Texan Allergy & Sinus Center Mountain Cedar Intra-Lymphatic Immunotherapy Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Texan Allergy & Sinus Center Mountain Cedar Intra-Lymphatic Immunotherapy Study (NCT03682965), a randomized phase 2 study. The primary outcome is Average Daily Total Combined Score (TCS).

2. Clinical Question

3. Trial Design

The registry describes a Phase 2, randomized, double-blind, parallel-group study with a placebo control. The brief summary calls it an investigator-initiated, multi-center study. Participants were assigned to intra-lymphatic Mountain Cedar allergenic extract or intra-lymphatic placebo. The record lists enrollment of 21 and status as completed. The recorded study start was 2018-09-28, and primary completion was 2019-03-06.

The active-treatment arm description specifies three injections of 0.1 mL, approximately 2 drops, every four weeks. The injections were given into a superficial inguinal lymph node with ultrasound guidance. The placebo description likewise specifies a series of three injections, but its full text is truncated in the registry record. The record identifies the intervention types as biological. It does not report the randomization sequence method, allocation concealment procedure, or how blinding was maintained.

The primary endpoint was average daily TCS up to 4 months. The record says the safety analysis included participants who received at least one dose of study intervention. Efficacy analyses used a per-protocol dataset that included participants who received three study treatment injections and completed at least 50% of expected electronic diary responses. The remainder of the population description is not reported in the registry record, so the full analysis-population rules cannot be reconstructed.

Several design details that would help interpret the findings are not reported in the registry record, including the original sample-size justification, the planned statistical analysis plan, interim analyses, the precise timing of the primary comparison and the handling of participants with missing outcome data. These gaps do not change the posted group summaries, but they limit assessment of how the reported analysis relates to the original protocol.

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

Analysis population for the primary outcome, as defined in the registry: Safety analysis included all participants who received at least one dose of study intervention. Efficacy analyses were on the per protocol dataset, which included participants who received three study treatment injections and completed at least 50% of expected electronic diary responses during the allergy season, with no major protocol violations. aLL enrolled patients met the criteria for inclusion in both the safety and per protocol analysis populations

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 Average Daily Total Combined Score (TCS), measured over Up to 4 months.

The primary endpoint, average daily Total Combined Score, combines symptom burden and use of rescue medication. The registry describes six symptom ratings: runny nose, stuffy nose, sneezing, itchy nose, gritty or itchy eyes, and watery eyes. Each symptom is rated from no symptoms to severe symptoms. Medication-use scores are added for oral antihistamine, eye drops and a nasal corticosteroid. The resulting daily score ranges from 0 to 38, with higher values reflecting more severe symptoms and greater associated medication use.

The registry identifies TCS as the preferred endpoint for rhinoconjunctivitis recommended by the European Academy of Allergy and Clinical Immunology. A combined symptom-and-medication measure can capture two related aspects of the experience being evaluated: symptoms themselves and the use of medicines to address them. A daily score also allows assessments across the pollen season rather than relying on one symptom rating at a single time point. These are general reasons such endpoints can be useful; the registry does not report the rationale for every design choice in this particular trial.

The outcome is described as average daily TCS up to 4 months, measured during the 2018-2019 Mountain Cedar pollen season. The full endpoint description is truncated in the registry record. The posted group summaries are means and standard deviations, and the efficacy population is described as per protocol. The record does not provide enough detail to establish how diary observations were combined into each participant's average or how incomplete diaries were handled.

7. Results Posted in the Registry

• Intra-lymphatic Allergenic Extract: mean 10.10 versus 13.00 on control; difference -2.90 (95% CI -8.11 to 2.31), standardized effect d = -0.49; z-test p = 0.276.

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.

Patient Reported Pain or Discomfort Following Intra-lymphatic Injections

• 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:
  • Intra-lymphatic Allergenic Extract: mean 0.50 versus 0.50 on control; difference 0.00 (95% CI -0.43 to 0.43), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intra-lymphatic Allergenic Extract and the control. The interval gives the range of effects that remain compatible with the data.

