Image-Guided Radiosurgery or Stereotactic Body Radiation Therapy in Treating Patients With Localized Spine Metastasis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Image-Guided Radiosurgery or Stereotactic Body Radiation Therapy in Treating Patients With Localized Spine Metastasis (NCT00922974), a randomized phase 2, phase 3 study. The primary outcome is Percentage of Patients With Complete or Partial Pain Response at 3 Months (Phase III).

2. Clinical Question

The trial record describes a comparison of radiation approaches for localized spine metastasis, with pain response as the primary phase III outcome. Its response definition includes both the measured pain score and whether narcotic pain medication increased. It also requires that pain at secondary treated sites did not increase. This makes the primary outcome a defined response category rather than simply any change in the pain score.

The question is statistical: how the recorded response proportions and their uncertainty compare between randomized groups. The observed percentages describe the participants included in the endpoint analysis; they do not by themselves establish why the groups differed or what an individual participant’s outcome would be. The registry’s own analysis and the unadjusted recalculation do not agree, so the sponsor’s reported analysis takes precedence when describing the trial’s formal result.

3. Trial Design

This was a randomized phase II/III study with a parallel-group design. The registry lists 399 enrolled participants and marks the study as completed. The study start is recorded as 2009-11, and primary completion as 2018-01. The sponsor is the Radiation Therapy Oncology Group. Masking is listed as none, so this was an unmasked comparison.

The two interventions were Radiosurgery/SBRT and external-beam radiation therapy. Arm descriptions are not reported in the registry record, so details beyond those intervention names cannot be established from the record. The primary endpoint pertains to the phase III component, rather than all enrolled participants: the eligible randomized participants with both baseline and 3 month NRPS scores were included. The reported endpoint counts were 139 in the Radiosurgery/SBRT arm and 76 in the external-beam arm.

The study included phase II and phase III components, and the registry lists outcomes from both components in its record. The precise transition or decision process between phases is not reported in the registry record. Nor are the randomization procedure, allocation concealment, stratification factors for the primary endpoint, or the original sample-size justification reported there. These details matter when assessing how treatment assignment was implemented and whether the observed analysis followed a prespecified plan; their absence from the record does not establish that no such procedures or plans existed.

The stated follow-up window for the primary pain response was baseline to 3 months. Other listed outcomes extend through two years or measure change at specified follow-up times. The record therefore supports an account of a randomized, open-label comparison and the endpoint analyses that are posted, but it does not provide every operational detail needed to reconstruct the full protocol.

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.

Phase II Component

Reasons for not completing this period:

Phase III Component

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Patients enrolled in the phase II component who were eligible and had treatment review information.

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: Eligible registered patients

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients With Complete or Partial Pain Response at 3 Months (Phase III), measured over Baseline and 3 months.

The primary endpoint is the percentage of phase III participants with a complete or partial pain response at 3 months. Pain was assessed with the Numerical Rating Pain Scale, an 11-point scale from 0 to 10, where 0 means no pain and 10 is the worst pain imaginable. Scores of 1-4 are described as mild, 5-6 as moderate, and 7-10 as severe. The endpoint population required both a baseline score and a 3 month score.

The registry defines pain response using the difference between the 3 month score and the baseline score: a positive value indicates increased pain, while a negative value indicates decreased pain. A complete response requires a post-treatment score of 0 at the index site, no increase in narcotic pain medication, and no increase in pain score at secondary treated sites. A partial response requires an improvement of at least 3 points at the index site, with the same requirements concerning medication and secondary sites. The index site is the lesion with the highest baseline pain score; if more than one lesion has that score, it is the most cephalad lesion.

A percentage is useful for expressing how common the defined response was among participants assessed for this endpoint. It does not convey the size of pain change for each participant, and a binary responder classification does not preserve all information in the underlying pain scores. The registry’s endpoint definition makes the result dependent on pain scores, medication use, and pain at other treated sites together.

