Controlled Clinical Study of Dupilumab in Patients With Nasal Polyps: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Controlled Clinical Study of Dupilumab in Patients With Nasal Polyps (NCT02898454), a randomized phase 3 study. The primary outcome is Change From Baseline at Week 24 in Nasal Congestion/Obstruction Symptom Severity Score.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group Phase 3 study. The registry lists quadruple masking, but does not identify in the posted record which roles were masked. The study enrolled 448 participants with bilateral nasal polyps and evaluated dupilumab alongside stable-dose intranasal mometasone furoate nasal spray.

Participants were assigned to placebo, dupilumab 300 mg every 2 weeks through Week 52, or dupilumab 300 mg every 2 weeks through Week 24 followed by every-4-week dosing through Week 52. For the latter schedule, matched placebo injections were alternated with dupilumab after Week 24. For the primary Week 24 assessment, the registry says participants assigned to dupilumab had received the every-2-week regimen and were analyzed as a pooled population. The posted primary comparison has 153 participants in the placebo group and 295 in the pooled dupilumab group.

The study’s overall duration and primary endpoint timing should be distinguished: the study was described as 52 weeks, while the primary endpoint was measured at Week 24. The registry’s objectives also covered nasal polyp scores, sinus imaging, symptoms, smell, participant-reported outcomes, quality of life, treatment with systemic corticosteroids or surgery, and safety. The study status is completed. Details such as the sequence-generation procedure, allocation concealment, and the specific responsibilities covered by masking are 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.

Before assignment: Randomization was stratified according to asthma and/or non-steroidal anti-inflammatory drug exacerbated respiratory disease (NSAID-ERD) history (yes/no), prior nasal polyps (NP) surgery (yes or not), and country.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis was performed on intent-to-treat (ITT) population which included all randomized participants who were analyzed according to the treatment group allocated by randomization. Data for this outcome measure was planned to be analyzed for the combined population of participants who received Dupilumab.

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: Analysis was performed on randomized population which included any participant who was allocated to a randomized treatment regardless of whether any treatment kit was used.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline at Week 24 in Nasal Congestion/Obstruction Symptom Severity Score, measured over Baseline, Week 24.

The primary endpoint is change from baseline at Week 24 in nasal congestion or obstruction symptom severity. Participants rated symptoms daily using an electronic diary on a scale from 0 to 3: 0 means no symptoms, 1 mild, 2 moderate, and 3 severe. Higher scores indicate greater severity. The posted endpoint is a mean change, so a negative change represents a reduction in the measured score from baseline.

A participant-rated symptom scale is useful because congestion and obstruction are experienced symptoms that may not be fully represented by an examination or imaging measure alone. Daily entries can also capture symptoms across time rather than relying only on a rating made at a clinic visit. These are general reasons to use diary-based symptom measures; they do not establish that any particular scale captures every aspect of a participant’s experience.

The endpoint is not a direct measure of nasal polyp size, sinus opacification, smell, or quality of life. Those outcomes appear elsewhere among the study’s objectives and secondary measures. The registry reports least-squares means and standard errors for the primary endpoint, with an analysis of covariance model. It identifies the analysis population as intent-to-treat, meaning randomized participants were analyzed according to their assigned group. The endpoint description does not give the full model specification, such as all covariates, in the registry record.

7. Results Posted in the Registry

• Dupilumab 300 mg (24 Weeks Pooled Arm): mean -1.25 versus -0.38 on control; difference -0.87 (95% CI -1.05 to -0.69), standardized effect d = -0.89; 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 at Week 24 in Opacification of Sinuses Measured by Lund Mackay (LMK) 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:
  • Dupilumab 300 mg (24 Weeks Pooled Arm): mean -5.21 versus -0.09 on control; difference -5.12 (95% CI -5.89 to -4.35), standardized effect d = -1.28; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Dupilumab 300 mg (24 Weeks Pooled Arm) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline at Week 24 in Total Symptom Score (TSS)

• 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:
  • Dupilumab 300 mg (24 Weeks Pooled Arm): mean -3.45 versus -1.00 on control; difference -2.45 (95% CI -2.94 to -1.96), standardized effect d = -0.96; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Dupilumab 300 mg (24 Weeks Pooled Arm) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline at Week 24 in the University of Pennsylvania Smell Identification Test (UPSIT) 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:
  • Dupilumab 300 mg (24 Weeks Pooled Arm): mean 9.71 versus -0.81 on control; difference 10.52 (95% CI 8.75 to 12.29), standardized effect d = 1.14; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dupilumab 300 mg (24 Weeks Pooled Arm) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary results presented alongside the primary endpoint show a broader pattern across sinus imaging, total symptom score, and smell identification. For each of these posted Week 24 comparisons, the registry’s reported ANCOVA results favor a greater mean change in the dupilumab group than in the placebo group, with reported confidence intervals that do not include zero and p-values below < 0.001. The tables contain the endpoint-specific estimates, so this overview does not repeat them.

