A Study of Bevacizumab in Combination With Bortezomib in Patients With Relapsed or Refractory Multiple Myeloma (AMBER): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Bevacizumab in Combination With Bortezomib in Patients With Relapsed or Refractory Multiple Myeloma (AMBER) (NCT00473590), a randomized phase 2 study. The primary outcome is Progression-free Survival (PFS).

2. Clinical Question

This is a treatment-comparison question in a randomized, parallel-group study. Random assignment is intended to make the groups comparable on average at the start of a trial, while blinding is intended to limit the influence of treatment knowledge on care and outcome assessment. The record identifies the study as single-masked but does not identify which people were masked. It also describes the trial as multicenter and placebo-controlled.

The endpoint addresses how long patients remain alive without recorded disease progression during follow-up. Overall response, duration of response, overall survival, and adverse events were also listed as secondary outcomes. Those outcomes can help describe the broader set of observations, but the primary statistical question concerns progression-free survival.

3. Trial Design

The registry describes NCT00473590, titled “A Study of Bevacizumab in Combination With Bortezomib in Patients With Relapsed or Refractory Multiple Myeloma (AMBER).” It was a randomized, blinded, placebo-controlled, multicenter, Phase II study with a parallel-group model. The study status is completed, and the recorded enrollment is 102. The registry lists a start date of 2007-06 and primary completion in 2009-11.

The experimental group received bortezomib plus bevacizumab; the control group received bortezomib plus placebo. Both recorded bortezomib schedules used an intravenous bolus on Days 1, 4, 8, and 11 of a 21-day cycle, for a maximum of eight cycles. Bevacizumab or placebo was administered as an intravenous infusion on the first day of each 21-day cycle during the blinded treatment phase. The dosing descriptions in the record specify bortezomib 1.3 mg/m^2, bevacizumab 15 mg/kg, and a 3- to 5-second bolus for bortezomib.

The primary outcome was median progression-free survival, measured from randomization to disease progression or death on study. The record describes the primary analysis population as randomized patients and the outcome timeframe as up to 116 weeks. The registry lists additional outcomes including overall response, duration of response, overall survival, and selected adverse events.

The registry record does not report the original sample-size justification, the planned target for each arm, or the assumptions used when the trial was designed. The posted enrollment and the counts in the outcome analyses describe different aspects of the record; they should not be treated as interchangeable denominators. Reasons for any differences in analysis counts 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized Patients

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 Progression-free Survival (PFS), measured over From randomization to disease progression or death on study (up to 116 weeks)..

Progression-free survival (PFS) measures the time from randomization until disease progression or death on study. In this trial, a death from any cause counted when it occurred within 30 days of the last response assessment. Disease progression was determined by the investigator using the International Myeloma Working Group's uniform response criteria. The primary result is expressed as a median time in months for each treatment group, estimated using Kaplan-Meier methodology.

A time-to-event endpoint retains information about when events occur, rather than reducing follow-up to a simple event/no-event count at a single date. The median describes the time by which the estimated PFS curve has reached the midpoint. It does not describe every patient's course, nor does it indicate that all patients experienced an event at the median time. Patients alive without progression at the time of analysis were censored at their last response assessment, as specified in the record.

In general, PFS is used in trials where delaying progression or death is a clinically relevant outcome and where follow-up can identify the timing of those events. Its interpretation depends on how progression is assessed, how deaths and censoring are handled, and how long participants are followed. The registry gives the endpoint definition and analysis method, but details such as independent review of progression and the full assessment schedule are not reported in the registry record.

7. Results Posted in the Registry

• BORT + P vs BORT + BV: hazard ratio 0.74 (95% CI 0.43–1.28), reported p = 0.280 (as reported in the registry).
• BORT + P vs BORT + BV: hazard ratio 0.71 (95% CI 0.42–1.20), reported p = 0.201 (as reported in the registry).

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.

Number of Participants With an Overall Response

• 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:
  • BORT + BV: 51.0% (25/49) versus 43.4% (23/53) on control; risk difference 7.6 percentage points (95% CI -11.7 to 27.0), risk ratio 1.18 (0.78–1.78); unadjusted two-proportion z-test p = 0.441.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BORT + BV and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With an Overall Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • BORT + BV: 51.0% (25/49) versus 43.4% (23/53) on control; risk difference 7.6 percentage points (95% CI -11.7 to 27.0), risk ratio 1.18 (0.78–1.78); unadjusted two-proportion z-test p = 0.441.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BORT + BV and the control. The interval gives the range of effects that remain compatible with the data.

