Safety and Efficacy Study of the Evoke™ SCS System With Feedback vs. Conventional Stimulation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of the Evoke™ SCS System With Feedback vs. Conventional Stimulation (NCT02924129), a randomized na study. The primary outcome is Number of Participants With Composite Endpoint Success.

2. Clinical Question

The clinical question is a comparison between two stimulation approaches, not a comparison of stimulation with no device or no treatment. The posted results describe endpoint counts in the two randomized groups. They do not establish from the endpoint alone which component of the composite accounts for success, since the registry record reports the composite count rather than separate counts for pain reduction and medication change.

3. Trial Design

The study, NCT02924129, is titled “Safety and Efficacy Study of the Evoke™ SCS System With Feedback vs. Conventional Stimulation.” Its official title describes a prospective, multicenter, randomized, double-blind study of the Evoke SCS system with feedback for chronic pain of the trunk and/or limbs. The design is parallel group, with feedback stimulation compared against conventional stimulation.

The registry record lists an enrollment of 134 and a completed status. The study start date is 2017-01-27, and primary completion is listed as 2018-06-21. The primary endpoint timeframe is 3 months. The posted primary endpoint counts use denominators of 62 for feedback and 63 for conventional stimulation. These are the denominators reported for that endpoint; the registry record does not explain the relationship between those denominators and the enrollment figure.

Randomization and double masking are reported, but the randomization procedure, allocation concealment details and the identities of people masked are not reported in the registry record. The protocol’s planned sample size and the original design assumptions are also not reported in the registry record. A separate planning illustration can be derived from the observed effects, but that is not evidence of the assumptions used when the trial was designed.

The registry record describes the feedback arm as closed-loop or automatic stimulation and the conventional arm as open-loop or manual stimulation. It reports the device intervention as the Evoke SCS System. Additional details of stimulation programming, treatment exposure, follow-up beyond the listed endpoint timeframe, or protocol deviations are not reported in the registry record. The record lists 10 outcome measures and 10 analyses overall, while nine secondary outcomes are listed as posted. The available secondary results include pain-score changes and a pain-reduction threshold outcome.

The trial has a binary primary endpoint: each participant is classified as a composite success or not. Its primary analysis population is ITT, but the registry description also specifies how presumed non-responders are treated. Those population and classification details matter when interpreting the counts, because the endpoint is not simply a count of participants who had a recorded pain-score change.

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: Intention-to-Treat (ITT), which included randomized patients with either known endpoint status or classified as a presumed non-responder (i.e., \<50% reduction in overall pain at trial or withdrew due to a device- or stimulation-related adverse event), and therefore imputed as a failure.

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 Number of Participants With Composite Endpoint Success, measured over 3 months.

The primary endpoint counts participants who meet a composite success definition at 3 months. Success requires both a reduction in overall trunk and limb pain VAS score greater than or equal to 50 percent and no increase in baseline pain medication. The VAS is described as a 0-to-100 mm scale, with 0 representing no pain and 100 representing worst imaginable pain. A participant who meets the pain reduction criterion but has an increase in baseline pain medication would not meet the full composite definition.

The endpoint is binary for analysis: each participant contributes a success or a failure classification. The ITT description includes randomized participants whose endpoint status is known and those classified as presumed non-responders. The latter include participants with less than 50% reduction in overall pain at trial or those who withdrew due to a device- or stimulation-related adverse event; they are imputed as failures. The registry record does not provide separate outcome counts for each reason for failure or a breakdown of the pain and medication components.

Using a composite can represent more than one aspect of an outcome in a single measure. In this case, it links a threshold of pain reduction to the absence of increased baseline medication. That makes the success count clinically interpretable as meeting both stated conditions, but it also means the count cannot identify which component most influenced the group-level result. The primary endpoint is therefore distinct from the secondary measures of average percentage change in leg or back pain and from the threshold outcome based on an 80% reduction.

7. Results Posted in the Registry

• Evoke SCS With Conventional: 60.3% (38/63) versus 82.3% (51/62) on control; risk difference -21.9 percentage points (95% CI -37.3 to -6.6), risk ratio 0.73 (0.58–0.92); unadjusted two-proportion z-test p = 0.007.

