Outcomes of controlled human malaria infection after BCG vaccination

Recent evidence suggests that certain vaccines, including Bacillus-Calmette Guérin (BCG), can induce changes in the innate immune system with non-specific memory characteristics, termed ‘trained immunity’. Here we present the results of a randomised, controlled phase 1 clinical trial in 20 healthy male and female volunteers to evaluate the induction of immunity and protective efficacy of the anti-tuberculosis BCG vaccine against a controlled human malaria infection. After malaria challenge infection, BCG vaccinated volunteers present with earlier and more severe clinical adverse events, and have significantly earlier expression of NK cell activation markers and a trend towards earlier phenotypic monocyte activation. Furthermore, parasitemia in BCG vaccinated volunteers is inversely correlated with increased phenotypic NK cell and monocyte activation. The combined data demonstrate that BCG vaccination alters the clinical and immunological response to malaria, and form an impetus to further explore its potential in strategies for clinical malaria vaccine development.

The authors show that BCG vaccination 5 weeks before controlled human malaria infection results in better control of parasitaemia and increased activation of NK cells and monocytes coinciding with the appearance of blood stage parasites in peripheral circulation. Due to the nature of the experiments, the number of volunteers are small and the changes are observed only in approximately half of the BCG-immunised volunteers but nevertheless significant. The increases in NK and monocyte activation appear to be due to a heightened reactivity of these cells rather than persistent activation and as such form part of the recently described innate or trained memory. The results are interesting and novel in that the effect of BCG vaccination on human malaria have not been investigated previously. However, the mechanisms underlying the increased responsiveness of NK cells after BCG vaccination are not (yet) known or why they occur only in a proportion of BCG vaccinated volunteers. Furthermore, given that BCG vaccination in infancy is part of the EPI programme in Sub-Saharan Africa, benefits for immunity to malaria or changes in vaccination regime to deploy such benefits seem unlikely. The authors state in the discussion that BCG vaccination may have implication for improving immunity to malaria but do not further elucidate how that can be achieved. To my knowledge -almost all infants born in sub-Saharan Africa will be immunised with BCG at or shortly after birth and any beneficial effects on severe malarial disease at least during infancy -if the benefits of BCG vaccination last long enough as the authors seem to think -should be present already. Maybe the authors could expand how they see BCG vaccination deployed?

Minor comments
Reviewer #2 (Remarks to the Author): This manuscript describes a human malaria CHMI study using the standard 5 mosquito-bite model to induce falciparum malaria. This model is usually used to assess the efficacy of vaccines against malaria, however in this study the investigators have assessed the effect of BCG vaccination on immunity to malaria. The rationale for this innovative study is well-described in the introduction and is to assess the impact of inducing innate immunity on protection from malaria.
Unfortunately, while the rationale for the study is well-presented, the results are not and is most cases are either non-significant or only marginally significant. In addition, many of the claims made, particularly in the abstract are not supported by the data presented. Firstly, the authors claim that the BGC-vaccinated participants experienced earlier and more severe clinical symptoms to malaria CHMI, but absolutely no detail is provided as to what these symptoms were or how they were graded and whether these symptoms were reported by participants themselves or observed by investigators (or whether either participants or investigators were blinded). As a consequence, one cannot determine the importance of this observation. Secondly, they claim that these symptoms were associated with the induction of the immune responses that they describe in the BCG-vaccinated group, but no evidence to support this association is presented and this association might be coincidental, particularly given the small numbers in this study. Thirdly, the author suggest that both the enhanced symptoms and induced immunity are associated with reduced parasitaemia at 5 weeks post CHMI, but again there is absolutely no analysis presented to support this. I couldn't even find the PCR data at 5 weeks in the manuscript.
Overall, the findings are weak and add little to the field. The trial is so poorly described that it is hard to determine the importance of the findings in the context presented. If the paper were re-written to describe the study to the standard usually expected, the findings would still be too marginal to be of importance. Most of the immunology figures only show the data for the BCG group, although the text describes comparisons with the unvaccinated group. Both ought to be shown to allow the reader to assess the validity of the claims made.
The study is also largely unreproducible as reported, particularly as the primary endpoint is not described nor the method used to assess it. No information is given about the method for the primary endpoint of the trial (malaria qPCR) and whether the interpretation of PCR data was made by investigators blinded to the vaccination status of the volunteers. It's not stated how often or for how long PCR was performed. One assumes that PCR was performed in real-time, but again this is not described. There is no CONSORT checklist and the T cell methods do not meet the MIATA guidelines, particularly for the ICS itself where the method is minimally described despite ample space in the supplementary to do this properly. The BCG dose is not specified.
The statistical analyses presented are appropriate, although often described in the text and not on the figure itself. Also, it would be useful to know where if a statistic is not given whether a test was performed and a non-significant result obtained and whether correction for multiple analyses were made. A Kaplan-Meier analysis should be performed for the qPCR data during follow-up.