Duration of Response

• 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:
  • BORT + P vs BORT + BV: hazard ratio 0.96 (95% CI 0.40–2.26), reported p = 0.918 (as reported in the registry).
  • BORT + P vs BORT + BV: hazard ratio 0.84 (95% CI 0.37–1.89), reported p = 0.666 (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 BORT + P vs BORT + BV and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between BORT + P vs BORT + BV and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description of the trial beyond PFS. They include overall response as a count and percentage, duration of response, overall survival, and selected adverse events. Among the posted secondary efficacy results, the response point estimate is numerically higher in the bevacizumab group; duration of response is reported as a time-to-event measure with sponsor-reported hazard-ratio analyses. The registry lists overall survival as an outcome, but no numerical overall-survival result is included in the record summarized for these results.

As a group, the secondary findings do not supply a clear statistical confirmation of the primary PFS comparison. The response recalculation is imprecise, while the reported duration-of-response comparisons have wide confidence intervals that include 1. Secondary outcomes can be useful for understanding the range of observed effects and for generating hypotheses, but they should not be treated as independent confirmations simply because they point in a similar numerical direction.

Multiple outcomes create multiple opportunities to observe an apparently noteworthy result by chance. Without a reported multiplicity strategy, unadjusted secondary p-values do not control the overall false-positive risk across the set of outcomes and analyses. In addition, secondary analyses may involve fewer participants or events than the primary analysis, and the response and duration outcomes apply to different types of observations. These features limit direct comparison across endpoints.

The secondary results are most appropriately interpreted as descriptive and exploratory alongside the primary endpoint. They can inform questions for future research, but the registry record does not report a plan for confirmatory secondary testing, an adjustment for multiplicity, or a complete numerical result for every listed secondary outcome. No secondary result alone establishes the overall effect of adding bevacizumab to bortezomib.

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

• Number of Participants With an Overall Response
• Percentage of Participants With an Overall Response
• Duration of Response
• Overall Survival (OS)
• Number of Participants With Selected Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data. Participants can have a progression or death event, or they can remain alive without documented progression when their information is last assessed. Kaplan-Meier methods estimate the probability of remaining event-free over time while accounting for participants whose follow-up ends without a recorded event. Such participants are censored at the last response assessment specified in the registry. Censoring allows their observed follow-up to contribute information up to that time; it does not establish what happened afterward.

What does the median PFS represent?

The median PFS is read from the estimated Kaplan-Meier curve at the time the estimated event-free proportion reaches its midpoint. It is a summary of the curve, not an average of individual follow-up times and not a statement that all participants had progression or death at that time. The medians reported are 5.1 months for BORT + P and 6.2 months for BORT + BV. Their confidence intervals express uncertainty in those median estimates.

What does the hazard ratio add?

A hazard ratio summarizes the relative event rates between groups over the observed follow-up, subject to the assumptions of the analysis. A value of 1 represents equal event rates under the comparison's direction and model. Values on either side of 1 indicate different estimated rates, but the numerical direction must be read together with which group is in the numerator and the outcome being modeled. The registry labels the comparison BORT + P versus BORT + BV and reports hazard ratios of 0.743 and 0.713. The record does not explain why two estimates are listed. The reported confidence intervals include 1, so the estimates are compatible with no group difference as well as a range of other effects.

The log-rank test compares the event-time experience between groups across follow-up. Its p-value indicates how compatible the observed comparison is with the null hypothesis of no difference, under the test's assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the chance that a result will replicate. The reported p-values are 0.280 and 0.201. They are both above 0.05, and the registry does not identify either comparison as statistically significant.

Why do confidence intervals matter?

A confidence interval conveys uncertainty around an estimate. A narrow interval indicates greater precision than a wide interval, while an interval crossing the null value signals that the data are compatible with no difference at the corresponding confidence level. For a hazard ratio, the null value is 1; for a difference, it is 0. The primary hazard-ratio intervals are broad enough to include values on either side of 1, so the estimates do not pin down a single effect magnitude.

How should binary outcomes be compared?

Overall response is a binary outcome: each participant is classified according to whether an overall response occurred. The posted counts are 23 of 53 in the bortezomib-plus-placebo group and 25 of 49 in the bortezomib-plus-bevacizumab group. A risk difference expresses the difference between the response proportions, with a positive value in this comparison pointing toward a higher observed proportion in the bevacizumab group. The recalculated estimate is 0.076, with a 95% confidence interval from -0.117 to 0.270 and an unadjusted p-value of 0.441. Since the interval includes 0, the comparison is uncertain and does not establish a difference.

