Treatment of Covid-19 With a Herbal Compound, Xagrotin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Covid-19 With a Herbal Compound, Xagrotin (NCT05017493), a randomized phase 1, phase 2 study. The primary outcome is Mortality.

2. Clinical Question

3. Trial Design

The registry describes an interventional, multicenter, randomized study of Xagrotin for early-stage Covid-19. It identifies the study as Phase 1 and Phase 2, with a parallel-group model and no masking. The study status is completed. The recorded study start was 2020-07-01, and the primary completion date was 2020-12-07.

Adults with confirmed Covid-19 were eligible if their disease was not more than 10 days old at enrollment, according to the brief summary. Participants in the treatment arm received Xagrotin together with standard care; participants in the control arm received standard care. The summary reports 361 participants in the treatment group and 178 in the control group. Separately, the registry lists total enrollment as 661. It does not explain the difference between this enrollment figure and the group counts used for the posted mortality results.

The treatment comparison is randomized, but the record does not describe the sequence-generation method, allocation concealment, or whether any stratification was used. Masking is listed as none, so the study was open label. The registry names Biomad AS as sponsor. It does not report the original sample-size justification, detailed treatment regimen, eligibility criteria beyond those in the brief summary, or a complete statistical analysis plan.

The posted primary outcome is mortality within 30 days after enrollment. The registry also lists three secondary outcomes: duration of disease from the beginning of treatment, hospitalization, and duration of hospitalization when it occurred. Results are available for duration of disease and duration of hospitalization, but hospitalization results are not reported in the registry record. No subgroup estimates are posted, although the brief summary says the investigators considered characteristics including gender, age, disease duration, smoking habits, and concomitant diseases.

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.

Before assignment: Age 18 or higher, Newly diagnosed (no longer than 10 days), PCR or clinically confirmed Covid-19

Overall Study

Reasons for not completing this period:

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: Both paitients who received and NOT received Xagrotin

6. Primary Endpoint

The registry lists the primary outcome as Mortality, measured over 30 days.

The primary endpoint counts participants who died by day 30 after enrollment. It is a binary outcome at the participant level: each person either died within the stated period or did not. The registry describes the measure as the number of participants who died, and gives the timeframe as 30 days. This makes the endpoint a fixed-time comparison rather than a measure of time until death.

Mortality is used in clinical trials because it is a direct, clearly defined event. A fixed follow-up period also gives the comparison a common time horizon. However, interpretation depends on knowing which participants were included in the outcome analysis, whether follow-up was complete, and how deaths and missing status were handled. Those details are not reported in the registry record.

The posted values are 2 participants in the treatment arm and 10 in the control arm, with group sizes of 361 and 178, respectively. The statistical comparison expresses the difference as a risk difference, with a confidence interval and an unadjusted p-value. These figures describe the registry results; they do not by themselves explain the study's conduct, establish the cause of any outcome, or answer questions beyond the defined 30-day period.

7. Results Posted in the Registry

• Treatment Arm: 0.6% (2/361) versus 5.6% (10/178) on control; risk difference -5.1 percentage points (95% CI -8.5 to -1.6), risk ratio 0.10 (0.02–0.45); unadjusted two-proportion z-test p = <0.001.

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.

Duration of Disease From Beginning of Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Treatment Arm: mean 9.90 versus 18.10 on control; difference -8.20 (95% CI -9.71 to -6.69), standardized effect d = -1.16; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Treatment Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Duration of Hospitalization When Occurred

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Treatment Arm: mean 5.56 versus 5.50 on control; difference 0.06 (95% CI -0.66 to 0.78), standardized effect d = 0.01; z-test p = 0.869.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of illness: duration of disease, hospitalization, and duration of hospitalization among those for whom it occurred. Their statistical patterns are not uniform. The posted duration-of-disease comparison is clearly separated from zero by its confidence interval, while the duration-of-hospitalization estimate is close to zero and its interval includes zero. Results for hospitalization itself are not reported in the registry record.

