Methods

Eligible studies of camostat were identified through www.clinicaltrials.gov. To be included, studies needed to be a RCT evaluating the efficacy of camostat in adults with acute SARS-CoV-2 as compared to the standard of care. The studies also needed to collect data on either viral or clinical endpoints to allow harmonization across studies in a meta-analysis. Ten studies were identified, and all were invited to participate. Out of these, six provided individual patient data for the meta-analysis: Stanford University (Stanford), Cancer Research UK (CRUK), Ghent University Hospital (UZ Ghent), National Institute of Health Sciences and Nutrition Salvador Zubiran (INCMNSZ), Aarhus University Hospital (Aarhus), and Assistance Publique–Hôpitaux de Paris (APHP). Table 2 describes each participating trial, including key inclusion/exclusion criteria, dose, and schedule of camostat administration, measurements collected, and sample size. Four eligible studies did not have individual patient data available for inclusion in this analysis. The individual patient data for one study became available only after the endpoint harmonization process described below [Reference Jilg, Chew and Giganti8]. The corresponding author from the other three studies were contacted and, while the authors initially responded, they ultimately did not share individual patient data with no reason provided [Reference Kinoshita, Shinoda and Nishizaki13, Reference Kim, Jeon and Kim14, Reference Chupp, Spichler-Moffarah and Søgaard22]. Results from all four studies have been reported. Due to the inconsistent endpoints collected across early studies of COVID-19, most endpoints reported in the publications cannot be combined with our endpoints in a traditional meta-analysis. However, one endpoint in Jilg. et al. aligned with our study endpoints and was incorporated in our analysis [Reference Jilg, Chew and Giganti8].

Table 2.

Summary of trials included in individual patient data meta-analysis

D = Day; NP = nasopharyngeal; V = Virtual visit.

When the investigators of the individual studies began collaborating, the first step was to compare protocols to assess feasibility of harmonizing key variables to pool individual patient data collected from the individual. After endpoint overlap across studies was assessed, we defined the objectives, endpoints, and methods appropriate to achieve our goals in a prespecified SAP (see Supplemental Materials) [Reference Berman and Parker23]. We modeled our design after the methods of Troxel et al. in following a Bayesian monitoring approach to avoid conflicts with the type I error control in the individual study designs, as several of the included studies had paused enrollment and could possibly continue to completion [Reference Troxel, Petkova and Goldfeld18].

Enrolled patients had been randomized into two arms: (1) the control arm, comprised of standard supportive care in addition to placebo in all trials except CRUK where the comparator was standard supportive care alone and (2) the treatment arm, comprised of camostat in addition to standard supportive care (see Table 2 for dosage). Randomization was performed in a 1:1 ratio camostat:control in all trials except UZ Ghent, which randomized in a 2:1 ratio. Randomization at Stanford was stratified by age and sex.

The individual studies were approved by the ethical review boards at their respective institutions. We used the Cochrane risk of bias tool for randomized trials to evaluate the risk of bias for each of the individual studies.

Statistical analyses

All analyses followed the intent-to-treat (ITT) principle and, as such, we grouped patients according to their randomized treatment and included all patients randomized by the time data were shared for analysis. All analyses were adjusted for age and sex, i.e. the randomization stratification variables used at Stanford.

All models were fit using a Bayesian framework, unless otherwise noted. As noted above, we followed a Bayesian monitoring approach to avoid conflicts with the type I error control in the individual study designs for the primary viral and primary clinical endpoints. The distributions and parameters in the model were refined during simulations prior to unblinding. After fitting the models, we evaluated our findings’ robustness to the choice of prior distributions, e.g. we centered the distribution of the beta coefficient at a nonzero value. For example, our primary analyses relied on uninformative priors, where the prior distribution for our parameter of interest is centered at 0. In sensitivity analyses, the center of the prior distribution for our parameter of interest would be nonzero.

To evaluate the harmonized viral endpoint, we derived the rate of change in the viral load over Days 1–5 by fitting a linear regression to each patient’s Day 1–5 data. Rate of change was compared between the two arms using a linear mixed effects model with a random intercept and random slope for trial to account for correlation between observations from the same trial and heterogeneity of effects across trials.

Odds of testing positive on Day 7 and Day 14 were evaluated by treatment arm using a generalized linear mixed-effects model with a random effect for trial, fit using frequentist methods. A separate model was fit to estimate odds ratios comparing camostat to placebo for Day 7 and for Day 14 because different studies had data available for each time point. Jilg et al. reported the number of participants testing positive on both Day 7 and Day 14 by arm in their Figure 2. We included these participants in a post hoc sensitivity analysis [Reference Jilg, Chew and Giganti8].

