Study Evaluating the Efficacy and Safety of Intranasal Administration of OPN-375 in Subjects With Chronic Rhinosinusitis With or Without the Presence of Nasal Polyps: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Evaluating the Efficacy and Safety of Intranasal Administration of OPN-375 in Subjects With Chronic Rhinosinusitis With or Without the Presence of Nasal Polyps (NCT03781804), a randomized phase 3 study. The primary outcome is Change From Baseline in Symptoms as Measured by a Composite Score for Each Symptom of Nasal Congestion, Facial Pain or Pressure Sensation, and Nasal Discharge (Anterior and/or Posterior) at the End of Week 4.

2. Clinical Question

3. Trial Design

The registry record describes a Phase 3, randomized, double-blind, placebo-controlled, parallel-group, multicenter study. It evaluated intranasal OPN-375 in people with chronic rhinosinusitis, with or without nasal polyps. The study had three arms: OPN-375 186 μg BID, OPN-375 372 μg BID, and matching placebo BID. The planned treatment duration recorded for each arm was 24 weeks. The registry lists an enrollment of 332 and a completed status.

The primary endpoint was assessed at the end of Week 4, while the study treatment period was 24 weeks. The registry record also lists secondary outcomes covering symptoms, functioning, and sinus imaging. These include the SNOT-22 total score and subdomains, symptom diary measures, and imaging-based scores. The posted secondary results include outcomes at Week 12 and Week 24 or early termination, as well as the Lund-Mackay staging score. The record lists 41 outcome measures and 33 posted secondary outcomes.

The listed study start was 2018-11-27, and primary completion was 2022-01-19. The registry record does not report the trial's original sample-size justification, detailed eligibility criteria, or the full allocation procedure. It identifies the study as randomized and double-blind, but does not report further operational details about randomization or masking in the information. Those details should not be inferred from the design labels alone.

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

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 Change From Baseline in Symptoms as Measured by a Composite Score for Each Symptom of Nasal Congestion, Facial Pain or Pressure Sensation, and Nasal Discharge (Anterior and/or Posterior) at the End of Week 4, measured over 4 Weeks.

The primary endpoint measures change from baseline in the combined severity of nasal congestion, nasal discharge, and facial pain or pressure. Participants recorded symptom severity as an instantaneous AM diary score, meaning the rating concerned severity immediately before the scoring time. The baseline value was based on averaged scores over the last 7 days of the single-blind run-in period; the Week 4 value was averaged over 7 days of diary entries.

Each of the three symptom ratings ranges from 0, none, to 3, severe. The composite is their sum and ranges from 0 to 9. Thus, it summarizes several symptoms in one measure, rather than treating a change in any single symptom as the primary outcome. A negative change indicates a lower recorded composite score relative to baseline, given the described scale.

Diary-based symptom measures can capture participants’ reported experience over time. Combining the three specified symptoms creates a single endpoint for the trial’s primary comparison. The registry record reports least-squares mean changes and their standard errors for the full analysis set. It does not report a threshold for a clinically important change, so the numerical size of a score change alone does not establish how important participants would consider that change.

7. Results Posted in the Registry

• OPN-375 186 μg BID: mean -1.58 versus -0.62 on control; difference -0.96 (95% CI -1.41 to -0.51), standardized effect d = -0.57; z-test p = <0.001.
• OPN-375 372 μg BID: mean -1.60 versus -0.62 on control; difference -0.98 (95% CI -1.43 to -0.53), standardized effect d = -0.58; 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.

Change From Baseline to Defined Timepoint - Subject Symptoms and Functioning as Measured by the Sinonasal Outcome Test - 22-item (SNOT-22) Total Score and Sub Domains

• 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 errors.
• Result:
  • OPN-375 186 μg BID: mean -18.05 versus -10.16 on control; difference -7.89 (95% CI -12.62 to -3.16), standardized effect d = -0.47; z-test p = 0.001.
  • OPN-375 372 μg BID: mean -22.77 versus -10.16 on control; difference -12.61 (95% CI -17.37 to -7.85), standardized effect d = -0.76; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 186 μg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 372 μg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Symptoms as Measured by a Composite Score for Each Symptom of Nasal Congestion, Facial Pain or Pressure Sensation, and Nasal Discharge (Anterior and/or Posterior)