These secondary outcomes provide context for the primary mortality comparison, but they do not directly replicate it. They measure different events and use different analysis populations or scales. In particular, duration of hospitalization when it occurred concerns a subset defined by hospitalization, rather than all randomized participants. The record does not state how that subset was formed for analysis or how missing duration measurements were handled. The registry’s brief summary also mentions investigation of participant characteristics, but corresponding subgroup results are not posted.

Unadjusted secondary results carry less weight because the registry does not report a multiplicity strategy or a prespecified hierarchy among outcomes. When several outcomes or analyses are considered, the chance of obtaining an apparently notable result can increase. An unadjusted p-value does not account for that wider set of comparisons. The registry lists hospitalization among the secondary outcomes but does not report its results, and it does not provide an analysis plan that would clarify how the secondary endpoints were intended to support interpretation of the primary endpoint.

The overall pattern is therefore mixed in its degree of statistical separation, with one reported duration outcome showing a clear difference and another not showing a clear separation from zero. This pattern should be treated as descriptive. It cannot establish a common effect across outcomes, and it does not provide a complete account of all registered secondary questions.

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

• Duration of Disease From Beginning of Treatment
• Hospitalization
• Duration of Hospitalization When Occurred

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a randomized, parallel-group comparison, with Xagrotin plus standard care in one arm and standard care in the other. The primary endpoint is binary: a participant either died by day 30 after enrollment or did not. For a binary endpoint, each group’s event count is interpreted in relation to its group size. The comparison can then be expressed as an absolute difference in event proportions, or as a relative measure such as a risk ratio or odds ratio. These measures answer related but distinct questions.

What does the risk difference describe?

The risk difference is the event proportion in one group minus the event proportion in the reference group, according to the comparison’s direction. Its scale is an absolute difference in proportions. A value below zero in this comparison indicates a lower observed event proportion in the treatment arm. The registry estimate is -0.051, and its confidence interval extends from -0.085 to -0.016. The interval provides a range of effect values compatible with the data under the method used to calculate it. It does not represent a range in which the true value is guaranteed to lie.

The risk ratio compares the event proportions by division, while the odds ratio compares the odds of the event. The posted risk ratio is 0.099, with a confidence interval from 0.022 to 0.445. The posted odds ratio is 0.094, with a confidence interval from 0.020 to 0.432. Relative measures can look especially large or small when events are uncommon; they should be read alongside the event counts and the absolute-scale estimate. The registry does not describe which measure was designated as the principal effect measure in a prespecified analysis plan.

What does the p-value address?

The unadjusted p-value for mortality is <0.001. In general, a p-value assesses how compatible the observed data are with a specified null hypothesis, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The word “unadjusted” indicates that the registry does not report a correction for multiple comparisons for this value. The specific test and its assumptions are not described in the registry record.

A p-value also does not correct for design or data-quality concerns. It cannot show whether allocation was concealed, whether outcome status was missing, or whether the analysis followed a prespecified plan. Those aspects require information about trial conduct and analysis, not a different reading of the p-value.

How should mean differences be read?

The secondary outcomes reported as means are continuous measures. The mean difference compares the average value in one arm with the average in the reference arm. For duration of disease, the posted estimate is -8.2 days, with a confidence interval from -9.707 to -6.693. The registry reports a standard deviation of 5.5 days in the treatment arm and 9.5 days in the control arm. For duration of hospitalization when it occurred, the mean difference is 0.06 days, with a confidence interval from -0.656 to 0.776. The corresponding standard deviations are 4.94 and 3.42 days.

A standard deviation describes variation among individual observations within a group; it is not the uncertainty interval for the group mean or for the difference between means. The confidence interval for a mean difference reflects uncertainty in the estimated contrast. When that interval includes zero, the posted data are compatible with no mean difference as well as with values on either side of zero, according to the calculation used. The reported p-value for duration of hospitalization is 0.869. The statistical method used to calculate the mean-difference intervals and p-values is not specified in the registry record.

Why can outcome counts and denominators matter?

For mortality, the arm sizes in the outcome data are 361 and 178. The adverse-event record lists 483 participants at risk in the treatment arm and 178 in the control arm. The record does not explain why the treatment-arm number differs between these parts of the registry. The overall enrollment is 661, also without a reconciliation to the outcome group counts. These distinct figures should not be silently combined or treated as interchangeable. The registry does not state whether they reflect different analysis populations, reporting processes, or another reason.