7. Results Posted in the Registry

• External Beam Radiation Therapy: 57.9% (44/76) versus 40.3% (56/139) on control; risk difference 17.6 percentage points (95% CI 3.8 to 31.4), risk ratio 1.44 (1.09–1.90); unadjusted two-proportion z-test p = 0.013.

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.

Percentage of Participants With Pain Response Through Two Years (Phase III)

• 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:
  • External Beam Radiation Therapy: 19.2% (25/130) versus 19.1% (40/209) on control; risk difference 0.1 percentage points (95% CI -8.5 to 8.7), risk ratio 1.00 (0.64–1.57); unadjusted two-proportion z-test p = 0.983.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between External Beam Radiation Therapy and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Pain Relapse Through Two Years (Phase III)

• 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:
  • External Beam Radiation Therapy: 97.5% (78/80) versus 91.4% (128/140) on control; risk difference 6.1 percentage points (95% CI 0.3 to 11.8), risk ratio 1.07 (1.00–1.13); unadjusted two-proportion z-test p = 0.076.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between External Beam Radiation Therapy and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With a Vertebral Compression Fracture Through Two Years (Phase III)

• 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:
  • External Beam Radiation Therapy: 21.5% (28/130) versus 19.6% (41/209) on control; risk difference 1.9 percentage points (95% CI -7.0 to 10.8), risk ratio 1.10 (0.72–1.68); unadjusted two-proportion z-test p = 0.669.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between External Beam Radiation Therapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover additional aspects of pain, adverse events, vertebral compression fracture, spinal cord damage, and quality of life or function. The detailed posted results include pain response through two years, pain relapse, and vertebral compression fracture. Across those outcomes, the results do not form a single clear pattern of separation between the radiation groups: some estimates are close, while other estimates are less precise or point in different directions. The posted comparisons should be read as additional context, not as replacements for the primary endpoint.

The secondary analyses include time-to-event methods and a competing-risk test, rather than all using the same comparison method as the primary binary response. Their estimates therefore address different statistical questions. A percentage of participants with an event by a follow-up period and a hazard ratio over follow-up are not interchangeable summaries. The registry also lists further outcomes, including spinal cord damage, adverse events, FACT-G, BPI worst pain, and EQ-5D, but numerical results for those outcomes are not reported in the registry record.

Unadjusted secondary findings carry less weight because several outcomes and comparisons can increase the chance of an apparently notable result arising by chance. The registry does not report a multiplicity adjustment, testing hierarchy, or analysis plan explaining which secondary outcomes were intended to be confirmatory. This does not make secondary outcomes uninformative; it means they should be interpreted as exploratory or supportive unless their prespecified status and multiplicity handling are established. Their overall pattern can inform questions for further study, but cannot settle the primary analysis discrepancy.

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

• Percentage of Participants With Pain Response Through Two Years (Phase III)
• Percentage of Participants With Pain Relapse Through Two Years (Phase III)
• Percentage of Patients With Adverse Events at 3 Months (Phase III)
• Percentage of Participants With a Vertebral Compression Fracture Through Two Years (Phase III)
• Percentage of Participants With Spinal Cord Damage Through Two Years
• Change in Functional Assessment of Cancer Therapy - General (FACT-G) Total Score at 3 Months (Phase III)
• Change in Brief Pain Inventory (BPI) Worst Pain Score Through Two Years (Phase III)
• Change in EuroQol 5 Dimension (EQ-5D) Index Score Through Two Years (Phase III)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is classified as having or not having the defined pain response. The arm-specific percentages estimate the fraction classified as responders among those included in each arm’s endpoint analysis. Their 95% confidence intervals describe the range of values reasonably compatible with the observed data under the method used to calculate them. A wider interval indicates less precision than a narrower interval, although interval width also depends on the estimated proportion and the analysis method.

What does the risk difference describe?

