Effectiveness of the Precision Spinal Cord Stimulator System at Sub-Perception Amplitude: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effectiveness of the Precision Spinal Cord Stimulator System at Sub-Perception Amplitude (NCT02314000), a randomized na study. The primary outcome is Proportion of Subjects With 50% or Greater Reduction in Overall Pain Intensity From Baseline.

2. Clinical Question

The registry describes the study objective as demonstrating sustained clinically significant pain relief when the system is used at sub-perception amplitude. The posted primary endpoint makes the question more specific: participants must meet the pain-reduction threshold and also have no increase in average daily pain-medication intake. It therefore concerns the proportion meeting both conditions, rather than pain intensity alone.

The crossover design means the comparison is not simply between two groups that each used only one setting. The registry says all subjects contributed toward each arm, as reflected in the participant counts. The posted outcome does not provide a separate result for each treatment sequence, or a description of how sequence or period effects were handled. Those details are not reported in the registry record.

3. Trial Design

This was a randomized, unmasked crossover study of the Precision or Precision Spectra Spinal Cord Stimulator System in people with chronic pain. The registry lists enrollment as 229 and status as completed. It identifies Boston Scientific Corporation as the sponsor. The study start is listed as 2014-12 and primary completion as 2016-12. The phase is recorded as NA.

The two arm descriptions define opposite starting sequences. One began with supra-perception amplitude and was followed by sub-perception stimulation; the other began with sub-perception amplitude and was followed by supra-perception stimulation. The registry identifies one device intervention. It does not report the duration of each treatment period, any washout interval, or the detailed timing of the crossover beyond those descriptions. These design details are not reported in the registry record.

The primary outcome was assessed at 90 days post activation. It counted participants with a 50% or greater reduction in overall pain intensity from baseline and no increase in average daily medication intake to treat pain. The registry explicitly notes that, because of the crossover design, all subjects contributed toward each arm. The posted counts are 32 of 119 for supra-perception amplitude and 41 of 118 for sub-perception amplitude.

Masking is listed as none. The record therefore identifies the study as unmasked, but does not describe who knew the assigned sequence or how outcome assessment was conducted. It also does not report the randomization procedure, allocation concealment, treatment-period adherence, or rules for handling participants who did not complete both periods. These details are not reported in the registry record. The design description supports understanding that both amplitude settings were used in different sequences, but does not by itself establish how the statistical comparison accounted for the paired or repeated observations inherent in a crossover study.

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

Analysis population for the primary outcome, as defined in the registry: Due to the nature of crossover study design, all subjects contributed towards each arm, as reflected in the number of participants.

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 Proportion of Subjects With 50% or Greater Reduction in Overall Pain Intensity From Baseline, measured over 90 days post activation.

The primary endpoint counts participants with a 50% or greater reduction in overall pain intensity from baseline at 90 days post activation, provided average daily medication intake to treat pain did not increase. A participant either meets both parts of this definition or does not, so the endpoint is binary and the posted result is a count of participants.

The pain threshold specifies a degree of change relative to each participant’s baseline rather than relying only on the average pain score at follow-up. The medication condition adds a second criterion: pain reduction counts toward the endpoint only when it occurs without an increase in average daily pain-medication intake. This makes the endpoint a combined measure of pain response and medication use as defined in the registry.

Such a responder outcome can be easier to interpret as a proportion meeting a stated threshold than a change in mean score alone. However, it also compresses the underlying information: it does not show how far above or below the threshold participants’ pain changes fell, nor the distribution of medication changes. The registry record does not report the instrument used to measure overall pain intensity, the handling of missing baseline or follow-up values, or further endpoint-scoring rules. Those details are not reported in the registry record.

7. Results Posted in the Registry

• SCS With Sub-perception Amplitude: 34.7% (41/118) versus 26.9% (32/119) on control; risk difference 7.9 percentage points (95% CI -3.9 to 19.6), risk ratio 1.29 (0.88–1.90); unadjusted two-proportion z-test p = 0.190.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant either met the combined responder definition or did not. The posted results therefore give participant counts for each condition. A risk is the proportion of participants meeting the endpoint within a condition. The comparison reports a risk difference, risk ratio, and odds ratio, which express contrasts between those condition-specific proportions in different ways.