• 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 errors.
• Result:
  • OPN-375 186 μg BID: mean -1.89 versus -1.35 on control; difference -0.54 (95% CI -1.11 to 0.03), standardized effect d = -0.26; z-test p = 0.064.
  • OPN-375 372 μg BID: mean -2.18 versus -1.35 on control; difference -0.83 (95% CI -1.41 to -0.25), standardized effect d = -0.40; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OPN-375 186 μg BID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 372 μg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline to Week 24/ET in the Lund-Mackay Staging System Total Score

• 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 errors.
• Result:
  • OPN-375 186 μg BID: mean -0.40 versus 0.10 on control; difference -0.50 (95% CI -1.24 to 0.24), standardized effect d = -0.19; z-test p = 0.186.
  • OPN-375 372 μg BID: mean -0.46 versus 0.10 on control; difference -0.56 (95% CI -1.30 to 0.18), standardized effect d = -0.21; z-test p = 0.137.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OPN-375 186 μg BID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OPN-375 372 μg BID and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the view beyond the Week 4 symptom composite. The registry lists measures of sinonasal symptoms and functioning, individual diary symptoms, and imaging-based assessments. The posted results include the SNOT-22 at Week 24, the composite symptom measure at Week 12, and the Lund-Mackay staging score at Week 24 or early termination. These outcomes address related but distinct aspects of chronic rhinosinusitis, and they are measured on different scales or at different times.

Across the posted results, the active-treatment estimates are not uniformly accompanied by the same degree of statistical evidence. Some active-versus-placebo comparisons have confidence intervals that exclude zero, while others include zero. This is a broad description of the pattern rather than a replacement for the endpoint-specific estimates. In particular, secondary measures should be interpreted alongside the primary Week 4 result, not as though they were additional primary endpoints or exact replications of it.

Secondary results can add context about whether the pattern extends across related outcomes and later assessments. However, the registry record does not report a multiplicity adjustment or a complete testing hierarchy for these results. When many outcomes and timepoints are examined, unadjusted p-values carry less weight as confirmatory evidence because the chance of at least one apparently notable result can increase. The secondary findings therefore provide supporting descriptive context, while their uncertainty and testing context limit strong conclusions from any single result.

The registry record lists 33 posted secondary outcomes but does not report separate formal analyses in the summary information. This means that estimates and recalculated comparisons should be read as the posted numerical summaries, not as a fully documented account of every planned analysis. The record does not report whether all measured secondary outcomes were included in a prespecified analysis plan.

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

• Change From Baseline to Defined Timepoint - Subject Symptoms and Functioning as Measured by the Sinonasal Outcome Test - 22-item (SNOT-22) Total Score and Sub Domains
• Change From Baseline in Symptoms as Measured by a Composite Score for Each Symptom of Nasal Congestion, Facial Pain or Pressure Sensation, and Nasal Discharge (Anterior and/or Posterior)
• Change From Baseline in Nasal Congestion Measured by AM and PM Diary Symptom Scores
• Change in Sense of Smell Scores Measured by AM and PM Diary Symptom Scores
• Change From Baseline in Nasal Discharge (Anterior and/or Posterior) Measured by AM and PM Diary Symptom Scores
• Change in Facial Pain or Pressure Sensation Measured by AM and PM Diary Symptom Scores
• Change From Baseline to Week 24/Early Termination (ET) in the Average Percent of the Volume Opacified in the Ethmoid and Maxillary Sinuses Among Patient Populations
• Change From Baseline to Week 24/ET in the Lund-Mackay Staging System Total Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a continuous score, and the registry reports a least-squares mean for each study arm. A least-squares mean is an estimated group mean produced by a statistical model. In general, model-based means can account for specified features of a study; however, the registry record does not report the primary model specification or the variables included in it. The term therefore identifies the reported estimate, but does not by itself reveal how the model was constructed.

What does the change score represent?

Change from baseline compares a participant’s score at a later assessment with the baseline value defined for the endpoint. The primary measure uses average AM diary scores for each of three symptoms. The registry defines baseline using the last 7 days of the single-blind run-in period and the Week 4 value using a 7-day diary average. The reported arm estimates are least-squares mean changes from baseline, rather than raw scores at Week 4. Because each symptom ranges from 0 to 3 and the composite is the sum of three symptoms, a more negative change represents a larger decline in the recorded composite score relative to baseline.

How should the standard errors be read?

