Clinical Trial of Safety and Efficacy of Ergoferon in Liquid Dosage Form in Treatment of Acute Upper Respiratory Tract Infections in Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial of Safety and Efficacy of Ergoferon in Liquid Dosage Form in Treatment of Acute Upper Respiratory Tract Infections in Adults (NCT01765920), a randomized phase 3 study. The primary outcome is Average Duration of Fever..

2. Clinical Question

3. Trial Design

The registry describes a phase 3, randomized, quadruple-masked, parallel-group trial with placebo control. Its official title identifies it as multicentre. The listed interventions were Ergoferon and placebo, and the record identifies Materia Medica Holding as sponsor. The status is completed; the recorded start is 2012-12 and primary completion is 2014-12. Enrollment was 342.

The two groups were assigned the same stated volume and frequency in their arm titles: Ergoferon or placebo, 5 ml 3 times a day. The placebo description says it followed the Ergoferon scheme. For the active arm, the record gives an initial schedule involving doses every 30 minutes for the first 2 hours and three further doses spaced through the rest of the day. The description ends while introducing the schedule from day 2, so the full later regimen is not reported in the registry record.

Masking and randomization are features intended to reduce certain biases in a comparison, but the registry record does not describe the implementation details or identify which roles were covered by quadruple masking. Allocation concealment procedures, randomization sequence methods, and deviations from assigned treatment are not reported in the registry record. The record also does not report the original sample-size justification or the assumptions used to plan the trial. These omissions limit what can be concluded about design decisions beyond the characteristics explicitly recorded.

The trial’s stated aims included evaluation of safety and clinical efficacy in adults with acute upper respiratory tract infections. The primary outcome was average fever duration. The registry additionally lists outcomes covering doctor-assessed symptoms, patient-reported symptoms, antipyretic use, and worsening of disease. The existence of those outcome definitions does not mean that numerical results for each are reported.

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: One patient in the placebo group did not have enough source data for primary outcome analysis.

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.

6. Primary Endpoint

The registry lists the primary outcome as Average Duration of Fever., measured over 1-7 days.

The primary endpoint is average duration of fever, expressed in days. Its source was tympanic temperature recorded by participants in a diary during treatment and observation, with measurements scheduled in the morning and evening. The registry defines the endpoint as the time from enrollment to the first return to the afebrile state or normalization of tympanic temperature to ≤37.0 °C.

This measure is intended to represent how long fever persisted after enrollment. Using a stated temperature criterion makes the event being timed operationally explicit, while diary measurements allow the endpoint to draw on repeated observations rather than a single temperature reading. Because measurements were made at set times, the recorded time to normalization is tied to the diary schedule; it is not necessarily the exact moment a participant’s temperature first crossed the threshold.

The registry reports the group outcome as a mean with standard deviation. The mean describes the average recorded duration, while the standard deviation describes variation among participants around that average. A mean comparison is a direct summary of the difference in average duration, but it does not show the full shape of the outcome distributions or how many participants had unusually short or long durations. The registry notes that a placebo-group participant lacked enough source data for the primary analysis. Further details about handling missing temperature records are not reported in the registry record.

7. Results Posted in the Registry

• Ergoferon (5 ml 3 Times a Day): mean 3.10 versus 3.60 on control; difference -0.50 (95% CI -0.78 to -0.22), standardized effect d = -0.38; 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.

Dynamics of Acute Upper Respiratory Tract Infections (URTI) Symptoms Severity According to the Physical Examination by the Doctor.

• 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:
  • Ergoferon (5 ml 3 Times a Day): mean 25.70 versus 28.50 on control; difference -2.80 (95% CI -5.59 to -0.01), standardized effect d = -0.22; z-test p = 0.049.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Ergoferon (5 ml 3 Times a Day) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Patients Who Have a Worsening of Disease.

• 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:
  • Ergoferon (5 ml 3 Times a Day): 1.8% (3/167) versus 1.2% (2/167) on control; risk difference 0.6 percentage points (95% CI -2.0 to 3.2), risk ratio 1.50 (0.25–8.86); unadjusted two-proportion z-test p = 0.652.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ergoferon (5 ml 3 Times a Day) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several perspectives on acute respiratory symptoms and events: doctor-assessed symptom severity, patient assessments using the Wisconsin Upper Respiratory Symptom Survey - 21, antipyretic use, and worsening of disease. The posted outcome descriptions indicate that these measures do not all represent the same construct. Some concern symptom severity, while others concern use of a medicine or a worsening event. They therefore complement the primary fever-duration measure rather than serving as interchangeable tests of the same outcome.

