Subacromial Corticosteroid Injection for Hemiplegic Shoulder Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Subacromial Corticosteroid Injection for Hemiplegic Shoulder Pain (NCT00597766), a randomized phase 2 study. The primary outcome is BPI 12 (Brief Pain Inventory, Question 12) Pain Questionnaire.

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 2, randomized, parallel-group study with enrollment of 28. Its status is completed. The listed start and primary completion dates are 2007-12 and 2012-02. The brief study description says the trial was designed to characterize the dose response of triamcinolone for hemiplegic shoulder pain after stroke.

Three active dose groups are listed: 20 mg, 40 mg, and 60 mg of triamcinolone, each combined with lidocaine. The arm descriptions also list lidocaine for Neer’s test. The brief description says eligible participants first had a test injection to identify pain localized to the subacromial space, with random assignment following a positive test. Further operational details of allocation are not reported in the registry record.

The registry’s masking designation is quadruple, while the brief description calls the study double-blinded. Which people or roles were masked, and how masking was maintained, are not reported in the registry record. The description says pain interviews took place at baseline and weeks 1, 2, 3, 4, 8, and 12, with laboratory-based assessments at baseline and weeks 4, 8, and 12. Follow-up was described as lasting 13 weeks.

The primary outcome is change in BPI-12 worst pain from baseline to week 12, with data from all listed time points used in the linear mixed model. Three secondary outcomes are listed: the upper-limb Fugl-Meyer Motor Assessment and pain-free external rotation and abduction range of motion. Their assessment schedules 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: Subjects had to have a positive Neer's test (50% pain reduction by subacromial lidocaine) to be enrolled and randomized. 59 were screened. 28 subjects were consented and enrolled.

Enrolled

Follow-up 1, Week 4

Reasons for not completing this period:

Follow-up 2, Week 8

Reasons for not completing this period:

Follow-up 3, Week 12

Analysis population for the primary outcome, as defined in the registry: We used available-cases. Missing values handled with maximum likelihood methods.

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: The number of participants was determined on a power analysis. The goal was 31 subjects per group.

6. Primary Endpoint

The registry lists the primary outcome as BPI 12 (Brief Pain Inventory, Question 12) Pain Questionnaire, measured over Baseline, weeks 1, 2, 3, 4, 8, 12 (7 times).

The primary endpoint is change from baseline to week 12 in Brief Pain Inventory Question 12, which asks about worst pain in the last week. The measure uses a scale from 0, meaning no pain, to 10, meaning worst pain possible. The registry reports least-squares means for this continuous outcome, with 95% confidence intervals.

A change score describes how the measured outcome differs from its baseline value. In this setting, a negative change indicates a lower reported worst-pain score at week 12 than at baseline. It is a scale-based measure of reported pain, not a direct measure of function or a laboratory measure. The listed secondary outcomes address motor assessment and pain-free shoulder range of motion, but they are distinct from the primary endpoint.

The endpoint is relevant to the study’s stated aim because the brief description frames the trial as an evaluation of pain relief across different injection doses. The registry says the week-12 estimates come from a linear mixed model and that data from all assessment times contribute to the slope and group-by-time analyses. The exact model specification, covariates, and handling of any outcome-scale features beyond what is stated are not reported in the registry record.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it is a score on a bounded pain scale, and the registry reports its mean change. The listed arm estimates are least-squares means from a linear mixed model. In general, a least-squares mean is a model-based estimate of a group mean, rather than simply a raw average. The registry states that the model used data from all time points to estimate slopes and group-by-time interactions, while the outcome measure reports the week-12-to-baseline comparison. The detailed model formula and any covariate adjustments are not reported in the registry record.

What does the group-by-time interaction test?

In general, a group-by-time interaction tests whether the modeled pattern of change over time differs between groups. It uses repeated measurements to assess whether the trajectories are distinguishable under the model. This differs from a single comparison at week 12: two groups could have different trajectories over the assessment period even if a single-time-point contrast gives a different impression, or vice versa. The registry reports interaction estimates for 20 mg versus 60 mg and 20 mg versus 40 mg, but does not provide confidence limits for those estimates.

