Author response:
Public Reviews:
Reviewer #1 (Public Review):
Summary:
In their paper, Zhan et al. have used Pf genetic data from simulated data and Ghanaian field samples to elucidate a relationship between multiplicity of infection (MOI) (the number of distinct parasite clones in a single host infection) and force of infection (FOI). Specifically, they use sequencing data from the var genes of Pf along with Bayesian modeling to estimate MOI individual infections and use these values along with methods from queueing theory that rely on various assumptions to estimate FOI. They compare these estimates to known FOIs in a simulated scenario and describe the relationship between these estimated FOI values and another commonly used metric of transmission EIR (entomological inoculation rate).
This approach does fill an important gap in malaria epidemiology, namely estimating the force of infection, which is currently complicated by several factors including superinfection, unknown duration of infection, and highly genetically diverse parasite populations. The authors use a new approach borrowing from other fields of statistics and modeling and make extensive efforts to evaluate their approach under a range of realistic sampling scenarios. However, the write-up would greatly benefit from added clarity both in the description of methods and in the presentation of the results. Without these clarifications, rigorously evaluating whether the author's proposed method of estimating FOI is sound remains difficult. Additionally, there are several limitations that call into question the stated generalizability of this method that should at minimum be further discussed by authors and in some cases require a more thorough evaluation.
Major comments:
(1) Description and evaluation of FOI estimation procedure.
a. The methods section describing the two-moment approximation and accompanying appendix is lacking several important details. Equations on lines 891 and 892 are only a small part of the equations in Choi et al. and do not adequately describe the procedure notably several quantities in those equations are never defined some of them are important to understand the method (e.g. A, S as the main random variables for inter-arrival times and service times, aR and bR which are the known time average quantities, and these also rely on the squared coefficient of variation of the random variable which is also never introduced in the paper). Without going back to the Choi paper to understand these quantities, and to understand the assumptions of this method it was not possible to follow how this works in the paper. At a minimum, all variables used in the equations should be clearly defined.
We thank the reviewer for this useful comment. We plan to clarify the method, including all the relevant variables in our revised manuscript. The reviewer is correct in pointing out that there are more sections and equations in Choi et al., including the derivation of an exact expression for the steady-state queue-length distribution and the two-moment approximation for the queue-length distribution. Since only the latter was directly utilized in our work, we included in the first version of our manuscript only material on this section and not the other. We agree with the reviewer on readers benefiting from additional information on the derivation of the exact expression for the steady-state queue-length distribution. Therefore, we will summarize the derivation of this expression in our revised manuscript. Regarding the assumptions of the method we applied, especially those for going from the exact expression to the two-moment approximation, we did describe these in the Materials and Methods of our manuscript. We recognize from this comment that the writing and organization of this information may not have been sufficiently clear. We had separated the information on this method into two parts, with the descriptive summary placed in the Materials and Methods and the equations or mathematical formula placed in the Appendix. This can make it difficult for readers to connect the two parts and remember what was introduced earlier in the Materials and Methods when reading the equations and mathematical details in the Appendix. For our revised manuscript, we plan to cover both parts in the Materials and Methods, and to provide more of the technical details in one place, which will be easier to understand and follow.
b. Additionally, the description in the main text of how the queueing procedure can be used to describe malaria infections would benefit from a diagram currently as written it's very difficult to follow.
We thank the reviewer for this suggestion. We will add a diagram illustrating the connection between the queueing procedure and malaria transmission.
c. Just observing the box plots of mean and 95% CI on a plot with the FOI estimate (Figures 1, 2, and 10-14) is not sufficient to adequately assess the performance of this estimator. First, it is not clear whether the authors are displaying the bootstrapped 95%CIs or whether they are just showing the distribution of the mean FOI taken over multiple simulations, and then it seems that they are also estimating mean FOI per host on an annual basis. Showing a distribution of those per-host estimates would also be helpful. Second, a more quantitative assessment of the ability of the estimator to recover the truth across simulations (e.g. proportion of simulations where the truth is captured in the 95% CI or something like this) is important in many cases it seems that the estimator is always underestimating the true FOI and may not even contain the true value in the FOI distribution (e.g. Figure 10, Figure 1 under the mid-IRS panel). But it's not possible to conclude one way or the other based on this visualization. This is a major issue since it calls into question whether there is in fact data to support that these methods give good and consistent FOI estimates.