What the risk difference describes

The risk difference is the absolute contrast between the proportions meeting the outcome. The registry reports a risk difference of 0.079 for sub-perception relative to supra-perception amplitude. A positive estimate means that the observed proportion was higher for the sub-perception condition in the direction used by the registry’s comparison. The confidence interval, from -0.039 to 0.196, expresses uncertainty around that estimate. Because the interval includes zero, the posted data are compatible with no difference as well as with differences in either direction.

How relative measures differ

The risk ratio compares the proportions as a ratio; the reported estimate is 1.292, with a 95% confidence interval from 0.878 to 1.901. The odds ratio compares the odds of meeting the endpoint; its reported estimate is 1.448, with a 95% confidence interval from 0.831 to 2.521. Ratios use a different scale from the risk difference, so their numerical values should not be compared directly with the difference estimate. For both ratios, the null value is one. Each reported interval includes that value.

General: An effect estimate is a summary of the observed contrast under a chosen statistical measure. A confidence interval conveys the uncertainty of that estimate under the method used to construct it. It is not a guarantee that the true effect lies inside the interval, and it does not directly assign probabilities to individual possible effects.

What the p-value means

The registry reports an unadjusted p-value of 0.19. General: A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null model and its assumptions were correct. It is not the probability that the null hypothesis is true, nor a direct measure of the size or importance of an effect. The registry record does not report a complete statistical analysis plan or details of the model underlying this comparison.

Why crossover structure matters

In a crossover study, a participant receives conditions in sequence, so observations from the same participant may be related. General: Analysis methods for crossover data can account for that within-participant relationship and may consider period or sequence effects. Treating paired observations as independent can affect the estimated uncertainty. The record says all subjects contributed toward each arm, but does not report whether or how the comparison accounted for pairing, period, or sequence. That limits what can be inferred about the method from the posted counts alone.

What is not specified

The registry lists one primary outcome measure and no posted secondary outcomes, while the comparison includes an unadjusted p-value. The record reports zero analyses in its analysis listing. It does not give a detailed model specification, covariate adjustment plan, analysis population definition beyond the note about crossover contributions, or missing-data procedure. Those details are not reported in the registry record. The unadjusted designation also means the reported p-value should not be described as adjusted for multiple comparisons.

General: For a binary endpoint, different methods can be used to estimate proportions and compare conditions, and the choice can affect uncertainty estimates. The registry record does not identify the precise calculation method for the confidence intervals or the effect estimates. The posted results can be described as registered, but details not in the record should not be inferred from the numerical values alone.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.079, with a 95% confidence interval from -0.039 to 0.196. The interval crosses zero, so the posted data do not exclude either no difference or differences in either direction. Its span indicates that the estimate is uncertain; the point estimate should not be treated as a precise measure of the contrast.

The reported relative measures also have intervals that include their respective null values. The risk ratio is 1.292, with an interval from 0.878 to 1.901; the odds ratio is 1.448, with an interval from 0.831 to 2.521. These estimates are consistent with a range of possible contrasts, rather than fixing one precise relative effect.

General: A confidence interval reflects sampling uncertainty under the method and assumptions used to calculate it. A wider interval indicates less precision, while a narrower interval indicates greater precision, all else equal. An interval that includes a null value is not proof that the conditions are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin; such a margin is not reported in the registry record.

The p-value of 0.19 is also part of the uncertainty picture, but it does not replace the effect estimate or its interval. The record does not report the interval-construction method or enough detail about crossover analysis to assess how repeated observations were handled. Accordingly, the precision represented by the posted interval should be interpreted in light of the statistical methods that are, and are not, described in the registry record.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrative calculations based on the observed effect, rather than the trial’s own design assumptions. The listed 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 defined as a stated fraction of the observed effect.

Planning for 100% of the observed effect gives 542 participants per arm for 80% power and 725 participants per arm for 90% power. Planning for 75% of the observed effect gives 946 participants per arm for 80% power and 1,266 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,088 participants per arm for 80% power and 2,795 participants per arm for 90% power.

In general, the 80% power column describes the planned number of participants per arm under which the specified calculation would have an 80% chance of detecting the assumed effect if that effect and the other assumptions were correct. The 90% power column makes the corresponding illustration for a 90% chance. These are planning probabilities under a model, not guarantees about a future study or the probability that the treatment effect is real.

Smaller effects are harder to distinguish from random variation, so the illustration requires more participants per arm as the assumed fraction of the observed effect decreases. The calculations are not observed power. The original trial’s sample-size justification and design assumptions are not reported in the registry record; these illustrative figures should not be treated as the trial’s planned enrollment target.

