Efficacy and Safety Study of Intranasal Administration of 100, 200, and 400 μg of Fluticasone Propionate Using a Novel Bi-directional Device: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of Intranasal Administration of 100, 200, and 400 μg of Fluticasone Propionate Using a Novel Bi-directional Device (NCT01624662), a randomized phase 3 study. The primary outcome is Change in 7-day Average Instantaneous Morning Diary Congestion/Obstruction Symptoms.

2. Clinical Question

The trial was designed to compare three dose levels with placebo in subjects with bilateral nasal polyposis and nasal congestion. The primary endpoint focuses on a participant-reported symptom, captured immediately before dosing in the morning. It therefore addresses the recorded level of congestion at a particular daily assessment time, rather than a broad measure of all nasal symptoms or a clinical judgment of polyp size.

The registry record identifies 323 participants enrolled overall. The primary endpoint analysis includes arm-specific participant counts, which differ from the overall enrollment. Those endpoint counts describe the participants included in that analysis; they should not be mistaken for the total number enrolled in the study. The outcome is a continuous score, and the posted arm estimates are least-squares means with standard errors.

3. Trial Design

This was a phase 3, randomized, double-blind, placebo-controlled, parallel-group, multicenter study sponsored by Optinose US Inc. The registry lists 323 participants enrolled and identifies bilateral nasal polyposis as the condition. The study status is completed. Its recorded start date is 2013-10-30, and its primary completion date is 2015-05-11.

During the 16-week double-blind treatment phase, participants received placebo or one of three OPN-375 doses: 100 mcg, 200 mcg, or 400 mcg twice daily. The study description identifies fluticasone propionate as the intervention and says it was administered using the Optinose device. Participants then entered an 8-week open-label extension in which all groups received OPN-375 400 mcg twice daily. The extension was intended to assess safety.

Random allocation and double masking are recorded, but the method used to generate or conceal the allocation is not reported in the registry record. The registry identifies a parallel-group model, meaning the randomized groups received their assigned double-blind treatment rather than switching between treatments during that phase. Further details about the multicenter sites, eligibility criteria beyond the stated population, adherence, and handling of treatment interruptions are not reported in the registry record.

The primary endpoint was assessed at Week 4 of the double-blind phase. The trial also posted a Week 16 congestion measure and other secondary outcome measures, including nasal symptoms, polyp assessments, and quality-of-life or sleep measures. The registry record does not report a complete statistical analysis plan or the original sample-size justification. The sample-size figures calculated from the observed effects are separate planning illustrations and do not describe the trial's original design assumptions.

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.

Double-Blind Treatment Phase (Wks 1-16)

Reasons for not completing this period:

Open-Label Extension Phase (Wks 17-24)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set includes subjects who received at least one dose of study drug and who had baseline assessments of polyp size (nasoendoscopy) and recorded morning nasal congestion/obstruction symptoms.

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 in 7-day Average Instantaneous Morning Diary Congestion/Obstruction Symptoms, measured over Baseline, Week 4 of the double-blind treatment phase.

The primary endpoint is the change in the 7-day average instantaneous morning diary congestion/obstruction score from baseline to Week 4 of the double-blind treatment phase. Participants recorded nasal symptoms electronically twice daily immediately before dosing. An instantaneous score refers to symptom severity at the time of scoring, in contrast to a reflective score that concerns symptoms over the previous 12 hours.

The scale ranges from 0 to 3. A score of 0 means no symptoms; 1 indicates mild symptoms that are clearly present but easily tolerated; 2 indicates moderate symptoms that are bothersome but tolerable; and 3 indicates severe symptoms that are hard to tolerate and interfere with activities or daily living. The outcome is continuous, and the registry reports least-squares mean changes with standard errors. A negative change indicates a lower score than baseline; in this symptom scale, that is a decrease in the reported severity of congestion/obstruction.

A daily diary can capture participants' own experience of symptoms over the treatment period, while a 7-day average reduces reliance on a single morning's report. The instantaneous morning measure also gives the endpoint a specific interpretation: it is not an all-day average, nor does it directly measure nasal polyp size. The registry describes the Full Analysis Set as participants who received at least one dose and had baseline polyp-size assessment by nasoendoscopy and recorded morning congestion/obstruction symptoms. Further details about the statistical model used to obtain the least-squares means are not reported in the registry record.