The registry reports standard errors beside the least-squares means. A standard error describes the statistical uncertainty in an estimated mean: it reflects how much the estimate would tend to vary across repeated samples under the analysis assumptions. It is not a measure of the spread of individual participants’ scores. Standard errors are useful for understanding the precision of group estimates, but a standard error alone is not a full account of uncertainty about the treatment comparison. Confidence intervals for the comparisons give a range of estimates compatible with the data and the stated statistical procedure.

What does a comparison with placebo show?

The posted comparisons are expressed as mean differences between an active-treatment arm and placebo. A negative estimate means that the active-treatment arm’s reported change was more negative than the placebo arm’s reported change. The comparison estimate should be considered with its confidence interval and p-value. The p-value addresses how compatible the observed data are with a specified null hypothesis under the analysis assumptions; it is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect.

The comparison calculations labeled recalculated are simple, unadjusted re-calculations from the posted summary statistics. They can provide a check on the direction and approximate size of the arm contrast, but do not reproduce a full participant-level model. The registry record does not report a discrepancy between these calculations and the posted summary information. The sponsor’s own analysis would take precedence if a discrepancy were flagged, but no such discrepancy is recorded for this trial.

Why does analysis population matter?

The primary endpoint identifies the full analysis set as its population. The registry record does not provide a full definition of that set or explain which randomized participants were included or excluded. Arm-level counts can differ across outcomes because the posted results refer to different measures and timepoints. Such counts should not be treated as interchangeable. The registry record does not report enough detail to attribute those differences to a particular reason.

More generally, missing outcome observations can affect the analysis, especially if missingness is related to participants’ health, treatment, or measured outcomes. Statistical methods make assumptions about how missing observations relate to observed data. The registry record does not report the primary missing-data method, the amount or pattern of missingness, or sensitivity analyses for missing data. Those absences limit assessment of how robust the estimates are to incomplete follow-up.

What can be concluded from the p-values?

The primary comparison p-values are reported as unadjusted. In general, an unadjusted p-value addresses an individual comparison without correcting for the number of hypotheses tested. When a study reports multiple outcomes, timepoints, or treatment contrasts, the chance of finding at least one small p-value can increase if many tests are considered together. The registry record does not report the complete prespecified testing hierarchy or a multiplicity-control procedure. For that reason, the primary result and the many secondary results should not be treated as if every comparison had the same confirmatory status.

General statistical interpretation also distinguishes statistical evidence from clinical importance. A small p-value does not tell how large or meaningful a difference is, while an estimate’s confidence interval describes uncertainty about its magnitude under the analysis. The registry record does not state a threshold for a clinically important change on the composite scale. Therefore, statistical evidence in the Week 4 contrast should be read alongside the score’s construction, the interval of plausible effects, and the limitations in the reported methods.

11. Confidence Intervals and Precision

The Week 4 comparison for OPN-375 186 μg BID versus placebo is -0.96, with a confidence interval from -1.406 to -0.514. The comparison for OPN-375 372 μg BID versus placebo is -0.98, with a confidence interval from -1.429 to -0.531. Both intervals lie below zero. In general, a confidence interval describes a range of values compatible with the observed data under the analysis assumptions and the method used to construct the interval. It is not a guarantee that the true effect lies within the interval, nor does it describe the range of individual participant outcomes.

The interval widths convey uncertainty: narrower intervals indicate more precision than wider intervals, for estimates on the same scale and under comparable methods. The Week 4 intervals still permit a range of possible comparison magnitudes, so the point estimates should not be treated as exact effects. The posted standard errors for the arm-level least-squares means are 0.161 for placebo and 0.161 for the 186 μg arm, and 0.163 for the 372 μg arm. These describe uncertainty in each arm mean, while the comparison intervals directly address uncertainty in the active-treatment versus placebo contrasts.

Precision is not the same as importance. The registry record does not report a clinical-importance threshold for the composite score, so the intervals cannot be classified against such a threshold from the record alone. They also reflect the reported analysis, whose model details and missing-data handling are not reported in the registry record. The estimates are most informative when read with the endpoint definition and those reporting limitations in mind.

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 observed effects, not the trial’s original design justification. For continuous outcomes such as this composite score, the listed figures are participants per arm, not total participants. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design that would have an 80% chance of detecting the assumed effect at the stated significance level, if the planning assumptions hold. The 90% power column describes the corresponding illustration for a 90% chance. These are design calculations, not probabilities that the trial’s result is correct, and they are not observed power. The figures are conditional on the assumed effect and statistical model used for the illustration.

