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70 Jacqueline YAP, Tony GIN
treatments, side effects of the treatment and
patient preferences.
In summary, the NNT is a very useful summary
measure because its interpretation is clinically
intuitive. However, one should be aware that NNTs
are tools which need to be used wisely.
Application of evidenced-based
medicine in pain medicine
In pain medicine, factors that have driven the use
of EBM include the:
• Presence of marked variations in management
in clinical practice
• Increasing cost of health care due to the rapid
development of new medical technology.
On the other hand, factors that have hindered the
application of EBM are the:
• Relative paucity of randomised controlled
trials in pain management
• Extensive spread of pain literature across
medical and surgical subspecialties and basic
science.
Issues to be considered when implementing
EBM
Individual baseline risk.- the effect of an intervention
may vary because patients do not share the same
morbidity or risk. For any given measurement of
treatment effectiveness, patients at higher risk will
generally experience greater levels of absolute risk
reduction or impact from a treatment.
reshold for implementation. – the evidence
of effectiveness alone does not imply that
an intervention should be accepted. e
implementation of an intervention depends on
whether the benefit is sufficiently large relative to
the risks and costs, and other issues such as equity
and willingness to take risks. ese differences
explain the variations in decisions made when the
same evidence is presented to different people.
One approach to the decision about whether
an intervention should be implemented is to
determine a threshold above which treatment
would be offered. is threshold might be expressed
in terms of cost effectiveness ratios that define the
cost of achieving a unit of benefit below which an
intervention is seen as worth implementing. When
evaluating the evidence, different decision makers
will use different criteria to prioritise treatments
for implementation. Policymakers may emphasise
societal gains in health and efficiency, while
clinicians may consider the well-being of their
patients to be most important.
Knowledge gaps - one should bear in mind that
the existence of knowledge gaps between medical
science and medical practice in pain medicine has
made the application of EBM in this field difficult.
In practice, this void is filled by “clinical judgment”
and “clinical experience”. In such situations,
clinicians should not only utilise available EBM
tools but also analyse resources from patients
(e.g. pain diaries) thus accommodating treatment
according to the patient.
Epistemological considerations - finally, the degree
to which clinicians adopt good quality research
into practice will be influenced by the extent
to whether the results conflict with their own
professional experience and beliefs. is reflects an
epistemological mismatch between the evidence
that researchers produce and the evidence that
practising clinicians value [6, 28].
Clinical Trials in Pain
Research
General principles
e single most important step in designing a trial
is to clearly and specifically define the research
question to be answered. is may seem relatively
straight forward, but challenges may influence
the trial design (e.g. requirement for very large
sample size or ethical concerns). e second step
in designing a trial is to clearly specify the primary
outcome to be assessed. After that, it should be
logical to determine the appropriate measurement
tools and methods of analysis. e primary outcome
measure should be specified before the data are
collected or analysed because otherwise there is
the risk that the methodology will be inadequate
and the results insufficient to answer the question
posed.
Randomisation
Randomisation aims to reduce the effect of
confounding variables and to eliminate selection
bias in trials. When randomisation is implemented
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Biostatistics in Pain Medicine 71
correctly and when sufficient numbers of
participants are enrolled, the distributions of all
potential confounding variables are likely to be
equal across groups. True randomisation requires
both a valid means of generating random assignment
and a mechanism to preserve the integrity of
random assignment. In a systematic review on
the effectiveness of transcutaneous electrical nerve
stimulation (TENS) in acute postoperative pain
by Carroll and colleagues [7], 17 studies were
regarded as randomised controlled trials in acute
postoperative pain. e authors concluded from
these randomised trials that there was no benefit
of TENS compared with placebo. Of the excluded
trials, 19 were not randomised controlled trials and
among these trials, it was concluded that TENS had
a positive analgesic effect. is review showed that
non-randomised studies overestimated treatment
effects.
Control group
Placebo controlled trials
A placebo is an inactive substance or treatment.
e placebo effect is defined as the “response of a
subject to a substance or to any procedure known
to be without any therapeutic effect for the specific
condition being treated” [5]. ough the extent of
the placebo effect has been questioned, it appears
to be real and of large magnitude in studies of pain
[21]. e placebo effect is conventionally assessed
by using placebo controlled trials. However, recent
literature has suggested an alternative approach
using hidden and open administration of study
treatment, which has the advantage of assessing
the placebo effect in studies without placebo
conditions in addition to providing information on
the magnitude of the placebo effect [2, 33].
