Lesser Tuberosity Osteotomy for Subscapularis Repair: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lesser Tuberosity Osteotomy for Subscapularis Repair (NCT02762903), a randomized na study. The primary outcome is Number of Subjects With Radiologic Evidence of Anatomic Healing.

2. Clinical Question

The registry describes the primary objective as assessing the clinical effectiveness of two techniques for subscapularis tendon repair during total shoulder replacement. Its stated hypothesis was that the lesser tuberosity osteotomy technique would be associated with lower rates of postoperative subscapularis dysfunction and rupture than tenotomy. The posted primary endpoint, however, is specifically a count of participants with radiologic evidence of anatomic healing. It is not itself a direct count of muscle dysfunction or rupture, and the registry record does not report a separate primary result for those outcomes.

The comparison concerns the repair technique used during the same general operation, rather than shoulder replacement versus no shoulder replacement. The results therefore describe the posted outcomes for these two surgical approaches in this trial; they do not, by themselves, establish how either approach compares with other procedures or with no surgery.

3. Trial Design

The registry identifies this as a randomized, parallel-group trial with no masking. Participants were assigned to one of two approaches for subscapularis repair during total shoulder arthroplasty: tenotomy or lesser tuberosity osteotomy. The listed interventions also include a shoulder prosthesis, and both arm descriptions specify its use during the operation.

Enrollment was 60. The trial status is completed, and the registry lists a start date of 2009-08 and primary completion date of 2013-06. The registry identifies Columbia University as the sponsor and osteoarthritis as the condition. The phase entry is NA. More detail about how randomization was generated or concealed, how participants were recruited, or how adherence to the assigned procedure was assessed is not reported in the registry record.

The primary result uses 30 participants in the tenotomy group and 29 in the osteotomy group. The outcome description says that its population includes only participants who completed final follow-up. The registry does not give a complete account of participant flow, reasons for any differences between enrollment and outcome denominators, or whether all randomized participants were included in other analyses.

The posted secondary outcomes include pain measured by a Visual Analogue Pain Scale, forward elevation strength, total intra-operative time, total subscapularis repair time, and external rotation strength. Detailed numerical results are available for forward elevation and external rotation strength. Results for the other named secondary outcomes are not reported in the registry record. No statistical analyses are listed in the registry record, so details such as adjustment methods, analysis populations, and handling of missing observations cannot be established from the posted information.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Only includes participants who completed the final follow-up.

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 Number of Subjects With Radiologic Evidence of Anatomic Healing, measured over Post operative at 1 year.

The primary endpoint is the number of participants with radiologic evidence of anatomic healing at one year after surgery. The registry describes this as tendon healing or tuberosity union based on radiographs. It is a binary outcome at the participant level: a participant either met the radiographic healing definition or did not. The posted values are counts, with the numbers assessed in each group serving as denominators.

Radiographic healing is relevant to a comparison of these repair techniques because the procedures differ in how the subscapularis is released and repaired. Imaging offers a way to assess the structural result of that repair. It is not interchangeable with pain, strength, range of motion, or other patient experiences and functional outcomes. Those outcomes can complement the imaging endpoint but address different aspects of recovery.

The registry states that the primary endpoint population includes only participants who completed final follow-up. This restriction matters when interpreting the group counts: the result applies to the participants included in that endpoint, and the posted record does not fully describe the outcomes or follow-up status of everyone enrolled. The registry also does not provide further detail about radiograph interpretation, the criteria used to classify healing, or whether image readers were masked to treatment group. These measurement details are not reported in the registry record.

7. Results Posted in the Registry

• Osteotomy: 93.1% (27/29) versus 86.7% (26/30) on control; risk difference 6.4 percentage points (95% CI -8.8 to 21.7), risk ratio 1.07 (0.90–1.28); unadjusted two-proportion z-test p = 0.413.

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.

Forward Elevation (FE) Strength

• 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:
  • Osteotomy: mean 150.00 versus 153.00 on control; difference -3.00 (95% CI -6.32 to 0.32), standardized effect d = -0.46; z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Osteotomy and the control. The interval gives the range of effects that remain compatible with the data.

External Rotation (ER) Strength

• 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:
  • Osteotomy: mean 52.00 versus 50.00 on control; difference 2.00 (95% CI 0.69 to 3.31), standardized effect d = 0.79; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Osteotomy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several distinct domains: pain, strength, and operative time. Detailed numerical results are posted only for forward elevation strength and external rotation strength. The Visual Analogue Pain Scale, total intra-operative time, and total subscapularis repair time are named as outcomes, but their numerical results are not reported in the registry record.

