Efficacy and Safety of Nitazoxanide in the Treatment of Colds Due to Enterovirus/Rhinovirus Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Nitazoxanide in the Treatment of Colds Due to Enterovirus/Rhinovirus Infection (NCT03605862), a randomized phase 3 study. The primary outcome is Time From First Dose to Symptom Response Over 21 Days of Follow up Based Upon the FLU-PRO Instrument (Novel Endpoint).

2. Clinical Question

The endpoint used daily evening FLU-PRO symptom diaries. A response required all 32 symptom ratings to meet their assigned thresholds for 2 consecutive daily diary periods, without symptom relief medication. The registry describes the thresholds as developed using blinded symptom data and their association with patient-reported usual health.

The trial also listed ability to perform all normal activities and proportions experiencing complications of EV/RV infection as secondary outcomes. The registry record gives a numerical result for complications, but a result for ability to perform all normal activities is not reported in the registry record.

3. Trial Design

This was a Phase III, randomized, triple-masked, parallel-group, placebo-controlled trial sponsored by Romark Laboratories L.C. The condition listed was colds due to enterovirus/rhinovirus infection. The trial record lists an overall enrollment of 1756 and a status of completed. The start date was 2018-09-11, and primary completion was recorded as 2019-02-04.

The intervention groups received nitazoxanide or matching placebo. Both regimens were oral tablets taken twice daily for 5 days; the nitazoxanide regimen was two 300 mg tablets at each dosing time. The record describes the design as randomized and triple masked but does not specify in the posted information which roles were masked or how randomization was implemented. Further details of allocation procedures are not reported in the registry record.

The primary efficacy population was the intent-to-treat infected population, defined in the record as participants with laboratory-confirmed EV/RV infection. That population included 286 participants assigned to nitazoxanide and 298 assigned to placebo. The overall enrollment and the primary-analysis population are different record-level quantities: the primary analysis was restricted to participants meeting the infection definition.

The trial recorded 11 outcome measures and 13 analyses. Its listed secondary outcomes included time from first dose to ability to perform all normal activities and proportions experiencing complications of EV/RV infection. The duration and details of follow-up for the primary symptom-response outcome are given as up to 21 days; the complications outcome has a 28-day timeframe. More detailed operational information, including the method used to confirm infection and the schedule of other assessments, is 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: The primary efficacy (intent-to-treat infected, ITTI) population consisted of 584 subjects (N=286 in NTZ group, N=298 in Placebo group) with laboratory-confirmed Enterovirus/Rhinovirus (EV/RV) infection.

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: All subjects receiving at least one dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Time From First Dose to Symptom Response Over 21 Days of Follow up Based Upon the FLU-PRO Instrument (Novel Endpoint), measured over Up to 21 days.

The primary endpoint was the time from first dose to symptom response, measured in hours over follow-up of up to 21 days. Participants used the FLU-PRO questionnaire once daily in the evening to rate the severity of 32 symptoms. The record defines response as meeting the assigned threshold for every symptom on 2 consecutive daily diary periods, with no use of symptom relief medication during that period.

The registry says the symptom thresholds were developed by applying an algorithm to blinded symptom data to identify a set most closely associated with patient-reported usual health. This makes the endpoint a composite diary-based event: it depends on symptom ratings across all listed symptoms, repeated confirmation across consecutive diaries, and the stated medication condition. It therefore differs from an outcome based on one symptom or a single assessment.

General statistical context: time-to-event endpoints use both whether an event occurs and how long it takes to occur. They can retain information about the timing of response, rather than reducing each participant’s experience to a yes-or-no outcome at one selected time. Their interpretation depends on how the event is defined and on the observation process, including diary completion and censoring. The registry record does not report details of censoring or how incomplete diaries were handled.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a time-to-event measure. The event is symptom response as defined by the FLU-PRO thresholds, and the measured time starts at first dose. The registry summarizes each group using a median and interquartile range. A median is the central point of an ordered distribution; the interquartile range describes the middle half of the observed values. These summaries are descriptive. They do not, by themselves, quantify the uncertainty in a difference between groups.

