Evaluation of the RD-X19 Treatment Device in Individuals With Mild COVID-19: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the RD-X19 Treatment Device in Individuals With Mild COVID-19 (NCT05817045), a randomized na study. The primary outcome is Number of Subjects With Sustained Resolution of COVID-19 Signs and Symptoms Without Subsequent Symptom Recurrence or Disease Progression (Until the End of the Study).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, sham-controlled, stratified, pivotal efficacy and safety study of the EmitBio RD-X19 device in individuals 40 years of age and older with mild COVID-19 in the at-home setting. The registry describes masking as quadruple and the model as sequential. The study is marked completed, and its phase is listed as NA. Enrollment is recorded as 330.

The registry lists two device interventions, RD-X19 and Sham. The active device description specifies 32 J/cm2 of electromagnetic energy directed at the oropharynx. The sham device also targets the oropharynx with electromagnetic energy, but at levels described as having lower inactivation potential against SARS-CoV2 in vitro. The registry does not report further operational details about device use beyond these descriptions and the at-home setting.

The study started on 2023-04-21, with primary completion on 2024-06-15. The primary outcome is defined over baseline through Day 14 and uses the Full Analysis Set. Its posted arm counts are 107 of 161 in Active and 120 of 166 in Sham. These counts describe the endpoint as registered; the reported sponsor analyses also include time-to-event estimates. The record does not explain how the registered enrollment relates to the primary outcome arm counts.

The registry lists two secondary outcome topics: two negative SARS-CoV-2 antigen tests without subsequent virological rebound during the remaining study time, and time to the first of two negative antigen tests. It posts results for two secondary outcomes. Details such as the randomization procedure, stratification factors, intended allocation ratio, and original sample-size justification are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS)

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Full Analysis Set (FAS): The Full Analysis Set (FAS) will consist of the set of randomized subjects, excluding: (i) subjects who were mis-randomized; and (ii) subject IDs corresponding to study participants that were re-randomized under a different subject ID.

6. Primary Endpoint

The registry lists the primary outcome as Number of Subjects With Sustained Resolution of COVID-19 Signs and Symptoms Without Subsequent Symptom Recurrence or Disease Progression (Until the End of the Study), measured over Baseline through Day 14.

The primary endpoint counts participants with sustained resolution of COVID-19 signs and symptoms without subsequent symptom recurrence or disease progression through the end of the study. Its timeframe is baseline through Day 14. The endpoint description covers cough, sore throat, nasal congestion, headache, chills and or sweats, myalgia, fatigue, and nausea, with or without vomiting. Each symptom is rated on a 4-point scale from none (0) to severe (3). Resolution is defined as all eight symptoms being assessed as none (0) or mild (1), with all remaining at or below 1 through study Day 14.

This kind of endpoint aims to capture a sustained state rather than a single favorable symptom rating: subsequent recurrence or progression affects whether a participant meets the outcome. The registry description also specifies how some observations are censored. Hospitalized participants are censored at 360 hours, corresponding to the end of the Day 14 time window. Participants who do not meet specified cases and take nirmatrelvir/ritonavir or molnupiravir after starting study treatment are censored when they first take that medication; other participants not meeting those cases are censored at their last recorded e-diary data.

The registry presents both participant counts and sponsor-reported hazard ratios for the primary outcome. A count is a straightforward summary of how many participants met the defined endpoint, while a time-to-event analysis uses the timing of the event and censoring. Those approaches do not necessarily estimate the same quantity. Further details of the sponsor model and its endpoint coding are not reported in the registry record.

7. Results Posted in the Registry

• Active: 66.5% (107/161) versus 72.3% (120/166) on control; risk difference -5.8 percentage points (95% CI -15.8 to 4.1), risk ratio 0.92 (0.80–1.06); unadjusted two-proportion z-test p = 0.253.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Subjects With Two Negative SARS-CoV-2 Antigen Tests (With a Minimum Time Between Tests of Six Hours) Without Subsequent Virological Rebound During the Subject's Remaining Time on Study

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active: 90.7% (146/161) versus 94.6% (157/166) on control; risk difference -3.9 percentage points (95% CI -9.6 to 1.8), risk ratio 0.96 (0.90–1.02); unadjusted two-proportion z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address virological observations: sustained absence of detectable antigen after two negative tests without later virological rebound, and time to the first of two negative antigen tests. The registry posts both participant-count summaries and sponsor-reported time-to-event analyses for these outcomes. Across those different summaries, the overall pattern is not uniform: the count-based recalculations do not show a clear separation, while some sponsor-reported time-to-event tests have smaller p-values. Those analyses answer related but not identical questions and should not be collapsed into a single conclusion.

