RR\ID Summary of Reviews: This preprint evaluates the diagnostic performance of Quantum-enhanced nanodiamond rapid test for early SARS-CoV-2 antigen detection. Peer reviewers praised the rigor of the study noting it as the first large-scale blinded clinical evaluation of spin-enhanced nanodiamond LFTs, moving beyond proof-of-concept to a performance assessment with real clinical samples. They urged the need for further work on membrane chemistry and blocking strategies to bring performance closer to its theoretical potential. They also suggested discussion of the drop in sensitivity at lower viral loads (<10⁴ copies/mL) in terms of balancing infectiousness detection with over diagnosis risk and suggest the authors to briefly comment on the potential utility of this assay for public health applications such as surveillance or contact tracing.  

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/vi2iegeo/release/1

Reviewer #1: Evidentiary Rating: Potentially Informative

Written Review: The authors claim that a spin-enhanced fluorescent nanodiamond (FND) lateral flow test for SARS-CoV-2 antigen detection achieves up to 1,100-fold greater sensitivity than conventional gold nanoparticle LFTs using identical antibodies. In a large, blinded clinical evaluation, the assay demonstrated 95.1% sensitivity (Ct ≤ 30) and 100% specificity, enabling SARS-CoV-2 detection on average two days earlier than conventional LFTs and within 0.6 days of RT-qPCR. They assert that this quantum-enhanced diagnostic platform could be adapted to other infectious and non-infectious diseases. 1. The study represents the first large-scale blinded clinical evaluation of spin-enhanced nanodiamond LFTs, moving beyond proof-of-concept to a performance assessment with real clinical samples. 2. The antibody screening process using biolayer interferometry is well executed, but screening on a single recombinant antigen source introduces potential epitope bias; inclusion of diverse antigen sources could further validate pair robustness. 3. The direct head-to-head comparison with in-house AuNP LFTs using identical reagents is a strong methodological choice, eliminating confounding variables common in cross-platform sensitivity claims. 4. While the assay achieves sub-pg/mL LoDs, residual non-specific binding limits ultimate sensitivity exploitation; more work on membrane chemistry or blocking strategies could push performance closer to the theoretical limit. 5. The sample size is adequate for preliminary evaluation, but a larger, more demographically and geographically diverse cohort is necessary to confirm real-world performance, especially in asymptomatic and early infection cases. 6. The assay’s 95.1% sensitivity at Ct ≤ 30 exceeds WHO “desirable” criteria, but the drop in sensitivity at lower viral loads (<10⁴ copies/mL) should be discussed in terms of balancing infectiousness detection with overdiagnosis risk. 7. The ROC, Bayesian regression, and infection dynamics modelling are sophisticated and well described, but providing raw Ct distribution histograms for positive samples would help readers assess viral load representativeness.

Reviewer #2: Evidentiary Rating: Reliable

Written Review: The authors present the development of a lateral flow assay prototype for the detection of SARS-CoV-2 nucleocapsid antigen, utilizing spin-enhanced nanodiamonds as fluorescent sensors. The manuscript provides sufficient detail regarding the evaluation of fluorescent nanodiamonds, optimization of anti-SARS-CoV-2 nucleocapsid capture and detection antibody pairs, assessment of assay sensitivity, and assay specificity for SARS-CoV-2 in comparison to other coronaviruses. Additionally, the authors include data demonstrating detection of SARS-CoV-2 nucleocapsid antigen in clinically relevant specimens, including nasal and nasopharyngeal swabs. The supplementary material includes a comparative analysis of the assay’s sensitivity relative to published data on various lateral flow tests, highlighting superior sensitivity achieved through the use of fluorescent nanodiamonds. Increased assay sensitivity may lead to earlier detection of SARS-CoV-2 infection thus providing opportunity for early intervention. Overall, the manuscript is well-organized, and the data are scientifically robust. I have a few minor comments for the authors’ consideration: 1. The authors state that the sensitivity of their assay is comparable to that of the Quanterix Simoa assay. Please provide a reference for the Simoa SARS-CoV-2 assay. 2. Could the authors briefly comment on the potential utility of this assay for public health applications such as surveillance or contact tracing?

RR\ID Summary of Reviews: This study by Freercks and colleagues examines how APOL1 genetic variants affect kidney transplant outcomes in people with HIV, analyzing data from US and South African cohorts. Peer reviewers rated the study as "reliable" and emphasized its novel contributions to transplant medicine. The reviewers noted that while sample sizes were necessarily small, the consistency of findings across two independent international cohorts strengthens the conclusions. They highlighted the clinical significance for transplant allocation decisions and risk stratification, while noting important limitations including potential selection bias. The reviewers emphasized that transplantation likely remains superior to dialysis despite increased APOL1 risks. They called for further research into mechanistic pathways and potential therapeutic interventions.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/dvlczo3x/release/1

Reviewer #1: Evidentiary Rating: Reliable

Written Review: The authors present data of how APOL1 renal risk variants (RRV) influence the outcomes in kidney transplant recipients who have HIV. In previous studies it has been found that kidney transplant recipients without HIV who receive a donor with APOL1 RRV are more likely to have shorter renal allograft survival. Currently the utilization of APOL1 RRV screening pre-transplant is not routinely done and additional data is required to determine if this screening and/or treatment of donors and recipients in high risk groups is of strong utility. 

This study describes recipient and donor characteristics, recipient outcomes based on the number of recipient APOL1 risk alleles, and recipient outcomes based on the numer of donor APOL1 risk alleles. Freecks, et al defined the composite outcome as death, graft failure, biopsy proven rejection, and HIVAN. In the South African cohort participants included recipients and donors with HIV. In the US cohort participants included recipients with HIV and donors with and without HIV (Participants from the HOPE in Action Kidney Transplantation clinical trial). All recipients and donors who had blood available had APOL1 genotyping performed. 

The authors found that recipients who received an organ from a donor who had >1 APOL1 risk allele were more at risk for a composite outcome which was found to be statistically significant in both the South African and US cohorts. The data aligns with previous studies that showed recipients without HIV who received an organ from a donor with a APOL1 RRV are more likely to have allograft failure. This study adds information about APOL1 RRV as it pertains to recipients who have HIV. We need to better understand how this information impacts the clinical practice of kidney transplantation and risk stratification, helps to predict recipient outcomes, and how it influences discussions with a high risk patient who is considering a kidney transplant. Is there effective therapy available to mitigate APOL1 RRV presence or is it going to be another variable when stratifying how risky a kidney transplant could be for a particular recipient in terms of 1-year and long term outcomes. 