7. Results Posted in the Registry

• OPN-375 100 mcg: mean -0.59 versus -0.24 on control; difference -0.35 (95% CI -0.54 to -0.16), standardized effect d = -0.56; z-test p = <0.001.
• OPN-375 200 mcg: mean -0.68 versus -0.24 on control; difference -0.44 (95% CI -0.63 to -0.25), standardized effect d = -0.70; z-test p = <0.001.
• OPN-375 400 mcg: mean -0.62 versus -0.24 on control; difference -0.38 (95% CI -0.57 to -0.19), standardized effect d = -0.60; 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.

Nasal Congestion/Obstruction Score (7-day Instantaneous Morning)

• 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-375 100 mcg: mean -0.99 versus -0.48 on control; difference -0.51 (95% CI -0.76 to -0.26), standardized effect d = -0.66; z-test p = <0.001.
  • OPN-375 200 mcg: mean -0.93 versus -0.48 on control; difference -0.45 (95% CI -0.70 to -0.20), standardized effect d = -0.60; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 100 mcg 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-375 200 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Rhinorrhea Score (7-day Instantaneous Morning)

• 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-375 100 mcg: mean -1.00 versus -0.42 on control; difference -0.58 (95% CI -0.83 to -0.33), standardized effect d = -0.76; z-test p = <0.001.
  • OPN-375 200 mcg: mean -0.84 versus -0.42 on control; difference -0.42 (95% CI -0.67 to -0.17), standardized effect d = -0.56; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 100 mcg 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-375 200 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Facial Pain or Pressure Score (7-day Instantaneous Morning)

• 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-375 100 mcg: mean -0.85 versus -0.48 on control; difference -0.37 (95% CI -0.62 to -0.12), standardized effect d = -0.48; z-test p = 0.004.
  • OPN-375 200 mcg: mean -0.81 versus -0.48 on control; difference -0.33 (95% CI -0.58 to -0.08), standardized effect d = -0.44; z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for OPN-375 100 mcg 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-375 200 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists 14 secondary outcome measures spanning nasal symptoms, polyp assessments, and patient-reported quality-of-life or sleep measures. The posted secondary results represented in the comparison data include congestion at Week 16, rhinorrhea, and facial pain or pressure. Across those outcomes, the arm estimates generally show more negative mean changes in the active-dose groups than in placebo, consistent in direction with the Week 4 primary congestion comparison. The extent of that pattern varies across outcomes and dose comparisons; the primary endpoint should remain distinct from this broader group of secondary observations.

These measures provide related but not interchangeable information. Congestion and rhinorrhea are symptom scores, while facial pain or pressure captures a different reported symptom. Polyp scores and quality-of-life or sleep measures assess other aspects of the condition and its reported impact. Agreement across different measures can add context, but it does not make them repeated measurements of the same endpoint or prove that one outcome caused another.

The secondary comparisons carry less inferential weight because many outcomes were assessed, and the registry record does not report whether or how multiplicity was controlled. The p-values for the secondary comparisons are unadjusted recalculations, not identified as results from a sponsor-reported statistical analysis. When many hypotheses are examined, the chance of one or more apparently notable findings arising by chance can increase. Without a prespecified hierarchy or adjustment method reported in the registry, isolated secondary p-values are best regarded as exploratory evidence.

Participant counts also differ among the posted secondary outcomes. The registry record does not explain the reasons for missing outcome measurements or report the missing-data method used for each measure. Thus, the apparent direction across outcomes is informative as a descriptive pattern, but it cannot resolve whether missingness or outcome-selection choices influenced particular estimates. The secondary data complement the primary result; they do not replace it or establish a comprehensive treatment effect across all measured domains.