The numerical secondary results that are reported should be interpreted separately from the primary result. The record gives a doctor-assessed symptom comparison and a participant count for worsening of disease, with distinct sponsor-reported tests for those outcomes. The registry record does not report numerical result details for the patient-reported survey or antipyretic-use outcomes. The range of outcomes makes it possible to consider whether symptom-related measures point in a consistent direction, but incomplete numerical reporting limits that assessment.

Secondary findings carry less weight when many outcomes are examined without a reported multiplicity plan. In general, testing multiple outcomes increases the chance that some results may appear unusual by chance, even when no corresponding effect exists. The registry record does not report whether multiplicity adjustments were planned or applied. A secondary p-value should therefore be treated as exploratory evidence unless its role and analysis plan are clear, rather than as independent confirmation of the primary endpoint.

The primary outcome remains the trial’s stated central measure for this interpretation. Secondary outcomes can add context about different aspects of illness, but they do not resolve the discrepancy between the sponsor’s primary test and the mean-based recalculation. Nor can the secondary results establish the completeness of unreported outcomes or substitute for missing analysis-plan information.

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

• Dynamics of Acute Upper Respiratory Tract Infections (URTI) Symptoms Severity According to the Physical Examination by the Doctor.
• Dynamics of Acute URTI Symptoms Severity According to the Daily Wisconsin Upper Respiratory Symptom Survey - 21 (WURSS-21) Assessment of the Patient (Including the Total WURSS-21 Score, "Symptoms" Domain Score, and "Ability" Domain Score).
• Percentage of Patients Who Used Antipyretics.
• Percentage of Patients Who Have a Worsening of Disease.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant contributes a duration measured in days, and the group summaries are means and standard deviations. A mean is the arithmetic average of observed values. A standard deviation describes how spread out those values are around the mean. Neither summary alone reveals the full distribution, so the mean-based comparison should be understood as a concise summary rather than a complete account of participant-level outcomes.

The simple unadjusted recalculation compares the Ergoferon mean with the placebo mean. Its reported mean difference is -0.5 days, with the active group subtracted from the comparator in the stated direction: Ergoferon minus placebo. The negative sign indicates that the observed average was lower in the Ergoferon group. This is a descriptive contrast calculated from posted summary statistics; it is not an adjusted estimate and does not incorporate covariates or an alternative analysis population.

A confidence interval for a mean difference expresses uncertainty around the estimate under the assumptions of the calculation. It gives a range of values compatible with the data and method at the stated confidence level. When an interval is entirely on one side of zero, it indicates that the corresponding method’s data are not compatible with a zero difference at that confidence level. It does not show that every participant experienced a difference, nor does it establish that the estimated contrast is clinically important. The primary recalculated interval is entirely below zero, but its numeric limits are not repeated because their recorded precision exceeds the display limit used for explanatory text.

A p-value addresses how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or importance of an effect. The recalculated unadjusted p-value for the mean comparison is <0.001. The registry separately reports a Kruskal-Wallis test for the primary endpoint. These are distinct analyses: the mean-based recalculation focuses on the difference in means, whereas the Kruskal-Wallis procedure is rank based. Their p-values need not match, and the registry does not explain the discrepancy between the reported analysis and recalculation.

In general, rank-based methods can be useful when an analysis is intended to compare distributions without relying on the same assumptions as a mean-based test. They do not, however, directly provide a mean difference. In general, over-dispersion means that variation in the data is greater than a model assumes; if present and ignored, standard errors and uncertainty assessments may be unreliable. The registry record does not report a model-based over-dispersion assessment for the primary endpoint, and no claim that over-dispersion occurred is warranted.

The primary outcome used diary-based tympanic thermometry twice daily. As a general measurement issue, assessments taken at scheduled intervals can locate a threshold crossing only in relation to those observation times. The registry’s definition is clear about the temperature threshold and timing origin, but details about diary completion, adherence, missing readings, or verification of diary entries are not reported in the registry record. The record states that a placebo participant did not have enough source data for the primary outcome analysis; it does not describe additional missing-data procedures.

