Developing Brain Stimulation as a Treatment for Chronic Pain in Opiate Dependent: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Developing Brain Stimulation as a Treatment for Chronic Pain in Opiate Dependent (NCT03681769), a randomized early/phase 1 study. The primary outcome is Change in Quantitative Pain Testing Following Active TMS Compared to Baseline.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-group, early-phase study listed as completed. The registry records an enrollment of 24. The study start date is 2019-02-22 and the primary completion date is 2021-03-19. Medical University of South Carolina is listed as the sponsor. The conditions listed are chronic pain, opiate dependence, and lower back pain.

The study description presents brain stimulation as an approach to investigate pain responses and pain-related brain network activity in people with chronic pain and opiate dependence. It describes two aims involving rTMS: stimulation of the dlPFC and stimulation of the mPFC. The registered intervention list includes active and sham stimulation for each of those targets. However, the posted primary outcome arms are titled iTBS to the left dlPFC and iTBS to the motor cortex. The record does not explain the relationship between the planned intervention descriptions and the arm labels used for the posted results.

For the primary outcome, each posted arm has 11 participants in the summary. The analysis is described as a change from baseline to 16 weeks in quantitative pain testing, measured in degrees C. The secondary outcome is patient-reported pain and discomfort at 16 weeks, also posted for those two arms. A randomized design can support a comparison between assigned groups, but the posted summary alone does not describe adherence, deviations from assignment, or which analysis population was used.

The registry record does not report the original sample-size justification, the detailed randomization procedure, or the masking implementation for each arm. It also does not report a detailed statistical analysis plan or whether the primary endpoint and analysis changed during the study. Those omissions limit what can be inferred about the study’s planned analyses and the relationship between planned and posted results.

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 Change in Quantitative Pain Testing Following Active TMS Compared to Baseline, measured over Change from baseline to 16 weeks.

The primary endpoint is change in quantitative pain testing from baseline to 16 weeks, expressed in degrees C. The registry describes this as a thermal pain threshold assessment and says that investigators expected to examine whether treatment and time interacted in reported painfulness. In general, quantitative sensory testing uses a standardized stimulus to measure a response to a sensory challenge. A thermal threshold measure can provide a structured outcome that differs from a general retrospective report of pain, although it does not capture every aspect of a participant’s pain experience.

The posted results report mean change and standard deviation for each arm. The left dlPFC arm has a mean change of 1.4 degrees C, with a standard deviation of 0.3; the motor cortex arm has a mean change of 0.3 degrees C, with a standard deviation of 0.15. These summaries describe the outcome as recorded, but the registry record does not specify how to interpret a positive or negative change in clinical terms or whether a particular change is considered important.

The endpoint is relevant to the stated research question because it measures a response to thermal pain testing over the study period. It is not identical to pain in everyday life, and it should be considered alongside the separately posted patient-reported pain and discomfort outcome. The record does not report the measurement protocol in enough detail to assess the test’s reliability, the meaning of the scale’s full range, or how missing measurements were handled.

7. Results Posted in the Registry

• Intermittent Theta Burst Stimulation (iTBS) to the Motor Cortex: mean 0.30 versus 1.40 on control; difference -1.10 (95% CI -1.30 to -0.90), standardized effect d = -4.64; z-test p = <0.001.

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 in Patient Reported Pain and Discomfort

• 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:
  • Intermittent Theta Burst Stimulation (iTBS) to the Motor Cortex: mean 5.90 versus 5.30 on control; difference 0.60 (95% CI -1.25 to 2.45), standardized effect d = 0.27; z-test p = 0.524.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intermittent Theta Burst Stimulation (iTBS) to the Motor Cortex and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: patient-reported pain and discomfort at 16 weeks. It complements the primary quantitative thermal pain test by describing participants’ reported experience rather than a response in a standardized sensory test. The different measures address related but non-identical aspects of pain, so agreement or disagreement between them would not automatically make either measure invalid.

The secondary result does not provide a clear contrast between the two arms in the summary-based recalculation: its interval spans zero, and the sponsor’s two-sided t-test is also reported without evidence of a clear difference. This is not inconsistent with the primary arm summaries, because the endpoints measure different things and are analyzed using different methods. The registry does not report a prespecified hierarchy between primary and secondary outcomes or a rule for interpreting a pattern across them.

