Patient Controlled Intrathecal Analgesia With Bupivacaine for Chronic Low Back Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Patient Controlled Intrathecal Analgesia With Bupivacaine for Chronic Low Back Pain (NCT02886286), a randomized phase 4 study. The primary outcome is Change From Baseline in the Numerical Rating Pain Scale (NRS).

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, quadruple-masked, crossover study. It is listed as Phase 4 and completed, with enrollment of 17. The study start is recorded as 2016-05 and primary completion as 2017-12. University Hospitals Cleveland Medical Center is listed as the sponsor.

A crossover design compares interventions within a study in which participants receive more than one intervention over the course of the trial. Randomization and masking are design features intended to reduce bias in assignment and assessment. The registry record does not report the allocation sequence, the order in which participants received the interventions, the duration of each treatment period, or whether a washout period was used. Those details matter when assessing possible period effects or carryover from an earlier intervention.

The intervention descriptions concern self-administered boluses through a Personal Therapy Manager in an intrathecal pump. In the bupivacaine-plus-opioid condition, the solution contained bupivacaine and an opioid; in the comparator condition, it contained an opioid without bupivacaine. The opioid options listed were hydromorphone, fentanyl, or morphine. The record does not specify how the choice among these opioids was made or whether it varied by participant.

The primary outcome population is described as all participants who received each intervention. The reported primary summary lists 16 participants for each intervention. The record does not explain the relationship between enrollment and the outcome counts, identify any exclusions, or describe missing outcome data. It also does not report the trial’s original statistical analysis plan or its original assumptions for design and sample size.

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: All participants who received each intervention were included in the analysis.

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: Participants who finished study.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Numerical Rating Pain Scale (NRS), measured over Before self-administered bolus using Patient Therapy Manager device (PTM) and within 30 minutes of PTM bolus.

The primary endpoint is titled change from baseline in the Numerical Rating Pain Scale. The scale runs from 0 to 10, where 0 means no pain and 10 means the worst imaginable pain. Participants recorded a pain score just before a self-administered bolus and the lowest pain score within 30 minutes after it. The registry describes the endpoint as a mean measured in units on a scale, with standard deviations reported for each intervention.

A pain rating is a direct patient-reported measure of the symptom the intervention was intended to address. Recording a score near the bolus and a score afterward focuses the measurement on short-term change associated with bolus use. The registry record does not further define the calculation used to turn those diary entries into the reported change, or explain how repeated bolus entries were combined for each participant. That leaves some ambiguity about the precise construction of the endpoint.

The posted summaries give mean values of 1.87 for bupivacaine plus opioid and 1.81 for opioid alone. The registry record does not state in the endpoint description whether a positive change denotes improvement or worsening, so the direction should not be assigned a clinical meaning beyond the stated score measurement. The endpoint addresses pain; it does not by itself measure functional status, overall treatment satisfaction, or longer-term pain control.

7. Results Posted in the Registry

• Opioid: mean 1.81 versus 1.87 on control; difference -0.06 (95% CI -1.05 to 0.93), standardized effect d = -0.04; z-test p = 0.906.

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.

Change From Baseline in Oswestry Disability Index (ODI)

• 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:
  • Opioid: mean 2.67 versus 0.88 on control; difference 1.79 (95% CI -4.59 to 8.17), standardized effect d = 0.19; z-test p = 0.583.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Opioid and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Patient Global Impression of Change (PGIC)

• 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:
  • Opioid: mean 1.25 versus -0.06 on control; difference 1.31 (95% CI -0.05 to 2.67), standardized effect d = 0.67; z-test p = 0.059.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Opioid and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in painDETECT

• 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:
  • Opioid: mean 0.25 versus 0.69 on control; difference -0.44 (95% CI -3.18 to 2.30), standardized effect d = -0.11; z-test p = 0.753.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Opioid and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering disability, patient global impression of change, painDETECT, average weekly pain ratings, and treatment satisfaction. Posted summaries are available for disability, patient global impression of change, and painDETECT; the registry lists five secondary outcomes in total. No reported analyses are listed for the posted secondary summaries, and the registry record does not provide results for average weekly pain ratings or treatment satisfaction in the posted outcome summaries.

Across the posted secondary results, the unadjusted intervals are broad relative to the estimates, and the intervals include zero. The corresponding unadjusted p-values do not provide a clear separation between interventions. This general pattern is consistent with the primary comparison’s uncertainty, rather than providing an independent, decisive signal that resolves it. The secondary outcomes measure related but distinct aspects of pain and functioning, so they should not be treated as interchangeable replications of the primary endpoint.

Secondary findings carry less weight when multiple outcomes are examined without a reported plan for controlling the chance of false-positive findings. The registry record does not report a multiplicity strategy, a hierarchy of outcomes, or adjustments to the secondary analyses. When many outcomes are considered, a nominally notable result can arise by chance even if no intervention difference exists. This is a general statistical concern, not evidence that any particular result is false.