The authors present the limitations of this study which are appropriate. For clarity within the manuscript I think it could be beneficial to separate donors with and without HIV in the US cohort. Current state makes some of the results/tables difficult to follow. Although we know outcomes in recipients with HIV who receive an organ from a donor with or without HIV are similar it would be beneficial to see if there is a difference in the APO1L risk alleles based on donor HIV status since this has not been looked at specifically.  The South African cohort only includes donors w/ HIV. 

Reviewer #2: Evidentiary Rating: Reliable

Written Review: The manuscript details how the presence of even one donor APOL1 renal risk variant was associated with an adjusted hazard ratio of a poor composite outcome (time to first rejection, HIV-associated nephropathy, graft failure or death). It showed the presence of one APOL1 RRV was associated with increased risk for allograft rejection in both SA and US cohorts. The data suggests donor APOL1 genotype, even a single RRV, is a major determinant of graft survival but recipient genotype plays a lesser role.

These finds are novel and of interest. My comments are: 1. Limitations include a small sample size which is unavoidable (particularly for donors with two RRVs) and there is also potential selection bias as only participants with available genomic data were included. Any explanation for why others were missing (e.g. no consent for collection)? 2. Models were adjusted for age, hypertension and diabetes mellitus - why were these three variables selected? Residual confounding is likely to be present for the analyses. 3. The problem with the composite outcome is the mechanistic pathways of APOL1 expression causing adverse outcomes is less clear (is there a difference in pathophysiology for rejection versus mortality)? It would be interesting to have further discussion on possible pathways for injury. For example, the SA cohort graft losses are more likely from rejection but the US cohort graft losses were more from other causes (e.g., RVT, other). 4. How do these outcomes compare to receiving donor kidneys that are HIV negative or donors that lack APOL1 RRV? If this data is available for comparison it would greatly strengthen the interpretation of the analysis. 5. It is important to highlight that even if transplant recipients with HIV receive kidneys from donors with HIV and APOL1 RRV and experience inferior post-transplant outcomes (versus receiving HIV negative or absence of APOL1 RRV), these outcomes are probably still superior to the alternative which is being on dialysis.

RR\ID Summary of Reviews: The manuscript by Stevens et al presents high-resolution cryoEM structures of herpesvirus capsids, revealing a previously uncharacterized form—the D-capsid—likely representing a genome-releasing state. Reviewers commend the technical rigor, large dataset, and detailed analysis of portal and scaffold-capsid interactions that clarify capsid maturation pathways. Several insightful questions were raised, including: What is the inner diameter of the portal pore, and does it change without terminal DNA? Why is the scaffold absent in C- and D-capsids despite similar portal structures? How is the portal stabilized in D-capsids lacking genome pressure? Reviewers also asked whether particle polishing was used to improve resolution and suggested clarifying potential misattributions of residue identities in portal-scaffold interactions.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/4rdxrk4s/release/1

Reviewer #1: Evidentiary Rating: Strong

Written Review: Stevens et al describe high-resolution structures of HSV-1 capsid from the nucleus-extracted samples. They identify a D-capsid with terminal DNA density inside the capsid, as well as DNA outside the individual D-capsids. The authors performed high-standard and convincing analysis of the portal region. The manuscript is technically strong and well presented. The methods are very well described.

I have minor comments: 1. What is the inner diameter of the portal pore? Does the diameter change in the absence of terminal DNA? 2. In the enlarged view of Figure 2A (model with densities), the residues that face the DNA (i.e., facing the central pore) should be indicated. 3. Could the author speculate why the scaffold is absent in C-capsid and D-capsid, since the local structure of the portal appears similar (Figure 4)? 4. Did the authors use particle polishing at the last step to further improve the resolution?

Reviewer #2: Evidentiary Rating: Strong

Written Review: The manuscript "Structure of a new capsid form and comparison with A-, B- and C-capsids clarify herpesvirus assembly" by Stevens et al describes extensive structural classification of herpes virus capsids using cryoEM single particle analysis. This analysis was possible due to the large size of the data set, and the expertise of the authors. In addition to identifying a new Herpes capsid type (D-capsids), the authors were able to characterize portal dynamics and interactions between scaffold and both portal and capsid. Further, their results allowed them to clarify the origin of Herpes A-capsids. The manuscript is relatively easy to read, the data is solid, and the structural interpretations are convincing. Below are a few minor issues and questions: 1. A schematic showing all the Herpes structural proteins would be useful. 2. Intro – 3rd paragraph, 2nd sentence should read “the viral genome IS EJECTED into the nucleus for transcription”. 3. In the section “Scaffolding protein is anchored to A- and B-capsid portal baskets and B-capsid shells via conserved hydrophobic motifs”, the authors state that “Investigators previously showed that portal protein residues 449-457—particularly Y451, P452, and E454 (43, 44)—are essential to the portal-scaffold interaction and thus efficient capsid assembly (43).” Should the first sentence refer to scaffold protein residues 449-457, not portal residues? Related, how does this interaction relate to portal-scaffold interactions described for HK97?  (Huet et al. Sci Adv 2023 Jun 16;9(24) doi: 10.1126/sciadv.adg8868) 4. In the first paragraph of the discussion, the last clause of the third sentence should read “including its interactions with the scaffold and its  dynamics with respect to the capsid shell” 5. It is interesting that the position of the portal in D-capsids is the same as in C-capsids despite the absence of a packaged genome (and accompanying pressure) in D-capsids. Does the structure show which interactions stabilize the portal position in D-capsid?

RR\ID Summary of Reviews: The preprint "West Nile Virus (Orthoflavivirus nilense) (WNV) RNA concentrations in wastewater solids at five wastewater treatment plants in the United States" investigates the potential for wastewater surveillance to detect WNV during known periods of community transmission. The study detected WNV RNA in a small number of wastewater samples, all from regions with confirmed cases, supporting the feasibility of this approach. Reviewers commended the innovation and relevance of the work but called for stronger correlations between wastewater and clinical data, clarification of methods, and molecular confirmation of results. The study contributes to growing evidence that wastewater monitoring can be a valuable and cost-effective addition to traditional public health surveillance systems.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/jkhu6syy/release/1

Reviewer #1: Evidentiary Rating: Potentially Informative

Written Review: In this study, the authors retrospectively screened 600 wastewater samples from locations that did and did not have known WNV case activity. Out of 600 samples, 9 were positive by ddPCR and these happened to be in samples that corresponded to regional WNV case activity.

