A Pivotal Study to Assess the InSpace™ Device for Treatment of Full Thickness Massive Rotator Cuff Tears: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Pivotal Study to Assess the InSpace™ Device for Treatment of Full Thickness Massive Rotator Cuff Tears (NCT02493660), a randomized na study. The primary outcome is Percentage of Participants in the Per Protocol Population With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears From Baseline to Month 12 With no SSSIs and no SADEs..

2. Clinical Question

3. Trial Design

The registry describes a prospective, single-blinded, multicenter, randomized, controlled, pivotal study with a parallel-group model. Participants were allocated to InSpace implantation or arthroscopic partial rotator cuff repair. The identity of the person or people who were blinded is not reported in the registry record, so the masking description does not establish whether participants, clinicians, outcome assessors, or analysts were masked.

The registry lists enrollment of 184 and identifies the study as completed. The listed start date is 2015-06-26, and the primary completion date is 2020-02-29. The phase is recorded as NA. OrthoSpace Ltd. is named as the sponsor. These registry entries describe the design and conduct at a high level; further information about randomization procedures, allocation concealment, study sites, eligibility criteria, and the timing of follow-up visits beyond the reported endpoints is not reported in the registry record.

The primary result uses the per-protocol population, with 88.0 participants listed in each arm for that endpoint. That population should not be treated as interchangeable with every participant enrolled or randomized: the registry does not give enough detail to reconstruct exclusions or the exact analysis set. The secondary outcomes include measures reported for an intent-to-treat population with available data, as well as per-protocol component outcomes. The reasons for using different populations across outcomes are not reported in the registry record.

The comparison addresses a composite measure of clinical-score improvement and safety-related conditions, rather than a single score alone. This makes the primary result dependent on each component of the composite and on the specified follow-up period. The trial design is randomized, but the posted numerical results and sponsor analysis use different reporting forms; the interpretation should distinguish the sponsor’s non-inferiority analysis from the unadjusted recalculation based on the posted arm summaries.

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: Subjects excluded (n=45) for various reasons, not meeting criteria (n=11), declined to participate (n=12), and Other (n=22) such as, no medical clearance for surgery, intra-op screen failures, enrollment full.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Percentage of participants in the Per Protocol Population (PP) with surgical treatment success of the InSpace device as a Primary surgical treatment for Full-thickness massive rotator cuff tears (MRCT).

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: Number of subjects who were randomized and received an InSpace implant and the number of subjects who received a Partial Repair of their rotator cuff.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants in the Per Protocol Population With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears From Baseline to Month 12 With no SSSIs and no SADEs., measured over Baseline to month 12.

The primary endpoint is the percentage of participants in the per-protocol population meeting a composite definition of treatment success from baseline to month 12. Success required a WORC improvement of at least 275 points and an ASES improvement of at least 6.4 points by week 6, with both improvements maintained at month 12. It also required no subsequent secondary surgical intervention and no serious adverse device effect.

The registry explains that the WORC score ranges from 0 to 2100, with a lower score better, while the ASES score ranges from 0 to 100, with a higher score better. The endpoint uses change thresholds rather than the final score alone: a participant must meet the specified improvement criterion for each measure. The composite therefore combines patient-reported or functional score changes with subsequent intervention and serious device-effect conditions. A participant who fails any required component does not meet the full composite definition.

A composite can represent several aspects of a treatment outcome in a single endpoint, which can make the primary question clinically broader than a score change alone. Its interpretation depends on all components, however. The primary percentage does not show which component most often determined success or failure. Component-level results are separately reported for WORC and ASES, but the full primary endpoint also includes the intervention and device-effect conditions. The registry does not report component-level counts for each reason for failing the primary composite.

7. Results Posted in the Registry

• Tendon Repair: 39.8% (35/88) versus 51.1% (45/88) on control; risk difference -11.4 percentage points (95% CI -26.0 to 3.3), risk ratio 0.78 (0.56–1.08); unadjusted two-proportion z-test p = 0.130.