Secondary outcomes include continuous symptom measures and a count of participants with worsening disease. The posted doctor-assessed symptom outcome is reported as a mean and standard deviation, and the registry reports a Kruskal-Wallis test for it. The worsening outcome is binary at the participant level, and the registry reports a Fisher exact test. In general, Fisher’s exact test evaluates evidence of association in a two-group categorical comparison and can be used when event counts are sparse. Its p-value does not give the size or precision of a risk difference; those require estimates and intervals, which the simple recalculation separately presents for the worsening outcome.

The posted calculations labeled as recalculated are unadjusted comparisons based on the available summary statistics. They should not be confused with the sponsor’s analysis. The registry’s sponsor-reported test is the governing analysis when the discrepancy flag is true. Adjustments for covariates, the prespecified analysis plan, and the relationship between planned and performed analyses are not reported in the registry record. Statistical methods are most interpretable when their target quantity, assumptions, and analysis population are all clear; several of those details are unavailable in this record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data and analysis locate an effect estimate. The primary mean difference is -0.5 days, and the simple recalculation’s confidence interval lies entirely below zero. In general, a narrower interval indicates greater precision, while a wider interval reflects more uncertainty about the range of values compatible with the data and method. An interval that excludes zero does not, by itself, show that the effect is important to patients or that the estimate will be reproduced in another study.

The uncertainty interval belongs to the simple unadjusted mean-based recalculation. It should not be attributed to the sponsor’s Kruskal-Wallis analysis, for which the registry does not report an estimate or confidence interval. Because the reported and recalculated analyses differ, the interval is best read alongside the explicit distinction between those methods. The registry’s reported analysis takes precedence over the recalculation, while the recalculation helps describe the posted group means and their mean-based uncertainty.

Precision is also affected by data completeness and measurement. A placebo participant lacked enough source data for the primary analysis, and the registry does not report further detail about missing temperature measurements or the handling of missingness. The diary schedule and the use of a threshold-based endpoint are relevant to how precisely fever duration can be identified. The record does not provide participant-level data or a distributional display in the registry record for this interpretation, so the mean and standard deviation cannot show whether observations were symmetric or strongly influenced by extreme values.

Confidence intervals describe statistical uncertainty under a method; they do not capture every source of uncertainty. Differences in analysis choices, missing-data handling, measurement practices, or generalizability may matter but are not quantified by the interval. The primary interval therefore supports a precise statement about the recalculated mean contrast, not a complete assessment of all uncertainty surrounding the trial.

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 calculation. For the primary continuous outcome, the listed quantities are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to be detected is set as the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For 100% of the observed effect, the illustration gives 107 participants per arm for 80% power and 143 participants per arm for 90% power. For 75% of the observed effect, it gives 190 participants per arm for 80% power and 254 participants per arm for 90% power. For 50% of the observed effect, it gives 427 participants per arm for 80% power and 572 participants per arm for 90% power. These are per-arm figures, not totals across groups. The sample-size note says that time-to-event tables use total events, but this primary outcome’s planning figures are for participants per arm.

In general, power is the probability that a planned study will detect an effect of a specified size under the assumed model and significance level. The 80% and 90% columns describe different planning targets: the 90% target seeks a higher chance of detecting the assumed effect than the 80% target, and therefore requires more participants under these calculations. The fractions refer to how much of the observed effect the planning exercise assumes a future study will need to detect. Smaller assumed effects require more participants to distinguish them from random variation under otherwise unchanged assumptions. These figures are not observed power.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.500; pooled standard deviation σ = 1.304.
2. n = 2 × (1.96 + 0.842)² × 1.304² / -0.500² = 106.7, rounded up to 107 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
delta <- -0.5                      # observed difference in means
sigma <- 1.30353922131656                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1765920)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 107 (80% power), 143 (90% power)
 75% of observed effect: n per arm = 190 (80% power), 254 (90% power)
 50% of observed effect: n per arm = 427 (80% power), 572 (90% power)
power.t.test: 107.7 
Simulated power at n = 107 per arm: 0.803 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 reports a sponsor analysis of the primary outcome using a Kruskal-Wallis test, with a superiority result and a p-value below the stated 0.05 planning significance level. The registry does not report a sponsor estimate of the mean difference or a confidence interval for that analysis. The simple recalculation instead compares the posted group means, giving a mean difference of -0.5 days and an unadjusted p-value of <0.001.