Secondary results generally carry less confirmatory weight when many outcomes or analyses are examined without a stated multiplicity procedure. Repeated testing increases the chance of observing an apparently notable result by chance, and an unadjusted p-value does not account for that. The registry record does not report multiplicity adjustment or a complete list of all analyses considered. The posted secondary finding should therefore be viewed as supportive descriptive information, not as an independent confirmation of the primary result.

The record also does not report a clinically important threshold for the patient-reported score, or sufficient details about its scale to interpret the size of a score difference. Its statistical uncertainty and practical meaning cannot be fully assessed from the posted result alone.

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

• Change in Patient Reported Pain and Discomfort

9. Statistical Interpretation

10. Statistical Methods Explained

The primary summaries are means and standard deviations for a continuous outcome. A mean describes the average observed change within an arm; the standard deviation describes the spread of individual observations around that average. These are descriptive summaries. They do not by themselves account for the study design, baseline values, repeated measurements, or any covariates that might be included in a model.

The simple recalculation compares the two arm means for change from baseline. In the posted contrast, the motor cortex arm is compared with the left dlPFC arm, producing a mean difference of -1.1 degrees C. The sign depends on the order of the groups in the contrast. A negative value in that ordering means the motor cortex group’s mean change is lower than the left dlPFC group’s mean change; it does not, without a defined direction of benefit, establish which change is better.

A standard error reflects uncertainty in an estimated quantity, taking account of sampling variability. Confidence intervals use the estimate and its uncertainty to describe a range of values compatible with the data under the method’s assumptions. They are not a range containing a guaranteed proportion of individual responses. The primary recalculated interval excludes zero, while the secondary recalculated interval spans zero. The confidence level for the recalculated intervals is not stated in the registry record, so it should not be assumed from the registry entries.

The unadjusted p-value addresses how compatible the observed contrast is with a null hypothesis of no difference under the assumptions of the recalculation. A small p-value does not measure the size or importance of an effect and does not give the probability that the null hypothesis is true. It also does not account for multiple outcomes or analyses unless a stated procedure does so. The registry record does not report an adjustment for multiplicity.

The sponsor-reported primary analysis is described as a mixed models analysis. In general, mixed models can account for correlated observations, such as repeated measurements from the same participant, and can model more than one source of variation. The registry record does not state the model’s fixed effects, random effects, covariance structure, analysis population, or missing-data assumptions. It also gives no model estimate or confidence interval. Those details are needed to understand precisely what the reported p-value tests.

The sponsor labels that result an equivalence analysis. In general, an equivalence analysis asks whether an estimated difference is sufficiently close to zero according to prespecified bounds. A p-value for an equivalence test cannot be interpreted in the same way as a conventional test for any difference. The equivalence margin, direction of testing, and decision rule are not reported in the registry record. Consequently, the reported p = .83 does not, on its own, show whether the groups met a defined equivalence criterion.

The sponsor’s secondary analysis is described as a two-sided t-test. In general, a two-sided test considers departures in either direction, rather than presuming that only one direction could be relevant. The simple recalculation gives an unadjusted p-value of 0.524, while the sponsor-reported value is .53. These are close as displayed, but the registry record does not state whether the sponsor’s test used precisely the same observations or handling of missing values as the recalculation.

Over-dispersion is a general concern when outcome variability exceeds what a model’s assumed distribution allows. If that occurs, standard errors can be too small and statistical tests can appear more certain than the data warrant. The posted primary outcome is continuous and is summarized with means and standard deviations; no over-dispersion assessment is reported. Therefore, the registry record does not support a claim that over-dispersion was present or that any correction was used.

The posted arms report 11 participants each for both outcomes. The enrollment figure and arm summaries do not establish whether all randomized participants contributed to every analysis, whether any measurements were missing, or whether an intention-to-treat population was used. The analysis population and missing-data approach are not reported in the registry record. These details matter because estimates can depend on which participants and measurements are included.

