A Randomized, Double-Blind Placebo-Controlled Peanut Sublingual Immunotherapy Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Randomized, Double-Blind Placebo-Controlled Peanut Sublingual Immunotherapy Trial (NCT00580606), a randomized phase 1, phase 2 study. The primary outcome is Percent of Participants Who Successfully Consumed 5,000 mg of Peanut Powder or at Least a 10-fold Increase in the Amount of Peanut Powder Compared to Their Baseline Oral Food Challenge.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, crossover Phase I/II pilot study. Its official title identifies a whole peanut extract, and its brief summary states that the purpose was to evaluate safety and immune response to daily sublingual immunotherapy in adults and children with peanut allergies. The record lists an enrollment of 40 and a completed status. The listed study dates are 2007-12 for start and 2010-12 for primary completion.

The primary results concern the double-blind period, when the randomized groups received low-dose peanut SLIT or placebo. The registry lists glycerinated peanut allergenic extract and glycerin placebo as the interventions. It describes an escalating-dose phase followed by maintenance. The regimen description for the peanut group is cut off in the registry record, so its complete dose range is not reported in the registry record. The placebo arm description gives a maintenance range and says participants continued it for at least 8 weeks before crossover.

The registry also describes crossover from placebo to open-label peanut SLIT and an open-label period for the original peanut group. This structure means the primary randomized comparison should be distinguished from later observations after crossover. Once participants in the placebo group cross over to active treatment, their later outcomes do not represent an ongoing randomized placebo comparison.

The primary analysis population was intention to treat, including all subjects randomized to double-blind treatment. The registry does not report the original sample-size justification, the detailed randomization procedure, the sequence allocation details, or the complete masking procedures. Those elements are not reported in the registry record. The pilot designation and Phase I/II classification describe the study’s stated stage and purpose, but do not establish what criteria were used to choose the enrollment target.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Double Blind (DB)

Open Label (OL)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intention to treat (ITT) population was used which included all subjects randomized to double-blind treatment.

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 Percent of Participants Who Successfully Consumed 5,000 mg of Peanut Powder or at Least a 10-fold Increase in the Amount of Peanut Powder Compared to Their Baseline Oral Food Challenge, measured over Week 44 (Double Blind Period).

The primary endpoint is the percentage of participants who met a defined oral food challenge criterion at Week 44 of the double-blind period. A participant counted as a success if they consumed, without dose-limiting symptoms, 5,000 mg of peanut powder or at least a 10-fold increase in the amount consumed at their baseline oral food challenge. The outcome is binary at the participant level: each participant either met the stated criterion or did not. The reported group percentages summarize the proportion meeting it.

An oral food challenge provides a direct, protocol-defined measure of how much peanut powder a participant could consume under the challenge conditions. The endpoint therefore captures challenge performance against a specified threshold; it is not itself a direct measure of immune response, everyday peanut exposure, or long-term persistence after treatment. The registry’s description specifies that the challenge was double-blind and placebo-controlled and that dose-limiting symptoms determined whether consumption counted as successful.

The endpoint was assessed in the intention-to-treat population of participants randomized to double-blind treatment. This population definition matters because it ties the primary comparison to the original randomized groups rather than only to participants who completed treatment or reached a particular dose. The registry does not report the detailed handling of missing challenge assessments, so the implications of incomplete endpoint data cannot be determined from the record.

7. Results Posted in the Registry

• Low Dose Peanut SLIT (Double Blind): 70.0% (14/20) versus 15.0% (3/20) on control; risk difference 55.0 percentage points (95% CI 29.5 to 80.5), risk ratio 4.67 (1.58–13.77); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percent of Participants Who Achieved a Maintenance Dose of 1,386 mcg

• 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:
  • Low Dose Peanut SLIT (Double Blind): 85.0% (17/20) versus 95.0% (19/20) on control; risk difference -10.0 percentage points (95% CI -28.3 to 8.3), risk ratio 0.89 (0.73–1.10); unadjusted two-proportion z-test p = 0.292.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose Peanut SLIT (Double Blind) and the control. The interval gives the range of effects that remain compatible with the data.

Percent of Participants Who Successfully Consumed 10,000 mg of Peanut Powder

• 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:
  • Low Dose Peanut SLIT (Double Blind to Open Label): 10.0% (2/20) versus 11.8% (2/17) on control; risk difference -1.8 percentage points (95% CI -21.9 to 18.4), risk ratio 0.85 (0.13–5.41); unadjusted two-proportion z-test p = 0.863.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose Peanut SLIT (Double Blind to Open Label) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend beyond the primary Week 44 challenge comparison. They cover achievement of a maintenance dose, consumption thresholds during or after open-label treatment, and serious adverse events. These outcomes address different aspects of the treatment course, and their timeframes and analysis populations are not necessarily the same as those for the primary endpoint. The overall pattern should therefore be read as complementary evidence rather than as a single additional test of the primary finding.

