Comparison of DTM™ SCS Therapy Combined With Conventional Medical Management (CMM) to CMM Alone in the Treatment of Intractable Back Pain Subjects Without Previous History of Lumbar Spine Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of DTM™ SCS Therapy Combined With Conventional Medical Management (CMM) to CMM Alone in the Treatment of Intractable Back Pain Subjects Without Previous History of Lumbar Spine Surgery (NCT06442410), a randomized na study. The primary outcome is Percentage of Individual Responders.

2. Clinical Question

The trial asks whether outcomes at six months differ between people assigned to DTM™ spinal cord stimulation (SCS) programming alongside conventional medical management (CMM) and people assigned to CMM alone. The study concerns chronic, intractable trunk pain, with or without lower-limb pain, among people without a previous history of lumbar spine surgery. The registry summary describes participants as refractory to conservative treatment and not candidates for lumbar spinal surgery.

3. Trial Design

The registry describes a randomized, unmasked, crossover study with an enrollment of 115. The recorded phase is NA, and the study status is completed. The study began on 2020-07-24, and primary completion was recorded on 2022-05-09. The sponsor is MedtronicNeuro.

The comparison is between DTM™ SCS programming combined with CMM and CMM alone. In the test-arm description, participants first underwent a Trial Phase with stimulation delivered from an external neurostimulator. Those who had a successful Trial Phase proceeded to permanent implantation of the Intellis™ SCS system. The description also refers to evaluation of DTM™ SCS therapy for up to 24 months, but the registry text does not give a complete account of the treatment sequence or all follow-up procedures. CMM was selected by the investigator as individualized conventional care.

The model is recorded as crossover, and safety results include an optional crossover group at six months. The registry record does not report enough detail to reconstruct the crossover schedule, the sequence allocation, or how treatment periods were incorporated into every analysis. It also does not report the original sample-size justification, details of any interim analyses, or a full statistical analysis plan. The primary endpoint is presented for a modified intent-to-treat population rather than all enrolled participants: successfully randomized test-arm participants who completed the Trial Phase and successfully randomized control-arm participants. That population definition matters when interpreting the group counts; enrollment should not be assumed to be the denominator for the primary comparison.

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 Non-Crossover

Optional Crossover at 6 Month

Analysis population for the primary outcome, as defined in the registry: Modified Intent to Treat (mITT): All successfully randomized subjects to the test arm who completed the Trial Phase and all successfully randomized subjects to the control arm.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Baseline analysis population included Modified Intent to Treat (mITT) population, defined as all successfully randomized subjects to the test arm who completed the Trial Phase and all successfully randomized subjects to the control arm.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Individual Responders, measured over 6 months.

The primary endpoint is the number of individual responders at six months. A responder was defined as a participant whose back-pain rating decreased by at least 50% on a 10 cm Visual Analog Scale (VAS). The scale is described in the registry as a psychometric instrument running from 0, no pain, to 10, the worst pain imaginable. The endpoint is therefore a binary classification derived from a pain rating: each participant either met the stated threshold or did not.

A threshold-based endpoint can make a group comparison easier to communicate than a mean change alone, because it expresses the number of participants reaching a defined amount of improvement. It also discards information: participants just above and just below the threshold are classified differently, while the size of changes among responders is not represented in the responder count. The VAS change outcomes reported separately retain information about the average scale change, but answer a different question.

The endpoint’s six-month time point and modified intent-to-treat population define the scope of the posted primary result. The registry record does not report further details about how missing six-month ratings were handled or whether additional responder definitions were prespecified.

7. Results Posted in the Registry

• Test Group - DTM™ SCS Programming Approach With Conventional Medical Management (CMM): 85.1% (40/47) versus 3.6% (2/56) on control; risk difference 81.5 percentage points (95% CI 70.3 to 92.8), risk ratio 23.83 (6.08–93.42); 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.