These measures complement rather than duplicate the primary symptom diary. Sinus opacification is an imaging measure, total symptom score represents a wider symptom construct, and the smell identification test assesses a different function. Consistency across distinct measures can help characterize the pattern of results, but does not make the endpoints equivalent or demonstrate that every outcome changed to the same degree.

The registry lists many further secondary measures and objectives, including participant-rated smell severity, quality of life, Week 52 outcomes, treatment with systemic corticosteroids or surgery, and safety. The presence of those objectives does not mean their results are all summarized in this discussion. The posted secondary result set contains 41 outcome measures, and individual tables should be consulted for the measures and analyses they report.

Secondary findings generally carry less confirmatory weight than a prespecified primary analysis, especially when many outcomes or time points are examined. Testing multiple outcomes increases the chance that some results will appear statistically notable by chance if no adjustment is made. The registry record does not report whether multiplicity adjustments were applied to the secondary analyses. Accordingly, the secondary pattern provides context for the primary finding, but should not be treated as a collection of independently definitive tests.

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

• Change From Baseline at Week 24 in Opacification of Sinuses Measured by Lund Mackay (LMK) Score
• Change From Baseline at Week 24 in Total Symptom Score (TSS)
• Change From Baseline at Week 24 in the University of Pennsylvania Smell Identification Test (UPSIT) Score
• Change From Baseline at Week 24 in Severity of Decreased/Loss of Smell as Assessed by Participant Daily
• Change From Baseline at Week 24 in 22-item Sino-nasal Outcome Test (SNOT-22) Scores
• Change From Baseline at Week 52 in Nasal Polyp Score
• Change From Baseline at Week 52 in Nasal Congestion/Obstruction Symptom Severity Score
• Change From Baseline at Week 52 in 22-item Sino-nasal Outcome Test Scores

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports an analysis of covariance, or ANCOVA, for the primary endpoint and presents least-squares means, standard errors, a least-squares mean difference, a confidence interval, and a p-value. These quantities address related but different questions. The posted summary also permits a simple unadjusted recalculation from the group-level summaries; that calculation is not a substitute for the registry’s model-based analysis.

What does ANCOVA do?

ANCOVA compares groups on an outcome while accounting for specified covariates in a regression model. In a randomized study, adjustment can improve precision when the covariates are prognostic and can account for baseline values when those are included in the model. This is a general explanation of the method. The registry says ANCOVA was used but does not report the complete covariate list or other detailed model specifications, so those cannot be described.

The reported least-squares means are model-based group estimates, rather than necessarily the raw arithmetic averages of all observed changes. They represent the fitted group means under the model’s adjustment approach. The registry reports standard errors for the arm-level estimates. A standard error summarizes how much an estimate would vary across repeated samples under the model and assumptions; it is not the spread of individual participants’ scores.

What does the difference represent?

The least-squares mean difference is the estimated contrast between the pooled dupilumab group and placebo group. For this symptom scale, a negative difference corresponds to a more negative mean change in the dupilumab group. The registry reports the adjusted contrast as -0.87. Its 95% confidence interval runs from -1.03 to -0.71. The interval expresses the uncertainty around the estimated contrast under the analysis model. It is not a range that contains 95% of individual participant outcomes.

The posted results also include a recalculated comparison based on summary statistics. That is a simple, unadjusted calculation and uses an approximate pooled standard deviation derived from the posted standard errors. It reports a mean difference of -0.87 and an unadjusted p-value of p < 0.001. Because this calculation does not reproduce the ANCOVA adjustment, it answers a less model-specific question. The sponsor’s reported ANCOVA result remains the trial’s reported analysis; the registry does not flag a discrepancy between it and the recalculation.

How should the p-value be read?

The sponsor’s reported p-value is p < 0.001. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, given the statistical model. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of the estimated difference. Here, the reported hypothesis test is identified as a superiority analysis, and the estimate and confidence interval provide the direction and scale of the contrast alongside the test result.