Reviewer #3 (Remarks to the Author):
This is a very interesting study about trained innate immunity in a malaria CHIM, and the authors make a fair case that this can exist. I am generally favorable to the report, although I think that there were some fundamental flaws in study design that cannot be corrected given the effort that is required for CHIM to be undertaken. First and foremost was the relatively short interval between BCG vaccine and challenge. The clinical observations surrounding trained innate immunity occur on a much longer time scale, so 5 weeks seems like a very short time interval between vaccine and challenge. My second objection to the trial design was the very very short period when parasitemia was tolerated. As parasitemia was always sub patent, there was very little to suggest that at least one more day of clinical illness was dangerous to the volunteers. I realize, of course, that Sauerwein and colleagues were probably told by their institutional ethics panel how much clinical illness was acceptable, but this decision contributes to what appear to be significant but small effects that run through the manuscript. A third deficiency, and one that may actually be addressable even at this time point, is the lack of transcriptomic data as well as ChIP seq data. Such data, while expensive and (in the case of ChIP seq) labor intensive, would greatly increase the impact of the manuscript.
All of this being said, this is a piece of work that has importance. Some minor comments: 1) why do the authors believe that BCG vaccinate patients were more symptomatic? This seems like a fairly robust observation, but the numbers are small and the explanation is not obvious. 2) during the pre erythrocytic stage, the authors conclude that the non BCG treated group showed no inflammation. Can this really be said? The number of parameters examined was very small. Please note that transcriptomic analysis of PBMC might have shown otherwise. 3) Figure 3C is not only negative data, but is predictable. I would drop it. 4) statements concerning the acquisition of anti-CSP antibodies seem rather trivial in nature. The authors are probably the world's experts on this topic, and should be aware that one challenge with 5 mosquitoes would not be likely to result in acquired immunity to sporozoite challenge. (as an aside, it would be nice if the authors included in the Methods section of the paper a little bit of data about what the actual challenge was. What percentage of their mosquitoes are actually infected and how many sporozoites per mosquito were expected as an infecting dose. How variable is sporozoite challenge? This may be in their earlier reports, but a short statement would be useful). 5) lines 144-146. Similar comments about making a sweeping statement about the lack of inflammation 6) lines 179-181. Is there already clinical data on the effects of BCG on surviving malaria? It seems that given the clinical studies published to date, some knowledge is already publicly available. 7) line 209-211. I do not understand what this means. The authors are using the word "allocation" in a way that is foreign to a native English speaker. Please re write the sentence. 8) Figures: I dno not understand why some of the figures are only showing data in the BCG group and not the controls. For example, 1D-F and Fig 2. In addition, I think the legends are a bit sparse in their descriptions of the experiments. I am not certain if this is because of a word count requirement, but they could be a little easier to understand.

