The Choice of Viral Load End Point in Early Phase Trials of COVID-19 Treatments Aiming to Reduce 28-Day Hospitalization and/or Death

Abstract

Background

Virologic end points are used in phase 2 trials for COVID-19 therapeutics, but they have not been established as surrogates for clinical end points. No meta-analysis using individual participant data (IPD) has been undertaken to identify viral load outcomes for which treatment effects are best associated with effects on hospitalization/death.

Methods

This meta-analysis combined IPD from 23 COVID-19 treatment versus control comparisons to calculate R², a surrogacy measure quantifying the relationship between the treatment effect on 28-day hospitalization/death and the treatment effect on the surrogate. R² ranges from 0 to 1, with a strong relationship ≥ 0.72, moderate 0.49 < R² < 0.72, and weak ≤ 0.49. We estimated R² for various viral load outcomes at days 3, 5, and 7, including change-from-baseline, slope, average area under the curve minus baseline (AAUCMB), and a change of at least 0.5 log₁₀ copies/mL from baseline to day 3.

Results

R ² was numerically highest for the change-from-baseline to day 3 (0.53; 95% confidence interval [CI], .26–.79), slightly lower for change-from-baseline to day 5 (0.49; 95% CI, .24–.75) and numerically lower for change-from-baseline to day 7 (0.40; 95% CI, .15–.65). All were statistically significant.

Discussion

Our study is the first to use IPD, allowing us to evaluate viral load collected on various study days as a surrogate to clinical outcomes. Change in log₁₀(viral load) from baseline to day 3 or day 5 are moderate surrogates for 28-day hospitalization/death and suitable primary end points in phase 2 clinical trials and are preferred over change-from-baseline to day 7. Slope and AAUCMB require more calculation but did not improve prediction so are not recommended.

This meta-analysis uses individual participant data to evaluate various SARS-CoV-2 viral load outcomes as surrogates for 28-day hospitalization/death. Change in log₁₀(viral load) from baseline to day 3 or 5 are moderate surrogates and suitable primary end points in phase 2 trials.

Many phase 2 trials of coronavirus disease 2019 (COVID-19) treatments aiming to reduce hospitalization/death use virologic end points. Virologic end points are not recommended as primary end points for phase 3 trials because they are not established surrogates for a measure of how a patient feels, functions, or survives, and the best timing, sampling methods, and measurement methods have not been established. For example, the phase 2 BLAZE-1 trial comparing bamlanivimab and bamlanivimab plus etesevimab to placebo specified the primary end point as change in viral load from baseline to day 11 [1]. Post hoc analysis suggested that day 7 might better predict clinical outcomes, so a subsequent phase 3 trial of bamlanivimab plus etesevimab versus placebo included a secondary outcome of change in viral load from baseline to day 7 [2]. The trial found bamlanivimab plus etesevimab reduced viral load from baseline to day 7 and reduced hospitalizations/deaths. In contrast, the PINETREE trial found that early remdesivir reduced hospitalization/death compared to placebo but did not affect change in viral load from baseline to day 7 [3]. ACTIV-2 found that the proportion of treatment effect (hospitalizations/deaths after day 3) explained by day 3 log₁₀(anterior nasal RNA) was only 0.08 [4].

Meta-analyses using aggregated data have started to elucidate the relationship between clinical outcomes and severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2) viral load. One meta-analysis of 17 trials testing COVID-19 treatments for outpatients found a medium correlation between the treatment effect on 28-day hospitalization/death and the treatment effect on change in log₁₀(viral load) from baseline to day 5–7 (R² = 0.53) [5]. An updated meta-analysis by the same authors including 5 additional trials demonstrated a higher but still moderate correlation (R² = 0.63) [6]. A separate meta-analysis of 22 clinical trials analyzed the relationship between the treatment effect on hospitalization/death and 3 log₁₀(viral load) outcomes: change-from-baseline to days 3, 5, and 7. The association was strongest for days 3 and 5 and weaker for day 7 [7]. A third meta-analysis of 32 trials estimated the relationship between the treatment effect on 14-day hospitalization/death and the multiplicative treatment effect on the slope of log₁₀(viral load) from days 1–8; R² was 0.097 but was 0.504 excluding an outlier trial, PANORAMIC [8, 9]. Various time points and transformations of viral load have not been systematically investigated in detail, and no study has yet analyzed individual participant data (IPD).