These results should not be collapsed into a single test result. The recalculation is an unadjusted mean-based analysis from summary statistics; the sponsor’s reported test is rank based. The discrepancy flag is true, so the sponsor’s own analysis takes precedence. This does not make the recalculated mean contrast disappear: it remains a description of the posted means. It does mean that the recalculated p-value and interval should not be presented as though they were the sponsor’s primary inferential result.

The registry does not explain why the two analyses differ, nor does it provide enough detail to determine whether the discrepancy reflects different test assumptions, analysis populations, or another analytic choice. No explanation should be inferred. Readers can distinguish the sponsor-reported test from the transparent, simple recalculation while recognizing that the record leaves the reason for the discrepancy unreported.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several outcomes and reports analyses for the primary endpoint and secondary measures. When researchers test multiple outcomes, the chance of at least one apparently noteworthy result arising by chance can increase. In general, multiplicity procedures can control or otherwise address that issue, but they may also affect how results should be interpreted. The registry record does not report a multiplicity strategy, whether secondary analyses were adjusted, or whether any outcomes were designated as confirmatory versus exploratory beyond the primary outcome designation.

The primary analysis population is not fully described. The record states that one placebo-group participant did not have enough source data for primary outcome analysis. It gives the group counts used for the primary outcome, but does not report a fuller definition of the analysis population, such as whether it was intention-to-treat or per-protocol. Details about the cause of insufficient source data, missing temperature readings, imputation, or sensitivity analyses are not reported in the registry record. The effect of that missing information on the estimate cannot be determined from the record.

The registry reports the primary sponsor test and the simple mean-based recalculation yields a different result; the discrepancy flag is true. The sponsor’s own analysis takes precedence, but the record does not explain the difference. The prespecified statistical analysis plan, any changes to it, and the handling of protocol deviations are not reported in the registry record. Interim analyses and stopping rules are also not reported, so no assumptions about them should be made.

These limitations do not erase the posted outcome data, but they narrow the claims that can be supported. The reported means describe the analyzed participants, while missing analysis-population and multiplicity details leave uncertainty about the broader analysis strategy. Complete reporting would help distinguish planned analyses from exploratory ones and clarify how missing observations were handled.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry’s adverse-event fields report zero serious events affecting participants in the Ergoferon group and zero in the placebo group. Deaths are reported as zero in both groups. The listed numbers at risk for serious adverse events are 169 for Ergoferon and 173 for placebo. These safety denominators differ from the primary-outcome analysis counts, so they should not be treated as the numbers contributing to the fever-duration comparison.

The record also reports other, non-serious adverse events affecting 7 participants in the Ergoferon group and 6 in the placebo group, with 169 and 173 participants at risk, respectively. These counts are not serious adverse events and should be kept separate from the serious-event figures. The registry does not list serious adverse-event terms. A zero count in the recorded fields means no events were reported in those fields; it does not establish that the treatment has no risk, or that unrecorded events did not occur.

Safety comparisons are descriptive in this record. The registry does not provide uncertainty intervals or a detailed causal assessment for these event counts. Differences in at-risk denominators and the absence of event-level information limit interpretation. The counts should be read as registry-reported observations, not as a complete characterization of safety.

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

The posted primary outcome data show lower average fever duration in the Ergoferon group than in the placebo group: 3.1 days compared with 3.6 days. The simple mean-based recalculation expresses this as a difference of -0.5 days and gives an unadjusted p-value of <0.001. The registry’s own primary analysis is a Kruskal-Wallis test, and the discrepancy flag indicates that the sponsor-reported analysis and simple recalculation do not align. The sponsor’s analysis takes precedence, while the mean comparison remains a descriptive summary of the posted results.

These findings do not by themselves establish that the difference is clinically important. The registry does not report a threshold for a meaningful change in fever duration, and statistical evidence is not a substitute for such a threshold. The record also does not provide enough information about missing data, analysis populations, multiplicity, or the reason for the discrepancy to remove those interpretive uncertainties.