Percentage of Individual Responders

• 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:
  • Test Group - DTM™ SCS Programming Approach With Conventional Medical Management (CMM): 83.7% (41/49) versus 1.8% (1/57) on control; risk difference 81.9 percentage points (95% CI 71.0 to 92.8), risk ratio 47.69 (6.81–334.10); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Test Group - DTM™ SCS Programming Approach With Conventional Medical Management (CMM) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Visual Analog Scale (VAS) Back Pain 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:
  • Test Group - DTM™ SCS Programming Approach With Conventional Medical Management (CMM): mean -5.69 versus -0.36 on control; difference -5.33 (95% CI -6.05 to -4.61), standardized effect d = -2.92; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Test Group - DTM™ SCS Programming Approach With Conventional Medical Management (CMM) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary results include one-month responder status and one-month change from baseline in VAS back-pain score. Their broad observed pattern is consistent with the primary result in the limited sense that the posted group summaries show more threshold responders and a greater decrease in mean VAS score in the DTM™ SCS plus CMM group than in the CMM-alone group. These secondary outcomes measure different features of pain, and their one-month timing does not answer exactly the same question as the six-month primary endpoint.

There are 13 secondary analyses and 14 outcome measures recorded. Repeatedly examining outcomes, time points, or related measures increases the chance that some results will appear statistically notable by chance when each is considered separately. In general, multiplicity procedures can control the overall false-positive risk across a family of tests, but the registry record does not report whether a correction, prespecified hierarchy, or other multiplicity strategy was used.

Accordingly, unadjusted secondary results carry less confirmatory weight than a clearly prespecified primary comparison. They can add context and show whether different outcome measures tell a broadly compatible story, but they should not be treated as independent replications of the primary finding. Their interpretation is further limited by the incomplete reporting of analysis details and missing-data handling. The registry record does not report a complete secondary analysis plan, and the method label for the VAS mean-change analysis does not clarify how the sponsor analyzed that continuous outcome.

The other outcome titles include responder measures and VAS change measures, but the number of registered measures alone does not establish that every result was collected, analyzed, or reported in the same way. The overall secondary pattern is therefore best read as supportive descriptive context, not as a separate demonstration that resolves limitations in the primary comparison.

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

• Percentage of Individual Responders
• Percentage of Individual Responders
• Percentage of Individual Responders
• Percentage of Individual Responders
• Percentage of Individual Responders
• Percentage of Individual Responders
• Change From Baseline in Visual Analog Scale (VAS) Back Pain Score
• Change From Baseline in Visual Analog Scale (VAS) Back Pain Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is counted as a responder or a non-responder using the registry’s threshold of at least 50% reduction in back-pain VAS rating. For such an outcome, group counts and denominators are the basic descriptive quantities. They show how many participants met the endpoint among those included in the analysis population. The primary counts are 40 of 47 in the DTM™ SCS plus CMM group and 2 of 56 in the CMM-alone group.

What does the registry test assess?

The registry reports a Chi-squared test for the primary comparison and gives p < 0.001, with the result classified as superiority. In general, a Chi-squared test assesses whether the observed distribution of categorical outcomes across groups is compatible with no association between group and outcome. It does not account automatically for every feature of a study design. The registry record does not report whether the primary test incorporated the crossover structure, adjusted for baseline variables, or used any additional model.

The unadjusted recalculation is based on the posted group counts and denominators. It is a simple comparison and does not replace the sponsor’s own analysis. The recalculated result is reported as p <0.001. Because both analyses report small p-values, they point to a clear observed separation, but their p-value thresholds should not be treated as identical: one is the registry’s stated value and the other is the unadjusted recalculation.

How should a p-value be understood?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of the analysis, if that null hypothesis were true. It is not the probability that the treatment has no effect, nor does it quantify the probability that the result will reproduce. A p-value does not show the magnitude or precision of a difference; counts and confidence intervals address other aspects of interpretation.

What does the crossover design add?