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

• Nasal Congestion/Obstruction Score (7-day Instantaneous Morning)
• Change in Rhinorrhea Score (7-day Instantaneous Morning)
• Facial Pain or Pressure Score (7-day Instantaneous Morning)
• Hyposmia Score (7-day Instantaneous Morning)
• Change in Total Nasal Polyp Score
• Polyp Grade of 0 in at Least One Nostril
• Sinonasal Outcome Test 22 (SNOT-22) Total Score
• MOS Sleep-R Score

9. Statistical Interpretation

10. Statistical Methods Explained

General: A randomized comparison is intended to make treatment groups comparable at the point of assignment, including for characteristics that may not be measured. Randomization does not guarantee identical groups, especially in a study of finite size, but it provides a basis for comparing outcomes according to assigned treatment. This trial is recorded as randomized, double-blind, and parallel-group. The registry record does not report the specific allocation-generation or concealment procedures.

What does a least-squares mean represent?

The primary outcome is reported as a least-squares mean, rather than simply being labelled an unadjusted arithmetic average. General: a least-squares mean is an estimate derived from a statistical model and may account for model terms or covariates. The model and any covariates used for the primary endpoint are not reported in the registry record, so the precise adjustment behind these estimates cannot be described from the registry alone. The accompanying standard error describes uncertainty in the estimated arm mean under the analysis that generated it; it is not a description of the spread of individual participants' scores.

How should the mean differences be read?

The mean difference is the estimated change in an active-dose group minus the estimated change in placebo. A negative value means the active-dose group's mean change is lower. Because lower values on this symptom scale mean less reported congestion, a negative comparison is in the direction of a larger decrease in the active group. General: a mean difference summarizes a contrast between group averages; it does not imply that each participant had a change equal to that contrast, nor does it describe the full distribution of individual outcomes.

The comparison estimates, intervals, and unadjusted p-values accompanying the posted means are recalculated simple unadjusted comparisons from summary statistics. They do not reproduce a model-based sponsor analysis. The recalculated standard deviations are approximated from the posted standard errors and sample sizes; the registry's reported arm estimates themselves are least-squares means with standard errors. These calculations are useful for a transparent comparison of posted summaries, but they should not be treated as a replacement for an analysis using participant-level data or the full trial model.

What does a confidence interval communicate?

General: a confidence interval gives a range of values compatible with the estimate under the method used to calculate it. A narrower interval indicates greater statistical precision than a wider interval, while an interval that includes zero leaves greater uncertainty about the direction of the contrast. The recalculated intervals for the Week 4 comparisons lie entirely below zero. The confidence level for the sponsor's own intervals is not reported in the registry record; the recalculated intervals are labelled 95%. A confidence interval is not a guarantee that the true effect lies within its endpoints, and it does not account for all uncertainty arising from study design, missing data, measurement, or analysis choices.

Why does over-dispersion matter?

General: over-dispersion occurs when observed variability is greater than a statistical model expects. If variability is underestimated, standard errors can be too small and intervals too narrow; if it is properly represented, uncertainty estimates are more credible. The primary endpoint is a continuous score, and the registry lists standard errors for arm estimates. It does not report an over-dispersion assessment or enough information to evaluate model fit. Accordingly, no conclusion about over-dispersion in the trial's primary analysis can be drawn from the registry record.

What is the role of p-values?

General: a p-value measures how incompatible the observed result is with a specified null model, assuming the statistical model and its assumptions apply. A small p-value is not the probability that the null hypothesis is true, and it does not measure the magnitude or clinical importance of an effect. The posted unadjusted p-values are below 0.001 for each primary comparison. Since the registry record does not state whether a multiplicity procedure was planned or applied, those individual values should not be interpreted as if the family of dose comparisons had been accounted for.

How do the secondary calculations differ?

The registry reports secondary outcomes on congestion, rhinorrhea, facial pain or pressure, and other measures. For some listed secondary contrasts, comparison estimates and unadjusted p-values are recalculated from the posted summary statistics. The registry does not list reported analyses for those secondary outcomes. General: a recalculated unadjusted result is a descriptive statistical comparison based on available group summaries, not necessarily the result of the trial's planned model. Differences in participant counts across outcomes can arise because outcome data are not available for every participant, but the reasons and missing-data procedures are not reported in the registry record.

