Herniectomy Versus Herniectomy With a Spinal Stabilization System for the Treatment of Complex Disc Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Herniectomy Versus Herniectomy With a Spinal Stabilization System for the Treatment of Complex Disc Disease (NCT00749996), a randomized phase 4 study. The primary outcome is To Demonstrate a Statistically Significant Difference in the Relief of Back Pain Between Both Treatment Groups. The Endpoint Will be the Difference Between Baseline and 6-month of the Patient's Back-pain Score on a Visual Analogue Scale (VAS)..

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 4 study of herniectomy alone compared with herniectomy followed by the DIAM™ Spinal Stabilization System. The registry record lists enrollment as 165, identifies the study as completed, and gives a start date of 2006-11 and a primary completion date of 2013-04. It names Medtronic Spinal and Biologics as sponsor. The record describes the treatment level as a single level from L2 to L5.

Masking is listed as none. That means the registry does not describe the study as blinded; it does not establish which participants or assessors knew treatment assignment in every part of the study. The listed investigational treatment combines a procedure with a device, while the control is the procedure alone. Consequently, the comparison addresses the addition of the stabilization system to herniectomy, rather than a comparison between surgery and no treatment.

The primary endpoint was back-pain change from baseline to 6 months. The posted arm results include 68 participants in the investigational group and 63 in the control group. The registry also posts a disability outcome at 12 months; the arm results for that outcome include 68 and 61 participants, respectively. These endpoint-specific counts need not match the enrollment figure: the record does not explain the flow of participants from enrollment to each analysis or why the available counts differ.

The record identifies the intent-to-treat population as the primary analysis dataset for treated subjects for analyses other than safety. It does not report details of how that population was defined or how missing outcome data were handled. The trial’s original sample-size assumptions and detailed statistical plan are not reported in the registry record.

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.

Before assignment: A total of 7 patients were enrolled but not randomized: 6 were excluded due to eligibility criteria not met, and 1 was excluded due to non-compliance issue.

Overall Study

Reasons for not completing this period:

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 To Demonstrate a Statistically Significant Difference in the Relief of Back Pain Between Both Treatment Groups. The Endpoint Will be the Difference Between Baseline and 6-month of the Patient's Back-pain Score on a Visual Analogue Scale (VAS)., measured over 6 Months.

The primary endpoint is the difference between baseline and 6 months in the patient’s back-pain score on a visual analogue scale. The registry describes a standardized scale from 0cm to 10cm, with 0cm meaning no pain and 10cm meaning the worst possible pain. The outcome is a continuous measure, and the posted summaries are means with standard deviations.

Change scores express how a participant’s measured pain level differs from their baseline level over the specified follow-up. In this record, the change is defined as the 6-month score minus the baseline score. Because higher scale values represent more pain, a negative change indicates a decrease in pain score; a larger negative change represents greater relief according to the registry’s definition. Comparing the average change between groups addresses whether the mean change differed between the treatment strategies.

A continuous pain score retains more gradation than a simple indicator of improvement or no improvement. The mean summarizes the group’s average change, while the standard deviation describes how much individual changes vary around that mean. These summaries do not show the full distribution of individual responses. Nor do they by themselves establish whether a difference is important to patients. The registry record does not report a threshold for a clinically important difference or a responder definition.

7. Results Posted in the Registry

• Investigational Group: mean -3.97 versus -3.37 on control; difference -0.60 (95% CI -1.59 to 0.39), standardized effect d = -0.21; z-test p = 0.233.

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.

To Demonstrate a Statistically Significant Difference in the Reduction of Disability Between Both Treatment Groups. The Endpoint Will be the Difference Between Baseline and 12 Months of the Patient's Score on the Oswestry Disability Index (ODI).

• 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:
  • Investigational Group: mean -38.55 versus -37.19 on control; difference -1.36 (95% CI -8.78 to 6.06), standardized effect d = -0.06; z-test p = 0.719.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Investigational Group and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a 12-month disability outcome in addition to the primary back-pain outcome, and a result is posted for that disability comparison. Across the posted outcomes, the broad pattern is that the group comparisons do not provide clear evidence of a difference in average change: the uncertainty intervals include zero, and the secondary result has a non-small reported p-value. This pattern is consistent with the uncertainty in the primary comparison; it does not demonstrate that the outcomes or treatment effects are identical.

