Study of Tecemotide (L-BLP25) in Subjects With Slowly Progressive Multiple Myeloma With no Symptoms and Who Have Had no Chemotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Tecemotide (L-BLP25) in Subjects With Slowly Progressive Multiple Myeloma With no Symptoms and Who Have Had no Chemotherapy (NCT01094548), a randomized phase 2 study. The primary outcome is Number of Participants With Overall Induced Mucinous Glycoprotein-1 (MUC-1)-Specific Immune Response.

2. Clinical Question

3. Trial Design

This was a randomized, open-label, parallel-group Phase II study of tecemotide (L-BLP25) in people with multiple myeloma. The two named regimens were tecemotide plus single low dose cyclophosphamide and tecemotide plus multiple low dose cyclophosphamide. The registry lists 34 participants enrolled. For the primary outcome, the arm counts were 17 and 15, respectively; the safety record lists 17 participants at risk in each group. Those figures refer to different posted outcome records and should not be treated as interchangeable denominators.

The official title describes eligibility as either chemotherapy-naïve, slowly progressive, asymptomatic multiple myeloma or Stage II/III multiple myeloma in a stable response or plateau phase after anti-tumor therapy. The registry does not report how participants in these disease categories were distributed between the study arms. It also does not provide further details in the arm descriptions about the cyclophosphamide schedules.

The primary outcome was the number of participants with an overall induced MUC1-specific immune response, assessed from randomization up to Week 104. The listed assays were lymphoproliferation, ELISPOT for interferon gamma, and intracellular interferon gamma cytokine assay in peripheral blood mononuclear cells. Secondary outcomes included immune-response measures, objective clinical response, time to progression, time to anti-tumor therapy, and adverse events. Six secondary outcomes are posted in the registry record.

The study status is completed. The recorded start was 2008-01 and primary completion was 2011-02. The original trial’s sample-size justification, detailed statistical plan, and any interim-analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: A total of 36 participants were screened for eligibility; 2 were excluded (mainly non-fulfillment of inclusion or exclusion) and 34 participants were enrolled and randomized.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Immunological diagnostic analysis set was defined as the subset of safety analysis set consisting of all the participants with at least one complete set of baseline (baseline/cyclophosphamide infusion visit or both), Week 5, and Week 9 data of either ELISPOT, proliferation assay or cytokine assay.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety analysis set included all the randomized participants who received at least 1 dose of trial treatment.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Overall Induced Mucinous Glycoprotein-1 (MUC-1)-Specific Immune Response, measured over From the date of randomization up to Week 104.

The primary endpoint counts participants who met a specified definition of overall induced MUC1-specific immune response. The registry required a response at least for two timepoints. At least one parameter in at least one of the lymphoproliferation, ELISPOT, or intracellular cytokine assays had to meet the stated response criteria, which included a ratio to background of at least 2 and a ratio of the background-corrected value to baseline of at least 2. The assay description also defines a timepoint-specific response using the difference between stimulated and unstimulated log-scale values and, for ELISPOT and proliferation assays, a comparison that accounts for standard errors.

This kind of endpoint is used to record whether a participant meets a predefined laboratory-response threshold, rather than to quantify a continuous change in symptoms or disease status. The registry’s stated purpose was to ascertain whether tecemotide induced a MUC1-specific T-cell response. A count of participants meeting the rule can therefore describe the frequency of the defined immune response in each regimen group. It does not by itself establish a clinical benefit or show how a laboratory response relates to later clinical outcomes.

The endpoint population was the immunological diagnostic analysis set: participants in the safety analysis set with at least one complete baseline, Week 5, and Week 9 data set from one of the listed assays. The registry reports 8 participants in the single low-dose group and 7 in the multiple low-dose group as having the outcome. How incomplete assay data were handled beyond the stated population definition is not reported in the registry record.

7. Results Posted in the Registry

• Tecemotide (L-BLP25) Plus Multiple Low Dose Cyclophosphamide: 46.7% (7/15) versus 47.1% (8/17) on control; risk difference -0.4 percentage points (95% CI -35.0 to 34.3), risk ratio 0.99 (0.47–2.08); unadjusted two-proportion z-test p = 0.982.