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.

Percent Change From Baseline in Leg Pain VAS Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Evoke SCS With Conventional: mean 67.80 versus 76.80 on control; difference -9.00 (95% CI -20.25 to 2.25), standardized effect d = -0.28; z-test p = 0.117.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Evoke SCS With Conventional and the control. The interval gives the range of effects that remain compatible with the data.

Percent Change From Baseline in Back Pain VAS Score

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Evoke SCS With Conventional: mean 57.50 versus 72.10 on control; difference -14.60 (95% CI -26.19 to -3.01), standardized effect d = -0.44; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Evoke SCS With Conventional than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Proportion of Subjects With Greater Than or Equal to 80% Reduction From Baseline in Overall Trunk and Limb Pain VAS Score

• 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:
  • Evoke SCS With Conventional: 42.9% (27/63) versus 58.1% (36/62) on control; risk difference -15.2 percentage points (95% CI -32.5 to 2.1), risk ratio 0.74 (0.52–1.05); unadjusted two-proportion z-test p = 0.089.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Evoke SCS With Conventional and the control. The interval gives the range of effects that remain compatible with the data.

The available secondary results cover average percentage change in leg pain, average percentage change in back pain and the proportion reaching an 80% reduction in overall trunk and limb pain. They address related but distinct aspects of pain response: group averages can reflect the distribution of changes across participants, while a threshold count focuses on the number meeting a defined response level. Neither continuous pain measure includes the medication condition built into the primary composite endpoint.

Across these outcomes, the descriptive averages are higher in the feedback group, and the 80% reduction count is also higher in that group. However, the unadjusted recalculated comparisons are not uniform in their uncertainty: the leg-pain and 80% threshold intervals include zero, while the back-pain interval does not. The sponsor’s posted analyses for these outcomes are labeled non-inferiority, and their interpretation depends on margins and analysis details that are not reported in the registry record.

These secondary findings provide context for the primary composite result, but they do not independently reproduce that endpoint. The primary result requires both a pain reduction threshold and no increase in baseline pain medication. The secondary outcomes either summarize mean pain change or use a different pain-reduction threshold, and the registry record does not provide a component-level breakdown of the primary composite.

Unadjusted secondary results carry less weight as confirmatory evidence when multiple outcomes are examined. In general, testing many outcomes can increase the chance of at least one apparently notable result arising by chance. The registry record does not report a multiplicity adjustment or hierarchy that would establish which secondary tests were confirmatory. The secondary pattern can therefore be considered descriptive and supportive context, but it should not be used to turn individual unadjusted results into definitive conclusions.

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

• Percent Change From Baseline in Leg Pain VAS Score
• Percent Change From Baseline in Back Pain VAS Score
• Proportion of Subjects With Greater Than or Equal to 80% Reduction From Baseline in Overall Trunk and Limb Pain VAS Score
• Proportion of Subjects With Greater Than or Equal to 50% Reduction From Baseline in Back Pain VAS Score
• Number of Participants With Composite Endpoint Success
• Percent Change From Baseline in Leg Pain VAS Score
• Percent Change From Baseline in Back Pain VAS Score
• Proportion of Subjects With Greater Than or Equal to 80% Reduction From Baseline in Overall Trunk and Limb Pain VAS Score

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods determine what a reported estimate compares, how uncertainty is represented and what question a test addresses. The primary outcome is a binary count, while several secondary outcomes are means of percentage change. The reported sponsor analyses are labeled non-inferiority; the recalculations are simple unadjusted comparisons of posted summary statistics. Those analyses should be read as related but not automatically equivalent.

What does a binary risk difference mean?

For a binary endpoint, each participant is classified as having or not having the event of interest. Here, the event is composite endpoint success. A risk difference compares the observed proportions of successes between two groups. Its sign depends on the order of subtraction. The recalculated risk difference is defined as conventional minus feedback, so a negative estimate corresponds to a lower observed success proportion in the conventional group. This direction convention should be kept in view when comparing the estimate with counts or with a result using the opposite group order.

