A Safety and Effectiveness Trial of Spinal Cord Stimulation of the Dorsal Root Ganglion for Chronic Lower Limb Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety and Effectiveness Trial of Spinal Cord Stimulation of the Dorsal Root Ganglion for Chronic Lower Limb Pain (NCT01923285), a randomized na study. The primary outcome is Primary Composite Endpoint - Treatment Success.

2. Clinical Question

3. Trial Design

The ACCURATE trial is identified in the registry as a prospective, randomized, multicenter, controlled clinical trial. Its listed phase is NA. It used a parallel-group design and had no masking. The two device groups were the AXIUM Neurostimulator System and a commercially available control spinal cord stimulation device. The sponsor is Abbott Medical Devices.

The registry records enrollment of 152 participants, a start date of 2013-08, primary completion in 2016-09, and status as completed. The registry's primary endpoint results are based on 69 AXIUM participants and 70 control participants. These endpoint denominators are distinct from the total enrollment, and the record explains that some participants did not have evaluable data for the primary endpoint. Safety results list 76 participants at risk in each group.

The primary endpoint was assessed at 3 months. The study also lists positional effects on paresthesia intensities as a secondary outcome, assessed at 3 months. The registry record reports one secondary outcome result. It does not report the full protocol, the reasons for choosing the enrollment target, the original sample-size assumptions, or detailed eligibility criteria in the registry record. Those details cannot be inferred from the posted enrollment or results.

Random allocation is intended, in general, to make treatment groups comparable on average with respect to measured and unmeasured baseline factors. In this trial, however, the registry lists no masking. Knowledge of assigned device may affect participant reporting, clinical decisions, or measurement procedures, depending on how assessments were conducted; those procedural details are not reported in the registry record. The registry also does not report enough information to judge how allocation was implemented or whether all planned analyses were completed.

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: Subjects excluded since they do not have evaluable data: Axium=4, Control=3. Seven subjects in the MITT analysis have no evaluable data for the study endpoints due to withdrawing prior to the 3-mo study visit and did not meeting criteria for treatment failure/success upon study exit.

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 Primary Composite Endpoint - Treatment Success, measured over 3 months.

The primary endpoint is a binary composite: each participant either met the registry definition of treatment success or did not. Success required at least 50% lower limb pain relief, measured as a reduction in Visual Analog Scale score, at the end of the trial phase; at least 50% relief at the 3-month visit after implantation; and absence of a stimulation-related neurological deficit. Failure to satisfy any required component means the endpoint is not met under this definition.

The Visual Analog Scale ranges from 0-100 mm, with higher scores indicating greater pain intensity; 0 represents No Pain and 100 mm represents Worst Imaginable Pain. The endpoint uses a threshold for relief rather than comparing average pain scores alone. A composite can capture more than one dimension relevant to the study question: symptom improvement and the absence of a specified neurological safety problem. At the same time, a composite proportion does not show which component most often determined success or failure. Component-specific primary endpoint results are not reported in the registry record.

For each arm, the reported percentage is the proportion of participants counted as meeting the composite endpoint among those included in that analysis. The registry notes exclusions for participants without evaluable endpoint data. Consequently, the reported percentages describe the analyzed participants and should be read alongside the missing-data explanation, not as proportions of all enrolled participants.

7. Results Posted in the Registry

• AXIUM Neurostimulator System: 81.2% (56/69) versus 55.7% (39/70) on control; risk difference 25.4 percentage points (95% CI 10.6 to 40.3), risk ratio 1.46 (1.15–1.85); unadjusted two-proportion z-test p = 0.001.

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.

Positional Effects on Paresthesia Intensities

• 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:
  • AXIUM Neurostimulator System: mean -0.10 versus 1.80 on control; difference -1.90 (95% CI -2.81 to -0.99), standardized effect d = -0.80; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AXIUM Neurostimulator System than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry reports one secondary outcome: positional effects on paresthesia intensities at 3 months. Its group summaries and inferential analysis address a continuous measure rather than the primary endpoint's binary composite. The reported test indicates a between-group difference on that secondary measure. It is therefore a related but distinct aspect of the device comparison, not another assessment of whether participants met the primary treatment-success definition.

The secondary finding can add context to the primary result by describing a different outcome dimension. It does not establish why the primary endpoint differed, identify which component of the composite drove the result, or show that the secondary measure predicts the primary outcome. The registry does not report analyses linking the secondary result to individual primary endpoint components, nor does it explain the clinical interpretation of a given score on the secondary scale.