Benets of placebo control
• Allows the specific efficacy of the new
intervention to be distinguished from the
placebo effect. e magnitude of the non-
specific effect in a study can be estimated by
the mean (or median) response in the placebo
control group. Assuming a simple additive
model of treatment effects, the placebo group
response can be subtracted from the response
of the active treatment group to estimate the
specific efficacy of the active intervention.
• Allows double-blinding in a trial, thereby
avoiding biases that might occur if patients or
investigators knew who was receiving which
treatment. For example, it would have been
impossible to blind participants or evaluators
if one group received a treatment and the
other did not. Bias is more likely to occur in
trials using no-treatment controls than those
using placebo controls.
Limitations of placebo control
• Placebo controlled trials do not always answer
a clinically relevant question. Practising
clinicians, who have several analgesics available
to be used clinically, may not want to know
whether another analgesic works better than
nothing, but rather, how the new analgesic
compares with existing standards of care.
• Ethical issues related to placebo controls
remain unanswered. Although a placebo
control has been considered to be appropriate
in situations where patients have failed all
standard treatment, it is difficult to justify the
chronic administration of a placebo in pain
syndromes that generally respond to a known
therapy. In this situation, an investigator
may consider giving both placebo and active
treatment groups access to a standard analgesic
“rescue” dose. Here, the “rescue” analgesic
then becomes another important outcome
measure. e other alternative may be to give
both placebo and active treatment as an add-
on treatment where all patients are already
on optimal doses of standard treatment. e
ethics of placebo controlled trials is further
discussed in Chapter 7.
No-treatment controlled trials
ere are two primary situations in which it may be
important to include a control group of participants
who receive no intervention.
• When it is critical to determine the overall
efficacy of a new treatment, but there are
practical and/or ethical problems with using
a placebo or sham control.
• When the goal of a trial is to assess the
magnitude of a placebo effect. To measure
the placebo effect properly requires the
comparison of patients receiving placebo with
those receiving no treatment at all. Here, the
placebo response needs to be distinguished
from the effects of regression to the mean.
Regression to the mean classically occurs
in medical conditions with fluctuating
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72 Jacqueline YAP, Tony GIN
symptoms. In this situation, subjects who have
enrolled in a clinical trial when their disease is
in a worse period will have a natural tendency
to improve during the progression of the trial.
e inclusion of a “no-treatment group” in
addition to a placebo group may differentiate
the placebo response from regression to the
mean. e improvement in the no-treatment
group may then be attributed to regression to
the mean, and the additional improvement in
the placebo group is the placebo response.
Non-inferiority and equivalence trials
Given the ethical concerns about placebo controlled
trials and the inability of no-treatment groups to
maintain blinding, investigators may decide to
show that a new drug is either “no worse than” (a
non-inferiority trial) or “as good as” (an equivalence
trial) a treatment that is commonly accepted as
effective. ese trials are standard in evaluating
medications for conditions where the risks of
placebo assignment are widely regarded as too great
(e.g. thrombolytic agents for acute myocardial
infarction). However, these trials are presently
not considered as standard in pain management
because the risks of temporarily forgoing the active
treatment are not as obvious. In addition, there are
potential problems with interpreting such studies:
• Demonstrating no significant differences
between two analgesics does not prove that
they are equivalent. ese trials require much
larger sample sizes, because equivalence
or non-inferiority must be documented
within relatively narrow margins. e lack
of significant differences may be a result of
inadequate power if the sample size is too
small.
• Demonstrating that two treatments are the
same does not show either of them worked.
ese trials assume that the standard therapy
would have been superior to placebo had a
placebo arm been included.