The secondary outcomes provide context for the primary symptom endpoint, but they measure different aspects of the illness course. A virological outcome is not interchangeable with sustained symptom resolution, and a pattern in one does not establish the same pattern in the other. The registry's primary endpoint remains the symptom-based outcome; secondary findings can inform interpretation but do not replace it.

Unadjusted secondary results carry less weight when several outcomes or analyses are examined because the chance of finding an apparently notable result can increase across multiple tests. The registry record lists 8 analyses overall, while the multiplicity strategy and any adjustment for multiple comparisons are not reported in the registry record. Without that information, secondary p-values should be treated as exploratory evidence rather than as stand-alone confirmatory findings. The record also does not report a hierarchy specifying which secondary outcome, if any, was intended to support a confirmatory claim.

Differences between count-based and time-to-event findings may reflect the event definition, event timing, censoring, or model assumptions. The registry record does not supply enough detail to determine which factor explains the differing patterns. The results are most appropriately read outcome by outcome, alongside each estimate and confidence interval, while keeping the primary endpoint and the limitations of multiple testing in view.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Subjects With Two Negative SARS-CoV-2 Antigen Tests (With a Minimum Time Between Tests of Six Hours) Without Subsequent Virological Rebound During the Subject's Remaining Time on Study
• Kaplan-Meier Estimates Time to First of Two Negative SARS-CoV-2 Antigen Tests

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is presented as a participant count, and the basic comparison is a risk difference. A risk is the proportion of participants in a group who meet the defined outcome. The risk difference subtracts the comparator-group risk from the active-group risk; the posted estimate is -0.058. The accompanying 95% confidence interval runs from -0.158 to 0.042. Because the interval covers zero, the data are compatible with no difference as well as with differences in either direction. The unadjusted p-value is 0.253. A p-value describes how unusual data at least this discrepant from the null hypothesis would be under the statistical model and null assumption; it is not the probability that the null hypothesis is true.

What does the sponsor's hazard ratio measure?

A hazard ratio is used in time-to-event analysis. It compares the instantaneous event rates between groups among participants who have not yet experienced the event and remain under observation. Its interpretation depends on which event is analyzed, how groups are ordered, the model, and the handling of censoring. The registry lists NPANCOVA as the method and gives hazard-ratio estimates, but the expansion of that method, model specification, covariates, and the precise contrast coding are not reported in the registry record. Consequently, the reported hazard ratios can be described as sponsor analyses, but their detailed modeling choices cannot be reconstructed from the record.

The sponsor reports three primary hazard-ratio analyses. Their estimates are 1.01, 1.02, and 1.02, with 95% confidence intervals 0.777 to 1.310, 0.774 to 1.337, and 0.782 to 1.342. The associated p-values are 0.948, 0.902, and 0.859. In general, a hazard-ratio interval that includes 1 does not establish a difference at the corresponding confidence level. These results are consistent with substantial uncertainty about the contrast, rather than a precise estimate of a distinct effect.

Why are counts and time-to-event results different?

A count of participants meeting the outcome reduces the endpoint to whether each participant met the definition. A time-to-event analysis also uses when the event occurred and can account for participants whose event time is not observed in the same way as others. The primary endpoint description includes censoring instructions for hospitalization, use of specified antiviral medications, and the last time with e-diary data. These rules affect which time contributes to the analysis. The record does not provide enough information to reproduce the sponsor's time-to-event analyses from the posted counts.

For the unadjusted count calculation, the risk difference and its interval summarize the two posted arm counts without adjustment. Other measures listed with that comparison include a risk ratio and an odds ratio, each with its own interval. These are alternative ways to express a binary-outcome contrast, not independent trial findings. A risk ratio compares the proportions directly; an odds ratio compares the odds of the outcome. Their numerical values and interpretations differ, especially when the outcome is common. The registry's sponsor analysis remains distinct from these simple summaries.