There appears to be some confusion on what we display in some key figures. We will clarify this further both here and in the revised text. In Figures 1, 2, and 10-14, we displayed the bootstrapped distributions including the 95% CIs. These figures do not show the distribution of the mean FOI taken over multiple simulations. We estimated mean FOI on an annual basis per host in the following sense. Both of our proposed methods require either a steady-state queue length distribution, or moments of this distribution for FOI inference. However, we only have one realization or observation for each individual host, and we do not have access to either the time-series observation of a single individual’s MOI or many realizations of a single individual’s MOI at the same sampling time. This is typically the case for empirical data, although numerical simulations could circumvent this limitation and generate such output. Nonetheless, we do have a queue length distribution at the population level for both the simulation output and the empirical data, which can be obtained by simply aggregating MOI estimates across all sampled individuals. We use this population-level queue length distribution to represent and approximate the steady-state queue length distribution at the individual level. Such representation or approximation does not consider explicitly any individual heterogeneity due to biology or transmission. The estimated FOI is per host in the sense of representing the FOI experienced by an individual host whose queue length distribution is approximated from the collection of all sampled individuals. The true FOI per host per year in the simulation output is obtained from dividing the total FOI of all hosts per year by the total number of all hosts. Therefore, our estimator, combined with the demographic information on population size, is for the total number of Plasmodium falciparum infections acquired by all individual hosts in the population of interest per year.
We evaluated the impact of individual heterogeneity on FOI inference by introducing individual heterogeneity into the simulations. With a considerable amount of transmission heterogeneity across individuals (namely 2/3 of the population receiving more than 90% of all bites whereas the remaining 1/3 receives the rest of the bites), our two methods exhibit a similar performance than those of the homogeneous transmission scenarios.
Concerning the second point, we will add a quantitative assessment of the ability of the estimator to recover the truth across simulations and include this information in the legend of each figure. In particular, we will provide the proportion of simulations where the truth is captured by the entire bootstrap distribution, in addition to some measure of relative deviation, such as the relative difference between the true FOI value and the median of the bootstrap distribution for the estimate. This assessment will be a valuable addition, but please note that the comparisons we have provided in a graphical way do illustrate the ability of the methods to estimate “sensible” values, close to the truth despite multiple sources of errors. “Close” is here relative to the scale of variation of FOI in the field and to the kind of precision that would be useful in an empirical context. From a practical perspective based on the potential range of variation of FOI, the graphical results already illustrate that the estimated distributions would be informative.
d. Furthermore the authors state in the methods that the choice of mean and variance (and thus second moment) parameters for inter-arrival times are varied widely, however, it's not clear what those ranges are there needs to be a clear table or figure caption showing what combinations of values were tested and which results are produced from them, this is an essential component of the method and it's impossible to fully evaluate its performance without this information. This relates to the issue of selecting the mean and variance values that maximize the likelihood of observing a given distribution of MOI estimates, this is very unclear since no likelihoods have been written down in the methods section of the main text, which likelihood are the authors referring to, is this the probability distribution of the steady state queue length distribution? At other places the authors refer to these quantities as Maximum Likelihood estimators, how do they know they have found the MLE? There are no derivations in the manuscript to support this. The authors should specify the likelihood and include in an appendix an explanation of why their estimation procedure is in fact maximizing this likelihood, preferably with evidence of the shape of the likelihood, and how fine the grid of values they tested is for their mean and variance since this could influence the overall quality of the estimation procedure.