Response to reviewers' comments:
We would like to thank the reviewers for their review and constructive comments. We feel this has given us the opportunity to significantly improve the manuscript. We have responded to the reviewers' remarks point-by-point below, and have indicated with tracked changes where the manuscript has been changed.
Sincerely yours on behalf of all authors, Prof. Robert W. Sauerwein

The authors show that BCG vaccination 5 weeks before controlled human malaria infection results in better control of parasitaemia and increased activation of NK cells and monocytes coinciding with the appearance of blood stage parasites in peripheral circulation. Due to the nature of the experiments, the number of volunteers are small and the changes are observed only in approximately half of the BCG-immunised volunteers but nevertheless significant. The increases in NK and monocyte activation appear to be due to a heightened reactivity of these cells rather than persistent activation and as such form part of the recently described innate or trained memory. The results are interesting and novel in that the effect of BCG vaccination on human malaria have not been investigated previously. However, the mechanisms underlying the increased responsiveness of NK cells after BCG vaccination are not (yet) known or why they occur only in a proportion of BCG vaccinated volunteers. Furthermore, given that BCG vaccination in infancy is part of the EPI programme in Sub-Saharan
Africa, benefits for immunity to malaria or changes in vaccination regime to deploy such benefits seem unlikely.
Authors' response: The most important novelty of the current study is the evidence that monocyte and NK cell responses after BCG vaccination correlate with decreased parasitaemia in a major clinically relevant infection. So far, BCG induced trained innate immune responses have been confined to in vitro cell stimulation studies where the underlying cellular mechanisms have been extensively explored by us and others (Arts et al. Cell Host and Microbe 2017;Chen Cheng et al. Science 2014;Saeed et al. Science 2014). Indeed, these studies were restricted to transcriptomic and epigenetic changes in monocytes rather than NK cells which clearly warrants further study in future trials. We have highlighted this in the discussion: Text added to the manuscript: 'A recent study examined the epigenetic and transcriptomic changes in monocytes of healthy volunteers vaccinated with BCG (Arts et al. Cell Host and Microbe 2018) , showing genome-wide changes in histone H3 acetylation at lysine 27 (H3K27ac) in 'responding' volunteers. Our study finds functional changes in NK cells as well, confirming previous in vitro observations (Kleinnijenhuis Clin Immunol 2014). This may be the result of increased monocyte activation, as NK cell activity against malaria is partially dependent on monocytes (Artavanis-Tsakonas, J Immunol 2003). Whether BCG induces epigenetic changes in NK cells as well should be subject of a future study.' As for malaria endemic countries where BCG is already part of the EPI program, these findings may a strong additional impetus to improve current BCG immunization practices and/or policies, particularly in areas where the incidence of tuberculosis is low.
The potential effect of BCG on malaria in endemic areas needs further study. A previous study showed that BCG revaccination did not reduce malaria morbidity (Rodrigues et al TMIH, 2006). However, this study did not take into account the effects of DTP vaccination during the study period, known to interfere with the overall non-specific effects of BCG (Roth et al. BMJ 2010). We have added the following text to the discussion. Text added to the manuscript: 'Though BCG vaccination is common practice in malaria endemic countries as part of the WHO Expanded Programme on Immunization, potential efficacy against malaria and other pathogens underscores the need for investment in timely and correct BCG administration. Epidemiological data and randomized trials suggest revaccination with live-attenuated vaccines such as BCG confers additional protection against all cause mortality (Benn et al, EBioMedicine 2016). It will be important to determine whether BCG revaccination induces non-specific beneficial effects against malaria. Although BCG revaccination did not reduce malaria morbidity in one study in Guinea-Bissau (Rodriguez et al, TMIH 2007)

Minor comment 2:
The authors state in the discussion that BCG vaccination may have implication for improving immunity to malaria but do not further elucidate how that can be achieved. To my knowledgealmost all infants born in sub-Saharan Africa will be immunised with BCG at or shortly after birth and any beneficial effects on severe malarial disease at least during infancy -if the benefits of BCG vaccination last long enough as the authors seem to think -should be present already. Maybe the authors could expand how they see BCG vaccination deployed?
Authors' response: Though improvements in the timing and correct administration of BCG vaccine may still be made in malaria endemic areas, the greatest gains may be obtained where BCG revaccination prior to the malaria transmission season may improve protection or the acquisition of immunity.