The treatment design includes an open-label extension after the double-blind phase. Because all extension participants received the same OPN-375 dose and the phase was open-label, extension observations do not retain the original placebo-controlled comparison. They may contribute safety information, but they do not provide the same blinded randomized contrast as the primary treatment phase. Details of extension efficacy analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The Week 4 mean differences are estimated with intervals that are separated from zero. The 100 mcg comparison is -0.35 units, with an interval from -0.544 to -0.156; the 200 mcg comparison is -0.44, with an interval from -0.634 to -0.246; and the 400 mcg comparison is -0.38, with an interval from -0.574 to -0.186. Each interval is below zero, so the posted summaries indicate a lower mean change for each dose than for placebo. The width of each interval also shows that the exact size of the difference remains uncertain.

The interval endpoints are not extremely close together relative to the point estimates. They allow a range of plausible differences, rather than identifying one exact effect. In particular, statistical evidence that an average difference is not zero does not remove uncertainty about how large that difference is. The values are expressed in score units, but the registry record does not report a threshold for a clinically important difference, so the intervals cannot by themselves establish the practical importance of the estimated changes.

The confidence level for the comparison intervals is not stated in the registry record. The intervals are recalculated 95% intervals based on the posted summary statistics. Their calculation uses approximated variability derived from the reported standard errors and sample sizes, so they should be distinguished from an interval produced by the complete trial analysis model. The registry record does not report participant-level data, model details, or a sponsor-reported confidence interval for these comparisons.

General: precision is influenced by the amount of information in the data and by outcome variability. Larger samples and less variable measurements can yield more precise estimates, all else being equal. The primary endpoint counts range from 79 to 82 across the four arms, and the reported standard errors are 0.07 in each arm. These summaries describe the endpoint analysis, not all enrolled participants. Precision also does not address bias, missing-data assumptions, multiplicity, or the possibility that the analysis model is misspecified.

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 assumptions. The registry record does not report the original sample-size justification or the assumptions used to plan enrollment. The figures for these continuous outcomes are participants per arm, not total participants across arms and not total events.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect as the effect to detect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For example, for the primary 100 mcg comparison, planning for 100% of the observed effect gives 50 participants per arm for 80% power and 67 participants per arm for 90% power. Planning for 75% gives 89 participants per arm for 80% power and 119 participants per arm for 90% power. Planning for 50% gives 200 participants per arm for 80% power and 268 participants per arm for 90% power.

The 80% power column indicates the estimated number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is present and the calculation's assumptions hold. The 90% column describes the corresponding target for a 90% chance. Smaller effects require more participants to distinguish them from random variation, which is why the scenarios using smaller fractions of the observed effect show larger planned sample sizes. These calculations are planning scenarios, not observed power.

The plotted curve should be read in the same way: it illustrates how the planning estimate changes as the assumed effect changes. It does not state how likely the trial was to succeed, and it does not establish that the observed effect will recur in another study. Results depend on the assumed effect and calculation method, and the actual trial's design rationale is not reported in the registry record.

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 = -0.350; pooled standard deviation σ = 0.624.
2. n = 2 × (1.96 + 0.842)² × 0.624² / -0.350² = 49.9, rounded up to 50 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 <- -0.35                      # observed difference in means
sigma <- 0.624151908669309                     # 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(1624662)
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 = 50 (80% power), 67 (90% power)
 75% of observed effect: n per arm = 89 (80% power), 119 (90% power)
 50% of observed effect: n per arm = 200 (80% power), 268 (90% power)
power.t.test: 50.9 
Simulated power at n = 50 per arm: 0.794 (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

The trial compares three active doses with placebo for its primary endpoint and includes multiple secondary outcomes. This creates a multiplicity question: when several treatment comparisons or outcomes are tested, the chance of at least one apparently unusual result can rise if each test is interpreted separately. The primary unadjusted p-values are below 0.001, but the registry record does not report a multiplicity adjustment, a testing hierarchy, or a prespecified strategy for controlling the family-wise error rate or false discovery rate. It is therefore not possible to determine from the registry whether the displayed primary tests were intended to be interpreted jointly or individually.

