Phase II Trial of Combination Immunotherapy With NeuVax and Trastuzumab in High-risk HER2+ Breast Cancer Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase II Trial of Combination Immunotherapy With NeuVax and Trastuzumab in High-risk HER2+ Breast Cancer Patients (NCT02297698), a randomized phase 2 study. The primary outcome is Invasive Disease-free Survival (DFS).

2. Clinical Question

The trial asks whether adding nelipepimut-S to trastuzumab and GM-CSF is associated with a different invasive disease-free survival outcome than trastuzumab and GM-CSF alone in the registry’s high-risk population. The primary outcome definition includes invasive local, regional, or distant recurrence, a new primary, or death due to any cause. Disease state was to be determined by patients’ physicians during routine follow-up.

The eligibility description includes patients who received neoadjuvant therapy with an approved trastuzumab-containing regimen and taxane-containing chemotherapy but did not achieve a pathologic complete response; patients with at least 4 positive lymph nodes after surgery as the first intervention; and patients with hormone receptor-negative disease and 1-3 positive lymph nodes after surgery as the first intervention. These are the registry’s criteria, not a basis for assuming that all people with HER2-positive disease are represented.

The randomized comparison therefore concerns a specific post-treatment, high-risk setting and a specific add-on immunotherapy strategy. It does not directly answer questions about other patient groups, other treatment regimens, or outcomes beyond those recorded in the trial.

3. Trial Design

The registry identifies NCT02297698 as a completed phase II, randomized, single-blinded, parallel-group trial sponsored by Cancer Insight, LLC. The listed enrollment is 100. The recorded start is 2014-10, and primary completion is recorded as 2021-12. The brief summary describes the study as multicenter and prospective.

Participants were randomized to trastuzumab plus NeuVax or trastuzumab plus GM-CSF. The posted outcome groups each contain 50 participants. The NeuVax arm is described as nelipepimut-S plus GM-CSF; the comparison arm received GM-CSF alone in an otherwise identical manner. The arm description states that participants were blinded to whether they received nelipepimut-S/GM-CSF or GM-CSF alone. The record does not identify the other party, if any, who was blinded.

For the primary outcome, follow-up is described from initiation of trastuzumab monotherapy through the end of the patient’s fifth year of study participation. The registry says disease state was assessed by patients’ own physicians during routine follow-up, approximately every three months for the first 24 months after completion of primary therapies and every six months thereafter, using clinical examination and laboratory and radiographic surveillance.

The trial also posted secondary outcomes for local and systemic toxicities and in vivo and in vitro immune responses. The toxicity timeframe extends from initiation of the vaccine or inoculation series and booster series up to 36 months. The immune-response timeframe extends from the first inoculation of trastuzumab monotherapy to the end of the fifth year of participation.

Details of the randomization procedure, allocation concealment, stratification, and the trial’s original sample-size justification are not reported in the registry record. The registered design and posted results should therefore be interpreted without assuming those procedures.

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

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 Invasive Disease-free Survival (DFS), measured over Initiation of trastuzumab monotherapy through the end of the patient's fifth year of participation in the study..

The primary endpoint is invasive disease-free survival (DFS). The registry defines it as the time from initiation of trastuzumab maintenance therapy to invasive local, regional, or distant recurrence, a new primary, or death due to any cause. The outcome is intended to capture whether a participant remains free of these specified events over follow-up, rather than measuring tumor response at a single visit.

Time-to-event endpoints are commonly used when the timing of recurrence or death matters and participants may have different lengths of follow-up. They can use information about when an event occurred, while accounting for participants whose event has not been observed by the end of available follow-up. That is a general statistical rationale for a survival endpoint; it does not establish which specific analytic methods were used in this trial.

The registry describes a follow-up schedule and identifies invasive DFS as the primary outcome. However, the posted primary results are participant counts by group, with a binary comparison, rather than a reported hazard ratio, median DFS, or event-time analysis. The time-to-event analysis method, handling of censoring, and detailed endpoint adjudication procedures are not reported in the registry record. Consequently, the posted summary does not by itself show the shape of the event-time experience or how the timing of events contributed to the comparison.

The endpoint is clinically relevant to the trial question because it covers invasive recurrence, a new primary, and death. Its interpretation still depends on how consistently those events were identified and analyzed, details that are not fully reported in the registry record.

