A Research Study to Examine the Difference Between Local Anesthetics Alone and Local Anesthetics Plus Steroids in the Treatment of Chronic Headache: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Research Study to Examine the Difference Between Local Anesthetics Alone and Local Anesthetics Plus Steroids in the Treatment of Chronic Headache (NCT00203294), a randomized na study. The primary outcome is Headache Severity as Measured on an 11-point Verbal Scale (0 to 10):0=No Pain 10=Excruciating Pain.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group study at Thomas Jefferson University. The phase is listed as NA, and the study status is completed. The record lists migraine as the condition. Its brief description frames the question as a comparison of greater occipital nerve block with local anesthetics alone against local anesthetics combined with a steroid for chronic daily headache.

The two treatment groups received bilateral greater occipital nerve blocks and trigger point injections in the cervical paraspinal and trapezius muscles bilaterally. Both groups used lidocaine 2% and bupivacaine 0.25%; one received saline and the other triamcinolone 40 mg. The registry describes participants as adults with chronic daily headache and headache of at least moderate intensity at treatment.

Enrollment is listed as 45. The brief description says the study expected to enroll 60 patients, while the primary outcome population lists 15 patients in the group without steroids and 14 in the steroid group. These are distinct registry figures: the expected enrollment, overall enrollment, and primary-outcome group counts should not be treated as interchangeable. The record does not explain the difference between them.

Study start is listed as 2005-06 and primary completion as 2006-06. The registry record does not report the masking procedures, allocation concealment, randomization method, or the original statistical design assumptions. It also does not report a protocol-level description of how the analysis population was determined. Those omissions limit what can be concluded about conduct and prespecification from the registry record alone.

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: There were 15 patients in group A (no steroids injected) and 14 in group B (steroids injected).

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 Headache Severity as Measured on an 11-point Verbal Scale (0 to 10):0=No Pain 10=Excruciating Pain, measured over 20 minutes.

The primary endpoint is headache severity measured on an 11-point verbal scale, with 0 defined as no pain and 10 as excruciating pain. The assessment was made twenty minutes after treatment. The reported group values are negative, and the registry describes the outcome as a mean; however, it does not fully explain the calculation or reference point underlying those negative values. They should therefore be read as the posted outcome values rather than as a separately reconstructed scale score.

Headache severity directly represents the symptom targeted by the study’s clinical question. A numerical scale gives a continuous measure that can be summarized by a group mean and standard deviation, and it permits estimation of a difference between group means. That summary can communicate both the direction and size of the observed contrast, while a confidence interval describes its statistical precision.

The brief assessment time is important to interpretation: this endpoint concerns the measurement twenty minutes after treatment, not longer-term headache control. The registry record does not report the primary endpoint at other time points or a longer-term follow-up result. It also does not state a threshold for a clinically important change on this scale. Statistical evidence about the mean contrast therefore does not by itself establish whether the observed difference matters to patients.

7. Results Posted in the Registry

• Lidocaine 2% and Bupivacaine 0.25% Plus Triamcinolone 40 mg.: mean -3.70 versus -3.29 on control; difference -0.41 (95% CI -2.01 to 1.19), standardized effect d = -0.18; z-test p = 0.615.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: headache severity is summarized using a mean and standard deviation for each treatment group. A mean describes the group’s average recorded value. A standard deviation describes how spread out the individual values are around that mean. These summaries are useful for a comparison of group averages, but they do not show the full distribution or reveal whether a small number of observations strongly influenced the result.

What does the mean difference represent?

The unadjusted recalculation compares the mean for the triamcinolone group with the mean for the group receiving saline. Its estimate is -0.41 units. The sign depends on the stated comparison order: a negative estimate means the steroid-group mean is lower than the comparator mean on the reported outcome values. The registry describes the endpoint as headache severity, but does not fully specify the reference used to produce the negative group values. Consequently, interpretation should stay close to the posted numerical contrast rather than infer a more detailed scoring convention.

This is a simple, unadjusted comparison of group summaries. It does not account for covariates or apply a model-based adjustment. The registry record does not report an adjusted estimate or explain whether the sponsor’s analysis used a different outcome definition, data structure, or statistical method. The recalculation is therefore best understood as a transparent summary-statistic comparison, not a substitute for a fully described trial analysis.

How should the confidence interval be understood?

A confidence interval gives a range of estimates compatible with the observed data under the method used. The recalculated interval is -2.01 to 1.19. Its inclusion of zero indicates that the data do not provide a clear distinction between a negative and positive mean contrast under this approach. The range also shows that the point estimate is not precise: materially different contrasts remain compatible with the summary statistics. A confidence interval is not a guarantee that the true effect lies within the particular interval, nor does it describe the probability that a treatment is beneficial.