The two posted interaction p-values are 0.16 and 0.77, respectively. A p-value describes how compatible the observed data are with a specified null hypothesis under the model and its assumptions; it is not the probability that the null hypothesis is true. These values do not show compelling evidence against equal modeled trajectories in the two reported comparisons. They do not prove that the groups have identical effects, nor do they test the unreported 40 mg versus 60 mg comparison.

How should the confidence intervals be read?

In general, a confidence interval represents the uncertainty associated with an estimate under the method used to calculate it. The arm-specific 95% confidence intervals accompany estimates of mean change from baseline. They should not be read as a range containing 95% of individual responses. Nor are they substitutes for confidence intervals around a between-group contrast. The registry does not report confidence intervals for the group-by-time estimates, so their precision cannot be assessed from those analyses as fully as it could be with interval estimates.

For the week-12 estimates, the 20 mg arm has a least-squares mean change of -1.7, with interval -3.9 to 0.6; the 40 mg arm has -2.2, with interval -4.4 to 0.0; and the 60 mg arm has -4.7, with interval -6.8 to -2.5. The fact that these intervals differ in their relation to 0.0 does not answer whether the dose groups differ. The relevant question for a dose comparison is the uncertainty around the between-group contrast, and the posted interaction analyses address trajectories rather than reporting week-12 pairwise contrasts.

What does a linear mixed model contribute?

In general, a mixed model can represent repeated observations from the same participant and account for the fact that measurements from one person are related. It can use available observations under its modeling assumptions, rather than requiring every participant to have a complete record at every scheduled time. The registry describes the outcome analysis as using a linear mixed model and says missing values were handled with maximum likelihood methods. It also says available cases were used. The missingness assumptions, model diagnostics, and sensitivity analyses are not reported in the registry record.

Maximum likelihood uses the observed data and the specified model to estimate parameters. Its validity depends on the model and assumptions about how missing observations arose. The registry’s brief statement does not establish whether those assumptions were examined or whether other missing-data approaches were used. The number of participants contributing to each time point is not reported in the registry record.

What can planning illustrations tell readers?

In general, a sample-size planning illustration asks how many participants per arm might be needed to detect an assumed effect under stated statistical assumptions. Such an illustration is not an observed result and is not observed power. The stated assumptions for the illustrations are a two-sided significance level of 0.05, equal allocation, and a normal approximation, with the effect expressed as a fraction of the observed effect. The record does not provide the trial’s own sample-size justification, and that justification is not reported in the registry record. Any planning estimate based on the observed effect should be treated as illustrative rather than as evidence that the trial was adequately powered.

10. Analyses Reported by the Sponsor

The registry’s posted analysis uses linear mixed models and reports group-by-time interaction estimates for 20 mg versus 60 mg and 20 mg versus 40 mg. The associated p-values are 0.16 and 0.77. These are the sponsor’s reported model-based tests of differences in trajectories over time. The week-12 arm estimates are least-squares mean changes from baseline, a different form of result from the interaction test.

No separate recalculated between-group contrast is reported in the registry record. The arm-specific week-12 estimates and their confidence intervals should not be treated as if subtracting them were equivalent to the sponsor’s longitudinal model analysis: a simple contrast of arm estimates would not reproduce the model’s use of repeated observations. There is no discrepancy flagged between sponsor and recalculated results. Accordingly, the sponsor’s own analysis remains the relevant reported inference; no unadjusted recalculation should replace it.

The registry does not provide confidence intervals for the interaction estimates. This limits how directly readers can assess their precision, even though the point estimates and p-values are reported. A distinct week-12 pairwise comparison with its own estimate and uncertainty is also not reported. The available record therefore supports interpretation of the sponsor’s two trajectory tests and the separate within-arm changes, but not a complete set of pairwise dose comparisons.

11. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures and eight analyses, including the primary outcome and three secondary outcomes. The posted primary analyses include two dose comparisons against the 20 mg group. The method used to address multiplicity across outcomes, time points, or comparisons is not reported in the registry record. Without a stated adjustment or testing hierarchy, the reported p-values should be read as the results of the named analyses, not as evidence that the overall family of tests was controlled for false-positive findings.

The primary measure was collected at baseline and weeks 1, 2, 3, 4, 8, and 12. The registry says the longitudinal model used data from all time points to obtain slopes and group-by-time interactions, while the arm-level outcome results concern week 12 compared with baseline. How the choice of time points and analyses was specified in advance is not reported in the registry record. The registry also does not report whether interim analyses were planned or conducted.

The analysis population is described as available cases, with missing values handled using maximum likelihood methods. The record does not give the number of observations available at each assessment, the extent or reasons for missingness, or details of the assumptions used for the missing-data model. Sensitivity analyses for missing data are not reported in the registry record. Consequently, the analysis description identifies the broad approach but does not allow a full assessment of how robust the estimates are to departures from its assumptions.

Enrollment was 28, while the brief description anticipated 105. The registry does not report the reason for the difference or a trial-specific sample-size justification. It is therefore not possible to determine from the record whether the final enrollment reflected a planned change, recruitment difficulty, or another explanation. The planning illustrations use an observed-effect premise and should not be interpreted as observed power or as proof that the study had a particular probability of detecting an effect.

12. 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

Serious events with the highest arm-level rate: gi illness requiring hospitalization (10.0%).

The registry reports serious adverse events for 0 participants in the 20 mg group, 0 in the 40 mg group, and 1 in the 60 mg group. The corresponding numbers at risk were 9, 9, and 10. These are counts within the registered groups; they do not establish whether an event was caused by treatment. The registry lists GI Illness requiring hospitalization as the top serious-event term at 10.0%, but does not identify which group that term belongs to in the record presented.

Other adverse events affected 0 participants in each group, with 9, 9, and 10 at risk, respectively. Death counts are not reported in the registry record. A zero count in the posted categories means no events were recorded in that category for the listed group; it does not rule out unrecorded events or establish that a treatment is free of risk.

These figures are descriptive and come from small groups. The record does not provide further detail about event timing, relatedness, severity beyond the serious-event classification, or the method used to collect adverse events. The one serious event in the 60 mg group should not be interpreted as a reliable estimate of comparative safety, and the serious-event term should not be assigned to a particular arm without an explicit group attribution.

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

The registry reports reductions from baseline in the arm-specific mean BPI-12 worst-pain scores at week 12, with the largest negative point estimate in the 60 mg group. The 20 mg estimate is -1.7, the 40 mg estimate is -2.2, and the 60 mg estimate is -4.7. These are estimates of within-group change, and their confidence intervals show uncertainty around those changes. They are not estimates of the causal difference between doses.

The two reported group-by-time comparisons are 20 mg versus 60 mg and 20 mg versus 40 mg. Their p-values are 0.16 and 0.77. Those analyses do not show compelling evidence of differing modeled trajectories for the respective groups, but they cannot demonstrate equivalence or establish that no dose difference exists. No direct 40 mg versus 60 mg analysis is reported. Nor does the registry provide a week-12 pairwise contrast with a confidence interval for each dose comparison.

The results do not establish which dose is preferable, whether any observed change is clinically important, or whether the findings apply beyond the enrolled study population. A threshold for a clinically meaningful BPI-12 change is not reported in the registry record. The short follow-up described in the record also means these findings concern the reported assessment period, not outcomes beyond it.

The trial was randomized, which is relevant to the design of treatment comparisons, but the available report is limited by enrollment of 28 and incomplete details about the analysis plan, missingness, and multiplicity. The record does not provide enough information to determine why enrollment was below the 105 anticipated in the brief description. Interpretation should therefore distinguish the observed pattern of estimates from the strength and scope of evidence supported by the reported between-group analyses.