To fill this gap, this study analyzes IPD from 23 COVID-19 treatment versus control comparisons to explore the utility of viral load end points in early phase trials of treatments aiming to reduce 28-day hospitalization/death. IPD is the gold standard of meta-analysis as it allows standardization of data, outcomes, and analyses across studies [10]. IPD allows calculation of change in log₁₀(viral load) from baseline to any study day for all trials. We analyze the relationship between the treatment effect on the clinical outcome and effects on various viral load outcomes at days 3, 5, and 7, including change-from-baseline, slope, average area under the curve minus baseline (AAUCMB), and a reduction of > 0.5 log₁₀ copies/mL from baseline to day 3.

METHODS

To select trials for inclusion, we searched PubMed on 8 December 2022 using the phrase “blinded randomized controlled trial AND clinicaltrials.gov AND viral AND LitCTREATMENT[filter],” which returned 220 publications. We retained phase 2 or 3 trials with virologic data and > 150 participants. We then excluded convalescent plasma, prevention trials, and trials of hospitalized participants, which left 7 trials. We also considered all trials in Parienti and de Grooth [5] and 4 large trials that had not yet published results: TOGETHER, ACTIV-2, COVID-OUT, and TACKLE. Supplementary File 1 provides details of trials screened, including reasons where IPD could not be obtained. Supplementary File 2 describes data cleaning procedures. SARS-CoV-2 RNA viral load measurement methods are described in the Supplementary Material. Statistical methodology was prespecified in the Statistical Analysis Plan, which was finalized before performing the analyses (see Supplementary Material).

The following viral load variables were analyzed as potential surrogates: change in log₁₀(viral load) from baseline to day 3, day 5, and day 7; slope of log₁₀(viral load) trajectory from day 1–5 and day 1–7; AAUCMB from day 1–5 (calculated as AUC/[5–1] − baseline) and day 1–7 (calculated as AUC/[7–1] − baseline); and viral load reduction of > 0.5 log₁₀ copies/mL from baseline to day 3. Baseline (day 1) was defined as enrollment. While our primary clinical outcome was 28-day hospitalization/death, a secondary clinical outcome also included 28-day emergency room (ER) visits. Treatment versus control comparisons with < 2 events in the control arm were excluded.

The trials had different viral load sampling schemes and visit windows (Supplementary Table 1), causing high missingness. Supplementary Table 2 shows viral load nonmissingness by study day and trial. On days 3, 5, and 7, overall missingness was 64%, 64%, and 71%, respectively. Supplementary Table 3 shows completeness of viral load data for planned sampling days; only 12% was missing not by design. A longitudinal model was created to model viral load based on time from symptom onset, including individual intercepts, covariates, and separate smoothing curves for each trial and arm. The smoothing curves incorporate information from viral load measurements on days close to the time points of interest to estimate viral load outcomes on days 3, 5, and 7 for all participants. Technical details are in the Supplementary Material. The model had very low bias and no trend by treatment or day (Supplementary Figure 1). Before model fitting, values below the lower limit of quantification (LLOQ) were imputed to LLOQ/2, with sensitivity analyses imputing to LLOQ/4 and LLOQ/8. Treatment effects on the clinical outcome were estimated using Firth logistic regression [11].