Reviewer #2 (Remarks to the Author):
This manuscript describes a human malaria CHMI study using the standard 5 mosquito-bite model to induce falciparum malaria. This model is usually used to assess the efficacy of vaccines against malaria, however in this study the investigators have assessed the effect of BCG vaccination on immunity to malaria. The rationale for this innovative study is well-described in the introduction and is to assess the impact of inducing innate immunity on protection from malaria.
Major comment 1: Unfortunately, while the rationale for the study is well-presented, the results are not and is most cases are either non-significant or only marginally significant. In addition, many of the claims made, particularly in the abstract are not supported by the data presented.

Firstly, the authors claim that the BGC-vaccinated participants experienced earlier and more severe clinical symptoms to malaria CHMI, but absolutely no detail is provided as to what these symptoms were or how they were graded and whether these symptoms were reported by participants themselves or observed by investigators (or whether either participants or investigators were blinded). As a consequence, one cannot determine the importance of this observation.
Authors' response: We have added detail about the collection and grading of adverse events to the manuscript. In short, both solicited and unsolicited adverse events were collected using patient diaries and daily questioning by the investigators. Adverse events were graded according to predefined criteria listed in the Clinical Trial Protocol. As reported, the BCG vaccinated group as a whole developed earlier and more severe symptoms that the unvaccinated controls. We did not perform further sub-analyses per to symptom type because of the small number of volunteers. Moreover, the types of adverse events occurring after CHMI have been extensively published previously (Roestenberg et al. NEJM, 2009;Roestenberg et al. PlosOne 2012). Text added to the manuscript: 'Recording of adverse events Subjects recorded clinical symptoms in a diary, from the time of BCG vaccination until 37 days after the CHMI, as described previously (Roestenberg et al., NEJM, 2009;Roestenberg et al., PLOSOne 2012).

Both solicited and unsolicited adverse events were recorded after questioning by the investigators at set time points: prior to BCG vaccination, prior to the CHMI, daily from day 6 after infection until 3 days after antimalarial treatment, and on day 37 post CHMI. Adverse events were graded according to criteria defined in the Clinical Trial Protocol: Mild (grade 1): awareness of symptoms that are easily tolerated and do not interfere with usual daily activity; Moderate (grade 2): discomfort that interferes with or limits usual daily activity; Severe (grade 3): disabling, with subsequent inability to perform usual daily activity, resulting in absence or required bed rest. Relatedness was assessed by the investigator, also on the bases of pre-defined criteria: Probable: An adverse event that follows a reasonable temporal sequence from the challenge procedure and cannot be reasonably explained by the known characteristics of the subject's clinical state; Possible: An adverse event for which insufficient information exists to exclude that the event is related to the study procedure; Not related: An event for which sufficient information exists to indicate that the aetiology is unrelated either because of the temporal sequence of events or because of the subject's clinical state or other therapies.'
Major comment 1 (cont): Secondly, they claim that these symptoms were associated with the induction of the immune responses that they describe in the BCG-vaccinated group, but no evidence to support this association is presented and this association might be coincidental, particularly given the small numbers in this study.
Authors' response: It is very unlikely that this increase in moderate/severe symptoms in the BCG vaccinated group is coincidental. Severe symptoms (requiring bedrest) occurred in 4/9 volunteers in the BCG vaccinated group, which is indeed remarkably high and substantially deviates from historical data. Across all combined CHMI studies at our center where treatment was initiated at 100 Pf/mL as in this study the incidence was 3/42 CHMI control volunteers (unpublished). The early and increased adverse events are present across the BCG vaccinated group. It is not possible to perform a proper statistical analysis to test association with inflammation considering the small number. However early symptoms (day 6, grade 1, 2 or 3) were seen in 4/4 BCG vaccinated volunteers with increased inflammation, and severe symptoms (grade 3) were seen in 3/4 BCG vaccinated volunteers with increased inflammation. This has been clarified in the abstract. Text added to the manuscript: 'BCG vaccinated volunteers reported earlier and more severe clinical symptoms and had heterologous, memory-like monocyte and (innate) lymphocyte re-activation that correlated with reduced parasitemia at 5 weeks post vaccination.'