The unadjusted risk difference compares the two response proportions by subtracting one proportion from the other, with the comparison oriented as external-beam radiation therapy relative to Radiosurgery/SBRT. The recalculated estimate is 0.176, and its 95% confidence interval is 0.038 to 0.314. This is an absolute contrast in proportions, rather than a ratio of the proportions. The interval describes uncertainty in that contrast. It is a recalculation from posted summary statistics, not a substitute for the sponsor’s analysis.

Why can analyses disagree?

The registry’s reported primary comparison uses Fisher Exact and gives p = 0.99. The posted recalculation uses the arm-level event counts and gives an unadjusted p-value of 0.013. Differences can arise when analyses use different methods, populations, definitions, or assumptions; the registry record does not explain the source of this particular discrepancy. It does not report enough detail to reconcile the analyses. Because the discrepancy is flagged, the sponsor’s own analysis takes precedence in describing the trial’s formal finding. The recalculation remains a descriptive check based on the posted summary statistics.

What does a p-value tell a reader?

A p-value is calculated under a null hypothesis and a statistical model. It describes how unusual data at least as incompatible with that null model would be if the model and its assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result occurred by chance in an everyday sense. A p-value also does not show whether an observed difference matters to participants. Interpretation requires the effect estimate, its uncertainty, the endpoint definition, and the analysis plan.

How should time-to-event analyses be read?

Some secondary outcomes have registry-reported stratified log-rank analyses with hazard ratios. A hazard ratio compares event rates over follow-up within the time-to-event model; it is not the same quantity as the difference between the percentages with an event by a particular time. The reported confidence interval conveys uncertainty in the hazard ratio, and a broad interval can leave substantial uncertainty about the magnitude and direction of the association. The registry gives hazard ratios and intervals for some secondary comparisons, but the details of the stratification and model specification are not reported in the registry record.

Gray’s test is reported for the vertebral compression fracture outcome. In general, Gray’s test is used to compare cumulative incidence when competing events are relevant. Competing events can prevent the event of interest from occurring or being observed in the usual way; accounting for them can matter when estimating event incidence. The registry does not provide the detailed analysis specification or explain how competing events were handled, so the test name alone does not permit reconstruction of the analysis.

Why do analysis populations matter?

The primary endpoint population is explicitly defined as eligible participants randomized in phase III who had both baseline and 3 month NRPS scores. That definition is important because the denominator is not simply the full enrollment. The registry reports endpoint counts of 139 and 76 for the two arms, but reasons for missing endpoint measurements and methods for handling missing data are not reported in the registry record. Without those details, it is not possible to assess whether missingness could have affected the observed response proportions.

Randomization is intended to support a fair comparison by assigning participants to groups, but the record does not describe the assignment procedure or concealment. Masking is listed as none. Knowledge of assigned treatment can matter especially for outcomes involving participant-reported pain, although the endpoint also has explicit scoring and medication criteria. The extent to which assessment procedures reduced potential influence is not reported in the registry record.

What is not established by the posted tests?

The trial is described as randomized and parallel, but details of the original statistical analysis plan, sample-size justification, interim analyses, and any multiplicity strategy are not reported in the registry record. The existence of several outcomes creates multiple opportunities for statistical comparisons. Without a reported adjustment or prespecified hierarchy, secondary p-values should be interpreted cautiously and should not be treated as independent confirmatory evidence. General statistical practice recognizes that testing multiple outcomes can increase the chance of at least one apparently noteworthy finding even when no corresponding effect exists.

11. Confidence Intervals and Precision

The primary arm estimates have 95% confidence intervals of 32.0% to 49.0% for Radiosurgery/SBRT and 46.0% to 69.0% for external-beam radiation therapy. These intervals show that the estimated response proportions have meaningful uncertainty. They are not guarantees that the true values lie within the displayed bounds, nor do they directly give the probability that one arm is better than the other. They characterize the precision of the estimates under the interval method.