The disability measure addresses a related but distinct aspect of the condition. Back pain and disability need not capture the same experience, and agreement in the broad statistical pattern does not make one endpoint a substitute for the other. The registry record does not report a joint analysis of the outcomes or explain whether the disability measure was intended to support a particular confirmatory claim.

Unadjusted secondary results generally carry less weight than a primary result when multiple outcomes or analyses are considered, because examining many results increases the chance that some may appear noteworthy by chance. This is a general statistical concern, not a claim that a particular secondary finding is false. The registry record does not report a multiplicity adjustment, a hierarchy for testing endpoints, or a plan for controlling the overall error rate. The secondary result should therefore be interpreted as supportive descriptive evidence rather than as an independent confirmation.

The record lists one secondary result, while its broader outcome-measure count indicates that not every listed measure necessarily has a posted result in this record. The registry does not explain whether other measures were unreported, not collected, or handled in another way. This limits conclusions about how complete the outcome picture is. The posted secondary result adds context, but it does not resolve uncertainty in the primary comparison or establish a broader pattern across unposted measures.

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

• To Demonstrate a Statistically Significant Difference in the Reduction of Disability Between Both Treatment Groups. The Endpoint Will be the Difference Between Baseline and 12 Months of the Patient's Score on the Oswestry Disability Index (ODI).

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the registry reports a mean change and standard deviation for each group. A mean is the arithmetic average of the measured changes. The standard deviation describes the spread of those changes around the group mean; a larger standard deviation indicates more variability among measured outcomes. These summaries allow a comparison of group averages but do not reveal whether the changes are symmetric, clustered, or influenced by unusual observations.

What does the mean difference represent?

The unadjusted comparison subtracts the control-group mean change from the investigational-group mean change. For the primary endpoint, the recalculated estimate is -0.6 units on the scale. The negative sign indicates that the investigational-group mean change was more negative. This is an unadjusted comparison of the posted summaries, not an estimate adjusted for baseline characteristics or other covariates. The registry’s reported analysis is a two-sided t-test of the net mean difference.

A t-test assesses how compatible the observed difference is with a null model in which the population means are equal, given the assumptions of the test. A two-sided test considers departures in either direction rather than only a prespecified direction. The p-value is not the probability that the null hypothesis is true, nor is it the probability that the result occurred by chance in an everyday sense. It is a measure of how unusual data at least as discrepant as those observed would be under the null model and the test assumptions.

What does a confidence interval add?

A confidence interval describes the uncertainty around an estimated effect. In repeated use of the same method under its assumptions, intervals constructed in this way would cover the underlying parameter at the stated rate. For an individual study, the interval gives a range of effect values compatible with the data and method; it is not a guarantee that the true effect lies within its endpoints. The primary 95% interval crosses zero, so it includes no mean difference along with values indicating a difference in either direction.

The standard errors listed for the groups reflect uncertainty in their estimated means. The recalculation uses the posted group sizes and standard deviations and treats the groups as independent. It is not a reconstruction of any covariate-adjusted or otherwise different sponsor model. If assumptions such as independence, the distributional behavior of the mean, or the completeness of the analyzed observations are not appropriate, the simple comparison may not capture all relevant uncertainty. The registry record does not provide diagnostics or fuller analytic detail with which to assess those matters.

How should the standardized effect be read?

The recalculation also expresses the primary mean difference in standardized units, using the pooled standard deviation; the listed standardized effect is -0.210. Standardization places a mean difference on a scale measured in standard deviations rather than the original pain units. It can help compare magnitudes across outcomes with different measurement units, but it does not itself identify clinical importance. Its interpretation also depends on the variability of the measured outcome in these groups.

The posted comparison is unadjusted. Randomization is intended to support fair group comparisons, but it does not eliminate chance imbalances, missing outcomes, or measurement limitations. No baseline-adjusted model, repeated-measures method, or sensitivity analysis is reported in the registry record. It is therefore not possible to determine from the posted summaries whether alternative model choices would materially change the estimates.

Why does over-dispersion matter in general?

General statistical explanation: over-dispersion occurs when observed variability is greater than a model assumes. If a model understates variability, standard errors can be too small and confidence intervals too narrow, making evidence appear more precise than it is. Appropriate methods can account for extra variability when the data and model require it. The posted outcomes are continuous means and standard deviations, and the registry record does not report an over-dispersion analysis. This general concept should not be mistaken for a finding about this trial.