For binary outcomes, the observed proportions are useful descriptions, but their uncertainty depends on the number of observations and the event frequency. A confidence interval helps distinguish an observed contrast from a precise estimate of the underlying contrast. The registry does not report a sponsor analysis for the posted overall-response comparison.

What does censoring mean in this study?

For PFS, the record states that participants alive without progression at analysis were censored at the last response assessment. This is a standard way to incorporate incomplete event-time follow-up, but it relies on assumptions about how censoring relates to the event process. If the reasons or timing of lost follow-up are related to prognosis, interpretation can be affected. The registry record does not describe the amount or reasons for censoring, or provide sensitivity analyses addressing it.

The primary analysis population is identified as randomized patients. That statement does not, by itself, supply all details about analysis-set construction or participant handling. The registry does not report the statistical analysis plan, any interim analyses, or a sample-size justification for the original trial. General statistical concepts explain how to read the posted measures, but they cannot fill gaps in the record's account of planned analysis choices.

11. Confidence Intervals and Precision

The primary PFS median estimates have 95% confidence intervals: 4.17 to 7.2 months for BORT + P and 4.4 to 8.54 months for BORT + BV. The intervals indicate uncertainty about the underlying median in each treatment group. They are not ranges containing 95% of individual participants' PFS times, and they do not mean that there is a 95% probability that a fixed true value lies inside the calculated interval.

The reported hazard-ratio intervals are also important for judging precision. The interval for the estimate of 0.743 extends from 0.432 to 1.276; the interval for 0.713 extends from 0.424 to 1.2. Both include the null hazard ratio of 1. The data therefore do not precisely distinguish the comparison from no difference, and the intervals also allow effects in either direction under the reported comparison. The registry does not explain why it records two PFS hazard-ratio analyses, which limits interpretation of their relationship.

For the response comparison, the recalculated risk-difference interval runs from -0.117 to 0.270 around an estimate of 0.076. It includes no difference and allows a range of possible differences. The group-specific response estimates also have reported confidence intervals: 30.1 to 57.7 percent for BORT + P and 36.3 to 65.2 percent for BORT + BV.

In general, confidence intervals communicate precision more fully than a point estimate alone. An interval that includes a null value does not prove equality, and an interval that excludes it would not, by itself, establish clinical importance. Interpretation also depends on the outcome definition, analysis method, and prespecified decision criteria, details that are not all reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the original design calculation for this trial. For binary outcomes, the entries are participants per arm. For time-to-event outcomes, the entries are total events across the comparison, not participants per arm. These units are different and should not be conflated when reading the display or its curve.

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. The 80% power column gives the planning sample size or event total that would yield an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were true. The 90% power column expresses the corresponding planning target for a 90% chance. These are design calculations, not findings about the trial participants.

The rows describe planning for 100%, 75%, and 50% of the observed effect. A smaller target effect requires more information to detect reliably, so the required sample size or event total increases as the effect being planned for becomes smaller. This relation is general: subtle differences are harder to distinguish from random variation than large differences, all else equal.

These figures are not observed power. Observed power is not a useful substitute for interpreting the estimated effect and its confidence interval after a trial. The trial's own design assumptions and original sample-size justification are not reported in the registry record. The displayed planning values should therefore be read only as conditional illustrations under the stated calculation assumptions, not as a reconstruction of why the study enrolled its recorded population.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.743, so ln(HR) = -0.2971.
2. d = 4 × (1.96 + 0.842)² / [ln(0.743)]² = 355.8, rounded up to 356 events in total 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
hr <- 0.743                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(473590)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 356 (80% power), 477 (90% power)
 75% of observed effect: events = 633 (80% power), 847 (90% power)
 50% of observed effect: events = 1,424 (80% power), 1,906 (90% power)
Simulated power with 356 events: 0.795 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 525 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 102 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 5.1          # control-arm median, months (converted from the posted unit)
hr          <- 0.743          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 320         p (1-sided)   0.0001
 Events: 161        ~HR at bound   0.5566
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.74   0.0338
   IA 2: 67%                   Z   2.5114
      N: 512         p (1-sided)   0.0060
 Events: 321        ~HR at bound   0.7555
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.74   0.5603
       Final                   Z   1.9930
      N: 526         p (1-sided)   0.0231
 Events: 482        ~HR at bound   0.8339
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.74   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The registry records sponsor-reported log-rank hazard ratios for the primary PFS comparison: 0.743 with a 95% confidence interval from 0.432 to 1.276 and p = 0.280, and 0.713 with a 95% confidence interval from 0.424 to 1.2 and p = 0.201. The record does not say why both estimates are listed or identify a distinction between their analysis populations or specifications. No separate recalculated hazard ratio is used for the time-to-event endpoint; the posted sponsor analyses are the relevant comparisons reported in the registry.

