Efficacy and Safety of LYR-210 for the Treatment of Chronic Rhinosinusitis in Adults (ENLIGHTEN 2): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of LYR-210 for the Treatment of Chronic Rhinosinusitis in Adults (ENLIGHTEN 2) (NCT05295459), a randomized phase 3 study. The primary outcome is Change From Baseline (CFBL) in the 7-day Average Composite Score of 3 Cardinal Symptoms (3CS) in Participants Without Nasal Polyps.

2. Clinical Question

The composite symptom score brings together three patient-rated symptoms recorded in a daily diary. Each symptom is rated from 0 to 3, with higher ratings indicating more severe symptoms; their sum ranges from 0 to 9. The comparison therefore concerns average change in symptom burden, not a count of people who improved or a time-to-event outcome.

3. Trial Design

ENLIGHTEN 2 is listed as a phase III, randomized, double-blind, controlled, parallel-group trial. The registry record reports enrollment of 182 and lists the study as completed. The recorded study start was 2022-05-13, and primary completion was 2025-04-02. Lyra Therapeutics is listed as the sponsor. These registry entries describe the planned and recorded trial structure; they do not by themselves establish how the trial was conducted at every site.

The active group received one administration of the LYR-210 drug matrix, while the control group received one mock administration procedure. Background therapy is listed, but its contents, timing, and allocation across groups are not reported in the registry record. The brief summary describes the trial as multicenter, although the registry record does not give a site count in the registry record for this account.

The primary endpoint was assessed at Week 24 in the population without nasal polyps. The posted arm summaries list 94 participants for LYR-210 and 49 for sham control for that endpoint. Those endpoint analysis counts are not interchangeable with the enrollment figure: an endpoint’s analysis population can differ from overall enrollment. The registry record does not explain the reasons for the analysis counts or describe participant flow, withdrawals, or missing endpoint observations.

Several additional outcomes are listed, including symptom scores in all participants, the SNOT-22 total score, a CT score, and rescue treatment requirement. The posted continuous outcomes include Week 24 or Week 20 assessments. Outcome-specific populations and analysis counts vary, so each result should be read in the context of its own stated population and time point rather than treated as if all endpoints used the same analysis group.

Allocation is recorded as randomized and masking as double. The registry record does not report the sequence-generation method, concealment procedures, who specifically was masked, or how masking was assessed. Details of the original sample-size rationale, the trial’s planned statistical analysis, and any interim analyses 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Analysis Set Without Nasal Polyps

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: ITT Analysis Set

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline (CFBL) in the 7-day Average Composite Score of 3 Cardinal Symptoms (3CS) in Participants Without Nasal Polyps, measured over Week 24.

The primary endpoint is change from baseline in the 7-day average composite score of three cardinal symptoms at Week 24, among participants without nasal polyps. The three symptoms are nasal blockage or congestion, nasal discharge, and facial pain or pressure. Participants recorded symptom severity each day, using a 0-to-3 rating for each symptom. Adding the three ratings produces a composite score from 0 to 9; higher scores represent worse symptoms.

Change from baseline expresses how the score at follow-up differs from the starting score. A negative change means the measured score is lower at follow-up than at baseline. Because higher scores reflect worse symptoms, a reduction in this measure corresponds to a reduction in the recorded symptom score. That is a description of the score’s direction, not a judgment about the clinical importance of a particular change.

A daily average can represent symptoms across a period more fully than a single-day rating, while combining the three symptoms gives one summary measure for the primary comparison. The endpoint is patient-reported through a diary, so its interpretation depends on the ratings recorded by participants and on the analysis of those records. The registry record does not report a minimum clinically important difference, a responder threshold, or details of how missing diary entries were handled.

The reported endpoint is a least-squares mean change with standard error. Least-squares means are model-based group summaries; the registry record does not describe the model used to obtain them. The endpoint and its Week 24 timing define the primary comparison, while the stated analysis population narrows that comparison to participants without nasal polyps.

7. Results Posted in the Registry

• LYR-210: mean -2.73 versus -1.61 on control; difference -1.12 (95% CI -1.92 to -0.32), standardized effect d = -0.48; z-test p = 0.006.

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.

