Efficacy and Safety of Lymphdiaral Basistropfen (HDC) in the Treatment of Chronic Low-back Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Lymphdiaral Basistropfen (HDC) in the Treatment of Chronic Low-back Pain (NCT01049373), a randomized phase 3 study. The primary outcome is Change in FFbH-R Between Screening and Week 15.

2. Clinical Question

3. Trial Design

The registry record describes a completed Phase 3, randomized, parallel-group, placebo-controlled study. Its official title identifies it as single-centre; the registry does not report the centre's name. The listed enrollment is 221. The study summary describes a 15-week treatment period, with primary outcome measurement between screening and week 15.

The study is categorized as quadruple-masked in the registry record, while its official title calls it double blind. The specific people or roles covered by masking, and how masking was maintained, are not reported in the registry record. Random allocation is recorded, but the sequence-generation and allocation-concealment methods are not reported.

The treatment groups were Lymphdiaral Basistropfen (HDC) and placebo solution. The placebo description specifies 10 drops t.i.d. For 15 weeks. The HDC arm description lists 10 drops t.i.d. but ends before giving its duration. The study summary identifies the treatment period as 15 weeks, but further regimen details are not reported in the registry record.

The primary outcome summaries use 103 participants in the HDC group and 89 in the placebo group, and the primary outcome population is labelled ITT. These group counts should not be treated as a complete account of participant flow: enrollment, analyzed outcome counts, and adverse-event risk groups are separate registry entries. Reasons for differences among those entries, withdrawals, adherence, and the handling of missing observations are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: screening visit (up to one week before baseline)

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT

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 FFbH-R Between Screening and Week 15, measured over between screening and 15 weeks treatment.

The primary endpoint was change in the Hannover Functional Questionnaire, FFbH-R, between screening and week 15. The record describes it as a patient questionnaire with 12 questions about limitations in activities of daily living. It characterizes the measure as intended for assessing functional impairment associated with back pain in everyday life.

The scale ranges from 0, the worst score, to 100, the best score. A positive change therefore indicates movement toward a higher, better-functioning score. The reported mean change was 8.8 units in the HDC group and 4.1 units in the placebo group. The recalculated difference in mean change was 4.7 units in favor of HDC, with a 95% confidence interval from 0.399 to 9.001.

Function is relevant to the study's stated focus on chronic low-back pain because it captures reported limitations in ordinary activities rather than pain intensity alone. The record does not report a threshold for a clinically important FFbH-R change, so the size of the estimated difference cannot be translated into a registry-defined level of meaningful benefit. The endpoint is a patient-reported measure; details about questionnaire completion procedures are not reported in the registry record.

7. Results Posted in the Registry

• Lymphdiaral Basistropfen (HDC): mean 8.80 versus 4.10 on control; difference 4.70 (95% CI 0.40 to 9.00), standardized effect d = 0.31; z-test p = 0.032.

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 FFbH-R Between Screening and 2 Weeks

• 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:
  • Lymphdiaral Basistropfen (HDC): mean 3.90 versus 0.60 on control; difference 3.30 (95% CI -0.32 to 6.92), standardized effect d = 0.26; z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lymphdiaral Basistropfen (HDC) and the control. The interval gives the range of effects that remain compatible with the data.

Change in Pain Score (SES), Subscale "Sensoric Pain"

• 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:
  • LYMPHDIARAL (HDC): mean -4.20 versus -1.80 on control; difference -2.40 (95% CI -4.27 to -0.53), standardized effect d = -0.36; z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LYMPHDIARAL (HDC) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary measures covering early functional change, pain scores, state of health, and Oswestry score. It records 15 secondary outcomes, while detailed numerical summaries and comparisons are available for only some of those entries. The listed outcomes include repeated entries for some measures. Their breadth means the secondary findings address several related but distinct aspects of the study rather than a single additional confirmatory question.

The detailed early FFbH-R comparison does not provide the same degree of statistical evidence as the primary result under its reported test. The detailed sensoric-pain comparison has a different direction of numeric change and a reported rank-test p-value of 0.046. These secondary results are not a uniform pattern that can be treated as an independent replication of the primary functional outcome. Their interpretation also depends on the scale and timing of each measure.

In general, when many outcomes or analyses are examined, some results may appear noteworthy by chance even if no adjustment is made. The registry record does not report a multiplicity-control procedure or identify a hierarchy for secondary outcomes. The secondary comparisons should therefore carry less weight than the designated primary endpoint, especially where results are selective, incomplete, or not supported by a stated analysis plan. Their role is to provide context about other measured domains, not to override the primary analysis or establish a separate treatment conclusion.