Participant selection
ere are two conflicting priorities in the selection
of participants. Ensuring homogeneity among
participants in a trial permits greater confidence
that the observed outcomes are a result of the
treatment and limits the variability that might
obscure the results. is approach increases
the internal validity of the study, but limits the
generalisability of the results. On the other hand,
enrolling a heterogeneous group of subjects is more
likely to reflect all those who could potentially
benefit from the intervention and allows detection
of potential variations in a treatment’s efficacy
among higher and lower risk patients. e external
validity or generalisability of the study will be
increased. However, this approach can substantially
increase the sample required to ensure that the trial
has adequate statistical power.
Blinding
A goal of clinical trials is to design the experiment
such that any observed changes in outcome are
caused specifically by the treatment being studied.
Moore has shown that studies in medicine can be
biased as a result of the structure of a trial [31]. For
example, non-randomised and unblinded studies
overestimated treatment effects by 40% and 17%
respectively. Blinding may be single (participant
blinded) or double (investigator and participant
blinded). Double blinding is preferable.
Participant blinding
Participants in all groups must believe they are
getting the real treatment. If the control group
believes they are getting the placebo treatment,
which may be a less effective intervention, the
trial may spuriously reveal a benefit in the active
treatment group. Participant blinding may be
difficult to maintain where there is an obvious
treatment effect or side effect. In addition to
creating appropriate placebos, investigators should
validate that the blinding was preserved by asking
participants the treatment they believe they
received. If the blinding was successful, this result
should be consistent with random allocation.
Investigator blinding
Blinding of outcome assessors is critical to minimise
the chance that evaluators will more favourably rate
those known to be receiving the active treatment,
impart different levels of enthusiasm, or prescribe
different co-interventions to patients in different
groups.
Sample size
e statistical power of a trial is the probability of
detecting a treatment difference when one truly
exists. Researchers traditionally consider a study
to be adequately powered if it has at least an 80%
chance of detecting an effect when one exists (i.e.
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Biostatistics in Pain Medicine 73
beta or type II error ≤ 0.2). However, one should
be aware that this value is arbitrary. In practice, the
power of a trial is decided by considering both the
sample size that can reasonably be enrolled, and
the relative importance of limiting false negative
conclusions (type II error) versus false positive
conclusions (type I error).
ere are various methods to work out the
sample size for different study designs and these
may involve formulae, sample size tables [26],
and computer programs such as PASS [19].
An alternative approach to presenting sample
size considerations is to calculate the size of the
effect that would need to be present to produce
a statistically significant outcome. Although this
approach is not recommended, it remains in
common use. For example, Cohen’s d Effect Size
is often used for sample size calculation, but one
should be aware that this is a poor substitute for the
investigator who avoids committing to an estimate
of the clinically important difference that should be
detected between interventions.
An often used standard formula for sample size
calculation for comparison of two means is:
N =
σ
2
ƒ(
α
,
β
)
Δ
2
where N = number of patients in each
treatment group
σ
= standard deviation of the primary
outcome measure
ƒ(
α
,
β
) = alpha and beta error
Δ = difference to be detected between
treatment effects
Investigators usually accept the conventional
α
and
β
errors, thus the main influence that they have
over sample size is their choice of Δ. Hopefully, the
treatment effect will be at least as large as Δ. In
addition, it is important to minimise all errors that
may increase the
σ
2
or variance of the treatment
effect in the study. A large variance will make it
more difficult to detect a difference, even if one
truly exists.
Increasing the likelihood of detecting the
dierence between treatment eects
e investigator has to decide the minimum
difference that he or she would like to detect. A
larger minimum difference requires a smaller
sample size. is may be achieved by maximising
the dose, intensity of treatment or baseline risk of
subjects.
Decreasing the variability in outcome
measurement
An improvement in the precision of an outcome
measurement will allow a reduction in sample size.
For example, Jensen & McFarland have suggested
that the variation in pain intensity over the course of
a week may introduce a large amount of variability
[23]. It was shown that this error can be decreased
by averaging daily pain measures over a week.
Adjusting for covariates with signicant
eects on the primary outcome
If one is aware of the covariates or confounding
variables that have significant effects on the
outcome, it is advisable to exclude these variables
from the study. If it is not possible to do so, then
these variables will need to be adjusted using
statistical techniques such as regression analysis.