CFBL in the 7-day Average Composite Score of 3CS in All Participants at Week 24

• 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:
  • LYR-210: mean -2.62 versus -1.72 on control; difference -0.90 (95% CI -1.65 to -0.15), standardized effect d = -0.37; z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LYR-210 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

CFBL in the 22-item Sino-Nasal Outcome Test (SNOT-22) Total Score at Week 24

• 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:
  • LYR-210: mean -22.40 versus -13.70 on control; difference -8.70 (95% CI -15.20 to -2.20), standardized effect d = -0.41; z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LYR-210 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

CFBL in the 3-D Volumetric CT Score at Week 20

• 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:
  • LYR-210: mean -2.70 versus -0.55 on control; difference -2.15 (95% CI -5.27 to 0.97), standardized effect d = -0.21; z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LYR-210 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide context around the primary symptom comparison. The posted pattern is directionally consistent across the two patient-reported measures: the estimated changes favor a larger reduction in the LYR-210 group relative to sham. The CT measure does not show the same level of statistical precision, with an interval that includes zero. These differences across outcomes are not necessarily contradictory because each measure captures a different aspect of the condition and may have different variability.

The all-participant symptom score is related to the primary symptom score, but it uses a broader population that includes all participants rather than only those without nasal polyps. The SNOT-22 is a separate patient-reported measure, while the CT score is an imaging-based measure. Their relationship to the primary endpoint is therefore complementary rather than interchangeable: agreement across related measures can add context, but variation across measures is expected and must be interpreted with their definitions and populations in mind.

The registry record also lists rescue treatment requirement through Week 24, but no result for that outcome is included among the posted secondary summaries described in the record. A listed endpoint without a posted estimate should not be treated as evidence of either a favorable or unfavorable result. The registry record does not explain the absence of a result for that listed outcome.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of at least one apparently notable result can increase as the number of tests grows. In general, multiplicity procedures control or otherwise address that issue; none is reported in the registry record. The secondary comparisons should therefore be read as descriptive evidence, not as a set of independent confirmatory tests. Their p-values do not automatically account for the number of outcomes or analyses considered.

The secondary findings can help assess whether the primary pattern is echoed by other measures, but they cannot replace the primary analysis or establish a broader conclusion on their own. The different time points, populations, measurement methods, and uncertainty all matter. No secondary result should be interpreted as proof that the primary finding is replicated, and the unreported analysis plan leaves the intended inferential role of the secondary outcomes unclear.

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

• CFBL in the 7-day Average Composite Score of 3CS in All Participants at Week 24
• CFBL in the 22-item Sino-Nasal Outcome Test (SNOT-22) Total Score at Week 24
• CFBL in the 3-D Volumetric CT Score at Week 20
• Rescue Treatment Requirement Through Week 24

9. Statistical Interpretation

10. Statistical Methods Explained

The registry record describes the primary outcome as a least-squares mean change from baseline and gives standard errors for the two groups. It also posts a mean difference, confidence interval, and unadjusted p-value. These quantities answer related but distinct questions: the group means describe average change, the difference contrasts the two group averages, the confidence interval describes estimation uncertainty, and the p-value assesses compatibility with a null comparison under specified assumptions.

What does a least-squares mean represent?

In general, a least-squares mean is an estimated group average from a statistical model. Unlike a raw arithmetic average, it can reflect adjustment for factors included in that model. The model and its adjustment variables are not reported in the registry record, so the posted least-squares means should not be interpreted as evidence about which covariates were included or how they affected the estimates. The values are presented as group summaries for the specified outcome and analysis population.

How should a mean difference be read?

In general, a mean difference subtracts one group’s mean from the other group’s mean, following a stated comparison order. For the primary outcome, the posted difference is -1.12 for LYR-210 relative to sham control. The score’s direction matters: lower composite scores indicate less severe recorded symptoms, and a negative change indicates a reduction from baseline. The sign of the difference therefore describes which group had the larger mean reduction in this comparison. It does not convert a group average into an individual-level result.

A confidence interval gives a range of values compatible with the observed data and the method’s assumptions. It communicates both the estimated direction and the uncertainty around the estimate. For a difference, an interval that includes zero is compatible with no difference under the interval procedure; an interval that excludes zero indicates that zero is not among the values covered by that interval. This is a statistical interpretation, not a measure of clinical importance. The primary interval excludes zero.

What does the p-value add?

In general, a p-value evaluates how well the observed data align with a null hypothesis under the assumptions of a statistical test. A smaller value indicates less compatibility with that null model, but it does not tell the probability that the null is true. It also does not measure the probability that the finding will replicate, the size of the effect, or whether a difference matters to patients. For the primary comparison, the posted unadjusted p-value is 0.006.

The registry record does not give enough information to reconstruct a model-based test from first principles. The posted comparison statistics include a recalculated unadjusted comparison based on summary statistics. Recalculation from group summaries is useful as a transparent descriptive check, but it may not reproduce an analysis that accounts for covariates, repeated measurements, or other features of a full participant-level dataset. No separate analysis records are listed. The discrepancy indicator is false, but that does not supply missing details of the sponsor’s analysis plan.

