Safety of Insulin Detemir Produced by a New Process as Measured by Antibody Formation in Subjects With Type 1 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety of Insulin Detemir Produced by a New Process as Measured by Antibody Formation in Subjects With Type 1 Diabetes (NCT00447382), a randomized phase 3 study. The primary outcome is Change From Baseline in Insulin Detemir - Human Insulin Cross-reacting Antibodies.

2. Clinical Question

The registry describes a safety comparison of detemir produced by a new method, NN729, with detemir produced by the previous method, NN304. The primary measure was an antibody change ratio, rather than a clinical event or a measure of glucose control. Antibody levels were measured in %B/T; the change ratio itself has no unit.

Both groups received basal detemir and mealtime aspart. The trial description says participants received the same total daily dose and frequency of basal insulin as their own pre-trial basal insulin, with doses individualized during the trial using plasma glucose measurements. The comparison therefore concerns the production process for the detemir used in otherwise described basal-bolus regimens, not a comparison of detemir with a different basal-insulin treatment.

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group trial. The registry lists enrollment of 330 and a completed status. The official title describes a 12-month, multinational, multicentre comparison; the treatment descriptions specify 52 weeks. The registry gives a start of 2007-03 and primary completion of 2008-07.

The trial was conducted in Germany, The Republic of Macedonia, Russian Federation, Serbia and South Africa. Participants were assigned to NN729 or NN304 detemir. Each arm also used insulin aspart as mealtime bolus insulin. The detemir doses were individually adjusted and administered subcutaneously 1-2 times daily; insulin aspart was administered subcutaneously at meals. The brief description says doses were individualized based on participants’ plasma glucose measurements.

The primary endpoint analysis used the Full Analysis Set, defined in the registry as all randomized subjects exposed to at least one dose of trial product who had a post-baseline observation. The primary endpoint arm summaries include 158 participants for NN304 and 152 for NN729. The registry also gives safety risk sets of 164 for NN304 and 166 for NN729. These counts refer to different analysis contexts and should not be treated as interchangeable.

Details of the randomization sequence, allocation concealment, specific blinding procedures, eligibility criteria beyond the stated condition, and protocol deviations are not reported in the registry record. The original sample-size justification and the trial’s planned statistical assumptions are also not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Eligible subjects were adults with type 1 diabetes treated with a basal-bolus regimen for at least 3 months prior to the study, who had a BMI (Body Mass Index) no greater than 35.0 kg/m\^2 and HbA1c no greater than 12.0%.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS (Full Analysis Set) All randomised subjects exposed to at least one dose of trial product with a post-baseline observation.

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 Change From Baseline in Insulin Detemir - Human Insulin Cross-reacting Antibodies, measured over week 0, week 52.

The primary endpoint was the change from baseline in insulin detemir–human insulin cross-reacting antibodies, measured from week 0 to week 52. Antibody concentration was measured as %B/T: the amount of tracer bound to antibodies in the precipitate, expressed as a percentage of the total tracer added to the mixture. The endpoint summarized the change ratio between baseline and the end of the trial; that ratio has no unit.

This measure addresses whether antibody response differed between the detemir production processes during the study period. It is a laboratory immunogenicity measure, not a direct measure of symptoms, clinical complications, glucose control or quality of life. The registry also lists hypoglycaemic episodes and several glycaemic-control measures as secondary outcomes, but those are not the primary endpoint.

In general, a prespecified primary endpoint gives a trial a central outcome for its main comparison and helps readers distinguish that question from the many additional outcomes that may be assessed. The registry record identifies the antibody measure and its timeframe, but details such as a clinically important threshold or a formal equivalence margin are not reported in the registry record.