7. Results Posted in the Registry

• Trastuzumab + GM-CSF: 94.0% (47/50) versus 84.0% (42/50) on control; risk difference 10.0 percentage points (95% CI -2.1 to 22.1), risk ratio 1.12 (0.97–1.29); unadjusted two-proportion z-test p = 0.110.

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.

Local and Systemic Toxicities

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Trastuzumab + GM-CSF: 86.0% (43/50) versus 92.0% (46/50) on control; risk difference -6.0 percentage points (95% CI -18.2 to 6.2), risk ratio 0.93 (0.81–1.07); unadjusted two-proportion z-test p = 0.338.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trastuzumab + GM-CSF and the control. The interval gives the range of effects that remain compatible with the data.

Evaluate in Vivo and in Vitro Immune Responses

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Trastuzumab + GM-CSF: 10.0% (5/50) versus 10.0% (5/50) on control; risk difference 0.0 percentage points (95% CI -11.8 to 11.8), risk ratio 1.00 (0.31–3.24); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trastuzumab + GM-CSF and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of the trial: local and systemic toxicities, and in vivo and in vitro immune responses. Taken together, their posted estimates do not form a consistent pattern of advantage across outcomes. The toxicity comparison and immune-response comparison concern different constructs, timeframes, and outcome definitions, so they should not be combined into a single summary of treatment effect.

These outcomes complement the primary invasive DFS question but do not answer it. Toxicity findings describe reported harms during the specified observation period; immune-response findings describe recorded immune outcomes. Neither is a substitute for recurrence, new primary disease, or death as defined in the primary endpoint. Likewise, a secondary result cannot clarify the timing of primary events when the posted primary comparison is a binary summary.

The registry reports unadjusted comparisons and no reported analyses for the secondary outcomes. Multiple outcomes create opportunities for chance findings, and the record does not describe a multiplicity adjustment or a hierarchy specifying which secondary tests were confirmatory. For that reason, secondary estimates carry less weight as evidence of treatment-group differences than a prespecified, adequately powered primary analysis would carry. This does not make them irrelevant: they provide descriptive context and can inform questions for future research, while remaining uncertain.

The registry does not report whether the secondary outcomes were analyzed according to a prespecified statistical plan, how missing observations were handled, or whether participants were assessed consistently across sites. Those omissions limit the strength of conclusions from the secondary results. The overall reading is therefore cautious: the secondary outcomes broaden the description of safety and immune response, but they neither establish a coherent treatment effect nor overturn the uncertainty in the primary comparison.

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

• Local and Systemic Toxicities
• Evaluate in Vivo and in Vitro Immune Responses

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical summaries help describe the randomized comparison, but they answer different questions. The primary outcome is labeled invasive DFS, while the posted group results are participant counts and the comparison is binary. The registry also posts a risk difference, a risk ratio, an odds ratio, confidence intervals, and unadjusted p-values. These measures should be read together rather than treated as interchangeable.

What does the risk difference express?

A risk difference is an absolute contrast between the proportions with the recorded outcome in two groups. It is expressed on the probability scale, so zero represents no difference. The registry’s primary risk difference is 0.1, comparing trastuzumab plus GM-CSF with trastuzumab plus NeuVax. The positive direction follows that comparison order: the posted outcome proportion is higher in the GM-CSF group. Because the outcome is identified as invasive DFS, that direction describes the posted DFS summary; it should not be extended to other outcomes or to an unreported event-time analysis.

The risk difference is often easier to interpret in absolute terms than a relative measure. It still depends on how the outcome was defined, which participants were included, and whether follow-up and missing observations were handled appropriately. Those analysis details are not fully reported in the registry record.

How do relative measures differ?

A risk ratio compares the outcome proportions as a ratio. A value of 1 represents equal proportions; values on either side describe relative differences, with direction depending on the group order and outcome coding. The posted primary risk ratio is 1.119. An odds ratio compares odds rather than proportions. Its no-association value is also 1, but odds are not the same quantity as probabilities. The posted primary odds ratio is 2.984.

Risk ratios and odds ratios can look more dramatic than an absolute risk difference, especially when the outcome is common. They do not replace the absolute group summaries. The confidence intervals for both relative measures include 1, so the estimates remain compatible with no relative difference as well as with differences in either direction.

What does a confidence interval communicate?