Why do standard errors matter?

In general, a standard error describes the sampling uncertainty of an estimated mean. It is not the spread of individual participant values: a standard deviation describes variation among observations, while a standard error describes precision of an estimate. The registry record reports standard errors for the least-squares means. A smaller standard error generally corresponds to a more precise estimate, all else equal, but interpretation also depends on the analysis model, sample size, and data completeness.

The posted recalculations use summary statistics and include an approximate pooled standard deviation for standardized-effect and planning illustrations. An approximation based on standard errors is not a substitute for the underlying participant-level distribution. In general, summary-based methods can be less informative when data are skewed, observations are dependent, or the model structure is important. The registry record does not report distributional diagnostics or the fitted model details needed to assess those possibilities.

What does randomization contribute?

In general, random allocation aims to make treatment groups comparable with respect to both measured and unmeasured factors at the start of a trial, on average. It supports a causal comparison when allocation is implemented as intended and follow-up, outcome measurement, and analysis preserve the benefits of randomization. The registry record identifies the trial as randomized and double-blind, but it does not report sequence generation, allocation concealment, masking details, or the balance of baseline characteristics. Those implementation details cannot be inferred from the designation alone.

The primary population is identified as the ITT Analysis Set Without Nasal Polyps. In general, intention-to-treat analysis refers to analyzing participants according to randomized assignment, but the exact operational definition, exclusions, and treatment of missing outcomes must be specified by the trial’s analysis plan. That plan and missing-data procedures are not reported in the registry record. The population label should be read as stated, without assuming unreported inclusion or imputation rules.

The endpoint is based on repeated daily diary ratings summarized over seven days. In general, repeated measures can contain correlated observations from the same participant, and analysis methods may need to account for that structure. The registry record does not say how daily reports were aggregated when incomplete, how baseline was defined, or whether any repeated-measures modeling was used. These omissions limit independent assessment of the endpoint calculation.

11. Confidence Intervals and Precision

The primary mean difference is -1.12, and its confidence interval excludes zero. This indicates that the estimated direction is not highly ambiguous with respect to the no-difference value under the interval method. The interval nevertheless spans a range of possible differences, so the point estimate should not be treated as exact. Its bounds reflect uncertainty in the estimated group contrast, not the range of individual participant outcomes.

Precision is affected by the amount and variability of information available, as well as by the analysis method. The primary endpoint summaries list standard errors of 0.239 for LYR-210 and 0.332 for sham procedure control. These describe the precision of the reported group means, not the typical variation in symptom scores among participants. The registry record does not report the model specification or enough detail to independently verify how uncertainty was estimated.

A confidence interval and a p-value address the comparison from different perspectives. The interval gives a range of estimates compatible with the data and method; the p-value assesses compatibility with a null hypothesis. Here, the primary interval excludes zero and the unadjusted p-value is 0.006. Neither statistic indicates whether the estimated difference meets a patient-centered threshold, because such a threshold is not reported in the registry record.

Precision also depends on the analysis population and endpoint. The primary endpoint analysis counts differ from those of other posted outcomes, and the registry record does not explain why. Missingness or exclusions can affect precision and may also affect validity if they are related to outcomes or group assignment. Without participant flow and missing-data methods, the impact of these factors cannot be assessed from the registry record alone.

When reading the interval, it is useful to keep its interpretation limited to the stated population, outcome, and time point: the Week 24 symptom score among participants without nasal polyps. It does not describe uncertainty for every secondary endpoint, for other follow-up times, or for outcomes not posted. Nor does a confidence interval represent a range in which a specified proportion of individual responses must fall.

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 illustrations express sample size as participants per arm. They are based on the observed effect and are not the original trial design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes a planning scenario in which the assumed design would have an 80% chance of detecting the specified effect at the stated significance level, if the planning assumptions and effect were correct. The 90% power column describes the corresponding scenario with a 90% chance. These are prospective planning interpretations, not probabilities that the posted result is true or that the trial’s finding will replicate.

Rows for planning at 100%, 75%, and 50% of the observed effect illustrate how the required number of participants changes when the assumed target effect changes. A smaller effect is harder to distinguish from random variation under the same assumptions, so the planning illustration requires more participants per arm for the smaller effects. These figures are not observed participant counts and do not establish the design rationale used by the sponsor.