The secondary results are also presented as unadjusted comparisons in the available summary data. The registry does not identify a confirmatory status or priority order for the secondary endpoints. Their results should consequently be treated as supportive or exploratory rather than as a set of independent confirmatory findings. No reported analyses are listed for the secondary outcomes in the registry record, and the original statistical analysis plan is not reported in the registry record.

The primary endpoint population is defined as the Full Analysis Set: participants who received at least one dose and had baseline polyp-size assessments and recorded morning congestion/obstruction symptoms. The arm counts for the Week 4 endpoint are 79 for placebo, 80 for OPN-375 100 mcg, 80 for OPN-375 200 mcg, and 82 for OPN-375 400 mcg. Counts for secondary outcomes differ. The registry record does not explain the reasons for these differences, report the amount or pattern of missing outcome data, or describe the method used to handle missingness.

General: missing-data methods matter because results can depend on why measurements are absent and on the assumptions used to represent them. Complete-case estimates may be affected if participants with missing outcomes differ systematically from those with observed outcomes. The registry record does not report sensitivity analyses or enough detail to assess robustness to missing-data assumptions. It also does not report interim analyses, stopping rules, or details of the prespecified statistical plan. These absences limit assessment of how the posted estimates relate to all planned analyses, without changing the numerical summaries themselves.

15. Safety Results

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

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: meningitis and sinusitis (1.3%), positional vertigo (1.2%).

During the double-blind phase, one participant in the placebo group and one participant in the OPN-375 400 mcg group were recorded as having a serious adverse event. No serious adverse events were recorded for the OPN-375 100 mcg or 200 mcg groups. In the open-label phase, no serious adverse events were recorded among the 299 participants at risk in the OPN-375 400 mcg group. These are counts during the listed study phases; they do not by themselves establish whether treatment caused an event.

The registry lists serious-event terms including Meningitis and Sinusitis at 1.3% and Positional vertigo at 1.2%. It does not specify in the summary which treatment group or phase those terms correspond to. Death counts are not reported in the registry record.

Safety counts require context. The double-blind groups were similar in size, while the open-label extension includes participants from the prior study groups receiving the same dose, and it lacks a placebo comparison. Serious events are uncommon in these group counts, so the observed numbers alone provide limited precision for comparing risk. The registry also reports other adverse events, but these totals do not establish causation or capture the full clinical context of individual events.

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

The posted primary results show decreases in the average morning congestion/obstruction score from baseline in all four randomized groups at Week 4. The active-dose group estimates are more negative than the placebo estimate, and the recalculated unadjusted comparisons are negative with intervals below zero. These findings describe average score differences in the analysis population and at the specified assessment time. They do not describe the response of every participant or establish that every individual experienced a decrease.

The numerical contrast is expressed in score units on a scale from 0 to 3. The registry record does not report a threshold for a clinically important change, so statistical separation from zero should not be equated with a judgment about practical or clinical importance. The outcome is a participant-reported symptom diary measure; it is not a direct measure of polyp size, and it does not represent every aspect of bilateral nasal polyposis.

The trial's randomized, double-blind, placebo-controlled phase provides a basis for comparing assigned groups. Still, interpretation depends on study conduct, the analysis model, missing-data handling, and multiplicity procedures. The registry does not report enough detail to evaluate all of these elements. The reported estimates and recalculated comparisons should therefore be read as evidence about the posted outcome summaries, not as a complete substitute for the trial's full analysis report.

The secondary outcomes offer context across other symptoms and measures, but their unadjusted status and the number of outcomes make isolated findings less conclusive. The open-label extension records safety after all groups moved to the same dose; it does not preserve the original blinded placebo contrast. Safety event counts describe what was recorded in the registry and do not establish that the study drug did or did not cause an event.

These results do not warrant medical advice or a treatment recommendation. They do not establish long-term effects beyond the recorded study phases, effects in populations not characterized in the registry, or comparative effectiveness against treatments other than placebo. The registry record does not report a threshold for interpreting symptom-score changes or the original sample-size justification. Those omissions limit the scope of conclusions that can be drawn from these summaries.