We thank the reviewer for pointing out these aspects of the work that can be further clarified. We will specify the ranges for the choice of mean and variance parameters for inter-arrival times as well as the grid of values tested in the corresponding figure caption or in a separate supplementary table. We maximized the likelihood of observing the set of individual MOI estimates in a sampled population given steady queue length distributions (with these distributions based on the two-moment approximation method for different combinations of the mean and variance of inter-arrival times). We will add a section to either the Materials and Methods or the Appendix in our revised manuscript including an explicit formulation of the likelihood.
We will add example figures on the shape of the likelihood to the Appendix. We will also test how choices of the grid of values influence the overall quality of the estimation procedure. Specifically, we will further refine the grid of values to include more points and examine whether the results of FOI inference are consistent and robust against each other.
(2) Limitation of FOI estimation procedure.
a. The authors discuss the importance of the duration of infection to this problem. While I agree that empirically estimating this is not possible, there are other options besides assuming that all 1-5-year-olds have the same duration of infection distribution as naïve adults co-infected with syphilis. E.g. it would be useful to test a wide range of assumed infection duration and assess their impact on the estimation procedure. Furthermore, if the authors are going to stick to the described method for duration of infection, the potentially limited generalizability of this method needs to be further highlighted in both the introduction, and the discussion. In particular, for an estimated mean FOI of about 5 per host per year in the pre-IRS season as estimated in Ghana (Figure 3) it seems that this would not translate to 4-year-old being immune naïve, and certainly this would not necessarily generalize well to a school-aged child population or an adult population.
The reviewer is indeed correct about the difficulty of empirically measuring the duration of infection for 1-5-year-olds, and that of further testing whether these 1-5-year-olds exhibit the same distribution for duration of infection as naïve adults co-infected with syphilis. We will nevertheless continue to use the described method for duration of infection, while better acknowledging and discussing the limitations this aspect of the method introduces. We note that the infection duration from the historical clinical data we have relied on, is being used in the malaria modeling community as one of the credible sources for this parameter of untreated natural infections in malaria-naïve individuals in malaria-endemic settings of Africa (e.g. in the agent-based model OpenMalaria, see 1).
It is important to emphasize that the proposed methods apply to the MOI estimates for naïve or close to naïve patients. They are not suitable for FOI inference for the school-aged children and the adult populations of high-transmission endemic regions, since individuals in these age classes have been infected many times and their duration of infection is significantly shortened by their immunity. To reduce the degree of misspecification in infection duration and take full advantage of our proposed methods, we will emphasize in the revision the need to prioritize in future data collection and sampling efforts the subpopulation class who has received either no infection or a minimum number of infections in the past, and whose immune profile is close to that of naïve adults, for example, infants. This emphasis is aligned with the top priority of all intervention efforts in the short term, which is to monitor and protect the most vulnerable individuals from severe clinical symptoms and death.
Also, force of infection for naïve hosts is a key basic parameter for epidemiological models of a complex infectious disease such as falciparum malaria, whether for agent-based formulations or equation-based ones. This is because force of infection for non-naïve hosts is typically a function of their immune status and the force of infection of naïve hosts. Thus, knowing the force of infection of naïve hosts can help parameterize and validate these models by reducing degrees of freedom.
b. The evaluation of the capacity parameter c seems to be quite important and is set at 30, however, the authors only describe trying values of 25 and 30, and claim that this does not impact FOI inference, however it is not clear that this is the case. What happens if the carrying capacity is increased substantially? Alternatively, this would be more convincing if the authors provided a mathematical explanation of why the carrying capacity increase will not influence the FOI inference, but absent that, this should be mentioned and discussed as a limitation.
Thank you for this question. We will investigate more values of the parameter c systematically, including substantially higher ones. We note however that this quantity is the carrying capacity of the queuing system, or the maximum number of blood-stage strains that an individual human host can be co-infected with. We do have empirical evidence for the value of the latter being around 20 (2). This observed value provides a lower bound for parameter c. To account for potential under-sampling of strains, we thus tried values of 25 and 30 in the first version of our manuscript.