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.

Time to Progression (TTP)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Tecemotide (L-BLP25) Plus Single Low Dose Cyclophosphamide vs Tecemotide (L-BLP25) Plus Multiple Low Dose Cyclophosphamide: hazard ratio 0.43 (95% CI 0.16–1.19), reported p = 0.094 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Tecemotide (L-BLP25) Plus Single Low Dose Cyclophosphamide vs Tecemotide (L-BLP25) Plus Multiple Low Dose Cyclophosphamide and the control. The interval gives the range of effects that remain compatible with the data.

Time to Anti-tumor Therapy

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Tecemotide (L-BLP25) Plus Single Low Dose Cyclophosphamide vs Tecemotide (L-BLP25) Plus Multiple Low Dose Cyclophosphamide: hazard ratio 0.67 (95% CI 0.26–1.70), reported p = 0.392 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Tecemotide (L-BLP25) Plus Single Low Dose Cyclophosphamide vs Tecemotide (L-BLP25) Plus Multiple Low Dose Cyclophosphamide and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span immune-response measures, clinical response, time to progression, time to anti-tumor therapy, and adverse events. The results that are numerically reported include the two time-to-event comparisons and safety counts. The registry outcome list also names immune and objective clinical response measures, but numerical results for those outcomes are not reported in the registry record summarized in this account. The available secondary results therefore do not support a complete assessment of all listed outcomes.

The time-to-event estimates show numerically different medians between the regimens, but their hazard-ratio confidence intervals include 1 and the reported p-values do not provide clear evidence of a difference. This uncertain pattern does not strengthen or overturn the primary immune-response finding. The primary endpoint records a laboratory-defined response, whereas progression and initiation of anti-tumor therapy are different outcomes. Similarity or difference in one domain cannot be assumed to establish the same pattern in another.

Secondary outcomes are often interpreted more cautiously because a study may examine several outcomes, timepoints, or analysis groups. If many comparisons are tested without adjustment, the chance of at least one apparently unusual result can increase. The registry does not report whether a multiplicity adjustment was planned or used, nor does it provide a complete numerical set of results for all listed secondary outcomes. Consequently, isolated secondary findings, where available, carry less weight than a prespecified primary analysis and should be considered exploratory unless the analysis plan establishes otherwise.

The registry record does not document a hierarchy among the secondary outcomes or identify which were confirmatory. That missing context prevents a reliable distinction between planned confirmatory analyses and exploratory analyses. The overall secondary pattern is therefore best described as incomplete and uncertain, rather than as corroboration of a clinical effect.

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

• Number of Participants With Baseline Immune Response and Initial Increase of MUC1 Specific Immune Response
• Number of Participants With Overall Induced Immune Response by Human Leukocyte-associated Antigen (HLA) Type
• Percentage of Participants With Objective Clinical Response (Complete Response [CR], or Partial Response [PR], or Minimal Response [MR]
• Time to Progression (TTP)
• Time to Anti-tumor Therapy
• Number of Participants With Treatment Emergent Adverse Events (TEAEs),Serious TEAEs, TEAEs of Grade 3 or 4 According to NCI-CTCAE v3.0, TEAEs Leading to Discontinuation and Injection Site Reactions (ISRs)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s posted analyses use methods suited to the outcome types: Fisher Exact for the binary primary response and Log Rank analyses for time-to-event outcomes. The calculations accompanying the posted summaries also include unadjusted comparisons. These methods answer related but distinct questions, so their estimates and p-values should be read in context rather than treated as interchangeable evidence.

What does the primary comparison measure?

The primary endpoint is binary at the participant level: a participant either meets the overall induced immune-response definition or does not. The reported counts are 8 of 17 for tecemotide plus single low dose cyclophosphamide and 7 of 15 for tecemotide plus multiple low dose cyclophosphamide. A risk difference expresses the difference between the groups’ observed event proportions, with the multiple-dose group compared against the single-dose group in the recalculation. Its estimate is -0.004. The corresponding interval, -0.350 to 0.343, includes zero, the value representing no difference in the underlying proportions.

