as 2 copies in T. b. rhodesiense isolates and 3 copies in EATRO1125/Lister427 lines, but this probably only represents a single difference between 2 clades, not 8 independent measurements. On adaptation to culture this gene is unchanged in MAK98 (excluding cA) and goes from 2→3 in MAK65. This last observation is interesting (especially if the 4 MAK65 lines are completely independent, which wasn't clear from the text), but whether such change is statistically significant across the whole genome needs testing.

    Notwithstanding the above, unique to this study are the copy number estimates for the same populations pre and post adaptation. I think if the authors could apply a method that tests for directional changes in these while accounting for effects of gene size and the heterogeneity due to sequencing discussed above, then an analysis of which of these were observed in both MAK65 and MAK98 - and which also shared by Lister427/EATRO1125 - would be very interesting and potentially very informative, but I don't think the current analysis is sufficient to support the claims made. The authors may want to consult a statistician, but I suspect biological replicates of the sequencing samples will be required.

    Minor comments:

    The concept of "gene ploidy" is rather unhelpful and I would suggest that the authors make a more strict distinction between changes in ploidy (caused by duplication/loss of chromosomes) and changes in gene copy number (predominantly due to array expansion/contraction). For example, a gene with copy number of 4 can exist as 2 copies on each of 2 homologous diploid chromosomes - and an expansion of one array that increases the copy number to 5 is not a change in ploidy.

    The purpose of Fig 1A/B is to compare the infections between 2 T.b. isolates (MAK65/98), but the parasitaemias are displayed on different scales and with different transforms making such comparison extremely difficult. Same for Fig 2A-D and F-G - text discusses growth rate, but can't be judged on linear scale.

    Very difficult to see PAD1 staining when overlaid with transmitted light (Fig1D) - could this be separated?

    Discussion is made comparing the proportion of cells with PAD1 staining, but it is unclear how many cells and replicates this is based on - percentages should be given with estimate of SEM, confidence intervals or similar.

    I found naming of the cultures derived from MAK65 and MAK98 confusing and counter-intuitive. I believe the following to be correct:

    MAK65 cA/cB are independent cultures with a total of 30 days in culture and the doubling time ~7h (after ~day 20) MAK65 cC/cD have only 17 days in culture but achieved a similar doubling time to cA/B after ~day 8. MAK98 cA has 33 days in culture, but grew slowly throughout (doubling time ~13h). MAK98 cB has 24 days in culture including a freezing step, but doubling time dropped to 10h after ~day 9. This really needs to be clearer in the manuscript and it would be extremely useful to have some indication of the number of generations each line has been through in culture. To me, it was confusing that MAK65 cA/cB have been longer in culture than cC/cD.

    "Our observations on copy number are the tip of the iceberg: a survey of just a single ~10 kb region revealed selection for smaller insertions, deletions and point mutations (S4 Fig).". S4 Fig shows a region around a repeated HSP70 gene, with a large number of SNP/INDELs versus reference. As would be expected, some of these are haplotype-specific, but changes in the ratio of the sequencing reads between the haplotypes should not be presented as evidence for selection without a statistical test for enrichment.

    The Supplemental data are an important resource here. They are too large to check extensively, but in trying to reproduce the copy number estimates for the unique genes, I found that the read counts for MAK98 and EATRO1125 in Sheet 5 to be identical except for some NA values in EATRO1125. This is presumably an error. I was also surprised that no genes have 0 count when DNA was mapped to 927 reference - except for DNA from 927 itself which is the one sample I'd expect not to have this behaviour. Is there an explanation for this?

    Significance

    Combined with evidence, reproducibility and clarity.

  7. Version published to 10.1101/2021.06.10.446608v1 on bioRxiv