For the unadjusted risk difference, the recalculated estimate is 0.176, with a 95% confidence interval from 0.038 to 0.314. That interval reflects uncertainty in the difference based on the posted summary statistics. It does not incorporate uncertainty about whether the recalculation matches the sponsor’s intended analysis. Because the sponsor’s reported Fisher Exact result is p = 0.99 and the discrepancy is flagged, the sponsor analysis remains the formal result to prioritize.

Confidence intervals are useful because they communicate more than a binary significant/not-significant label. Their range indicates which effect sizes remain compatible with the data under the method. Yet a confidence interval cannot account for unreported design choices, missing-data handling, or multiplicity adjustments. Nor does it establish clinical importance; that requires context and criteria not reported in the registry record.

The primary analysis denominators are 139 and 76, and the record defines the endpoint population as participants with both baseline and 3 month scores. The smaller analyzed population relative to total enrollment means the precision pertains to that endpoint set. The record does not report why participants lack an endpoint measurement or whether missingness differed by arm. Those omissions constrain conclusions about how well the estimates represent all randomized participants.

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 not the trial’s original design justification. For the primary binary endpoint, the displayed planning figures are participants per arm. They are based on the observed effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. In contrast, planning illustrations for time-to-event outcomes give the total number of events, not participants per arm, using the Schoenfeld method.

The 80% power column describes the number of participants per arm the illustration estimates would be needed to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and model were correct. The 90% power column makes the same kind of planning calculation for a higher chance of detecting that effect, and therefore generally requires more participants. These are prospective design illustrations, not a measure of the trial’s achieved power.

For the primary endpoint, planning for 100% of the observed effect gives 126 participants per arm for 80% power and 168 participants per arm for 90% power. Planning for 75% of the observed effect gives 224 participants per arm for 80% power and 299 participants per arm for 90% power. Planning for 50% of the observed effect gives 500 participants per arm for 80% power and 669 participants per arm for 90% power. Smaller effects require more participants because they are harder to distinguish from random variation.

These figures are illustrations based on the observed contrast, not evidence that the trial was adequately or inadequately powered. They are not observed power. The original sample-size justification and the trial’s own design assumptions are not reported in the registry record.

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 = 0.403; treatment proportion p₁ = 0.579; average p̄ = 0.491.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7070 = 1.3857.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6959 = 0.5857.
4. n = (1.3857 + 0.5857)² / (0.1761)² = 125.4, rounded up to 126 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 <- 0.402877697841727                          # control proportion
p1 <- 0.578947368421053                          # 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(922974)
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 = 126 (80% power), 168 (90% power)
 75% of observed effect: n per arm = 224 (80% power), 299 (90% power)
 50% of observed effect: n per arm = 500 (80% power), 669 (90% power)
power.prop.test: 125.4 
Simulated power at n = 126 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

The registry reports a Fisher Exact analysis comparing the two primary endpoint groups, with p = 0.99. It does not provide a corresponding effect estimate or confidence interval for that reported test. A separate simple unadjusted recalculation from the posted arm-level counts gives a risk difference of 0.176, a 95% confidence interval from 0.038 to 0.314, and an unadjusted p-value of 0.013.

These results conflict. The registry flags a discrepancy, but does not explain whether it reflects a difference in the analysis population, test implementation, endpoint coding, or another analytic detail. No explanation should be inferred from the available record. The recalculation is an independent unadjusted calculation from the posted summary statistics; it is not the sponsor’s analysis and does not replace it.

For interpreting the trial’s formal result, the sponsor’s own analysis takes precedence. The recalculation can help readers see what the posted counts imply under a straightforward unadjusted comparison, while also identifying that the record is internally inconsistent. The two results should be presented together with that distinction intact, rather than selecting the more statistically significant result or treating the discrepancy as resolved.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes across pain response, pain relapse, adverse events, fracture, spinal cord damage, function, and quality of life. Testing more than one outcome creates a multiplicity problem: as the number of statistical tests grows, the chance of obtaining at least one result that appears unusual under a null model can also grow. This general concern applies even when each individual test is performed correctly.