A widely accepted method to evaluate a surrogate is meta-analysis quantifying the relationship between the treatment effects on a surrogate and the treatment effects on the clinical outcome with the coefficient of determination (R²) [12]. Because we analyzed a binary outcome and both binary and numeric surrogates, we applied the information-theoretic R², which can be thought of as a generalization of R² when one or both outcomes are not numeric and is equivalent to the standard R² when the surrogate and clinical outcomes are normally distributed [13]. See Supplementary Material for further details. A nonparametric bootstrap was used to estimate uncertainty. Surrogate threshold effects (STE) were determined by the intersection of the upper limit of the 95% prediction interval from a linear regression model for the association of treatment effects on the clinical outcome (log odds ratio [OR]) with treatment effects on the viral load outcome and 0, the null value of the clinical outcome [14]. The STE shows the minimum value of the treatment effect on the viral load outcome to predict a nonzero clinical effect.

Analyses were performed on a modified intention-to-treat (mITT) population including randomized participants who received at least some study drug/placebo, contributed at least 1 postbaseline viral load measurement, and had baseline viral load > LLOQ. From this population, 3% missing baseline viral load were excluded (Supplementary Table 4). TOGETHER-Metformin was excluded due to an expression of concern [15, 16]. Some treatment groups share concurrent control groups. Each treatment was compared to the subset of participants who received the control for that treatment (Supplementary File 2).

Two subgroup analyses were performed. One included participants enrolled within 3 days of symptom onset, as the relationship between the treatment effect on the clinical outcome and that on viral load may be stronger when enrollment is close to symptom start. The other excluded data from comparisons stopped early for efficacy or futility based on an unblinded interim data analysis (ACTIV-2 SAB-185 low-dose phase 3, COVID-OUT-Fluvoxamine, and COMET-ICE) as interim treatment effect estimates are subject to bias [17]. Analyses were performed in R version 4.3.2.

RESULTS

Participant Characteristics

We received IPD from 36 unique treatment versus control comparisons nested within 9 trials (Supplementary File 2 describes handling of shared controls). Trial information is in Table 1 with timelines in Figure 1. Supplementary Table 4 summarizes mITT exclusion counts by trial. Supplementary File 3 summarizes baseline characteristics by treatment and trial. Supplementary File 4 summarizes numbers and proportions of participants experiencing the primary and secondary clinical outcomes by treatment and trial and dropout numbers.

Table 1.

Description of Trials Included in Meta-analysis

Trial Name	General Description	Location(s)	Number of Sites	Participants in mITT Population
ACTIV-2 [18]	Randomized controlled platform trial testing 12 agents compared to their own control groups in both phase 2 and phase 3 trials	United States, Argentina, Brazil, Guatemala, Mexico, the Philippines, and South Africa	173	1882
TOGETHER [15, 16, 19–21]	Randomized controlled platform trial with 4 treatments compared to their own placebo groups	Brazil	13	1686
PINETREE [3]	Phase 3 randomized controlled trial of remdesivir versus placebo	United States, Spain, Denmark, and the United Kingdom	64	384
BLAZE-1 phase 2 [1, 2, 22]	Phase 2 randomized controlled trial, comparing multiple treatments to the same placebo group	United States	41	533
BLAZE-1 phase 3 [2, 22]	Phase 2/3 randomized controlled trial with 3 agents compared to their own placebo groups	United States	41	1939
BLAZE-4	Phase 2 randomized controlled trial comparing bamlanivimab alone, bamlanivimab + etesevimab, bamlanivimab + VIR-7831, bebtelovimab alone, and bebtelovimab + bamlanivimab + etesevimab to placebo 3 distinct trials were considered, of which 2 compared multiple treatments to the same placebo group	United States	93	1167
COVID-OUT [23]	Phase 3 randomized controlled trial of metformin, ivermectin and/or fluvoxamine, using a 2 × 3 factorial design The first factor was metformin versus placebo, and the second was ivermectin versus fluvoxamine versus placebo We included a subset of participants from the placebo only, metformin only, ivermectin only, and fluvoxamine only allocations in our meta-analysisa	United States	6	412
COMET-ICE [24]	Phase 3 randomized controlled trial of sotrovimab versus placebo	United States, Canada, Brazil, Spain, and Peru	57	666
BCN-PEP [25]	Phase 3 open-label randomized controlled trial of hydroxychloroquine versus placebo	Spain	3	268

Abbreviation: mITT, modified intention-to-treat.