Patient-reported Treatment Satisfaction at the End of Study

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Intra-lymphatic Allergenic Extract: 90.9% (10/11) versus 90.0% (9/10) on control; risk difference 0.9 percentage points (95% CI -24.3 to 26.1), risk ratio 1.01 (0.76–1.33); unadjusted two-proportion z-test p = 0.943.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intra-lymphatic Allergenic Extract and the control. The interval gives the range of effects that remain compatible with the data.

Percentage Change in Allergen-specific Serum IgE

• 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:
  • Intra-lymphatic Allergenic Extract: mean 148.00 versus 201.00 on control; difference -53.00 (95% CI -244.03 to 138.03), standardized effect d = -0.24; z-test p = 0.587.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intra-lymphatic Allergenic Extract and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several kinds of information: participant-reported injection discomfort, treatment satisfaction, allergen-specific serum IgE, peak pollen-season combined scores and safety measures. The posted numerical summaries available for some secondary outcomes describe broadly similar group values or uncertain differences, while the registry also reports a test for treatment satisfaction. Other listed secondary outcomes do not have detailed results in the numerical summaries described in the record. The secondary findings therefore provide a partial, varied picture rather than a single consistent statistical confirmation of the primary result.

Secondary endpoints can help characterize dimensions not captured by the primary score, but they do not replace the primary comparison. Their relationship to the primary result is also limited by the primary-analysis discrepancy: the sponsor-reported rank-based test and the recalculated mean comparison differ, and the registry does not explain why. Secondary outcomes cannot resolve that discrepancy, particularly when their own analysis details or precision information are incomplete.

Unadjusted secondary results carry less weight because multiple endpoints and comparisons create more opportunities for apparently notable findings. In general, without a prespecified hierarchy or a multiplicity adjustment, the chance of at least one false-positive result increases as the number of tests grows. The registry lists multiple secondary outcomes, but does not report a multiplicity procedure or a complete analysis plan. Any secondary p-value should therefore be read as specific to its own test rather than as confirmatory evidence across the outcome family.

The record reports eight outcome measures overall and lists six secondary outcomes. It does not contain complete numerical results for every listed secondary measure. Missing details include the full measurement and analysis information for some outcomes, and the timing and handling of incomplete observations are not fully reported. The posted secondary information can describe the observed patterns for measures with available summaries, but it cannot establish a comprehensive or adjusted secondary conclusion.

More generally, secondary outcomes may be exploratory, supportive or confirmatory depending on the protocol and analysis plan. The registry record does not state how each secondary outcome was positioned, nor whether the reported tests followed a prespecified hierarchy. Without that context, the sensible reading is descriptive: consider the direction and uncertainty where reported, avoid treating isolated unadjusted p-values as definitive, and keep these outcomes distinct from the primary endpoint.

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

• Number of Peak Pollen Season Days With a Lower Group Average Total Combined Score
• Patient Reported Pain or Discomfort Following Intra-lymphatic Injections
• Patient-reported Treatment Satisfaction at the End of Study
• Percentage Change in Allergen-specific Serum IgE
• Total Safety Score (TSS) for Active and Placebo Treatment Groups
• Number of Subjects Who: Experienced Anaphylaxis, Were Treated With Epinephrine, or Experienced Any Other Treatment-emergent SAE Within 60 Minutes of Any of Three Planned ILIT Procedures

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Kruskal-Wallis method for the primary comparison and a p-value of 0.004. It also provides group means and standard deviations that permit a simple unadjusted recalculation of the difference in means. These are different statistical approaches, and their results should not be treated as if they answer exactly the same question.

What does the Kruskal-Wallis method test?

In general, the Kruskal-Wallis test is a rank-based method for comparing groups. Rather than relying directly on the numerical distances between outcome values in the way a mean-based comparison does, it uses the ordering of observations. In a comparison of two groups, it can be understood as a rank-based test of whether the outcome distributions differ. The method is often considered when distributional assumptions underlying a mean-based analysis may be unsuitable, though the registry does not report why this method was selected for this trial.

A rank-based p-value does not itself quantify a difference in TCS units. It does not give the direction or size of a difference without accompanying summaries, and it does not show the range of effect sizes compatible with the data. The record reports a superiority classification and p = 0.004 for the test, but does not report its test statistic, an effect estimate or an associated confidence interval. It also does not explain how the test was applied to repeated daily diary scores or to the per-protocol dataset.