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.

Composite Endpoint Component Level Success for WORC at Month 12 Compared to Baseline in the Per Protocol Population (PP)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tendon Repair: 87.5% (77/88) versus 89.8% (79/88) on control; risk difference -2.3 percentage points (95% CI -11.6 to 7.1), risk ratio 0.97 (0.88–1.08); unadjusted two-proportion z-test p = 0.635.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tendon Repair and the control. The interval gives the range of effects that remain compatible with the data.

Composite Endpoint Component Level Success for ASES at Month 12 Compared to Baseline in the Per Protocol Population (PP)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tendon Repair: 90.9% (80/88) versus 96.6% (85/88) on control; risk difference -5.7 percentage points (95% CI -12.8 to 1.4), risk ratio 0.94 (0.87–1.02); unadjusted two-proportion z-test p = 0.119.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tendon Repair and the control. The interval gives the range of effects that remain compatible with the data.

The available numerical component results show high success percentages in both arms for WORC and ASES, with the posted values somewhat higher for InSpace on each measure. These are component-level outcomes, not the full primary composite. They do not include all the primary endpoint’s requirements concerning maintenance, subsequent secondary surgical intervention, and serious adverse device effects. The component percentages therefore provide related context without directly reproducing the primary endpoint.

The registry also lists a broader set of secondary outcomes, including a composite endpoint, score changes, and other measures at follow-up. Numerical results are not posted for all listed outcomes in the analyzed record. Where no numerical result is available, the outcome’s direction or size cannot be inferred. The differing populations and available-data descriptions also matter: some outcomes are identified as per-protocol, while others are identified as intent-to-treat with available data.

A secondary analysis can help explore whether the primary pattern is reflected in related measures, but it generally carries less weight than the prespecified primary analysis. Multiple outcomes create more opportunities for chance findings, especially when results are considered without an adjustment for multiplicity. The registry does not report a multiplicity adjustment or a hierarchy governing the secondary analyses. The posted secondary results should therefore be treated as supportive or exploratory rather than as independent confirmation of the primary conclusion.

The ASES component has a sponsor-reported non-inferiority analysis with a p value below 0.05, but its non-inferiority margin and model estimate are not reported in the registry record. That result should not be interpreted as a superiority finding, and it cannot resolve the limitations in interpreting the primary sponsor analysis. The component-level percentages, the full composite, and the sponsor’s non-inferiority tests address related but distinct statistical questions.

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

• Composite Endpoint of WORC Improvement ≥275 and ASES Improvement ≥6.4 at Week 6 Maintained at Month 24 no Subsequent Secondary Surgical Intervention (SSSI) and no Serious Adverse Device Effect (SADEs) (Pre-specified). Composite WORC ASES and Safety to M24
• Composite Endpoint Component Level Success for WORC at Month 12 Compared to Baseline in the Per Protocol Population (PP)
• Composite Endpoint Component Level Success for ASES at Month 12 Compared to Baseline in the Per Protocol Population (PP)
• Mean Change From Baseline to Month 24 in the Intent To Treat (ITT) Population With Available Data With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears Through to Month 24. WORC
• Mean Change From Baseline to Month 24 in the Intent To Treat (ITT) Population With Available Data With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears Through to Month 24. ASES
• Mean Change From Baseline to Month 24 for Constant-Murley (CS) in the Intent To Treat Population (ITT) With Available Data With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears
• The Mean Change From Baseline to Month 24 for EQ-5D-5L for Intent To Treat (ITT) Population With Available Data With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears
• Mean Change From Baseline to Month 24 for VAS in the Intent To Treat (ITT) Population With Available Data With Surgical Treatment Success of the InSpace Device as a Primary Surgical Treatment for Full-thickness Massive Rotator Cuff Tears

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either meets the composite success definition or does not. The registry reports the percentage meeting that definition in each arm. A binary outcome is useful when success is defined by a set of required conditions, but it compresses the underlying information. It does not show how far a score changed beyond the threshold, nor does the aggregate percentage identify which composite component was responsible when success was not achieved.