In general, this parameter influences the steady-state queue length distribution based on the two-moment approximation, more specifically, the tail of this distribution when the flow of customers/infections is high. Smaller values of parameter c put a lower cap on the maximum value possible for the queue length distribution. The system is more easily “overflowed”, in which case customers (or infections) often find that there is no space available in the queuing system/individual host upon their arrival. These customers (or infections) will not increment the queue length. The parameter c has therefore a small impact for the part of the grid resulting in low flows of customers/infection, for which the system is unlikely to be overflowed. The empirical MOI distribution centers around 4 or 5 with most values well below 10, and only a small fraction of higher values between 15-20 (2). When one increases the value of c, the part of the grid generating very high flows of customers/infections results in queue length distributions with a heavy tail around large MOI values that are not supported by the empirical distribution. We therefore do not expect that substantially higher values for parameter c would change either the relative shape of the likelihood or the MLE.
Reviewer #2 (Public Review):
Summary:
The authors combine a clever use of historical clinical data on infection duration in immunologically naive individuals and queuing theory to infer the force of infection (FOI) from measured multiplicity of infection (MOI) in a sparsely sampled setting. They conduct extensive simulations using agent-based modeling to recapitulate realistic population dynamics and successfully apply their method to recover FOI from measured MOI. They then go on to apply their method to real-world data from Ghana before and after an indoor residual spraying campaign.
Strengths:
(1) The use of historical clinical data is very clever in this context.
(2) The simulations are very sophisticated with respect to trying to capture realistic population dynamics.
(3) The mathematical approach is simple and elegant, and thus easy to understand.
Weaknesses:
(1) The assumptions of the approach are quite strong and should be made more clear. While the historical clinical data is a unique resource, it would be useful to see how misspecification of the duration of infection distribution would impact the estimates.
We thank the reviewer for bringing up the limitation of our proposed methods due to their reliance on a known and fixed duration of infection from historical clinical data. Please see our response to reviewer 1 comment 2a.
(2) Seeing as how the assumption of the duration of infection distribution is drawn from historical data and not informed by the data on hand, it does not substantially expand beyond MOI. The authors could address this by suggesting avenues for more refined estimates of infection duration.
We thank the reviewer for pointing out a potential improvement to the work. We acknowledge that FOI is inferred from MOI, and thus is dependent on the information contained in MOI. FOI reflects risk of infection, is associated with risk of clinical episodes, and can relate local variation in malaria burden to transmission better than other proxy parameters for transmission intensity. It is possible that MOI can be as informative as FOI when one regresses the risk of clinical episodes and local variation in malaria burden with MOI. But MOI by definition is a number and not a rate parameter. FOI for naïve hosts is a key basic parameter for epidemiological models. This is because FOI of non-naïve hosts is typically a function of their immune status and the FOI of naïve hosts. Thus, knowing the FOI of naïve hosts can help parameterize and validate these models by reducing degrees of freedom. In this sense, we believe the transformation from MOI to FOI provides a useful step.
Given the difficulty of measuring infection duration, estimating infection duration and FOI simultaneously appears to be an attractive alternative, as the referee pointed out. This will require however either cohort studies or more densely sampled cross-sectional surveys due to the heterogeneity in infection duration across a multiplicity of factors. These kinds of studies have not been, and will not be, widely available across geographical locations and time. This work aims to utilize more readily available data, in the form of sparsely sampled single-time-point cross-sectional surveys.
(3) It is unclear in the example how their bootstrap imputation approach is accounting for measurement error due to antimalarial treatment. They supply two approaches. First, there is no effect on measurement, so the measured MOI is unaffected, which is likely false and I think the authors are in agreement. The second approach instead discards the measurement for malaria-treated individuals and imputes their MOI by drawing from the remaining distribution. This is an extremely strong assumption that the distribution of MOI of the treated is the same as the untreated, which seems unlikely simply out of treatment-seeking behavior. By imputing in this way, the authors will also deflate the variability of their estimates.