The aim of this study is very important and it builds on an established wastewater surveillance technique used for a growing list of human pathogens. Unfortunately, many of these programs have been defunded in the United States and it is unclear if we will be able to reestablish this public health tool in the future. In any event, integrating surveillance of vector-borne diseases into the wastewater surveillance pipeline would streamline these activities and potentially save money in the long run. Pilot studies are needed before that can occur. This pilot study provides some evidence that WNV can be detected in wastewater. This reviewer appreciates how specific primers and probes can be for their target, but also understands how messy wastewater is and underscores the importance of verifying that the amplicons are actually due to WNV vRNA. In order to move this study from potentially informative to reliable or even strong, the amplicons should be cloned and sequenced and verified that they are indeed due to WNV. It may also be possible to use a panel of primers to reconstruct a WNV gene from a few of these samples to confirm that the isolate obtained from the wastewater matches what was circulating in the regional mosquito/bird/human population and that it has mutations that are representative once the virus readapts to humans. 

Reviewer #2: Evidentiary Rating: Reliable

Written Review: The authors performed environmental surveillance of West Nile Virus (WNV) from several wastewater (WW) sites across the USA (places of known WNV cases as well as ones generally without WNV cases). They successfully detected signal in several samples, all within regions of known WNV circulation. However, these detections were highly sporadic in nature, even in regions with persistent clinical detections (i.e. NE). The authors suggest that this data can be used to complement traditional WNV monitoring and acknowledge that there is weak correlation between WW detection of the WNV signal to clinical cases. With such weak correlation can the WW surveillance of WNV be currently used as a reliable surveillance tool to detect WNV in the population?

Suggestions to improve manuscript: 1. The authors present clinical and WW detections for each location showcasing the potential utility of using WW to detect WNV. It would be helpful for the reader if the authors could address why there was such sporadic detection of WNV signal in WW for NE while clinical detections were persistent and the highest out of the 5 regions tested. Furthermore, the authors noted there was weak correlation between WW signal and clinical detections; can such weak correlation translate to a reliable WW surveillance of WNV? 2. It would be helpful for authors to address why there is such a high variation in data presented in Figure 2. 3. Page 10 the appropriate reference for Wolfe et al is missing 4. It would be helpful to include data of the WNV assay specificity and sensitivity for the in silico and in vitro results (page 8; results) 5. Table 1 – please include the 5’- designation in the primer sequences 6. Would be helpful to include the name of the state in Figure 1. 7. It would be helpful to include data for all sites sampled in Figure 2; specifically for SJ and OSP. Also would help to include the number of replicates for each data point.

Reviewer #3: Evidentiary Rating: Reliable

Written Review: The COVID-19 pandemic reasserted the importance of public health preparedness and surveillance networks for infectious disease. To this end, the pandemic served as a ‘coming of age’ of wastewater surveillance (WS) serving as an unbiased ‘community swab’ and an important tool public health turned to, especially as clinical testing was overwhelmed during successive resurgences of SARS-CoV-2.

Beyond COVID, WS has found utility as an effective tool to deal with any number of threats. Even before the WHO ended the Public Health Emergency of International Concern for COVID-19 in May 2023, WS had been successfully extended to multiple additional targets, responsive to other seasonal respiratory diseases (influenza, RSV), foodborne illness (enteroviruses) and diseases of emerging concern such as Mpox, and more recently measles and highly pathogenic avian influenza. The response from public health has been near unanimous voicing overwhelming support for more widespread adoption of this powerful tool.

Here Zulli and colleagues from the pan-US program WastewaterSCAN extend the utility of WS to West Nile Virus (WNV), an arbovirus that has become endemic throughout regions of the world, including North America where it is a nationally notifiable condition accounting for thousands of cases reported annually and nearly 3,000 deaths since 1999. WNV is a potential candidate for WS given that symptomatic patients are known to shed virus in urine and its utility is amplified considering conventional surveillance is both labour-intensive and costly, often relying on pooled mosquito testing.

The study is a retrospective analysis of samples selected from five locations in two states and includes locations where there have been confirmed human infections by WNV and others where infections have not been recorded nor are they expected because of effective mosquito control programs. As North America’s largest network carrying out WS, WastewaterSCAN is uniquely positioned to conduct retrospective analyses with a large repository of archived samples for assay validation.

Method validation demonstrated target specificity and a recent fractionation study by members of WastewaterSCAN (Roldan-Hernandez et al. 2025, Environ. Sci.: Water Res. Technol., 11, 88), suggested that WNV partitions preferentially to wastewater solids rendering surveillance a potential add-on to existing monitoring programs, most of which target solids.

While over 600 samples were tested, there were only 9 positive samples; however, each originated from a location with reported cases of WNV. Through the evolution of WS, we have come to expect positive correlation between target RNA presence and clinical cases, despite infections often being mild or asymptomatic and unreported. Yet none of the three sites yielding positive samples in the current study showed a significant correlation with known cases of infection from that region. There was, however, a significant correlation between weekly WNV RNA presence and incidence rates in an aggregate analysis of samples from all five sites. Given the pan-US reach of WastewaterSCAN, inclusion of more samples from locations typically recording high case numbers (e.g. Texas) and/or higher frequency samples or samples spanning multiple years for the chosen locations could have strengthened this relationship and perhaps yielded site-specific relationships between WNV RNA presence and cases. Likewise, inclusion of freshly collected samples rather than archived frozen samples may have yielded a stronger relationship with clinical cases.

While scientists from WastewaterSCAN and elsewhere continue to press the boundaries of WS rendering it applicable to many priorities identified by public health, this reemergent discipline is now beset by challenges that extend beyond the technical. Funding across North America for WS is being withdrawn or not renewed despite current biothreats including generational scale outbreaks of measles that are affecting both the US and Canada and avian influenza that continues to hop species and was detected in multiple jurisdictions in wastewater last spring and summer. Abandoning such a powerful and cost-effective public health tool cannot be an option.