Major comment 1 (cont):
Thirdly, the author suggest that both the enhanced symptoms and induced immunity are associated with reduced parasitaemia at 5 weeks post CHMI, but again there is absolutely no analysis presented to support this. I couldn't even find the PCR data at 5 weeks in the manuscript.
Authors' response: The statement in the abstract that BCG vaccination reduces parasitemia at 5 weeks post CHMI, is indeed an error and has been corrected. The sentence has been changed to: 'BCG vaccinated volunteers reported earlier and more severe clinical symptoms and had heterologous, memory-like monocyte and (innate) lymphocyte re-activation that correlated with reduced parasitemia at 5 weeks post vaccination.'

Major comment 1 (cont):
Overall, the findings are weak and add little to the field. The trial is so poorly described that it is hard to determine the importance of the findings in the context presented. If the paper were re-written to describe the study to the standard usually expected, the findings would still be too marginal to be of importance. Most of the immunology figures only show the data for the BCG group, although the text describes comparisons with the unvaccinated group. Both ought to be shown to allow the reader to assess the validity of the claims made.
Authors' response: We clearly disagree with the reviewer. Data from this study, small and exploratory as it is, provide already important findings with potential field impact: 1) BCG vaccinated volunteers with an altered immune response are distinct from both BCG non-responders and controls across a number of relevant parameters, and 2) there are already strong correlations between altered immune responses and parasitemia. In our opinion, these clear findings in already a small cohort form a firm basis for required further confirmation in larger study groups. The reviewer also notes that the immunology data should be shown for the control group as well. In figure 1D-F and Figure 2A-J data from the control group volunteers are shown as a box-plot, allowing direct comparison with the BCG vaccinated volunteers. We have clarified this in the legend of the figures.

Major comment 1 (cont):
The study is also largely unreproducible as reported, particularly as the primary endpoint is not described nor the method used to assess it. No information is given about the method for the primary endpoint of the trial (malaria qPCR) and whether the interpretation of PCR data was made by investigators blinded to the vaccination status of the volunteers. It's not stated how often or for how long PCR was performed. One assumes that PCR was performed in real-time, but again this is not described.
Authors' response: The qPCR was performed in real-time, once daily from day 6 after challenge until day 3 post antimalarial treatment, according to previously published protocols. This has been added to the methods section. Text added to the manuscript: 'qPCR was performed prospectively, once daily from day 6 after CHMI until day 3 after anti-malarial treatment, according to previously published protocols (Hermsen et al. Mol Biochem Parasitol 2001;Schats et al. PlosOne 2015;Walk et al. Malaria J 2015).'

Major comment 1 (cont):
There is no CONSORT checklist and the T cell methods do not meet the MIATA guidelines, particularly for the ICS itself where the method is minimally described despite ample space in the supplementary to do this properly. The BCG dose is not specified.
Authors' response: Many of the items on the CONSORT checklist (blinding, interim analysis etc.) are not applicable to this study. Furthermore, as this was an exploratory study to answer basic immunological questions, it was not possible to completely pre-define all secondary outcome measurements nor calculate a sample size for each secondary outcome prior to study start. Detailed method information is provided for each immunology assay including supplier for each reagent and antibody used. The culture medium for the T cell ICS assay has been added as well as the specifics of the flow cytometer. We present the gating strategy for a representative sample but feel that complete reporting of the T cell raw data (according to MIATA recommendations) will be overdone given the relative contribution of these data to the overall message of the paper.

Major comment 1 (cont):
The statistical analyses presented are appropriate, although often described in the text and not on the figure itself. Also, it would be useful to know where if a statistic is not given whether a test was performed and a non-significant result obtained and whether correction for multiple analyses were made. A Kaplan-Meier analysis should be performed for the qPCR data during follow-up.
Authors' response: Generally, we did not perform broad statistical analyses on each time point given the small study size. Therefore the outcome of the tests not always presented on the figures. We performed statistical analysis of the qPCR Kaplan-Meier curve (figure 1A) and added the p-value to the figure (non significant).