Study designs
Some investigators have suggested crossover designs,
enriched enrolment designs, and n-of 1 designs to
increase power and reduce sample size. However,
these designs have their respective disadvantages
inherent to the architecture and requirements of
the trial design [27].
Outcome measurement
Measures of pain can be unidimensional or
multidimensional. Unidimensional measures of
pain include pain relief scales such as the visual
analogue scale, categorical scale and numerical
rating scale. Multidimensional measures (e.g.
McGill Pain Questionnaire) provide additional
information about the characteristics of the pain
and its impact.
Most measures of pain are based on subjective
self-report. Self-report measures can be influenced
by a variety of factors such as mood and sleep
disturbance. Multiple outcome measures are
required to adequately capture the complexity of
the pain experience and how it can be modified by
pain management interventions. Although there
are no objective measures of pain, associated factors
such as hyperalgesia (e.g. mechanical withdrawal
threshold) or functional impairment (e.g.
ambulation) may provide additional information.
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74 Jacqueline YAP, Tony GIN
Analgesic requirement is also commonly used as a
surrogate measure of pain.
So, how do we evaluate pain, and what is considered
a successful or non-successful outcome, bearing in
mind that pain is a multidimensional subjective
phenomenon? In 2003, under the auspices of the
Initiative on Methods, Measurement, and Pain
Assessment in Clinical Trials (IMMPACT), specialists
from academia, governmental agencies and the
pharmaceutical industry participated in a consensus
meeting and identified core outcome domains that
should be considered by investigators in chronic
pain clinical trials (Table 6.02) [39]. Investigators are
recommended to assess outcomes representing six
core domains as shown in the table below.
is landmark guideline was followed by further
recommendations by IMMPACT on the core
outcome measures for chronic pain trials (Table
6.03) [12]. Criteria used to assess potential
outcome measures include the appropriateness
of the measure’s content and conceptual model,
reliability, validity, responsiveness, acceptability,
feasibility, availability, equivalence of different
methods of administration, and translations for
different cultures and languages.
It is important to acknowledge that wide disagreement
exists on the choice of the best outcome measure.
e recommendations by IMMPACT are meant
to be outcome measurements to be considered in
chronic pain clinical trials. ese recommendations
are not meant to be a compulsory requirement for
publication in scientific journals or to imply that
positive outcomes for all these outcome measures
must be obtained to judge if a treatment is effective.
Some of the dispute can be explained by the
differences in the questions that are being studied
and the data that can be practically collected. Please
refer to the next main section for further discussion
regarding the statistical requirements of outcome
measurement tools in pain studies and Chapter 4
for further information on pain evaluation.
Analysis
Different analytic approaches may be possible
depending on the type of data available, the trial
structure and the different questions that need to
be answered. Specific statistical tests and analyses
are readily covered in statistical textbooks and
will not be discussed in detail in this chapter.
However, there are some concepts in relation to the
interpretation of the results that are essential, and
these will be discussed below.
Table 6.02 Core outcome domains in chronic pain
trials [39]
• Pain
• Physical functioning
• Emotional functioning
• Participants’ ratings of improvement and
satisfaction with treatment
• Symptoms and adverse events
• Participant disposition (e.g. adherence to the
treatment regimen and reasons for premature
withdrawal from the trial).
Copyright permission granted from Copyright Clearance
Center’s Rightslink/Elsevier Limited.
Table 6.03 Core outcome measures in chronic pain
trials [12]
• Pain:
11-point (0–10) numerical rating scale of pain
intensity
Categorical rating of pain intensity (none,
mild, moderate, severe) in circumstances in
which numerical ratings may be problematic
Use of rescue analgesics
• Physical functioning (either one of two
measures):
Multidimensional Pain Inventory Interference
Scale
Brief Pain Inventory interference items
• Emotional functioning (at least one of two
measures):
Beck Depression Inventory
Profile of Mood States
• Participant ratings of global improvement and
satisfaction with treatment:
Patient Global Impression of Change
• Symptoms and adverse events:
Passive capture of spontaneously reported
adverse events and symptoms and use of open-
ended prompts
• Participant disposition:
Detailed information regarding participant
recruitment and progress through the trial,
including all information specified in the
CONSORT guidelines [30].