Fisher Exact is a method for testing association in a small two-by-two count table. It evaluates how compatible the observed counts are with a null hypothesis of no association, given the fixed margins used by the test. The registry reports p = 1.000. A p-value is not the probability that the null hypothesis is true, nor is it a measure of the size or importance of a difference. It describes how unusual the observed data, or data more extreme under the test’s definition, would be if the null hypothesis held.

The unadjusted recalculation gives p = 0.982. This is close to the sponsor’s reported Fisher Exact p-value, and the registry indicates no discrepancy. A small difference between two p-values can arise from different calculation conventions, but the registry does not give enough detail to identify a specific reason. The sponsor’s reported analysis remains the registry’s formal result.

How should time-to-event analyses be read?

Time to progression and time to anti-tumor therapy are time-to-event outcomes. A median time is the point at which the estimated event-time distribution reaches its midpoint; it is not an average and does not describe every participant’s experience. The median estimates are accompanied by confidence intervals where reported. An upper confidence limit is not reported for the multiple-dose group’s time-to-progression median, and upper limits are also not reported for either group’s time-to-anti-tumor-therapy median.

The Log Rank method compares event-time patterns across groups while accounting for the ordering of event times. The registry reports hazard ratios of 0.431 for time to progression and 0.666 for time to anti-tumor therapy, with p-values of 0.094 and 0.392. A hazard ratio is a relative measure of event rates over follow-up under the model’s interpretation; it is not a ratio of medians. Its meaning depends on the group order and event definition. The posted comparisons identify the comparison as single-dose versus multiple-dose, and the hazard ratios should be read with that stated order in mind.

The confidence intervals for these hazard ratios include 1, the reference value for equal hazards. That means the posted data do not rule out the no-difference value at the reported interval level. The p-values likewise do not show strong evidence against the null comparison. Neither result proves that the underlying hazards are identical: limited event information can leave considerable uncertainty. The registry does not report the number of events contributing to each analysis or the detailed handling of censoring.

Why can count-based and time-to-event results differ?

The primary outcome records a participant-level laboratory response under a specific assay rule. The secondary time-to-event outcomes concern progression or the time to further anti-tumor therapy. They differ in endpoint, timing, and analysis population requirements. A pattern in one outcome need not reproduce in another, and a laboratory response cannot be treated as a substitute for a clinical event outcome. The registry’s outcome descriptions do not establish that immune response predicts either time-to-event outcome.

General statistical point: confidence intervals describe a range of estimates compatible with the data under the method’s assumptions. Wide intervals indicate limited precision. For time-to-event outcomes, fewer observed events generally mean less information about the hazard comparison. The event counts and the assumptions used in the trial’s original design are not reported in the registry record, so the precision of those analyses cannot be attributed to a particular number of events or design target.

What is not documented?

The registry does not report the original statistical analysis plan, the original sample-size justification, an interim-analysis plan, or a multiplicity adjustment procedure. It also does not describe missing-data methods for the secondary outcomes. These omissions limit reconstruction of the intended analysis and make it difficult to assess whether the posted analyses were prespecified or how all outcomes were handled. The primary analysis population is defined by availability of assay data, but that definition alone does not explain how missing measurements or participants were treated in each analysis.

11. Confidence Intervals and Precision

For the primary comparison, the recalculated risk difference is -0.004, with an interval from -0.350 to 0.343. The point estimate is close to zero, but the interval is broad and spans zero. It is compatible with differences favoring either regimen as well as with little difference. The result therefore gives a weakly localized estimate rather than a precise estimate of the between-group contrast. The registry’s reported Fisher Exact p-value is 1.000; the recalculated unadjusted p-value is 0.982.