The posted primary comparison uses the Gehan-Wilcoxon test. General statistical context: this is a rank-based method for comparing time-to-event distributions. It accounts for the ordering of observed event times and can give relatively greater weight to earlier events than some other time-to-event tests. The test evaluates evidence of a group difference under its assumptions; it does not directly report the size of that difference. The registry does not report a primary effect estimate or confidence interval alongside the test result, so the magnitude and precision of a contrast are not fully expressed by the posted analysis.

For binary outcomes, a risk difference compares the observed proportions in two groups by subtracting one group’s proportion from the other’s. General statistical context: a confidence interval describes the range of effect values that are reasonably compatible with the data and the method used to construct the interval. If an interval for a risk difference includes zero, the data do not distinguish the estimated difference from no difference at the stated confidence level. This does not establish equivalence or rule out meaningful effects; the interval’s width matters as well as whether it includes zero.

The registry’s complications analysis reports a Fisher exact test. General statistical context: Fisher’s exact test evaluates association between group assignment and a binary outcome using the observed counts, and is often used when event counts are limited. An unadjusted re-calculation from posted counts gives a risk-difference interval that includes no difference. The re-calculation is not a replacement for the sponsor’s analysis: the registry’s reported test is the sponsor’s analysis, and it takes precedence when there is a discrepancy. No discrepancy is identified in this record.

The sample-size illustrations are planning calculations based on the observed complications effect, not the trial’s original design. They assume a two-sided significance level of 0.05, equal allocation, and a normal approximation. The displayed scenarios plan for 100%, 75%, or 50% of the observed effect. For example, planning for 75% of that effect gives 2,396 participants per arm for 80% power and 3,207 participants per arm for 90% power. These figures are illustrations of how required sample size changes with the assumed effect size; they are not observed power and do not show that the original trial was designed with these assumptions. The trial’s own sample-size justification is not reported in the registry record.

General statistical context: power is a design property calculated for a specified effect size, significance level, allocation, and analysis plan. It is not a measure of the probability that a particular observed result is true. Planning calculations based on the observed effect are especially dependent on that estimate, which may be imprecise. Smaller assumed effects generally require larger samples to detect under otherwise similar assumptions. The displayed planning values do not establish that the trial had adequate power for its primary endpoint or for its secondary outcomes.

The planning description distinguishes event-total calculations for time-to-event outcomes from per-arm participant counts for other outcomes. The complications illustrations are participant counts per arm. No separate numerical planning illustration for the primary endpoint is reported in the registry record. The record also does not report the intended effect size, power target, or sample-size rationale used for the trial’s original design.

The counts used in the primary efficacy analysis are for participants with laboratory-confirmed infection, whereas the safety record gives group-specific numbers at risk for adverse-event summaries. These populations and denominators should be interpreted in relation to their specific analyses, not treated as interchangeable. The registry record does not report additional detail on the analysis populations for every outcome.

10. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a Gehan-Wilcoxon test comparing time to symptom response. Its reported result does not establish a statistically significant difference between nitazoxanide and placebo. The registry does not post a primary effect estimate or confidence interval for that test, so the reported group medians and interquartile ranges provide descriptive context rather than a complete estimate of the treatment contrast.

For complications, the sponsor reports a Fisher exact test. The unadjusted re-calculation from the posted counts produces a risk-difference interval that includes no difference, consistent with the lack of a statistically significant result in the sponsor’s analysis. The sponsor’s analysis takes precedence when a discrepancy exists; the registry record does not flag a discrepancy for this outcome. The re-calculation is a simple unadjusted analysis of the posted summary counts and does not replace the registry-reported test.

Neither analysis should be read as proof of equivalence. The primary result lacks a posted confidence interval for the contrast, while the complications re-calculation remains compatible with no difference and with effects in either direction. The statistical tests address evidence against a no-difference hypothesis; they do not establish the size, importance, or certainty of an effect on their own.