What does the recalculated mean difference represent?

The recalculation uses the posted group means, standard deviations and sample sizes to form an unadjusted difference in means. The estimate is -2.9 TCS units, calculated as the allergenic-extract group mean relative to the placebo group mean. The accompanying 95% confidence interval is -8.113 to 2.313, and the unadjusted p-value is 0.276. This calculation is a summary-statistics comparison, not a replacement for the sponsor's analysis and not evidence that the trial's original plan used a mean-based test.

In general, a mean difference is useful when the mean is a meaningful summary of the outcome and the group data can reasonably support inference about means. A confidence interval expresses uncertainty in the estimated difference under the assumptions of the calculation. The interval's inclusion of zero means that the recalculation does not exclude no mean difference at the conventional two-sided 0.05 threshold. That statement applies to this recalculation; it does not overturn the sponsor's reported rank-based result.

Why can the analyses differ?

General statistical reasoning offers several possible reasons for divergence between a rank-based test and a comparison based on means. The two methods summarize different features of the data, and the rank method can respond to ordering and distribution shape, while the mean comparison is sensitive to numerical distances and extreme values. Small samples can also make statistical summaries especially variable. However, the registry record does not report individual-level scores, the distributions, the exact analysis dataset for the reported test, or the sponsor's explanation. No particular reason for the discrepancy can therefore be identified from the record.

The discrepancy is explicitly flagged in the record. In this situation, the sponsor's own analysis takes precedence when reporting what the sponsor concluded. The recalculation remains informative as a transparent comparison of the posted means, but it should be labeled as a recalculation and not presented as the sponsor's test result. The two p-values answer different analysis procedures and should not be combined or averaged.

What does a p-value say?

In general, a p-value describes how surprising data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it is not the probability that the observed result arose by chance in an ordinary, assumption-free sense. A smaller p-value may indicate stronger incompatibility with the null under the specified test, but it does not measure clinical importance, precision or the probability that a finding will replicate.

The primary reported p-value is 0.004, while the recalculated unadjusted p-value is 0.276. Because the registry does not report a multiplicity adjustment or the original analysis plan, neither number should be read as documenting control of false-positive risk across all outcomes and analyses. The reported result also lacks an effect estimate and interval that would communicate magnitude and precision for the rank-based comparison.

How should the secondary tests be viewed?

The registry includes a Wilcoxon (Mann-Whitney) analysis for treatment satisfaction, with p = 0.23. In general, this is another rank-based method for comparing two groups. The registry does not give an adjusted p-value or a multiplicity plan. Other posted secondary summaries include means, standard deviations or proportions; recalculations for those outcomes use the posted summaries and should be distinguished from sponsor analyses. A method's general properties do not resolve missing details about how a particular endpoint was measured or analyzed in this trial.

In general, using multiple outcomes and comparisons increases the chance that at least one result appears notable by chance if each is assessed without adjustment. The number of planned analyses and the intended hierarchy are not reported in the registry record. The posted p-values therefore need to be interpreted as analysis-specific rather than as a complete, multiplicity-controlled account of the study.

11. Confidence Intervals and Precision

For the recalculated primary mean difference, the estimate is -2.9 TCS units and its 95% confidence interval runs from -8.113 to 2.313. In general, a confidence interval describes a range of values reasonably compatible with the data and the assumptions of the method. It reflects sampling uncertainty; it is not a range containing a fixed proportion of individual participants' scores, and it is not a guarantee that the true effect lies inside this particular interval.

The interval includes zero, the value corresponding to no mean difference. It also extends to values on both sides of zero, so the recalculation does not estimate the direction with high precision. The relatively broad range, together with the group sizes of 11 and 10, indicates limited precision in the mean comparison. The posted estimate alone should not be read as a stable measure of the size of a group difference.

This interval belongs to the simple mean-based recalculation. The sponsor-reported Kruskal-Wallis analysis has p = 0.004, but the registry gives no confidence interval or effect estimate for it. Consequently, the precision of the sponsor's rank-based result cannot be judged from a reported interval. A p-value, even a small one, is not a substitute for an effect estimate with uncertainty.