For time to progression, the median was 15.2 months in the single low-dose group, with an interval from 14.5 to 20.8, and 38.9 months in the multiple low-dose group, with an interval from 17.3 and no reported upper limit. The reported hazard ratio was 0.431, and its 95% confidence interval was 0.157 to 1.185. For time to anti-tumor therapy, the median estimates were 24.7 and 36.7 months; the listed intervals were 14.8 and no reported upper limit, and 23.3 and no reported upper limit, respectively. The hazard ratio was 0.666, with a 95% confidence interval from 0.261 to 1.698.

Both hazard-ratio intervals include 1, so they do not exclude the no-difference reference. Their breadth also indicates uncertainty about the size and direction of the underlying comparison. The median estimates alone do not establish that one regimen differs from the other; the formal time-to-event comparisons and their uncertainty are important context.

Confidence intervals are not guarantees that the true value lies inside a particular interval. In general, they describe the range of estimates compatible with the observed data under the method’s assumptions. Here, the small primary group counts and the broad time-to-event intervals mean that the posted results do not tightly pin down the effects. The registry does not report enough detail about event counts or missing-data handling to explain the precision more specifically.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect, not on the original trial design. For the binary primary outcome, each entry is the number of participants per arm. For the time-to-event outcomes, entries are total events across the groups, not participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for the illustrations; the trial’s original design assumptions are not reported in the registry record.

The 80% power column describes a planning target under which the test would have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher chance of detection and therefore generally requires more information. For the binary outcome, the illustrations give participants per arm; for time-to-event outcomes, they give total events needed. The very large participant counts in the binary illustrations reflect the small observed risk difference used as the effect reference. The time-to-event illustrations likewise depend on the observed hazard-ratio effects and use total events.

The rows for 100%, 75%, and 50% of the observed effect show how the planning requirement changes when the target effect is smaller than the observed estimate. Smaller effects are harder to distinguish from random variation and therefore need more participants or, for time-to-event analyses, more events. These figures are not observed power: they are planning illustrations under stated assumptions, not a measure of the probability that this completed trial detected an effect.

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 = 0.471; treatment proportion p₁ = 0.467; average p̄ = 0.469.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7057 = 1.3832.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7057 = 0.5939.
4. n = (1.3832 + 0.5939)² / (-0.0039)² = 254,180.9, rounded up to 254,181 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 <- 0.470588235294118                          # control proportion
p1 <- 0.466666666666667                          # 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(1094548)
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 = 254,181 (80% power), 340,276 (90% power)
 75% of observed effect: n per arm = 451,934 (80% power), 605,011 (90% power)
 50% of observed effect: n per arm = 1,016,975 (80% power), 1,361,440 (90% power)
power.prop.test: 254180.9 
Simulated power at n = 254,181 per arm: 0.806 (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

For the primary binary outcome, the registry reports a Fisher Exact test with p = 1.000. The recalculated unadjusted comparison gives a risk difference of -0.004, an interval from -0.350 to 0.343, and p = 0.982. The registry indicates no discrepancy between the sponsor analysis and the recalculation. Both p-values are consistent with the posted counts providing little evidence of a difference between the regimens. The recalculated interval adds information about the range of plausible differences, but it is broad.

The registry also reports Log Rank analyses for the two time-to-event outcomes. The reported hazard ratios, confidence intervals, and p-values are 0.431 (95% CI 0.157 to 1.185; p = 0.094) for time to progression and 0.666 (95% CI 0.261 to 1.698; p = 0.392) for time to anti-tumor therapy. These are sponsor-reported analyses, not recalculations from summary counts. Their intervals include 1, and the point estimates should be interpreted with the group order and uncertainty in view.

The sponsor’s reported analysis is the formal registry result. The unadjusted recalculation is a separate check based on posted summary statistics; it does not replace the sponsor’s analysis or recover details that are absent from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and multiple secondary outcomes, including immune-response measures, objective clinical response, time to progression, time to anti-tumor therapy, and adverse events. Testing several outcomes can increase the chance of obtaining at least one small p-value by chance when each test is considered separately. Statistical approaches such as a prespecified hierarchy or adjustment for multiple comparisons can address that issue, but whether either approach was used is not reported in the registry record.