RR\ID Summary of Reviews: Reviewers found the preprint to be strong, highlighting the novelty of the identified lineages and its implications towards selection dynamics and transmission of mobile genetic elements. Overall, reviewers had minor comments regarding further contextualization of the study's findings with previous work on V. cholerae surveillance and states the study stresses the importance for improved surveillance of V. cholerae.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/g7yom7wv/release/1

Reviewer #1: Evidentiary Rating: Strong

Written Review: Overall, the paper is well-written, easy to follow, and provides an important addition to the growing body of V. cholerae phylogenetic data in endemic regions like Bangladesh. While V. cholerae in outbreaks tends to be clonal or near-clonal, examination of pathogen diversity during continued circulation in endemic regions has revealed striking co-circulation of genetically distinct lineages as well as interesting new insights into how traits are acquired and lost in V. cholerae, especially within known mobile genetic elements and genetic regions associated with phage defense. The phylogenetic analyses and identified trends are robust and convincing, despite some limitations to sampling coverage acknowledged by the authors. I have only a few minor comments to help contextualize the authors' findings:  * Does the north-south trend in genomic diversity (with BD1 more prevalent near the India-Bangladesh border) suggest that spread of BD1 from its likely origin in India occurred primarily through local short-range transmission and less through longer-range introduction methods like air travel?  * An interesting observation the authors made that raises further questions was that all the BD1 isolates were serotype Ogawa and all the BD2 isolates were serotype Inaba. Were the wbeT inactivating mutations in the BD2 isolates all the same? Has this been observed before in the literature where serotype perfectly aligns with phylogenetic grouping? Since BD1 underwent a serotype switch to Inaba in 2020 it is striking that zero Inaba isolates were identified. Additionally, what were the serotypes of the BD3 isolates? Further discussion of these questions and provision of additional genetic data about the Inaba genotypes would be helpful to place the serotype findings in context especially since the serotype landscape of 2020 onwards is known.  * Are there any phylogenetic signals that suggest how BD1 or subsequent BD1 lineages have fared against current outbreak clones? In other words, does the success of BD1 appear confined to endemic circulation? * Is there any information about cholera vaccine status or vaccination campaign locations at the time of the study?  * Did the authors observe any variants in key virulence/colonization loci such as TCP and/or the CTX prophage? * Could the authors speculate on the fate of BD3 and why it has not been detected in studies using isolates from 2020 onwards? * It would be helpful for the authors to include a "summary" figure or timeline that illustrates how this new 2018-19 dataset informs the current understanding of BD lineage dynamics, especially considering this data fills

Reviewer #2: Evidentiary Rating: Strong

Written Review: This study provides critical insights into the evolutionary dynamics, antimicrobial resistance (AMR), and ecological fitness of Vibrio cholerae by analyzing its genome diversity across Bangladesh over the course of a year. By employing long-read nanopore sequencing on 273 isolates collected from cholera patients across seven hospitals in 2018–2019, researchers uncovered significant spatial and temporal variation in V. cholerae lineages. The dominant lineages identified were BD-1, BD-2a, BD-2b, and a novel lineage, BD-3. BD-1 was more prevalent in the northern regions, likely originating from India, while higher lineage diversity, including BD-2 variants and BD-3, was observed in the southern coastal areas, indicating distinct transmission routes and environmental pressures shaping bacterial populations. The study also highlights the importance of genomic structure in understanding lineage traits. Long-read sequencing enabled accurate detection of structural variations, including ICE deletions, that are difficult to resolve with short-read methods. The distinct ICE types observed across lineages (e.g., VchInd5 in BD-1 and BD-3, and VchInd6 or ICE absence in BD-2) underline the genetic modularity influencing phage and antibiotic resistance. These findings underscore the dynamic and localized evolution of V. cholerae, shaped by interactions between host immunity, bacteriophages, environmental reservoirs, and human intervention through antibiotics.

One of the key findings is the coexistence of multiple V. cholerae lineages within a single outbreak season, in contrast to the slower, decade-scale lineage replacement seen in past pandemics. This coexistence reflects complex selective dynamics influenced by phage predation and antibiotic pressure. For instance, the BD-2a lineage, though lacking a genetic element SXT-ICE often associated with resistance—still persisted throughout the sampling period. This suggests that lineages with lower resistance profiles may benefit from ecological or phage-mediated interactions, such as those described by negative frequency-dependent selection, where less common lineages or traits are favored due to reduced phage targeting or competition. AMR gene analysis revealed the presence of at least 10 resistance genes in every isolate and interestingly, resistance genes that were prevalent in 2006, suggesting ongoing shifts in the costs and benefits of maintaining certain resistance genes. Overall, this work expands our understanding of how V. cholerae adapts and persists within endemic settings, emphasizing the need for continuous genomic surveillance to track lineage emergence, resistance evolution, and the ecological mechanisms sustaining cholera transmission. However, This work builds on prior regional studies such as Shah et al. (2014), which examined V. cholerae O1 during the 2010 Pakistan floods and highlighted the role of environmental disruption in amplifying clonal spread. Unlike that outbreak, which featured limited genomic diversity and a single dominant clone, the current study in Bangladesh reveals substantial co-circulation of multiple lineages, each with distinct ICE content and resistance profiles. This contrast underscores a critical knowledge gap in understanding how environmental, geographic, and temporal factors drive V. cholerae diversification across South Asia, calling for more integrated genomic surveillance across borders.

Reviewer #2: Evidentiary Rating: Potentially Informative

Written Review: The reviewed manuscript is devoted to clarification of taxonomy and antimicrobial resistance (AMR) spectrum of Enterobacter strains which were isolated from clinical specimens of patients with bloodstream infections in several hospitals in Nigeria during 2014-2020. The authors used all necessary molecular tools, WGS, bioinformatic and phylogenetic analysis, MLST typing etc. which resulted to obtain very important original data. According to the data presented, the authors were able to clarify to which Enterobacter spp. and subspecies the strains, previously isolated and incorrectly identified, belong. Also, comparative analysis of the genomes investigated with other representative genomes of Enterobacter spp. widely identified elsewhere in Nigeria. A special attention was paid to detailed characteristics of AMR of the strains investigated and, further, retrospective analysis of their possible role in some Enterobacter-related outbreaks. In fact, this is a great study which will be very interesting to the research community worldwide. Role of Enterobacter hormaechei as an etiological factor of blood infections is not well studied yet. However, this is very critical for both fundamental research and Public Health to unravel pathogenic potency of this organism and to avoid wrong diagnostics as well. 