Precision and statistical significance are related but distinct. In general, a confidence interval can help show both the range of plausible effects and whether values such as no difference remain compatible with the data. Here, the recalculated interval communicates uncertainty about the mean difference, while the sponsor-reported analysis communicates a test result without a corresponding interval. The discrepancy and absence of an explanation mean the two forms of evidence should be kept separate.

Confidence intervals also depend on the analysis assumptions and the population included. The registry describes efficacy analyses as per protocol, but the remaining eligibility details for that dataset are truncated. The reported summaries do not allow an independent assessment of the underlying score distribution, missing diary patterns or the sensitivity of estimates to analysis-population choices. These limitations further qualify how precisely the posted results can be generalized beyond the analyzed participants.

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 illustrations use the observed effect as a starting point and show planning values for detecting specified fractions of that effect. For the continuous outcomes shown, the entries are participants per arm, not total participants. The 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 the stated fraction of the observed effect. Time-to-event illustrations, if present, would instead give total events using the Schoenfeld method; the outcomes discussed in these planning illustrations are not time-to-event outcomes.

The 80% power column means the number of participants per arm in a hypothetical design that, under those assumptions and for the specified effect, would have an 80% chance of rejecting the null hypothesis when that effect is present. The 90% power column uses a higher target chance of detecting the specified effect under the same general planning framework. These are design calculations, not claims about the results of the enrolled trial. The original trial's own sample-size justification and assumptions are not reported in the registry record.

Rows for 100%, 75% and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects generally require more participants to distinguish from random variation under otherwise similar assumptions. The displayed values are illustrations based on effects observed in a small study, so they should not be mistaken for a definitive recommendation about the size of a future trial. In particular, uncertainty in the observed effect can make planning calculations that use it unstable.

These figures are planning illustrations, not observed power. Observed power is not a useful way to reinterpret a completed result; the confidence interval and effect estimate are more informative about uncertainty. The planning assumptions do not establish what the investigators originally intended, and the registry does not report the original design calculation or whether any such calculation informed enrollment.

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 = -2.900; pooled standard deviation σ = 5.878.
2. n = 2 × (1.96 + 0.842)² × 5.878² / -2.900² = 64.5, rounded up to 65 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 <- -2.9                      # observed difference in means
sigma <- 5.87796957424836                     # 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(3682965)
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 = 65 (80% power), 87 (90% power)
 75% of observed effect: n per arm = 115 (80% power), 154 (90% power)
 50% of observed effect: n per arm = 258 (80% power), 346 (90% power)
power.t.test: 65.5 
Simulated power at n = 65 per arm: 0.798 (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 registry's own primary analysis is a Kruskal-Wallis comparison of the allergenic-extract and placebo groups, reported with p = 0.004 and classified as superiority. The record also provides means and standard deviations for the groups. A simple unadjusted recalculation from those summaries gives a mean difference of -2.9, a 95% confidence interval from -8.113 to 2.313 and p = 0.276.

These results are discrepant: the sponsor-reported rank-based test and the recalculated mean comparison do not yield the same statistical conclusion. The sponsor's own analysis takes precedence for describing the sponsor-reported finding. The recalculation is a separate, unadjusted analysis based only on the posted summary statistics; it should not be substituted for the sponsor's test or described as the trial's planned analysis.

The registry does not explain the discrepancy. It does not provide the rank-test statistic, a rank-based effect estimate, an interval for that analysis, or sufficient detail to reconstruct the efficacy dataset and procedure. The group means alone cannot resolve how the rank-based test behaved. Therefore, the sponsor's reported p-value can be stated, but its magnitude and precision in terms of TCS units cannot be assessed from the reported analysis information. The recalculated interval offers uncertainty information for a different estimand, the difference in means, and should remain clearly distinguished.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and multiple secondary outcomes, but does not report a multiplicity adjustment, testing hierarchy or statistical analysis plan describing how the family of outcomes was handled. Multiplicity matters because repeated testing can increase the overall probability of a false-positive finding when every result is assessed at an unadjusted threshold. This is a general statistical concern; the record does not establish whether any adjustment was used outside the information reported.