14. Why This Trial Matters Statistically

This trial illustrates why within-group change and between-group evidence answer different questions. Each dose group has a model-based estimate of change from baseline, but the research question about dose response requires comparisons between groups. The arm estimates appear ordered by dose, yet that ordering alone does not show that dose groups differ. The reported group-by-time tests address longitudinal differences for two comparisons, and neither is a direct test of the 40 mg group against the 60 mg group.

It also highlights the role of repeated-measures models. The registry says the linear mixed model included data from all assessment times when estimating slopes and group-by-time interactions, while the main arm estimates focus on week 12 compared with baseline. Readers need to keep the longitudinal estimand separate from the single end-of-period change. Treating those as interchangeable can lead to overstatement of what the analysis tested.

Precision and reporting are especially important in a study with enrollment of 28 and arm sizes of 9, 9, and 10 for the primary outcome. Confidence intervals accompany the arm-level changes, but not the reported interaction estimates. A fuller account of between-group uncertainty, multiplicity, missing-data assumptions, and the planned sample-size rationale would make the evidence easier to evaluate.

Finally, the difference between the anticipated enrollment of 105 in the brief description and recorded enrollment of 28 is material context, but the reason is not reported. Statistical interpretation benefits from acknowledging that gap without inventing an explanation. The record supports careful description of the posted estimates and tests, while leaving important design and analysis details unresolved.

15. 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 record gives limited detail about the trial’s statistical plan. It does not report a trial-specific sample-size justification, the reason enrollment of 28 differed from the 105 anticipated in the brief description, or whether any changes to the planned design occurred. The listed planning assumptions are illustrative and do not explain the original enrollment target.

The primary results include arm-specific week-12 changes and two group-by-time tests against the 20 mg group. Confidence intervals for the interaction estimates are not reported, and a direct 40 mg versus 60 mg analysis is not reported. This leaves the precision and completeness of the dose comparisons difficult to assess. The record does not identify a multiplicity strategy across the reported outcomes and analyses.

Although the record describes available-case analysis and maximum likelihood handling of missing values, it does not report missing-data counts by time point, reasons for missingness, model diagnostics, or sensitivity analyses. The exact linear mixed-model specification, including any covariates and covariance structure, is also not reported. These omissions prevent a detailed assessment of the model assumptions and the robustness of the estimates.

There is a difference in masking terminology: the registry designation is quadruple, whereas the brief description calls the study double-blinded. The specific masked roles are not reported. The secondary outcomes are named, but their assessment schedules and detailed results are not included in the record. Further adverse-event details, including event relatedness and death counts, are also not reported. These limitations do not negate the posted results, but they constrain how fully readers can judge their precision, completeness, and generalizability.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Subacromial Corticosteroid Injection for Hemiplegic Shoulder Pain — NCT00597766.
• Registry record last updated 2017-12-13; status last verified 2017-11.
• Results first posted 2017-12-13.
• 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.

19. Record Summary

This completed Phase 2 randomized parallel-group trial evaluated 20 mg, 40 mg, and 60 mg triamcinolone with lidocaine for hemiplegic shoulder pain after stroke. The primary outcome was change in BPI-12 worst pain from baseline to week 12, analyzed with a linear mixed model using data from all listed assessment times for the trajectory analyses.

Enrollment was 28. The registry reports least-squares mean changes of -1.7, -2.2, and -4.7 for the 20 mg, 40 mg, and 60 mg groups, respectively, with 95% confidence intervals. Reported group-by-time tests compared 20 mg with 60 mg and 20 mg with 40 mg; a direct comparison of the two higher doses is not reported. The registry describes available-case analysis and maximum likelihood handling of missing values. It reports one serious adverse event in the 60 mg group, while death counts are not reported in the registry record.