What does the unadjusted risk difference describe?

The recalculation compares the proportion meeting the endpoint in the Tendon Repair arm with the proportion in the InSpace arm. The reported risk difference is negative, reflecting a lower observed success proportion in the comparator arm in this calculation. This is an unadjusted contrast formed from the posted arm summaries; it is not the sponsor’s logistic-regression estimate. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence for the trial’s formal non-inferiority assessment.

An unadjusted risk difference is direct to interpret because it expresses the contrast in percentage-point terms. It does not account for covariates or other features of the analysis model. The registry does not report enough information to determine whether the sponsor’s regression adjusted for particular variables, how missing values were handled, or whether the model used the same population and endpoint derivation as the recalculation. Consequently, the two analyses need not match exactly, and the simple calculation should be treated as a descriptive check rather than a replacement for the sponsor’s analysis.

How should the p values be read?

The unadjusted recalculation has a p value of 0.13. A p value describes how incompatible the observed data are with a specified null model under the assumptions of the test; it is not the probability that a treatment is effective or ineffective. The recalculation is not a non-inferiority test, because it does not incorporate a non-inferiority margin. The registry reports a logistic-regression non-inferiority analysis for the primary endpoint, but its margin and model estimate are not reported in the registry record. The sponsor’s analysis cannot be reconstructed from the p value alone.

Non-inferiority asks whether the results rule out an unacceptable loss relative to a comparator, where the acceptable margin is defined in advance. The margin is central to that interpretation. A statistically reported non-inferiority analysis cannot be judged solely by whether its p value meets a threshold; readers also need the margin, the direction of the test, the analysis population, and the relevant effect estimate and uncertainty. Those details are not reported in the registry record.

What is the role of confidence intervals?

A confidence interval expresses uncertainty around an estimated effect under a statistical model. A wide interval signals that the data are compatible with a broad range of effects, while a narrower interval indicates greater precision. For the unadjusted risk difference, the recalculated interval includes the null value of no difference and extends to values in both directions. That means the posted summary data do not pin down the direction of the underlying difference with high precision. The interval is for the simple recalculation, not for the sponsor’s regression analysis.

Confidence intervals also help distinguish the estimated effect from its uncertainty. A point estimate alone can appear more definitive than the evidence warrants. For a non-inferiority question, the interval must be interpreted in relation to the non-inferiority margin, which is not reported in the registry record. The registry does not provide the sponsor model’s interval or estimated effect, limiting assessment of the precision of the formal analysis.

Why do analysis populations matter?

The primary outcome is reported for the per-protocol population. Per-protocol analyses generally focus on participants meeting specified study requirements, but the exact rules used in this study are not reported in the registry record. An intent-to-treat analysis generally retains participants according to randomized assignment, while analyses limited to available data can exclude observations without recorded outcomes. The registry lists some secondary outcomes for an intent-to-treat population with available data, but it does not give the missing-data procedures or explain how the analysis sets were constructed.

Analysis population choices can affect a non-inferiority assessment because departures from assigned treatment or missing outcomes may influence the apparent similarity between groups. The registry record does not provide enough detail to evaluate that issue in this trial. For that reason, the per-protocol primary percentages and secondary results from other populations should be read as results from their stated analysis sets, not as interchangeable estimates.

Why can over-dispersion matter in other outcome types?

General statistical context: over-dispersion occurs when observed variability exceeds what a chosen model expects. It can make standard errors too small if the model does not account for the extra variation. The primary endpoint is a binary percentage, and the registry does not report a dispersion estimate or an over-dispersion adjustment for it. The concept should not be taken as evidence that over-dispersion occurred in this analysis.