Figure 2.

Forest plot displaying estimates and credible intervals by trial for the harmonized viral endpoint (Panel a) and the harmonized clinical endpoint of time to symptom resolution (Panel b).

To evaluate the harmonized clinical endpoints, time until symptom resolution was compared between treatment arms using a two-parameter frailty proportional hazards model to account for within-trial correlation. The hazard ratio for time to clinical improvement was estimated from a Weibull model with Gamma frailties.

In secondary analyses, we used a Cox proportional hazards model, fit using frequentist methods and stratified by trial to compare the time to the first of hospitalization, supplemental oxygen use, and death. The proportional hazards assumption was visually assessed. Patients who did not experience the composite endpoint were right-censored at the end of the patient’s follow-up or Day 28, whichever was earlier. We performed the hospitalization efficacy analysis in (1) all trials collecting data on hospitalization and supplemental oxygen and (2) the subset of patients from the INCMNSZ and APHP trials.

The model parameterizations and additional details are provided in the SAP (Supplemental Materials). Estimates obtained using Bayesian methods are presented with 95% credible intervals. When fitting frequentist models, we performed two-sided tests with alpha =0.05 and present 95% confidence intervals. All analyses were conducted in R version 4.2.1 [25]. We used the “rstanarm” package to fit the Bayesian models in R.

Results

431 patients were included in at least one individual patient-level data meta-analysis. The number enrolled in individual trials ranged from 34 to 114. Viral endpoints through Day 5 were derived from 118 patients at UZ Ghent and Stanford; 75 patients from Stanford and APHP contributed viral data at Day 7; 74 patients from Stanford, INCMNSZ, and APHP had viral data available at Day 14; and 240 patients contributed symptom or other clinical data from Stanford, CRUK, UZ Ghent, INCMNSZ, and Aarhus. In a sensitivity analysis, we additionally included 178 patients for whom we were able to extract the secondary viral endpoint of testing positive at Day 7 and 14 from Figure 2a of Jilg et al. [Reference Jilg, Chew and Giganti8].

The mean age of participants in the IPDMA studies ranged from 39 to 56 years with a minimum age of 18 and a maximum of 84. Most studies had slightly more females with a range of 37–62% female by study (Table 3). We assessed the risk of bias in the individual studies to be low using the Cochrane risk of bias tool for randomized trials.

Table 3.

Baseline characteristics of all patients overall and by trial

Discussion

This study is the most comprehensive evaluation of the effectiveness of camostat to treat COVID-19 to date. Treatment with camostat in these studies, primarily in outpatient settings, showed no difference in decline in viral shedding and no improvement in symptoms as compared to standard supportive care in patients with mild COVID-19. While there was some heterogeneity in patient populations and how the drug was administered across the trials, little heterogeneity was observed in results prior to pooling.

At the onset of the COVID-19 pandemic, numerous clinical trials were swiftly initiated, mainly targeting hospitalized patients with severe illness. However, the majority of COVID-19 patients are diagnosed and treated in outpatient settings, where there is a significant demand for treatments that can be administered conveniently to prevent worsening of the condition. The search for effective preventive and therapeutic treatments against COVID-19 in outpatient clinical trials is challenging with regard to constructional and organizational issues as well as within constantly shifting landscapes from changing virus variants to rise and fall in incidence [Reference Grenier, Loniewski and Plazy26]. Recruitment slowed in the present individual studies in parallel with the roll-out of the COVID-19 vaccination campaign along with the introduction of monoclonal antibodies and other therapeutics that perturbed equipoise and made placebo control ethically unacceptable.

At the same time the SAP was being developed, a MOU was being drafted between the institutions conducting the participating studies and Ono, the sponsor and supplier of camostat for some participating studies. The effort required to gain consensus across institutions on the MoU, including the data sharing agreement adhering to the requirements of the GDPR covering the trial data collected in the European Union, was by far the most-challenging and time-consuming step of the process in this IPDMA.