Specific comments:

P2, the section Abstract:  1. The authors could rephrase this sentence: ‘Among 98 Enterobacter received, Enterobacter hormaechei subspecies xiangfangensis predominated (43), followed by other E. hormachei subspecies (18), E. cloacae (26), E. roggenkampii (4), E. bugandensis (3), E. kobei (2), E. asburiae (1) and E. cancerogenous (1).’ As: ‘…… followed by other E. hormachei subspecies (18), and Enterobacter spp., such as: E. cloacae (26), E. roggenkampii (4), E. bugandensis (3), E. kobei (2), E. asburiae (1) and E. cancerogenous (1).’  2. ‘E. hormaechei, often misidentified and rarely…’ instead ‘Enterobacter hormaechei, often misidentified and rarely’.  3. ‘…retrospective detection of likely outbreaks…’ – the retrospective analysis of likely Enterobacter-related outbreaks?  4. Some repetitions should be excluded from the text of the Abstract and through the text of the manuscript as well. 

P3, IMPACT STATEMENT  5. ‘Accurate identification of Enterobacter…’? Spp., strains, pathogens etc., please, clarify. 

P5, the section INTRODUCTION  6. ‘…limitations of conventional biochemical methods.’ – diagnostic methods? 

P5, the section METHODS  7. The title for subsection ’Collection of Presumptive bloodstream Enterobacter sp.’ may be difficult for potential readers, please, rephrase.  8. ‘…Heterogenous cultures were purified…’ – how? purified from which microorganisms? Does it mean that the research was performed with contaminated cultures? Coinfections? In this case why the Enterobacter spp. are recognized as the etiological agents of blood infections? Are these heterologous cultures Klebsiella pneumoniae, Staphylococcus aureus, Pseudomonas aeruginosa and other pathogens which were previously identified as the causative agents of blood infections and isolated from the relevant clinical specimens (page 8)? Thus, Enterobacter spp. investigated in the current research, could be only accompanying microorganisms but not responsible for development of blood infections directly. 

P6, the subsection Whole Genome Sequence analysis  9. ‘Mapping to reference…’ what?  10. ‘Antimicrobial resistance genes, virulence genes, and…’ – which virulence genes? MLST and AMR only? 

P7, the subsection Whole Genome Sequence analysis  11. …’ STs were assigned as follows: G20500026: assigned - ST-1995, G20500682: assigned - ST-1996, G18503215: assigned - ST-1997, G18503415: assigned - ST-1998 and G18503407: assigned - ST-1998.’ – for which Enterobacter spp.? The relevant IDs assigned by the PubMLST database must be included/ 

PP7-10, the section Results  12. The authors should present only specific comments for the data presented in Figures 1-3 while not duplicating the relevant content as identical numbers and percentages. The text in the current version of the manuscript is difficult for understanding for potential readers of the Journal. 

PP11-12, the subsection Potential Enterobacter health-care associated infection outbreaks detected  13. According to the text of this subsection, the authors described mainly the AMR profiles of the E. hormaechei strains while not features of outbreaks; the titles for this subsection may be corrected. 

PP12-13, the subsection Genomic context of Enterobacter genomes from this study and Enterobacter genomes from Sands et al., 2021 study  14. This title could be corrected to make it more valuable for potential readers of the manuscript.  15. All citations of the research of Sands et al. must be corrected according to the Journal rules.  16. The text from this subsection is certainly difficult for meaning. Based on the WGS data obtained, the authors focused their attention on re-identification of the Enterobacter strains which were isolated and identified earlier by the group of Sands et al., 2021. These findings should be presented in a more readable format available for readers worldwide. 

P20 –please, add necessary information on the ref. 17 (year, Vol, pp, link etc.). 

Doubtless, WGS is a very attractive method for laboratory diagnostics of pathogenic microorganisms, especially rare or novel ones. However, the authors could discuss what is preferable for low-resource settings – WGS or some other molecular diagnostic methods, for instance, 16S RNA & MLST typing & multiplex PCR for simultaneous identification of AMR and pathogen genes etc. It may be important to use resource-limited settings for preliminary analysis especially when there is no reason to WGS for detailed characteristics of extended numbers of clinical specimens under a large-scale examination in hospitals, monitoring and retrospective investigations and others.

Reviewer #1: Evidentiary Rating: Reliable

Written Review: This study demonstrates the importance of ongoing whole genome sequencing (WGS) to allow for accurate diagnosis and treatment in critical infections, such as sepsis/bacteraemia. Misidentification of Enterobacter spp. is an ongoing issue across multiple settings, and this study provides a staggering example of exactly how prolific this issue is. The statement "Sentinel labs sent a total of 63 isolates as Enterobacter spp., and of these, 27 were verified as Enterobacter by VITEK2, out of which WGS eventually identified 13 as belonging to the genus" reflects a real ongoing issue with some of the fundamental processes in microbial diagnostics that is often overlooked, in both low and high resource settings.  

The relatively low numbers across time and locations make it difficult to observe any clear trend, if one truly exists. Instead, the Enterobacter spp. and strains recovered are diverse across locations and reflect the sporadic occurrence of strains carrying variable antimicrobial resistance genes. The descriptive analysis of the samples obtained during the study period will provide a useful catalogue for comparison with future studies and/or studies looking at other sites in Africa and globally. More data from Africa is always a good thing, as it provides additional global context and more avenues for rapid comparison and infection control responses. This is exemplified in the study, where the only other data available on Enterobacter from Nigeria was from a single study conducted in 2021. Thus, the true prevalence and impact of Enterobacter in Nigeria remains largely unknown. 

Antimicrobial resistance (AMR) was similarly diverse, with the alarming detection of carbapenemase (blaNDM) and colistin (mcr) resistance genes in the area. There was variable concordance between phenotype and genotype for both E. cloacae and E. hormaechei species, which is not unusual. More information on antibiotic availability and prescribing in Nigeria may have provided more context to the levels of AMR likely driven by antibiotic use in the area.  