11. Confidence Intervals and Precision

The recalculated primary risk difference has a confidence interval that runs from negative values through positive values. In practical terms, the posted summaries are compatible with a range that includes no difference as well as differences in either direction. The unadjusted p value is 0.13, which is consistent with the interval’s inclusion of the null value under the recalculation’s assumptions. These are features of the simple recalculation, not the sponsor’s logistic-regression analysis.

Precision is distinct from the direction of the point estimate. The reported arm percentages favor a higher observed composite success percentage in the InSpace arm, but the interval indicates uncertainty around the size and direction of the contrast. Without the sponsor model’s estimated effect and confidence interval, the precision of its formal non-inferiority analysis cannot be assessed from the registry record.

For a non-inferiority question, interval interpretation also depends on the acceptable margin. The margin is not reported in the registry record, so readers cannot compare the sponsor estimate’s uncertainty with that decision boundary. The sponsor’s reported p value does not supply the missing effect estimate or interval. It is therefore not possible to determine from the posted record how close the formal estimate was to any non-inferiority boundary.

The score-component percentages are comparatively high in both arms, but those component results do not establish the precision of the full composite contrast. A high component-level success percentage can coexist with a lower full-composite percentage because the composite requires additional conditions. Component-level confidence intervals and the sponsor’s modeled estimates are not reported in the registry record. The posted percentages should consequently be read as point summaries, not as precise evidence about all possible treatment differences.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total events: the endpoint is a binary percentage, and the planning illustrations express the required number of participants in each arm. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

For planning around 100% of the observed effect, the illustration gives 301 participants per arm for 80% power and 402 participants per arm for 90% power. For planning around 75% of the observed effect, it gives 537 and 719 participants per arm, respectively. For planning around 50% of the observed effect, it gives 1,214 and 1,624 participants per arm, respectively. Smaller effects require more participants to distinguish them from random variation under the stated assumptions.

The 80% column means that, if the assumptions and chosen effect were correct, the design would have an 80% chance of detecting that effect using the stated test procedure. The 90% column describes the corresponding chance at the higher target. These are prospective planning illustrations calculated from the observed effect, not the trial’s original design assumptions. The original sample-size justification is not reported in the registry record. These figures are not observed power.

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 = 0.511; treatment proportion p₁ = 0.398; average p̄ = 0.455.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7042 = 1.3802.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6996 = 0.5888.
4. n = (1.3802 + 0.5888)² / (-0.1136)² = 300.2, rounded up to 301 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 <- 0.511363636363636                          # control proportion
p1 <- 0.397727272727273                          # 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(2493660)
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 = 301 (80% power), 402 (90% power)
 75% of observed effect: n per arm = 537 (80% power), 719 (90% power)
 50% of observed effect: n per arm = 1,214 (80% power), 1,624 (90% power)
power.prop.test: 300.2 
Simulated power at n = 301 per arm: 0.804 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as logistic regression for a non-inferiority comparison between InSpace Implantation and Tendon Repair. It records a p value for that analysis but does not provide the model’s effect estimate, confidence interval, or non-inferiority margin. Those missing details prevent an independent reconstruction of the sponsor’s formal conclusion from the registry record.

The unadjusted recalculation uses the posted arm summaries and gives a risk difference with a confidence interval spanning no difference, alongside an unadjusted p value of 0.13. It is a simple comparison, not the reported regression analysis, and it does not test non-inferiority against a margin. The registry flags a discrepancy between the recalculation and the sponsor’s analysis. In that circumstance, the sponsor’s own analysis takes precedence for describing the trial’s formal result; the recalculation is useful as a transparent descriptive check, not as a substitute.