A confidence interval gives a range of effect estimates compatible with the observed data under the method’s assumptions. It is not a guarantee that the true effect lies within the particular interval, and it does not assign a probability to individual values within the range. A narrower interval indicates more precision; a wider interval indicates greater uncertainty. The primary risk-difference interval extends from -0.021 to 0.221, crossing zero. That range allows the possibility of a small difference in the opposite direction from the point estimate as well as a larger positive difference. The relative-effect intervals also cross their no-difference value of 1.

What does the p-value say?

The primary unadjusted p-value is 0.11. A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it is not a measure of effect size or clinical importance. A value above a conventional threshold does not prove there is no effect; it indicates that the analysis did not provide strong evidence against the null model at that threshold. The planning assumptions list a two-sided significance level of 0.05, but the trial’s own original statistical plan is not reported in the registry record.

All listed comparison p-values are unadjusted. Where multiple outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. General statistical practice may address this through a prespecified multiplicity strategy, but whether one was planned or used in this trial is not reported in the registry record. The secondary results should not be interpreted as if they were adjusted confirmatory tests.

Why does the endpoint analysis matter?

In general, a time-to-event analysis uses both whether an event occurred and when it occurred. It also needs a defined approach for participants whose event has not been observed by the end of follow-up. A simple binary summary does not communicate all of that timing information. Although invasive DFS is defined as a time-to-event outcome, the registry results posted for this comparison are counts and binary summaries. The statistical model, censoring rules, and any adjustment for follow-up are not reported in the registry record. This distinction limits the conclusions that can be drawn from the posted summaries.

The registry record reports no analysis entries for the primary or secondary outcomes. The comparisons described in the posted results therefore do not document a sponsor-reported adjusted model. The registry also does not report the original analysis plan, interim analyses, analysis-population definitions, or missing-data methods. Without those details, the estimates are best read as the unadjusted comparisons that they are, with uncertainty represented by their confidence intervals.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.1, with a 95% confidence interval from -0.021 to 0.221. Because the interval crosses zero, the posted results are compatible with no absolute difference as well as with a difference in either direction. The interval’s positive end allows a larger increase in the outcome proportion in the comparison group than its negative end allows in the opposite direction. The point estimate alone would conceal that uncertainty.

The relative estimates are also imprecise. The risk ratio is 1.119, with a 95% confidence interval from 0.973 to 1.287. The odds ratio is 2.984, with a 95% confidence interval from 0.743 to 11.99. Both intervals include 1, the no-relative-difference value. The broad odds-ratio interval in particular permits a wide range of relative effects and should not be read as a precise estimate merely because its point estimate is above 1.

A confidence interval reflects sampling uncertainty under the statistical method used. It does not cover every possible source of uncertainty. For example, uncertainty about outcome classification, missing observations, follow-up, or the analysis model is not necessarily captured by the interval. The registry record does not report enough detail to assess all of those issues.

In general, precision tends to improve with more information, but event frequency, allocation, follow-up, and the analysis method also matter. The registered enrollment and group summaries provide context, but the posted confidence intervals are the most direct indication of the uncertainty in these effect estimates. They do not support a precise conclusion about the size or direction of a treatment-group difference.

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 per arm, not totals or event counts. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation uses the observed effect as its starting point and considers detecting 100%, 75%, or 50% of that observed effect. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect were the true one. The 90% power column expresses the corresponding planning target for a 90% chance. These are design probabilities under a model, not guarantees about the results of a future study. For each assumed effect fraction, the corresponding per-arm figures are listed in the registry-derived planning display.

The displayed planning values rise as the assumed effect becomes smaller. This is the usual relationship: a smaller difference is harder to distinguish from random variation, so a larger study is generally needed to achieve the same planned power under otherwise similar assumptions. The figures are illustrations based on the observed effect in this trial, rather than a record of the trial’s actual design rationale. They should not be treated as a recommendation for a future study without considering its target population, endpoint, follow-up, and analysis plan.

This is not observed power. Observed power is not a useful substitute for reading the estimated effect and its confidence interval; the planning figures instead show how sample-size requirements change under stated assumptions.