12. 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 = 0.269; treatment proportion p₁ = 0.347; average p̄ = 0.308.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6530 = 1.2799.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6506 = 0.5476.
4. n = (1.2799 + 0.5476)² / (0.0786)² = 541.3, rounded up to 542 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 <- 0.26890756302521                          # control proportion
p1 <- 0.347457627118644                          # 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(2314000)
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 = 542 (80% power), 725 (90% power)
 75% of observed effect: n per arm = 946 (80% power), 1,266 (90% power)
 50% of observed effect: n per arm = 2,088 (80% power), 2,795 (90% power)
power.prop.test: 541.3 
Simulated power at n = 542 per arm: 0.804 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and no posted secondary outcomes. It reports a comparison with an unadjusted p-value of 0.19. The record does not report a multiplicity adjustment or a broader testing plan. Without that information, the p-value should be described as unadjusted and should not be interpreted as accounting for other analyses that may or may not have been performed.

The record lists zero analyses in its analysis listing, even though a primary outcome comparison and an unadjusted p-value are posted. It does not explain that distinction or provide a full statistical analysis plan. The model, analysis population rules, planned covariates, and treatment of the crossover sequence are not reported in the registry record.

The primary outcome note says all subjects contributed toward each arm because of the crossover design. The posted participant counts are 119 for supra-perception amplitude and 118 for sub-perception amplitude, while overall enrollment is 229. The registry does not explain the difference between the enrollment count and the arm-specific outcome counts. It also does not state whether these counts reflect missing endpoint data, exclusions, or another analysis rule. No reason should be inferred from the counts alone.

Missing-data handling is not reported in the registry record. The record does not describe how participants without an evaluable outcome were treated, whether imputation was used, or whether sensitivity analyses were conducted. The analysis population beyond the crossover note is likewise not specified. These omissions matter because the estimated proportion can depend on which participants are included and how unobserved outcomes are handled.

General: Multiplicity refers to the increased chance of a chance finding when many outcomes, comparisons, or analyses are tested. Prespecifying a primary outcome and an analysis plan helps readers understand which result is central and how additional testing is handled. The registry identifies a primary outcome, but does not report enough detail to assess the full analysis and missing-data strategy.

14. 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

Serious events with the highest arm-level rate: pneumonia (1.4%), gastroenteritis (0.7%), cystitis (0.7%), diverticular perforation (0.7%), enterocolitis heamorrhagic (0.7%).

For all study patients through the end of the randomized phase, the registry reports 7 serious adverse events among 140 participants at risk, zero other adverse events in the listed other-event category, and zero deaths. For the supra-perception amplitude group, it reports 3 serious adverse events among 140 at risk, zero other adverse events, and zero deaths. For the sub-perception amplitude group, it reports 4 serious adverse events among 140 at risk, zero other adverse events, and zero deaths.

The serious-event terms listed include Pneumonia at 1.4%, and Gastroenteritis, Cystitis, Diverticular Perforation, Enterocolitis Heamorrhagic, and Post Procedure Infection at 0.7% each. These are term-specific entries in the registry. The record does not provide further context about event timing, severity beyond the serious-event classification, relatedness to the device or treatment, or whether an individual could contribute more than one event. The terms should not be read as proof of causation.

General: Adverse-event counts describe reports within the stated safety groups and observation period. They do not, on their own, establish comparative risk, especially when the record does not explain event-level handling or the statistical method used. The safety figures are descriptive and should be interpreted alongside the registry’s group definitions and the limits of the information recorded.

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

The primary result describes how many participants met a specific combined endpoint: at least a 50% reduction in overall pain intensity from baseline, with no increase in average daily medication intake to treat pain, at 90 days post activation. The registry reports 32 of 119 participants meeting this definition with supra-perception amplitude and 41 of 118 with sub-perception amplitude. Its risk-difference estimate is 0.079, with a 95% confidence interval from -0.039 to 0.196.

The interval includes zero, and the unadjusted p-value is 0.19. These results do not establish a clear difference between the amplitude conditions. They also do not establish that the conditions are equivalent. The uncertainty interval spans contrasts in both directions, and the registry does not report an equivalence margin or an equivalence analysis.

The endpoint is narrower than the broad idea of pain relief. It counts participants meeting a defined threshold and medication condition; it does not show the distribution of pain changes, the amount of change among responders, or medication patterns for participants who did not meet the endpoint. The registry lists no secondary outcomes, so the posted results do not supply a broader set of outcomes for interpreting the study.