A risk difference stays on the absolute probability scale. It describes the group contrast in the observed success proportions rather than a ratio of probabilities. Its confidence interval represents a range of values compatible with the data and the calculation’s assumptions. An interval that includes zero is compatible with no difference on this scale under the calculation; an interval that does not include zero indicates that zero is outside that particular interval. Neither statement alone determines the clinical importance of the estimate.

What does the sponsor’s non-inferiority test ask?

In general, a non-inferiority test evaluates whether one treatment is not worse than another by more than a prespecified margin. The margin defines how much difference is acceptable for that specific question. A non-inferiority p-value depends on the chosen margin, direction of comparison and analysis plan. The registry record labels the primary and listed secondary analyses as non-inferiority, but the non-inferiority margin and full hypothesis specifications are not reported in the registry record. The reported p-value therefore cannot be interpreted as a general test that the groups are identical, nor can it be mapped directly to the recalculated risk-difference p-value without the missing details.

The registry says the primary analysis used a normal approximation to the binomial. In general, this method approximates the sampling distribution of a binary outcome contrast with a normal distribution. The quality of that approximation depends on the data and the exact procedure used. The record does not provide enough detail to reproduce the sponsor’s non-inferiority test or its confidence bounds for the primary outcome.

How do the continuous outcomes differ?

The secondary leg- and back-pain outcomes are reported as mean percentage changes from baseline, with standard deviations. A mean describes the group average, while a standard deviation describes variability among participant values around that average. The recalculations compare these means as unadjusted mean differences. The sign again depends on group order: the reported recalculated contrast is conventional minus feedback. The standardized effect shown in the calculations expresses the contrast relative to a pooled standard deviation; it is a scale-free summary, not a direct clinical threshold.

The registry’s continuous-outcome analysis is labeled a two-sided t-test and specifies a mean difference in final values. The recalculation instead uses the posted mean percentage-change summaries. A comparison of final values and a comparison of percentage changes from baseline can target different parameters. The registry record does not report sufficient detail about the underlying data, adjustments or exact model to establish that the sponsor’s test and recalculated comparison estimate the same quantity. The difference in p-values should therefore be read in light of the distinct analysis descriptions, rather than treated as a direct replication check.

In general, standard errors quantify the sampling uncertainty of an estimate and are used to construct confidence intervals and test statistics. Larger variability or less information tends to make estimates less precise. For the posted continuous summaries, the group means and standard deviations support an unadjusted comparison; participant-level data would be needed to evaluate assumptions and alternative models in detail. The recalculation does not adjust for baseline values or other covariates.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variability exceeds what a model assumes. For count or binary data, an analysis that assumes less variability than is actually present can produce uncertainty estimates that are too narrow and tests that appear more decisive than warranted. The primary outcome is a binary participant count, but the registry record does not report an over-dispersion assessment or an alternative variance model. The simple recalculation likewise does not test for over-dispersion.

What is the role of the analysis population?

The ITT population aims to retain randomized participants in the groups to which they were assigned. The registry’s endpoint description specifies that participants with known status are included and identifies a class of presumed non-responders as failures. That rule affects the binary outcome classification. In general, explicit rules for missing or unavailable outcomes matter because different assumptions can change the number of successes and the estimated contrast. The record does not report additional sensitivity analyses for missing outcomes or a full accounting of endpoint status by reason.

Because the primary and secondary outcomes are multiple opportunities to examine results, unadjusted p-values warrant caution. In general, when many hypotheses are tested, the chance of observing at least one apparently notable result by chance can increase. A prespecified multiplicity strategy can address that concern, but such a strategy is not reported in the registry record. The recalculated p-values are therefore descriptive inferential summaries and should not be read as multiplicity-adjusted evidence.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is -0.219, with a 95% confidence interval from -0.373 to -0.066. The interval lies on the conventional-minus-feedback scale. It conveys uncertainty around the estimated absolute difference in composite success proportions under this calculation. Because zero is outside the interval, the recalculated interval is inconsistent with a zero risk difference at its stated confidence level, subject to the calculation’s assumptions. It does not incorporate the registry’s non-inferiority margin or any unreported adjustments.