11. Multiplicity, Missing Data and Analysis Populations

The registry lists 11 outcome measures and 13 analyses, including the primary symptom-response outcome and secondary outcomes. The posted record does not describe a multiplicity strategy, a hierarchy of outcomes, or a plan for controlling the chance of false-positive findings across multiple comparisons. It is therefore not reported in the registry record whether the secondary analyses were adjusted, treated as exploratory, or assessed under another prespecified approach.

General statistical context: when several hypotheses are tested, each test can contribute to the chance of at least one apparently positive result even if no true effects exist. Multiplicity procedures can control that overall risk, often at a cost to power for individual comparisons. Without knowing the planned testing family and adjustment method, secondary p-values should be interpreted cautiously and should not be treated as independent confirmatory evidence.

Missing-data methods are also not reported in the registry record. This matters particularly for a diary-based primary endpoint, because the response definition requires ratings for all 32 symptoms over 2 consecutive daily diary periods. The record does not state how missed diary entries, withdrawal, use of symptom relief medication, censoring, or other incomplete observations were handled in the time-to-event analysis. It also does not report the completeness of diary data by group.

The primary efficacy population is described as intent-to-treat infected and consists of laboratory-confirmed EV/RV cases. The record does not provide further detail about how participants without confirmed infection, or participants with other deviations from the intended analysis, were treated in other analyses. A complete accounting of analysis populations and missing outcomes is not reported in the registry record.

The registry does not report interim analyses, stopping rules, or a statistical analysis plan that would clarify these issues. Their absence from the record should not be taken to mean that such procedures were or were not used. It means that the posted information does not allow readers to assess the planned handling of multiplicity, missing data, or all analysis populations in detail.

12. 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% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac failure congestive (0.1%), cholelithiasis (0.1%), gastroenteritis viral (0.1%), post procedural infection (0.1%), urosepsis (0.1%).

The adverse-event record gives group-specific numbers at risk of 872 for nitazoxanide and 884 for placebo. Serious adverse events were recorded for 4 participants in the nitazoxanide group and 1 in the placebo group. Other adverse events were recorded for 200 and 58 participants, respectively. Deaths were recorded as 0 in each group. These safety denominators differ from the primary efficacy population, so they should not be substituted for the denominators in the symptom-response analysis.

The listed serious-event terms each have a reported frequency of 0.1%: cardiac failure congestive, cholelithiasis, viral gastroenteritis, post procedural infection, urosepsis, and status epilepticus. The record does not provide enough detail to determine whether these terms represent separate people, whether events were judged related to treatment, or how event severity and timing were assessed. No causal conclusion follows from the counts alone.

These are descriptive safety figures. Differences in the recorded counts do not, by themselves, establish that treatment caused or prevented events. The registry record does not report inferential comparisons or confidence intervals for these adverse-event summaries.

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

The posted results describe a randomized comparison of nitazoxanide and placebo in participants with laboratory-confirmed EV/RV infection. For the primary endpoint, the observed median time to symptom response was 122.5 hours with nitazoxanide and 137.1 hours with placebo. The sponsor’s Gehan-Wilcoxon comparison did not establish a statistically significant difference. The registry therefore does not provide clear statistical evidence of a difference in time to response in this analysis.

That finding is not proof that the treatments have identical effects. A non-significant test can occur when the true difference is absent, but also when the data are not sufficiently precise to distinguish a difference. The registry does not provide a primary contrast estimate with a confidence interval, limiting direct assessment of the plausible size of a difference. The descriptive medians and interquartile ranges should not be interpreted as a definitive estimate of the group effect.

The complications outcome also does not establish a statistically significant difference in the sponsor’s analysis. Its unadjusted re-calculation has an interval that includes no difference. The posted numerical results for that outcome are therefore inconclusive as evidence of a group difference. A result for the listed ability-to-perform-normal-activities outcome is not reported in the registry record.

The findings apply to the analyses and populations described in the registry, especially the infected primary efficacy population. They do not establish effects in populations not described in the record, nor do they settle questions that the posted outcomes did not measure. Interpretation is further limited by unreported detail on missing data, analysis populations beyond the primary definition, and multiplicity handling.