For overall response, the registry posts group counts and percentages but no sponsor-reported comparison analysis. A simple unadjusted recalculation from the posted counts gives a risk difference of 0.076, with a 95% confidence interval from -0.117 to 0.270 and p = 0.441. This calculation is not a replacement for a sponsor analysis or a prespecified model. It does not include adjustment for covariates or multiplicity.

The registry does not flag a discrepancy between a sponsor result and a recalculation. The response recalculation and sponsor-reported PFS analyses answer different outcome questions and should not be combined into a single test. The response result is secondary, and its unadjusted analysis carries less inferential weight when multiple outcomes and comparisons are considered.

16. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, with some outcomes reported in more than one form. Each additional endpoint or analysis creates another opportunity for a chance finding. When several hypotheses are tested, the probability of at least one nominally unusual result can rise unless the testing strategy accounts for multiplicity. This is a general statistical concern, not evidence that any particular result in this trial is false.

The registry record does not report whether secondary comparisons were adjusted for multiplicity, which outcomes were intended to be confirmatory, or whether a hierarchy or gatekeeping strategy was specified. It also does not report the full statistical analysis plan. Consequently, the secondary p-values should be treated as unadjusted unless the posted analysis explicitly states otherwise. They do not carry the same confirmatory force as a prespecified primary comparison with a known testing plan.

The primary PFS analysis population is identified as randomized patients. The registry describes censoring for participants alive without progression at the last response assessment, but it does not report the extent of missing data, reasons for incomplete follow-up, or sensitivity analyses for alternative assumptions. The handling of missing data for the binary response outcome is also not reported in the registry record.

Although the record specifies an endpoint definition, Kaplan-Meier estimation, and log-rank comparisons, it does not give the original sample-size justification, interim-analysis plan, or detailed prespecified statistical plan. These omissions make it difficult to assess whether all analysis choices followed an original protocol or whether the two reported PFS analyses reflect planned alternatives. No explanation for the duplicate PFS comparisons is reported. Interpretation should therefore stay close to the results and methods that are explicitly recorded.

17. 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: dehydration (10.0%), renal failure acute (6.0%), thrombocytopenia (4.0%), diarrhoea (4.0%), pneumonia (4.0%).

The registry reports serious adverse event figures for groups labeled BORT + P and BORT + BV. For serious adverse events, the reported number affected is 26 among 50 at risk in BORT + P and 24 among 50 at risk in BORT + BV. For other adverse events, the reported number affected is 41 among 50 at risk in BORT + P and 43 among 50 at risk in BORT + BV. These counts describe participants recorded as affected in the relevant categories; they do not indicate how many events each person experienced.

The most frequently listed serious adverse-event terms include dehydration at 10.0%, acute renal failure at 6.0%, thrombocytopenia at 4.0%, diarrhoea at 4.0%, pneumonia at 4.0%, and orthostatic hypotension at 4.0%. The registry's percentages should be read as reported, and the category-level counts should not be added because participants may have experienced more than one event. The record does not provide deaths in the safety summary shown, and it does not give further detail about event timing, severity grading, attribution, or exposure-adjusted rates.

These figures are descriptive safety summaries. They do not establish that an event was caused by either study treatment, and differences in counts are not, by themselves, evidence of a treatment-related difference in risk. A complete safety assessment would require context about follow-up and the full adverse-event reporting methods, which are not reported in the registry record.

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

The posted results describe a randomized comparison of bortezomib with bevacizumab versus bortezomib with placebo in patients with relapsed or refractory multiple myeloma. The primary PFS medians were 5.1 months and 6.2 months, respectively. The sponsor-reported log-rank analyses did not report a statistically significant group difference: the two p-values were 0.280 and 0.201, and both hazard-ratio confidence intervals included 1.