Secondary results generally carry less confirmatory weight than a clearly prespecified primary analysis, especially when several outcomes or tests may be examined. Testing multiple hypotheses without an adjustment increases the chance that at least one result appears statistically unusual by chance. The registry record does not report whether a multiplicity procedure was planned or used. The secondary p-value should therefore be read as nominal evidence for that specific comparison, not as a multiplicity-adjusted confirmation of the overall trial conclusion.

The number of posted secondary outcomes is limited in the registry, but the record does not establish whether this represents every outcome collected or every analysis considered. The full protocol and statistical analysis plan are not reported in the registry record. This limits conclusions about outcome selection, analysis hierarchy, and whether the reported secondary result was planned before data were examined.

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

• Positional Effects on Paresthesia Intensities

9. Statistical Interpretation

10. Statistical Methods Explained

What does a binary endpoint comparison estimate?

General statistical explanation: a binary endpoint records whether an event or criterion is present for each participant. For this trial, the event is meeting the composite definition of treatment success. An arm-specific percentage estimates how common that event was among participants analyzed in that arm. The risk difference compares the two proportions by subtracting one from the other; the posted recalculation gives the estimate as 0.255. This is an absolute contrast, unlike a ratio measure, which compares proportions multiplicatively.

The registry also reports a risk ratio of 1.457 with a 95% confidence interval of 1.148 to 1.848, and an odds ratio of 3.424 with a 95% confidence interval of 1.592 to 7.364. These measures express the same binary outcome using different scales. A risk ratio compares event probabilities, while an odds ratio compares event odds. They are not interchangeable, and the odds ratio should not be read as though it were a percentage-point difference. For a clear clinical reading, the arm percentages and absolute risk difference are often easiest to interpret directly.

What do the chi-squared tests address?

The registry identifies chi-squared tests for both its non-inferiority and superiority analyses. General statistical explanation: a chi-squared test evaluates whether the observed distribution of a categorical outcome across groups is compatible with a specified null hypothesis. A p-value measures how unusual data at least as discrepant as those observed would be if that null hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of the difference.

Non-inferiority and superiority answer different questions. A non-inferiority analysis evaluates whether an intervention is not worse than a comparator by more than a prespecified margin. A superiority analysis evaluates evidence that one group has a better outcome than the other under the chosen endpoint definition. The registry reports results labelled non-inferiority and superiority, but the margin and the full testing procedure are not reported in the registry record. Without those details, the p-value for non-inferiority cannot be fully interpreted as a test against a particular clinical margin.

What does the recalculation add?

The recalculated risk difference and its confidence interval are simple, unadjusted calculations from the posted summary statistics. They offer a transparent descriptive contrast on the proportion scale. The recalculated p-value is also unadjusted. It is not a substitute for the sponsor's analysis, which is the primary source for the trial's own inferential plan and reported tests. Here, the record does not flag a discrepancy between the recalculation and sponsor analysis, although the p-values differ because the reported analyses are not presented as the same calculation.

General statistical explanation: an adjusted analysis may account for prespecified factors or design features, whereas an unadjusted analysis compares the groups without those adjustments. The registry record does not provide enough detail to establish whether the sponsor's analyses included additional adjustments beyond the reported chi-squared method. No such adjustments should be assumed from the summary alone.

How should uncertainty and missing outcomes be considered?

A confidence interval gives a range of estimates compatible with the data and the method used, under its assumptions. Its width reflects statistical precision: narrower intervals indicate less sampling uncertainty on that scale, while wider intervals indicate more. The arm-specific intervals and the interval for the risk difference help readers judge the range of plausible values, rather than relying only on whether a p-value crosses a conventional threshold.

The registry states that Axium=4 and Control=3 participants were excluded because they did not have evaluable data. It also notes that seven participants in the MITT analysis had no evaluable data for the study endpoints because they withdrew before the 3-mo study visit and did not meet criteria for treatment failure or success upon study exit. The record does not describe imputation, sensitivity analyses, or other procedures for handling these missing outcomes. Missingness can affect interpretation if the participants with unavailable outcomes differ systematically from those with observed outcomes. That is a general concern, not evidence that the posted comparison is biased in a particular direction.

Why can secondary analyses be less conclusive?

General statistical explanation: when multiple endpoints, time points, groups, or analyses are tested, the chance of obtaining at least one nominally small p-value can increase. Methods that control multiplicity adjust the decision threshold or otherwise account for the family of tests. The registry record does not report a multiplicity plan, so the reported secondary p-value should be treated as an unadjusted result unless other documentation establishes otherwise. This is one reason to give primary, prespecified outcomes more weight than exploratory or secondary findings.