The recalculated comparisons are simple, unadjusted comparisons based on posted summaries. They are useful for describing what those summary statistics imply, but they are not a substitute for the sponsor’s full analysis. The primary sponsor result uses a mixed-model equivalence approach, whereas the recalculation compares posted change means. No discrepancy flag is recorded, but the methods differ and the registry record does not provide enough detail to reconcile them fully.

Why do the primary p-values differ in purpose?

A conventional difference test and an equivalence test address different questions. A conventional test asks whether evidence is inconsistent with no difference; an equivalence test asks whether the difference is contained within prespecified acceptable bounds. Since the registry record gives no equivalence margin or model estimate, the primary sponsor p-value should be reported as recorded rather than treated as a simple test of whether the groups differ.

What does the recalculation leave out?

The recalculation uses the arm-level means and variability rather than individual participant data. It cannot adjust for baseline outcome values, repeated measurements, covariates, or the study’s randomization structure beyond the posted summary comparison. It also does not correct for multiple outcomes. For these reasons, it is a descriptive statistical check and not a replacement for a prespecified analysis.

11. Confidence Intervals and Precision

The primary arm summaries are based on 11 participants in each group. The recalculated mean difference is -1.1 degrees C, and its interval excludes zero. This indicates that the interval under the recalculation’s assumptions is not compatible with a zero contrast. The registry record does not state the confidence level for this interval, and the interval should not be mistaken for the sponsor’s model-based interval: none is reported for the mixed-model analysis.

The reported standard deviations are 0.3 degrees C for the left dlPFC arm and 0.15 degrees C for the motor cortex arm. They describe observed spread within the posted summaries, not precision of the estimated difference. Precision of a group contrast also depends on sample size and the analysis method. The small arm summaries mean that the estimates should be interpreted as uncertain descriptions of this study, not as fixed values for other groups or settings.

For the secondary outcome, the recalculated mean difference is 0.6 points, with an interval from -1.246 to 2.446. Because this interval includes zero and values on either side, the summary is compatible with a range of possible between-group contrasts under the recalculation. The registry record does not give a threshold for meaningful differences on this score, so statistical uncertainty cannot be translated into a conclusion about practical importance.

Confidence intervals help show the range of estimates that the data and method permit; they do not address every source of uncertainty. In particular, the registry does not report missing-data handling, the full analysis population, or enough model detail to assess the sponsor’s primary estimate. The interval from a summary-based recalculation should therefore be kept distinct from uncertainty under the sponsor’s mixed model.

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 planning figures are participants per arm, not total events. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the stated fraction of the observed effect as the effect to detect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect is real and the assumptions hold. The 90% power column gives the corresponding estimate for a higher chance of detection. These are planning targets, not guarantees. For the primary outcome, planning for 100% of the observed effect gives 1 participant per arm for 80% power and 1 for 90% power; planning for 75% gives 2 per arm for either target; planning for 50% gives 3 per arm for 80% and 4 per arm for 90%.

For the secondary outcome, planning for 100% of the observed effect gives 213 participants per arm for 80% power and 285 per arm for 90% power. Planning for 75% gives 379 and 507 participants per arm, respectively; planning for 50% gives 852 and 1,140 participants per arm, respectively. Smaller effects need more participants to detect under otherwise unchanged assumptions. This is not observed power: it is a planning illustration calculated from the observed effect, not a measure of the study’s achieved ability to detect an effect.

These projections can be unstable when they are based on an effect estimated from a small study, particularly when the observed effect is large. They also do not incorporate design features that are not listed in the planning assumptions. They should be read as conditional illustrations rather than as a reconstruction of the trial’s original design.

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 = -1.100; pooled standard deviation σ = 0.237.
2. n = 2 × (1.96 + 0.842)² × 0.237² / -1.100² = 0.7, rounded up to 1 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 <- -1.1                      # observed difference in means
sigma <- 0.237170824512628                     # 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(3681769)
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 = 1 (80% power), 1 (90% power)
 75% of observed effect: n per arm = 2 (80% power), 2 (90% power)
 50% of observed effect: n per arm = 3 (80% power), 4 (90% power)
power.t.test: 2.2 
Simulated power at n = 1 per arm: NA (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a mixed models analysis labelled equivalence, with p = .83. No model estimate, confidence interval, or equivalence margin is posted. Because the result is specifically labelled as an equivalence analysis, its p-value should not be treated as interchangeable with a conventional test for a difference. The information needed to determine whether the sponsor concluded equivalence is not reported in the registry record.

