A Study Comparing the Clinical Equivalence of Two Mometasone Nasal Sprays in the Relief of the Signs and Symptoms of Seasonal Allergic Rhinitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing the Clinical Equivalence of Two Mometasone Nasal Sprays in the Relief of the Signs and Symptoms of Seasonal Allergic Rhinitis (NCT01038427), a randomized phase 3 study. The primary outcome is Mean Change From Baseline in Reflective Total Nasal Symptom Score (rTNSS) (Equivalence: Per-Protocol Population).

2. Clinical Question

The central statistical distinction is between asking whether two treatments are sufficiently similar and asking whether one treatment is better than another. An equivalence analysis needs a prespecified range of differences considered clinically unimportant. The equivalence margin is not reported in the registry record, so the reported interval alone cannot show whether the equivalence criterion was met. The posted primary analysis is a ratio of test to reference least-squares means with a 90% confidence interval; the registry does not state the margin alongside that result.

The study’s setting, including further inclusion criteria and the sites involved, is not reported in the registry record beyond the official title’s description of a multi-site study. The record describes seasonal allergic rhinitis as the condition and presents symptom scores as the principal measure of treatment response.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group Phase 3 study with a placebo control. Its official title also describes the study as double-blind and multi-site. The record lists Sandoz as sponsor and marks the study completed. The recorded study start was 2009-12-02, and primary completion was 2010-02-16. Enrollment is listed as 795.

Three arms were included: the Lek Pharmaceuticals test mometasone spray, the NASONEX® reference spray, and placebo nasal spray. The two active sprays were each administered once daily at 200 mcg (4 actuations) for 14 days. Placebo was administered once daily for 14 days; a dose in mcg is not reported for that arm. The registry states that the study compared the efficacy and safety of the test and reference formulations and also tested both formulations for superiority against placebo.

The primary outcome was mean change from baseline in reflective Total Nasal Symptom Score (rTNSS), analyzed for equivalence in the per-protocol population. Only the test and reference arms were included in that primary equivalence analysis. The registry also lists instantaneous Total Nasal Symptom Score (iTNSS) analyses, including an equivalence analysis in the per-protocol population and superiority analyses in the intent-to-treat population. Investigator and patient assessments of clinical global improvement are listed among the secondary outcomes.

Further details about randomization procedures, allocation concealment, the operational meaning of the masking description, and the trial’s original statistical design assumptions are not reported in the registry record. The record does not report the equivalence margin or a sample-size justification. These omissions limit what can be inferred about how the original design was planned and how the analysis was intended to establish equivalence.

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: Participants who met the inclusion/exclusion criteria entered a 7-day placebo lead-in period. Following this placebo lead-in period, on Day 1 participants who continued to meet eligibility criteria were randomly assigned in a 2:2:1 ratio to one of three treatment groups (Test Product:Reference Product:Placebo).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-Protocol population was used in this analysis. To determine equivalence, only the test and reference treatment arms were analyzed.

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 Mean Change From Baseline in Reflective Total Nasal Symptom Score (rTNSS) (Equivalence: Per-Protocol Population), measured over Baseline, 14 days.

The primary endpoint is the mean change from baseline in reflective Total Nasal Symptom Score (rTNSS), measured from baseline through 14 days. Participants recorded a reflective symptom score twice a day, approximately 12 hours apart. A rating asked participants to look back over the preceding 12 hours; the first daily rating was recorded before dosing.

The score combines ratings for nasal congestion, runny nose, sneezing, and itchy nose. Each symptom was rated on a four-point scale from 0, no symptom, to 3, severe symptom. The mean of each symptom’s ratings over the randomized treatment period was summed to produce the mean rTNSS. The resulting scale ranges from 0 to 12, with a lower score indicating less severe symptoms. Baseline was calculated using the symptom scores recorded over the 72 hours before the randomized treatment period.

Change was defined as mean baseline rTNSS minus mean post-randomization rTNSS. Under that definition, a positive change indicates lower symptoms after randomization and is considered favorable. This direction matters when interpreting the group means and the difference between them.