The secondary endpoint is a continuous measure, and the registry reports a Wilcoxon (Mann-Whitney) analysis for it. General statistical explanation: this rank-based test compares the distributions of observations between groups and does not require the same normal-distribution model as a conventional two-sample t-test. The registry labels its reported parameter Mean Difference (Net), but the specific construction of that parameter is not explained in the record. The listed group means and standard deviations are descriptive statistics; they do not by themselves reveal the shape of the underlying distributions or the full analysis population.

Statistical methods answer particular questions under particular assumptions. They cannot resolve missing protocol details, determine whether the outcome definition is clinically meaningful for every participant, or establish how results apply beyond the studied population. Those judgments require the trial's full documentation and context, which are not reported in the registry record.

11. Confidence Intervals and Precision

The primary arm percentages are estimates, not exact population values. Their 95% confidence intervals are 69.9% to 89.6% for the AXIUM group and 43.3% to 67.6% for the control group. The width of each interval reflects the combination of observed data and the interval method. The intervals show that the estimated proportions are subject to sampling uncertainty, even though the point estimates are each stated to one decimal place.

For the primary between-group comparison, the recalculated risk difference is 0.255, and its 95% confidence interval is 0.106 to 0.403. The interval is entirely on the positive side of zero, consistent with a higher observed success proportion in the AXIUM arm in this unadjusted comparison. This describes the direction and statistical precision of the recalculation; it does not establish the clinical importance of every value within the interval. Clinical interpretation would require a prespecified threshold for a meaningful difference, which is not reported in the registry record.

A confidence interval is not a guarantee that the true effect falls inside the particular interval. General statistical explanation: the stated confidence level describes the long-run performance of the interval procedure under its assumptions, rather than the probability that this one fixed interval contains the true value. Intervals also do not correct for missing outcomes, lack of masking, or multiplicity unless the method explicitly addresses those issues.

The secondary analysis reports its own uncertainty interval, and its group summaries have different levels of spread. These figures should be interpreted on that outcome's scale, not used as a direct measure of precision for the primary binary endpoint. The registry does not provide enough detail to determine whether all uncertainty intervals account for the same design or analysis features. Precision should therefore be judged alongside the methods and endpoint definitions, not from decimal detail alone.

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 figures are illustrations based on the observed effect, rather than the trial's original design calculations. For this binary outcome, the entries are participants per arm. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the stated effect under those assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. These are planning concepts: power is the probability of detecting an effect of the specified size if that effect is present and the assumed model and design apply. They are not guarantees that a future study will detect the effect.

For planning for 100% of the observed effect, the figures are 52 participants per arm for 80% power and 69 participants per arm for 90% power. For planning for 75% of the observed effect, they are 97 and 129 participants per arm, respectively. For planning for 50% of the observed effect, they are 228 and 304 participants per arm. Smaller effects require more participants to detect with the same target power, because a modest contrast is harder to distinguish from random variation.

These planning figures are not observed power. Observed power calculated after a study is complete largely restates the observed effect and its uncertainty; it does not provide a separate measure of how convincing the result is. The confidence intervals and the design assumptions are more useful for understanding the observed evidence and for planning a new study.

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 = 0.557; treatment proportion p₁ = 0.812; average p̄ = 0.684.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6573 = 1.2882.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6322 = 0.5321.
4. n = (1.2882 + 0.5321)² / (0.2545)² = 51.2, rounded up to 52 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 <- 0.557142857142857                          # control proportion
p1 <- 0.811594202898551                          # 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(1923285)
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 = 52 (80% power), 69 (90% power)
 75% of observed effect: n per arm = 97 (80% power), 129 (90% power)
 50% of observed effect: n per arm = 228 (80% power), 304 (90% power)
power.prop.test: 51.2 
Simulated power at n = 52 per arm: 0.812 (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 analyses use chi-squared tests and report a non-inferiority result of p < 0.001 and a superiority result of p < 0.001. The simple recalculation from the posted group summaries gives a risk difference of 0.255, a 95% confidence interval from 0.106 to 0.403, and an unadjusted p-value of 0.001. The registry does not flag a discrepancy between the recalculation and the sponsor's analysis.

The recalculation is a plain, unadjusted comparison of the posted binary summary data. It does not reproduce the sponsor's full analysis plan, and the registry record does not give the non-inferiority margin or all details needed to reconstruct that plan. Different formulations of a test can produce different p-values while addressing related questions. In this case, the sponsor's reported analyses remain the relevant source for the trial's own inferential claims; the recalculated estimate and interval provide a complementary absolute-scale description of the observed contrast.