The lack of efficacy of camostat on SARS-CoV-2 viral load in the present meta-analysis is in agreement with the findings in previously published RCTs where swab specimens from the nasopharynx or oropharynx were taken [Reference Jilg, Chew and Giganti8, Reference Gunst, Staerke and Pahus11–Reference Kim, Jeon and Kim14]. Regarding the role of TMPRSS2 in viral entry into the cells, it might be thought that the inhibitory effect of camostat may especially be effective in the early phase of COVID-19. SARS-CoV-2 RNA levels peak around symptom onset and then gradually decline, supporting that administration of camostat might best be started as early as possible in the course of infection [Reference Puhach, Meyer and Eckerle27]. In the present study, patients’ treatment was started within 5–7 days after symptom onset and the optimal time point for therapeutic intervention might have been exceeded. However, data from Kinoshita et al. and UZ Ghent did not show significant reductions in viral load when treatment was started at 3 days median time of symptom onset (interquartile range 0–5 and 1–4, respectively) [Reference Tobback, Degroote and Buysse12, Reference Kinoshita, Shinoda and Nishizaki13]. In conclusion, SARS-CoV-2 viral load reduction by camostat is unlikely to be effective, even when treatment is started as early as possible in clinical practice. These results do not, however,exclude potential effects of this drug if administered as a prophylactic, for instance to close contacts of patients.

There was insufficient evidence to conclude camostat affected the time to subjective symptom resolution or the time to hospitalization in the present meta-analysis, which is in agreement with all previous studies evaluating main COVID-19 symptoms [Reference Jilg, Chew and Giganti8, Reference Tobback, Degroote and Buysse12–Reference Kim, Jeon and Kim14]. In contrast, therapeutic benefits in terms of clinical endpoints have been described by Sakr et al. and Karolyi et al. [Reference Sakr, Bensasi and Taha9, Reference Karolyi, Pawelka and Omid10]. These studies included moderate to severely ill patients hospitalized with COVID-19 pneumonia and concomitant therapies may also have had confounding effects on their outcomes. Taken together, camostat is unlikely to be an effective treatment for symptoms in COVID-19 outpatients.

This study has numerous strengths, including its sample size, patient level data, and diversity in population as a result of participation by six trials across six different countries. The analysis highlights how a pooled analysis can be used in circumstances where equipoise may be lost and/or other extenuating circumstances can halt the progress of a clinical trial, threatening its ability to yield informative results. Unlike meta-analyses performed on published results, our meta-analysis is unlikely to be subject to the publication bias encountered with traditional meta-analyses, because we did not identify participating studies by searching published studies. Identified studies that were not included in the IPDMA all similarly concluded that camostat is not an effective treatment of COVID-19 in this patient population. Limitations of our study include the heterogeneous study designs resulting in different doses administered, inconsistent measurement schedules across trials, differing ascertainment of outcomes, and varying amounts of data available to contribute to the findings. This heterogeneity likely biases the estimates towards the null. Not all studies made their safety data available, and we observed heterogeneity in reporting safety data for the reporting studies, a common problem in clinical trials [Reference Schroll, Maund and Gøtzsche28]. The heterogeneity of study conduct is particularly apparent in the collection of AEs across trials. As in all meta-analyses, the interpretation of the results is limited by data from eligible trials that are unavailable at the time of the analysis. While the eligible trials that were not included in this individual patient-data meta-analysis were all published, a traditional meta-analysis was not conducted in addition to the IPDMA because the endpoints collected and reported across studies differed widely.

In the future, strong consideration should be given to the idea of multiple centers joining forces to design one multi-center study of the efficacy of a given compound. This is particularly important in a pandemic, where the difficulties of initiating such studies are great, and the landscape is fast-moving and unpredictable. A multi-center study designed in collaboration at the start could very well have resulted in arriving at these findings much earlier. Furthermore, the authors here advocate for other similar efficiencies of trial design including platform or master protocols where multiple drugs can be studied simultaneously. At Stanford University, the camostat agent was indeed being studied as one of the sub-protocols in a platform protocol for this purpose [Reference Bunning, Hedlin and Purington21]. Conducting a clinical trial requires a great deal of resources to establish its infrastructure. We believe it is critical for academic and research institutions to pool resources to study multiple agents simultaneously, and that for any given agent, that it be studied in a multi-center framework. Not only will this yield huge gains in efficiency allowing us to address our questions faster and with fewer resources, but it will also allow us to achieve a higher generalizability of findings.

In summary, our team joined together in a creative manner to salvage much effort that was invested in the launching of our respective trials so that we could draw conclusions with strength. We did so in the middle of a pandemic and applied novel principles to design an overarching study that enabled our respective initial study designs to continue if needed. While harmonization of outcomes was key to the pooled analysis, we did not harmonize on triggering rules. Each trial had the flexibility to develop their own stopping rules to inform next steps. In addition, we considered both virologic and clinical endpoints. Such flexibility was critical for enabling participation by as many trials as possible. Our biggest challenge was gaining consensus in data sharing agreements that worked across our international regulatory bodies. With increased experience in collaborating on global clinical trials, we believe these challenges to inefficiencies can and should be learned and overcome.