Overall, this study describes a small cohort of WGS Enterobacter spp. from bloodstream infections across Nigeria. Despite the title, I am not completely convinced of Enterobacter hormaechei's role as a "key pathogen" in bloodstream infections in the area, given the generally low and diverse rates of Enterobacter infection across the study set. Ongoing work is required to gain further insight into species and strain circulation in the area for both Enterobacter spp. and other pathogenic bacteria more generally.

RR\ID Summary of Reviews: This preprint presents findings about bloodstream infections in Nigerian hospitals. Expert reviewers praised the study for showing the problems of correctly identifying Enterobacter species using standard laboratory methods. They valued the addition of genetic data from a region not often studied, noting that such information helps global monitoring efforts. The detailed study of antibiotic resistance patterns, including concerning findings of resistance to last-resort antibiotics like carbapenems and colistin, was also an important strength. However, reviewers pointed out several limitations. The small number of samples collected across multiple hospitals and years makes it hard to prove that E. hormaechei is truly a "key pathogen" as claimed. Questions were raised about whether some samples might contain multiple bacteria rather than pure cultures, which could affect the results. Reviewers also noted differences between laboratory test results and genetic test results for antibiotic resistance. They emphasized that despite this research, we still don't know how common and important Enterobacter infections truly are in Nigeria.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/azolkhby/release/1

Reviewer #5: Evidentiary Rating: Reliable

Written Review: The manuscript by Sajib and colleagues describes what they term MultiSeq-AMR, which is amplicon-sequencing approach for a more rapid detection of bloodstream infections and the detection of antimicrobial resistance markers in order to more rapidly identify effective treatment measures for septicemia.  The ability to ID and get a predicted AMR profile in a rapid fashion is key for patients suffering sepsis and limits the use of empiric therapies, which are either not the most effective or have potential side effects.

The approach on the surface seems like a good way to more rapidly identify pathogens and AMR genes from blood cultures. There are a couple of concerns, the first being that the study seems a bit incomplete, in that several of the AMR panels were not assessed in the manuscript.  The other concerns were around the performance of the methods for some of the key pathogens and not being able to detect pathogens like Pseudomonas and certain Streptococcus.  These are key, since many Pseudomonas are resistant to multiple antimicrobials and some of the Strep are very susceptible and can be treated with antibiotics with less-worrisome side effect profiles.

Lines 69-72 and other parts of the paper: in the first sentence (i.e. ln 69)  state that the need for the enrichment in the blood cultures is to get the bacterial/fungal genes above the background host DNA, how many reads mapped back to host DNA in the BAC/ALERT samples?  I mention the latter point because understanding the impact of  the host DNA background is important to understand the role of time and amplification needs. You may be able to minimize the culture time and numbers of amplification cycles to get the microbial DNA levels up for adequate positivity in a minimum time.

Another limitation of the study is the lack of a cost-benefit type analyses of the different sequencing yields, what is the acceptable sensitivity (i.e. when is the 2Mbp yield okay) vs. time component for treatment, since the larger yields mean a longer time to results.  This is not really discussed at all in the discussion section and would benefit the readers.  As would a cost comparison, when is cost-effective to use this approach since the blood cultures need to be completed regardless of if MultiSeq-AMR is done or not.

For the spiking experiments in the sheep’s blood, did you do multiple species inoculations?  This would be important, as this seemed to cause issues when these occurred in the BAC/ALERT samples.

Line 109 and 147: Which of the aadA genes? You screen for both aadA1 and aadA2.

Overall the figures are helpful, although in some cases the text is too small to read when shrunk down to the publication size embedded in the manuscript. Similarly, the colors in panel C of the figures, it is difficult to make out some of the subtle color differences for some of the taxa, especially in the blue-violet/purple ranges.

The protocols provided are also very helpful to understand the workflow and procedures used in the manuscript.

Reviewer #4: Evidentiary Rating: Strong

Written Review: While the manuscript presents an interesting approach to detecting pathogens and antimicrobial resistance (AMR) in bloodstream infections (BSI), I have several concerns that need to be addressed to improve the relevance and reliability of the protocol.

1. Specificity of the Protocol for BSI

The authors establish an amplicon-based detection protocol for BSI, but I did not see how their design is specifically tailored to BSI. The choice of AMR genes and the pathogen primers appear to be general-purpose primers used for microbial 16S and 18S sequencing, and the AMR genes are selected based on the Resfinder database, which is not specific to BSI. This suggests that the protocol is a generalized method rather than a specialized protocol designed specifically for BSI.

1. Lack of Direct Clinical Relevance

Presence of AMR is determined by AMR primers with cutoffs on alignment length (>40%), while pathogen species is determined by 16S/18S primers with a cutoff on relative abundance > 25%. By design, the AMR amplicon cannot be linked to 16S/18S by nanopore long reads, which may make the results derived from this protocol lack direct relevance to clinical diagnosis. We do not know whether the detected AMR genes belong to the dominant pathogens. To improve reliability, a simple yet effective approach would be to analyze the abundance of AMR genes as well. Although this is feasible within the current framework, the authors have not implemented it . The reliability of such AMR abundance analysis based on amplicon sequencing analysis depends on the amplification efficiency of the designed primers for different genes. It is crucial that these primers do not alter the original proportions of these genes in the sample. This can be easily verified using known concentration standards in mixed amplification experiments or by comparing mock sample amplification results with metagenomic sequencing results. However, the authors didn't work on this type of validation, indicating a lack of consideration in the protocol design.

1. Reliability of Abundance Cutoff for pathogen detection

The authors claim a reasonable abundance cutoff of > 25% for pathogen detection, but they do not provide analysis on how this determination was made (line 248 states "data not shown"). It seems arbitrary, and the number of samples tested in this work is insufficient to validate its applicability in real clinical samples. This is evident from the failure to detect two spike-in pathogens in two samples with sheep matrix. In the reviewer's opion, the cutoff should be adaptive and thereby dynamic among samples with different community compositions rather than a fixed cutoff for all samples. A number like the median abundance or abundance of the top 25th percentile of the community should be a better solution.

1. Writing Style and Presentation

The section detailing how the protocol is set up and run is the core information of this protocol study and should be presented in the results section, not just in the methods session.