Neither the sponsor's p-values nor the recalculated p-value states the probability that the result is true. The effect estimate and its interval describe magnitude and uncertainty, while the test results describe compatibility with specified null hypotheses under their respective methods. Reading these together is more informative than treating one p-value as a complete account of the trial.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators evaluate more than one outcome, time point, subgroup, or statistical contrast. General statistical explanation: as the number of tests grows, the probability of at least one nominally significant result can rise even when no true effects exist. Prespecified procedures such as family-wise error control or false-discovery approaches can address different multiplicity goals. The registry record does not report whether the trial used such a procedure, or how it handled the relationship between the non-inferiority and superiority tests.

The record reports both non-inferiority and superiority analyses for the primary endpoint, as well as one secondary outcome analysis. It does not state whether these tests were ordered in a prespecified sequence, whether one test was contingent on another, or whether the secondary analysis was adjusted for multiplicity. The reported p-values therefore should not be assumed to have a particular family-wise interpretation beyond the tests explicitly named in the record.

Missing primary endpoint data are specifically noted. The record says Axium=4 and Control=3 participants were excluded because they lacked evaluable data. It further says seven participants in the MITT analysis had no evaluable data for study endpoints because they withdrew before the 3-mo visit and did not meet the criteria for treatment failure or success upon study exit. The record does not describe how these cases were treated in the statistical analysis beyond that explanation, and it does not report imputation or sensitivity analyses.

The phrase MITT appears in the registry's missing-data description, but the record does not fully define the analysis population or explain its relationship to other populations such as intention-to-treat or per-protocol sets. The exact handling of participants who withdrew, received an implant, or lacked later assessments is not reported in the registry record. These details matter because estimates can depend on who is included and how missing outcomes are treated.

The no-masking design and missing outcome data are separate considerations. Missing data may reduce precision and can create bias if availability of an outcome is related to the outcome itself or to treatment assignment. Lack of masking may affect outcome assessment or reporting for subjective measures. The registry's summary does not establish that either issue changed the result, but it also does not contain enough information to rule out their influence. Interpretation should reflect that uncertainty without assuming a particular direction of bias.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: substance relayed disorder/overdose or withdrawal (2.6%), wound infection (2.6%), arthritis (2.6%), abnormal blood chemistry (1.3%), lower extremity/bilateral leg pain (1.3%).

The registry lists 76 participants at risk for serious adverse events in each device group. It reports 8 participants with a serious adverse event in the AXIUM group and 15 in the control group. For other, non-serious adverse events, the record lists 5 participants affected in each group, with 76 at risk in each. Deaths are listed as 0 in both groups.

These are participant counts, not event counts: the record does not provide the total number of serious events experienced by participants or detail recurrence. Serious adverse event is also not the same category as a device-related event; the posted counts do not establish that an event was caused by the assigned device. The registry does not report event-level attribution or a complete account of severity, timing, or duration for all events.

The listed serious adverse-event terms include substance-related disorder/overdose or withdrawal, wound infection, arthritis, abnormal blood chemistry, lower extremity/bilateral leg pain, and injury/ADL. The registry gives percentages for these terms, but the summary alone does not clarify all coding, overlap, or attribution details. A zero death count in the posted groups describes the observed record and does not establish absence of other safety concerns.

Safety comparisons need cautious interpretation because the group counts are limited and the record gives no confidence intervals or formal comparative safety analysis for these summaries. The figures describe what was reported, not a definitive estimate of relative risk or proof of causation.

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

The primary result means that, among participants included in the endpoint analysis, a larger observed proportion in the AXIUM group met the registry's composite success definition than in the control group. The definition requires both specified levels of pain relief and no stimulation-related neurological deficit. The posted arm percentages, confidence intervals, and comparative tests describe the direction and statistical uncertainty of that particular result.

It does not mean that every participant experienced the same outcome, that each component of the composite improved, or that the observed group contrast will apply unchanged to other people or settings. The composite combines pain relief with a neurological safety condition, and the registry does not give separate results for its components. It also does not report a clinically important difference threshold for the primary outcome, so statistical evidence alone cannot establish the magnitude of benefit that patients or clinicians would consider meaningful.

The comparison concerns two implanted spinal cord stimulation devices in an unmasked randomized trial. It does not compare stimulation with no device or with every other form of care. The registry does not report enough information about participant characteristics, concurrent treatments, or clinical practice details to define the full context for generalization.