17. Why This Trial Matters Statistically

This trial illustrates several statistical features common to dose-ranging clinical studies. Multiple randomized doses allow investigators to compare several treatment groups with a common placebo group, but they also create multiplicity concerns. Interpreting each unadjusted comparison independently can overstate the strength of evidence if the full testing structure is not considered. The registry record does not describe a multiplicity plan, making that distinction important when reading the small posted p-values.

The primary endpoint is a repeated diary-based symptom measure summarized as a 7-day morning average. Such an endpoint gives a defined measurement time and a scale with an explicit interpretation, while also relying on participant reporting and adequate diary completion. The posted mean changes and standard errors communicate group averages and their uncertainty, but they cannot show the spread of individual responses or explain how missing diary entries were handled.

The registry results also illustrate the difference between reported trial analyses and recalculations from group summaries. Recalculated comparisons can make posted estimates easier to interpret as dose-versus-placebo contrasts, but they are not a substitute for the complete statistical model or participant-level analysis. Keeping those sources distinct helps readers avoid treating an approximation as the sponsor's original inferential analysis.

Finally, the study's double-blind placebo phase and open-label extension answer different questions. The randomized phase supports comparative interpretation across assigned groups, whereas the extension gives safety follow-up after participants receive the same open-label dose. The extension cannot be interpreted as an ongoing placebo-controlled efficacy comparison. Together, these design details show why endpoint definition, analysis population, multiplicity, missing data, and phase-specific comparisons all matter when assessing trial results.

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 offers limited detail about the statistical methods behind the primary least-squares means. It does not report the model specification, covariates, handling of repeated measurements, or assumptions used to produce the primary results. The comparison intervals and p-values described in this analysis are recalculated from posted summary statistics, with approximated variability, rather than derived from participant-level data. They are useful for orientation but cannot reproduce every feature of the trial analysis.

The registry does not report the original sample-size justification or the assumptions used to select the enrollment target. The displayed sample-size figures are planning illustrations based on observed effects, not evidence of the study's original power or design rationale. The record also does not report a multiplicity plan, interim-analysis details, or a complete analysis plan, limiting assessment of whether the posted tests align with prespecified hypotheses.

For the primary endpoint, the registry defines the Full Analysis Set, but does not report how missing diary observations were handled, how many measurements were missing, or why secondary endpoint sample sizes vary. It does not report sensitivity analyses addressing missing data. These gaps make it difficult to assess how robust the estimates are to assumptions about participants without recorded outcomes.

The primary endpoint is a self-reported symptom score at a specific morning assessment, and the record does not state a clinically important difference threshold. Therefore, statistical differences cannot be directly translated into a judgment of practical importance from these data alone. The open-label extension has no concurrent placebo group and should not be treated as a continuation of the blinded randomized efficacy comparison. Finally, the registry summary does not provide detailed site-level information or sufficient participant characteristics to assess how well the enrolled sample represents other populations.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of Intranasal Administration of 100, 200, and 400 μg of Fluticasone Propionate Using a Novel Bi-directional Device — NCT01624662.
• Registry record last updated 2018-12-05; status last verified 2018-01.
• Results first posted 2018-12-05.
• 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

NCT01624662 is a completed phase 3 randomized, double-blind, placebo-controlled, parallel-group, multicenter study sponsored by Optinose US Inc. It enrolled 323 participants with bilateral nasal polyposis. The double-blind phase compared OPN-375 100 mcg, 200 mcg, and 400 mcg twice daily with matching placebo for 16 weeks, followed by an 8-week open-label phase in which participants received OPN-375 400 mcg twice daily.

The primary endpoint was change in the 7-day average instantaneous morning diary congestion/obstruction score at Week 4. Posted mean changes were -0.24 for placebo and -0.59, -0.68, and -0.62 for the three active doses, respectively. Recalculated unadjusted dose-versus-placebo differences were negative, with intervals below zero. The registry record does not report the original sample-size justification, multiplicity approach, full statistical analysis plan, or missing-data procedures. Serious adverse event counts were low in the listed groups; the counts alone do not establish causation.