A confidence interval is not a range containing a fixed proportion of individual participant outcomes. In general, it is a method for expressing the uncertainty of an estimate across repeated samples under specified assumptions. A narrower interval indicates greater precision for the parameter being estimated; a wider interval indicates more uncertainty. Precision is not the same as clinical importance, and an estimate’s direction does not by itself establish that the difference matters to participants.

The secondary estimates show differing precision. For the recalculated leg-pain mean difference, the interval runs from -20.25 to 2.246 and includes zero. For back-pain change, the interval runs from -26.19 to -3.009 and excludes zero. For the 80% reduction risk difference, the interval runs from -0.325 to 0.021 and includes zero. These intervals correspond to different outcome measures and should not be compared as if they represented the same quantity.

The registry’s reported continuous analyses give 95% intervals for final-value mean differences: -2.4 to 20.4 for leg pain and 2.9 to 26.3 for back pain. These use a different analysis description from the recalculated percentage-change contrasts. The primary sponsor analysis reports a p-value but no confidence interval in the registry record. The record also does not report the non-inferiority margin needed to interpret precision against that criterion. Thus, the posted information supports an assessment of uncertainty for the recalculated contrasts, but not a complete reconstruction of the sponsor’s primary inferential framework.

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 illustrations are planning calculations based on fractions of the observed effect, not the original trial’s design calculations. The primary and available secondary outcomes are binary or continuous, so the displayed figures are participants per arm, not total event counts. The note about total event counts applies to time-to-event outcomes, and no such outcome is included in these calculations.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation and an effect to detect equal to the stated fraction of the observed effect. The protocol’s original sample-size justification and design assumptions are not reported in the registry record. The equal allocation and other assumptions belong to this planning illustration, and should not be assumed to describe the trial’s original design.

For each effect-size scenario, the 80% power column gives the estimated number of participants per arm that the planning calculation would require to have an 80% chance of detecting that specified effect under the stated assumptions. The 90% power column gives the corresponding estimate for a 90% chance. These are planning probabilities under a statistical model, not guarantees about what a future study will observe. Smaller effects require more participants to distinguish the effect from random variation at the same power and significance level. The table’s rows therefore illustrate how requirements rise as the assumed detectable effect is reduced from the observed effect.

The planning figures are not observed power. Observed power is not a useful substitute for reading the estimated effect and its uncertainty after results are known. These illustrations are most useful for understanding how sample-size needs depend on the assumed effect and desired power, rather than for judging the success or adequacy of this completed trial.

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 = 0.823; treatment proportion p₁ = 0.603; average p̄ = 0.713.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6398 = 1.2540.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6207 = 0.5224.
4. n = (1.2540 + 0.5224)² / (-0.2194)² = 65.6, rounded up to 66 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 <- 0.82258064516129                          # control proportion
p1 <- 0.603174603174603                          # 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(2924129)
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 = 66 (80% power), 88 (90% power)
 75% of observed effect: n per arm = 111 (80% power), 148 (90% power)
 50% of observed effect: n per arm = 232 (80% power), 310 (90% power)
power.prop.test: 65.6 
Simulated power at n = 66 per arm: 0.803 (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’s own primary analysis is labeled non-inferiority and reports p < 0.001 using a normal approximation to the binomial. The recalculation uses the posted primary counts to estimate an unadjusted risk difference and gives p = 0.007. These p-values address different specified analyses: a non-inferiority test depends on its margin and direction, whereas the recalculation compares the observed success proportions without that framework. The registry record does not report the margin or full testing details, so the sponsor’s test cannot be reconstructed from the listed information alone.

For continuous secondary outcomes, the registry describes two-sided t-tests of mean differences in final values. The recalculations compare the posted means of percentage change from baseline. Since those descriptions do not necessarily target the same parameter, their estimates and p-values are not direct substitutes for one another. For example, the registry-reported p-values for the continuous outcomes are each listed as p < 0.001, while the recalculated unadjusted p-values differ. That contrast should be understood alongside the different analysis descriptions and not taken on its own as evidence that either result is erroneous.