7. Results Posted in the Registry

• NN729: mean 1.89 versus 1.81 on control; difference 0.08 (95% CI -0.11 to 0.27), standardized effect d = 0.09; z-test p = 0.419.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Detemir Specific Antibodies

• 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:
  • NN729: mean 1.06 versus 1.14 on control; difference -0.08 (95% CI -0.19 to 0.03), standardized effect d = -0.16; z-test p = 0.157.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NN729 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Total Antibodies

• 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:
  • NN729: mean 1.55 versus 1.55 on control; difference 0.00 (95% CI -0.14 to 0.14), 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 NN729 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 23 posted secondary outcomes among 24 outcome measures. These include hypoglycaemic episodes; changes in HbA1c and fasting plasma glucose; nine-point self-measured plasma glucose; detemir-specific and total antibodies; and selected haematology measures. This range covers safety, glycaemic control, immunogenicity and laboratory outcomes, so it addresses questions beyond the primary antibody comparison.

The secondary antibody measures are related to the primary endpoint because they also concern antibody responses, but they are not identical measures. The other secondary outcomes address different aspects of safety or glycaemic control. They should not be combined into a single conclusion about the primary endpoint, which was specifically the change in insulin detemir–human insulin cross-reacting antibodies.

The available registry summaries do not support a full directional synthesis across all secondary outcomes. Individual results are not included in the record details available for every listed outcome, and the listed outcomes differ in scale and subject matter. A result on one secondary measure cannot be assumed to apply to the others.

In general, unadjusted secondary results carry less weight as confirmatory evidence when many outcomes are tested. The chance of at least one apparently notable result can increase across multiple comparisons, even when no single effect is dependable. The registry record does not report whether a multiplicity adjustment was planned or applied. Secondary outcomes can still provide useful context, but they should be interpreted with their estimates, uncertainty, completeness and analysis plan in view rather than as independent confirmation of the primary result.

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

• Hypoglycaemic Episodes
• Glycaemic Control Parameters (Change in HbA1c)
• Glycaemic Control Parameters (Change in Fasting Plasma Glucose [FPG])
• Glycaemic Control Parameters (9-point Self Measured Plasma Glucose [SMPG])
• Change From Baseline in Detemir Specific Antibodies
• Change From Baseline in Total Antibodies
• Clinical Laboratory Values (Change in Haematology - Basophilis)
• Clinical Laboratory Values (Change in Haematology - Eosinophils)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the reported mean difference describe?

The arm summaries are means of a continuous measure. The primary endpoint reports the average change ratio for each group, and the re-calculation subtracts the NN304 mean from the NN729 mean. A positive mean difference therefore indicates a higher posted mean in the NN729 group for this particular measure; it does not by itself indicate a clinically better or worse outcome. The endpoint’s ratio scale and interpretation should be kept distinct from a difference between the two group means.

The re-calculation is unadjusted: it uses posted summary statistics rather than a participant-level model that could account for baseline values, stratification variables, repeated measures or other covariates. Such adjustments are not part of this simple calculation. The registry reports the sponsor’s own analysis separately as an ANOVA treatment ratio. ANOVA is a method for comparing group means under a specified model; the registry record does not give enough detail to reconstruct every element of that model.

What is a confidence interval?

In general, a confidence interval describes the range of estimates reasonably compatible with the data and the statistical method used. A narrower interval indicates greater precision for that estimate, while a wider interval indicates more uncertainty. The interval does not assign a probability to a fixed true value after the data have been observed. Its interpretation also depends on the model and assumptions underlying the analysis.

For a difference in means, an interval that spans zero is consistent with both a negative and a positive difference at the stated confidence level. That does not show that the true difference is exactly zero. For a ratio, the reference value is different from the reference for a difference; the ratio’s scale must be considered when interpreting its interval. The registry’s treatment-ratio result and the unadjusted mean-difference re-calculation therefore have distinct reference points and should be read according to their own scales.

What does a p-value say?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A p-value should be read alongside the estimate, its confidence interval, study design and analysis plan.

The registry reports p = 0.649 for the sponsor’s ANOVA treatment-ratio analysis; the simple unadjusted re-calculation reports p = 0.419. Neither value, considered alone, establishes that the production processes are equivalent. The registry record does not report a formal equivalence or non-inferiority margin against which to assess that claim.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model assumes. If variability is understated, standard errors may be too small and confidence intervals too narrow, making results appear more precise than they are. Appropriate methods for over-dispersed data depend on the outcome and model. The primary endpoint is summarized as a continuous measure with a standard error; the registry record does not describe a special over-dispersion adjustment, and the posted information does not establish that over-dispersion was present.

