Before rotavirus vaccine introduction, rotavirus was a substantial cause of morbidity and mortality among children less than five years old, resulting in approximately 2 million hospitalizations and 352,000 to 592,000 deaths each year globally.¹ Countries began introducing rotavirus vaccines into their national immunization programs in 2006.² Currently, four rotavirus vaccines are prequalified by the World Health Organization: GlaxoSmithKline’s (GSK) Rotarix (RV1), Merck’s RotaTeq (RV5), the Serum Institute of India’s Rotasiil, and Bharat Biotech’s Rotavac. By the end of 2023, over 120 countries had introduced at least one of these vaccines into their national immunization schedules.³ Rotavirus vaccination has reduced morbidity and mortality among children less than five years old, with approximately 14,600 to 46,700 deaths in 2016 avoided by vaccination.⁴

The two vaccine formulations in use the longest — RV5 and RV1 — are considered safe and effective. Pre-licensure clinical trials in the early 2000s for RV5 and RV1 reported 98.0% (95% CI: 88.3–100%) and 95.8% (95% CI: 89.6–98.7%) efficacy, respectively, against severe RVGE.⁵ However, these trials were conducted predominantly in high-income countries with low child mortality. Additional trials in lower-income countries with higher child mortality revealed heterogeneity in rotavirus vaccine performance, with efficacy against severe RVGE ranging from 18% to 98% for RV5 and from 49% to 96% for RV1.^6–9 Moreover, rotavirus vaccine effects appeared consistently lower in countries with higher child mortality.^10–12

Individual-level factors that interfere with the immune response mounted after vaccination, like nutritional deficiencies, co-administered oral poliovirus vaccine, and transplacental antibody transfer,^13–16 may affect rotavirus vaccine efficacy (VE). Generally, children in high child mortality settings are more subject to immune-interfering factors than children in low child mortality settings, which has been proposed as one explanation for the observed trend of lower VE in higher child mortality settings.¹⁷ Therefore reducing the impact of interfering factors should mean VE from high child mortality settings becomes similar to VE observed in low child mortality settings.¹⁸ However, interventions like withholding breastfeeding or providing nutritional supplementation only modestly improve rotavirus vaccine immunogenicity,¹⁹ leaving a persistent heterogeneity in VE.

One explanation for the persistent heterogeneity may be differences in rotavirus exposure between infants in high and low child mortality settings. At a given point in time, the population-level infection prevalence affects an individual’s probability of being exposed to infection. Given that high child mortality settings usually have greater rotavirus prevalence than low child mortality settings,⁴ infants in high child mortality settings likely have more exposures to rotavirus in a given time period than their counterparts in low child mortality settings. Crucially, because VE is conceptually a reduction in susceptibility per infectious exposure for partially immunizing pathogens,²⁰ standard VE estimates will be confounded by the number of infectious exposures even in randomized controlled trials.²¹ The magnitude of bias therefore varies as a function of the population-level prevalence and, by extension, incidence.

The ideal solution is to record each infectious exposure for use in analysis; however, collecting such data accurately is difficult, if not impossible. We hypothesized that rotavirus VE is more similar between countries than comparisons of published estimates would suggest and that heterogeneity in infectious exposures might underlie part of the observed differences in vaccine performance. Using multi-country data from RV1 clinical trials, we evaluated the utility of different proxies for the magnitude of infectious exposure by comparing VE estimates adjusted for each proxy to crude, country-specific VE.