The recalculated interval is based on the group means, standard deviations, and sample sizes listed for the primary outcome. It is not the confidence interval from either of the registry’s Fisher Exact analyses; those analyses have no interval or estimate attached. The two kinds of results should not be treated as if they came from the same statistical procedure.

What does the p-value tell the reader?

The unadjusted recalculated p-value is 0.615. In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. Here, the recalculated p-value is consistent with the wide interval and the small estimated mean contrast. It does not establish equality or equivalence.

The registry lists two Fisher Exact tests with p <0.01, but does not identify the associated outcome parameter or provide estimates. Fisher Exact is generally used for categorical data, whereas the primary endpoint is described as a continuous measure summarized by means and standard deviations. This distinction makes the absent analysis details especially important. The record does not establish that the Fisher Exact tests concern the primary continuous endpoint, and no explanation for the difference from the recalculation is reported.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability exceeds what a statistical model assumes. If a model understates variability, its standard errors can be too small and its intervals too narrow; a model that handles the variability appropriately can produce more cautious uncertainty estimates. The registry’s primary outcome is summarized with standard deviations, but it does not report an over-dispersion assessment or a model-based analysis. This is a general consideration, not a reported feature of this trial.

More broadly, the mean and standard deviation do not reveal whether the scale values follow the assumptions of a particular parametric test. The registry record does not report diagnostic checks, transformations, robust methods, or a rationale for selecting the reported Fisher Exact tests. Without those details, the sponsor’s analysis cannot be independently reconstructed from the posted record.

What is not described?

The registry record does not report a complete statistical analysis plan, treatment of missing outcomes, analysis population, covariate adjustment, or multiplicity procedure. It also does not report the original sample-size justification or interim analyses. These details matter because they clarify which comparisons were planned, how incomplete observations were handled, and how multiple tests were interpreted. Their absence does not prove that such procedures were not performed; it means they cannot be evaluated from the registry record.

10. Confidence Intervals and Precision

The recalculated mean difference is -0.41 units, with an approximate 95% confidence interval from -2.01 to 1.19. This interval is the clearest summary of the precision of the unadjusted comparison from the posted continuous outcome statistics. Its breadth indicates that the estimated contrast is uncertain, and its span across zero means that the summaries are compatible with a difference in either direction under this calculation.

The group means are based on 15 patients without steroids and 14 with triamcinolone. With groups of this size, uncertainty can be substantial, especially when individual measurements vary. The standard deviations are 2.76 and 1.49, respectively. These figures describe observed dispersion within each group; they do not, on their own, establish why the variability differs.

Precision is distinct from statistical significance and clinical importance. A narrow interval would indicate a more precise estimate, but would not automatically imply a meaningful effect. A broad interval may include potentially important contrasts while also including little or no difference. The registry record does not report a threshold for a clinically meaningful change, so the confidence interval cannot be classified against such a threshold.

The two Fisher Exact results are not accompanied by confidence intervals or effect estimates. Their precision and practical magnitude therefore cannot be assessed from the registry record. Because the results do not align with the summary-statistic recalculation, and the record does not explain their outcome or analysis basis, the recalculated interval should not be presented as the uncertainty interval for the sponsor’s analyses. The sponsor’s own analysis takes precedence when the record’s discrepancy flag is true, but the missing details leave the distinction unresolved.

11. 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 illustrations based on the observed mean difference, not counts of events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. These are planning calculations, not the original design assumptions; the trial’s own design assumptions are not reported in the registry record.

In plain terms, the 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions hold. The 90% power column gives the corresponding per-arm figure for a design targeting a 90% chance. The figures are not the number enrolled in this study and do not describe the probability that the trial’s result is correct.

The rows illustrate planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The listed per-arm figures rise as the effect used for planning becomes smaller: 469 and 628 for planning at 100% of the observed effect; 834 and 1,116 at 75%; and 1,875 and 2,510 at 50%, for the 80% and 90% power targets respectively. Smaller effects need more participants to detect under otherwise unchanged assumptions.

These calculations are not observed power. They are planning illustrations based on the recalculated observed effect and do not establish what the trial was designed to detect. Because the observed estimate is uncertain, the figures should be read as conditional planning scenarios, not as a forecast or a recommendation for a future study.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.410; pooled standard deviation σ = 2.240.
2. n = 2 × (1.96 + 0.842)² × 2.240² / -0.410² = 468.7, rounded up to 469 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.41                      # observed difference in means
sigma <- 2.2402686677503                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(203294)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 469 (80% power), 628 (90% power)
 75% of observed effect: n per arm = 834 (80% power), 1,116 (90% power)
 50% of observed effect: n per arm = 1,875 (80% power), 2,510 (90% power)
power.t.test: 469.6 
Simulated power at n = 469 per arm: 0.798 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry lists two sponsor analyses using Fisher Exact, each with p <0.01. The analyses have no accompanying estimate, confidence interval, parameter, or outcome description. The registry record therefore does not show what numerical contrast those tests address or how they relate to the continuous primary endpoint of headache severity.