What are the analysis populations and limitations of summary-data calculations?

The primary population is defined as randomized participants exposed to at least one dose and with a post-baseline observation. This definition excludes participants without a post-baseline observation from that primary analysis population, but the reasons for missing observations and the methods used to handle missing data are not reported in the registry record. The arm counts for the primary measure are 158 and 152, while the safety risk sets are 164 and 166; these reflect different reported analysis contexts.

The re-calculation uses posted arm means, standard errors and sample sizes. It is a simple unadjusted calculation, not a reproduction of the participant-level analysis. In general, summary-data re-calculations can help readers understand the scale and precision of a comparison, but they cannot account for modeling details or adjustments that are not represented in the summaries. The registry’s own analysis remains the reported sponsor analysis, and the re-calculation should be understood as a complementary statistical reading rather than a replacement.

11. Confidence Intervals and Precision

The primary re-calculated mean difference is 0.08, with a 95% confidence interval from -0.114 to 0.274. The interval extends on both sides of zero, indicating that the posted summaries are compatible with a range of possible differences in either direction. Its width is important: the point estimate alone does not convey how uncertain the comparison is.

The registry’s own analysis reports a treatment ratio of 1.04, with a 95% confidence interval from 0.86 to 1.26. On a ratio scale, the reference value for no difference is 1, rather than zero. This interval also includes its no-difference reference value. The two intervals are expressed on different scales, so their numerical endpoints should not be compared as if they represented the same quantity.

In general, confidence intervals summarize statistical uncertainty under the analysis method; they do not address every source of uncertainty. For example, they do not resolve questions about missing data, the choice of endpoint, or whether the study population represents other settings. They also do not establish that any values within an interval are clinically unimportant. The registry record does not report a clinically meaningful threshold for the antibody endpoint.

Precision depends in part on the amount of information available and on variability. The primary endpoint summaries include 158 participants for NN304 and 152 for NN729, with a standard error of 0.07 in each arm. The reported interval gives a more direct sense of uncertainty about the between-group estimate than the p-value alone. Neither the interval nor the p-value establishes equivalence between the processes.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. This is a continuous-outcome comparison, and the registry’s planning illustration uses equal allocation between two arms. The stated assumptions are a two-sided significance level of 0.05, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 1,864 participants per arm for 80% power and 2,495 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,314 participants per arm for 80% power and 4,436 participants per arm for 90% power. Planning for 50% of the observed effect gives 7,455 participants per arm for 80% power and 9,980 participants per arm for 90% power.

In plain language, 80% power means that, under the stated planning assumptions and if the specified effect were real, the design would have an 80% chance of detecting an effect at the chosen significance level. The 90% column describes a higher planned chance of detection under the same kind of assumptions. Smaller effects require more participants to distinguish them from random variation with a similar chance of detection. These numbers are planning illustrations, not observed power and not the trial’s original design calculation.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = 0.080; pooled standard deviation σ = 0.872.
2. n = 2 × (1.96 + 0.842)² × 0.872² / 0.080² = 1,863.6, rounded up to 1,864 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.0799999999999998                      # observed difference in means
sigma <- 0.871657251238331                     # 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(447382)
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 = 1,864 (80% power), 2,495 (90% power)
 75% of observed effect: n per arm = 3,314 (80% power), 4,436 (90% power)
 50% of observed effect: n per arm = 7,455 (80% power), 9,980 (90% power)
power.t.test: 1864.5 
Simulated power at n = 1,864 per arm: 0.801 (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 reports the sponsor’s analysis as an ANOVA treatment ratio of 1.04, with a 95% confidence interval from 0.86 to 1.26 and p = 0.649. The simple re-calculation from the posted arm summaries instead gives a mean difference of 0.08, with a 95% confidence interval from -0.114 to 0.274 and an unadjusted p-value of 0.419.