The two strength comparisons do not show a uniform pattern. One estimate is imprecise and compatible with no mean difference, while the other has a confidence interval that does not include zero and an unadjusted p-value of 0.003. These findings may provide context about function, but they do not answer the primary question about radiographic anatomic healing. Nor can they establish a consistent effect across all functional and perioperative outcomes, particularly when results for three listed outcomes are not posted.

Secondary outcomes generally carry less evidential weight than a pre-specified primary outcome because they may be more numerous, may involve different measurement scales, and can increase the chance of apparently notable findings occurring by chance. The registry record does not report whether a multiplicity strategy was specified or used. The reported secondary p-values are unadjusted, so they should not be interpreted as if they accounted for all outcomes examined.

The secondary results can still help describe the range of outcomes considered, but they should be treated as supporting or exploratory evidence. They neither overturn nor resolve the uncertainty in the primary radiographic comparison. A fuller assessment would require the missing secondary numerical results and information about the planned outcome hierarchy and analysis methods, none of which is reported in the registry record.

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

• Mean Visual Analogue Pain Scale (VAS)
• Forward Elevation (FE) Strength
• Total Intra-Operative Time
• Total Subscapularis Repair Time (in Minutes)
• External Rotation (ER) Strength

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each included participant is counted according to whether radiographic evidence of anatomic healing was recorded. For a binary endpoint, a group risk is the proportion of participants in that group who experienced the event of interest. The comparison is a risk difference, which expresses the difference between those group proportions. A positive risk difference means the event was more frequent in the group named first in the comparison—in this case, osteotomy—than in the tenotomy group. This is a general interpretation of the measure, not a claim about clinical importance.

What does the confidence interval communicate?

A confidence interval describes uncertainty around an estimated effect. In general, an interval that includes zero for a difference measure is compatible with no group difference as well as with differences in either direction. The primary interval runs from -0.088 to 0.217, so it includes zero and values on both sides of it. Its breadth indicates that the posted estimate is not precise enough to pin down the size or direction of the difference. A confidence interval is not a guarantee that the true effect lies within its limits, and it does not say how likely a particular effect value is.

How should the p-value be read?

The unadjusted p-value for the primary comparison is 0.413. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-value and confidence interval address the same comparison from different angles: the p-value summarizes evidence relative to a null value, while the interval displays a range of effect estimates compatible with the data under its method.

The record identifies the p-value as unadjusted. It does not report a statistical analysis plan, the exact test used, or whether any adjusted analysis was performed. Consequently, interpretation should not assume that the posted result accounts for multiple outcomes or other modeling choices.

What do the secondary continuous outcomes measure?

Forward elevation strength and external rotation strength are reported as means with standard deviations. A mean describes the arithmetic average in a group; a standard deviation describes spread among individual observations around that average. The comparisons are mean differences, with confidence intervals and unadjusted p-values. General interpretation follows the sign of the difference: a positive value means the average is higher in the osteotomy group, and a negative value means it is lower, given the comparison direction. These group averages do not show the full distribution of individual outcomes.

For these continuous outcomes, over-dispersion is a general concern when the observed variation is greater than a statistical model assumes. Greater variation can make estimates less precise than a model allowing only smaller variation would suggest. The registry record does not describe a model used to assess over-dispersion, and the posted summaries alone do not establish whether it was present. The posted standard deviations provide some information about variability, but do not reveal the shape of the outcome distributions or the presence of unusual observations.

What can and cannot be inferred from the analyses?

The registry record does not list reported analyses beyond the posted outcome summaries and comparisons. It does not state whether the primary analysis followed an intention-to-treat principle, whether covariates were adjusted for, or how missing outcome data were handled. Those methods can affect estimates and their uncertainty, so their absence limits appraisal. The randomized design is a relevant strength for a group comparison, but the registry information does not permit a full assessment of whether analysis preserved the benefits of randomization.

The numerical secondary comparisons are unadjusted. When multiple outcomes are examined, the chance of finding at least one result that appears noteworthy by chance can increase. General statistical practice may address this through pre-specification, adjustment, or cautious interpretation, but the registry record does not state what approach, if any, was planned. The secondary findings therefore warrant more caution than a single pre-specified primary comparison, especially since several listed secondary outcomes lack posted numerical results.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.064, and its 95% confidence interval extends from -0.088 to 0.217. The interval crosses zero, so the posted data are compatible with no difference as well as with a difference favoring either group. Its width is important: the point estimate alone gives a single summary, while the interval shows that the data leave considerable uncertainty about the size and direction of the comparison.

Precision is influenced by the amount of information available, including the number of participants with observed outcomes and the frequency of the event. The primary endpoint denominators are 30 and 29, and the outcome population is restricted to participants who completed final follow-up. The registry does not provide enough participant-flow detail to assess fully how follow-up affected the available information. The confidence interval should therefore be read as precision for the posted analysis, not as a complete account of uncertainty arising from missing or unobserved outcomes.