^aRefer to Supplementary File 2 for more details.

Figure 1.

Timelines of trials included in meta-analysis. Dark bars indicate periods of enrollment, while light bars show the period of follow-up after the last enrollment. BLAZE-1 phase 3 and BLAZE-4 consist of 3 and 8 treatment versus control comparisons, respectively, in the meta-analysis but are only shown once here due to deidentification of the dates.

Time trends of viral load were visualized by trial and treatment (Supplementary Figures 2–4). These were sorted by treatment effect on the clinical outcome and support the prespecified end points as plausible surrogates and did not reveal a threshold/alternative end point.

Primary Outcome

Figure 2 visualizes the relationship between the treatment effect on the 3 change-from-baseline log₁₀(viral load) outcomes and the treatment effect on the clinical outcome. There were 7212 participants in the primary analysis from 23 treatment versus control comparisons, after excluding 13 comparisons with < 2 events in the control arm. Supplementary Table 5 summarizes our population in each analysis. Among the 3 change-from-baseline outcomes, R² was highest for the change-from-baseline to day 3 (0.53; 95% confidence interval [CI], .26–.79), slightly lower for change-from-baseline to day 5 (0.49; 95% CI, .24–.75), and numerically lower for change-from-baseline to day 7 (0.40; 95% CI, .15–.65), although all were statistically significantly greater than zero. The numeric values corresponding to this figure are in Supplementary Tables 6–10. While R² is the standard surrogacy measure, we also report the exponentiated slopes from the linear regression models used to estimate R² for these 3 change-from-baseline outcomes (Supplementary Table 11) to facilitate comparison to Elias et al [7]. These models regress the log(OR) (treatment effects on the clinical outcome) on the treatment effects on the viral load outcome plus trial-specific intercepts (Supplementary Material, Statistical Methods). Thus, the exponentiated slopes represent multiplicative effects of the viral load treatment effect on the clinical outcome effect. The STE for change-from-baseline to day 3 was 0.62, meaning that a change in viral load by day 3 must be > 0.62 log₁₀ copies/mL relative to control to predict a nonzero clinical effect on 28-day hospitalization/death. The STEs for change-from-baseline to day 5 and day 7 were higher, 0.92 and 1.02, respectively. STEs are shown in Supplementary Figure 5.

Figure 2.

Treatment effect estimates on change-from-baseline log₁₀(viral load) outcomes (x-axis) and primary clinical outcome of 28-day hospitalization/death (y-axis) with 95% confidence intervals.

R ² for AAUCMB day 5 was similar to change-from-baseline to day 3 (0.52 and 0.53, respectively), and R² for AAUCMB day 7 was similar to change-from-baseline to day 5 (0.49, both) (Supplementary Table 6). Other prespecified viral load end points included the viral load slope from days 1–5 and 1–7, and the viral load reduction of > 0.5 log₁₀ copies/mL from baseline to day 3. R² for log₁₀(viral load) slope from days 1–5 and 1–7 are equivalent to change-from-baseline for days 5 and 7 because this is equivalent to rescaling the x-axis, which does not affect the residuals. Of the participants, 98% experienced a reduction in viral load of > 0.5 log₁₀ copies/mL from baseline to day 3, so this viral load end point was not evaluated as a useful surrogate as there were no meaningful differences between treatment groups. Therefore, sensitivity, subgroup, and secondary analyses were performed only for the change-from-baseline end points.