The simple recalculation from posted means gives a mean difference of -1.1 degrees C and an unadjusted p-value of <0.001. It is an unadjusted comparison of the posted change summaries, not a reproduction of the sponsor’s mixed model. The registry record does not explain why the results differ in form or how the mixed model handled measurements, baseline values, or other design features. The discrepancy indicator is false, but the available information is still insufficient to reconcile the distinct analyses.

For the secondary outcome, the sponsor reports a two-sided t-test p-value of .53, while the unadjusted recalculation gives 0.524. The sponsor analysis is the trial’s reported analysis; the recalculation is a summary-based check. Neither should be presented as if it were the other, and the primary sponsor p-value does not resolve the missing equivalence margin or estimate.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and one secondary endpoint, and it reports two analyses. It does not report whether additional outcomes, time points, subgroups, or analytical approaches were examined. Nor does it state whether the primary and secondary tests were placed in a prespecified hierarchy or whether any adjustment for multiple testing was planned. If multiple hypotheses are tested, the chance of at least one false-positive finding can increase; in general, multiplicity procedures are used to control that risk. No such procedure is reported in the registry record.

The primary outcome is described as a change from baseline to 16 weeks, and the sponsor analysis is labelled mixed models equivalence. The record does not provide the statistical analysis plan, the model specification, the equivalence margin, or a confidence interval for that analysis. It also does not say whether any interim analyses were conducted. These details are not reported in the registry record and should not be inferred from the posted p-value.

Missing-data handling and analysis populations are also not reported. The registry does not state whether all randomized participants were included in the analysis, whether the analysis followed assigned treatment, how missing outcomes were handled, or whether participants were excluded after randomization. The arm-level summaries do not answer those questions. In general, missingness can affect an estimate when the likelihood of an outcome being missing is related to the outcome or to treatment assignment.

The record does not report baseline outcome values by arm or an adjusted treatment estimate. It therefore cannot establish whether the change comparison was adjusted for baseline measurements. Details such as protocol deviations, treatment adherence, and the handling of any repeated observations are likewise not reported. These omissions constrain assessment of the analysis and its robustness, but they do not show that any particular problem occurred.

16. 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.

The posted adverse-event summaries list 11 participants at risk in each of the two reported arms. Each arm has zero serious adverse events, zero other adverse events, and zero deaths in the registry summary. No serious adverse-event terms are listed.

These figures describe the events recorded in the posted summaries. A zero count is not proof that an event cannot occur, and it does not establish that the groups have identical safety profiles. The record does not provide event definitions, exposure time, detailed monitoring methods, or information about events outside the reported categories. The adverse-event summary also covers the two arms named in the outcome results, not every active or sham intervention listed elsewhere in the registry. The counts should therefore be interpreted as a limited report of events in this study, not as a general safety estimate.

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

The posted data describe a completed randomized study comparing two stimulation arms in people with chronic pain and opiate dependence. For the primary quantitative pain-testing outcome, the arm means differ in the posted change summaries, and a simple unadjusted recalculation produces a contrast whose interval excludes zero. Separately, the sponsor reports a mixed-model equivalence analysis with p = .83. Since the registry gives no equivalence margin, estimate, or interval for that analysis, its result cannot be translated into a claim that the groups were equivalent or different.

The secondary patient-reported outcome does not show a clear between-arm contrast in the posted summary-based analysis. It measures a different aspect of pain from the quantitative thermal test, so the two endpoints need not produce identical patterns. Neither outcome establishes a threshold for meaningful benefit, and the record does not provide enough detail to judge whether the observed changes are important to participants.