The sponsor analysis is reported as non-inferiority, but the information needed to interpret that claim fully is not reported in the registry record. In particular, the non-inferiority margin and model estimate are needed to assess how the result relates to the prespecified boundary and how precise it is. The reported analysis label and p value alone do not show the magnitude of the difference or its clinical meaning.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary composite endpoint and multiple secondary outcomes. Testing or interpreting many outcomes can increase the chance of observing apparently notable results by chance. Statistical approaches can address this through prespecified testing hierarchies or multiplicity adjustments, but whether either approach was used is not reported in the registry record. The registry also does not report a complete statistical analysis plan or the order in which the outcomes were tested. The secondary p values therefore require cautious interpretation, particularly when considered apart from the primary endpoint.

The primary analysis population is per protocol, while some secondary outcomes are described as intent-to-treat with available data. The registry record does not provide the rules defining the per-protocol population, the number of observations available for each secondary measure, or the reasons observations may be missing. It also does not report how missing outcome data were handled, whether imputation was used, or whether sensitivity analyses were conducted.

Missing data can affect both the percentages and the comparability of the analysis groups, especially if missingness is related to outcome or treatment. Available-data analyses may reflect participants with recorded measurements rather than everyone assigned to a group. Without the missing-data procedures and outcome-specific denominators, the potential impact cannot be assessed from the registry record.

For non-inferiority analyses, analysis-population choices and missing data deserve particular attention because departures from assigned treatment or incomplete follow-up can make groups appear more similar. The registry identifies the primary result as per protocol and reports a sponsor logistic-regression non-inferiority analysis, but details about adherence, treatment switching, exclusions, and sensitivity analyses are not reported in the registry record. The record also does not report the non-inferiority margin or full model output. These omissions limit independent assessment of the formal non-inferiority finding.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: eg. pain or inflammation (12.1%), eg.prostate cancer, leukemia, parathyroid tumor (4.4%), eg. dizziness, aphasia, cerebrovascular accident (4.3%), eg. event leading to death, non-cardiac chest pain, surgical failure (3.3%), eg.laryngeal granuloma, chronic obstructive pulmonary disease, pulmonary mass (3.2%).

The registry reports serious adverse events among participants at risk in each arm: 22 affected participants among 93 at risk in InSpace Implantation and 22 among 91 at risk in Tendon Repair. For other adverse events, it reports 67 affected among 93 at risk in the InSpace arm and 69 among 91 at risk in the Tendon Repair arm. The registry records no deaths in the InSpace group and one death in the Tendon Repair group.

These counts describe participants with reported events and the corresponding at-risk denominators; they do not establish that the intervention caused an event. The serious-event terms include examples such as pain or inflammation, cancers, neurological events, and surgical failure. The listed terms are not a complete causal assessment, and the registry does not provide enough detail to compare event severity, timing, duration, relatedness, or recurrence between groups.

The primary composite separately excludes participants with a serious adverse device effect. That endpoint condition is not identical to the broader serious-adverse-event counts: the registry does not provide the cross-tabulation needed to identify which serious events were considered device effects or how they affected primary success. Safety counts should therefore be read alongside, not substituted for, the composite efficacy result.

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

The posted primary percentages show that the composite success outcome was observed in 51.1% of the InSpace per-protocol arm and 39.8% of the Tendon Repair per-protocol arm. This is a descriptive comparison of the recorded endpoint. The unadjusted recalculation has uncertainty spanning no difference, while the registry separately reports a sponsor logistic-regression non-inferiority analysis. These two analyses answer different statistical questions and should not be conflated.

The result does not establish that InSpace is superior to Tendon Repair. The sponsor’s analysis is labeled non-inferiority, and the registry does not report the margin or model estimate needed to evaluate that claim independently. Nor does the unadjusted recalculation establish equivalence: an interval that includes no difference can also include differences in either direction. Failure to demonstrate a clear difference is not proof that treatments are identical.

The percentages also do not mean that each participant experienced the same kind of improvement. The composite requires both a WORC and an ASES threshold, maintenance of both improvements, and absence of subsequent secondary surgery and serious adverse device effects. Aggregate success rates do not reveal which component drove the result for individual participants, the size of their score changes, or their experience beyond the endpoint definition.