Rows for planning for 100%, 75%, or 50% of the observed effect show how the assumed effect size changes the illustrative sample-size requirement. Smaller effects need more participants to detect them with the same power, so the figures rise as the assumed fraction of the observed effect becomes smaller. A curve based on these values should be read as a planning relationship between assumed effect size and participants per arm, not as a projection of what would happen in a future study. These calculations do not account for every possible design feature, such as attrition or analysis choices, unless explicitly included in the stated assumptions.

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 = -0.960; pooled standard deviation σ = 1.673.
2. n = 2 × (1.96 + 0.842)² × 1.673² / -0.960² = 47.7, rounded up to 48 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 <- -0.96                      # observed difference in means
sigma <- 1.67316108011154                     # 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(3781804)
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 = 48 (80% power), 64 (90% power)
 75% of observed effect: n per arm = 85 (80% power), 114 (90% power)
 50% of observed effect: n per arm = 191 (80% power), 256 (90% power)
power.t.test: 48.7 
Simulated power at n = 48 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, timepoints, treatment comparisons, or related hypotheses. In general, if each test is considered separately without adjustment, the chance of at least one small p-value across a collection of tests can be greater than the chance for a single test. A multiplicity strategy may define a hierarchy, allocate significance levels, or use another method to control error rates. The registry record does not report a multiplicity adjustment, testing hierarchy, or detailed statistical analysis plan for the posted outcomes. The primary endpoint is identified, but the record does not provide enough information to determine how the broader set of secondary hypotheses was handled.

The listed p-values for the comparisons are unadjusted. They can be read as evidence for individual comparisons under their respective analyses, but not as proof that the entire family of outcomes has been evaluated with a controlled error rate. This distinction is particularly relevant to the secondary outcomes, where measures and timepoints vary. The primary result is the central comparison, while secondary findings should be considered in their wider testing context.

Missing data are another important consideration. The primary analysis population is called the full analysis set, but its exact definition is not reported in the registry record. The record does not report the number or pattern of missing outcome values, the method used to handle them, or sensitivity analyses testing alternative assumptions. In general, complete-case analyses, model-based methods, and imputation methods rely on different assumptions about why observations are missing. Without the stated approach and missingness information, it is not possible to assess how those choices might affect the estimates.

The numbers of participants included in posted outcome summaries vary by measure and timepoint. The registry record does not explain those variations, and they should not be assumed to indicate a particular form of withdrawal, missingness, or analysis exclusion. These reporting gaps do not change the reported estimates, but they limit independent assessment of the analysis and its robustness.

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% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 pneumonia (1.8%), alcoholic pancreatitis (0.9%), ankle fracture (0.9%), pyrexia (0.9%), pneumonia staphylococcal (0.9%).

The registry lists serious adverse events for each treatment group as counts among participants at risk: 1 for OPN-375 186 μg BID, 2 for OPN-375 372 μg BID, and 3 for placebo. The corresponding groups at risk are 111, 109, and 112. Deaths are listed as 0 in each group. These are descriptive registry counts and should be read as reported, rather than used to infer comparative risk without a prespecified safety analysis and its methods.

The record lists COVID-19 pneumonia at 1.8% and alcoholic pancreatitis, ankle fracture, pyrexia, pneumonia staphylococcal, and uterine leiomyoma at 0.9% each among the top serious terms. It does not provide further context for each term in the information. The registry also records other adverse events affecting 37 participants in each active-treatment group and 14 in placebo, with the corresponding at-risk counts of 111, 109, and 112. These are not the same category as serious adverse events.

Counts alone do not establish that a treatment caused an event, and the registry record does not report a comparative safety model or adjusted estimates. They should be understood as descriptive reporting over the study rather than as a complete evaluation of safety.

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

The posted primary result describes average change in a three-symptom composite at the end of Week 4. Both active-treatment arms had more negative mean changes than placebo, and both reported comparison confidence intervals lay below zero. The results therefore show a difference in the measured average change between each active arm and placebo in the posted primary analysis. They do not describe how every participant responded, and they do not establish the effect on every symptom separately.