The primary result itself has an additional interpretive complication: the sponsor-reported Kruskal-Wallis p-value differs from the unadjusted recalculation based on posted means and standard deviations. The registry flags a discrepancy, but the analysis plan and explanation are not reported in the registry record. It is therefore not possible to determine from the record whether the reported test was the prespecified primary procedure, whether any alternative analysis was planned, or how the sponsor addressed the difference.

The efficacy analysis population is described as per protocol, including participants who received three study treatment injections and completed at least 50% of expected electronic diary responses. Safety analyses included participants who received at least one dose. These definitions indicate that the efficacy and safety analyses did not necessarily use the same population. The remaining text describing the per-protocol dataset is truncated. The number excluded from efficacy analyses, the reasons for exclusion and the group-specific diary completion patterns are not reported in the registry record.

Missing diary data can matter for a daily symptom score because the available observations may not represent all scheduled assessment days. In general, missingness can affect estimates if the likelihood of a missing observation is related to symptoms, treatment, adherence or other outcome-related factors. The registry does not report its missing-data method, any sensitivity analyses, or how daily observations were aggregated for participants with incomplete diaries. The stated minimum diary-response threshold does not, by itself, explain how missing responses were handled.

The record also does not report interim analyses, the original sample-size justification, or the complete protocol-level statistical plan. These omissions restrict assessment of prespecification, multiplicity control and robustness to analysis choices. They do not show that particular procedures were or were not used; they mean those details are not reported in the registry record. The distinctions among the per-protocol efficacy dataset, the safety population and the posted outcome summaries should be kept in mind when interpreting the estimates.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the allergenic-extract group among 11 participants at risk and zero in the placebo group among 10 participants at risk. It also reports zero deaths in both groups. These figures describe the serious-event counts recorded for the study; they do not establish that serious events are impossible or that the risk is absent. With a small number of participants, uncommon events may not be observed.

For other adverse events, the registry reports that 5 of 11 participants in the allergenic-extract group and 1 of 10 in the placebo group were affected. The record does not provide the serious-event terms, and the listed serious terms are empty. It reports that the study considered anaphylaxis, epinephrine treatment and other treatment-emergent serious adverse events within 60 minutes of planned injection procedures, but event-specific numerical details beyond the summary counts are not reported in the registry record.

The safety population included participants who received at least one dose. The record does not provide enough detail to evaluate duration of follow-up for all safety outcomes, event severity or relatedness, or the distribution of other adverse events by type. These counts are descriptive and should be read alongside the limited sample size and the specific registry definitions, not as a complete characterization of safety.

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

The registry reports a primary rank-based comparison with p = 0.004, while a simple recalculation from the posted means and standard deviations gives a mean difference of -2.9 TCS units, a 95% confidence interval from -8.113 to 2.313 and an unadjusted p-value of 0.276. The sponsor's own analysis takes precedence when stating the sponsor-reported result, but the discrepancy is unexplained. The record does not report an effect estimate or confidence interval for the rank-based analysis, which makes it difficult to describe its magnitude or precision in the TCS scale.

The recalculation indicates a lower posted mean TCS in the allergenic-extract group than in the placebo group, but its interval spans zero and includes differences in either direction. It therefore does not give a precise estimate of the mean difference. The sponsor's reported p-value is not itself a measure of effect size, and it does not provide the same precision information as an interval. The analyses should remain separate rather than being combined into a single conclusion.

The record documents a randomized, double-blind, placebo-controlled design, but enrollment was 21. The small group sizes constrain precision and make results more vulnerable to the influence of individual observations. The record also does not provide the complete analysis plan, missing-data procedures, multiplicity handling or full details of the efficacy population. These gaps limit confidence in a complete reconstruction of the result.

These statistics do not establish whether a particular person will experience a change, nor do they answer every question about symptom burden, medication use, tolerability or safety. The TCS combines symptom ratings with rescue medication scores, so its result is a summary measure rather than a separate finding for each symptom or medicine. The available safety counts are also limited and should not be interpreted as proof of no risk.