The secondary outcomes are also reported as unadjusted comparisons, and the record does not describe whether the crossover structure was handled in the analysis. Their role is therefore exploratory in interpretation. They can suggest questions for further study, but they do not overcome the limits of the primary result or establish a broad effect on function, pain characteristics, or satisfaction.

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

• Change From Baseline in Oswestry Disability Index (ODI)
• Change From Baseline in Patient Global Impression of Change (PGIC)
• Change From Baseline in painDETECT
• Change From Baseline in Average Weekly Numeric Pain Rating Score (NRS)
• Change From Baseline in Treatment Satisfaction

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is reported as a mean with a standard deviation, using units on a pain scale. A mean gives the arithmetic average of observed values. A standard deviation describes how dispersed values are around that average. These summaries are useful for describing the reported groups, but they do not show every participant’s response or the shape of the outcome distribution.

What does the mean difference represent?

The unadjusted contrast is expressed as opioid alone relative to bupivacaine plus opioid. Its estimate is -0.06. This sign follows the stated comparison order; it is not a measure of whether pain improved unless the direction and construction of the change score are defined. The registry record gives the diary timing and the scale anchors, but does not fully define how repeated bolus entries were reduced to the reported participant-level outcome.

For a general explanation, a mean difference places the two group averages on the same scale and expresses their separation in the outcome’s original units. It is directly interpretable in scale units, unlike a standardized effect measure. A standardized effect expresses a contrast relative to variability, but the registry record does not provide a clinically meaningful threshold for either form of effect.

Why does the crossover design matter?

In general, a crossover design can compare each participant’s outcomes under different interventions, which may account for stable differences between participants. This relies on appropriate handling of the repeated observations and the trial periods. Analyses may need to account for within-participant correlation, treatment sequence, period effects, and possible carryover. The registry confirms a randomized crossover design but does not report the sequence, treatment-period details, washout procedures, or a model that addresses these features. Consequently, the posted group summaries alone do not show whether the comparison used the paired information the design can generate.

For general context, observations from the same participant tend to be related rather than independent. Treating related observations as independent can misstate uncertainty. Conversely, a suitable paired analysis can use the within-participant contrast. The registry record does not report enough methodological detail to determine how the sponsor handled this issue. The recalculated unadjusted comparison is based on posted summary statistics and should not be mistaken for a reported crossover model.

How should the confidence interval and p-value be read?

A confidence interval represents uncertainty around an estimated effect under the calculation’s assumptions. For the primary contrast, the reported interval crosses zero. Thus, the data do not distinguish a zero mean difference from contrasts on either side of zero at the interval’s stated confidence level. The registry record does not state the confidence level in the primary outcome entry; the interval is the posted unadjusted interval used in the comparison summary.

The unadjusted p-value is 0.906. In general, a p-value describes how unusual data at least as extreme as those observed would be under a specified null hypothesis and test assumptions. It does not measure the probability that the null hypothesis is true, nor does it establish equivalence. The registry record does not report a multiplicity adjustment or a sponsor-reported inferential analysis for this endpoint.

What does over-dispersion mean in general?

For continuous outcomes, a standard deviation larger than the mean is not by itself evidence of a problem; the measures have different interpretations and can vary independently. More generally, over-dispersion refers to variability greater than an assumed statistical model allows. If a model understates variability, its standard errors may be too small and its confidence intervals too narrow. That concern is relevant only when a particular model makes a dispersion assumption. The registry record does not identify a model for the posted primary comparison, so over-dispersion cannot be assessed from the summaries alone.

What is and is not reported?

The primary analysis population is described as all participants who received each intervention, and the outcome summaries provide the group sizes, means, and standard deviations. The registry record does not report a protocol-defined estimand, missing-data method, sensitivity analysis, adjustment covariates, or the sponsor’s full statistical plan. These omissions prevent a full appraisal of whether the analysis followed its original plan or how robust the result is to alternative assumptions.

The comparison calculations are unadjusted recalculations from the posted summaries. The registry does not report an inferential analysis for the primary endpoint, and the secondary outcomes also have no reported analyses listed. The recalculated results are useful for describing the apparent contrast and its uncertainty, but they do not replace analyses using participant-level data and the trial’s intended crossover methods.

11. Confidence Intervals and Precision

The primary unadjusted mean difference is -0.06, with a confidence interval that includes zero. This interval is the key precision cue: the point estimate is close to zero, but the range of compatible values also extends in both directions. The estimate therefore does not pin down the size or direction of a comparative effect precisely enough to rule out meaningful alternatives.

