Comparison of Ibuprofen, Cyclobenzaprine, or Both for Acute Cervical Strain: A Randomized Clinical Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Ibuprofen, Cyclobenzaprine, or Both for Acute Cervical Strain: A Randomized Clinical Trial (NCT00790270), a randomized phase 2 study. The primary outcome is Use of Rescue Medications.

2. Clinical Question

The question is clinically framed around short-term symptoms and additional medication use. Rescue use can reflect whether a participant sought or needed medication beyond the assigned study medicines, but it is not interchangeable with a pain score or a direct measure of the amount of pain experienced. The record does not give a threshold defining a clinically important difference in rescue use, nor does it report a protocol-defined comparison of the combination against each single medication as a separate primary hypothesis. The available summaries therefore describe the observed group counts and the comparisons against cyclobenzaprine, rather than establishing that any one regimen is superior in a broader population.

3. Trial Design

The registry identifies this as a randomized, parallel-group phase 2 trial. Its masking entry is quadruple. The record names Stony Brook University as sponsor and identifies cervical strain as the condition. Enrollment is recorded as 61. The study status is completed; the recorded start is 2003-01 and primary completion is 2004-01.

Participants were assigned to one of three arms: cyclobenzaprine, ibuprofen, or ibuprofen plus cyclobenzaprine. The posted primary outcome counts are 13 participants in the cyclobenzaprine arm, 9 in the ibuprofen arm, and 9 in the combination arm. The corresponding arm sizes are 21, 20, and 20. Those counts describe the posted outcome data; they should not be taken as additional information about the assignment process, adherence, or completeness of follow-up.

Randomization and a parallel-group structure support comparisons between assigned groups, while masking can reduce some forms of bias when implemented successfully. However, the registry does not report the randomization method, how allocation was concealed, who was masked, or whether masking was maintained. It also does not report dose schedules, treatment duration, eligibility criteria, participant flow, or details of adherence. Those details cannot be reconstructed from the design labels alone.

The primary outcome timeframe is 24 hours. The registry also identifies resumption of work or school as a secondary outcome, with a next-day timeframe, and lists time to resumption of work among the secondary outcomes. Numerical results for time to resumption of work are not reported in the registry record. The posted results are therefore a brief account of short-term outcome counts, not a complete description of all trial procedures or all planned assessments.

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

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 Use of Rescue Medications, measured over 24 hours.

The primary endpoint is the number of participants who used additional rescue medication beyond the study medicines. The registry describes the timeframe as 24 hours and further characterizes the population as patients using additional analgesics on the day following enrollment. In the posted results, the endpoint is represented as a count of participants with the event in each arm.

Rescue-medication use is a binary outcome at the participant level: each participant either is or is not counted as having used additional medication during the specified period. This gives a direct, interpretable summary of how often participants turned to medication beyond their assigned study drugs. It may provide information about short-term symptom management, but the endpoint does not measure pain intensity itself, the amount of rescue medication taken, or the reason for taking it. Those details are not reported in the registry record.

For the comparisons, the risk difference expresses the difference between the proportions with rescue-medication use in the two arms being compared. A negative estimate in these comparisons means the event proportion is lower in the ibuprofen or combination arm than in the cyclobenzaprine reference arm. This description is specific to the direction of the posted comparison; it is not by itself evidence of a reliable or clinically important difference. The confidence interval and statistical test are relevant to how uncertain the estimate is.

The endpoint is useful for describing an observable, short-term event, but its interpretation depends on the trial’s definitions and follow-up procedures. Details such as permitted rescue medicines, how use was recorded, and how missing outcome observations were handled are not reported in the registry record.

7. Results Posted in the Registry

• Ibuprofen: 45.0% (9/20) versus 61.9% (13/21) on control; risk difference -16.9 percentage points (95% CI -47.0 to 13.2), risk ratio 0.73 (0.40–1.31); unadjusted two-proportion z-test p = 0.278.
• Ibuprophen Plus Cyclobenzaprine: 45.0% (9/20) versus 61.9% (13/21) on control; risk difference -16.9 percentage points (95% CI -47.0 to 13.2), risk ratio 0.73 (0.40–1.31); unadjusted two-proportion z-test p = 0.278.