Sensitivity and Subgroup Analysis

R ² for sensitivity analyses imputing values below LLOQ to LLOQ/4 and LLOQ/8 did not substantially change our results (Supplementary Tables 12 and 13). The subgroup analysis for participants enrolled within 3 days of symptom onset included 3673 participants, about half the primary analysis. R² values were lower (0.11, 0.18, and 0.22 for change-from-baseline to days 3, 5, and 7, respectively) and not statistically significant. We conjectured this was due to the substantially reduced sample size, which leads to more noise in both treatment effects (Supplementary Table 14). To evaluate this conjecture, we performed a post hoc analysis using the complement subgroup, those enrolled more than 3 days after symptom onset, which included 3539 participants. R² results were similar to the original subgroup (0.05, 0.22, and 0.21 for change-from-baseline to days 3, 5, and 7, respectively) (Supplementary Table 15). This lends justification that lower R² results in the original subgroup are due to a smaller sample size; if the R² results in the original subgroup represented weaker true correlations, we would expect R² results from the complement subgroup to be similar to or larger than the full analysis. Our subgroup analysis excluding comparisons that stopped early for efficacy or futility based on unblinded interim data analysis included 6103 participants. The R² value for change-from-baseline to day 3 was 0.56, slightly higher than the primary estimate (0.53), while the others were close to the primary results (Supplementary Table 16). Figure 3 displays R² estimates for the primary analysis, the sensitivity analyses, and 2 subgroup analyses.

Figure 3.

R ² estimates with 95% confidence interval for change-from-baseline viral load end points (day 3, 5, 7) for the primary model, sensitivity analyses for imputation procedure for values < lower limit of quantification (LLOQ), and 2 subgroup analyses. A black line is shown at the null value of 0.

Secondary Outcome

A secondary clinical outcome included ER visits within 28 days, as well as hospitalization/death. There were 8278 participants from 32 treatment versus control comparisons in this secondary analysis, after excluding 4 comparisons due to low event rates. Despite the larger sample size and event rates, R² values were lower (0.37, 0.38, and 0.37 for change-from-baseline to days 3, 5, and 7, respectively) than for the primary analysis but still statistically significant (Supplementary Table 17).

DISCUSSION

We found change-from-baseline to day 3 or 5 in log₁₀(viral load) could be considered phase 2 surrogate measures for 28-day hospitalization/death. The guidelines for the correlation coefficient created by the German Institute for Quality and Efficiency in Health Care [26] define surrogates as strong when R² ≥ 0.72, moderate when 0.49 < R² < 0.72, and weak when R² ≤ 0.49. These guidelines have been applied previously in surrogacy meta-analyses [27, 28]. In our analysis, change-from-baseline to day 3 and 5 in log₁₀(viral load) are moderate surrogates and thus would not be considered clinically validated to be used instead of hospitalization/death in a phase 3 clinical trial, but could be used as primary end points in a phase 2 trial. Change-from-baseline to day 7 in log₁₀(viral load) has a weak R² and shows lack of validity as a surrogate. Change-from-baseline to day 3 was the most predictive of all viral load outcomes analyzed. The predictive power was similar for change-from-baseline to day 5, but lower for day 7. This trend is consistent with Elias et al [7], although they used a different statistical summary—the exponentiated slopes from their regression model. In our analysis, the exponentiated slopes from the regression model are similar for days 5 and 7 (Supplementary Table 10), although day 7 values are more scattered from the regression line, leading to lower R². We report the exponentiated slopes for comparison to Elias et al [7], but in our view, R² better quantifies how well the surrogate can predict a treatment effect for a new trial: a viral load surrogate with steeper slope but with scatter above and below the line predicts the treatment effect of a new trial worse than one with a less steep slope with all points exactly on the line. Our day 3 and 5 values (R² = 0.53 and 0.49) are consistent with those in Parienti and de Grooth [5] (0.53 for change-from-baseline to day 5–7) and Singh et al [8] (0.504, after excluding an outlier), but our day 7 value is lower (0.40). Our values are lower than the estimate for day 5–7 in [6] (0.63). Our STE for our best surrogate (change in log₁₀(viral load) from baseline to day 3) was higher than those reported in Parienti and de Grooth and de Grooth and Parienti [5, 6] (0.62 compared to 0.41 and 0.42). Our R² for AAUCMB day 5 was similar to change-from-baseline to day 3, and R² for AAUCMB day 7 was similar to change-from-baseline to day 5, possibly because AAUCMB incorporates values at earlier time points. Because the change-from-baseline end points require less data and computation and are easier to interpret, we recommend them over AAUCMB end points with similar performance.