That pattern means the estimates do not provide precise evidence of a difference in PFS in this trial. It does not prove that the regimens have identical effects. The confidence intervals leave uncertainty about the size and direction of the underlying difference, and the registry does not explain why two primary hazard-ratio analyses are recorded. The observed median difference should not be interpreted alone as proof of a treatment effect.

The secondary response results are also uncertain, and the registry does not report multiplicity adjustment. The duration-of-response analyses are time-to-event comparisons and likewise have broad intervals. These outcomes add context but do not overturn or resolve the uncertainty in the primary result. The safety counts describe recorded adverse events, not a causal comparison of treatment-related risk.

The study was Phase II and its stated purpose was a preliminary assessment of safety and efficacy. The registry record does not report the original power assumptions or a confirmatory testing strategy. Consequently, these results are best understood as estimates from this completed trial rather than as definitive evidence for a clinical decision. No treatment recommendation follows from the statistical results alone.

19. Why This Trial Matters Statistically

This trial is a useful example of why a point estimate and a significance test should not be read in isolation. The two median PFS estimates are different, but the time-to-event comparison is accompanied by confidence intervals that include the null hazard ratio and p-values above 0.05. The statistical message is therefore not simply the direction of the medians; it is the combination of the estimates and their uncertainty.

It also illustrates the distinction between a median and a hazard ratio. The medians summarize the estimated event-free time in each group at a particular point on the survival curve, whereas the hazard ratio compares event rates over follow-up. These measures are related but not interchangeable. A reader should consider both the endpoint definition and the analytical approach when interpreting a time-to-event comparison.

The record also exposes practical limits of registry reporting. Two primary hazard-ratio analyses are listed without an explanation of their relationship, and important design and analysis details are not reported. Such gaps can prevent readers from determining which analysis was intended as primary or how planned decisions relate to posted findings. This is especially relevant when interpreting secondary outcomes without a stated multiplicity strategy.

Finally, the planning illustrations demonstrate how assumed effect size affects the information required for a future study. They are not a reconstruction of this trial's original design and should not be mistaken for evidence that the trial was adequately or inadequately powered. The distinction between planning quantities, observed estimates, and inferential conclusions is central to sound biostatistical interpretation.

20. 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 questions about the PFS analysis unresolved. It reports two log-rank hazard ratios for the same labeled comparison but does not identify why there are two estimates, what distinguishes them, or which was considered primary. Both are presented with confidence intervals and p-values, but the record does not supply analysis-set or model details that would clarify their relationship.

Further design information is not reported, including the original sample-size justification, the trial's planned statistical assumptions, any interim-analysis plan, and a full statistical analysis plan. The single-masking designation is recorded, but the identity of the masked parties is not specified. Details about the progression assessment schedule, independent review, and the extent and reasons for censoring are also not reported in the registry record.

The registry does not describe missing-data handling for the response outcomes or provide sensitivity analyses for PFS censoring. It does not report a multiplicity strategy for the several secondary outcomes. The listed overall-survival outcome has no numerical result in the posted results, limiting assessment of that endpoint. These gaps do not invalidate the reported estimates, but they restrict the conclusions that can be drawn from them.

The safety summary provides counts and selected serious adverse-event terms, without details in this record about event attribution, time at risk, or exposure-adjusted analyses. Group counts for different adverse-event categories may overlap, so they cannot be summed to represent unique participants. Finally, the study is a Phase II preliminary assessment, and the registry record alone does not establish how broadly the findings apply beyond the enrolled trial population.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Bevacizumab in Combination With Bortezomib in Patients With Relapsed or Refractory Multiple Myeloma (AMBER) — NCT00473590.
• Registry record last updated 2017-06-14; status last verified 2017-05.
• Results first posted 2012-01-19.
• 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.

24. Record Summary

NCT00473590 was a completed, randomized, single-masked, placebo-controlled, multicenter, parallel-group Phase II study of bevacizumab with bortezomib in relapsed or refractory multiple myeloma. The registry records enrollment of 102, a start date of 2007-06, and primary completion in 2009-11.

The primary outcome was median PFS. The reported group medians were 5.1 months for BORT + P and 6.2 months for BORT + BV. The registry lists two log-rank hazard-ratio analyses, both with confidence intervals including 1 and p-values above 0.05; it does not explain the difference between those analyses.

Overall response, duration of response, overall survival, and selected adverse events were listed as secondary outcomes. The posted results offer descriptive and exploratory evidence, with uncertainty and reporting gaps that limit stronger conclusions. The original sample-size rationale, detailed analysis plan, and multiplicity approach are not reported in the registry record.