The registry also does not report numerical results for every listed secondary outcome in the information available in the record. Absence of a posted estimate is not evidence that an outcome had no effect; it means that its result cannot be evaluated from the registry record. No further direction, magnitude, or significance should be inferred for those outcomes.

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

• Change in FFbH-R Between Screening and 2 Weeks
• Change in Pain Score (SES), Subscale "Sensoric Pain"
• Change in Pain Score (SES), Subscale "Sensoric Pain"
• Change in Strength of Pain (Visual Analog Scale VAS)
• Change in Strength of Pain (Visual Analog Scale VAS)
• Change in State of Health (BF-S)
• Change in State of Health (BF-S)
• Change in Oswestry Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a numeric change score on the FFbH-R scale. The registry reports group means and standard deviations. A mean describes the average observed change within a group; a standard deviation describes how spread out individual observations are around that group's mean. These summaries make a mean difference interpretable in the scale's own units.

What does the mean difference represent?

The recalculated contrast is the HDC group's mean change minus the placebo group's mean change. The posted mean changes are 8.8 and 4.1 units, and the recalculated mean difference is 4.7 units. Since higher FFbH-R scores indicate better function, a positive difference points toward a larger average improvement in the HDC group. This is a comparison of group averages, not a statement about each participant's response.

Why is the registry's test different from the recalculation?

The registry reports a Wilcoxon (Mann-Whitney) analysis for the primary comparison. This is a rank-based method: in general, it compares the ordering of observations between groups rather than directly testing a difference in means. The recalculated result instead uses the posted summary statistics to estimate a mean difference and its uncertainty. The two procedures answer related but not identical statistical questions, so their p-values need not match. The registry's reported p-value is 0.043; the recalculated unadjusted p-value is 0.032. The sponsor's own analysis takes precedence.

In general, rank-based methods can be useful when an analysis is based on the ordering of observations rather than a model centered on means. Their interpretation is not automatically a difference in medians; that would require additional assumptions about the distributions. Distributional details and the rationale for choosing the reported test are not reported in the registry record.

What does the confidence interval add?

The recalculated 95% confidence interval for the mean difference is 0.399 to 9.001 units. In general, a confidence interval expresses the precision of an estimate under the assumptions of the method: a narrower interval indicates greater precision, while a wider one leaves more possible values compatible with the data and method. It is not a range containing a fixed proportion of individual participant outcomes, nor does it assign a probability to the true effect after the data have been observed.

The interval is calculated for the mean contrast, not the rank-based test. Its lower and upper limits are both above zero, but that does not establish clinical importance. The record does not report an FFbH-R threshold for a clinically important difference. The interval also does not account for unreported uncertainties such as missing-data handling or possible departures from the recalculation's assumptions.

Why can over-dispersion matter?

In general, over-dispersion means that observations vary more than a statistical model expects. When a model assumes less variability than is actually present, standard errors may be too small and intervals may be too narrow. The primary outcome is continuous and its group standard deviations are reported, but the registry does not describe an over-dispersion model or a model-based adjustment. Over-dispersion is therefore a general statistical consideration, not a reported feature established for this analysis.

The recalculation is an unadjusted comparison based on posted group summaries. It does not reproduce the participant-level rank analysis, adjust for covariates, or incorporate a reported missing-data model. The registry identifies the primary analysis population as ITT, but its detailed definition and implementation are not reported. Interpretation should keep the distinction between the sponsor's reported test and the separate summary-statistic recalculation clear.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 4.7 FFbH-R units, with a 95% confidence interval from 0.399 to 9.001. The point estimate is expressed in the scale's units, and the interval communicates uncertainty around that average contrast under the recalculation's method. Because the interval extends from close to zero to a larger positive difference, it allows a range of plausible magnitudes rather than identifying one exact effect.

In general, a confidence interval is a measure of statistical precision, not a measure of clinical importance. A narrow interval would constrain the range more tightly; a broad interval would leave greater uncertainty. The reported interval lies above zero, but the registry record does not state what FFbH-R difference would be important to patients. It is therefore not possible to classify the full range as clinically meaningful or unimportant using a registry-defined threshold.

This interval belongs to the recalculated comparison of means. The registry's reported primary analysis is a Wilcoxon (Mann-Whitney) test with p = 0.043, and no confidence interval for that rank-based result is reported in the registry record. The recalculated interval should not be attributed to the sponsor's test.

The interval also does not address every source of uncertainty. It is based on the posted summary statistics and does not resolve the unreported details of missing observations, outcome analysis implementation, or participant flow. Its precision is consequently best understood as precision for the stated unadjusted mean comparison, not as a complete measure of uncertainty about all aspects of the study.