The recalculated comparison is labeled unadjusted because it uses summary statistics rather than participant-level data or a reported adjusted model. It can be a useful check on the direction and approximate size of the sponsor’s result, but it cannot reproduce details that are not present in the registry record. In this case, the sponsor’s analysis is separately reported and closely resembles the recalculation. Where the registry does not disclose the full analysis population, missing-data procedures, or model specification, those uncertainties remain part of the interpretation.

11. Confidence Intervals and Precision

The primary recalculated estimate is a mean difference of -0.6, with a 95% confidence interval from -1.586 to 0.386. Its breadth reflects uncertainty in the estimated difference. The interval crosses zero, so the data are compatible with no average difference and with effects in either direction. The estimated direction alone should not be treated as a definitive result.

The interval also helps distinguish statistical uncertainty from clinical importance. Its endpoints are expressed in the scale’s units, but the registry record does not state which differences would be noticeable or important to patients. Without a prespecified clinical threshold, the interval cannot be classified as excluding or including only clinically meaningful effects. The scale’s defined range gives the measure context, but it does not supply that threshold.

The sponsor’s 95% interval, from -1.59 to 0.38, is close to the recalculated interval. Minor differences in the displayed endpoints are consistent with the estimates being reported at different precision. The same general reading applies: the interval includes zero and does not pin down a direction with high precision. The record does not provide a separate precision target or a statement that the comparison was designed to establish equivalence.

General statistical explanation: narrower intervals indicate more precise estimates, while wider intervals indicate greater uncertainty, all else being equal. Precision depends on the amount and variability of outcome information and on the analysis method. The posted standard deviations show considerable variation in individual changes relative to the estimated group difference, but the registry summaries do not permit a detailed account of the outcome distributions or the reasons for missing observations.

For the secondary disability comparison, the reported 95% interval also spans zero and is wide. The results therefore leave uncertainty about the size and direction of the average difference. Confidence intervals should be considered alongside the endpoint definition, participant counts, and analysis limitations, rather than read as a stand-alone verdict.

12. Planning a Similar Trial: Sample Size

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

The sample-size planning values are participants per arm, not total participants or total events. The planning display uses the observed effect as its reference and gives illustrations for detecting 100%, 75%, and 50% of that effect. Its stated 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 the stated fraction of the observed effect. Time-to-event planning displays, if present, would instead give total events, but the outcomes in this analysis are not time-to-event outcomes.

The 80% power column describes the planned number of participants per arm that, under those assumptions and for the specified effect, would give an 80% chance of rejecting the null hypothesis if that effect were the true effect. The 90% column uses a higher probability of detecting the specified effect, and consequently requires more participants per arm in the displayed illustrations. These are planning calculations, not counts from the trial.

The rows for smaller fractions of the observed effect require more participants per arm. This is expected: smaller differences are harder to distinguish from ordinary sampling variation. The figures are based on the observed effect, which is uncertain, so they are illustrations rather than a sample-size justification for this study. The trial’s original design assumptions, including its own planned effect and sample-size rationale, are not reported in the registry record. This is not observed power.

The curve should be read as a visual expression of the same planning relationship between effect size and participant requirement under the stated assumptions. It does not show a new trial result or a probability that the observed finding is true. Planning values depend on the assumptions and effect chosen, and should not be interpreted as a retrospective measure of whether the study was successful.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.600; pooled standard deviation σ = 2.854.
2. n = 2 × (1.96 + 0.842)² × 2.854² / -0.600² = 355.2, rounded up to 356 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
delta <- -0.6                      # observed difference in means
sigma <- 2.85415853277854                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(749996)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 356 (80% power), 476 (90% power)
 75% of observed effect: n per arm = 632 (80% power), 846 (90% power)
 50% of observed effect: n per arm = 1,421 (80% power), 1,903 (90% power)
power.t.test: 356.2 
Simulated power at n = 356 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s reported primary analysis is a two-sided t-test of the net mean difference. It reports -0.61, with a 95% confidence interval from -1.59 to 0.38 and p = 0.228. The unadjusted recalculation from the posted group summaries gives -0.6, a 95% confidence interval from -1.586 to 0.386, and p = 0.233.