What does statistical significance tell the reader?

Statistical significance is a convention for assessing compatibility with a null model, not a measure of clinical importance, safety, or certainty. A small p-value does not by itself establish that an effect is large or meaningful. A larger p-value does not show that groups are equivalent. Confidence intervals are useful alongside p-values because they show a range of effect estimates compatible with the data and model. Neither measure repairs limitations in endpoint definition, missing data, study conduct, or incomplete reporting.

The registry record includes a Full Analysis Set label for the primary endpoint. The exact membership rules for that set are not reported in the registry record. It also includes an unadjusted recalculation based on posted counts; this is not the same as a model-based sponsor analysis. The record does not report enough detail to establish the relationship between all analyses, their prespecified status, or the treatment of multiplicity. Those omissions limit how far the results can be interpreted as a single confirmatory test.

11. Confidence Intervals and Precision

The primary unadjusted risk difference is -0.058, and its 95% confidence interval is -0.158 to 0.042. The interval crosses zero, so the observed counts do not pin down the direction of the underlying difference. It is compatible with a negative contrast and with a positive one. The interval is therefore more informative than the point estimate alone: it conveys uncertainty that remains despite the numerical estimate being negative.

The sponsor's primary hazard-ratio confidence intervals are 0.777 to 1.310, 0.774 to 1.337, and 0.782 to 1.342. Each includes 1, the value corresponding to no relative difference in the hazard under the usual interpretation of a hazard ratio. Their breadth indicates that the reported analyses do not estimate the contrast with high precision. Because the registry record does not describe the differences among these analyses, the three estimates should not be selected or combined by an invented rule.

A confidence interval is not a range that is guaranteed to contain the true value, nor is it a probability statement about a particular effect after the data have been observed. In general, it is a method for expressing the uncertainty of an estimate under the model and sampling assumptions used. Its width reflects both the information in the data and the analysis method. For this trial, interpretation also depends on censoring and on whether the count-based or time-to-event estimand is of interest.

The secondary outcome recalculations and sponsor analyses have their own intervals, which also matter when judging how much precision the data offer. Their results are not substitutes for the primary endpoint. Interval estimates should be read with attention to the endpoint definition, the direction of the contrast, and the analysis used; the registry record does not report all details needed to resolve those aspects for every sponsor analysis.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustration is a planning exercise based on the observed effect, not a report of the trial's original design assumptions. For binary outcomes such as the primary participant-count endpoint, the entries are participants per arm. For time-to-event outcomes, the entries are total events, using the Schoenfeld approach. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect.

The 80% power column describes the participants per arm, or total events for a time-to-event outcome, required under those assumptions for an 80% chance of detecting the specified effect if it is present. The 90% power column gives the corresponding planning quantity for a 90% chance. These are conditional planning calculations, not guarantees about what a future study will find. The original trial's own sample-size justification and design assumptions are not reported in the registry record.

The rows labeled as planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the illustration changes when the target effect is smaller than the estimate observed in this trial. Smaller effects need more participants per arm, or more total events for time-to-event analyses, to reach the same planned power under the stated assumptions. The curve expresses that general relationship; it should be read as a planning aid rather than as evidence about the trial's achieved precision.

These figures are not observed power. They do not tell whether the completed study had a particular probability of finding a statistically significant result after the outcome data were known. Planning figures depend on the assumed effect and analysis conditions, while precision of the completed trial is better judged from its estimates and confidence intervals.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.723; treatment proportion p₁ = 0.665; average p̄ = 0.694.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6519 = 1.2776.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6506 = 0.5475.
4. n = (1.2776 + 0.5475)² / (-0.0583)² = 980.2, rounded up to 981 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.72289156626506                          # control proportion
p1 <- 0.664596273291925                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(5817045)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 981 (80% power), 1,312 (90% power)
 75% of observed effect: n per arm = 1,720 (80% power), 2,303 (90% power)
 50% of observed effect: n per arm = 3,817 (80% power), 5,109 (90% power)
power.prop.test: 980.2 
Simulated power at n = 981 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry's sponsor analyses for the primary outcome are time-to-event analyses reported as hazard ratios. Their three estimates are 1.01, 1.02, and 1.02, with 95% confidence intervals that include 1 and p-values of 0.948, 0.902, and 0.859. These are the sponsor's model-based results as posted in the registry.