The registry record does not report a multiplicity adjustment, a hierarchy of outcomes, or a plan distinguishing confirmatory from exploratory analyses. It also does not report the original statistical analysis plan or whether any interim analyses were conducted. Without this information, the status of secondary p-values and the family of tests to which they belong cannot be reconstructed. Secondary p-values should therefore be interpreted with caution rather than as stand-alone confirmation.

For the primary endpoint, the registry defines an analysis population consisting of eligible phase III participants randomized in the study who had both baseline and 3 month NRPS scores. The endpoint counts are 139 in the Radiosurgery/SBRT group and 76 in the external-beam group. The record does not report reasons for absent scores, the extent of missingness by group, or a method for handling missing endpoint data. It also does not say whether participants with incomplete measurements were excluded, imputed, or treated in another way beyond the stated endpoint population definition.

These omissions matter because the estimated response percentages describe the analyzed participants. If availability of scores is related to prognosis, treatment assignment, or pain response, the analyzed group could differ from the randomized population in ways that affect interpretation. The registry data do not establish that such bias occurred; they leave it unassessable. Details of intention-to-treat analyses, sensitivity analyses for missing data, and the original sample-size justification are not reported in the registry record.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fever (5.9%), back pain (5.9%), hemoglobin decreased (2.9%), chills (2.9%), alanine aminotransferase increased (2.9%).

The safety record gives counts at risk and counts affected by serious and other adverse events for three groups: Radiosurgery/SBRT in phase II, Radiosurgery/SBRT in phase III, and external-beam radiation therapy. Serious adverse events were recorded for 5 of 34 participants at risk in the phase II Radiosurgery/SBRT group, 19 of 196 in the phase III Radiosurgery/SBRT group, and 10 of 117 in the external-beam group. Other adverse events were recorded for 30 of 34, 141 of 196, and 76 of 117 participants at risk, respectively.

These are descriptive counts, not estimates adjusted for differences in follow-up or participant characteristics. The registry also lists deaths of 1, 144, and 80 in those same groups. The record does not establish from these counts whether deaths were caused by treatment, the underlying cancer, or other factors. The top listed serious event terms include fever and back pain, each shown as 5.9%, along with several terms shown as 2.9%. These listings do not provide a complete account of each participant’s clinical course or establish comparative causality.

Safety counts should be read alongside the group denominators and the outcome definitions. The record does not report detailed exposure time or a complete explanation of how event attribution was determined, limiting direct comparisons between groups.

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

The posted primary response percentages describe the proportion of analyzed phase III participants who met a specific combined pain-response definition at 3 months. That definition depends on the index-site pain score, changes in narcotic medication, and pain scores at other treated sites. The result is therefore not simply a comparison of average pain scores, and it does not summarize every aspect of pain or function.

The arm estimates and their confidence intervals show uncertainty around the observed response proportions. The unadjusted recalculation gives a different inferential result from the sponsor’s reported Fisher Exact analysis, and the registry flags this discrepancy. The sponsor’s analysis takes precedence as the trial’s own reported analysis, while the recalculation remains a check based on posted summary data. The record does not explain the difference, so no single explanation should be assumed.

These results do not establish that either treatment approach works or does not work. They do not show that the groups are equivalent, because an equivalence or noninferiority framework and margin are not reported. They also do not determine what an individual participant would experience. Group-level percentages are averages over the analyzed population and do not predict an individual outcome.

The secondary outcomes add context but have their own definitions, follow-up periods, and analysis methods. The registry’s lack of reported multiplicity handling, missing-data methods, and fuller analysis details limits how definitively they can be interpreted. The most defensible reading is bounded: the posted data show the stated response proportions in the defined endpoint population, the formal sponsor test is p = 0.99, and an unadjusted recalculation conflicts with that reported test. Important design and analysis details are not reported in the registry record.