General statistical principle: uncertainty in a comparison depends on both the size of the estimated effect and the amount and variability of information available. For binary outcomes, the event counts and group sizes inform precision. For continuous outcomes, both the sample size and the variability of observations matter. Unequal group sizes can also affect the balance of information between arms. The registry reports unequal outcome group sizes, but does not give the original rationale for allocation or the design assumptions used when the trial was planned.

What does the record omit about the analysis?

The registry reports no posted analysis entries. It does not identify the analysis population, describe treatment of missing observations, give a protocol-defined estimand, or state whether covariate adjustment was planned. It also does not report a method for handling multiple endpoints or subgroup analyses. The brief summary mentions investigation of participant characteristics, but no subgroup results are posted. Without these details, the posted estimates can be described and compared, but the full analytic pathway cannot be assessed.

General statistical principle: over-dispersion matters when the variability in observed data exceeds what a chosen model assumes. If a model underestimates variability, its standard errors can be too small and intervals too narrow. The primary endpoint is reported as participant event counts, not as a count of repeated events per person, and no over-dispersion parameter is reported. The registry does not give enough information to assess whether over-dispersion was relevant to any model used for the posted results.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty around an estimate. It gives a range of values that are compatible with the observed data under the specified statistical method and its assumptions. It is not a guarantee that the true effect lies within that range, and its width is not a measure of clinical importance. A narrower interval indicates greater statistical precision than a wider interval on the same scale.

For 30-day mortality, the risk-difference estimate is -0.051, with a confidence interval from -0.085 to -0.016. The interval is entirely below zero, so the range of values compatible with this calculation is on the negative side of the no-difference value. This is consistent with the unadjusted p-value of <0.001, while still leaving uncertainty about the size of the difference. The confidence interval does not remove uncertainty about study conduct, the analysis population, or how complete outcome follow-up was.

The relative estimates also have intervals that lie below 1: 0.022 to 0.445 for the risk ratio and 0.020 to 0.432 for the odds ratio. A value of 1 represents no relative difference for these measures. These intervals are broad on their respective relative scales, illustrating that the point estimates should not be treated as exact descriptions of the effect.

For duration of disease, the mean-difference interval is -9.707 to -6.693 days. For duration of hospitalization when it occurred, it is -0.656 to 0.776 days, which spans zero. These intervals address uncertainty in their respective mean differences and should not be compared directly with the mortality interval because the endpoints use different scales. The registry record does not specify the interval-calculation methods, confidence level, or any adjustment for multiple comparisons. The displayed estimates therefore require interpretation in the context of the posted methods and the information that is not reported.

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 figures are planning illustrations based on the observed effect, not the trial’s original design justification. The registry record does not report the original sample-size assumptions. These illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect.

For the binary mortality comparison and the continuous secondary comparisons, the figures are participants per arm, not total participants across both arms and not total events. The 80% power column gives the number of participants per arm in the planning calculation that would yield an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions held. The 90% power column uses a higher chance of detection and therefore generally calls for more participants per arm for the same assumed effect.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants per arm as the target effect becomes smaller. These are prospective planning scenarios calculated from observed results; they are not observed power and do not establish what the trial was designed to detect.

The original study’s sample-size rationale, target effect, and planned power are not reported in the registry record. The enrollment figure and outcome group sizes also differ, and the record does not reconcile them. The planning estimates should therefore be read as conditional illustrations rather than as a description of the actual recruitment plan or analysis population.