The secondary results have different precision. The forward elevation mean-difference interval ranges from -6.323 to 0.323, while the external rotation interval ranges from 0.695 to 3.306. These intervals describe uncertainty for their respective outcomes and use their own measurement scales; they should not be compared as if they measured the same quantity. Their interpretation also needs to account for their secondary status and the absence of reported multiplicity procedures.

Confidence intervals do not by themselves establish whether an effect matters clinically. The registry record does not report a threshold for a meaningful difference in radiographic healing or strength. Thus, even a precise estimate would need clinical context to judge importance, and the primary interval is not precise enough to support a narrow estimate of the comparative effect.

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 figures are planning illustrations based on the observed effect, not the trial's own original design assumptions. The registry record does not report the assumptions used to plan the original trial. For the binary primary endpoint and the continuous secondary outcomes, the listed values are participants per arm, not total events. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect.

The 80% power column gives the estimated number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are not guarantees: actual study results depend on the true effect, variability, outcome frequency, and whether the planning assumptions hold.

The rows describe planning for the full observed effect and for smaller fractions of that observed effect. Smaller effects need more participants to distinguish them from random variation with the same planned power and significance level. The figures are therefore sensitive to the effect size chosen; planning from an observed effect can be optimistic if that estimate is imprecise or larger than the effect a future study should be designed to detect. These calculations are planning illustrations, not observed power.

The sample-size values should not be read as evidence that the trial had a particular probability of detecting its observed result. They also do not recover the original design rationale. The record does not report the trial's own target effect, original power calculation, or planned sample-size assumptions.

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 = 0.867; treatment proportion p₁ = 0.931; average p̄ = 0.899.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4264 = 0.8358.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4240 = 0.3568.
4. n = (0.8358 + 0.3568)² / (0.0644)² = 343.3, rounded up to 344 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 <- 0.866666666666667                          # control proportion
p1 <- 0.931034482758621                          # 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(2762903)
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 = 344 (80% power), 460 (90% power)
 75% of observed effect: n per arm = 655 (80% power), 876 (90% power)
 50% of observed effect: n per arm = 1,568 (80% power), 2,098 (90% power)
power.prop.test: 343.3 
Simulated power at n = 344 per arm: 0.809 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, but does not report a statistical analysis plan or a multiplicity adjustment. The primary comparison is accompanied by an unadjusted p-value. The secondary strength comparisons also have unadjusted p-values. When multiple outcomes are tested, the chance of at least one result appearing statistically notable by chance can rise. Without a reported strategy for controlling or interpreting that issue, secondary results should be treated cautiously and the primary endpoint should remain central to interpretation.

The record lists six outcome measures overall and names five secondary outcomes, but detailed numerical results are not available for all of them. Whether the unreported outcomes were collected, analyzed, or omitted from the posted results is not reported in the registry record. It also does not state whether other outcomes or analyses were planned but not posted. These gaps make it difficult to assess selective outcome reporting.

The primary outcome population is explicitly limited to participants who completed final follow-up. The primary denominators are 30 for tenotomy and 29 for osteotomy, while total enrollment is 60. The registry does not describe the disposition of every enrolled participant or give reasons for any difference between enrollment and endpoint denominators. It does not report imputation, sensitivity analyses, or another method for handling missing outcomes.

The registry record does not state whether the analysis used all randomized participants in their assigned groups, whether participants were excluded after randomization, or whether per-protocol analyses were conducted. These details matter because excluding participants or analyzing them outside their assigned group can compromise the comparability created by randomization. The posted data are therefore best understood as the reported results for the stated endpoint population, with missing-data and analysis-population methods not reported in the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures show zero affected participants among 30 at risk in each group, and the death count is zero in each group. For other adverse events, 2 of 30 participants are listed in the tenotomy group and 5 of 30 in the osteotomy group. These are descriptive counts in the registry record; they do not, by themselves, establish a difference in safety between the procedures.

The registry does not list serious adverse event terms, and the record does not provide event-level detail, definitions, severity, relatedness, or timing. It is therefore not possible to characterize the nature of the other adverse events or determine whether any were associated with the procedure. The numbers at risk for adverse-event reporting are 30 in each group, which differ from the primary outcome denominators. The record does not explain the difference in reporting populations.

Zero reported serious events or deaths should be read as no such events recorded in these group counts, not as proof that serious events cannot occur. Small descriptive counts also offer limited precision for comparing uncommon outcomes. The posted safety figures should be considered alongside the incomplete event detail and the trial's size.