The unadjusted recalculation’s p-value is reported as p < 0.001. Its formatting differs from the sponsor’s p-value, in part because the two results come from different analytical approaches. The sponsor’s ANCOVA incorporates the model used for the trial’s reported estimate. A p-value should therefore be interpreted together with its method, the confidence interval, and the endpoint definition rather than as a stand-alone ranking.

Why can an adjusted estimate differ from a simple recalculation?

A simple recalculation uses the published group summaries and does not have access to participant-level data or the full fitted model. ANCOVA may use baseline measurements and other covariates, if specified, and can therefore produce a model-adjusted estimate and uncertainty that are not identical to a calculation from arm summaries. The posted primary point estimates are similar, but the summary calculation should not be treated as a reconstruction of the complete trial analysis.

General statistical considerations also apply to a daily symptom score. The scale is bounded and has ordered response categories. Treating a change score with a continuous-outcome model can be useful for estimating an average contrast, but model adequacy depends on the observed data and assumptions. The registry identifies the outcome as a score and the method as ANCOVA; diagnostic checks and alternative model analyses are not reported in the registry record.

What cannot be inferred from the method description?

The registry’s concise record does not specify the covariates in the primary ANCOVA, the approach to missing diary entries, the assumptions used for missing endpoint data, or whether sensitivity analyses were conducted. It also does not report the trial’s original sample-size justification or detailed statistical analysis plan. These omissions do not change the values posted for the primary analysis, but they limit independent assessment of how modeling choices and incomplete data may affect the result.

11. Confidence Intervals and Precision

The primary adjusted estimate is a least-squares mean difference of -0.87, with a 95% confidence interval from -1.03 to -0.71. The interval excludes zero and remains on the negative side of the scale, consistent with the direction of the posted group means. Its width conveys uncertainty about the average contrast: values within the interval are more compatible with the data and model than values far outside it, though the interval is not a list of possible individual responses.

A confidence interval is generally constructed by a method that, over repeated samples under the model’s assumptions, would cover the target quantity at the stated rate. It does not mean that there is a 95% probability that this particular fixed effect lies inside this particular interval. The interval also does not address sources of uncertainty not represented by the model, such as limitations in measurement, missing-data assumptions, or how well the study population represents other settings.

The posted arm-level standard errors are 0.07 for placebo and 0.06 for the pooled dupilumab group. These describe precision of the estimated arm means, not the amount of variation among participants. The registry’s adjusted confidence interval is the more direct summary of precision for the between-group contrast. The recalculated interval is based on an unadjusted summary-statistic approach and should be distinguished from the sponsor’s ANCOVA interval.

Precision is not the same as importance. A relatively narrow interval can indicate a more precisely estimated average contrast, but does not establish how participants value a change on the scale or whether it is meaningful in a particular context. The registry record does not provide a threshold for a clinically important difference for this endpoint.

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 table and curve are planning illustrations based on the observed effect, not the trial’s original design calculation. For this continuous endpoint, the displayed figures are participants per arm, not total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the model assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. These are hypothetical design calculations, not descriptions of what happened in the completed trial.

Rows show planning for 100%, 75%, and 50% of the observed effect. The smaller the effect a future study aims to detect, the more participants it generally needs under otherwise unchanged assumptions. The displayed values should be read as scenario-specific illustrations, not as a recommended sample size: real planning also depends on the endpoint, expected variability, allocation, significance level, missing data, and other design choices. The table does not establish the power of the completed study; this is not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.870; pooled standard deviation σ = 0.978.
2. n = 2 × (1.96 + 0.842)² × 0.978² / -0.870² = 19.8, rounded up to 20 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 <- -0.87                      # observed difference in means
sigma <- 0.977530520895645                     # 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(2898454)
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 = 20 (80% power), 27 (90% power)
 75% of observed effect: n per arm = 36 (80% power), 48 (90% power)
 50% of observed effect: n per arm = 80 (80% power), 107 (90% power)
power.t.test: 20.8 
Simulated power at n = 20 per arm: 0.783 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is ANCOVA and gives a least-squares mean difference of -0.87, with a 95% confidence interval from -1.03 to -0.71 and p < 0.001. This is the analysis reported for the trial. The simple recalculation shown alongside it uses the posted group summaries rather than participant-level data or the complete ANCOVA model; it gives a mean difference of -0.87 and p < 0.001.