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 = 0.056; treatment proportion p₁ = 0.006; average p̄ = 0.031.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2446 = 0.4794.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2419 = 0.2036.
4. n = (0.4794 + 0.2036)² / (-0.0506)² = 181.9, rounded up to 182 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 <- 0.0561797752808989                          # control proportion
p1 <- 0.00554016620498615                          # 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(5017493)
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 = 182 (80% power), 244 (90% power)
 75% of observed effect: n per arm = 389 (80% power), 520 (90% power)
 50% of observed effect: n per arm = 1,019 (80% power), 1,363 (90% power)
power.prop.test: 181.9 
Simulated power at n = 182 per arm: 0.854 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists mortality as the primary outcome and three secondary outcomes: duration of disease from the beginning of treatment, hospitalization, and duration of hospitalization when it occurred. The registry reports four outcome measures in total, but results are not available for every listed secondary outcome. It records no posted analysis entries. The record does not describe a prespecified hierarchy of endpoints, a family of hypotheses, or a method for adjusting inference when multiple outcomes or subgroup comparisons are examined.

Multiplicity matters because each statistical comparison creates an opportunity to observe a result that appears unusual under a null hypothesis. When several comparisons are made, interpreting every unadjusted p-value as if it were the only test can overstate the strength of evidence. The posted values are unadjusted, and the registry does not say whether any multiplicity procedure was used outside the information shown in the record. It is therefore not possible to determine how the investigators planned to control the overall error rate or prioritize the secondary outcomes.

The brief summary says the investigators examined the impact of characteristics such as gender, age, disease duration, smoking habits, and concomitant diseases. No subgroup analysis estimates or interaction tests are posted. The number of such analyses, whether they were prespecified, and how they were intended to be interpreted are not reported in the registry record.

Information about missing data and analysis populations is also absent. The registry does not state whether all randomized participants were included in each analysis, how incomplete follow-up was handled, or whether any participants were excluded after randomization. The overall enrollment is 661, while the mortality outcome groups contain 361 and 178 participants; the treatment-arm adverse-event denominator is different again. The record does not explain these differences. They may reflect different reporting populations or other processes, but the reason is not reported in the registry record and should not be inferred.

These omissions limit assessment of whether the posted estimates correspond to the intended analysis and how robust they are to missing outcomes or analytic choices. They do not invalidate the reported numbers, but they leave important aspects of the statistical evidence unresolved.

15. 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 2.3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: xagrotin (5.6%).

The registry’s adverse-event data list 1 serious adverse event in the treatment arm and 10 in the control arm. The corresponding at-risk counts are 483 and 178. The record does not explain why the treatment-arm at-risk count differs from the 361 participants shown for the mortality outcome, so these figures should be read as the adverse-event record reports them rather than assumed to represent the same analysis population.

The adverse-event record also lists 113 participants with other adverse events in the treatment arm and 15 in the control arm. The record’s top serious-term entry is “Xagrotin” at 5.6%. It does not provide enough accompanying detail to determine the meaning or denominator of that label, so it should not be interpreted as a rate for a specific clinical event without further information. Death counts in the adverse-event record are 2 and 10, respectively.

These figures describe reported event counts, not a complete assessment of safety. Definitions, event severity categories, attribution procedures, exposure duration, and the handling of overlapping events are not reported in the registry record. The difference in group sizes and the unexplained denominator also matter when reading raw counts. No conclusion about comparative safety should be drawn from counts alone without the missing context.

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

The registry results show that the recorded number of deaths by day 30 was lower in the Xagrotin-plus-standard-care arm than in the standard-care arm. The posted risk-difference estimate is negative, its confidence interval is below zero, and the unadjusted p-value is <0.001. Those statistics describe the observed randomized-group comparison and its uncertainty under the method used for the posted calculation.

They do not, by themselves, establish why the groups differed. Randomization can support causal interpretation when it is properly conducted and when outcomes and analyses are handled appropriately, but the registry record does not provide details on sequence generation, allocation concealment, missing data, or analysis populations. The trial was unmasked, and the record does not describe how that feature was managed in outcome ascertainment or other parts of the study.

The finding is specific to the registered comparison, the participants described, and the 30-day mortality endpoint. It does not provide information about outcomes after that timeframe. Nor does it settle the interpretation of the secondary endpoints: the registry does not report hospitalization results, and the available duration outcomes show different degrees of statistical separation. The posted results do not establish how the findings apply to other populations, treatment regimens, or settings.