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.

Resumption of Work or School

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ibuprofen: 70.0% (14/20) versus 38.1% (8/21) on control; risk difference 31.9 percentage points (95% CI 3.0 to 60.8), risk ratio 1.84 (0.99–3.40); unadjusted two-proportion z-test p = 0.041.
  • Ibuprophen Plus Cyclobenzaprine: 65.0% (13/20) versus 38.1% (8/21) on control; risk difference 26.9 percentage points (95% CI -2.6 to 56.4), risk ratio 1.71 (0.91–3.21); unadjusted two-proportion z-test p = 0.085.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ibuprofen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ibuprophen Plus Cyclobenzaprine and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns resumption of work or school the next day. Its overall pattern is directionally more favorable to the two arms containing ibuprofen than to cyclobenzaprine alone, although the strength of evidence differs between the two comparisons. A separate listed secondary outcome is time to resumption of work, but numerical results for that measure are not reported in the registry record.

This pattern does not mirror the primary outcome in the sense of answering the same question. The primary endpoint counts additional rescue-medication use; resumption of work or school records an activity on the next day. A difference in one does not establish a difference in the other, and the registry does not report an analysis that connects them. The primary comparisons themselves do not provide clear statistical evidence of a difference, so the secondary pattern should not be used to recast the primary result as conclusive.

The secondary results carry less weight because they are not reported as adjusted for multiple comparisons, and the registry record does not describe a prespecified hierarchy or analysis plan. When several outcomes or comparisons are examined, some apparently notable results can occur by chance even when there is no underlying effect. This general concern is one reason to treat unadjusted secondary findings as exploratory rather than confirmatory.

The record does not provide the planned status of each secondary analysis, missing-data handling, or a sponsor-reported analysis for these outcomes. It also does not report whether resumption was assessed by self-report or another method. These gaps limit interpretation of both the observed pattern and its generalizability. The secondary results can motivate further investigation, but they do not on their own settle the broader clinical question posed by the trial.

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

• Time to Resumption of Work
• Resumption of Work or School

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparisons concern binary outcomes: whether a participant used rescue medication or resumed work or school. For a binary outcome, the event proportion is the number of participants with the event divided by the number in the arm. The risk difference compares those proportions by subtraction. It is expressed on the probability scale, so a value of zero corresponds to equal observed proportions; a negative value in the primary comparisons indicates a lower observed event proportion in the non-reference arm. The same sign convention means a positive value in the work-or-school comparisons indicates a higher observed proportion in the non-reference arm.

What does the risk difference describe?

The risk difference is an absolute contrast between the observed proportions, not a relative measure. It conveys the size and direction of the difference on the outcome’s own scale. Its interpretation depends on which event is being counted and which arm is used as the reference. It does not adjust for participant characteristics or other variables. The registry record does not report adjusted primary analyses.

Relative measures such as a risk ratio or odds ratio can also describe binary outcomes, but they answer a different scale question. A risk ratio compares proportions as a ratio, while an odds ratio compares odds. These relative measures can appear more or less pronounced than an absolute difference, particularly when events are common. The essential interpretation still depends on uncertainty, the event definition, and the study context. No relative-measure estimate is needed to understand the primary posted comparison, which is reported as a risk difference.

How should a confidence interval be read?

A confidence interval gives a range of effect estimates compatible with the observed data under the method used to calculate it. It communicates uncertainty around the point estimate. An interval that includes zero for a risk difference is compatible with no difference, as well as with effects in either direction when its bounds extend across zero. That does not mean every value in the interval is equally plausible, nor does it give the probability that the true effect lies in the interval. The primary comparison intervals cross zero, so the data do not tightly determine the direction or size of the difference.

What does the p-value add?

A p-value is calculated under a specified null model, typically one in which the groups have no difference in the outcome. It describes how unusual data at least as incompatible with that model would be if the model and analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The primary comparisons have unadjusted p-values of 0.278. The secondary comparisons have unadjusted p-values of 0.041 and 0.085. These values should be considered alongside the effect estimates, their intervals, the endpoint hierarchy, and the analysis plan, which is not reported in the registry record.