The result also does not settle all safety questions. The adverse-event summaries are counts, and the registry does not provide detailed event attribution or a complete safety analysis. Nor does a nominally small p-value remove uncertainty arising from missing endpoint data, possible measurement effects in an unmasked study, or unreported analysis-plan details.

Overall, the posted data document a difference in the primary endpoint proportions between the randomized groups and provide statistical evidence against equality under the reported comparisons. They do not, by themselves, establish causal mechanisms, long-term outcomes, or applicability beyond the studied trial. Such conclusions would require information not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a binary composite endpoint should be read through its definition, not only its percentage. The primary outcome combines pain relief thresholds at specified assessments with the absence of a stimulation-related neurological deficit. That construction makes the result a summary of several requirements, while leaving open which component most influenced the observed classification. Component-level reporting would help readers understand what the combined result represents, but those results are not reported in the registry record.

It also shows the value of presenting an absolute contrast alongside hypothesis tests. The arm percentages and recalculated risk difference express the observed comparison in terms of the probability of meeting the endpoint, while the confidence interval conveys uncertainty. A p-value alone cannot show the size of an effect or the range of estimates compatible with the data. Different statistical summaries answer related but distinct questions, so they should be interpreted together.

The registry reports both non-inferiority and superiority tests, yet the margin and full testing strategy are absent. This highlights a general reporting principle: a test label and p-value are not enough to reconstruct the clinical threshold or decision rule. Details of the hypothesis, analysis population, missing-data approach, and multiplicity handling are important for interpreting a randomized trial.

Finally, the distinction between trial-planning illustrations and the original design is important. Planning figures based on the observed effect can show how required participant counts vary with target effect and power, but they do not reveal what assumptions guided this trial before enrollment. The original sample-size justification is not reported in the registry record. Keeping these design questions separate from the observed result helps prevent a retrospective calculation from being mistaken for a prospective plan.

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.

The registry record leaves important design and analysis details unspecified. It does not report the original sample-size justification, the non-inferiority margin, the detailed statistical analysis plan, or whether multiplicity adjustments were used. It also does not report full eligibility criteria, baseline characteristics, or the exact method used to implement random allocation. These omissions restrict assessment of the trial's prespecification and the comparability of the groups.

The study was unmasked. Because the primary endpoint includes pain relief measured using a Visual Analog Scale, knowledge of assigned device could potentially influence reporting or assessment. The record does not describe safeguards for outcome assessment or how the neurological deficit component was adjudicated. This is a consideration for interpretation, not evidence that the assessment was biased.

Some participants lacked evaluable primary endpoint data. The registry explains the number and circumstances in its MITT analysis description, but it does not state how missing outcomes were handled analytically or report sensitivity analyses. Without those details, readers cannot determine how robust the result is to alternative assumptions about participants who withdrew before the 3-month assessment.

The primary endpoint is composite, and component-specific results are not reported in the registry record. This prevents assessment of whether the observed contrast was mainly associated with pain relief, the neurological condition, or both. The record also reports only one secondary outcome, and does not clarify whether that represents all outcomes considered in the study. Finally, the safety summary gives affected-participant counts but limited event detail and no comparative uncertainty estimates. These limits do not negate the posted observations, but they constrain how broadly and precisely they can be interpreted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Safety and Effectiveness Trial of Spinal Cord Stimulation of the Dorsal Root Ganglion for Chronic Lower Limb Pain — NCT01923285.
• Registry record last updated 2020-11-24; status last verified 2020-11.
• Results first posted 2020-11-24.
• 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

The ACCURATE trial was a completed, randomized, parallel-group, unmasked, multicenter device study with enrollment of 152 participants. It compared the AXIUM Neurostimulator System, designed to stimulate the dorsal root ganglion, with a commercially available control spinal cord stimulation device for chronic lower limb pain in people diagnosed with Complex Regional Pain Syndrome or Peripheral Causalgia.

The primary endpoint was a composite treatment-success measure assessed at 3 months. The registry reports a higher success proportion in the AXIUM group than in the control group and reports chi-squared non-inferiority and superiority analyses. A simple unadjusted recalculation gives a positive risk difference with a confidence interval that does not include zero. The registry also reports one secondary positional paresthesia outcome and serious adverse-event counts.

Interpretation is limited by missing endpoint data, the unmasked design, and details not reported in the registry record, including the non-inferiority margin, original sample-size justification, multiplicity plan, and full analysis procedures. The posted results describe the trial observations; they do not by themselves establish long-term outcomes or applicability beyond the studied participants.