Our findings were robust to different LLOQ imputations and to inclusion/exclusion of comparisons that stopped early. A subgroup analysis of people enrolling within 3 days of symptom onset did not find significant R² values, probably because this restriction cut the sample size approximately in half. Our analysis found viral load outcomes to be less predictive of the secondary clinical outcome of 28-day hospitalization/death/ER visit, even with a larger sample size and event rate. This may be because ER visits that do not result in a hospitalization are less severe, with lower viral loads.

Previous meta-analyses by Parienti and de Grooth, Elias et al, and Singh et al included aggregated trial data, whereas our study uses IPD [5–8]. This allowed for calculation of change in log₁₀(viral load) from baseline to any study day for all trials, instead of being limited to studies that had planned viral load end points on a certain day. Using IPD has several advantages over trial-level summaries or aggregated data that we were able to employ. IPD allows standardization of data, outcomes, and analyses across studies, and may include additional participants and/or a longer follow-up time than published results [10]. While using IPD in meta-analysis is more resource and time intensive, it allows for published aggregated data to be verified, improving data quality. IPD meta-analyses can include unpublished results, such as ACTIV-2 and BLAZE-4 in our results [29, 30]. With IPD, meta-analytic approaches can be applied within subgroups (as demonstrated), while aggregated data may not have enough power to detect those differences in treatment effect or may not be available [10, 31]. Multiple individual predictors can be used together in analysis, and IPD can make complex statistical modeling possible. Our longitudinal model for log₁₀(viral load) included random intercepts, individual-level covariates, which could be time-varying, and separate smoothing curves for each trial and arm. IPD allows us to account for within-subject correlation in longitudinal data [32], as seen in our model with random intercepts. Missing data on an individual level can be assessed and handled in the same way across all trials; in our analysis, we were able to handle values < LLOQ consistently and infer missing viral load values. Together, this supports the current view that IPD is the gold standard of meta-analysis and provides our study with a clear advantage over previous COVID-19 meta-analyses [33 ]. Future pandemic preparedness should include ways to access IPD from clinical trials with relevant clinical outcomes and potential surrogate measures [34].

One limitation of our meta-analysis was the amount of missing data on exact study days used for viral load end points (Supplementary Table 2). Most data on these study days had to be inferred from our longitudinal model. However, missingness for a given day is greatly reduced when 2 adjacent days are considered. For example, 36% of participants had nonmissing viral load for day 3, but 82% had nonmissing viral load on day 2, 3, or 4. Additionally, most data were missing not by design (Supplementary Table 3). Because our model included arm-specific smoothing curves, prespecified individual covariates, and individual random intercepts, it likely does a reasonable job of inferring missing values. Another limitation is the time frame of our trials, which limits generalizability of our results. We included trials with enrollment spanning early 2020 through early 2022, with the majority covering the ancestral, Alpha, and Delta strains of SARS-CoV-2. We have limited data from the Omicron wave. Vaccination rates in our trials were lower than the current population as some studies were conducted before widespread vaccine availability. For example, participants in the PANORAMIC trial, which was not included in our meta-analysis, were mostly vaccinated and infected with the Omicron strain [9]. PANORAMIC was highly influential in [8] as excluding it changed R² from 0.097 to 0.504; other trials included in this analysis and Elias et al [7] included primary unvaccinated participants from the Delta and pre-Delta pandemic waves [7, 8]. As immunity builds in a population, we expect lower viral levels on average, which could erode the predictive power of viral load as a surrogate that was established under conditions of less immunity. A contemporary trial using a primary end point of hospitalization/death could require a large sample size due to event rates that would likely be lower than in trials included in our meta-analysis. A third limitation is that our meta-analysis, like others before it, included a relatively small number of trials. Fourth, our IPD meta-analysis could only include studies for which IPD was available. We were not able to obtain IPD from some studies included in other meta-analyses, such as MOVe-OUT/HETERO (molnupiravir), EPIC-HR/EPIC-SR (Paxlovid), and REGEN/REGEN2400/REGEN1200 (casirivimab/imdevimab) [5–8]. Finally, viral load was measured using different assays in different trials, which have different LLOQs, but we believe that each assay's LLOQ represents a lower limit below which values are clinically unimportant.