In general, a randomized comparison can help estimate differences between groups under the study conditions, while the strength of the inference depends on implementation, measurement and analysis. The registry record supports reporting the posted summaries and the sponsor's test, with the discrepancy and uncertainty stated explicitly. It does not justify a clinical recommendation or a broad claim beyond the outcomes and participants described.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, an uncertainty interval and a test result answer different statistical questions. The posted means allow a reader to see the direction and scale of a recalculated mean difference, and its confidence interval shows substantial uncertainty. The sponsor-reported rank-based test gives a p-value but no corresponding effect estimate or interval. Because the two procedures produce discrepant results, presenting one without the other would conceal an important feature of the record.

The example also highlights that a small p-value does not automatically communicate a large or precisely estimated effect. A p-value is tied to a test and its assumptions, while effect estimates express magnitude and confidence intervals describe uncertainty. The registry's p = 0.004 for the reported Kruskal-Wallis test cannot be translated into TCS units from the information reported. The recalculated interval is in TCS units, but pertains to a mean-based comparison and includes zero.

Small studies can be informative about feasibility, measurement and the range of observed outcomes, but their estimates may be imprecise. The enrollment of 21 and efficacy groups of 11 and 10 place the reported values in that context. The planning illustrations based on the observed effect further show how sample-size requirements depend on the size of the effect one aims to detect, but those illustrations do not recover the original design rationale.

Finally, the record demonstrates the importance of reporting analysis populations, missing-data methods and multiplicity plans. The efficacy population is described only in part, and several analysis-plan details are not reported. Transparent reporting of the test, effect estimate, interval and population would make it easier to understand whether a statistical result is robust and what it means on the outcome scale. These are general lessons in interpretation, not conclusions about unreported procedures in this study.

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-analysis discrepancy is a central limitation. The registry reports a Kruskal-Wallis p-value of 0.004, while the recalculated mean comparison gives p = 0.276 and a confidence interval spanning zero. The record does not explain the difference or give an effect estimate and interval for the sponsor-reported test. Without individual-level data and fuller analysis details, the discrepancy cannot be independently investigated.

The study enrolled 21 participants, with posted primary efficacy summaries for 11 in the allergenic-extract group and 10 in placebo. Such small groups limit precision and make the summaries sensitive to individual outcomes. The registry does not report participant characteristics, detailed eligibility criteria or the extent to which the analyzed groups represent the intended population, so generalizability cannot be assessed from the record alone.

The endpoint description and efficacy-population description are truncated. The record states that efficacy analyses used a per-protocol dataset and gives an injection-completion and diary-response criterion, but does not report the full rule set or the number of participants excluded. It also does not report how missing daily diary responses were handled, how participant-level averages were constructed, or whether sensitivity analyses were conducted.

The registry does not report the original sample-size justification, the full statistical analysis plan, interim analyses, a multiplicity procedure or the intended hierarchy of primary and secondary tests. These omissions limit evaluation of prespecification and false-positive risk. The numerical secondary information is also incomplete relative to the listed outcome set, which constrains a comprehensive assessment across outcomes.

Safety reporting is limited to summary counts in the registry record. Serious adverse event counts and deaths are reported as zero in both groups, but the sample is small and event details are sparse. The record does not provide a complete account of event type, severity, relatedness or follow-up duration. These are reporting and precision limitations; they do not establish that additional methods or analyses were absent from the study's conduct.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Texan Allergy & Sinus Center Mountain Cedar Intra-Lymphatic Immunotherapy Study — NCT03682965.
• Registry record last updated 2021-04-20; status last verified 2021-03.
• Results first posted 2021-02-26.
• 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 Phase 2, randomized, double-blind, parallel-group, placebo-controlled study of intra-lymphatic Mountain Cedar allergenic extract. Enrollment was 21. The primary endpoint was average daily TCS up to 4 months, combining nasal and eye symptom ratings with rescue medication use.

The sponsor-reported primary analysis was a Kruskal-Wallis comparison with p = 0.004. A recalculation from posted group means and standard deviations gives a mean difference of -2.9 TCS units, a 95% confidence interval from -8.113 to 2.313 and p = 0.276. The discrepancy is flagged in the registry record, and the sponsor's own analysis takes precedence. The record does not explain the difference or report an effect interval for the sponsor's analysis.

Interpretation is limited by small groups, incomplete analysis-plan and missing-data details, and incomplete reporting for some secondary outcomes. Safety summaries report no serious adverse events or deaths in either group, with other adverse events reported in both groups.