We pooled individual-level data from infants enrolled in eleven of GSK’s Phase II and III clinical trials of RV1 conducted between 2000 and 2012. We included randomized, double-blind, placebo-controlled trials that enrolled only healthy infants, had similar key inclusion/exclusion criteria, and used similar vaccine schedules, gastroenteritis (i.e., outcome) definitions, and stool sample collection timings (Supplemental Table 1). Five trials collected stool samples for all episodes of gastroenteritis (referred to as any-severity trials), one trial collected stool samples for episodes of gastroenteritis leading to medical intervention, and the remaining five trials collected stool samples for episodes of gastroenteritis resulting in oral rehydration therapy administration and/or hospitalization. One trial included multiple RV1 treatment arms with different 50% cell culture infectious dose (CCID₅₀) concentrations, but infants assigned to RV1 arms with CCID₅₀ <10^6.0 were excluded from analysis. Finally, for multi-country trials, trial data for each country were included if at least one episode of severe gastroenteritis (defined as a Vesikari score ≥11 in trial protocols)²² occurred in the placebo group.

Protocol-specified follow-up ranged from approximately one to two years after infants received the last study dose, so we restricted analysis to data collected during infants’ first year of life for consistency. We ultimately created two pooled datasets: one including data from all eleven trials and one including data only from the five any-severity trials. Data were deidentified and obfuscated by GSK before sharing. Emory University’s Institutional Review Board determined this study did not meet the definition of human subjects research requiring approval. Data management and analyses were conducted in R (version 4.0.3). Analysis code and dummy data are available at https://github.com/AAmin23/dissertation.

We included 83,592 infants from 23 countries and 11 RV1 trials in our RV1 VE analyses. 774 RVGE episodes occurred, of which 373 were severe. A quarter (n = 22,309) of infants resided in either Mexico or Peru and half (n = 40,955) were female. The median age at first study dose was 8 weeks (interquartile range (IQR): 6–11) and median duration of follow-up was 29 weeks (IQR: 4.4–33). 53% (n = 45,305) of infants received two RV1 doses. Most characteristics did not substantially differ between treatment groups, although infants who received RV1 had longer median follow-up time (29 weeks; IQR: 4.6–33) than infants who received a placebo (25 weeks; IQR: 4.3–33), likely due to higher RVGE incidence and therefore earlier censoring in the unvaccinated (Table 1).

Approximately 14% (n = 11,949) of infants in the entire pooled dataset were enrolled in any-severity trials in eight countries. 640 RVGE episodes occurred, of which 258 were severe. Nearly 79% (n = 9,399) of infants in any-severity trials resided in China, Finland, or South Africa and half (n = 5,808) were female. The median age at first study dose administration was 10 weeks (IQR: 7.0–12) and median duration of follow-up was 34 weeks (IQR: 30–38). 63% (n = 7,481) received two RV1 doses. No characteristics substantially differed between treatment groups (Table 2).

When compared to the standard VE estimation approach, adjustment for rate-based proxy metrics of infectious exposure reduced heterogeneity in country-specific rotavirus VE estimates. Country-specific estimates of RV1 VE against any-severity and severe RVGE varied substantially when we used the standard model. Consistent with previous findings, RV1 VE estimates against severe RVGE were generally higher than VE estimates against any-severity RVGE. These model structures also resulted in more precise VE estimates than those from the standard model, since treating the metrics as continuous variables required fewer degrees of freedom. The observed reduction in VE estimate heterogeneity when using RVGE rates, which should be a function of the unobserved exposures to rotavirus, is consistent with our hypothesis as to why VE estimates in different countries are less comparable when infectious exposures are not explicitly considered. However, our VE estimates apply to the first year of life only; heterogeneity in reported VE for the second year of life onward may be a function of both unobserved exposures to rotavirus and differential rates of waning immunity.

However, not all metrics decreased heterogeneity in RV1 VE estimates similarly. Age-based metrics modestly decreased heterogeneity in country-specific VE estimates, even though the average age of infection theoretically increases as infants experience fewer rotavirus exposures. The lack of decreased heterogeneity, the modest correlation between RVGE rates and median age at RVGE outcomes, and the similar or higher BICs compared to the standard model all support the idea that age-based metrics may not reflect the desired information about underlying rotavirus exposures. Because we limited trial data to the first year of life, the median age metric we calculated using trial data could not be higher than 52 weeks, which is likely not reflective of the true severe RVGE age distribution in a country. To examine a wider range of ages, we used external information for our median age at RVGE hospitalization metric. However, many countries in our dataset lacked a hospitalization age estimate in the review, so we assigned them the median age for their respective child mortality quintile.²³ Many countries therefore had the same median age of disease at RVGE hospitalization, which likely does not reflect the true variation in ages. Age of disease may still be a useful metric for rotavirus exposures given a sufficiently granular data source.