A crossover study can involve participants receiving more than one treatment condition in sequence, allowing comparisons that may use within-participant information. The registry identifies the model as crossover and reports an optional crossover at six months in the safety listings. The precise sequence, timing, and analysis of treatment periods are not reported in the registry record. Consequently, the primary comparison should be read as the registry presents it, without assuming that the reported Chi-squared test adjusted for within-participant correlation or period effects. In general, analyses of crossover data may need to account for such features because observations from the same participant are not necessarily independent and outcomes may vary by period.

The primary population is modified intent to treat. It includes successfully randomized subjects in the test arm who completed the Trial Phase and successfully randomized subjects in the control arm. This differs from a population defined as everyone enrolled, and the test-arm condition may affect who contributes to the primary endpoint. The record does not report the number or reasons for participants who did not meet this population definition, or whether sensitivity analyses assessed the impact of those exclusions.

What are the other outcome measures?

The registry reports 13 secondary analyses and 14 outcome measures. The posted secondary results include responder status at one month and change from baseline in VAS back-pain score at one month. A responder count remains binary; a mean change is continuous. For the VAS result, the reported group means are -5.69 cm for the DTM™ SCS plus CMM group and -0.36 cm for the CMM-alone group, with standard deviations of 2.17 and 1.46. The unadjusted recalculation reports a mean difference of -5.33 cm and a confidence interval from -6.046 to -4.614, with p <0.001. The registry’s reported analysis for this outcome is labeled Chi-squared and NON-INFERIORITY, despite the endpoint being a continuous mean change; the record does not provide enough detail to resolve that method-label relationship.

For continuous outcomes, a mean summarizes the center of the observed values, while a standard deviation describes their spread. A mean difference compares group averages, and its confidence interval conveys uncertainty in that estimate under the analysis assumptions. The registry record does not report the full modeling specification for the secondary outcomes, including any baseline adjustment or handling of repeated measurements.

Why do design and analysis details matter?

Randomization is intended, in general, to balance prognostic factors between groups on average, but the registry record does not describe the randomization procedure or allocation concealment. Masking is recorded as none. Lack of masking can matter for outcomes based on participant ratings, because expectations or knowledge of treatment assignment may influence reporting. This is a general consideration, not evidence that such influence occurred in this trial.

The original sample-size assumptions and any prespecified analysis plan are not reported in the registry record. The planning illustrations associated with the observed results use their own stated assumptions and should not be mistaken for the original trial design. Likewise, posted secondary p-values do not establish that multiplicity was controlled. These limits make it important to distinguish the reported counts and estimates from questions the registry does not answer.

11. Confidence Intervals and Precision

A confidence interval gives a range of values that are compatible with the observed data under a specified statistical method and its assumptions. In general, a narrower interval indicates greater precision for the quantity being estimated; it does not guarantee that the estimate is unbiased or that the method’s assumptions are appropriate. An interval is not a range containing a fixed proportion of individual participant outcomes, and it is not the probability that the true effect lies within that particular interval.

For the six-month binary outcome, the posted counts are 40 of 47 responders in the test group and 2 of 56 in the control group. The unadjusted recalculation reports a risk-difference confidence interval from 0.703 to 0.928. This interval describes uncertainty in the unadjusted difference in responder proportions, on the risk-difference scale. The confidence interval is relatively informative about the size of the observed separation under that calculation, but it does not address unreported design features, missing outcomes, or potential effects of the crossover structure.

The one-month VAS comparison has a recalculated mean difference of -5.33 cm, with a confidence interval from -6.046 to -4.614. This interval concerns the difference between group means in change from baseline, not the variation among individual participants. The group standard deviations describe observed dispersion, whereas the confidence interval concerns uncertainty in the estimated contrast.