Reviewer #3: Evidentiary Rating: Reliable

Written Review: The researchers are tackling an important problem – how do we identify resistance rapidly, on time scales relevant for individual patient treatment. In particular, they developed a method that can diagnose infection and, importantly, AMR genes present in the population, in a largely unbiased manner. The research is timely and important, and the paper presented fairly well although there could be some improvement in the description of the method.

The workflow, and especially the motivations for different steps, are not clearly explained. For example, the results start by presenting data about PCR pools, but lack the detail on where those pools come from, what exactly was being amplified, etc. While this information can be found in the methods, the text would benefit from a bit more detail in the results as well. I would also suggest to the authors to include a figure with an illustration of the workflow. 

Identifying AMR genes is not comprehensive as it is limited only to known/previously characterized AMR genes. This is a general issue with PCR-based methods, as one must a priori know what they are looking for, while resistance can be a product of many potential genes and, especially, many different mutations. This image gets even more complicated when observing across many bacterial strains and species, as a mutation can alter its phenotypic effects based on the genetic background. I also found it difficult to understand what genes and mutations were included in the primer list. 

The presented technique was validated using reference strains and previously sequenced strains. A major validation that is missing would include more diverse strains. In particular, I am concerned how well the presented technique that relies on PCR would perform across both very similar and very diverse sequences. One could explore this computationally by, for example, asking how well the chosen set of primers designed to identify E. coli AMR mutations would perform across the entire library of known E. coli isolates. 

I would appreciate better quantification of how well the culture enrichment works, and are species lost? 

The authors do a decent job discussing the above limitations, but I would recommend having a bit more detail in the discussion. 

Reviewer #2: Evidentiary Rating: Reliable

Written Review: The overall rating of “reliable” was a compromise between acknowledging the incredible amount of work that went into developing the MultiSeqAMR  multiplex schema and its potential usefulness for diagnosis, against the fact that the validation experiments, while promising, were too small a sample to adequately challenge the system.

Benchmarking of MultiSeqAMR was performed in 3 experiments. The first was using 21 pure DNAs of bacterial/fungi of known genome sequence. This was the lowest hurdle but the results were very good – no amplification of negative controls and 95% species and >99% AMR genes were accurately identified. The second experiment was sequencing 36 positive and 3 negative blood cultures. Again, the results were promising in terms of sensitivity, although specificity was lower with some false positives. The relatively low number of negative blood cultures tested is a problem. The third experiment was to use 13 spiked sheep’s blood, followed by blood culture enrichment as a simulation of a “real life” experiment.  There were 2 negative controls, again -  too small a number. The species assignment was quite accurate (11/13 correct) and the AMR assignment had 96% agreement.

These results are a promising start but don’t in any way cover the true breadth of genetic diversity of real hospital blood cultures. The fundamental problem with the PCR based approach for detection is that of primer specificity and false negative results. It would be necessary to use many more real samples with accompanying metagenomic sequence data, to understand the  performance  of the individual primer pairs. Additionally, many of 91 AMR primers were not challenged with a true positive control.

The introduction did not cover much about the previous experiences of developing nanopore schema for PCR amplicon sequencing.

The protocols for replicating the experiments are extensive and will be very useful for experimentalists. However, there needs to be a supplementary table with a list of primer sequences used.

While the experimental details are strong, the steps in primer design are not detailed and the only parameter given in design is the Tm.  The primers should have been cross validated by comparison against the blast database.

BACT/ALERT is mentioned several times, including the abstract without an explanation of what the technology is.

Line 84.  The technology is stated to be “cost-effective” but no detail of cost (including labor) are given , or comparisons to other approaches.

Reviewer #1: Evidentiary Rating: Potentially informative

Written Review: This study introduced 91 AMR primer sets, along with two primer sets targeting bacterial 16S rRNA and fungal 28S rRNA, for amplicon sequencing. The workflow was validated using genomic DNA extracted from reference isolates, BACT/ALERT samples, and spiked-in blood samples under a 6-hour blood culture procedure.

However, despite the 91 AMR primer sets being distributed across pools 1–7 and pools 8–12, only the first seven pools were used in the experiment, covering just 49 AMR genes​. This limitation raises concerns about the comprehensiveness of the approach and suggests high experimental complexity, as each sample requires at least eight separate reactions (pool 1-7 and species identification), making it less efficient compared to individual PCR experiments.

A major issue in this study is the lack of clear ground truth regarding the types and quantities of AMR genes present in the samples​. Without this reference, it is impossible to accurately assess how many AMR genes were correctly detected. For instance, as shown in Figure 1C, the high occurrence of blaSHV suggests that all samples carrying this gene. However, blaSHV should not be present in fungi, raising concerns about the true positive definition. To improve clarity, the authors should at least provide the ground truth for each sample, along with a clear definition of how it was determined, as supplemental information. Furthermore, as described in line 437, the authors used ResFinder to identify AMR determinants. However, the low identity threshold (40%) may lead to the identification of different gene alleles rather than the intended target genes​.

Moreover, since the study does not disclose the raw analytical data nor provide access to the analysis pipeline, it is impossible to fully assess the accuracy and reliability of the AMR gene prediction.

Figure 1-3 are similar, but the presentation could be clearer. Panel B would be more effectively represented as a three-column table, displaying the actual species, predicted species, and abundance value. Panel C should primarily indicate which species are missing due to low sequencing yield, as this information can be easily described in the text. For panel D, the Y-axis is unclear, particularly regarding the notation of certain AMR genes (e.g., why VanHBX?, OxaB as oxaB?, crpP?, blaLEN?). Additionally, Panel F and G appear redundant, as their information could be more efficiently conveyed using numerical values in the text.

RR\ID Summary of Reviews: This preprint introduces MultiSeq-AMR, a rapid, cost-effective amplicon sequencing workflow for detecting bloodstream infections (BSI) and antimicrobial resistance (AMR) markers. The method, validated using reference isolates, clinical samples, and spiked blood, demonstrates high accuracy in species identification (100%) and AMR gene detection (99.4%) potentially within <12h of blood sample collection. Reviewers acknowledge the potential of MultiSeq-AMR for rapid diagnosis but highlight limitations, including small sample sizes, insufficient validation of all AMR primer pools, concerns about primer specificity and false positives and its clinical relevance. Suggestions for improvement include expanding validation with more diverse samples, providing detailed primer sequences, and addressing cost-effectiveness. Despite these critiques, the workflow is seen as a promising step toward faster, more precise BSI diagnosis in clinical settings.