Why distinguish planned from observed results?

The arm counts and event counts describe what was posted as observed. By contrast, the sample-size illustrations use an observed effect as a planning input and estimate participant requirements under stated assumptions. Such illustrations are not analyses of whether the completed trial had sufficient power after the fact. They do not recover the original sample-size rationale, which is not reported in the registry record.

For binary outcomes, the event counts are a compact summary, but their uncertainty can be considerable when arm sizes are limited. A few event classifications can appreciably change the observed proportion. Confidence intervals help make that limitation visible. They do not repair design limitations or account for unreported features such as missing observations, adherence, or deviations from assigned treatment.

What is meant by an unadjusted comparison?

An unadjusted comparison uses the posted group summaries without accounting for additional covariates or a more complex model. The estimates are simple, unadjusted comparisons. This is transparent and makes the arm-level contrast easy to interpret, but it can differ from an analysis specified in a trial protocol, especially if that analysis adjusts for baseline variables or uses a different method. No such sponsor analysis is reported in the registry record, and there is no discrepancy flagged between the summaries and the recalculated comparisons.

Random assignment can support a causal interpretation when the trial conduct, outcome ascertainment, and analysis preserve the benefits of assignment. The registry’s randomization label alone does not document these details. Without information on allocation, missing data, analysis population, adherence, and protocol deviations, the statistical summaries should be interpreted as comparisons of the posted arm results rather than as a complete account of the trial’s inferential analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.169 for ibuprofen versus cyclobenzaprine and also -0.169 for the combination versus cyclobenzaprine. The posted confidence intervals for these comparisons extend from negative to positive values and include zero. That means the observed data do not pin down whether the underlying difference favors the comparison arm, favors the reference arm, or is close to no difference. The point estimates alone should not be treated as precise estimates of the effect.

The intervals are broad relative to the point estimates, indicating substantial uncertainty. This is consistent with the limited arm sizes and the number of observed events. A confidence interval is not a guarantee about the range of effects in the population; it describes uncertainty according to the statistical method and assumptions used. Details of the interval calculation are not reported in the registry record.

The secondary work-or-school comparisons also have uncertainty. The interval for the ibuprofen comparison lies above zero in the posted calculation, while the interval for the combination comparison extends across zero. These interval patterns are useful descriptive evidence, but they do not resolve concerns about secondary-outcome interpretation, multiplicity, or the absence of reported sponsor analyses.

Precision and statistical significance are related but distinct. A small p-value does not by itself indicate a large or meaningful effect, and a non-small p-value does not establish that an effect is absent. The primary intervals allow a range of effects, so the result is better characterized as inconclusive about the direction and magnitude than as evidence of equivalence. The registry does not report a clinically important threshold against which to judge the estimated 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 sample-size illustrations are planning scenarios based on the observed effects, not the trial’s own original design assumptions. For these binary outcomes, the figures are participants per arm, not total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario asks what sample size would be needed to detect the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm estimated to give an 80% chance of detecting the specified effect under the planning assumptions, if that effect were the true one and the analysis assumptions held. The 90% power column applies the same idea with a higher chance of detection, which generally requires more participants. These are prospective planning quantities, not evidence about what the completed trial could or could not detect.

The rows use the full observed effect and smaller fractions of that effect. Planning for 75% of the observed effect requires more participants per arm than planning for 100%; planning for 50% requires still more. This reflects a general statistical principle: smaller effects are harder to distinguish from random variation, so more information is needed. The resulting figures are particularly sensitive to the observed effect used as the planning input. When that effect comes from a small study, it can be an unstable basis for future planning.

The numbers are not observed power, and they do not show that the trial had a particular probability of finding a result after it was completed. They are illustrations under the stated assumptions only. The record does not report whether the trial’s actual design used these assumptions, what effect its investigators intended to detect, or whether other design features informed its planned enrollment.