These results do not show how either arm compares with sham stimulation, because sham arms are not included in the posted outcome summaries. They also do not establish that a stimulation approach reduces reliance on opiates: the posted endpoints concern quantitative pain testing and patient-reported pain and discomfort, not opioid use or dependence outcomes. The registry description gives broader aims, but the posted results do not answer all of those aims.

Small arm summaries, missing details about the analysis population and missing data, and the unresolved difference between the primary sponsor analysis and the simple recalculation all limit certainty. The results are best understood as findings from the specific comparisons and outcomes posted, not as a basis for treatment recommendations or broad conclusions about people outside the study.

18. Why This Trial Matters Statistically

Statistically, this study illustrates why the choice of endpoint and analysis matters. The primary outcome is a quantitative change measure, while the secondary outcome is a participant-reported score. They can capture related but different experiences, and conclusions should not be transferred from one measure to the other without a stated rationale.

The primary result also shows why a reported model-based analysis should be distinguished from a simple recalculation of arm summaries. The sponsor labels its analysis as mixed-model equivalence, while the summary-based recalculation compares mean changes. Those approaches answer different questions or may rely on different assumptions. Without the model estimate, equivalence margin, and analysis details, a reader cannot fully connect the two results.

The registry’s intervention descriptions and posted outcome arm labels do not align clearly: the registered list includes active and sham dlPFC and mPFC stimulation, whereas the posted comparison names left dlPFC and motor cortex iTBS. This limits the scope of conclusions that can be drawn about the planned active-versus-sham and target-specific questions.

Finally, the planning illustrations show how strongly projected sample sizes depend on the assumed effect size. Smaller effects require more participants under the listed assumptions. Such planning calculations can help frame future study design, but estimates based on observed effects from a small study can be unstable and are not evidence of achieved power. The registry record does not report the original sample-size rationale, leaving the relationship between enrollment and the investigators’ initial design assumptions unclear.

19. 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.

Several limitations are specific to the information in this registry record. First, the intervention descriptions and posted results use different arm labels. The listed interventions include active and sham stimulation to the dlPFC and mPFC, while the posted results compare left dlPFC iTBS with motor cortex iTBS. The record does not explain this difference, so the posted comparison should not be treated as a reported active-versus-sham test or as a complete report of the listed interventions.

Second, the primary sponsor analysis is described as a mixed-model equivalence analysis, but the record gives only its p-value. It does not report the equivalence margin, model estimate, confidence interval, model specification, or analysis population. This prevents a full interpretation of the sponsor’s primary result and makes it difficult to reconcile with the unadjusted recalculation from posted summaries.

Third, the record does not report the original sample-size justification, missing-data approach, participant flow, adherence, or the handling of protocol deviations. These details are important for judging the precision and potential biases of a randomized comparison. Their absence is a reporting limitation, not evidence that any particular issue occurred.

Finally, the outcomes posted do not include a sham comparison, opioid-use outcome, or a reported threshold for clinically meaningful change. The primary endpoint is a quantitative thermal test, and the secondary endpoint is patient-reported pain and discomfort. Conclusions must remain limited to these posted measures and comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Developing Brain Stimulation as a Treatment for Chronic Pain in Opiate Dependent — NCT03681769.
• Registry record last updated 2023-02-10; status last verified 2023-01.
• Results first posted 2023-02-10.
• 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.

23. Record Summary

NCT03681769 is listed as a completed, randomized, quadruple-masked, parallel-group, early-phase study sponsored by Medical University of South Carolina. The registry records an enrollment of 24, with a start date of 2019-02-22 and primary completion date of 2021-03-19. The study concerns chronic pain and opiate dependence.

The primary endpoint is change in quantitative pain testing from baseline to 16 weeks. Posted summaries compare left dlPFC iTBS with motor cortex iTBS. The sponsor reports a mixed-model equivalence analysis with p = .83; a separate unadjusted recalculation from the arm summaries gives a mean difference of -1.1 degrees C and p < 0.001. The registry does not report the equivalence margin or enough model detail to reconcile these analyses.

One secondary endpoint reports patient pain and discomfort at 16 weeks. The adverse-event summaries list zero serious events, zero other events, and zero deaths in each posted arm. The record does not report the original sample-size justification, missing-data procedures, or a multiplicity plan.