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/2mufupox/release/3

RR\ID Summary of Reviews: The preprint explores the geographic distribution and burden of non-malarial febrile illnesses (NMFIs) across Tanzania. Reviewers praised the study’s strong epidemiological design, robust dataset, and public health relevance but noted key methodological limitations, including reliance on passive surveillance, lack of laboratory-confirmed diagnoses, and the potential influence of care-seeking behaviors. They recommended refining statistical analyses, clarifying fever definitions, and addressing potential misclassification of malaria-related fevers. While the study highlights the growing public health importance of NMFIs, further research with improved diagnostic rigor is needed to better inform treatment and surveillance strategies. 

Read directly in RR\ID: https://rrid.mitpress.mit.edu/pub/2e7wtunn/release/2

Reviewer #4: Evidentiary Rating: Potentially Informative

Written Review: The manuscript investigates the prevalence and geographic distribution of non-malarial febrile illnesses by malaria transmission (burden) strata in Mainland Tanzania. It claims that non-malarial febrile illnesses are more common in lower malaria transmission areas and that demographic factors influence their prevalence. Targeted diagnostic and treatment strategies are suggested by the author.

While the study covers a broad geographical area and includes a large sample size, the methodology has several limitations, including the definition of adults (>15 years is flawed). The study design is quite confusing, making it nearly impossible to reproduce. The conclusions remain speculative without laboratory confirmation of bacterial, viral, or other parasitic infections as the cause of fever. The exclusion of severe cases and health care recruitment further limits the generalizability of the findings as many households have anti-malarial which are given to children or adults with fever and therefore do not seek health care. Although the study provides valuable epidemiological data, conclusions overstate the implications of the findings due to methodological weaknesses. The recommendation targeted point-of-care testing lacks substantiation, given that no specific NMFI pathogens were identified. The manuscript is potentially informative but requires significant methodological improvements to substantiate its claims. Future studies should incorporate comprehensive diagnostic testing and determine the potential causes of fever. By authors suggesting that patients with fever who come from high-prevalence regions, other factors that cause fever should be prioritized and investigated, this is not only clinically detrimental but also increases the cost of care. The best approach is to treat malaria first, and if patients do not improve, other causes of fevers should be explored.

Reviewer #2: Evidentiary Rating: Strong

Written Review: The research article titled “Mapping of the country-wide prevalence of non-malarial febrile illnesses in areas with varying malaria transmission intensities in Mainland Tanzania” addresses an important and very interesting research topic relating to the diagnosis and management of non-malaria fevers in Tanzania and other Africa countries. This article examines in great depth and details the occurrence and distribution patterns as well as the risk factors of non-malaria fevers in Tanzania. The study has a sound design and methodology and the findings are credible. The authors concludes by recommending a proper selection of health care interventions targeting age population groups affected by non-malaria fevers in Tanzania and other malaria endemic countries. There is no doubt about the public health relevance of the findings presented and hence I strongly recommend the article for publication and wider dissemination. However, there are few minor grammatical errors which need careful proofreading of the manuscript by the authors.

Reviewer #3: Evidentiary Rating: Reliable

Written Review: This is an important study to understand the epidemiology of non-malaria febrile illness (NMFI) in public health facilities in mainland Tanzania.  It is the first large-scale study of NMFIs in Tanzania. The study was large and mostly representative of all districts in Tanzania, across a variety of transmission zones. The paper is well written, and the statistical methods are appropriate for the study design and analytic goal.  The authors address several limitations of their study and possible explanations for the results they saw. 

A main limitation of this study is that it is cross sectional in nature and takes place in health facilities, which is a form of passive surveillance. The prevalence of NMFI at health facilities may be different than that in the community at large if there are variations in care seeking behaviors that result in the population visiting a HF being unrepresentative of the population at large.  The authors briefly touched on differences in care-seeking between males and females, but their paper could be strengthened if they discuss care seeking more broadly and the possible impacts of this on their results (if they believe there would be any). 

Additionally, the authors note that some of the malaria-febrile illnesses identified may have been secondary malaria infections (the malaria did not cause the fever). The study did not test for other etiological agents to decipher between these, which would add strength to their findings. 

However, despite these limitations, this study successfully has shown the large number of NMFIs that exist in Tanzania, highlighting regions where additional research could be done to better understand the etiology of these fevers to craft better clinical guidelines and tests. The authors have provided reliable evidence that NMFI is highly prevalent.

Reviewer #1: Evidentiary Rating: Reliable

Written Review: The report reflects a strong epidemiological design of a rigorously implemented study.  The strengths include a large representative sample obtained from 26 regions of mainland Tanzania, using a well-trained team and was supervised and monitored to generate reliable data. The outcome was well-defined and apparently reliably ascertained.  The analyses were well conducted, and relevant results are presented to justify their key conclusions.

There are a few areas that should be considered.

1. For example, fever is defined either by history obtained from the patient or by measurement of the temperature.  The authors could clarify this. Are there patients who were included based on their claim that they had a fever in the past 24 hours. Are there patients who were afebrile at the time of sampling? 
2. It is assumed that some basic history was collected, including symptoms referable to the respiratory tract, gastrointestinal system, urinary tract, joints or skin. Such symptoms would be helpful in prompting doctors to consider concurrent conditions. Were these data collected? Did they differ in their frequency from participants who has malaria versus those who were negative?
3. It is quite possible that other lab tests may not have been done, in particular a complete blood count. The white blood cell count, and platelet count often show different patterns in malaria versus non-malaria patients. If these were done, it would increase the informational value of the data presented. 
4. The assumption in this study is that all these patients had acute symptoms and had not been treated before. Could this be confirmed?  If there are patients who had longer duration symptoms, looking at the data stratified by those characteristics might be helpful. 
5. With respect to sampling, why is it that some sites in low malaria transmission zones recruited many participants?  Was enrollment consecutive and therefore these sites had a large volume of patients? 
6. Table 2 - presents p-values for single proportions. The meaning of these P-values and the statistical test used to generate them should be included as table notes. 
7. Figure 4 - is there a trend in NMFI prevalence by malaria transmission ?  It may be assumed that the horizontal bars and whiskers shown in the box plots are medians and interquartile ranges. Figure notes could help resolve this.