We thank the reviewer for pointing out aspects of the work that can be further clarified. It is difficult to disentangle the effect of drug treatment on measurement, including infection status, MOI, and duration of infection. Thus, we did not attempt to address this matter explicitly in the original version of our manuscript. Instead, we considered two extreme scenarios which bound reality, well summarized by the reviewer. First, if drug treatment has had no impact on measurement, the MOI of the drug-treated 1-5-year-olds would reflect their true underlying MOI. We can then use their MOI directly for FOI inference. Second, if the drug treatment had a significant impact on measurement, i.e., if it completely changed the infection status, MOI, and duration infection of drug-treated 1-5-year-olds, we would need to either exclude those individuals’ MOI or impute their true underlying MOI. We chose to do the latter in the original version of the manuscript. If those 1-5-year-olds had not received drug treatment, they would have had similar MOI values than those of the non-treated 1-5-year-olds. We can then impute their MOI by sampling from the MOI estimates of non-treated 1-5-year-olds.
The reviewer is correct in pointing out that this imputation does not add additional information and can potentially deflate the variability of MOI distributions, compared to simply throwing or excluding those drug-treated 1-5-year-olds from the analysis. Thus, we can include in our revision FOI estimates with the drug-treated 1-5-year-olds excluded in the estimation.
- For similar reasons, their imputation of microscopy-negative individuals is also questionable, as it also assumes the same distributions of MOI for microscopy-positive and negative individuals.
We imputed the MOI values of microscopy-negative but PCR-positive 1-5-year-olds by sampling from the microscopy-positive 1-5-year-olds, effectively assuming that both have the same, or similar, MOI distributions. We did so because there is a weak relationship in our Ghana data between the parasitemia level of individual hosts and their MOI (or detected number of var genes, on the basis of which the MOI values themselves were estimated). Parasitemia levels underlie the difference in detection sensitivity of PCR and microscopy.
We will elaborate on this matter in our revised manuscript and include information from our previous and on-going work on the weak relationship between MOI/the number of var genes detected within an individual host and their parasitemia levels. We will also discuss potential reasons or hypotheses for this pattern.
Reviewer #3 (Public Review):
Summary:
It has been proposed that the FOI is a method of using parasite genetics to determine changes in transmission in areas with high asymptomatic infection. The manuscript attempts to use queuing theory to convert multiplicity of infection estimates (MOI) into estimates of the force of infection (FOI), which they define as the number of genetically distinct blood-stage strains. They look to validate the method by applying it to simulated results from a previously published agent-based model. They then apply these queuing theory methods to previously published and analysed genetic data from Ghana. They then compare their results to previous estimates of FOI.
Strengths:
It would be great to be able to infer FOI from cross-sectional surveys which are easier and cheaper than current FOI estimates which require longitudinal studies. This work proposes a method to convert MOI to FOI for cross-sectional studies. They attempt to validate this process using a previously published agent-based model which helps us understand the complexity of parasite population genetics.
Weaknesses:
(1) I fear that the work could be easily over-interpreted as no true validation was done, as no field estimates of FOI (I think considered true validation) were measured. The authors have developed a method of estimating FOI from MOI which makes a number of biological and structural assumptions. I would not call being able to recreate model results that were generated using a model that makes its own (probably similar) defined set of biological and structural assumptions a validation of what is going on in the field. The authors claim this at times (for example, Line 153 ) and I feel it would be appropriate to differentiate this in the discussion.
We thank the reviewer for this comment, although we think there is a mis-understanding on what can and cannot be practically validated in the sense of a “true” measure of FOI that would be free from assumptions for a complex disease such as malaria. We would not want the results to be over-interpreted and will extend the discussion of what we have done to test the methods. We note that for the performance evaluation of statistical methods, the use of simulation output is quite common and often a necessary and important step. In some cases, the simulation output is generated by dynamical models, whereas in others, by purely descriptive ones. All these models make their own assumptions which are necessarily a simplification of reality. The stochastic agent-based model (ABM) of malaria transmission utilized in this work has been shown to reproduce several important patterns observed in empirical data from high-transmission regions, including aspects of strain diversity which are not represented in simpler models.