The record also does not report the original sample-size justification, a complete analysis plan, a multiplicity strategy, or a reconciliation of the enrollment and outcome denominators. Those gaps do not change the values that are posted, but they restrict how fully the analysis can be evaluated. A p-value is not a measure of the probability that a treatment is effective, and a confidence interval is not a guarantee about the true effect. Together, the results describe a sizeable observed difference with statistical uncertainty, while leaving questions about conduct, completeness, and analysis unresolved.

17. Why This Trial Matters Statistically

This trial is statistically notable because its primary endpoint is a participant-level event count, while the registry reports unequal group sizes and a substantial difference in the posted event counts. Interpreting the contrast on an absolute scale as well as relative scales helps distinguish the size of the observed difference from how it is expressed. The confidence interval and p-value add information about statistical uncertainty, but neither substitutes for the design and analysis details needed to evaluate the result fully.

The record also illustrates why denominators deserve attention. The overall enrollment is 661, the mortality outcome groups are 361 and 178, and the treatment-arm adverse-event record lists 483 at risk. The registry does not reconcile these figures. A reader cannot assume that the same participants contributed to every outcome, or infer why the denominators differ. Clear reporting of analysis populations would make the results easier to assess.

Several registered outcomes are not accompanied by posted results, and the secondary comparisons have different patterns. Without a reported multiplicity plan or analysis hierarchy, secondary p-values need cautious interpretation. The absence of subgroup results is also important because the brief summary mentions participant characteristics that were investigated, but the record does not show those analyses.

Finally, the planning illustrations demonstrate how strongly sample-size requirements depend on the effect a study aims to detect. Their assumptions are stated, but the trial’s original design rationale is not. That distinction prevents retrospective planning calculations from being mistaken for evidence about the study’s intended power. The case therefore emphasizes transparent reporting of trial design, denominators, analysis choices, and all registered outcomes alongside point estimates and uncertainty intervals.

18. 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 leaves important trial-design details unspecified. It identifies the study as randomized, parallel, and unmasked, but does not describe sequence generation, allocation concealment, or the process for assigning participants. The trial is described as multicenter, but the number and locations of centers are not reported. Details of the Xagrotin regimen, including dose and treatment duration, are also not reported in the registry record.

There is an unexplained difference between the overall enrollment of 661 and the mortality outcome groups of 361 and 178. The treatment-arm at-risk count for adverse events is 483, rather than the mortality outcome group count of 361. The registry does not explain whether these counts reflect different populations, reporting conventions, or another reason. No analysis population is named, and the record does not state how missing or incomplete outcome data were handled.

The primary endpoint is defined by death within 30 days after enrollment, but the registry does not give details about follow-up completeness or outcome ascertainment. It reports no analysis entries and does not provide the original statistical plan, sample-size justification, or multiplicity approach. Although the brief summary mentions investigation of participant characteristics, corresponding subgroup findings are not posted.

Hospitalization is listed as a secondary outcome, but its results are not reported in the registry record. The posted duration outcomes do not resolve that missing result, and the record does not explain the analysis population for duration of hospitalization when it occurred. The adverse-event listing also lacks details about definitions, attribution, and the denominator for the top serious-term entry. These limitations constrain interpretation of both the efficacy comparisons and the safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatment of Covid-19 With a Herbal Compound, Xagrotin — NCT05017493.
• Registry record last updated 2021-12-02; status last verified 2021-11.
• Results first posted 2021-12-02.
• 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.

22. Record Summary

NCT05017493 is a completed, randomized, unmasked, parallel-group Phase 1 and Phase 2 study sponsored by Biomad AS. It compared Xagrotin plus standard care with standard care for adults with confirmed Covid-19 whose disease was not more than 10 days old at enrollment. The recorded study start was 2020-07-01, and primary completion was 2020-12-07.

The primary outcome was mortality by day 30 after enrollment. The registry posts 2 deaths among 361 treatment-arm participants and 10 among 178 control-arm participants, with a risk difference of -0.051 and an unadjusted p-value of <0.001. Duration-of-disease and duration-of-hospitalization results are also posted; hospitalization results are not reported in the registry record. Analysis populations, missing-data procedures, multiplicity methods, and the original sample-size justification are not reported.