Copyright permission granted from Copyright Clearance
Center’s Rightslink/Elsevier Limited.
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Biostatistics in Pain Medicine 75
Statistical signicance versus Clinical
signicance
e p-value indicates the probability of obtaining a
value for the test statistic at least as extreme as the
one observed, assuming that the null hypothesis
is true. A p-value of 0.05 is conventionally used
to signify statistical significance. is convention
implies that one has a 5% chance of incorrectly
rejecting the null hypothesis. It is important to be
aware that a number of factors can contribute to a
statistical significance. One could get a statistically
“significant” result when the effect is very large
(despite having only a small sample) or if the sample
is very large (even if the actual effect is small). As the
sample size increases, the test statistic necessary to
achieve a conventional level of statistical significance
decreases. For example, if there are 30 subjects in
a study, a Pearson correlation coefficient of 0.10
may not be statistically significant. However, if the
sample size is 200, a Pearson correlation of 0.10
could be statistically significant at p <0.001.
e traditional method of reporting p-values to
quantify the significance of a result is gradually
being replaced by methods to present the range
of plausible results that are compatible with the
data. e most common method for presenting
a summary measure of effect is to report a point
estimate of the effect, along with a 95% confidence
interval around this estimate. Confidence intervals
can be easily calculated for most point estimates and
statistical programs will usually provide these [1].
e classical interpretation of a (95)% confidence
interval is that if we take repeated samples and
recalculate the confidence interval each time,
(95)% of these calculated intervals will contain
the true population parameter that we are trying
to estimate. However, a common interpretation is
that a 95% confidence interval for an estimate is the
range of values within which one believes with 95%
probability that the true population value lies.
Practically, the confidence interval can be used
to provide the same information derived from
the p-value, i.e. the statistical significance. An
x% confidence interval that includes the value
of no difference (0 for difference, 1 for ratios)
indicates that the treatment under investigation
is not statistically significantly different from the
control at a p-value of (100-x)%. If it does not
contain the value of no difference then the findings
are statistically significant. Confidence intervals
also aid the interpretation of clinical trial data by
putting upper and lower bounds on the likely size
of any true effect. is helps to interpret borderline
significance and non-significance. Finally, the
width of the confidence intervals can assist in
determining the uncertainty of the result — the
narrower the interval, the more precise the estimate
of the true effect.
It is important to acknowledge that statistical
significance and clinical significance are not
necessarily equivalent. It is the magnitude of effect
that determines the clinical significance, not the
presence of statistical significance. One strategy
in evaluating the size of treatment effect is to
calculate the “Effect Size” (ES). e ES measures
the magnitude of the difference between groups,
controlling for the variation within the groups; and
can be thought of as standardised differences. e
ES may simply be the difference between the mean
values of the two groups divided by the standard
deviation (Cohen’s d Effect Size) [10], but different
approaches to calculate the ES are available.
In other words, although a p-value denotes
whether the difference between the two groups is
likely to occur solely by chance, the ES quantifies
the amount of difference between the two groups.
Quantification of the size of the effect does not
depend on the sample size but on the strength of
the intervention. However, one should not solely
interpret the magnitude of change or ES as an
indication of a “clinically important difference”.
A small ES may still be a clinically important
difference and vice versa, depending on what is being
studied. Indeed, there is a growing recognition that
traditional methods such as statistical significance
tests and effect sizes should be supplemented by
methods for determining the clinically important
difference [20].
e determination of a clinically important
difference plays a key role in the interpretation
of pain studies since an improvement in outcome
measures does not necessarily lead to improved
function and patient satisfaction. Reporting
outcomes in this way provides information that can
be readily translated into improved patient care.
Despite disagreements on how to establish a
clinically important difference, it is accepted
that it should be based on standards provided by
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76 Jacqueline YAP, Tony GIN
clinicians and patients. Two methods to establish
the external validity are by “expert opinion” by
practising clinicians and the patient’s assessment
of how changes in symptom scales correspond to
global questions. For example, two reports that have
investigated the clinically important difference for
the measurement of pain have demonstrated that a
33% change in the pain intensity score is considered
clinically important by patients [13, 14].