A symptom score provides a repeated, patient-recorded measure of the condition being studied rather than a single assessment at one visit. For a comparison of formulations, the endpoint gives a common quantitative outcome on which to assess the pattern of symptom change. The primary analysis used the per-protocol population and compared only the test and reference sprays. This use is consistent with the stated equivalence question, but interpretation of equivalence also depends on the margin against which the estimated difference is judged. That margin is not reported in the registry record.

7. Results Posted in the Registry

• Test: mean 1.98 versus 1.82 on control; difference 0.16 (95% CI -0.20 to 0.53), standardized effect d = 0.07; z-test p = 0.377.

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.

Mean Change From Baseline in Instantaneous Total Nasal Symptom Score (iTNSS) (Equivalence: Per-Protocol Population)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test: mean 1.90 versus 1.66 on control; difference 0.24 (95% CI -0.12 to 0.61), standardized effect d = 0.11; z-test p = 0.191.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Instantaneous Total Nasal Symptom Score (iTNSS) (Superiority: Intent-to-Treat Population)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Test: mean 1.93 versus 1.63 on control; difference 0.30 (95% CI -0.06 to 0.67), standardized effect d = 0.13; z-test p = 0.104.
  • Placebo: mean 0.91 versus 1.63 on control; difference -0.72 (95% CI -1.12 to -0.33), standardized effect d = -0.34; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Test 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 Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the symptom assessment beyond the primary reflective score. They include instantaneous Total Nasal Symptom Score (iTNSS) analyses, clinical global improvement assessed by the investigator, and clinical global improvement assessed by the patient. The registry reports four secondary outcomes, but the posted analysis details include symptom-score results rather than results for every listed global-improvement measure. Further results for the global assessments are not reported in the registry record.

Across the reported symptom-score analyses, the record includes both an equivalence comparison between the active sprays and superiority comparisons against placebo. The analyses use different populations and methods: the iTNSS equivalence analysis is per-protocol, while the superiority analyses are intent-to-treat and the sponsor reports ANCOVA for comparisons with placebo. The overall pattern should therefore be understood as related evidence on symptom scores, not as one uniform analysis repeated across outcomes.

The secondary findings provide context for the primary rTNSS result because both symptom measures concern nasal symptoms during the treatment period. They are not interchangeable endpoints: reflective and instantaneous ratings ask participants to assess different time frames. Nor can a result from a superiority comparison against placebo answer the primary equivalence question between the test and reference sprays. Each comparison has its own estimand and interpretation.

Unadjusted secondary results carry less weight when multiple outcomes and comparisons are considered. General statistical explanation: examining many hypotheses increases the chance that some results will appear statistically strong by chance, particularly if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity adjustment or hierarchy for these secondary analyses. Their results are therefore best treated as supportive context rather than as independent confirmation of the primary conclusion. The record does not report enough detail to determine whether all planned secondary analyses are posted.

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

• Mean Change From Baseline in Instantaneous Total Nasal Symptom Score (iTNSS) (Equivalence: Per-Protocol Population)
• Mean Change From Baseline in Instantaneous Total Nasal Symptom Score (iTNSS) (Superiority: Intent-to-Treat Population)
• Clinical Global Improvement Based on the Investigator's Assessment
• Clinical Global Improvement Based on the Patient's Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric symptom score, and the registry reports group means and standard deviations. A mean summarizes the average score change in a group. The standard deviation describes how spread out individual scores are around that group mean. They answer different questions: the mean describes the group’s average change, while the standard deviation describes participant-to-participant variability.

What does an unadjusted mean difference represent?

The recalculated comparison subtracts the reference group mean from the test group mean. For the primary endpoint, that unadjusted difference is 0.164. Because the endpoint is defined as baseline minus post-randomization score, a positive difference means the test group’s average change is numerically greater. This calculation uses the posted group summaries and does not adjust for other variables. It is a descriptive, unadjusted comparison, not the registry’s least-squares-mean ratio analysis.

An unadjusted p-value assesses how compatible the observed difference is with a model in which the group means are equal, under the assumptions of that test. It does not measure the probability that the treatments are equivalent, and it does not give the probability that the null hypothesis is true. The primary recalculation’s p-value is 0.377. A p-value above a conventional significance threshold is not proof that the means are identical, and a nonsignificant difference test cannot substitute for a formal equivalence analysis.