This IPD meta-analysis evaluated various viral load outcomes at days 3, 5, and 7 as possible surrogates for 28-day hospitalization/death. IPD allowed us to evaluate viral load surrogate measures on any individual day. Change in log₁₀(viral load) from baseline to day 3 or 5 perform better as surrogates and are recommended over change in log₁₀(viral load) from baseline to day 7. Future work could aim to identify a viral load threshold value at day 3, 5, or 7 that is predictive of a poor clinical outcome; in a new trial in more recent populations, we recommend sampling viral load on days 1, 3, 5, and 7. The number of trials used in both our meta-analysis and previous results was fairly small, and R² could be heavily influenced by a single outlier trial, as seen in Singh et al [8]. R² can also be affected by sample size, as in our subgroup analysis. Taken together, our results suggest that change in log₁₀(viral load) from baseline to day 3 or 5 are moderate surrogates for 28-day hospitalization/death so may be used as end points in phase 2 clinical trials.

Supplementary Data

Supplementary materials are available at The Journal of Infectious Diseases online (http://jid.oxfordjournals.org/). Supplementary materials consist of data provided by the author that are published to benefit the reader. The posted materials are not copyedited. The contents of all supplementary data are the sole responsibility of the authors. Questions or messages regarding errors should be addressed to the author.

Notes

Acknowledgments . We thank Dr Dean Follmann for his invaluable help with the manuscript, and Dr Lori Dodd for contributions to early conceptualization and coordination. This work utilized the computational resources of the NIH HPC Biowulf cluster (https://hpc.nih.gov).

Author contributions. G. E. P., D. R., and D. M. S. contributed conceptualization. G. E. P., D. R., M. D. H., and V. D. G. contributed methodology. V. D. G. performed validation. A. M. and G. E. P. drafted the manuscript. A. M., E. C., and G. E. P. performed formal analysis. S. J. A. contributed resources and project administration. T. A. M., C. T. B., C. M., N. G., M. A., C. B., S. C., P. K. L., O. H., N. L. K., L. F. M., D. R. B., C. S., and O. M. contributed investigation, resources, and data curation. A. M. and E. C. performed visualization. G. E. P. contributed supervision. All authors reviewed and edited the manuscript.

Disclaimer. The content is the responsibility of the authors and should not be construed to represent US Food and Drug Administration's views or policies. The content of this publication does not necessarily reflect the views or policies of the Department of Health and Human Services, nor does mention of trade names, commercial products, or organizations imply endorsement by the US Government.

Data availability. Data are not publicly available.

Financial support. This project has been funded in whole or in part with federal funds from the National Cancer Institute, National Institutes of Health (NIH) (contract number 75N91019D00024); and the NIH (grant numbers UL1TR001442, UM1AI069424, and UM1AI068636 to D. M. S.). D. R. B. is supported by the National Institutes of Health (grant number K24AI184270). M. D. H. is supported by the National Institutes of Health (grant number UM1AI068634). C. M. is supported by NIH, National Institute of Allergy and Infectious Diseases (grant numbers UM1 AI068634 and 3UM1 AI068634-15S1). C. T. B. is supported by the National Center for Advancing Translational Sciences (grant numbers KL2TR002492 and UL1TR002494), and the NIH, National Institute of Diabetes and Digestive and Kidney Diseases (grant number K23DK124654). The collection of the nasal swab samples and conduct of COVID-OUT was supported by the Parsemus Foundation and Rainwater Charitable Foundation.