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 illustrations are stated as participants per arm for this continuous outcome, not as total events. They use the observed mean difference as a reference and show hypothetical requirements for detecting the full observed effect, 75% of that effect, or 50% of that effect. For the full observed effect, the illustrations give 163 participants per arm for 80% power and 219 participants per arm for 90% power. For planning for 75% of the observed effect, they give 290 participants per arm for 80% power and 388 participants per arm for 90% power. For planning for 50% of the observed effect, they give 652 participants per arm for 80% power and 873 participants per arm for 90% power.

The stated 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 the stated fraction of the observed effect. In plain terms, the 80% column represents a hypothetical design with an 80% chance of detecting the specified effect under those assumptions if it were present; the 90% column represents a higher target chance. Smaller effects require more participants per arm to detect at the same power target.

These are planning illustrations, not observed power and not evidence about the original study's design. The original sample-size justification and design assumptions are not reported in the registry record. The illustrations use the observed effect as their reference, so they should not be interpreted as proof that the observed estimate is the true effect or as a forecast of a future study's result.

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 = 4.700; pooled standard deviation σ = 15.140.
2. n = 2 × (1.96 + 0.842)² × 15.140² / 4.700² = 162.9, rounded up to 163 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 <- 4.7                      # observed difference in means
sigma <- 15.1396864321279                     # 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(1049373)
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 = 163 (80% power), 219 (90% power)
 75% of observed effect: n per arm = 290 (80% power), 388 (90% power)
 50% of observed effect: n per arm = 652 (80% power), 873 (90% power)
power.t.test: 163.8 
Simulated power at n = 163 per arm: 0.795 (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's own primary analysis is a Wilcoxon (Mann-Whitney) comparison, with p = 0.043. The recalculated comparison uses the posted means and standard deviations and gives a mean difference of 4.7 units, a 95% confidence interval from 0.399 to 9.001, and an unadjusted p-value of 0.032. The recalculation is a simple summary-statistic analysis, not a reproduction of the sponsor's rank-based test.

The two p-values differ because the procedures use different information and test different statistical contrasts. A rank-based analysis uses the ordering of participant observations; the recalculation estimates a difference in group means. The registry record marks no discrepancy. Accordingly, the sponsor's own analysis takes precedence for describing the trial's reported statistical result, while the recalculated mean difference and interval offer a separate view of the posted summaries.

The registry does not report a confidence interval for the sponsor's rank-based comparison. The recalculated interval should not be presented as though it accompanied that test. Neither p-value alone describes effect size or clinical importance, and the record does not provide a threshold for meaningful change on the FFbH-R scale.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes and analyses. It reports 16 outcome measures and 4 analyses overall, and 15 secondary outcomes are posted. Examining multiple endpoints can increase the chance that at least one result appears unusual by chance. In general, multiplicity procedures address this issue by controlling how evidence is evaluated across a family of tests or by defining a prespecified testing order.

A multiplicity adjustment, a prespecified hierarchy among secondary endpoints, and the status of secondary analyses as confirmatory or exploratory are not reported in the registry record. The primary result can be read as the designated main comparison, while the unadjusted secondary findings should be interpreted cautiously and should not be treated as a collection of independent confirmations.

The primary analysis population is labelled ITT. The precise definition of that population, the handling of participants without an endpoint measurement, and the methods used for missing data are not reported in the registry record. Participant flow, reasons for missing observations, and sensitivity analyses addressing missingness are also not reported. These omissions make it difficult to assess whether the posted outcome summaries represent all randomized participants as intended by the ITT label.

The registry does not report whether interim analyses were conducted, what stopping rules may have applied, or whether the reported analysis followed a prespecified statistical plan. The original sample-size assumptions and justification are not reported either. These are distinct uncertainties: the planning illustration uses stated hypothetical assumptions, but it does not reveal how the trial itself was designed or analyzed. No particular interim procedure, missing-data method, or multiplicity strategy can be inferred from the record.

16. 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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: intervertebral disc protrusion (1.8%), musculosskeletal pain (0.9%), neoplasm malignant (0.9%), knee operation (0.9%), intestinal operation (0.9%).

The serious adverse event entries give 6 affected participants among 112 at risk in the HDC group and 7 among 109 at risk in the placebo group. These are the registry's participant counts for serious adverse events; they are not calculated rates or a complete assessment of the types, timing, duration, or severity of every event.

The record lists serious-event terms including intervertebral disc protrusion at 1.8%, and musculosskeletal pain, neoplasm malignant, knee operation, intestinal operation, and post herpetic neuralgia at 0.9% each. The registry does not provide further case-level context for these entries in the information recorded. Death counts are not reported in the registry record.