The registry record does not provide enough detail about margins, models, covariate adjustment or the complete analysis plan to reconcile every reported analysis with the recalculations. The recalculated values are transparent summaries of posted group-level statistics, but they cannot replace participant-level analysis or the sponsor’s prespecified analysis. No discrepancy is flagged for this record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint alongside multiple secondary outcomes and analyses. When several hypotheses are tested, the chance of at least one small p-value can increase even if no corresponding effect exists. General methods for addressing this include adjusting significance thresholds, controlling the false discovery rate, or prespecifying a testing hierarchy. Which approach, if any, was used for this trial is not reported in the registry record.

The posted analyses are labeled non-inferiority, but the non-inferiority margins are not reported in the registry record. Without the margins and complete hypotheses, the reported p-values cannot be interpreted against a clearly stated acceptable difference. The record also does not report whether the primary analysis was the sole confirmatory test, how secondary tests were ordered, or whether any interim analyses were planned or conducted. Those details should not be inferred from the posted p-values.

The primary population description states that the ITT analysis included randomized participants with known endpoint status or those classified as presumed non-responders. The latter category includes participants with less than 50% reduction in overall pain at trial or withdrawal due to a device- or stimulation-related adverse event, who were imputed as failures. This is a stated classification rule, but the registry record does not provide a full accounting of endpoint availability, missingness reasons or how every participant was handled.

In general, missing-data assumptions matter because observed outcomes may differ systematically from unobserved ones. Treating specified cases as failures is one explicit rule, but it does not reveal the impact of other missing data or establish whether results are robust to alternative assumptions. Sensitivity analyses for missing outcomes and the detailed analysis population flow are not reported in the registry record.

Randomization and double masking are reported, but further details of sequence generation, concealment, masking procedures and any departures from the assigned intervention are not reported in the registry record. Similarly, the record does not describe interim monitoring or stopping rules. These omissions limit assessment of the full prespecified statistical framework; they do not establish that a procedure was or was not used.

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: cellulitis (1.5%), arrhythmia and irregularities (1.5%), cardiac chest pain (1.5%), dehydration (1.5%), diverticulitis (1.5%).

The serious adverse event summaries report 7 affected participants among 67 at risk in the feedback group and 4 among 67 at risk in the conventional group. Other adverse events are reported for 14 among 67 at risk in the feedback group and 15 among 67 at risk in the conventional group. The registry reports zero deaths in each group. These counts describe the posted safety summaries and their stated at-risk denominators.

The serious adverse event terms listed at 1.5% each are cellulitis, arrhythmia and irregularities, cardiac chest pain, dehydration, diverticulitis and epidural abscess. The record does not specify in this list which group each term belongs to, nor does it provide a detailed participant-level account for these terms. The same participant may also contribute to more than one event category; the registry record does not clarify that issue in the listed summary.

Safety counts are descriptive. They do not by themselves establish whether an event was caused by the device or stimulation, or whether group differences are statistically meaningful. The at-risk denominators in the safety report differ from the posted primary endpoint denominators; the registry record does not explain the difference. Interpretation should remain tied to the event definitions, follow-up and reporting details available in the registry record.

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

The posted primary endpoint counts indicate that more participants in the feedback group met the composite success definition than in the conventional group. The unadjusted recalculation estimates a negative risk difference for conventional minus feedback, with an interval excluding zero. The registry’s own primary analysis is reported as a non-inferiority test, but the margin and full testing plan are not reported in the registry record. These results should therefore be understood as evidence about the posted comparison under the analyses described, not as a complete account of every statistical question relevant to the trial.

The endpoint is a composite of pain reduction and medication use. A success means meeting both conditions; a failure does not reveal which condition was not met. The posted results do not separate those components, and they do not show how individual pain scores changed over time. Secondary pain outcomes add context but are not equivalent to the composite.

The findings are specific to the randomized comparison of feedback-controlled and conventional Evoke SCS in the enrolled population and to the reported endpoint timeframe. The registry record does not report enough detail to assess all features of treatment delivery, participant characteristics, missing outcomes or analysis choices. The results therefore do not establish how the comparison would apply to people outside the studied population, to other devices or treatment approaches, or to outcomes not reported in the registry.