Incorporating valid proxies for infectious exposures may help address the underlying confounding due to differences in infectious exposures between countries,²¹ thus reducing apparent heterogeneity in vaccine effects. Adjusting for trial site or country may be intended to address known differences in disease burden; however, these variables are inherently categorical and do not address the underlying relationship between the magnitude of infectious exposure and subsequent bias of VE estimates. A better proxy for the relationship may be disease or infection rate, which is more directly tied to infectious exposures. Some of the increased precision in VE estimates when using rate-based proxies may be because they were continuous variables, which generally reduce loss of information and have better power compared to their categorical counterparts. Others have demonstrated improved estimate precision when using continuous variables instead of categorial variables.²⁶ We see a similar phenomenon when comparing the model using continuous severe RVGE rate to the model using quartiles of severe RVGE rate.

We assumed that our proxy metrics only reflected the unobserved magnitude of infectious exposures to rotavirus. However, these metrics may correlate with other country-level prevalence of factors that directly influence VE (e.g., higher RVGE rate in countries that still use oral poliovirus vaccine). Additionally, in higher-incidence settings, the rotavirus concentration may be higher per infectious exposure, which could also result in a lower true VE.^4,27 Our proxy metrics may inadvertently control the higher prevalence of factors thereby directly influencing VE in higher-incidence settings. Finally, some countries had relatively few episodes of RVGE in the placebo group, which limits the robustness of their calculated infectious exposure metrics.

Our work was subject to other limitations aside from our proxy metrics for infectious exposures. The multi-country trials were not powered for country-specific analyses, though VE estimates from proxy-adjusted models did not appear overly sensitive to sparse data. However, the lack of power highlights a methodologic challenge when estimating VE and its associated confidence intervals, which is most noticeable in estimation from the standard model. Since most data originated from trials with more serious RVGE as the endpoint of interest, we could not robustly examine any-severity RVGE rate as a proxy metric or evaluate VE estimates against any-severity RVGE. We also could not adjust for concomitant oral poliovirus vaccine administration, which is known to influence RV1 immunogenicity, due to strong collinearity with the country and proxy metrics.¹⁵ This limitation could explain the persistently low estimates in Malawi and South Africa, as their trial protocols were the only ones that also had protocol-specified concomitant oral poliovirus vaccine administration. Finally, we did not examine the impact of RVGE misclassification, which may also relate to observed heterogeneity in VE estimates.²⁸ Misclassification could explain why adjusting for the severe RVGE rate resulted in greater attenuation of VE heterogeneity than adjusting for the any-severity RVGE rate, as more infants with severe disease shed higher viral quantities, reducing the likelihood of diagnostic misclassification.²⁷

Overall, we demonstrate proof-of-concept for reducing the impact of unobserved infectious exposures when estimating VE from epidemiologically-different settings. Our country-specific estimates of RV1 VE against severe RVGE when controlling for the severe RVGE rate were generally within seven percentage points (78% to 85% VE) of each other. This range is substantially less than the heterogeneity of reported VE estimates in the literature but on the lower side of VE estimates from low child mortality countries.²⁹ Based on these findings, we argue that failure to account for infectious exposures to rotavirus may explain a substantial amount of the heterogeneity among country-specific estimates reported in the literature for RV1 VE. RV1 evaluations should try to address differences in the magnitude of infectious exposures, either with proxies of exposure or direct measurement of exposure when possible, to reduce artifacts from uncontrolled confounding. This principle may apply to RV5, imperfectly-immunizing vaccines for other pathogens, and observational studies.