All non-time-to-event illustrations in this trial are expressed per arm; no time-to-event planning outcome is included among the posted endpoints. The figures are planning illustrations computed from a summary-based observed effect. They do not account for any unreported trial-specific features such as attrition, covariate adjustment, outcome missingness, or a different allocation plan. 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 = -1.120; pooled standard deviation σ = 2.320.
2. n = 2 × (1.96 + 0.842)² × 2.320² / -1.120² = 67.3, rounded up to 68 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 <- -1.12                      # observed difference in means
sigma <- 2.31951118291324                     # 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(5295459)
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 = 68 (80% power), 91 (90% power)
 75% of observed effect: n per arm = 120 (80% power), 161 (90% power)
 50% of observed effect: n per arm = 270 (80% power), 361 (90% power)
power.t.test: 68.3 
Simulated power at n = 68 per arm: 0.793 (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 registry record lists several secondary outcomes in addition to the primary endpoint, but it does not report a multiplicity strategy. When many outcomes or comparisons are tested, the chance of at least one result appearing notable by chance can increase. In general, prespecified approaches such as a testing hierarchy or an adjustment to significance thresholds can address this concern. It is not reported in the registry record whether any such approach was planned or used. The posted unadjusted secondary p-values should therefore not be read as multiplicity-controlled evidence.

The record does not list separate reported analysis records, and it does not provide a full statistical analysis plan. Details such as model choice, covariates, testing order, planned contrasts, and rules for interpreting secondary outcomes are not reported in the registry record. The stated outcome summaries remain interpretable descriptively, but the inferential status of each test cannot be confirmed from the available registry entries.

Missing-data handling is also not reported in the registry record. For the daily symptom diary, it is not stated how incomplete days or weeks were treated, how a seven-day average was constructed when diary entries were absent, or whether imputation or another method was used. The record does not describe missing observations for the other endpoints, nor does it report reasons for missingness or sensitivity analyses.

The primary analysis population is named as the ITT Analysis Set Without Nasal Polyps. The exact operational definition of that set, including any exclusions after randomization, is not reported. The endpoint summaries show analysis counts that differ across outcomes, but the registry record does not explain participant flow or why those counts differ. It is therefore not possible to determine from these registry entries whether every randomized participant contributed to each outcome or how the analysis preserved the randomized comparison.

These omissions are important because multiplicity, missingness, and analysis population can affect both uncertainty and interpretation. They do not erase the posted estimates, but they limit assessment of whether the reported tests follow a prespecified confirmatory plan and whether the observed data may be affected by incomplete outcome collection.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: lumbar spinal stenosis (0.9%), colon adenoma (0.9%), transient ischaemic attack (0.9%).

The registry record lists serious adverse events for 2 of 112 participants at risk in the LYR-210 group and 0 of 60 at risk in the sham procedure control group. It lists other adverse events for 48 of 112 at risk in the LYR-210 group and 17 of 60 at risk in the sham group. Deaths are reported as 0 in each group. These are counts in the safety summaries, separate from the endpoint analysis counts used for efficacy outcomes.

The listed serious-event terms are lumbar spinal stenosis, colon adenoma, and transient ischaemic attack, each reported as 0.9%. The registry record does not specify in the registry record which group each listed term occurred in, whether events were considered related to an intervention, or the event-level timing and clinical context. The term list should not be used to infer causation.

These summaries describe reported counts, not comparative safety estimates adjusted for differences in exposure or follow-up. The registry record does not provide definitions, follow-up duration for safety, severity details beyond serious-event classification, or statistical comparisons. A zero count in a group means no event was recorded in that summary; it does not establish that the underlying risk is zero.

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

The posted primary result describes a greater mean reduction in the recorded three-symptom score in the LYR-210 group than in the sham group at Week 24 among participants without nasal polyps. The group estimates, difference, confidence interval, and unadjusted p-value collectively characterize that comparison. The confidence interval excludes zero, while the registry record does not report a clinically important threshold that would indicate how meaningful the magnitude is to participants.

This is a group-level result for a specific population, outcome, and time point. It does not show that every participant’s symptoms changed in the same direction or by the same amount. It also does not provide the distribution of individual changes, the proportion meeting a response threshold, or the relationship between score change and other outcomes. Those results are not reported in the registry record.

The primary endpoint is a patient-reported symptom score, not a direct measure of every feature of chronic rhinosinusitis. Secondary measures add other perspectives, but they have different definitions and degrees of precision. The CT outcome does not provide the same statistical clarity as the patient-reported outcomes, and the registry record does not report a result for rescue treatment requirement. No conclusion about outcomes beyond the posted measures follows from the primary comparison alone.