Statistical evidence and clinical importance are related but distinct. A confidence interval describes uncertainty in an estimated contrast; it does not define a threshold for a meaningful difference. The registry record does not report a clinical importance threshold for the primary risk difference. Nor does the reported non-inferiority p-value establish equivalence, since the margin and full test specification are unavailable. The appropriate reading is a bounded description of the observed endpoint results and their stated uncertainty, rather than a general claim about treatment effectiveness or individual outcomes.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and the direction of a contrast matter. The primary event is a composite success, and the recalculated risk difference is expressed as conventional minus feedback. Without keeping both the composite definition and subtraction order in view, the sign of the estimate could easily be misread. Reporting the group counts alongside an absolute contrast helps clarify what is being compared.

It also demonstrates the distinction between a sponsor’s non-inferiority test and a simple unadjusted recalculation. A p-value is meaningful only in relation to the hypothesis and analysis that produced it. Here, the registry labels the sponsor analyses as non-inferiority, while the posted summary counts allow an unadjusted contrast. Because the non-inferiority margin is not reported in the registry record, the sponsor’s inferential question cannot be fully reconstructed from the record alone.

The secondary results emphasize that related outcomes do not necessarily point to identical conclusions. Mean changes, responder thresholds and a composite involving medication use answer different questions and can have different precision. Their interpretation also depends on whether multiplicity was addressed, a strategy not reported in the registry record.

Finally, the sample-size illustrations show how planning needs depend on the effect chosen for detection and the desired power. They are distinct from the original trial design assumptions, which are not reported in the registry record, and from post-trial observed power. Together, these issues make the study useful for understanding how outcome definition, test choice, uncertainty and planning assumptions shape the statistical reading of a clinical trial.

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.

Several limitations are specific to the information reported for this trial. The registry record does not report the non-inferiority margin, complete statistical analysis plan, original sample-size justification, or whether any interim analyses were planned or conducted. As a result, the sponsor’s non-inferiority p-values cannot be assessed against a fully specified hypothesis or reproduced from the registry record.

The primary endpoint is composite, but no separate counts for pain reduction and medication change are reported. The ITT description states that certain presumed non-responders were imputed as failures, but a full participant flow and breakdown of endpoint status by reason are not reported in the registry record. The relationship between the enrolled number and the endpoint denominators is also not explained.

The available recalculations use group-level summary statistics and are unadjusted. They cannot account for participant-level covariates, verify distributional assumptions, or reproduce a participant-level model. The sponsor’s reported continuous analyses refer to mean differences in final values, whereas the recalculations compare percentage changes from baseline. This limits direct comparison between the two sets of results.

Multiplicity procedures, detailed masking and allocation methods, treatment adherence, protocol deviations, and sensitivity analyses are not reported in the registry record. The safety summaries provide counts and selected event terms, but do not supply detailed event timing, attribution or participant-level overlap. These limitations concern the completeness of the statistical record and do not imply that unreported procedures or information were absent from the study itself.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of the Evoke™ SCS System With Feedback vs. Conventional Stimulation — NCT02924129.
• Registry record last updated 2024-01-03; status last verified 2023-12.
• Results first posted 2021-05-25.
• 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

NCT02924129 is a completed, prospective, multicenter, randomized, double-blind, parallel-group study of the Evoke SCS system with feedback versus conventional stimulation for chronic pain of the trunk and/or limbs. Enrollment is listed as 134, with a primary endpoint timeframe of 3 months.

The primary outcome counts participants meeting a composite success definition based on pain reduction and no increase in baseline pain medication. The posted counts are 51 of 62 in the feedback group and 38 of 63 in the conventional group. The registry reports a non-inferiority analysis with p < 0.001; an unadjusted recalculation gives a risk difference of -0.219 for conventional minus feedback, with a 95% confidence interval from -0.373 to -0.066.

The registry record does not report the non-inferiority margin, original sample-size assumptions or full multiplicity and missing-data plans. Secondary results and safety summaries add context, but their interpretation is limited by the distinct outcome definitions and the level of detail available.