A separate unadjusted recalculation from the posted primary-outcome means, standard deviations, and group sizes gives a mean difference of -0.41, a 95% confidence interval of -2.01 to 1.19, and p = 0.615. This recalculation is a simple comparison of the continuous summaries; it is not the sponsor’s analysis. The registry flags a discrepancy between the two, and the sponsor’s own analysis takes precedence. The recalculation should not be substituted for, or described as correcting, the sponsor’s result.

The two approaches cannot be reconciled without knowing the outcome, coding, analysis population, and statistical method behind the reported Fisher Exact tests. Those details are not reported in the registry record. Accordingly, the sponsor’s reported p-values can be stated as posted, but their meaning for the primary continuous endpoint remains unclear. The recalculated comparison is informative as an independent summary-statistic check, while not resolving the discrepancy.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists two secondary questions: neck pain, and associated symptoms including nausea, phonophobia, and photophobia. The associated symptoms were to be assessed using a four-point scale from none to severe. The record lists four outcome measures and two posted secondary outcomes. It does not provide enough information to determine how all listed outcomes map to the analyses or how their results were handled.

Multiplicity arises when several outcomes, time points, or comparisons are tested. In general, conducting many tests can increase the chance of at least one apparently notable result even when no underlying difference exists. Statistical plans may address this through prespecified primary outcomes, adjustment procedures, or a clear hierarchy of tests. The registry record does not report a multiplicity procedure or an analysis hierarchy. It is therefore not possible to determine whether the reported p-values were adjusted or how the secondary outcomes were considered alongside the primary endpoint.

The record lists two Fisher Exact results with p <0.01 but does not link either one to an outcome or provide its estimate. This lack of attribution prevents a reader from assessing whether they correspond to the primary outcome, secondary outcomes, or other comparisons. It also prevents a clear accounting of how many analyses contributed to the reported findings.

The registry record does not report missing-data counts for the primary or secondary outcomes, methods for handling missing values, or the analysis population used for the sponsor’s tests. It does not state whether the analyses followed an intention-to-treat approach, a per-protocol approach, or another population definition. The primary outcome population lists 15 and 14 patients, but that alone does not establish whether these counts include all randomized participants or whether any randomized participants lacked outcome data.

These omissions do not establish that multiplicity or missing data were mishandled. They limit the ability to evaluate robustness, reproduce the sponsor’s analysis, and distinguish prespecified from exploratory results. The registry record also does not report interim analyses or the trial’s complete statistical plan.

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 2% reporting threshold.

The adverse-event record lists a GON block-only group with 22 participants at risk for serious adverse events and 22 at risk for other adverse events. It reports zero affected for both categories. The GON block plus steroid group lists 23 participants at risk in each category and also reports zero affected for serious and other adverse events.

These figures describe the counts recorded in the registry for the stated groups. They should not be interpreted as proof that no adverse events of any kind occurred outside the categories or reporting period represented by those fields. The registry record does not report the event definitions, observation window, ascertainment procedures, or an explanation of how these safety groups relate to the primary-outcome groups.

Deaths are not reported in the registry record. No serious adverse event terms are listed. The available counts can be stated as posted, but the limited detail does not support a broader comparative safety conclusion. In particular, the group counts at risk should not be assumed to equal the primary outcome analysis counts.

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

The primary-outcome summaries describe headache severity twenty minutes after treatment in two randomized groups. The mean values were -3.29 in the group without steroids and -3.7 in the group receiving triamcinolone. The unadjusted recalculation estimates a mean difference of -0.41, with a 95% confidence interval from -2.01 to 1.19 and p = 0.615. These statistics indicate substantial uncertainty around the estimated contrast and do not clearly separate the group means under that calculation.

This result does not establish that the treatments are equivalent. A conclusion of equivalence requires a prespecified equivalence margin and an analysis designed to test it; neither is reported in the registry record. Nor does the recalculation establish that either approach is more effective. The confidence interval includes contrasts on both sides of zero, and the record does not report a threshold for a clinically meaningful change.

The registry separately reports two Fisher Exact tests with p <0.01. Since no outcome parameter or estimate accompanies them, their relevance to the primary continuous measure is uncertain. The registry flags a discrepancy, so the sponsor’s analysis takes precedence over the unadjusted recalculation. At the same time, the missing analysis details make it impossible to explain how those reported tests relate to the means and standard deviations.