These findings are limited to the studied population, treatment approaches, follow-up, and analysis populations described in the registry. The record lists additional outcomes, but not all have numerical results available. It does not provide enough information about missing data, endpoint adjudication, the non-inferiority margin, or the sponsor model to resolve all questions about robustness and clinical importance. The results are statistical evidence from this trial record, not individualized medical guidance.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and analysis framework matter as much as the arm percentages. The primary outcome combines two score-improvement thresholds with maintenance and safety-related conditions. Its result cannot be interpreted as a simple comparison of WORC or ASES change alone. Component outcomes are informative, but they do not capture all the requirements of the composite.

It also illustrates the difference between a straightforward recalculation and a sponsor’s model-based non-inferiority analysis. The unadjusted calculation is transparent and can be checked from the posted arm summaries, but it is not equivalent to a regression analysis and does not test against a non-inferiority margin. Because the registry flags a discrepancy, the sponsor analysis takes precedence as the formal trial analysis. At the same time, missing model estimates and margin details limit what a reader can independently verify.

Finally, a randomized design does not remove the need to examine analysis populations, missing data, multiplicity, and precision. The registry identifies a per-protocol primary outcome and available-data secondary outcomes, but does not report key details about how these were constructed or how uncertainty was handled in the sponsor analysis. Reading the result with these distinctions in view helps prevent descriptive differences, component results, and non-inferiority claims from being treated as interchangeable evidence.

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 does not report the non-inferiority margin, the sponsor model’s effect estimate, or its confidence interval. Without those details, the reported non-inferiority analysis cannot be independently evaluated against its decision boundary. The record also does not provide the full statistical analysis plan, including model covariates, test direction, or sensitivity analyses.

The primary endpoint is reported for the per-protocol population, but the rules defining that population and the reasons for any exclusions are not reported in the registry record. The registry gives no detailed account of missing data, outcome-specific available-data counts, imputation, or sensitivity checks. These omissions make it difficult to assess whether the reported analysis sets represent the randomized groups comparably.

The registry identifies the trial as single-blinded but does not report who was blinded. It also does not report details about allocation concealment, site-level conduct, or procedures for assessing the composite components. The full composite combines score thresholds, maintenance, subsequent surgery, and serious device effects, yet component-level reasons for not meeting the primary endpoint are not reported.

The record lists multiple secondary outcomes, while the numerical results available for analysis cover only some component measures. A multiplicity strategy is not reported, and outcome hierarchy details are unavailable. The serious adverse event summaries provide counts but not enough information about event timing, duration, relatedness, recurrence, or cross-tabulation with the primary composite. These limits constrain interpretation of both efficacy and safety patterns and should temper conclusions drawn from the posted percentages.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Pivotal Study to Assess the InSpace™ Device for Treatment of Full Thickness Massive Rotator Cuff Tears — NCT02493660.
• Registry record last updated 2022-06-15; status last verified 2022-06.
• Results first posted 2021-07-22.
• 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 describes a completed, prospective, single-blinded, multicenter, randomized, controlled, parallel-group pivotal study of InSpace implantation versus arthroscopic partial rotator cuff repair for full-thickness massive rotator cuff tears. Enrollment is listed as 184; the primary per-protocol endpoint results list 88.0 participants in each arm.

The primary endpoint was composite success from baseline to month 12, requiring WORC and ASES improvement by week 6, maintenance at month 12, and no subsequent secondary surgical intervention or serious adverse device effect. Posted success percentages were 51.1% for InSpace and 39.8% for Tendon Repair. The sponsor’s analysis is reported as logistic-regression non-inferiority, but the margin and model estimate are not reported in the registry record. The unadjusted recalculation is a separate descriptive analysis, and the discrepancy flag means the sponsor’s analysis takes precedence.

The registry also reports WORC and ASES component results and safety counts. Missing-data procedures, multiplicity methods, and several details needed to independently assess the formal non-inferiority analysis are not reported in the registry record.