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 = 0.840; treatment proportion p₁ = 0.940; average p̄ = 0.890.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4425 = 0.8673.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4368 = 0.3676.
4. n = (0.8673 + 0.3676)² / (0.1000)² = 152.5, rounded up to 153 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 <- 0.84                          # control proportion
p1 <- 0.94                          # 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(2297698)
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 = 153 (80% power), 204 (90% power)
 75% of observed effect: n per arm = 299 (80% power), 400 (90% power)
 50% of observed effect: n per arm = 733 (80% power), 980 (90% power)
power.prop.test: 152.5 
Simulated power at n = 153 per arm: 0.813 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and two secondary outcomes. Examining multiple outcomes can increase the chance of observing an apparently notable result by chance, especially when many comparisons are made. Statistical plans often address this issue by defining a testing hierarchy, adjusting significance thresholds, or identifying analyses as exploratory. A multiplicity strategy for this trial is not reported in the registry record. The posted secondary comparisons are unadjusted, so they should not be treated as confirmatory evidence without further information.

The record does not report the trial’s full statistical analysis plan, whether any interim analyses were planned or conducted, or the criteria for stopping or continuing the study. It also does not state whether the posted results follow an intention-to-treat, per-protocol, or other analysis population. Randomization supports a fair comparison when preserved in analysis, but the analysis population and treatment of participants after randomization affect how that comparison is interpreted.

Missing-data procedures are not reported in the registry record. For an outcome involving follow-up over time, it matters whether participants had complete outcome assessment, how withdrawals and loss to follow-up were handled, and whether observations were censored or otherwise excluded. The registry gives the planned surveillance schedule but does not provide a detailed account of missingness or censoring in the posted results.

Also not reported are the randomization sequence-generation method, allocation concealment, stratification factors, endpoint adjudication procedures, and any covariate-adjusted primary model. The record’s primary results are presented as participant counts and an unadjusted binary comparison, although invasive DFS is defined as a time-to-event outcome. These reporting gaps do not prove that procedures were absent; they mean that they are not documented in the registry record. They limit assessment of multiplicity, missing data, and the exact analysis population and should temper any strong claim based on the posted comparisons.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: left breast infection (2.0%), fever (2.0%), unintended pregnancy (2.0%), procedural complication-tram flap failure (2.0%), sepsis (2.0%).

The registry separates serious adverse events from other adverse events and reports participant counts by randomized group. It lists 3 participants with serious adverse events in the trastuzumab plus NeuVax group and 5 in the trastuzumab plus GM-CSF group. For other adverse events, the posted counts are 43 and 38, respectively. Deaths are listed as 0 and 1, respectively. These are descriptive counts, not proof that the treatment assignment caused or prevented an event.

The listed serious-event terms include Left Breast Infection, Fever, Unintended Pregnancy, Procedural Complication-Tram Flap Failure, Sepsis, and UTI - Pyelonephritis, each recorded as 2.0%. These terms should be read as the registry’s listed categories; the record does not establish that they are mutually exclusive or that each was judged related to study treatment.

Although each group’s adverse-event denominator is recorded as 50 at risk, counts alone do not describe event timing, duration, severity beyond the registry’s serious/non-serious classification, or attribution. The safety summaries are useful for describing what was recorded, but the registry does not report a detailed comparative safety analysis or causal assessment.

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

The primary result describes a numerical difference in the posted invasive DFS summaries between the randomized groups. The point estimate favors a higher recorded DFS proportion in the trastuzumab plus GM-CSF comparison group, but the confidence interval crosses no difference and the unadjusted p-value does not provide strong evidence of a between-group difference. The result is therefore uncertain rather than proof of benefit, harm, or equivalence.

It does not establish that adding nelipepimut-S improves or worsens outcomes. It also does not establish that the regimens are equivalent: absence of clear evidence for a difference is not evidence that all clinically relevant differences have been ruled out. The confidence interval allows a range of plausible effects, and the registry does not report a time-to-event model that would show how event timing and follow-up contributed to the comparison.

The findings apply most directly to the high-risk HER2-positive population described in the registry and to the tested treatment comparison. The results should not automatically be extended to people outside the stated eligibility categories, to other treatment settings, or to outcomes not assessed. The trial’s primary endpoint includes invasive recurrence, a new primary, and death, but the posted summary does not separately report those components.

The secondary results provide descriptive information on toxicity and immune response, but they are unadjusted and do not replace the primary endpoint. The record does not report a multiplicity procedure, missing-data handling, or a detailed analysis population. Those omissions further limit how strongly any single posted comparison can be interpreted.