The posted secondary results do not form a uniform confirmation of the primary endpoint. In particular, outcomes based on reaching a maintenance dose or consuming a higher amount at a later assessment measure different milestones from meeting the primary double-blind challenge criterion. A participant’s status on one outcome cannot be assumed from another outcome, and the results should not be collapsed into a general claim about all measures of response.

The registry lists six secondary outcomes, but detailed numerical results are not present in the record for every listed outcome. Where results are posted, the record does not report sponsor analyses alongside them. The calculated comparisons are unadjusted. The registry does not state whether the secondary outcomes were ordered in a hierarchy, whether a subset was designated confirmatory, or whether a multiplicity procedure was used.

As a general statistical point, testing several outcomes creates more opportunities for a nominally small p-value to occur by chance across the set of tests. Without a prespecified hierarchy or an adjustment procedure, unadjusted secondary results carry less confirmatory weight than a clearly designated primary comparison. This does not make them uninformative; it means they are better treated as supportive or exploratory unless the record establishes a stronger inferential plan. The primary randomized result remains distinct from these later or differently defined outcomes.

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

• Percent of Participants Who Achieved a Maintenance Dose of 1,386 mcg
• Percent of Crossover Participants Who Successfully Consumed 5,000 mg of Peanut Powder or at Least a 10-fold Increase in the Amount of Peanut Powder Compared to Their Baseline Oral Food Challenge After 44 Weeks of Open Label Peanut Protein Consumption
• Percent of Crossover Participants Who Achieved an Open Label Peanut Protein Consumption Maintenance Dose of 3,696 mcg
• Number of Participants With Serious Adverse Events (SAEs)
• Number of Crossover Participants With Serious Adverse Events (SAEs) During 44 Weeks of Open Label Peanut Protein Consumption
• Percent of Participants Who Successfully Consumed 10,000 mg of Peanut Powder

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either met the oral food challenge success definition or did not. For each randomized group, the registry reports the percentage meeting the criterion. The central comparative measure is the risk difference, which expresses the difference between the two group proportions. In general, a risk difference is easier to interpret in absolute terms than a relative measure because it describes how far apart the outcome proportions are. The registry reports the risk difference as 55, while the unadjusted recalculation expresses it as 0.55.

What does the reported test assess?

The sponsor’s reported analysis names Barnard’s Statistic and gives a risk difference with a confidence interval and p-value. As a general statistical explanation, Barnard’s test is an unconditional exact test for comparing binary outcomes in two independent groups. It assesses whether the observed separation in the groups is compatible with the null hypothesis of no difference, subject to the test’s assumptions. The reported p-value is < 0.001. A p-value is not the probability that the null hypothesis is true, and it does not measure the probability that the finding will replicate.

The recalculated comparison uses the posted group summaries and is unadjusted. It is not a replacement for the analysis specified or conducted by the sponsor. In this case, the recalculated p-value is also < 0.001, while its interval limits differ from those in the sponsor’s report. The registry record does not give further details about the sponsor’s full analysis procedure, such as any additional covariate adjustment or software implementation. Such details are not reported in the registry record.

Why use a confidence interval as well as a p-value?

As a general statistical explanation, a confidence interval describes a range of effect estimates compatible with the observed data under a specified method and its assumptions. Its width conveys precision: a wider interval leaves more uncertainty about the magnitude. Its position relative to zero helps indicate whether the data are compatible with no risk difference under that method. Confidence intervals are not guarantees that the true effect falls inside the particular interval, and a 95% interval does not mean there is a 95% probability that the fixed true effect lies in it.

Here, the sponsor’s reported interval is positive throughout, which aligns with the reported test result. The recalculated interval is also positive throughout. The intervals are not interchangeable because they come from different analyses. The registry does not report which interval construction or other technical choices produced the sponsor’s confidence limits, beyond identifying Barnard’s Statistic and the risk difference.

What does the intention-to-treat population contribute?

The primary outcome description says the intention-to-treat population included all subjects randomized to double-blind treatment. As a general principle, analyzing people according to their randomized assignment preserves the basis of a randomized comparison and avoids defining the main groups solely by treatment completion or adherence. The record does not explain how missing endpoint values, withdrawals, or other incomplete observations were handled. It is therefore not possible to determine whether every randomized participant contributed an observed challenge outcome or what assumptions were used for missing data.

How should the design shape the comparison?