The matching displayed point estimate does not make the two analyses interchangeable. The sponsor’s analysis is adjusted according to the trial’s model, while the recalculation is unadjusted and depends on summary-statistic approximations. Their confidence intervals and p-values should therefore be understood as products of different methods, not as competing versions of the same model fit.

The registry does not flag a discrepancy between the recalculation and the reported analysis. The sponsor’s result is the appropriate reference for what the trial’s reported ANCOVA concluded. The recalculation is useful as a transparent, limited cross-check of the contrast in the posted summaries, but cannot verify model assumptions or reproduce analyses that require participant-level records.

15. Multiplicity, Missing Data and Analysis Populations

The registry presents a primary endpoint analysis and numerous additional outcomes. It describes nasal congestion or obstruction symptom severity and nasal polyp score among the primary objectives, and identifies sinus CT opacification as a co-primary objective for Japanese participants. It also lists secondary objectives across symptoms, smell, imaging, quality of life, treatment with systemic corticosteroids or surgery, different dosing schedules, subgroups, and safety. This breadth makes it important to know how the testing strategy was planned.

When multiple hypotheses are tested, the chance of at least one false-positive result can rise if each test is interpreted using the same threshold without adjustment. Statistical procedures for multiplicity can control or otherwise address this issue, but they need to be understood in the context of which hypotheses were prespecified, their hierarchy, and the population to which each applies. The multiplicity strategy and any adjustment for the primary or secondary outcomes are not reported in the registry record. The p-values for secondary outcomes should therefore be read with that limitation in mind.

The primary population is described as intent-to-treat: all randomized participants were analyzed according to their assigned treatment group. This preserves the randomized comparison in the stated analysis population. The registry’s primary endpoint description is truncated after noting the combined population, so further details about analysis sets cannot be established from this record alone.

Missing-data handling is also not reported in the registry record. The endpoint depends on daily electronic diary entries, but the record does not say how missing diary days were summarized, how participants without a Week 24 assessment were handled, or what assumptions were made about data that were not observed. The record does not describe sensitivity analyses for those assumptions. This matters because an analysis can be affected if missingness relates to symptoms, treatment experience, or other factors.

The statistical analysis plan, full model covariates, interim analyses, and original sample-size rationale are not reported in the registry record. Their absence does not invalidate the posted estimates, but limits assessment of prespecification and robustness. The posted results should be interpreted as the analyses described in the registry, with these unreported details left unresolved.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: nasal polyps (2.0%), facial bones fracture (1.3%), abdominal pain upper (0.7%), pancreatitis (0.7%), pyrexia (0.7%).

The registry lists serious adverse events for three treatment groups. Serious events affected 16 of 150 participants in the placebo group, 12 of 148 in the dupilumab group that changed from every-2-week to every-4-week dosing, and 8 of 149 in the dupilumab group that continued every-2-week dosing. The record lists one death in the group that changed dosing and none in the other two groups.

These are counts of participants with at least one serious adverse event as presented in the registry, not a comparison adjusted for follow-up time or participant characteristics. The number of participants at risk differs from the primary endpoint group counts, so the safety figures should be read with their own denominators. The posted record also identifies nasal polyps, facial bones fracture, upper abdominal pain, pancreatitis, pyrexia, and eosinophilic granulomatosis with polyangiitis among the leading serious-event terms, with the listed percentages in the safety table.

The registry figures alone do not establish whether an event was caused by treatment, how long participants were followed for safety, or how event severity and relatedness were adjudicated. Those details are not reported in the registry record. Counts should be interpreted descriptively and should not be used to infer comparative risk without fuller context.

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

The posted result describes an average Week 24 difference in change on a participant-rated nasal congestion or obstruction scale between two randomized groups receiving the same background nasal corticosteroid therapy. The adjusted estimate is negative, and its confidence interval lies below zero. In the context of the scale, that pattern corresponds to a larger average reduction in symptom severity in the pooled dupilumab group than in the placebo group.

This finding is specific to the study population, the treatment regimens, the background therapy, the endpoint definition, and the Week 24 assessment. It does not directly answer what happened at every other time point, how the two later dupilumab schedules compare, or how an individual participant would respond. At Week 24, the dupilumab groups were pooled because the registry states they had received the same every-2-week regimen up to that point.