The trial’s original statistical analysis plan, including any multiplicity strategy, is not reported. An interim-analysis plan is also not reported. It is therefore not possible to determine from the registry whether the reported outcomes were assigned different confirmatory roles, whether the testing sequence was prespecified, or whether any adjustment was applied. The secondary results should be read cautiously in the absence of that information.

The primary outcome population is defined as a subset of the safety analysis set with at least one complete set of baseline, Week 5, and Week 9 data from one of the specified assays. This definition indicates that assay availability mattered for inclusion in the immunological diagnostic analysis set. The registry does not describe how missing assay values were handled, whether partial data were otherwise used, or how participants without the required measurements were represented in the analysis.

Missing-data handling for the time-to-event and other secondary analyses is also not reported in the registry record. In general, missing outcomes can affect both the number of participants contributing information and the interpretation of comparisons; the direction and size of any effect depend on why data are missing and how analyses handle them. No particular missingness mechanism or method can be inferred.

The listed enrollment is 34, while the primary arm counts are 17 and 15 and the safety record gives 17 participants at risk in each group. These are the posted figures for different outcome records; the registry does not explain the difference in analysis counts. They should not be reconciled by assumption. The trial’s original sample-size justification and target are not reported.

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: atrial fibrillation (11.8%), sepsis (11.8%), retinal detachment (5.9%), abdominal pain (5.9%), non-cardiac chest pain (5.9%).

The safety record lists 17 participants at risk in each group. Serious adverse events affected 6 participants in the single low-dose group and 5 in the multiple low-dose group. The record also lists other adverse events for 17 participants at risk and 17 affected in each group. These are participant counts, not measures of event duration or severity beyond the serious-event classification.

The registry lists atrial fibrillation and sepsis at 11.8% each among the top serious adverse event terms, and retinal detachment, abdominal pain, non-cardiac chest pain, and pyrexia at 5.9% each. The record does not link these term percentages to a particular study arm in the listed summary, so they should not be assigned to one regimen. Death counts are not reported in the registry record.

These figures describe the posted safety experience; they do not establish whether an event was caused by a study treatment. The registry does not give further detail about event timing, recurrence, exposure duration, or arm-specific distributions of the listed terms. Differences in counts should be interpreted cautiously in a study of this size, and the counts alone do not establish comparative safety.

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

The primary result describes the number of participants who met the registry’s laboratory-based definition of an induced MUC1-specific immune response. The posted counts are 8 in the single low-dose group and 7 in the multiple low-dose group. The recalculated risk difference is close to zero, but its interval is broad and includes differences in either direction. The sponsor’s Fisher Exact result and the recalculated unadjusted comparison do not provide clear evidence of separation in the primary outcome.

This does not prove that the two regimens are equivalent. Demonstrating equivalence or non-inferiority requires a design and analysis that specify an appropriate margin and evaluate the result against that margin; such information is not reported in the registry record. A non-significant comparison also does not show that a treatment has no biological effect. It means the posted data do not provide strong evidence against the tested null comparison under the reported analysis.

Nor does the primary immune-response outcome establish a change in clinical course. The endpoint is based on assay thresholds and repeated timepoints. The registry separately lists clinical response and time-to-event outcomes, which measure different aspects of the disease experience. The two posted time-to-event comparisons have broad intervals that include their no-difference reference, so they also do not settle whether the regimens differ on those outcomes.

The results should not be generalized beyond the study population and analysis definitions without additional evidence. The official title describes people with different disease and treatment histories, while the registry does not report their distribution by arm. The primary analysis set required specified immune-assay data, and missing-data methods are not reported.