Reviewer #3 (Remarks to the Author):
This is a very interesting study about trained innate immunity in a malaria CHIM, and the authors make a fair case that this can exist. I am generally favorable to the report, although I think that there were some fundamental flaws in study design that cannot be corrected given the effort that is required for CHIM to be undertaken. First and foremost was the relatively short interval between BCG vaccine and challenge. The clinical observations surrounding trained innate immunity occur on a much longer time scale, so 5 weeks seems like a very short time interval between vaccine and challenge.
Authors' response: Designed as proof-of-concept study for potential innate effects, we deliberately choose for a relatively short interval between BCG and malaria i.e. before a person may have acquired adaptive immune responses through exposure. Previous studies with ex vivo cell restimulation have shown that the effect is detectable as from 2 weeks post vaccination. Studies on BCG vaccination in mice show effects on malaria infection at 1-2 months post vaccination. Based on this data we selected 5 weeks as a clinically relevant time point. However, we agree with the reviewer that follow-up studies should investigate its effects against malaria over a longer time window, as effects on innate immunity can persist up to one year after BCG vaccination (Kleijnijenhuis, PNAS, 2012).

Reviewer #3 (cont):
My second objection to the trial design was the very very short period when parasitemia was tolerated. As parasitemia was always sub patent, there was very little to suggest that at least one more day of clinical illness was dangerous to the volunteers. I realize, of course, that Sauerwein and colleagues were probably told by their institutional ethics panel how much clinical illness was acceptable, but this decision contributes to what appear to be significant but small effects that run through the manuscript.
Authors' response: As these studies are conducted in healthy volunteers, the ethical board, indeed, requires us to use very stringent safety criteria. As suggested by the reviewer, a follow-up that would include at least a slightly longer study period allowing to see potential effects on blood stage parasite replication, would be of great value. While we see already clear effects on pre-erythrocytic stages, we may consider in a next study to use the established malaria blood stage challenge model administrating a very small inoculum intravenously thereby allowing a number of parasite replication cycles before curative treatment is initiated.

Reviewer #3 (cont):
A third deficiency, and one that may actually be addressable even at this time point, is the lack of transcriptomic data as well as ChIP seq data. Such data, while expensive and (in the case of ChIP seq) labor intensive, would greatly increase the impact of the manuscript.
Authors' response: We recently published data on epigenetic changes after BCG showing genomewide changes in histone H3 acetylation at lysine 27 (H3K27ac) in monocytes one month after BCG vaccination (Arts et al. 2018 Cell Host and Microbe). Analysis of 646 differential peaks (baseline vs. 1 month after vaccination) showed changes in the regulation of several important signaling and inflammatory pathways. Moreover, differences were found in H3K27ac between BCG-responders and non-responders. Although the main message of this paper focuses on clinical parasitological effects, confirmation of these findings could indeed add value and benefit our present dataset. However, due to limitations in samples for analysis, we will be unable to draw tangible conclusions. In 3 BCG vaccinated volunteers representing 1 non-responder and 2 responders we found ≥2-fold changes in H3K27ac in 40 regions following vaccination, at least indicating that epigenetic changes do occur. Some of these regions overlap with the promoter/enhancer of several important genes in immune response, such as NCF2, IFIT5, MR1. However, further studies are obviously needed to specifically accommodate this valuable suggestion of the reviewer. Text added to the manuscript: 'A recent study examined the epigenetic and transcriptomic changes in monocytes of healthy volunteers vaccinated with BCG (Arts et al. Cell Host and Microbe 2018) , showing genome-wide changes in histone H3 acetylation at lysine 27 (H3K27ac) in 'responding' volunteers. Our study finds functional changes in NK cells as well, confirming previous in vitro observations (Kleinnijenhuis Clin Immunol 2014) . This may be the result of increased monocyte activation, as NK cell activity against malaria is partially dependent on monocytes (Artavanis-Tsakonas, J Immunol 2003). Whether BCG induces epigenetic changes in NK cells as well should be subject of a future study.' Minor comment: All of this being said, this is a piece of work that has importance. Some minor comments: 1) why do the authors believe that BCG vaccinate patients were more symptomatic? This seems like a fairly robust observation, but the numbers are small and the explanation is not obvious.