These results are not direct numerical counterparts. The sponsor reports a treatment ratio, while the re-calculation is a difference between posted group means and does not reproduce the sponsor’s model. Both summaries show uncertainty around the comparison, but interpretation should preserve the distinction in scale and method. The registry record does not provide enough detail to reconstruct all aspects of the sponsor’s ANOVA.

No discrepancy is flagged between the posted sponsor result and the recalculation. The re-calculation is therefore best read as a transparent, unadjusted check based on summary data, not as a correction to or replacement for the registry’s own analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and a broad set of secondary outcomes. It lists 24 outcome measures, 23 posted secondary outcomes and 5 analyses. Testing multiple outcomes raises a multiplicity question: when many comparisons are made, some may appear notable by chance even if the underlying effects are absent. In general, statistical procedures can control error across a family of tests, but the appropriate approach depends on the trial’s planned questions and hierarchy.

Whether a correction or other multiplicity strategy was prespecified or used is not reported in the registry record. The record also does not state whether secondary outcomes were ordered in a testing hierarchy or intended to be exploratory. Consequently, the secondary findings should not be treated as though they necessarily had the same confirmatory status as the primary endpoint.

The primary analysis population is the Full Analysis Set, defined as randomized participants who received at least one dose and had a post-baseline observation. This is a specific population definition; it does not by itself explain how participants without a post-baseline measurement were handled, why observations were missing, or whether missingness differed between groups. Those missing-data details are not reported in the registry record. The methods for handling protocol deviations and the analysis population used for each secondary outcome are also not fully described in the record.

In general, missing-data assumptions matter because analyses can be affected when the availability of an outcome is related to participants’ characteristics or outcomes. The available arm counts differ by analysis context: primary endpoint summaries and safety risk sets use different counts. Those differences should be retained as reported rather than interpreted as evidence of a particular reason for missingness. Further details about imputation, sensitivity analyses, interim analyses and the planned statistical analysis are not reported in the registry record.

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: hypoglycaemic unconsciousness (1.8%), diabetic ketoacidosis (1.2%), gastroenteritis (1.2%), dehydration (0.6%), hypoglycaemic (0.6%).

The registry reports serious adverse events affecting 19 participants in the NN304 group among 164 at risk and 8 participants in the NN729 group among 166 at risk. It also reports other adverse events affecting 56 participants among 164 at risk for NN304 and 70 among 166 at risk for NN729. These are counts of participants affected and the corresponding risk sets, not measures of event severity beyond the serious-versus-other categories recorded.

The registry lists serious-event terms including hypoglycaemic unconsciousness at 1.8%, diabetic ketoacidosis at 1.2%, gastroenteritis at 1.2%, dehydration at 0.6%, hypoglycaemic at 0.6% and ketosis at 0.6%. The record does not specify the arm distribution for these listed terms in the details. Death counts are not reported in the registry record.

These figures describe reported events during the trial; they do not establish that an event was caused by a treatment or allow a complete assessment of comparative safety. In general, adverse-event counts should be interpreted with the observation period, definitions, participant exposure and completeness of reporting in mind. Further detail on those matters is not reported in the registry record.

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

The posted primary results describe the antibody change ratio over the trial period for two groups receiving detemir made by different production processes, together with mealtime insulin aspart. The registry’s own analysis and the simple unadjusted re-calculation both leave uncertainty around the between-group comparison. The reported estimates do not establish a clear difference in the primary measure, but they also do not prove that the processes produce identical results.

A finding that does not establish a difference is not automatically evidence of equivalence. Equivalence or non-inferiority requires a prespecified margin and a design and analysis that assess whether the uncertainty is sufficiently narrow relative to that margin. Such a margin is not reported in the registry record. The confidence interval therefore cannot be read as a formal demonstration that any difference is acceptably small.

The primary endpoint is an antibody measure. It does not by itself answer whether participants had different clinical outcomes, glucose control or quality of life. The registry lists those kinds of measures among the secondary outcomes, but their presence does not change what the primary endpoint represents.