The estimates and interval limits are close, and both intervals include zero. The small displayed differences in the estimate, interval endpoints, and p-value do not change the broad interpretation of uncertainty. The registry record does not flag a discrepancy between the reported analysis and recalculation. The recalculation is a simple check from summary statistics; it is not a replacement for the sponsor’s analysis or a reproduction of unreported modeling choices.

The registry record does not give enough detail to establish whether the sponsor’s calculation used exactly the same rounding, population handling, or implementation as the recalculation. The sponsor’s result remains the reported analysis, while the recalculation provides a transparent, unadjusted comparison based on the posted means, standard deviations, and group counts.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, comparisons, or analyses are tested. Even if each test uses a conventional threshold, considering many tests can raise the chance of at least one result appearing statistically notable when there is no underlying effect. Statistical approaches can account for this, or a prespecified hierarchy can identify which comparisons are confirmatory. The registry record does not report a multiplicity adjustment, testing hierarchy, or detailed plan for handling multiple analyses.

The primary endpoint is specified at 6 months, and the posted secondary disability outcome is at 12 months. The record does not explain whether other time points or outcomes were considered in the analysis plan, or whether all planned results are posted. The absence of those details does not establish that selective reporting occurred; it means the registry record does not permit assessment of that possibility.

Missing-data handling is also not reported in sufficient detail. The primary endpoint summaries include 68 participants in the investigational group and 63 in the control group, while the disability summaries include 68 and 61. The registry record does not explain why the counts differ by endpoint, whether any observations were missing, how missing values were handled, or whether sensitivity analyses assessed their influence. Different endpoint counts can affect precision and may affect the interpretation if outcome availability is related to participant characteristics or outcomes.

The registry identifies the intent-to-treat population as the primary analysis dataset for treated subjects, except for safety analyses. It does not define the analysis set in operational terms, state how participants were assigned to that set, or describe departures from assigned treatment. The posted endpoint counts alone do not establish whether all randomized participants were included under an intent-to-treat approach.

These omissions limit the ability to evaluate the robustness of the findings. They do not, by themselves, show that the analysis was inappropriate. A fuller protocol and statistical analysis plan, along with participant flow and missing-data sensitivity analyses, would be needed to clarify these issues; such details are not reported in the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: pain in extremity (8.5%), back pain (5.6%), intervertebral disc protrusion (2.8%), sciatica (2.8%), myocardial infarction (1.4%).

The adverse-event record gives separate at-risk and affected counts for serious and other adverse events. For serious events, the investigational group lists 15 affected among 73 at risk, and the control group lists 19 among 71 at risk. For other adverse events, the corresponding figures are 44 among 73 and 40 among 71. These are descriptive counts for the safety record; they are not the same as the endpoint-specific group counts used in the efficacy summaries.

The registry lists serious-event terms with percentages, including pain in extremity at 8.5% and back pain at 5.6%, followed by intervertebral disc protrusion and sciatica at 2.8% each, and myocardial infarction and anal abscess at 1.4% each. The record does not clarify whether people could contribute more than one event term, so the listed terms should not be added or treated as mutually exclusive categories. Death counts are not reported in the registry record.

These figures describe events recorded during the study; they do not establish that a treatment caused an event or permit a complete comparison of risks without further information about definitions, follow-up, and event handling. The registry record does not provide those details in the posted safety summary.

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

The posted data describe a randomized comparison of herniectomy alone with herniectomy plus the DIAM™ Spinal Stabilization System. For the primary endpoint, average back-pain scores declined from baseline in both groups according to the reported mean changes. The estimated between-group difference is modest in the scale’s units, and the confidence interval includes no difference. The analysis therefore leaves uncertainty about the size and direction of any average difference between the strategies.

This is not proof that the treatments are equivalent. Equivalence requires a specific design and a prespecified range within which differences would be considered sufficiently small; such a framework is not reported in the registry record. Nor does a non-significant comparison show that no participant experienced an important change. Group means can conceal individual variation, and the record does not post responder summaries that would describe how many people reached a particular improvement threshold.

The results also do not establish clinical importance. The registry defines the pain scale and the direction of change, but does not report a threshold for a clinically important difference. Statistical uncertainty and clinical relevance are separate questions: even a precise estimate would need a meaningful interpretive threshold, while an uncertain estimate cannot support a precise claim about benefit.