Precision is distinct from the observed point estimate. A small estimate can be precise or imprecise depending on the width of its interval; an interval that crosses zero is not automatically evidence of no effect. Here, the reported standard deviations are 1.4 and 1.47, and the primary outcome summaries each include 16 participants. The registry record does not give a clinically important difference against which the interval could be judged.

The confidence interval is an unadjusted recalculation from the posted summary statistics. Its interpretation depends on the assumptions used to construct it. The registry record does not report a crossover-specific model or enough detail to assess whether the interval accounts for the relationship between observations from the same participant. The interval should therefore be understood as describing uncertainty in the unadjusted comparison, not as a complete analysis of every feature of the trial design.

The p-value of 0.906 is consistent with substantial uncertainty around the contrast, but it does not quantify the probability of no effect. Nor does it show that the treatments are equivalent. The registry record provides neither an equivalence margin nor a prespecified threshold for a clinically important difference. On the available information, the precision is insufficient to make a confident claim about the comparative size or practical importance of the primary outcome difference.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They are illustrative calculations based on the observed effect, not the trial’s original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry record does not report the trial’s own sample-size justification or original design assumptions.

The 80% power column describes the illustrative number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the chosen effect if that effect were the true effect and the model assumptions held. The 90% power column uses a higher target chance of detection, which requires more participants per arm for the same assumed effect. These are planning quantities for a hypothetical future design, not a measure of the probability that the completed trial found a true effect.

The planning rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power under the calculation assumptions. The figures should not be interpreted as a recommended design without considering the outcome, crossover structure, analysis plan, and a clinically meaningful target effect.

This is not observed power. It is a planning illustration based on the observed contrast and specified assumptions; it does not describe the probability that the completed study detected an effect.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.060; pooled standard deviation σ = 1.435.
2. n = 2 × (1.96 + 0.842)² × 1.435² / -0.060² = 8,984.6, rounded up to 8,985 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 <- -0.0600000000000001                      # observed difference in means
sigma <- 1.43542676580869                     # 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(2886286)
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 = 8,985 (80% power), 12,028 (90% power)
 75% of observed effect: n per arm = 15,973 (80% power), 21,383 (90% power)
 50% of observed effect: n per arm = 35,939 (80% power), 48,112 (90% power)
power.t.test: 8985.5 
Simulated power at n = 8,985 per arm: 0.797 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and several secondary outcomes, but the record does not report a multiplicity procedure, a hierarchy for testing outcomes, or an adjustment to the unadjusted comparisons. Multiplicity matters because testing several outcomes can increase the chance that at least one appears statistically notable by chance. Without a prespecified strategy, secondary p-values are best treated as exploratory rather than as confirmatory evidence.

The record identifies the primary analysis population as all participants who received each intervention. It does not report a detailed analysis population definition, an intention-to-treat approach, exclusions from the outcome summaries, or how participants who did not complete an intervention period were handled. Enrollment is listed as 17, while the primary arm summaries list 16 participants each; the registry record does not explain the relationship between these figures. The figures should not be combined or interpreted as evidence about the number of unique participants contributing data.

Missing-data handling is not reported in the registry record. It does not state whether diary entries were incomplete, whether any imputation was used, or whether sensitivity analyses assessed assumptions about missing outcomes. These details matter because missing outcomes can affect both the estimated contrast and its uncertainty, particularly if missingness is related to pain response or treatment experience.

The registry identifies a randomized crossover design but does not report the treatment sequence, period structure, washout details, or statistical method for handling repeated observations. It also does not report an interim-analysis plan or the trial’s full statistical analysis plan. These omissions limit assessment of analysis choices and of whether the reported summaries correspond to the intended primary analysis. They do not establish that any specific problem occurred; they identify information that is 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 registry reports zero serious adverse events in each intervention group. It lists 16 participants at risk for serious adverse events in each group. The record also lists 3 other, non-serious adverse events in each group, with 16 at risk in each. No deaths are reported in either group, and no top serious adverse event terms are listed.

These counts describe the registry’s reported safety summaries; they do not establish that no unrecorded events occurred. The record does not provide details about event types for the non-serious events, event timing, severity, relatedness to treatment, or how repeated events were counted. Because the design is crossover, the group summaries should not be read as independent parallel groups without further information on how exposure and events were assigned to each condition.

Zero reported serious adverse events is a descriptive finding in this record, not proof that serious events cannot occur. The safety information is limited, and the registry record does not report a detailed safety analysis or comparative inference.

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

The posted primary summaries show similar mean outcome values for the two intervention conditions: 1.87 with bupivacaine plus opioid and 1.81 with opioid alone. The unadjusted mean difference is -0.06, and its confidence interval includes zero. These data do not establish a clear difference in the measured pain-score change between the conditions.