The results apply most directly to the trial as recorded: adults with acute upper respiratory tract infections assigned to liquid Ergoferon or placebo under the reported study conditions. Whether the same outcome pattern would occur in other populations, settings, or treatment regimens cannot be determined from this record alone. The registry’s safety counts should likewise be understood as reported observations, not proof that no risk exists.

In general, a clinical trial result is one part of an evidence assessment. The observed group contrast, its uncertainty, the method used to test it, completeness of outcome reporting, and relevance of the measured endpoint all matter. Here, those considerations support a bounded reading: the registry reports a difference in average fever duration, but the analysis discrepancy and unreported design and analysis details constrain how far the result can be interpreted.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and statistical method matter when interpreting a clinical comparison. The primary outcome is a mean duration, while the sponsor’s reported test is Kruskal-Wallis. A mean difference and a rank-based test answer related but non-identical questions. Reporting both the outcome summaries and the sponsor’s test makes the distinction visible; the discrepancy flag further signals that readers should not treat the recalculation as a replacement for the sponsor’s analysis.

The endpoint also shows how measurement choices shape an outcome. Fever duration was derived from participant diary entries and tympanic thermometry scheduled twice daily, using a stated threshold. This definition is more interpretable than an unspecified judgment of fever resolution, but its timing depends on when observations were collected. It also highlights the importance of reporting the completeness and handling of diary data, particularly because the registry notes insufficient source data for a placebo participant in the primary analysis.

The secondary outcomes span different kinds of evidence, including clinician assessment, patient reporting, medication use, and worsening. Such breadth can enrich a clinical description, but it also makes prespecified outcome hierarchies and multiplicity reporting important. Those details are not reported in the registry record. Statistical significance on a single outcome should therefore be read in the context of the complete reporting record, not in isolation.

Finally, the sample-size illustrations show how planning requirements depend on the effect size a future study aims to detect and the chosen power target. They are not the original design justification and do not describe what power this completed trial achieved. Keeping planning calculations, observed estimates, and sponsor-reported tests separate is a basic but consequential part of sound biostatistical interpretation.

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 most direct trial-specific limitation in the registry record is the discrepancy between the sponsor’s reported primary test and the simple recalculation from posted group summaries. The sponsor’s analysis takes precedence, but the record does not explain the discrepancy or provide a sponsor-reported effect estimate and confidence interval. This makes it harder to connect the reported test to the magnitude and precision of the mean contrast.

The primary endpoint relies on participant diary measurements of tympanic temperature twice daily. The registry defines the threshold and observation schedule, but does not report diary adherence, missing measurement patterns, validation procedures, or sensitivity analyses. It notes insufficient source data for a placebo participant, while broader missing-data handling is not reported. The mean and standard deviation also do not reveal the outcome distribution or the influence of unusually long or short durations.

The record does not report the original sample-size justification, the prespecified analysis plan, analysis-population definitions, multiplicity handling, interim analyses, or stopping rules. It identifies several secondary outcomes, but numerical result details for every named measure are not reported in the registry record. These gaps constrain assessment of whether all planned outcomes and analyses are represented.

Safety reporting is limited to aggregate counts in the registry fields; serious adverse-event terms are not listed. The safety denominators differ from those used for the primary outcome, and the record does not provide a detailed account of event timing or causal assessment. These are limitations of the available registry information and should not be taken as evidence that unreported events occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Trial of Safety and Efficacy of Ergoferon in Liquid Dosage Form in Treatment of Acute Upper Respiratory Tract Infections in Adults — NCT01765920.
• Registry record last updated 2021-01-05; status last verified 2019-01.
• Results first posted 2020-12-11.
• 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

The registry describes a completed, phase 3, randomized, quadruple-masked, parallel-group, placebo-controlled trial of liquid Ergoferon in adults with acute upper respiratory tract infections. Enrollment was 342. The primary outcome was average fever duration, defined using diary-recorded tympanic temperature and a threshold of ≤37.0 °C. The posted means were 3.1 days for Ergoferon and 3.6 days for placebo.

The sponsor’s reported primary analysis used a Kruskal-Wallis test. A simple unadjusted recalculation from the posted means gives a mean difference of -0.5 days and p <0.001; because the discrepancy flag is true, the sponsor’s analysis takes precedence. The registry does not explain the discrepancy. Missing-data procedures, the original sample-size justification, multiplicity handling, and several other analysis-plan details are not reported in the registry record.