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 = 0.619; treatment proportion p₁ = 0.450; average p̄ = 0.535.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7054 = 1.3826.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6952 = 0.5851.
4. n = (1.3826 + 0.5851)² / (-0.1690)² = 135.5, rounded up to 136 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 <- 0.619047619047619                          # control proportion
p1 <- 0.45                          # 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(790270)
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 = 136 (80% power), 181 (90% power)
 75% of observed effect: n per arm = 240 (80% power), 321 (90% power)
 50% of observed effect: n per arm = 536 (80% power), 716 (90% power)
power.prop.test: 135.5 
Simulated power at n = 136 per arm: 0.793 (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 more than one outcome and reports more than one comparison. When several outcomes, arms, or analyses are examined, the chance of encountering an apparently unusual result by chance can increase. Statistical approaches may address this through a prespecified primary outcome, a testing hierarchy, or an adjustment for multiple comparisons. The registry record does not report a multiplicity adjustment, testing hierarchy, or detailed statistical analysis plan. The secondary p-values should therefore be read as unadjusted and exploratory, not as results that have been shown to control the overall chance of false-positive findings.

The primary outcome is identified, which helps distinguish it from secondary outcomes, but the record does not say whether the analyses were prespecified in a protocol or whether any outcomes or comparisons were added or changed. Nor does it report interim analyses or stopping rules. Such information is not reported in the registry record, so no assumptions about the trial’s monitoring or analysis decisions are warranted.

Missing-data handling is also not reported. The posted arm sizes and event counts do not establish whether every randomized participant had an observed outcome, how unavailable observations were treated, or whether the outcome analysis included all randomized participants. The registry does not report an intention-to-treat population, a per-protocol population, or a missing-data sensitivity analysis. These omissions matter because conclusions can depend on how participants with incomplete outcomes are handled.

There is no reported sponsor analysis in the registry record for the posted comparisons. Consequently, the available estimates are best understood as simple unadjusted calculations from the posted summary counts. No discrepancy is flagged between those calculations and a sponsor analysis. If an official trial analysis used a different prespecified method, its details and results are not reported in the registry record.

These reporting gaps do not demonstrate that the trial lacked appropriate procedures; they mean that the record does not allow readers to verify them. Clear protocol and analysis reporting would help distinguish confirmatory findings from exploratory ones and assess the robustness of results to missingness and analytic choices.

15. 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 1% reporting threshold.

The registry reports zero serious adverse events in the cyclobenzaprine arm, zero in the ibuprofen arm, and zero in the combination arm. It also reports zero other adverse events in each arm. These entries describe the adverse-event counts recorded in the registry for the groups at risk; they should not be interpreted as proof that no adverse effects occurred beyond what was captured or reported.

The record does not list serious adverse-event terms, and deaths are not reported in the registry record. Details about how adverse events were defined, collected, assessed for relationship to study medication, or followed over time are not reported. The short 24-hour primary outcome timeframe should not be mistaken for a complete account of safety follow-up; the registry does not describe the adverse-event observation period in detail.

With limited group sizes, zero reported events cannot establish that an event is impossible or that risks are identical across arms. These figures are descriptive registry entries, not a comprehensive safety comparison. They should be read alongside the limitations in reporting and should not be used alone to infer safety in other populations or settings.

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

The results describe a short-term randomized comparison of three study arms in participants with cervical strain. For the primary outcome, rescue-medication use was less common in the observed ibuprofen and combination arms than in the cyclobenzaprine arm. The risk-difference estimates point in that direction, but their confidence intervals include zero and the unadjusted p-values do not provide strong evidence of a difference. The data therefore leave substantial uncertainty about the size and direction of any underlying difference.

The secondary next-day work-or-school outcome shows a different, more favorable direction for the arms containing ibuprofen. Because these are unadjusted secondary results and the registry does not report a multiplicity plan, they are suggestive rather than confirmatory. The record does not provide numerical results for the listed time-to-resumption outcome. Taken together, the results are not a definitive answer to whether combining the medicines improves outcomes compared with either medicine alone.

The trial does not directly report a pain-intensity measure in the posted primary outcome. Rescue use may reflect additional medication use, but it does not show how much pain participants experienced or how they rated symptom relief. The work-or-school measure likewise captures a functional event, not a complete measure of recovery. The registry record does not report a clinically important difference threshold for either outcome.