Precision should be considered alongside the population and analysis definitions. The primary population excludes test-arm participants who did not complete the Trial Phase, and the record does not report the missing-data pattern or sensitivity analyses. Confidence intervals based on the posted summaries cannot resolve those uncertainties. The registry’s own primary report gives a p-value but no confidence interval for its analysis, so the recalculated interval is not a substitute for a registry-reported interval from the sponsor’s full analysis.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations give participants per arm for the responder outcomes and for the VAS mean comparison; they are not totals across both arms. No time-to-event outcome is involved in these illustrations, so the total-events convention for time-to-event planning does not apply. The illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the effect to detect. The original trial’s own design assumptions are not reported in the registry record.

The 80% power column describes a planning scenario in which the assumed design would have an 80% chance of detecting the specified effect at the stated significance level, if the planning assumptions were correct. The 90% power column describes the corresponding scenario with a 90% chance. These are prospective planning quantities, not measures of how likely the completed trial was to detect an effect after the results were known. They are not observed power.

For the six-month responder comparison, the illustrations give 5 participants per arm for 80% power and 6 for 90% power when planning for 100% of the observed effect; for 75% of that effect, they give 9 and 11; for 50%, they give 16 and 21. For the one-month responder outcome, corresponding figures are 5 and 6, 8 and 10, and 15 and 20. For the one-month VAS change, the figures are 2 and 3, 4 and 5, and 8 and 10. These small planning figures reflect the large observed contrasts used as inputs, not an independently established design requirement.

Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm under the same assumptions. The illustrations also rely on a normal approximation and equal allocation, and do not describe the complexities of the crossover design or any original protocol choices. They should therefore be read as conditional planning examples based on the posted effects, rather than as recommendations for another 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 = 0.036; treatment proportion p₁ = 0.851; average p̄ = 0.443.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7026 = 1.3770.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4015 = 0.3379.
4. n = (1.3770 + 0.3379)² / (0.8153)² = 4.4, rounded up to 5 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 <- 0.0357142857142857                          # control proportion
p1 <- 0.851063829787234                          # 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(6442410)
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 = 5 (80% power), 6 (90% power)
 75% of observed effect: n per arm = 9 (80% power), 11 (90% power)
 50% of observed effect: n per arm = 16 (80% power), 21 (90% power)
power.prop.test: 4.4 
Simulated power at n = 5 per arm: 0.888 (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 reports a Chi-squared test, classifies the comparison as superiority, and gives p < 0.001. The unadjusted recalculation from the posted six-month counts gives p <0.001 and a risk-difference confidence interval from 0.703 to 0.928. Both describe a strong separation in the posted responder counts, but they are not the same analysis: the registry result is the sponsor’s reported test, while the recalculation is a simple unadjusted comparison of summary counts.

The registry record does not provide the sponsor’s complete statistical specification or a confidence interval for the primary comparison. It therefore is not possible to establish from the record whether the sponsor’s test used covariate adjustment, incorporated crossover features, or handled missing data in a particular way. The sponsor-reported result should be distinguished from the recalculation rather than assumed to be reproducible from the summary counts alone.

The secondary VAS entry also reports a Chi-squared method and a NON-INFERIORITY label, although the outcome is a mean change. The unadjusted recalculation treats the posted summaries as a continuous comparison. Without further methodological details, the reported secondary label cannot be reconciled fully with that recalculation. The record does not report a detailed statistical plan explaining these choices.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, or statistical tests are examined. Even if each test is conducted at a conventional significance threshold, the chance of at least one apparently significant result across a set of tests can increase as the number of tests grows. In general, a prespecified testing hierarchy or multiplicity adjustment can help control this issue. The registry lists 13 secondary analyses and 14 outcome measures, but a multiplicity strategy is not reported in the registry record. The primary result is therefore distinct from the secondary findings, which should not be given the same confirmatory interpretation without knowing whether and how multiple testing was addressed.