The study is described as a crossover trial, but the primary endpoint timeframe is the Week 44 double-blind period and the primary population includes participants randomized to double-blind treatment. The primary comparison is consequently the comparison between the randomized double-blind groups, not a before-and-after comparison within individuals. The later crossover and open-label phases concern subsequent exposure and should not be conflated with the initial placebo-controlled contrast. The registry does not report a primary analysis that combines the later open-label observations with the double-blind endpoint.

As a general point, crossover designs can make within-participant comparisons possible when outcomes and treatment periods are suitable, but their analysis must account for sequence, period, and possible carryover effects. Whether those features were assessed for any later analysis is not reported in the registry record. No assumptions about such analyses should be inferred from the design label alone.

Why can binary outcomes be statistically challenging?

As a general explanation, binary outcomes contain fewer possible values than continuous measurements, and the amount of information depends on how many participants experience each outcome in each group. When event proportions are near the extremes, some common approximations may behave poorly, particularly with small samples. Exact methods can be used to avoid relying on certain large-sample approximations, although they still depend on the study design and the method’s assumptions.

Over-dispersion is a general concern when observed variation exceeds what a chosen probability model expects, for example when participants differ in ways that make outcomes more variable than a simple model allows. It is not a separate quantity reported for this binary primary endpoint, and no over-dispersion adjustment is described in the registry record. The record identifies the endpoint as a percentage of participants with an event and names Barnard’s Statistic for the sponsor’s primary analysis; it does not report a model for over-dispersion.

Finally, a statistically significant comparison does not establish clinical importance by itself. Interpretation also depends on what the challenge criterion represents, the size and precision of the observed difference, safety information, and the limits of the study population and follow-up. The registry supports a specific comparison at a specific assessment point, not an unrestricted conclusion about all forms of peanut exposure or all patients with peanut allergy.

11. Confidence Intervals and Precision

The sponsor-reported primary risk difference is 55, with a 95% confidence interval from 22.2 to 77.6. The interval does not include zero, and the sponsor reports p < 0.001. These results support a positive difference in the percentage meeting the challenge criterion in the low-dose peanut SLIT group compared with placebo under the sponsor’s analysis. The interval nevertheless spans a range of possible magnitudes, so the estimate is not exact.

The unadjusted recalculation from the posted group summaries gives a risk difference of 0.55, with its interval from 0.295 to 0.805. The recalculated interval is wider than the sponsor’s interval in absolute terms on the proportion scale. Both analyses indicate a positive difference, but their limits differ. The sponsor’s own analysis takes precedence for the trial’s reported result; the recalculation is a separate check based on the posted summaries.

As a general statistical point, confidence interval width reflects precision as well as effect magnitude. A narrow interval constrains plausible values more closely, while a wide interval allows more uncertainty about the exact effect. An interval is conditional on the analysis method and the study data; it does not account for every possible source of bias, limitations in endpoint measurement, missing data, or uncertainty about generalizing beyond the study.

Each double-blind group had 20 participants. With groups of this size, the percentages are based on a limited number of participant outcomes, so single outcomes can matter appreciably to the proportions. The registry’s intention-to-treat definition is reported, but its method for handling missing outcome data is not reported in the registry record. Precision estimates do not correct for that unreported information or for any design and measurement limitations.

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 illustrations of the participants per arm that would be needed under stated assumptions to detect specified fractions of the observed effect. The figures are participants per arm, not total participants and not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each illustration, the effect to detect is the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the planned chance of detecting an effect of the specified size if that effect were the true effect and the assumptions held. The 90% power column uses a higher target chance of detecting that same effect and therefore generally calls for more participants per arm. These are design-planning quantities, not guarantees about what a future study will find.

Each planning scenario changes the effect size being targeted. Planning for 100% of the observed effect uses the full observed estimate as the target; planning for 75% or 50% uses a smaller target effect. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under the same assumptions. The illustrations use the observed effect as their starting point, so they should not be treated as independent evidence that the observed effect is stable or likely to recur.

The effect used in planning is an assumption for the illustration, not a result from a newly conducted trial. This is not observed power. The original enrollment of 40 does not reveal the study’s original power target or design calculation, because those assumptions are not reported in the registry record. The displayed planning values are useful for understanding how sample-size needs change with target effect and power, but they do not show that the completed study was adequately or inadequately planned.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.150; treatment proportion p₁ = 0.700; average p̄ = 0.425.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6991 = 1.3702.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5809 = 0.4889.
4. n = (1.3702 + 0.4889)² / (0.5500)² = 11.4, rounded up to 12 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
p0 <- 0.15                          # control proportion
p1 <- 0.7                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(580606)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 12 (80% power), 15 (90% power)
 75% of observed effect: n per arm = 20 (80% power), 27 (90% power)
 50% of observed effect: n per arm = 42 (80% power), 55 (90% power)
power.prop.test: 11.4 
Simulated power at n = 12 per arm: 0.851 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis compares the randomized double-blind groups using Barnard’s Statistic and reports a risk difference of 55, a 95% confidence interval from 22.2 to 77.6, and p < 0.001. The recalculation uses the posted group summaries to make a simple, unadjusted comparison. It gives a risk difference of 0.55, a different confidence interval, and p < 0.001.