The estimates also do not establish durability beyond the specified assessment or applicability to populations not represented by the primary analysis set. The registry record does not report follow-up results beyond the stated endpoint times or subgroup findings beyond the specified population. It does not provide enough detail to assess how missing outcomes, treatment adherence, or analysis choices affected the result.

Statistical evidence of a group difference and clinical importance are related but distinct. A p-value and confidence interval quantify evidence and precision under statistical assumptions; they do not by themselves determine whether the size of the difference matters to patients. No medical advice or treatment recommendation follows from these registry statistics. The result should be understood as one trial’s posted comparison, with the design and reporting limitations noted in the record.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definition is central to clinical-trial interpretation. The primary outcome is not a generic measure of disease status: it is a diary-based composite of nasal blockage, nasal discharge, and facial pain or pressure, assessed at a stated time point and in a stated population. Knowing the score range and direction makes the sign of the estimated change interpretable and helps prevent a negative value from being misread as worsening.

The record also shows how a randomized comparison can be described through several layers of statistical information. Group estimates communicate average changes, a mean difference states the contrast, a confidence interval communicates precision, and a p-value addresses compatibility with a null comparison. Each has a separate role. None alone answers questions about individual response, clinical importance, or unmeasured outcomes.

The analysis counts vary between the primary and secondary outcomes, underscoring why enrollment should not be substituted for the number contributing to a particular endpoint. Without participant flow and missing-data detail, the reasons for those differences remain uncertain. This is a practical limitation when interpreting registry results and assessing whether the randomized comparison was preserved in each analysis.

Finally, secondary outcomes can help describe whether a primary pattern appears across different measures, but multiple testing affects how much confidence to place in unadjusted findings. The record’s lack of a reported multiplicity plan and detailed statistical analysis plan makes careful separation of primary evidence from secondary context especially important. That distinction is useful in biostatistics because it keeps the strength of a conclusion aligned with the amount and type of evidence actually reported.

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 contains outcome summaries but not the complete analysis plan or separate reported analysis records. It does not describe the statistical model behind the least-squares means, covariate adjustment, handling of repeated diary observations, or the exact derivation of the seven-day average. As a result, the posted summary statistics do not permit independent evaluation of every modeling decision.

Participant flow and reasons for differences in endpoint analysis counts are not reported. Missing-data procedures, assumptions about missingness, and sensitivity analyses are also not reported in the registry record. Those details are particularly relevant for a daily diary endpoint and for understanding how each analysis population relates to randomized assignment.

The registry record does not report a multiplicity adjustment or the prespecified inferential role of the secondary outcomes. Several outcomes are listed, and the unadjusted comparisons should be interpreted cautiously in that context. In addition, no estimate is posted for the listed rescue treatment requirement outcome among the secondary summaries.

The primary result applies to participants without nasal polyps at Week 24. It should not automatically be generalized to all participants or to other time points. The CT assessment is at Week 20, and the SNOT-22 and all-participant symptom score are at Week 24; these differences in measure, population, or timing limit direct comparisons across endpoints. The record does not report a clinically important threshold for interpreting the primary score difference.

Safety summaries give event counts but do not provide exposure-adjusted comparisons, event-level attribution, or detailed timing in the registry record reported. The record’s double-blind designation does not include details about who was masked or whether masking remained successful. These gaps limit the degree to which efficacy and safety findings can be evaluated beyond the posted descriptive summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of LYR-210 for the Treatment of Chronic Rhinosinusitis in Adults (ENLIGHTEN 2) — NCT05295459.
• Registry record last updated 2026-02-19; status last verified 2026-01.
• Results first posted 2026-02-19.
• 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

ENLIGHTEN 2 (NCT05295459) is a completed phase III randomized, double-blind, parallel-group trial sponsored by Lyra Therapeutics. The registry record reports enrollment of 182 and compares a single administration of LYR-210 with a sham procedure control. Background therapy is also listed, without further details in the record details.

The primary endpoint is change from baseline in the 7-day average composite score of three cardinal symptoms at Week 24 among participants without nasal polyps. The posted least-squares mean changes were -2.73 for LYR-210 and -1.61 for sham, with an unadjusted mean difference of -1.12 and an unadjusted p-value of 0.006. The confidence interval excludes zero.

Secondary outcome summaries include symptom, SNOT-22, and CT measures, with different analysis counts and time points. The registry record does not report a full statistical analysis plan, missing-data methods, or multiplicity handling. Serious adverse event counts were 2 of 112 in the LYR-210 group and 0 of 60 in the sham group; deaths were reported as 0 in both groups. Interpretation is limited to the outcomes and details posted in the registry record.