The separate recalculation uses the posted participant counts: 107 of 161 in Active and 120 of 166 in Sham. It gives an unadjusted risk difference of -0.058, a 95% confidence interval from -0.158 to 0.042, and an unadjusted p-value of 0.253. It is a simple comparison of proportions and does not reproduce the sponsor's time-to-event method. The two approaches use different summaries of the endpoint and should not be expected to match numerically.

The registry does not report sufficient model detail to reconcile the hazard-ratio analyses with the count-based recalculation or to identify the distinctions among the three sponsor analyses. The posted results do not flag a discrepancy between the sponsor results and the recalculation. The recalculation is therefore best treated as a transparent, unadjusted companion summary, not as a correction to the sponsor analysis or as a replacement for a prespecified analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 8 analyses overall and posts multiple analyses for the primary and secondary outcomes. It does not report whether the analyses were prespecified as a hierarchy, whether one analysis was designated as the sole primary inferential test, or whether p-values were adjusted for multiple comparisons. A multiplicity plan matters because repeated testing can make nominal p-values less persuasive as confirmatory evidence. Without a reported plan, the primary and secondary p-values should be interpreted in the context of the several analyses reported, not as if each were the only test conducted.

The primary endpoint identifies the Full Analysis Set as its population. The membership rules for that set, including how participants were included or excluded, are not reported in the registry record. The secondary outcome populations are also not specified in the posted results. Safety counts use their own at-risk group sizes, which are reported separately from the primary outcome group sizes.

The primary endpoint description does give censoring rules for particular circumstances: hospitalization, taking nirmatrelvir/ritonavir or molnupiravir after initiating study treatment in specified cases, and the last time e-diary data were recorded in other cases. Those are endpoint-specific instructions. They do not, by themselves, describe all missing-data handling, explain the frequency or reasons for missing observations, or identify sensitivity analyses. Such details are not reported in the registry record.

The distinction between censoring and missingness is important in time-to-event analysis. Censoring records that an event time is not observed beyond a specified point; interpretation relies on assumptions about the censoring process. Missing symptom records can also affect whether sustained resolution is established. The registry's outcome description states how some observations are censored, but broader assumptions and checks are not reported. The record does not report interim analyses, stopping rules, or a complete statistical analysis plan.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent non-serious adverse event terms

For serious adverse events, the posted at-risk group sizes are 158 in Active and 162 in Sham, with 0 serious events in each group. The registry lists 0 deaths in both groups. No serious adverse event terms are listed. These figures describe the reported safety counts; they should not be read as proof that serious harms are impossible or that the groups have identical safety profiles.

The registry also reports other, non-serious adverse events for 18 participants in Active and 12 in Sham. Those counts are distinct from the serious-event figures and are not a complete description of event types or severity beyond the registry categories. The record does not provide further information about event definitions, exposure time, relatedness assessments, or how the safety analysis population was determined.

Safety counts are descriptive and depend on the participants included in each at-risk group and on the period and procedures for event collection. They do not establish a comparative risk by themselves. The serious-event counts are small enough that the absence of reported events in these groups should be interpreted with appropriate caution, especially without further detail on follow-up and event ascertainment.

17. What the Result Does, and Does Not, Mean

The posted primary results do not show a statistically clear difference between RD-X19 and the sham device on the registered measure of sustained symptom resolution. The unadjusted count comparison has an interval that includes zero, and the sponsor-reported primary hazard-ratio intervals include 1. These results indicate uncertainty in the estimated contrast; they do not establish that the devices have exactly the same effect.

The findings also do not demonstrate equivalence or non-inferiority. Such conclusions require an appropriate design, prespecified margins, and analysis plan. These details are not reported in the registry record. A non-significant test is not evidence by itself that a meaningful difference has been ruled out, particularly when the confidence intervals still permit effects in either direction.

The endpoint is a defined symptom-based measure over baseline through Day 14, with censoring rules for certain circumstances. It is not a general measure of every aspect of COVID-19, nor should a result on this endpoint automatically be extended to other populations, settings, devices, or outcomes. The registered population was individuals 40 years of age and older with mild COVID-19 in the at-home setting. The registry record does not establish applicability beyond that scope.