The point estimates express the same broad direction of difference, but the interval limits are not identical. That can occur when analyses use different statistical procedures or interval construction. The registry does not give enough technical detail to identify every reason for the difference. The discrepancy flag is false, but that does not make the recalculation the official trial analysis.

The sponsor’s own analysis takes precedence when describing what the trial reported. The recalculation is best understood as a transparent secondary check using the posted group summaries, not as a correction to the sponsor’s result. Both analyses indicate a positive primary comparison, while the sponsor’s stated method and estimate remain the appropriate reference for the trial’s own reported inference.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists six secondary outcomes. It reports a sponsor analysis for the primary comparison. The record does not report a multiplicity adjustment for the secondary outcomes, nor does it describe a hierarchy or gatekeeping plan that would control the overall chance of false-positive findings across multiple tests. Whether such procedures were specified in the full protocol or statistical analysis plan is not reported in the registry record.

As a general statistical explanation, multiplicity arises when several hypotheses are tested and the results are considered together. If each test is interpreted using the same nominal threshold without adjustment, the chance of at least one false-positive finding across the set can be greater than for a single test. This is why the primary endpoint is usually distinguished from secondary or exploratory outcomes. The registry’s posted information does not establish which secondary findings, if any, were intended as confirmatory.

The primary population is explicitly described as intention to treat and includes all subjects randomized to double-blind treatment. This is an important population definition, but it does not reveal how incomplete endpoint information was treated. The registry does not report the number of missing Week 44 challenge assessments, reasons for missingness, imputation methods, or sensitivity analyses for missing data. Those details are not reported in the registry record.

The record also does not describe the analysis population for each secondary endpoint in enough detail to establish whether it is identical to the primary intention-to-treat population. Crossover and open-label outcomes may concern participants who entered later treatment phases, but the specific handling of eligibility and missing observations for every endpoint is not reported. As a result, secondary estimates should be interpreted in light of their stated timeframe and the limits of the population information available.

These omissions do not invalidate the posted primary estimate, but they limit independent assessment of the full analysis plan. In particular, the record does not allow a reader to verify whether the endpoint definitions, missing-data rules, multiplicity approach, and analysis populations were all prespecified in the same way as the posted results.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaphylactic reaction (5.6%), urticaria (5.0%).

For the double-blind period before the Week 44 oral food challenge, the registry reports one participant with a serious adverse event in the low-dose peanut SLIT group and none in the placebo group. These counts describe serious adverse events in the listed groups; they do not by themselves establish whether an event was caused by treatment. The registry also reports other adverse events for the groups, but the counts should be read in the context of the record’s separate serious and other adverse-event categories.

The record lists additional safety groups for the open-label and crossover periods. It reports one serious adverse event in the low-dose peanut SLIT group continuing into open label and none in the listed crossover high-dose groups. These later groups reflect different treatment phases and should not be combined with the initial blinded comparison as though they were one parallel randomized safety comparison.

The registry lists anaphylactic reaction and urticaria among the top serious terms, with 5.6% and 5.0%, respectively. The record does not provide enough information in these fields to assign those percentages to a particular randomized arm or to infer a treatment relationship. Death counts are not reported in the registry record. The safety counts are descriptive and do not establish comparative safety with precision.

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

The primary result means that, at the Week 44 double-blind oral food challenge, a larger percentage of participants assigned to low-dose peanut SLIT met the registry’s defined consumption criterion than participants assigned to placebo. The sponsor reports a risk difference of 55, with a 95% confidence interval from 22.2 to 77.6 and p < 0.001. The outcome definition includes consumption without dose-limiting symptoms of 5,000 mg of peanut powder or at least a 10-fold increase over baseline challenge consumption.

The result does not mean that all participants in the peanut SLIT group met the criterion, or that placebo participants could not meet it. It does not establish what an individual participant will experience. Group-level percentages and a comparative estimate describe the trial participants under its procedures, not each person’s outcome.