Why does equivalence require a margin?

General statistical explanation: equivalence testing asks whether the plausible treatment difference is sufficiently small to fall within a prespecified interval of acceptable differences. The margin must be chosen before examining the results and justified for the clinical question. A confidence interval is then compared with both boundaries of that margin. Merely failing to find a statistically significant difference does not establish equivalence. The registry reports a primary ratio estimate and a 90% confidence interval but does not report the equivalence margin. Consequently, the criterion cannot be checked from the registry record alone.

The primary sponsor-reported statistic is a ratio of test to reference least-squares means. Least-squares means are model-based estimates, generally adjusted for variables included in the model; however, the model specification and adjustment variables are not reported in the registry record. The result is expressed as a ratio, whereas the recalculation is an unadjusted difference in group means. Because these are different measures and analyses, their numerical values are not directly interchangeable.

What does a confidence interval communicate?

General statistical explanation: a confidence interval describes a range of values compatible with the data and the assumptions of the analysis at the stated confidence level. A narrower interval indicates greater precision for the estimated quantity; a wider interval indicates more uncertainty. For an ordinary difference analysis, an interval that includes zero indicates that a zero difference is among the values compatible with the data at that confidence level. For an equivalence analysis, the relevant question is whether the interval lies wholly within the prespecified equivalence limits, not simply whether it includes or excludes zero.

The recalculated primary confidence interval is an unadjusted interval for a mean difference. The registry’s primary interval is a 90% interval for a ratio of least-squares means. Each interval addresses its own estimand and method. Neither interval should be read as a statement about every participant’s response; both describe uncertainty about a group-level estimate.

Why can variation affect precision?

General statistical explanation: when individual outcomes vary widely within groups, it can be harder to estimate a difference in group averages precisely. The standard deviations reported for the primary groups describe substantial spread in the symptom-change scores relative to the scale’s group means. Statistical precision also depends on the number of observations included in the analysis and on the analysis method. A posted standard deviation does not, on its own, reveal the full distribution of scores or whether the model assumptions fit the data.

Over-dispersion is a concern when outcome variability exceeds what a statistical model assumes. General explanation: if a model understates variability, standard errors can be too small and confidence intervals too narrow; an analysis that accounts for the extra variation may give more appropriate uncertainty estimates. The primary endpoint is continuous, and the registry provides standard deviations, but it does not report a diagnostic assessment of model fit or an over-dispersion analysis. No conclusion about such diagnostics should be inferred from the summary statistics alone.

Why do populations and analyses differ?

The primary rTNSS equivalence outcome used the per-protocol population, which the registry identifies as the population for that analysis. Per-protocol analyses generally concern participants meeting the protocol’s specified requirements, but which requirements were applied and how deviations were handled are not reported in the registry record. The iTNSS superiority analyses used the intent-to-treat population. The registry does not provide the detailed rules for that population or explain how missing observations were handled.

Different populations can produce different estimates because the participants included may differ, and different models can produce different estimates because they use different assumptions or adjustments. Thus, the reported ANCOVA results and the unadjusted recalculations should be kept distinct. ANCOVA is a regression-based method that can compare groups while accounting for specified covariates. The registry reports ANCOVA for the intent-to-treat superiority comparisons, but the covariates, model details, and adjusted estimates are not reported in the record. The reported p-values should not be treated as if they came from the unadjusted calculations.

The registry lists multiple outcomes and analyses, including two symptom-score types and clinical global assessments. When many outcomes or comparisons are examined, the chance of obtaining at least one apparently strong result by chance can increase. General statistical explanation: multiplicity methods can address this issue by adjusting significance thresholds or confidence intervals, or by identifying a primary family of hypotheses in advance. The registry record does not report a multiplicity adjustment or a hierarchy for the secondary analyses. Secondary p-values therefore warrant more cautious interpretation than a single prespecified primary result.

11. Confidence Intervals and Precision

The unadjusted primary comparison estimates a mean difference of 0.164, with a 95% confidence interval from -0.200 to 0.528. The interval includes zero and extends in both directions. That means the unadjusted summary is compatible with a range of possible test-versus-reference differences, including a small difference in either direction. It does not demonstrate that the groups are identical, nor does it establish equivalence.