In general, a small randomized study can be informative about feasibility and the observed outcomes while leaving substantial uncertainty about effects. The posted results are compatible with a range of possibilities. They do not establish that either regimen is better, worse, or interchangeable, and they are not a basis for individual treatment decisions.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it places a mechanistic laboratory endpoint at the center of a randomized comparison while also listing clinical and safety outcomes. That distinction matters: an immune-response count can describe whether participants crossed an assay-based threshold, but it cannot by itself establish a clinical effect. Keeping endpoint types separate prevents a laboratory signal from being overinterpreted as evidence about progression or subsequent therapy.

The primary result also illustrates the difference between a point estimate and its precision. The recalculated risk difference is close to zero, but the interval stretches across zero and includes appreciable differences in either direction. Reporting only the point estimate or p-value would obscure that uncertainty. The same issue appears in the time-to-event analyses, where the hazard-ratio intervals are broad and include 1.

The randomized parallel-group design allows a direct comparison of the two named combinations, but the study enrolled 34 participants and the primary analysis counts are modest. The registry does not report the original sample-size justification or analysis plan, so the intended detectable effect and the original precision goals cannot be reconstructed. Planning illustrations based on observed effects are not substitutes for that missing design information.

Finally, the record highlights why complete outcome reporting and transparent analysis methods matter. The registry identifies several secondary outcomes, but numerical results are not available for all of them in the posted record. The multiplicity plan, interim analyses, and missing-data methods are also not reported. Those omissions constrain interpretation even when the available estimates and tests are described clearly. The findings are most useful when read as a limited, uncertain comparison rather than as a definitive answer about treatment effects.

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 principal limitation is the modest study size: the registry lists 34 participants enrolled, with primary outcome counts of 17 and 15. The primary comparison is consequently imprecise, as reflected in the broad interval around the recalculated risk difference. The original sample-size justification and intended detectable effect are not reported in the registry record.

The study was open-label, with no masking reported. The primary endpoint uses laboratory assays and explicit response criteria, but the registry does not report whether assay assessment was blinded to regimen. It also does not provide further arm-level descriptions beyond the names of the two cyclophosphamide schedules.

The primary outcome applies to the immunological diagnostic analysis set, defined by availability of complete baseline, Week 5, and Week 9 data from at least one listed assay. The record does not explain how many participants failed to meet this data requirement or how missing measurements were handled. Differences between enrollment, primary analysis, and safety counts are not explained in the registry.

Time-to-event estimates are uncertain, and the event counts contributing to those analyses are not reported. The upper confidence limits for several median estimates are not reported. The registry also does not provide numerical results for all listed secondary outcomes in the record, or a plan for controlling multiplicity. Its original statistical analysis plan and interim-analysis plan are not reported.

The official title encompasses participants with different disease and treatment histories, but the distribution of these categories across arms is not reported. This limits assessment of the composition of each group. The safety summary gives serious adverse event counts and selected terms, but does not provide full event timing, exposure, or term-by-arm detail in the posted figures.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Tecemotide (L-BLP25) in Subjects With Slowly Progressive Multiple Myeloma With no Symptoms and Who Have Had no Chemotherapy — NCT01094548.
• Registry record last updated 2016-02-22; status last verified 2016-01.
• Results first posted 2016-02-22.
• 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

NCT01094548 was a randomized, open-label, parallel-group Phase II study of tecemotide (L-BLP25) plus either single low dose or multiple low doses of cyclophosphamide in people with multiple myeloma. The registry lists 34 participants enrolled and describes an overall induced MUC1-specific immune response as the primary outcome, assessed from randomization up to Week 104.

The primary outcome counts were 8 of 17 for the single low-dose regimen and 7 of 15 for the multiple low-dose regimen. The registry reports a Fisher Exact p-value of 1.000; the unadjusted recalculation gives a risk difference of -0.004, an interval from -0.350 to 0.343, and p = 0.982. The posted time-to-event comparisons are also uncertain, with hazard-ratio intervals that include 1.

The registry lists six secondary outcomes. Numerical results for all listed secondary outcomes, the original statistical analysis plan, the original sample-size justification, multiplicity procedures, interim analyses, and missing-data methods are not reported in the registry record. The available findings describe the recorded outcomes but do not establish a definitive difference between the regimens.