The primary population is modified intent to treat. It includes successfully randomized test-arm subjects who completed the Trial Phase and successfully randomized control-arm subjects. The record does not report how many randomized people were excluded from that population, why they were excluded, or whether the analysis population was specified before results were known. It also does not report the amount of missing outcome data, the reasons for missingness, or the procedure used to handle missing six-month ratings.

Missing data can affect a comparison if the likelihood of an outcome being unavailable is related to group assignment or to the outcome itself. This is a general statistical concern, not a claim about what happened in the study. Sensitivity analyses can assess whether conclusions change under alternative assumptions about missing outcomes; such analyses are not reported in the registry record.

The registry record also does not report the full statistical analysis plan, the original sample-size justification, whether interim analyses were conducted, or details of randomization and allocation concealment. Masking is recorded as none. For a participant-reported pain scale, lack of masking is relevant as a potential source of measurement influence in general, but the record does not establish that it altered the reported scores. These gaps constrain assessment of the robustness of both primary and secondary analyses.

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: osteoarthritis (4.0%), postoperative wound infection (3.6%), post procedural infection (2.0%), jaw fracture (2.0%), lung neoplasm malignant (2.0%).

The safety listings report serious adverse events affecting 15 of 55 participants at risk in the DTM™ SCS plus CMM group, 3 of 57 in the CMM-alone group, and 10 of 50 in the optional crossover group. Other adverse events affected 29 of 55, 6 of 57, and 21 of 50, respectively. No deaths are listed in any of these groups.

These figures are descriptive counts of participants affected, not a randomized comparison adjusted for exposure time, treatment sequence, baseline risk, or other factors. The optional crossover group is listed separately, so its count should not be combined with either original group as though it were an independent parallel arm. The registry record does not give enough detail to determine the timing of every event relative to treatment or to attribute events to a particular intervention.

The serious-event terms listed include osteoarthritis at 4.0%, postoperative wound infection at 3.6%, and post procedural infection, jaw fracture, lung neoplasm malignant, and meningitis viral at 2.0% each. Such term-level percentages do not by themselves establish causation, severity patterns beyond the serious-event classification, or comparative risk. Serious adverse event counts should be interpreted alongside the study’s group definitions and the incomplete event-level information in the registry record.

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

The posted data show that the number of participants meeting the six-month responder definition was substantially higher in the DTM™ SCS plus CMM group than in the CMM-alone group within the registry-defined modified intent-to-treat population. The registry’s Chi-squared analysis reports p < 0.001 and labels the result superiority. The unadjusted recalculation from the summary counts also indicates a clear group separation. This is a description of the observed trial result, not a claim that an intervention will have the same effect in every setting or for every person.

The outcome is based on a specific threshold for self-reported back-pain change. It does not capture all dimensions of pain, function, quality of life, or treatment burden. The posted secondary outcomes add information about one-month responder status and average VAS change, but they do not replace the six-month primary endpoint or establish long-term outcomes. The trial summary describes follow-up of up to 24 months for successful trial participants proceeding to implantation, but detailed long-term results are not included among the outcomes analyzed in this explanation.

The registry’s unmasked crossover design, the modified intent-to-treat population, and the absence of reported information about missing outcomes and analysis details limit what can be concluded. In particular, the summary record does not show how the primary test accounted for crossover structure, or whether the test-arm Trial Phase completion requirement could affect the analyzed population. These uncertainties do not erase the observed counts, but they matter when judging how fully the statistical result represents the study design.

The data do not establish the cause of individual adverse events, quantify every trade-off between possible benefits and harms, or resolve questions about durability and generalizability. They also do not provide individualized medical guidance. The statistical conclusion is narrower: the registry reports a marked difference in the six-month responder counts between the analyzed groups, with a small p-value under the reported test, while important design and analysis details remain unreported.