The interval’s width reflects uncertainty in the estimated difference. General statistical explanation: confidence intervals quantify precision for the estimate under the analysis assumptions; they do not contain a guaranteed range for the true value, and they do not describe the range of individual participant outcomes. The reported group standard deviations indicate variability in individual score changes, while the confidence interval concerns uncertainty about the group-level contrast.

The registry’s primary equivalence analysis reports a ratio of test to reference least-squares means of 106.644, with a 90% confidence interval from 91.860 to 123.997. This is a different estimand and confidence level from the unadjusted mean-difference recalculation. The registry does not report the equivalence margin, so the interval cannot be assessed against the required limits. A ratio interval’s interpretation also depends on the scale and analysis definition used by the sponsor; further details are not reported in the registry record.

These intervals should be read as estimates with uncertainty, not as a verdict based solely on whether they cross a reference value. For a standard difference test, zero is the no-difference value. For equivalence, the prespecified margin defines the acceptable range, and the entire interval must be evaluated relative to that margin. The registry record does not provide the margin needed for that judgment.

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 planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. They illustrate sample sizes under the stated planning assumptions, rather than report observed trial sizes or the original trial’s design target. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The 80% power column describes the number of participants per arm that would give an 80% chance of detecting the chosen effect under those assumptions if that effect were real. The 90% power column describes the corresponding planning target for a 90% chance. These are design-planning probabilities, not guarantees for a future study.

Rows planning for 100%, 75%, and 50% of the observed effect represent progressively smaller target effects. Smaller effects generally require more participants to detect with the same power and significance level, because they are harder to distinguish from random variation. The figures change with the endpoint and comparison used, so they should be read in the context of the particular estimate from which they were generated.

These calculations are planning illustrations based on observed effects, not observed power for this completed trial. They do not establish whether the original study was adequately designed, because the registry does not report the original design assumptions or justification. They also do not establish equivalence: the planning figures are for detecting a stated effect under the listed assumptions, while formal equivalence planning requires an equivalence margin and a design appropriate to that question.

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 = 0.164; pooled standard deviation σ = 2.297.
2. n = 2 × (1.96 + 0.842)² × 2.297² / 0.164² = 3,078.8, rounded up to 3,079 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 <- 0.164                      # observed difference in means
sigma <- 2.29675969321558                     # 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(1038427)
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 = 3,079 (80% power), 4,122 (90% power)
 75% of observed effect: n per arm = 5,474 (80% power), 7,328 (90% power)
 50% of observed effect: n per arm = 12,316 (80% power), 16,487 (90% power)
power.t.test: 3079.8 
Simulated power at n = 3,079 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. Analyses Reported by the Sponsor

For the primary per-protocol equivalence analysis, the registry reports a test-to-reference ratio of least-squares means of 106.644, with a 90% confidence interval from 91.860 to 123.997. A p-value is not reported for this equivalence result. The equivalence margin and fuller model details are not reported in the registry record, so the result cannot be independently judged against the criterion used by the sponsor.

The unadjusted recalculation instead compares the posted group means and gives a mean difference of 0.164, with a 95% confidence interval from -0.200 to 0.528 and an unadjusted p-value of 0.377. This is not a replication of the sponsor’s analysis: it uses an unadjusted difference rather than a ratio of least-squares means, and it uses a different confidence level. The two results therefore answer related but non-identical statistical questions.

The registry does not flag a discrepancy between its reported result and the recalculation. The sponsor’s reported analysis remains the relevant result for describing the trial’s stated equivalence analysis, while the recalculation is a simple, unadjusted check using the posted summaries. Neither should be substituted for the other, and the recalculation cannot supply the unreported equivalence margin or model specification. The posted information does not establish whether the sponsor’s equivalence criterion was met.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, with several comparisons across active treatments and placebo. Testing multiple outcomes or treatment contrasts can increase the chance of a false-positive result somewhere among the set of tests. General statistical explanation: multiplicity can be handled through prespecified procedures such as adjusted significance thresholds, adjusted intervals, or a testing hierarchy that determines which hypotheses are confirmatory. These choices affect how p-values and confidence intervals should be interpreted.