That conclusion is not the same as saying the interventions are equivalent or that neither intervention changes pain. The study compares two bolus conditions, and the registry does not provide an untreated comparison. A difference from baseline or a comparison between conditions cannot by itself establish how either condition compares with no bolus or with usual care. The record also does not state a clinical threshold for an important score change, so statistical summaries alone cannot determine whether a possible difference would matter to patients.

The result is specific to the recorded endpoint and its stated timing: pain ratings before a Personal Therapy Manager bolus and the lowest rating within 30 minutes afterward. It does not directly answer longer-term pain control or establish effects on every secondary outcome. The registry lists functional status as part of the study purpose, but the primary endpoint is a pain rating. The secondary summaries do not remove uncertainty in the primary comparison.

Interpretation is constrained by enrollment of 17, the primary summaries listing 16 participants per intervention, and the absence of a reported crossover-specific analysis. The registry record does not explain the difference between enrollment and outcome counts, or how repeated observations and missing data were handled. It also does not report the original analysis plan, multiplicity approach, or a clinically meaningful threshold. Accordingly, the posted results are informative as descriptive summaries but do not support a definitive statement about comparative effectiveness or equivalence.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to analyze patient-reported outcomes in a crossover study. When participants receive more than one intervention, a comparison can potentially use each participant as their own reference. That opportunity depends on having clear information about treatment sequence, periods, carryover, and the analysis of within-participant observations. The registry identifies the crossover design but does not report those details or the analysis model.

The primary contrast illustrates why the estimate, its precision, and the design must be read together. The mean difference is small, but the confidence interval crosses zero and the p-value is 0.906. Neither the point estimate nor the p-value alone establishes equivalence. Without a prespecified clinically meaningful margin, the result cannot answer whether any plausible difference would matter in practice.

The record also illustrates the distinction between reported outcome summaries and a complete inferential analysis. Means and standard deviations describe the posted data, while a model and analysis plan would clarify how the randomized crossover structure, repeated measures, missing outcomes, and multiple endpoints were handled. Those methods are not reported in the registry record.

Finally, planning illustrations based on an observed effect can help show how uncertain estimates translate into future study requirements, but they are sensitive to the assumed effect and model. They are not the original trial’s design rationale and do not measure the completed study’s power. These issues make the trial a relevant example of why statistical interpretation depends on both numerical results and transparent reporting of design and analysis choices.

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 description leaves the exact construction of the change score unclear. Participants recorded pain just before a bolus and the lowest score within 30 minutes afterward, but the registry does not explain how multiple diary observations were combined or how the reported group value was derived. It also does not explicitly state whether positive change indicates improvement or worsening.

The registry describes a randomized crossover design but does not report sequence assignment, treatment-period length, washout, possible carryover, or period effects. The primary comparison available from the posted summaries is unadjusted and does not show whether within-participant information was used. This makes it difficult to judge whether the analysis matches the design.

The enrollment figure is 17, while the primary outcome summaries list 16 participants for each intervention. The registry record does not explain this difference or specify the participant-level relationship between the intervention summaries. Missing-data procedures, exclusions, and sensitivity analyses are also not reported.

The record does not state a clinically important difference for the pain scale, an equivalence margin, or the original sample-size justification. No multiplicity strategy is reported for the primary and secondary outcomes. The registry lists five secondary outcomes, but the posted secondary summaries cover only disability, patient global impression of change, and painDETECT; reported analyses are not listed for those summaries. These reporting gaps limit both clinical interpretation and assessment of the full analysis.

The safety record provides counts but little context about event type, timing, severity, relatedness, or event-counting methods. The available results should therefore be interpreted as a limited account of outcomes and safety, rather than a full evaluation of the trial’s design and conduct.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Patient Controlled Intrathecal Analgesia With Bupivacaine for Chronic Low Back Pain — NCT02886286.
• Registry record last updated 2022-03-24; status last verified 2022-02.
• Results first posted 2022-03-24.
• 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 Phase 4 randomized, double-blind, quadruple-masked crossover study compared intrathecal opioid boluses with and without bupivacaine for chronic intractable pain. The registry lists enrollment of 17, with a primary outcome of Numerical Rating Pain Scale change measured around a self-administered bolus. The outcome summaries list 16 participants per intervention.

The reported primary means are 1.87 for bupivacaine plus opioid and 1.81 for opioid alone. The unadjusted mean difference is -0.06, with a confidence interval spanning zero and an unadjusted p-value of 0.906. These summaries do not establish a clear difference or equivalence.

The registry record does not report a crossover-specific analysis, missing-data approach, multiplicity plan, clinically meaningful threshold, or original sample-size assumptions. Safety summaries list zero serious adverse events and no deaths in each intervention group, alongside 3 other adverse events per group. The findings are descriptive and should be interpreted in light of the limited analysis and reporting details.