These data should not be generalized automatically beyond the studied setting, participants, treatment procedures, and short-term measures. Eligibility, dosing, adherence, participant characteristics, missing-data handling, and detailed analysis methods are not reported in the registry record. The absence of reported adverse events is also not proof of no risk. The appropriate interpretation is limited to the posted counts and the uncertainty around the comparisons, not a treatment recommendation or a broad claim that one regimen works or does not work.

17. Why This Trial Matters Statistically

This trial is a useful example of why an observed difference and a statistically persuasive result are not the same thing. The primary point estimates favor the ibuprofen-containing arms for rescue-medication use, but the confidence intervals extend across no difference. A directional pattern can be visible in the counts while still being too uncertain to establish the size or even the direction of the underlying effect.

It also illustrates the value of looking at absolute effects and intervals rather than relying on a single p-value. The risk difference describes the contrast on the outcome’s probability scale, while the interval conveys how much the estimate could vary given the data and method. The primary p-values and confidence intervals tell a consistent story of substantial uncertainty, not proof that the groups are identical.

The secondary outcome highlights another common interpretive challenge. Its pattern may appear more encouraging, but unadjusted secondary comparisons have less evidential weight when the testing plan and multiplicity handling are not reported. A result should be interpreted according to its role in the study, not selected simply because it appears more statistically notable than the primary outcome.

Finally, the sample-size illustrations distinguish planning from retrospective claims about a completed trial. They show how assumptions about the effect size influence participant requirements, but they cannot establish the trial’s original rationale or observed power. This separation is important for responsible statistical interpretation: estimates, uncertainty, planning scenarios, and registry reporting gaps each answer different questions.

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 registry record leaves several trial-specific details unclear. It names the condition and study arms but does not report eligibility criteria, baseline characteristics, treatment doses, administration schedules, adherence, or participant flow. Without those details, it is difficult to assess how closely the enrolled participants and study procedures correspond to other clinical settings.

The posted primary comparisons are unadjusted and based on limited arm sizes. Their intervals are broad, and the primary endpoint captures rescue-medication use rather than pain intensity or the amount of additional medication. The record does not report the definition of a clinically important difference, the method used to ascertain rescue use, or whether outcome assessors were masked in practice.

The record also does not describe missing-data handling, the analysis population, protocol deviations, allocation concealment, or the statistical analysis plan. There is no reported sponsor analysis, and the secondary results are unadjusted. The registry does not report a multiplicity approach or numerical results for time to resumption of work. These are limits on what can be evaluated from the record, not evidence that appropriate methods were or were not used.

Safety information is sparse: the registry entries report no adverse events, but the event definitions and observation period are not detailed, and deaths are not reported in the registry record. The available summaries should therefore be viewed as a limited account of short-term outcomes rather than a comprehensive assessment of benefit, harm, or durability.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Ibuprofen, Cyclobenzaprine, or Both for Acute Cervical Strain: A Randomized Clinical Trial — NCT00790270.
• Registry record last updated 2012-11-21; status last verified 2012-10.
• Results first posted 2012-11-21.
• 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

The registry describes a completed, randomized, parallel-group phase 2 trial sponsored by Stony Brook University, with quadruple masking recorded. Enrollment is 61, and the condition is cervical strain. The three arms received cyclobenzaprine, ibuprofen, or ibuprofen plus cyclobenzaprine.

The primary outcome was participant use of additional rescue medication within 24 hours. The posted risk-difference estimates favor the ibuprofen and combination arms over cyclobenzaprine, but the confidence intervals include no difference and the unadjusted p-values are 0.278. The secondary work-or-school outcome has a more favorable directional pattern for the ibuprofen-containing arms, but the comparisons are unadjusted and should be treated cautiously.

The registry reports zero serious and zero other adverse events in each arm. Details of the statistical plan, missing-data handling, participant characteristics, and several trial procedures are not reported in the registry record. Overall, the posted findings are informative as short-term descriptive comparisons, but their precision and reporting limitations preclude a definitive interpretation.