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

The registry results document the observed outcomes among participants included in the posted analyses. For the primary endpoint, radiographic healing was recorded in 26 of 30 tenotomy participants and 27 of 29 osteotomy participants. The risk-difference estimate is positive, but its confidence interval includes zero and the unadjusted p-value is 0.413. This means the data do not precisely establish the direction or size of a difference between these groups for this endpoint.

These findings do not demonstrate that the repair techniques are equivalent, and they do not establish that one technique is clinically superior. Equivalence would require a suitable design and a pre-specified margin, neither of which is reported in the registry record. The stated study hypothesis concerns dysfunction and rupture, whereas the posted primary endpoint is radiographic anatomic healing. The posted endpoint result should not be recast as a direct test of every element of that hypothesis.

The secondary strength results add information about selected functional measures, but they are unadjusted and are not a replacement for the primary endpoint. Results for pain and operative time outcomes named in the registry are not reported in the registry record. The overall evidence therefore remains incomplete across the outcome domains listed.

More broadly, the record describes one randomized comparison in participants undergoing total shoulder arthroplasty for osteoarthritis. It does not report detailed randomization procedures, a complete account of follow-up, an analysis plan, or the full secondary results. Such limits mean that the posted estimates should be interpreted in their specific trial context rather than generalized to all patients, surgeons, settings, or shoulder procedures. The statistical results describe uncertainty in the observed data; they do not provide medical advice or guarantee an individual outcome.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between structural healing and other dimensions of outcome. Radiographic union or tendon healing is a measurable endpoint relevant to the repair technique, while strength, pain, and operative time address different questions. A study may show different patterns across these endpoints, and no single measure should be assumed to represent every aspect of recovery.

The primary comparison illustrates why an effect estimate and its precision should be read together. The point estimate is positive, but the interval includes zero and extends across a range of effects. A reader who focuses only on the point estimate could overstate certainty; a reader who focuses only on the p-value could miss the information about plausible effect sizes. Both the estimate and interval matter.

The trial also highlights the importance of complete reporting. The record identifies the primary outcome population as participants completing final follow-up, but does not provide a full participant-flow account or missing-data methods. It names several secondary outcomes without posting all their numerical results, and it does not describe adjustment for multiple comparisons. These details affect how confidently readers can interpret the reported analyses.

Finally, the sample-size illustrations are distinct from the original trial design. They show how planning requirements depend on the effect chosen, but they cannot establish what assumptions motivated enrollment or whether the completed study met an original target. Keeping those distinctions clear helps readers avoid treating post hoc planning figures as evidence about the trial's design or its observed power.

18. 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 primary outcome analysis includes participants who completed final follow-up, and the registry record does not report the full participant flow or reasons for any differences between enrollment and outcome denominators. It also does not describe how missing observations were handled or provide sensitivity analyses. This limits assessment of whether the posted endpoint population represents all randomized participants.

The registry does not report important details about the conduct of randomization, allocation concealment, or outcome assessment. The trial is listed as unmasked, but the record does not state whether radiograph assessors or other outcome assessors were masked. It also does not describe the radiographic criteria for healing in detail. These omissions make it harder to evaluate potential risks of bias in assignment and outcome measurement.

Numerical findings are not posted for all named secondary outcomes. The statistical analysis plan, multiplicity approach, and any covariate-adjusted analyses are not reported in the registry record. Consequently, it is not possible to determine whether the displayed secondary tests were planned in advance or how they relate to the full set of outcomes assessed.

The primary group denominators are 30 and 29, and the result is based on a limited number of participants. The primary confidence interval is broad and includes no difference, so the estimate has limited precision. Adverse-event counts are also descriptive, and the registry does not supply event terms or detailed safety definitions. These trial-specific reporting and precision limitations constrain how strongly the results can support conclusions beyond the observed outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Lesser Tuberosity Osteotomy for Subscapularis Repair — NCT02762903.
• Registry record last updated 2024-08-06; status last verified 2024-07.
• Results first posted 2024-08-06.
• 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.

22. Record Summary

This completed randomized, parallel-group, unmasked trial compared tenotomy with lesser tuberosity osteotomy for subscapularis repair during total shoulder arthroplasty in participants with osteoarthritis. Enrollment was 60, and Columbia University is listed as the sponsor.

The primary endpoint was the number of participants with radiologic evidence of anatomic healing at one year, among participants completing final follow-up. The posted risk difference for osteotomy versus tenotomy is 0.064, with a 95% confidence interval from -0.088 to 0.217 and an unadjusted p-value of 0.413. The interval includes zero, leaving the comparative effect uncertain.

Detailed numerical secondary results are posted for forward elevation and external rotation strength. Other named secondary outcomes do not have results reported in the registry record. The record also does not report the original sample-size assumptions, a complete analysis plan, or missing-data methods.