The result is limited to the stated twenty-minute assessment. It does not establish whether changes persisted, whether neck pain or associated symptoms differed, or how outcomes developed at later times. The record lists secondary questions but does not provide their outcome estimates in the registry record described for this result.

The most defensible reading is therefore narrow: the posted continuous summaries produce an imprecise unadjusted comparison, while the sponsor’s reported tests are statistically different in form and insufficiently described to interpret against the primary outcome. The registry information does not support a treatment recommendation, a claim of benefit or lack of benefit, or a generalization beyond the studied participants and assessment.

17. Why This Trial Matters Statistically

This trial highlights how the interpretation of a result depends on more than a p-value. The primary endpoint is continuous, and the posted group means and standard deviations allow an unadjusted estimate of the mean contrast and its confidence interval. That recalculation conveys both the direction of the estimate and its uncertainty, rather than reducing interpretation to a threshold-based decision.

The record also illustrates why statistical transparency matters. Two Fisher Exact results are reported, each with p <0.01, yet neither has an attached outcome estimate or description. The recalculated comparison from the continuous summaries instead has p = 0.615. Because the registry identifies a discrepancy, the sponsor’s own analysis takes precedence, but absent methods prevent readers from understanding the basis for the different results. Reporting the test name alone is not enough to assess the magnitude or relevance of a finding.

Small outcome groups make precision an important part of interpretation. The confidence interval is broad and includes values on either side of zero. That pattern underscores the difference between failing to establish a clear contrast and establishing that two approaches are equivalent. It also explains why planning illustrations based on a smaller target effect require more participants under the stated assumptions, without implying that those figures reflect the original design.

Finally, the record distinguishes a short-term symptom assessment from broader clinical questions. A single assessment twenty minutes after treatment cannot answer questions about durability. Secondary outcomes and safety counts address other dimensions, but the record lacks enough analysis detail to connect them to an overall conclusion. This makes transparent outcome definitions, analysis populations, uncertainty intervals, and clear attribution of tests especially important.

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 population includes 15 patients without steroids and 14 with steroids, while overall enrollment is listed as 45 and the brief description says 60 patients were expected. The registry record does not explain the difference among these counts or identify how many randomized participants contributed to each analysis. The small primary-outcome groups also leave the mean contrast imprecise.

The primary result is recorded at twenty minutes after treatment. The registry record does not report longer-term primary headache-severity results, so the posted outcome cannot establish persistence. While the record lists secondary aims concerning neck pain and associated symptoms, their effect estimates are not included in the results.

The treatment descriptions identify lidocaine 2%, bupivacaine 0.25%, saline, and triamcinolone 40 mg, and describe bilateral nerve blocks and trigger point injections. However, the registry does not explain procedural standardization, masking procedures, allocation concealment, or adherence. These omissions limit assessment of how consistently treatment was delivered and how potential sources of bias were controlled.

The registry lists two Fisher Exact results with p <0.01 but no outcome parameter or estimate, while the unadjusted continuous recalculation gives a different result. The discrepancy is flagged, and the sponsor’s own analysis takes precedence, but the registry record does not provide enough information to reproduce or reconcile it. It also does not report the statistical analysis plan, missing-data handling, analysis population, multiplicity procedure, interim analyses, or original sample-size justification.

Finally, the adverse-event record provides counts but not definitions or observation details, and deaths are not reported in the registry record. These limits call for a cautious reading of the posted statistics and do not establish that unreported procedures or outcomes were absent from the study.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Research Study to Examine the Difference Between Local Anesthetics Alone and Local Anesthetics Plus Steroids in the Treatment of Chronic Headache — NCT00203294.
• Registry record last updated 2014-05-07; status last verified 2014-04.
• Results first posted 2014-05-07.
• 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, single-masked, parallel-group comparison at Thomas Jefferson University. Adults with chronic daily headache received bilateral greater occipital nerve blocks and trigger point injections using local anesthetics with saline or with triamcinolone. The primary outcome was headache severity on an 11-point verbal scale twenty minutes after treatment.

The primary outcome population lists 15 patients without steroids and 14 with steroids. The unadjusted recalculation gives a mean difference of -0.41, a 95% confidence interval of -2.01 to 1.19, and p = 0.615. The registry also reports two Fisher Exact tests with p <0.01 but does not identify their outcome parameters. With a flagged discrepancy, the sponsor’s own analysis takes precedence; the registry record does not explain the difference.

The record lists secondary questions about neck pain and associated symptoms, and adverse-event counts of zero affected in both reported safety categories for each group. Longer-term outcomes, deaths, and important analysis details are not reported in the registry record.