Adverse-event counts alone do not establish whether an event was caused by treatment. The registry record does not provide enough detail to assess event relatedness, exposure duration, or differences in underlying risk. The serious-event entries should be read as descriptive safety reporting, not as proof of safety or harm.

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

The primary result describes an average change in back-related functional limitation over the study's treatment period. The HDC group had a higher mean FFbH-R change than the placebo group, and the recalculated mean difference was 4.7 units. The reported rank-based analysis also gives p = 0.043. These results are evidence about the measured comparison in this trial, not a general conclusion about all people with chronic low-back pain or all possible uses of the remedy.

The direction of the primary mean contrast favors HDC on a scale where higher scores represent better function. The confidence interval for the recalculated mean difference runs from 0.399 to 9.001, illustrating that the estimate is uncertain in magnitude. The record does not specify a clinically important FFbH-R threshold, so statistical evidence cannot be translated into a registry-defined judgment about the practical importance of the change.

The result does not show that every participant improved, that the groups differed in every secondary outcome, or that any observed change was caused solely by the assigned intervention. Randomization supports a comparative design, but important implementation details and missing-data methods are not reported. The secondary findings involve multiple outcomes and lack a reported multiplicity procedure, so they are less conclusive than the primary comparison.

The study's safety entries are descriptive and do not establish causation or rule out uncommon harms. The registry record also does not report long-term outcomes, so the results cannot establish whether differences persist beyond the recorded treatment period. No medical recommendation follows from these statistics; clinical decisions require evidence and context beyond the registry's posted results.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint, analysis method, and effect estimate need to be read together. The primary outcome is a patient-reported functional measure with an interpretable scale direction: higher scores indicate better function. The mean contrast gives an estimate in FFbH-R units, while the registry's rank-based analysis supplies the sponsor-reported test result. Keeping those statistical targets distinct avoids treating two related but different analyses as though they were identical.

The example also shows the value of precision estimates. A p-value alone does not indicate the range of plausible effect magnitudes. The recalculated confidence interval conveys uncertainty around the mean difference, while the absence of a registry-defined clinically important threshold leaves practical importance unresolved. Statistical evidence, precision, and clinical meaning are related but separate considerations.

Finally, the record makes visible common limits of registry-based interpretation: incomplete reporting of analysis plans, missing-data handling, multiplicity, and participant flow. Multiple secondary outcomes can broaden the clinical picture, but without a reported strategy for interpreting them they offer weaker confirmation. Safety counts likewise require context before causal conclusions are drawn. These distinctions help readers assess what the trial's posted results support without extending the findings beyond the evidence recorded.

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.

The registry record gives limited detail on trial conduct and analysis. Although it identifies randomization and masking, it does not describe sequence generation, allocation concealment, the people masked, or how masking was maintained. The official title calls the study double blind, while the registry classification is quadruple masking; the difference is not explained in the registry record.

The HDC arm description ends before specifying treatment duration, while the study summary describes a 15-week treatment period. The detailed HDC composition is recorded, but the incomplete regimen description limits reconstruction of the assigned intervention from the record alone. The site is identified as single-centre in the official title, but its name and setting details are not reported.

The primary outcome is labelled ITT, but the record does not define the analysis population, explain why the primary summaries use the posted group counts, or describe missing-data methods. It does not provide participant flow, adherence, or sensitivity analyses. The original sample-size justification, multiplicity strategy, and statistical analysis plan are also not reported. Consequently, the robustness of the posted results and the prespecification of secondary analyses cannot be fully assessed.

The primary recalculation is based on summary statistics and is not the same as the reported rank-based test. A clinical-importance threshold for FFbH-R change is not reported. Secondary outcome detail is incomplete, and the safety entries do not include enough case-level context to assess causation. These limitations constrain interpretation of both the magnitude and broader meaning of the findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Lymphdiaral Basistropfen (HDC) in the Treatment of Chronic Low-back Pain — NCT01049373.
• Registry record last updated 2012-09-06; status last verified 2012-06.
• Results first posted 2012-09-06.
• 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

NCT01049373 is a completed, randomized, parallel-group, placebo-controlled Phase 3 study of Lymphdiaral Basistropfen (HDC) for chronic low-back pain. The official title describes a single-centre study, and the registry classifies masking as quadruple. The study summary describes treatment over 15 weeks.

The primary endpoint was change in FFbH-R between screening and week 15. Mean change was 8.8 units with HDC and 4.1 units with placebo. The registry reports a Wilcoxon (Mann-Whitney) p-value of 0.043; the unadjusted recalculation estimates a mean difference of 4.7 units, with a 95% confidence interval from 0.399 to 9.001. Clinical importance, missing-data handling, and the original sample-size justification are not reported in the registry record.