A multiplicity adjustment or prespecified hierarchy is not reported in the registry record. The posted p-values should therefore be read as reported for their particular analyses, not assumed to control the overall false-positive risk across all outcomes and contrasts. This matters especially for secondary analyses, which are often interpreted in the context of the primary result and may not have the same confirmatory status. The registry does not state the planned status of each secondary test.

The primary equivalence margin is also not reported. That is an important omission for evaluating the stated primary question: an equivalence conclusion depends on an acceptable difference being prespecified and on the confidence interval falling within its boundaries. The reported ratio and 90% confidence interval alone do not reveal the margin. The record also does not describe the sponsor’s detailed model specification or the variables used to obtain the least-squares means.

The primary endpoint is analyzed in a per-protocol population, while the iTNSS superiority analyses are reported for an intent-to-treat population. The registry does not provide the operational definitions of these analysis populations, protocol-deviation rules, or details of how participants were handled in each analysis. Missing-data methods, amounts of missing outcome data, and sensitivity analyses for missingness are not reported in the registry record. These details are relevant because analysis populations and missing-data handling can affect estimates and their uncertainty.

The record does not report interim analyses, stopping rules, or the trial’s full statistical analysis plan. It also does not report the original sample-size justification. These absences do not establish that such procedures were not used; they mean the registry record does not document them for this analysis. Conclusions should stay within the analyses and information that are posted.

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 2% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record reports zero serious adverse events in each of the test, reference, and placebo groups. It also reports five other adverse events in each group. The record lists zero deaths in all three groups. These counts are reported alongside the corresponding numbers at risk: 317 for test, 320 for reference, and 158 for placebo for both serious and other adverse events.

Serious and other adverse events are separate categories in the record. The fact that no serious adverse events are reported does not mean that no adverse events of any kind occurred; the record separately lists other events. The event terms and further details about the five other events in each group are not reported in the registry record. The registry also does not provide information about event severity beyond the serious-versus-other categorization, timing, relatedness to treatment, or how events were collected.

These figures are descriptive counts for the recorded groups. They do not, by themselves, establish that the treatments have equal safety, and they should not be used to infer safety beyond the study and its recorded follow-up. The timeframe for adverse-event collection is not reported in the registry record. Safety interpretation also depends on the type of event, exposure, and completeness of reporting, details that are not available in these summary counts.

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

The posted results describe mean symptom-score changes over 14 days for the test spray, reference spray, and placebo. Under the registry’s scoring convention, a positive change represents a favorable reduction in the score after treatment began. The primary per-protocol group means for the test and reference sprays are both positive, and the unadjusted comparison estimates a mean difference of 0.164 with a confidence interval that includes zero.

That unadjusted result does not demonstrate that the two active sprays are identical. Nor does a lack of a statistically clear difference in an ordinary difference test establish equivalence. Equivalence is a distinct statistical claim that requires a prespecified margin and a confidence interval assessed against that margin. The registry reports a sponsor-run ratio analysis with a 90% confidence interval but does not report the equivalence margin, so the equivalence decision cannot be verified from the record alone.

The intent-to-treat iTNSS analyses include sponsor-reported ANCOVA results for each active spray versus placebo. These findings address superiority comparisons on a different symptom measure and in a different analysis population from the primary endpoint. They should not be treated as a replacement for the primary active-treatment equivalence comparison. The registry’s posted summary does not supply all of the model details or the multiplicity approach needed for broader claims across endpoints.

The adverse-event summary reports no serious adverse events and no deaths in the listed groups, along with other adverse events. These are descriptive registry counts, not proof of equal safety or a complete account of the events’ nature and timing.

In short, the record contains quantitative evidence about symptom scores and a sponsor-reported equivalence analysis, but important information needed to assess the equivalence criterion is absent. The estimates describe group averages with uncertainty; they do not predict an individual participant’s response, establish clinical importance, or justify conclusions beyond the study’s measured outcomes and recorded period.