The estimate is not a measure of nasal polyp size, sinus imaging, smell, or quality of life. Those outcomes are distinct, even when they provide related information about the condition. The registry’s secondary results can add context, but do not replace the primary endpoint or resolve the limits of its measurement.

Statistical evidence also is not the same as clinical importance. The confidence interval summarizes uncertainty under the reported model; it does not say whether participants would consider the observed scale difference important. The registry record does not provide a threshold for clinically meaningful change, individual responder results for this endpoint, or enough information to translate the group mean into a prediction for a particular person.

Finally, the result concerns the comparison as studied: dupilumab added to stable intranasal mometasone furoate versus placebo added to that background therapy. It should not be generalized from this registry summary to other treatment settings or populations without evidence that supports doing so. No treatment recommendation follows from the statistical description alone.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and treatment contrast matter as much as the headline estimate. The primary measure is a daily participant-rated symptom score, while the randomized comparison holds background intranasal corticosteroid therapy in common. The result therefore addresses an add-on-treatment contrast for a specific symptom measure, not a broad comparison of treatment with no care.

It also demonstrates how adjusted analyses and summary-statistic recalculations answer related but not identical questions. The registry reports an ANCOVA estimate with a confidence interval and p-value. A separate unadjusted calculation from the posted summaries is a useful arithmetic cross-check, but it cannot reproduce the model or its use of participant-level information. Readers need to distinguish the reported trial analysis from a recalculation rather than treating every number as interchangeable.

The trial’s multiple objectives highlight the importance of endpoint hierarchy and multiplicity. Nasal symptoms, polyp scores, imaging, smell, and quality of life address different aspects of the study question. A pattern across these measures can be informative, but the evidential weight of each depends on prespecification, analysis methods, and any adjustment for multiple testing—details not fully described in the registry record.

Lastly, the example clarifies that precision, statistical significance, and practical meaning are separate ideas. The primary confidence interval gives a model-based range for the average contrast, while the scale’s interpretation and participants’ own assessments of meaningful change require different information. A careful reading keeps those statistical and interpretive claims distinct.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is based on daily participant ratings on a bounded, ordered symptom scale. The registry reports group-level model estimates but does not provide the distribution of individual changes, the completeness of diary reporting, or the proportion meeting any responder definition. The result therefore cannot show how uniform or varied participant experiences were.

The primary comparison is assessed at Week 24 within a study described as lasting 52 weeks. It should not be taken as a direct estimate of the treatment contrast at Week 52. The study includes a later change in dosing for one dupilumab group, but the Week 24 pooled analysis cannot compare that schedule with continued every-2-week treatment because both groups followed the every-2-week regimen through the primary assessment.

The primary endpoint page focuses on nasal congestion or obstruction, although the registry’s primary objectives also include nasal polyp score and a Japanese-participant CT objective. Those questions have different outcomes and analysis populations. The result cannot stand in for results on those measures.

The registry does not report detailed ANCOVA covariates, missing-data procedures, sensitivity analyses, the multiplicity strategy, or the trial’s original sample-size justification. It also does not give enough information to assess the completeness of follow-up or the representativeness of participants beyond the stated condition. These are limitations of what can be evaluated from the registry record, not proof that particular analyses were absent from other study documents.

Finally, both groups received background intranasal mometasone furoate nasal spray. The comparison estimates the difference associated with adding the assigned study treatment in that setting; it does not isolate the effect of background therapy or establish results in settings with different background care.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Controlled Clinical Study of Dupilumab in Patients With Nasal Polyps — NCT02898454.
• Registry record last updated 2019-10-23; status last verified 2019-10.
• Results first posted 2019-10-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed randomized, double-blind, parallel-group Phase 3 study enrolled 448 participants with bilateral nasal polyps. Participants received placebo or one of two dupilumab schedules, with stable background intranasal mometasone furoate nasal spray. The primary result is change from baseline at Week 24 in participant-rated nasal congestion or obstruction severity.

The registry reports an ANCOVA least-squares mean difference of -0.87 between the pooled dupilumab group and placebo, with a 95% confidence interval from -1.03 to -0.71 and p < 0.001. The result is an average contrast for this endpoint and time point. The record also posts secondary outcomes and serious adverse event counts, which should be read using their respective definitions and analysis populations.

Important details—including the full model specification, missing-data approach, multiplicity strategy, and original sample-size rationale—are not reported in the registry record. Those gaps limit how fully the posted summary can be independently assessed.