18. Why This Trial Matters Statistically

This study illustrates why reading clinical trial statistics involves more than comparing two percentages or deciding whether a p-value crosses a threshold. The primary endpoint is clearly described as a responder percentage, but its classification combines pain scores, medication changes, and pain at secondary treated sites. Understanding that definition is necessary before interpreting what the percentages represent.

It also illustrates the importance of keeping sponsor-reported analyses distinct from unadjusted recalculations. Here, the registry’s own Fisher Exact analysis and the recalculation from the posted counts conflict, and the registry flags the discrepancy. That makes transparency about the source and status of each result essential. A recalculation can be informative as a check, but cannot silently replace the trial’s reported analysis.

Confidence intervals add information about precision that a single p-value cannot provide. The primary estimates have intervals broad enough to leave uncertainty around the response proportions and their contrast. The sample-size illustrations show how planning requirements change when a smaller effect is targeted, while also making clear that such figures are not observed power and are not the original trial’s design justification.

Finally, the record highlights common limits in registry-based interpretation: missing-data handling, multiplicity plans, and detailed analysis specifications may not be available. Recognizing those gaps is part of statistical analysis, not a reason to invent missing details. The result is a more careful account of what the record establishes and what remains uncertain.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details that would help interpret the estimates are not reported in the registry record. The randomization procedure and allocation concealment are not described, and masking is listed as none. This is relevant because the primary outcome includes participant-reported pain scores. The record does not describe any steps used to reduce potential influence in outcome assessment.

The primary endpoint applies to phase III participants with both baseline and 3 month NRPS scores, with reported arm counts of 139 and 76. The record does not explain why other participants are not included in those denominators, how missing scores were handled, or whether sensitivity analyses assessed the effect of missing measurements. Consequently, the estimates cannot be assumed to represent every randomized participant without qualification.

The registry reports a discrepancy between the sponsor’s Fisher Exact result and the unadjusted recalculation from the posted counts, but does not explain its source. The sponsor’s reported analysis takes precedence, while the unresolved discrepancy limits independent reconciliation. The registry also does not report the original statistical analysis plan, multiplicity strategy, interim analyses, or sample-size justification. The phase II/III label is present, but the phase-transition criteria and decision process are not reported.

Arm descriptions beyond intervention names are absent. Numerical results for several listed secondary outcomes are also not reported in the registry record. These gaps restrict assessment of treatment delivery, outcome completeness, and the relationship between the primary result and the full set of planned outcomes. They do not prove that the omitted procedures or analyses were absent from the conduct of the study; they mean the registry record does not document them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Image-Guided Radiosurgery or Stereotactic Body Radiation Therapy in Treating Patients With Localized Spine Metastasis — NCT00922974.
• Registry record last updated 2025-04-29; status last verified 2021-04.
• Results first posted 2019-05-16.
• 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

NCT00922974 is a completed randomized phase II/III parallel-group study sponsored by the Radiation Therapy Oncology Group. It enrolled 399 participants and compared Radiosurgery/SBRT with external-beam radiation therapy for localized spine metastasis. Masking is listed as none.

The primary phase III endpoint was the percentage of eligible randomized participants with both baseline and 3 month NRPS scores who had complete or partial pain response at 3 months. The posted response estimates were 40.3% for Radiosurgery/SBRT and 57.9% for external-beam radiation therapy. The registry’s reported Fisher Exact analysis gives p = 0.99, while a simple unadjusted recalculation gives p = 0.013; the discrepancy is flagged, and the sponsor’s own analysis takes precedence.

Secondary outcomes cover pain, adverse events, fracture, spinal cord damage, function, and quality of life. The record does not report several details needed to fully reconstruct the analysis, including missing-data handling, multiplicity plans, and the original sample-size justification.