18. Why This Trial Matters Statistically

This trial is statistically notable because it combines a randomized comparison with a patient-reported, threshold-based pain endpoint and a crossover model. The main result is readily interpretable as counts of participants meeting a prespecified-looking responder definition, but the record does not provide the full analysis plan needed to establish which design features were incorporated into the reported test. That distinction illustrates why a striking group contrast and a complete account of its analysis are separate requirements for interpretation.

The modified intent-to-treat definition is especially relevant. Test-arm participants had to complete the Trial Phase to enter the primary analysis population, while control-arm participants were included if successfully randomized. This eligibility difference is explicit in the registry definition and should remain visible when interpreting the result. It also highlights why enrollment totals cannot be substituted for endpoint denominators.

The unmasked design and reliance on a participant-rated pain scale raise general questions about measurement and expectations, without demonstrating that either influenced the findings. The crossover designation also makes analysis details important, because repeated or sequential treatment observations may require methods that account for participant-level dependence and period effects. Those details are not reported in the registry record.

Finally, the trial shows why secondary outcomes, safety counts, confidence intervals, and planning illustrations need separate readings. Secondary findings may align descriptively with the primary pattern but are less confirmatory when multiplicity handling is unknown. Safety counts do not establish causation. Recalculated confidence intervals describe precision under an unadjusted method, and sample-size illustrations based on observed effects are not evidence about original design adequacy. Together, these distinctions support a more careful reading than relying on a single p-value or headline result.

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 interpreting this registry record. First, the study is labeled crossover, but the record does not describe the treatment sequence, period structure, carryover considerations, or whether the primary analysis accounted for within-participant dependence. An optional crossover at six months appears in the safety listings, but that alone does not reconstruct the primary comparison’s design or analysis.

Second, the primary population requires test-arm participants to complete the Trial Phase. The group denominators are therefore not simply the full enrollment, and the record does not report the number or characteristics of people who did not enter the modified intent-to-treat population. No missing-data method or sensitivity analysis is reported. The potential effect of these population and missingness choices cannot be evaluated from the posted summaries.

Third, the study was unmasked, and the primary endpoint is based on participant-reported pain ratings. This is a potential source of measurement influence in general, but the record does not establish whether it affected responses. The exact randomization procedure and allocation concealment are also not reported.

Fourth, the registry’s primary result gives a Chi-squared test and p-value but does not include a confidence interval or a complete statistical specification. The unadjusted recalculation uses summary counts and may not reflect design adjustments in the sponsor’s analysis. For the continuous VAS secondary outcome, the reported method label is Chi-squared and the analysis type is NON-INFERIORITY; the record does not explain this combination. Multiplicity handling for the secondary outcomes is also not reported.

Finally, the available summary does not provide detailed event timing or attribution for adverse events, and the listed safety groups should not be treated as directly comparable risk estimates. Long-term outcome details, original sample-size justification, and interim-analysis information are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparison of DTM™ SCS Therapy Combined With Conventional Medical Management (CMM) to CMM Alone in the Treatment of Intractable Back Pain Subjects Without Previous History of Lumbar Spine Surgery — NCT06442410.
• Registry record last updated 2024-11-07; status last verified 2024-10.
• Results first posted 2024-11-07.
• 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

NCT06442410 is a completed, randomized, unmasked crossover study sponsored by MedtronicNeuro. It enrolled 115 participants and compared DTM™ SCS programming with CMM against CMM alone for intractable back pain in people without previous lumbar spine surgery.

The six-month primary endpoint was the number of participants with at least a 50% reduction in back-pain VAS rating. In the modified intent-to-treat population, the posted counts were 40 of 47 in the DTM™ SCS plus CMM group and 2 of 56 in the CMM-alone group. The registry reports a Chi-squared superiority analysis with p < 0.001. The unadjusted recalculation reports p <0.001.

Secondary results include one-month responder status and VAS change. Safety listings report serious adverse events and other adverse events in the original groups and an optional crossover group, with no deaths listed. Details of missing-data handling, multiplicity, the full analysis plan, and the original sample-size justification are not reported in the registry record.