These results are statistical descriptions of one trial record, not medical advice. They neither establish that nitazoxanide works nor establish that it does not work. They show that the posted analyses did not demonstrate a statistically significant difference on the reported primary and complications comparisons, while leaving uncertainty about the size of effects compatible with the data.

14. Why This Trial Matters Statistically

This trial illustrates how a clinical endpoint’s definition shapes the statistical question. The primary outcome is not a single symptom score or a symptom status at one visit. It is time until all 32 diary symptoms meet assigned thresholds for 2 consecutive daily periods without symptom relief medication. That composite rule is clinically interpretable as a sustained response under the registry definition, but it also makes diary completeness and event-time handling important to analysis.

The trial also demonstrates why descriptive summaries and comparative inference need to be distinguished. Group medians and interquartile ranges describe observed timing, while the Gehan-Wilcoxon test addresses evidence of a distributional difference. Without a reported primary effect estimate and confidence interval, readers have less direct information about the magnitude and precision of the contrast than the group summaries alone might suggest.

The secondary complications outcome uses a different scale and method. Its participant counts and Fisher exact comparison do not answer the same question as a time-to-response analysis. A simple unadjusted re-calculation can help illustrate uncertainty, but it should remain secondary to the registry’s own analysis and cannot remedy missing reporting on the analysis plan or multiplicity.

Finally, planning calculations based on the observed effect are not retrospective proof of power. They depend on explicit assumptions about the effect to detect, allocation, significance level, and method. The record’s planning illustration helps show how sample-size requirements can change when the assumed effect is smaller, but it does not reveal the rationale or adequacy of the trial’s original design.

15. 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 does not post a primary effect estimate or confidence interval for the time-to-symptom-response comparison. The reported medians and interquartile ranges are useful descriptive summaries, but they do not convey the uncertainty in a direct between-group contrast. The primary test’s p-value is reported without a corresponding effect estimate in the registry record.

The endpoint depends on daily diary ratings for 32 symptoms and a response sustained across 2 consecutive diary periods, without symptom relief medication. Details of missing diary handling, censoring, and diary completeness are not reported in the registry record. Those omissions make it difficult to assess how incomplete observation could affect the time-to-event result.

The primary efficacy population is defined, but the registry provides limited detail about analysis populations for other outcomes. The safety summaries use different group-specific numbers at risk from the primary efficacy analysis. Readers should therefore avoid treating all outcome denominators as if they represented the same population.

The registry lists ability to perform all normal activities as a secondary outcome, but a numerical result for it is not reported. The record also does not report whether secondary analyses were adjusted for multiplicity, how outcomes were prioritized, or whether interim analyses or stopping rules were used. The sample-size illustrations are based on the observed complications effect and are not the trial’s design justification.

Finally, the posted complications comparison is a secondary result and the unadjusted re-calculation is compatible with no difference. Neither that result nor the primary non-significant comparison establishes equivalence. These reporting and precision limitations constrain conclusions to the analyses and outcomes for which numerical information is posted.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Efficacy and Safety of Nitazoxanide in the Treatment of Colds Due to Enterovirus/Rhinovirus Infection — NCT03605862.
• Registry record last updated 2022-04-14; status last verified 2022-04.
• Results first posted 2022-04-14.
• 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.

19. Record Summary

The registry describes a completed, randomized, triple-masked, parallel-group Phase III trial of nitazoxanide versus placebo for colds due to EV/RV infection. Overall enrollment was 1756. The primary efficacy analysis included 584 participants with laboratory-confirmed infection: 286 assigned to nitazoxanide and 298 assigned to placebo.

The primary endpoint was time from first dose to symptom response based on daily FLU-PRO ratings over follow-up of up to 21 days. The sponsor used a Gehan-Wilcoxon comparison, which did not establish a statistically significant difference. The posted complications analysis also did not establish a statistically significant difference. A result for ability to perform all normal activities is not reported in the registry record.

The registry does not report the primary contrast’s confidence interval, missing-data procedures, or a multiplicity strategy. These omissions limit assessment of precision and the broader secondary-outcome evidence.