In general, randomized trials can estimate comparative effects, but the strength of the conclusion depends on the study design, outcome measurement, completeness of follow-up, and analysis. Here, the registry supports a cautious statement about the observed summaries and their uncertainty. It does not justify a medical recommendation or a claim that one regimen works or does not work.

17. Why This Trial Matters Statistically

This trial is statistically instructive because the primary endpoint is defined as a time-to-event outcome, while the posted comparison is presented as participant counts and a binary risk difference. Those summaries communicate the recorded group proportions, but they do not reveal the timing of recurrence or death. Recognizing the distinction prevents a binary comparison from being mistaken for a complete survival analysis.

The result also illustrates why estimates and confidence intervals matter more than a threshold-only reading of a p-value. The primary point estimate is positive in the comparison order, yet its confidence interval includes zero and the relative-effect intervals include 1. The data therefore leave substantial room for uncertainty about the effect’s size and direction. A p-value alone would not convey that range.

The trial’s randomized parallel-group design is relevant to causal comparison, but randomization does not eliminate the need to understand the analysis population, follow-up, endpoint ascertainment, and missing-data procedures. The registry record does not report several of these details. Statistical interpretation should distinguish information that is recorded from assumptions that cannot be checked in the registry.

The secondary outcomes and safety counts also demonstrate the importance of outcome hierarchy and multiplicity. Several outcomes can add useful context, but unadjusted comparisons should not be treated as multiple independent confirmations. The registry’s lack of a reported multiplicity plan makes a cautious interpretation especially important.

Finally, the planning illustrations show how assumptions about the effect to detect influence sample-size requirements. They are based on the observed effect and do not explain the trial’s original design. Separating planning illustrations from observed findings avoids confusing a design exercise with evidence about the strength of the completed trial.

18. Limitations

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

Several limitations are specific to how this trial’s results are recorded. The primary endpoint is invasive DFS over follow-up through the patient’s fifth year of participation, but the posted primary comparison is a binary participant-count summary. The registry does not report a hazard ratio, median DFS, survival curve estimate, censoring rules, or a time-to-event model. Thus, the posted comparison does not show when events occurred or how differences in follow-up were handled.

The registry describes physician assessment during routine surveillance, but it does not report whether outcomes were centrally adjudicated, whether assessors were blinded, or how disagreements in disease classification were resolved. The record identifies the study as single-blinded and describes participants as blinded to the control assignment, but does not specify all parties who were blinded.

The record does not report the analysis population, missing-data methods, baseline characteristics, randomization procedure, allocation concealment, stratification, or an adjusted analysis. It also does not document an original sample-size justification or a multiplicity plan. These omissions prevent a full assessment of balance, potential bias, and the prespecified statistical approach.

The reported secondary outcomes have distinct definitions and timeframes, and their analyses are unadjusted. Safety information is presented as counts and listed terms without a detailed attribution analysis. The registry summaries therefore support descriptive interpretation but leave important questions about completeness, timing, and analysis unresolved.

These are reporting limitations in the registry record; they do not establish that the trial did not use additional procedures or analyses. They do mean that those procedures cannot be evaluated from the record, and that the posted results should not be interpreted more strongly than their documented methods allow.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase II Trial of Combination Immunotherapy With NeuVax and Trastuzumab in High-risk HER2+ Breast Cancer Patients — NCT02297698.
• Registry record last updated 2023-12-12; status last verified 2023-11.
• Results first posted 2023-12-12.
• 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.

22. Record Summary

NCT02297698 is a completed, randomized, single-blinded phase II parallel-group trial of trastuzumab plus NeuVax versus trastuzumab plus GM-CSF alone in high-risk HER2-positive breast cancer. The registry lists enrollment of 100 and identifies invasive DFS as the primary outcome.

The posted primary summaries show 42 participants in the trastuzumab plus NeuVax group and 47 in the trastuzumab plus GM-CSF group. The risk-difference estimate is 0.1, with a 95% confidence interval from -0.021 to 0.221 and an unadjusted p-value of 0.11. The interval includes no difference, leaving the comparative result uncertain.

Secondary outcomes concern local and systemic toxicities and immune responses. Safety summaries include serious and other adverse-event counts and deaths. The registry record does not report key details of the statistical analysis plan, missing-data handling, analysis populations, or time-to-event methods. Interpretation should therefore remain tied to the posted summaries and their documented uncertainty.