Presentation of results
e hypothesis should be clearly stated with a careful
description of the randomisation and blinding
procedure. All randomised participants should be
accounted for, and an intention-to-treat analysis of
all participants is typically appropriate even when
some participants drop out early or never received
their assigned intervention. It is often informative
to also report the number of patients that declined
to enter the trial. Brief descriptions of the rationale
behind the choice of measurement tool and
analytical strategies are useful. e results from any
subgroup analysis should not be considered as the
primary result but rather as the basis for hypothesis
testing on future studies. Recommendations to
improve the quality of reporting in randomised
controlled trials are provided by the Consolidated
Standards of Reporting Trials (CONSORT)
guidelines [30].
Limitations of randomised
controlled trials
Although large randomised controlled trials are
considered as the study design providing the best
evidence in EBM, many important questions may
not be answered because of ethical or practical
limitations. ere are several other issues potentially
limiting the design and conduct of randomised
controlled trials in pain research. ese include,
but are not limited to the following below.
Selective enrolment
Clinical trials can only provide information
specific to the population from which the study
participants were drawn even when properly
designed and carefully conducted. Selective
enrolment may alter the conclusion of a trial if
differences between those who enrol and those
who do not are related to outcome. For example,
patients whose pain is well managed on currently
available analgesics may be less willing to participate
in a trial than those whose pain remains difficult
to treat. Patients who have not responded well to
treatment may also be less likely to respond to a
new drug. Hence, the selective enrolment of these
patients may reduce the observed efficacy of the
new analgesic drug.
Poor compliance
It is not uncommon for patients with chronic pain
to not comply with their prescribed treatment
regimens in clinical settings. is problem may be
exacerbated in randomised controlled trials because
some participants will receive a treatment they
would not have chosen if given the opportunity.
A large number of non-compliance and dropouts
may bias the results of a trial. Although intention-
to-treat analysis may mitigate this bias, if non-
compliance or dropouts are substantially higher in
one group than the other, such analysis may prevent
the detection of a true effect from the treatment.
If the problem is significant, then per protocol
analysis should be done in addition to intention-
to-treat analysis, participant non-compliance and
dropouts reported in detail and results interpreted
with caution.
Measurement tools
e reliability, validity and sensitivity of some of
the currently available instruments to measure
pain and other health-related outcomes may not
be optimal to detect small to moderate changes
in the patient’s clinical condition. Moreover, the
availability of measurement tools may also be
limited in certain conditions, e.g. limited validated
translated measurement tools for quality of life.
Outcome Measurement and
Questionnaires in Studies of
Pain
ere is no single measurement tool that is
universally applicable, or preferable in pain
medicine. e decision on which instrument is most
appropriate for a given clinical situation should be
guided by considerations such as the question the
trial is attempting to answer, the amount of change
to be detected and the ability of the chosen scale to
detect such a change. Regardless of the instrument
chosen, it should be characterised by three features:
reliability, validity and responsiveness. e textbooks
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Biostatistics in Pain Medicine 77
on the statistical analysis of multivariate statistics
by Stevens [36] and Tabachnich [38] can provide a
more in-depth discussion of the statistical analysis.
Reliability
e result should be reproducible if the instrument
is used repetitively in the same person without any
change in the person’s condition.
Test-retest reliability
is tests the stability of the instrument with
repeated administrations, assuming that the
outcome being assessed is stable over time. is
may be true for many characteristics, but pain does
not necessarily remain stable. Hence, the test-retest
reliability may be of limited value as an estimate
of the reliability of pain scales. e exceptions are
scales that assess average pain over a period of time
because these would be expected to have greater
stability than measures of current pain. Reliability
coefficients for analysing the test-retest reliability
traditionally utilise the Pearson correlation
coefficient or the Spearman rho. However, these
coefficients are limited estimates of reliability. e
Intraclass Correlation Coefficient (ICC) is the
preferred index, as it reflects both correlation and
agreement. An acceptable reliability level is set at
ICC values above 0.90. If the data are nominal,
then percent agreement may be obtained and the
kappa statistic applied. Recommendations for the
interpretation of kappa (
κ
) values for the strength
of agreement are
κ
≤0.20 (poor), 0.21≥
κ
≤0.40
(fair), 0.41 ≤
κ
≤0.60 (moderate), 0.61≤
κ
≤0.80
(good), 0.81≤
κ
≤1.00 (excellent).