In what sense this ABM makes a set of biological and structural assumptions which are “probably similar” to those of the queuing methods we present, is not clear to us. We agree that relying on models whose structural assumptions differ from those of a given method or model to be tested, is the best approach. Our proposed methods for FOI inference based on queuing theory rely on the duration of infection distribution and the MOI distribution among sampled individuals, both of which can be direct outputs from the ABM. But these methods are agnostic on the specific mechanisms or biology underlying the regulation of duration and MOI.
Another important point raised by this comment is what would be the “true” FOI value against which to validate our methods. Empirical MOI-FOI pairs for FOI measured directly by tracking cohort studies are still lacking. There are potential measurement errors for both MOI and FOI because the polymorphic markers typically used in different cohort studies cannot differentiate hyper-diverse antigenic strains fully and well (5). Also, these cohort studies usually start with drug treatment. Alternative approaches do not provide a measure of true FOI, in the sense of the estimation being free from assumptions. For example, one approach would be to fit epidemiological models to densely sampled/repeated cross-sectional surveys for FOI inference. In this case, no FOI is measured directly and further benchmarked against fitted FOI values. The evaluation of these models is typically based on how well they can capture other epidemiological quantities which are more easily sampled or measured, including prevalence or incidence. This is similar to what is done in this work. We selected the FOI values that maximize the likelihood of observing the given distribution of MOI estimates. Furthermore, we paired our estimated FOI value for the empirical data from Ghana with another independently measured quantity EIR (Entomological Inoculation Rate), typically used in the field as a measure of transmission intensity. We check whether the resulting FOI-EIR point is consistent with the existing set of FOI-EIR pairs and the relationship between these two quantities from previous studies. We acknowledge that as for model fitting approaches for FOI inference, our validation is also indirect for the field data.
Prompted by the reviewer’s comment, we will discuss this matter in more detail in our revised manuscript, including clarifying further certain basic assumptions of our agent-based model, emphasizing the indirect nature of the validation with the field data and the existing constraints for such validation.
(2) Another aspect of the paper is adding greater realism to the previous agent-based model, by including assumptions on missing data and under-sampling. This takes prominence in the figures and results section, but I would imagine is generally not as interesting to the less specialised reader. The apparent lack of impact of drug treatment on MOI is interesting and counterintuitive, though it is not really mentioned in the results or discussion sufficiently to allay my confusion. I would have been interested in understanding the relationship between MOI and FOI as generated by your queuing theory method and the model. It isn't clear to me why these more standard results are not presented, as I would imagine they are outputs of the model (though happy to stand corrected - it isn't entirely clear to me what the model is doing in this manuscript alone).
We thank the reviewer for this comment. We will add supplementary figures for the MOI distributions generated by the queuing theory method (i.e., the two-moment approximation method) and our agent-based model in our revised manuscript.
In the first version of our manuscript, we considered two extreme scenarios which bound the reality, instead of simply assuming that drug treatment does not impact the infection status, MOI, and duration of infection. See our response to reviewer 2 point (3). The resulting FOI estimates differ but not substantially across the two extreme scenarios, partially because drug-treated individuals’ MOI distribution is similar to that of non-treated individuals (or the apparent lack of drug treatment on MOI as pointed by the referee). We will consider potentially adding some formal test to quantify the difference between the two MOI distributions and how significant the difference is. We will discuss which of the two extreme scenarios reality is closer to, given the result of the formal test. We will also discuss in our revision possible reasons/hypotheses underlying the impact of drug treatment on MOI from the perspective of the nature, efficiency, and duration of the drugs administrated.
Regarding the last point of the reviewer, on understanding the relationship between MOI and FOI, we are not fully clear about what was meant. We are also confused about the statement on what the “model is doing in this manuscript alone”. We interpret the overall comment as the reviewer suggesting a better understanding of the relationship between MOI and FOI, either between their distributions, or the moments of their distributions, perhaps by fitting models including simple linear regression models. This approach is in principle possible, but it is not the focus of this work. It will be equally difficult to evaluate the performance of this alternative approach given the lack of MOI-FOI pairs from empirical settings with directly measured FOI values (from large cohort studies). Moreover, the qualitative relationship between the two quantities is intuitive. Higher FOI values should correspond to higher MOI values. Less variable FOI values should correspond to more narrow or concentrated MOI distributions, whereas more variable FOI values should correspond to more spread-out ones. We will discuss this matter in our revised manuscript.