Secondary virological findings should be interpreted separately from the primary symptom outcome. Their analyses involve different endpoints, and the record does not report a multiplicity plan. Safety counts are also descriptive and cannot establish comparative safety on their own. Taken together, the registry record supports a careful account of the estimates and their uncertainty, rather than a broad claim about treatment benefit or lack of benefit.

Interpretation is further limited by incomplete reporting of the statistical plan, analysis distinctions, missing-data handling, and outcome populations beyond the primary Full Analysis Set label. These gaps do not invalidate the posted results, but they restrict independent assessment and make it important to distinguish the registry's reported analyses from the simple unadjusted recalculations.

18. Why This Trial Matters Statistically

This trial illustrates why the definition of an endpoint is central to interpreting a clinical comparison. The primary outcome is not merely a symptom score at one observation: it requires all eight symptoms to reach none or mild and remain at or below that threshold through Day 14, without subsequent recurrence or disease progression. That sustained criterion gives the outcome a different meaning from a single-time-point rating or a virological test.

The record also illustrates the difference between a binary summary and a time-to-event analysis. Participant counts offer an accessible comparison of how many met the endpoint, while hazard-ratio analyses use event timing and censoring. Both can be useful, but they do not answer exactly the same question. A sound reading keeps the estimand and analysis method attached to each result rather than treating all effect measures as interchangeable.

Precision is equally important. The primary count estimate is accompanied by an interval that spans both directions, and the sponsor's primary hazard-ratio intervals include 1. The estimates therefore need to be read with uncertainty, not reduced to whether a p-value crosses a threshold. This is particularly relevant when the registry reports several analyses and does not describe a multiplicity strategy.

The registry record also shows the limits of registry-level reporting. It provides trial design features, outcome definitions, selected results, and safety counts, but does not report a full statistical analysis plan, the original sample-size justification, or detailed missing-data methods. Recognizing those boundaries is part of statistical interpretation: conclusions should track what the analyses estimate and what the record makes possible to assess.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the randomization procedure, stratification factors, allocation ratio, or the original sample-size justification. Although the study is described as stratified and sequential, details needed to evaluate those design features are not reported in the registry record. The record also does not state how the registered enrollment of 330 relates to the primary outcome arm counts of 161 and 166.

The primary endpoint includes explicit censoring instructions, but the record does not give a full account of missing observations, the amount of missing data, sensitivity analyses, or assumptions about censoring. The Full Analysis Set is named, but its membership rules are not reported. The analysis populations for the secondary outcomes are also not specified.

Several sponsor analyses are posted for the primary and secondary outcomes, but the registry does not explain their differences, specify the full model, identify the exact contrast coding, or describe which analysis was designated for confirmatory inference. The expansion of NPANCOVA and its implementation details are not reported. A multiplicity strategy is also not reported, limiting the strength of inferences from multiple p-values.

The safety results provide group counts, but details about event definitions, collection procedures, exposure time, and relatedness assessments are not reported in the registry record. The record therefore supports a description of the posted counts, but not a comprehensive safety assessment. These reporting limitations call for restraint when drawing conclusions beyond the specific estimates, outcomes, and population that are documented.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the RD-X19 Treatment Device in Individuals With Mild COVID-19 — NCT05817045.
• Registry record last updated 2024-10-24; status last verified 2024-10.
• Results first posted 2024-10-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT05817045 is a completed randomized, double-blind, sham-controlled, stratified study of the EmitBio RD-X19 device in individuals 40 years of age and older with mild COVID-19 in the at-home setting. The registry lists quadruple masking, a sequential model, and enrollment of 330. The study started on 2023-04-21, with primary completion on 2024-06-15; its phase is listed as NA.

The primary outcome was sustained resolution of COVID-19 signs and symptoms without recurrence or progression through Day 14. The posted counts were 107 of 161 in Active and 120 of 166 in Sham. The unadjusted comparison and sponsor-reported time-to-event analyses do not show a statistically clear separation, with intervals that include the respective no-difference values.

The record also posts two secondary virological outcomes and safety counts. Multiplicity, detailed missing-data methods, the full statistical analysis plan, and the original sample-size justification are not reported in the registry record.