18. Why This Trial Matters Statistically

This trial raises a central biostatistical distinction: a study designed to compare two formulations for equivalence cannot be interpreted as though it were only a conventional test for a difference. In a difference test, a result that is not statistically significant may reflect similarity, imprecision, or both. Formal equivalence requires defining in advance how much difference is acceptable and demonstrating that the plausible differences lie within that range. The registry reports the primary ratio estimate and interval but not the margin needed to evaluate that claim.

The study also illustrates why the analysis population and outcome definition matter. The primary question uses reflective symptom ratings and a per-protocol analysis, while the reported superiority comparisons use instantaneous ratings and an intent-to-treat analysis. These outcomes are related but measure symptoms over different recall periods. Their estimates cannot be treated as repeated measurements of precisely the same quantity.

Comparing a recalculated unadjusted mean difference with a reported ratio of least-squares means highlights the importance of the estimand and statistical model. Different methods can produce statistics on different scales and answer different questions. Clear reporting of model details, confidence intervals, margins, and analysis populations is essential for readers to distinguish the sponsor’s intended test from a simple summary-statistic comparison.

Finally, the registry’s multiple outcomes and comparisons make multiplicity relevant. Without a reported adjustment or hypothesis hierarchy, secondary results should be interpreted cautiously. Together, these features make the record a useful example of how the form of the question, not merely the presence of a p-value or interval, governs what a clinical trial result can support.

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 registry record does not report the equivalence margin for the primary analysis. Without that margin, readers cannot assess whether the sponsor-reported 90% confidence interval satisfies the planned equivalence criterion. The record also does not provide the full statistical analysis plan, the sample-size justification, or the trial’s original design assumptions, so the original planning rationale cannot be evaluated.

Further details of the sponsor’s primary model are not reported, including the method used to estimate least-squares means and any adjustment variables. The recalculated comparison is unadjusted and therefore is not a direct reconstruction of the sponsor’s model-based ratio analysis. The registry does not flag a discrepancy, but the different estimands and confidence levels remain important limitations in comparing the two summaries.

The analysis populations are named, but their detailed definitions and handling rules are not reported. Missing-data methods, the amount of missing outcome data, protocol deviations, and sensitivity analyses are also not reported in the registry record. These omissions limit assessment of whether the per-protocol and intent-to-treat estimates are robust to population selection and incomplete observations.

The record lists investigator- and patient-assessed clinical global improvement as secondary outcomes, but results for those assessments are not reported in the information available for this analysis. A multiplicity plan or adjustment is not reported, which limits the confirmatory interpretation of multiple secondary comparisons. The registry also does not report further details of the other adverse events, such as event terms, timing, or relatedness to treatment.

Finally, the primary endpoint covers baseline through 14 days. The registry record does not support conclusions about outcomes beyond that period. The posted summaries describe group-level outcomes and do not characterize how responses varied among individuals beyond the reported standard deviations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Comparing the Clinical Equivalence of Two Mometasone Nasal Sprays in the Relief of the Signs and Symptoms of Seasonal Allergic Rhinitis — NCT01038427.
• Registry record last updated 2021-02-03; status last verified 2021-01.
• Results first posted 2021-02-03.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, quadruple-masked, parallel-group Phase 3 study comparing a Lek Pharmaceuticals mometasone nasal spray with NASONEX® and placebo for seasonal allergic rhinitis. The active sprays were given once daily at 200 mcg (4 actuations) for 14 days; placebo was given once daily for 14 days.

The primary outcome was mean change from baseline in reflective Total Nasal Symptom Score, analyzed for equivalence in the per-protocol population. The registry reports a test-to-reference ratio of least-squares means and a 90% confidence interval. An unadjusted recalculation reports a mean difference with a 95% confidence interval that includes zero. These are different analyses, and the equivalence margin is not reported in the registry record.

Secondary analyses include instantaneous symptom scores and global-improvement assessments. The posted record includes ANCOVA superiority p-values for active treatments versus placebo, while multiplicity procedures and detailed missing-data methods are not reported. The adverse-event summary lists no serious events or deaths and five other events in each group. The results describe the recorded outcomes over the study period and do not, on their own, establish the primary equivalence criterion.