The secondary disability comparison contributes related information but does not remove the uncertainty. Its result is also compatible with no mean difference, and the record does not report multiplicity procedures or enough missing-data detail to assess all possible sources of bias. The absence of those details should be treated as a limitation of the available record, not as proof that the trial analysis was invalid.

These findings are limited to the study population, treatment comparison, outcomes, and follow-up periods recorded. They do not answer questions about other procedures, other patient groups, longer follow-up beyond the posted outcomes, or individual treatment decisions. They are statistical descriptions of the posted results, not medical advice.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares the addition of a device to a procedure rather than comparing treatment with no intervention. The randomized parallel-group structure provides a framework for estimating the difference between those strategies, while the unmasked design and incomplete analysis details constrain what can be inferred from the registry record.

The primary endpoint uses a continuous pain measure and a defined change direction. That makes it possible to describe the magnitude and variability of average change rather than reducing the outcome to a simple yes-or-no classification. At the same time, interpretation depends on the units and on whether a difference matters to patients; the record does not supply a clinical-importance threshold.

The example also shows why effect estimates and confidence intervals matter alongside p-values. A p-value alone cannot convey the range of effects compatible with the data, and a result that does not cross a conventional significance threshold is not proof of no effect. Here, the interval spans zero, leaving material uncertainty about the between-group mean difference.

Comparison of the sponsor’s reported analysis with a simple recalculation is useful as a consistency check. The close estimates support the conclusion that the posted summary statistics broadly reproduce the reported comparison, while the registry’s missing information on multiplicity, missing data, and the original design assumptions remains important.

Finally, the planning illustrations show how sample requirements depend on the effect chosen for detection. They are not a retrospective measure of study power and do not reveal the rationale used in the original design. Keeping estimation, hypothesis testing, clinical relevance, and planning distinct is essential to a careful reading of clinical trial results.

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.

The registry record gives limited information about participant eligibility and baseline characteristics. It identifies complex disc disease at a single level from L2 to L5 and lists sciatica and back pain, but does not provide a fuller account of the study population. The record also does not explain participant flow from enrollment to each endpoint analysis. As a result, the reasons for the differing endpoint-specific counts are not reported in the registry record.

The study is listed as unmasked. Awareness of treatment assignment can matter for outcomes based on patient-reported pain or disability, although the registry record does not describe the specific procedures used to collect or assess these measures. The record does not report whether outcome assessment was otherwise standardized beyond the scale description.

The primary endpoint is a change score, but the record does not provide a prespecified clinical-importance threshold, responder definition, or baseline outcome summaries by group. Without those details, the clinical meaning of the estimated average difference is difficult to judge. The posted arm means and standard deviations do not show the full distribution of individual changes.

The original sample-size rationale, detailed statistical analysis plan, multiplicity strategy, and missing-data procedures are not reported in the registry record. It is also not clear from the posted summary whether all planned outcomes and time points are represented. The intent-to-treat population is named for the primary analysis, but the record does not explain its implementation.

The safety record gives affected counts and selected serious-event terms, but does not provide fuller definitions, event-level detail, or enough information to infer causality. Death counts are not reported in the registry record. These limitations are specific to the information available for this trial and affect the scope of interpretation rather than proving that a particular result is biased.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Herniectomy Versus Herniectomy With a Spinal Stabilization System for the Treatment of Complex Disc Disease — NCT00749996.
• Registry record last updated 2016-01-28; status last verified 2016-01.
• Results first posted 2014-05-23.
• 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 registry record describes a completed, randomized, unmasked, parallel-group phase 4 study of herniectomy alone versus herniectomy followed by the DIAM™ Spinal Stabilization System for complex disc disease at a single level from L2 to L5. Enrollment is listed as 165, with Medtronic Spinal and Biologics named as sponsor.

The primary outcome is mean change in back-pain score from baseline to 6 months on a visual analogue scale. The sponsor reports a two-sided t-test with a mean difference of -0.61, a 95% confidence interval from -1.59 to 0.38, and p = 0.228. The unadjusted recalculation is close and its confidence interval also includes zero. A disability outcome at 12 months is posted as a secondary result and likewise does not provide clear evidence of a mean difference.

The registry record does not report the original sample-size rationale, detailed missing-data procedures, or multiplicity plan. The results are best read as uncertain estimates of average differences, not as proof of equivalence or as evidence about outcomes that were not posted.