The results apply to the reported study setting and population as described in the record: people with type 1 diabetes receiving a basal-bolus regimen, with individualized detemir and mealtime aspart. The record does not provide enough detail to assess how well the findings apply to populations or regimens not described. No medical conclusion or treatment recommendation follows from the antibody comparison alone.

18. Why This Trial Matters Statistically

This trial illustrates why the scale of an endpoint matters. The primary outcome is a change ratio in antibody levels, while the sponsor’s reported comparison is a treatment ratio and the simple re-calculation is a mean difference. Each is a legitimate statistical summary of a particular quantity, but their values and reference points cannot be read as though they were the same measure.

It also illustrates the distinction between failure to establish a difference and evidence of equivalence. The primary interval includes the no-difference value, yet interpretation of equivalence would require a margin and corresponding analysis. Those details are not reported in the registry record, so the posted result should be described as uncertain rather than as proof that the processes are identical.

The trial’s numerous secondary outcomes raise the importance of multiplicity and outcome hierarchy. Results across antibodies, hypoglycaemia, glycaemic control and laboratory values answer distinct questions. Without a reported multiplicity strategy, secondary findings warrant cautious interpretation and should not be treated as a collection of independent confirmations.

Finally, the registry provides multiple analysis contexts, including the primary Full Analysis Set and safety risk sets. Keeping those populations distinct helps prevent misleading comparisons. Together, these features make the trial a useful example of reading an endpoint, estimate, interval, sponsor analysis and planning illustration in context, rather than reducing the statistical interpretation to a single p-value.

19. Limitations

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

The registry record leaves important design and analysis details unspecified. The original sample-size justification, full statistical analysis plan, randomization implementation, allocation concealment, details of blinding, interim analyses and missing-data methods are not reported in the registry record. These omissions limit how fully the sponsor analysis can be reconstructed and how the planned status of secondary findings can be assessed.

The primary endpoint is a laboratory antibody measure. The record does not report a clinically meaningful threshold or a formal equivalence or non-inferiority margin for interpreting the comparison. The trial’s 52-week treatment period also defines the timeframe of the reported comparison; longer-term outcomes are not described in the primary endpoint information.

The primary endpoint counts and safety risk sets are not the same, and the record does not explain all differences between analysis populations. The Full Analysis Set requires exposure and a post-baseline observation. Reasons for absence of observations and sensitivity analyses addressing missing data are not reported in the registry record.

The record describes sites in five countries and a basal-bolus regimen using individualized detemir and mealtime aspart. It does not include detailed demographic or baseline clinical characteristics in the registry record for this interpretation. Consequently, the extent to which the enrolled participants represent other groups or treatment settings cannot be assessed from these details alone. The wide set of secondary outcomes also complicates interpretation because the multiplicity plan is not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety of Insulin Detemir Produced by a New Process as Measured by Antibody Formation in Subjects With Type 1 Diabetes — NCT00447382.
• Registry record last updated 2024-01-02; status last verified 2023-12.
• Results first posted 2011-05-12.
• 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

NCT00447382 is a completed phase 3 randomized, double-blind, parallel-group trial comparing insulin detemir produced by the NN729 process with detemir produced by the NN304 process in people with type 1 diabetes. The regimen included individualized basal detemir and mealtime insulin aspart. The official title describes a 12-month comparison, and the arm descriptions specify 52 weeks.

The primary endpoint was change from baseline to week 52 in insulin detemir–human insulin cross-reacting antibodies. The registry reports an ANOVA treatment ratio of 1.04, with a 95% confidence interval from 0.86 to 1.26 and p = 0.649. The unadjusted re-calculation from posted summaries gives a mean difference of 0.08, with a 95% confidence interval from -0.114 to 0.274 and p = 0.419.

The registry lists 23 posted secondary outcomes, but multiplicity procedures, the original sample-size justification and details of missing-data handling are not reported in the registry record. The findings describe the recorded antibody comparison and should not be interpreted as proof of equivalence or as a clinical treatment recommendation.