(3) I would suggest that outside of malaria geneticists, the force of infection is considered to be the entomological inoculation rate, not the number of genetically distinct blood-stage strains. I appreciate that FOI has been used to explain the latter before by others, though the authors could avoid confusion by stating this clearly throughout the manuscript. For example, the abstract says FOI is "the number of new infections acquired by an individual host over a given time interval" which suggests the former, please consider clarifying.
We thank the reviewer for this helpful comment as it is fundamental that there is no confusion on the basic definitions. EIR, the entomological inoculation rate, is closely related to the force of infection but is not equal to it. EIR focuses on the rate of arrival of infectious bites and is measured as such by focusing on the mosquito vectors that are infectious and arrive to bite a given host. Not all these bites result in actual infection of the human host. Epidemiological models of malaria transmission clearly make this distinction, as FOI is defined as the rate at which a host acquires infection. This definition comes from more general models for the population dynamics of infectious diseases in general. (For diseases simpler than malaria, with no super-infection, the typical SIR models define the force of infection as the rate at which a susceptible individual becomes infected). For malaria, force of infection refers to the number of blood-stage new infections acquired by an individual host over a given time interval. This distinction between EIR and FOI is the reason why studies have investigated their relationship, with the nonlinearity of this relationship reflecting the complexity of the underlying biology and how host immunity influences the outcome of an infectious bite.
We agree however with the referee that there could be some confusion in our definition resulting from the approach we use to estimate the MOI distribution (which provides the basis for estimating FOI). In particular, we rely on the non-existent to very low overlap of var repertoires among individuals with MOI=1, an empirical pattern we have documented extensively in previous work (See 2, 3, and 4). The method of _var_coding and its Bayesian formulation rely on the assumption of negligible overlap. We note that other approaches for estimating MOI (and FOI) based on other polymorphic markers, also make this assumption (reviewed in 5). Ultimately, the FOI we seek to estimate is the one defined as specified above and in both the abstract and introduction, consistent with the epidemiological literature. We will include clarification in the introduction and discussion of this point in the revision.
(4) Line 319 says "Nevertheless, overall, our paired EIR (directly measured by the entomological team in Ghana (Tiedje et al., 2022)) and FOI values are reasonably consistent with the data points from previous studies, suggesting the robustness of our proposed methods". I would agree that the results are consistent, given that there is huge variation in Figure 4 despite the transformed scales, but I would not say this suggests a robustness of the method.
We will modify the relevant sentences to use “consistent” instead of “robust”.
(5) The text is a little difficult to follow at times and sometimes requires multiple reads to understand. Greater precision is needed with the language in a few situations and some of the assumptions made in the modelling process are not referenced, making it unclear whether it is a true representation of the biology.
We thank the reviewer for this comment. As also mentioned in the response to reviewer 1’s comments, we will reorganize and rewrite parts of the text in our revision to improve clarity.
References and Notes
(1) Maire, N. et al. A model for natural immunity to asexual blood stages of Plasmodium falciparum malaria in endemic areas. Am J Trop Med Hyg., 75(2 Suppl):19-31 (2006).
(2) Tiedje, K. E. et al. Measuring changes in Plasmodium falciparum census population size in response to sequential malaria control interventions. eLife, 12 (2023).
(3) Day, K. P. et al. Evidence of strain structure in Plasmodium falciparum var gene repertoires in children from Gabon, West Africa. Proc. Natl. Acad. Sci. U.S.A., 114(20), 4103-4111 (2017).
(4) Ruybal-Pesántez, S. et al. Population genomics of virulence genes of Plasmodium falciparum in clinical isolates from Uganda. Sci. Rep., 7(11810) (2017).
(5) Labbé, F. et al. Neutral vs. non-neutral genetic footprints of Plasmodium falciparum multiclonal infections. PLoS Comput Biol 19(1) (2023).