The study is described as a randomized crossover, but the registry does not report how the comparison handled repeated measurements, period effects, or sequence. The available result should therefore be interpreted as the posted comparison, with uncertainty about the analytical details. Missing-data procedures and the exact analysis population are also not reported in the registry record.

These findings are statistical descriptions of the registered outcome, not medical advice. They do not establish what an individual participant would experience, and they do not by themselves determine the clinical importance of a possible difference. That judgment would require context beyond the endpoint counts and estimates recorded.

16. Why This Trial Matters Statistically

This trial is statistically interesting because its crossover structure means the same participants contributed to both amplitude conditions, according to the registry’s outcome note. Crossover designs can make within-participant comparisons informative, but the analysis needs to account appropriately for the relationship between observations from the same person. The registry record does not explain how the posted comparison handled that feature, or whether period and sequence effects were considered. This makes clear reporting of the analysis especially important.

The primary outcome is a binary responder measure with two requirements: a 50% or greater reduction in overall pain intensity and no increase in average daily pain-medication intake. This endpoint is interpretable as a proportion meeting a threshold, but it conceals the amount and distribution of changes within each response category. Reading the effect estimate alongside the participant counts and confidence interval helps avoid treating the responder proportions as a complete description of all pain outcomes.

The reported risk-difference interval includes zero and extends in both directions. That feature illustrates why an estimate should be considered together with its precision rather than interpreted from its point estimate or p-value alone. The unadjusted p-value is 0.19, while the record does not provide a full statistical analysis plan, a missing-data strategy, or details about multiplicity.

The planning illustrations also show how assumptions about the effect to detect influence the participant numbers required in a future study. Smaller assumed effects correspond to larger planning figures. These calculations are based on the observed effect and should not be mistaken for the original trial’s sample-size justification, which is not reported in the registry record. Together, the design and reporting features make the distinction between the observed estimate, its uncertainty, and the assumptions behind planning calculations important for statistical interpretation.

17. 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 several trial-specific details unclear. Although the study is identified as randomized and crossover, the randomization procedure, allocation concealment, treatment-period lengths, washout arrangements, and detailed timing of the sequence are not reported. Masking is listed as none, but the record does not specify which people involved in treatment or outcome assessment knew the sequence.

The primary outcome counts are posted for 119 participants in the supra-perception condition and 118 in the sub-perception condition, while enrollment is 229. The registry says all subjects contributed toward each arm, but does not explain the arm-specific counts or whether any endpoint data were missing. Missing-data rules, exclusions, adherence definitions, and sensitivity analyses are not reported in the registry record.

The record does not describe the statistical model or how the crossover data were analyzed. In particular, it does not state whether the analysis accounted for within-participant pairing, treatment sequence, or period effects. It also does not give a detailed endpoint measurement instrument or scoring procedure beyond the stated response threshold and medication condition. These gaps limit assessment of how the posted estimates were produced.

Only the primary outcome is posted, with no secondary outcomes listed. The registry does not report the full analysis plan, multiplicity procedures, or the original sample-size justification. Safety reporting is also limited to the posted event counts and terms; event timing, relatedness, and event-level overlap are not described. These limitations concern what is documented in the registry record and do not by themselves determine the quality or conduct of the study.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Effectiveness of the Precision Spinal Cord Stimulator System at Sub-Perception Amplitude — NCT02314000.
• Registry record last updated 2021-02-11; status last verified 2021-01.
• Results first posted 2019-04-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT02314000, titled “Effectiveness of the Precision Spinal Cord Stimulator System at Sub-Perception Amplitude,” is a completed randomized, unmasked crossover study of the Precision or Precision Spectra Spinal Cord Stimulator System in people with chronic pain. Enrollment is listed as 229; the start is 2014-12 and primary completion is 2016-12. Boston Scientific Corporation is listed as sponsor.

The primary outcome was the proportion with a 50% or greater reduction in overall pain intensity from baseline, without an increase in average daily medication intake to treat pain, at 90 days post activation. The posted counts were 32 of 119 with supra-perception amplitude and 41 of 118 with sub-perception amplitude. The risk difference was 0.079, with a 95% confidence interval from -0.039 to 0.196 and an unadjusted p-value of 0.19.

The registry lists no secondary outcomes. It does not report key analysis details, missing-data handling, or the trial’s original sample-size justification.