The composite has a defined scale, with each symptom rated from 0, none, to 3, severe, and the three ratings summed to a range of 0 to 9. That construction makes the direction of the change interpretable as a decline in the recorded symptom score. The registry record does not report a threshold for a clinically important difference, so statistical evidence alone cannot say whether the observed magnitude would be meaningful to participants or clinicians.

The result also should not be extended beyond the study’s measured population and conditions. The registry describes chronic rhinosinusitis with or without nasal polyps, but does not report detailed eligibility criteria in the information. Secondary endpoints address other domains and timepoints, and the record’s missing multiplicity and analysis details limit how strongly they can corroborate the primary result. The posted safety counts are descriptive and do not establish comparative causation.

More broadly, a trial estimate is an average with uncertainty. It is not an individual prediction, and a confidence interval is not a statement about the range of individual outcomes. The posted results support a statistical description of the Week 4 endpoint under the reported analysis; they do not settle every question about durability, patient-important change, or outcomes not represented by the recorded measures.

17. Why This Trial Matters Statistically

This study is statistically informative because it places two active dose groups alongside a matching placebo group in a randomized, double-blind, parallel design. Randomization and masking are design features intended to reduce certain sources of bias, although the registry record does not report the operational details needed to assess how those features were implemented. The primary endpoint is clearly defined as a composite of three diary-based symptoms at a specified assessment time, allowing the reported contrast to be understood in relation to a stated score and baseline period.

The result also illustrates why estimates, confidence intervals, and p-values answer different questions. The point estimates describe the magnitude and direction of the group contrasts; the intervals convey uncertainty about those contrasts; and the p-values summarize compatibility with a null hypothesis under the analysis assumptions. Considering these together is more informative than relying on a p-value alone. The secondary measures extend the outcome picture, while also illustrating why unadjusted findings across many outcomes require caution.

Finally, the posted planning illustrations show the dependence of sample-size requirements on the effect assumed for detection. They are not a reconstruction of the trial’s original design, and they do not represent observed power. Distinguishing an effect-based planning exercise from the actual design rationale is essential when interpreting enrollment and the precision of the results. The registry record’s missing details about analysis plans, missing data, and multiplicity remain relevant limits on how fully the statistical evidence can be assessed.

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 does not report the original sample-size justification or the detailed assumptions used to plan the study. The planning illustrations are based on observed effects and stated assumptions, so they should not be treated as evidence that the study was designed around those values. The record identifies the primary endpoint population as the full analysis set but does not define that population in detail.

The primary model specification, covariate adjustments, randomization procedure, and handling of missing observations are not reported in the registry information. The record also does not report a multiplicity strategy or the complete analysis plan for the secondary outcomes. These gaps make it harder to assess the assumptions behind the least-squares means and to determine how robust the results are to alternative analysis choices.

The Week 4 endpoint combines three symptom scores, which gives a single primary measure but does not show the separate contribution of each symptom in the primary result. The registry record does not state a clinically important difference threshold for the composite. Secondary outcomes cover other symptoms, functioning, and imaging, but their unadjusted comparisons should not be treated as confirmatory evidence without further information about testing plans.

Safety reporting is also limited to the counts and top serious terms listed in the registry record. The record does not provide a comparative safety analysis in the information. These limits do not negate the posted findings, but they constrain conclusions about clinical importance, robustness, and the broader pattern of benefits and harms.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Evaluating the Efficacy and Safety of Intranasal Administration of OPN-375 in Subjects With Chronic Rhinosinusitis With or Without the Presence of Nasal Polyps — NCT03781804.
• Registry record last updated 2024-05-29; status last verified 2024-05.
• Results first posted 2023-09-18.
• 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

The registry record identifies a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group, multicenter study of intranasal OPN-375 in chronic rhinosinusitis, with or without nasal polyps. The study compared 186 μg BID and 372 μg BID with matching placebo over 24 weeks and lists an enrollment of 332.

The primary outcome was change from baseline in a composite of nasal congestion, nasal discharge, and facial pain or pressure at the end of Week 4. The posted least-squares mean changes were -1.58, -1.6, and -0.62 for the 186 μg, 372 μg, and placebo groups, respectively. Both active-versus-placebo comparisons were reported with unadjusted p-values of <0.001.

The record also includes secondary symptom, functioning, and imaging outcomes, plus descriptive adverse-event counts. Details of the original sample-size rationale, model specification, missing-data handling, and multiplicity procedure are not reported in the registry record.