The endpoint is a challenge result at a specified assessment point. It does not by itself demonstrate that participants could consume peanut without symptoms in everyday settings, that any change persisted after treatment, or that the same result would apply to people outside the enrolled study population. The record includes later outcomes after open-label treatment and after discontinuation, but those address different timeframes and do not extend the primary randomized comparison.

The result also does not resolve the full balance of benefits and harms. Serious adverse-event counts are limited descriptive data from the registry record, and the record does not provide a complete analysis of causal attribution or precision for safety comparisons. The findings should be understood as evidence about the stated trial endpoint and treatment period, not as a general recommendation or a complete assessment of peanut allergy care.

Finally, statistical significance is not a measure of clinical importance on its own. The estimated difference is substantial in direction and the sponsor’s interval is positive, but interpretation still depends on the study’s pilot design, sample size, endpoint relevance, incomplete reporting of analysis details, and applicability to other settings and populations.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through both its endpoint definition and its comparison structure. The primary endpoint is not a vague report of improvement: it is a participant-level success criterion based on consumption during a double-blind placebo-controlled oral food challenge. The outcome and assessment time make clear what the reported percentage represents, while also marking what it does not represent.

The randomized double-blind comparison gives the primary result a clear comparator. The risk difference communicates the absolute separation between the groups, and the confidence interval shows that the estimated magnitude remains uncertain even when the reported result is statistically significant. Reading the point estimate, interval, and p-value together is more informative than treating a significance threshold as the whole conclusion.

The registry also demonstrates why a recalculation should be distinguished from the sponsor’s analysis. Unadjusted calculations from posted summaries can act as a check and help readers understand the data, but different methods can yield different interval limits. The sponsor’s own analysis remains the reported trial analysis, and the recalculation should not silently replace it.

Finally, the crossover and open-label phases highlight the need to separate randomized comparisons from later follow-up. Secondary endpoints can add information about maintenance and later challenge outcomes, but they do not automatically reinforce the primary finding, especially when multiplicity procedures and analysis populations are not fully described. This is a useful example of interpreting a statistically clear primary contrast while retaining appropriate caution about precision, safety, missing data, and generalizability.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The study is identified as a Phase I/II pilot trial, and each initial double-blind group included 20 participants. The resulting estimates are based on a small study population, which limits the precision available for both the primary comparison and uncommon safety outcomes. The confidence interval conveys uncertainty in the primary estimate, but it does not address all forms of bias or uncertainty about generalization.

The primary endpoint depends on a defined oral food challenge threshold. That makes the measure specific and interpretable, but it is not equivalent to everyday exposure or long-term tolerance. The registry’s primary timeframe is Week 44 of the double-blind period. Later outcomes occur after crossover or open-label treatment and should not be treated as extensions of the original placebo-controlled comparison.

The crossover structure creates an important interpretive distinction between the initial blinded phase and later treatment periods. After crossover, the original placebo group receives peanut treatment, so later outcomes do not retain the same randomized placebo comparison. The registry record does not report enough detail to assess the analysis of sequence, period, or possible carryover effects for later outcomes.

Reporting is incomplete for several methodological questions. The original sample-size justification, detailed statistical analysis plan, multiplicity approach, missing-data handling, and complete analysis populations for the secondary outcomes are not reported in the registry record. The dose description for the original peanut arm is also truncated. These limitations restrict independent evaluation of how all planned analyses relate to the posted results.

The serious adverse-event figures are counts in defined study phases, not a complete causal assessment. The registry record does not report deaths, and the listed serious-event terms cannot be assigned to a particular arm from the information reported. These gaps make it inappropriate to draw broad comparative safety conclusions from the counts alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Randomized, Double-Blind Placebo-Controlled Peanut Sublingual Immunotherapy Trial — NCT00580606.
• Registry record last updated 2019-08-21; status last verified 2019-08.
• Results first posted 2012-10-30.
• 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 randomized, triple-masked, crossover Phase I/II pilot study of daily peanut sublingual immunotherapy in adults and children with peanut allergies. Enrollment was 40. The primary endpoint was the percentage meeting a defined oral food challenge consumption criterion at Week 44 of the double-blind period, analyzed in the intention-to-treat population of participants randomized to double-blind treatment.

The posted primary results were 70% for low-dose peanut SLIT and 15% for placebo. The sponsor reported a risk difference of 55, a 95% confidence interval from 22.2 to 77.6, and p < 0.001 using Barnard’s Statistic. The registry also describes crossover and open-label treatment, with later outcomes that should be distinguished from the initial randomized comparison.

Interpretation is limited by the pilot sample size and by unreported details concerning the original design assumptions, missing data, multiplicity, and some secondary analysis populations. The primary result is specific to the stated challenge endpoint and assessment period.