Rater reliability
ere are two forms of rater reliability: the intra-
rater reliability (stability of data recorded by
one individual across two or more periods of
measurement) and the inter-rater reliability (the
variation between two or more raters who measure
the same group of subjects). e ICC can be used
to evaluate rater reliability.
Alternate forms
Many instruments exist in two or more versions,
called equivalent or alternate forms. Interchange
of these forms can be supported by establishing
their parallel reliability based on their statistical
equivalence. Correlation coefficients have been
used most commonly to assess equivalence. e
determination of limits of agreement is also a useful
estimate of the range of error expected when using
two different versions of an instrument.
Internal consistency
e internal consistency reflects the extent to
which items measure various aspects of the same
characteristic. e Cronbach’s coefficient alpha is
most often used as the reliability coefficient. is
statistic evaluates the items in a scale to determine if
they are measuring the same construct or if they are
redundant, suggesting which items can be discarded
to improve homogeneity of scale. Cronbach’s alphas
that are 0.90 or greater are usually accepted as
evidence of excellent internal consistency. Values
between 0.70 and 0.90 suggest that the scale has
adequate internal consistency, while values less than
0.70 do not have adequate internal consistency. e
item-to-total correlation allows one to examine how
each item on the scale relates to the instrument as
a whole. ese correlations will be very high if the
instrument is homogenous.
Validity
e validity is the extent to which an instrument
measures what it is supposed to measure.
Content validity
e content validity indicates that the items that
make up an instrument adequately sample the
universe of content that defines the variable being
measured. For example, pain intensity is better
measured if it includes ratings of current, least, worst
and average pain. e content validity is assessed
by using an expert panel to provide judgements on
the items in an instrument.
Criterion validity
e criterion validity indicates that the outcome of
an instrument conforms to a known gold standard.
It can be tested as concurrent or predictive validity.
e concurrent validity shows how well a measure
correlates with other well-validated tests of the
same parameter. e predictive validity is defined
as how well an instrument can forecast some future
criterion.
Construct validity
e construct validity establishes the degree
to which an instrument measures an abstract
construct and reflects theoretical components
of the construct. For example, the construct
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78 Jacqueline YAP, Tony GIN
of catastrophising in pain is reflected in the
Pain Catastrophizing Scale as consisting of
three domains: rumination, magnification and
helplessness [37]. e construct validity can
be measured by a variety of methods such as
the known groups method, convergence and
discrimination analysis, and factor analysis.
Responsiveness
Responsiveness can be defined as the ability of an
instrument to detect minimal clinically important
changes [17]. An instrument which shows a
relatively small change in score while the patient
improves dramatically is poorly responsive. On the
other hand, if the instrument shows some change
while the clinical improvement is small, then
the instrument is regarded as highly responsive.
To detect change over time, a tool must be both
reliable (consistent response when no change
has occurred) and responsive to clinical change
(when change has occurred). Instruments which
are more responsive provide greater study power,
thereby allowing a study to be completed with
fewer subjects. erefore, investigators should
use measures that are sensitive to the type of
condition and clinical change under investigation.
For example, disease specific measures are
generally more sensitive to the disorder under
consideration, and therefore more likely to
reflect clinical changes. Responsiveness may be
analysed by using statistical significance testing
to demonstrate that the instrument was able to
distinguish between the two groups, measuring the
effect size and comparing ROC curves (a graphical
representation of the balance between sensitivity
and specificity) [32] to determine which measure
would be preferred for detecting change.
Issues in outcome measurement
for clinical trials in pain research
Sensitivity of pain scales in chronic pain
studies
e relative sensitivity of several common pain
scales have been well studied in single-dose analgesic
trials in acute pain, but there are few comparative
data on the sensitivity of pain scales in repeated
dose analgesic trials. Until these comparisons are
done, choices of pain scales can only be empirical.
A potential problem with pain scales is that as time
passes, patients may not be able to remember the
baseline level of pain. In addition, visual analogue
scales or numerical rating scales are rather abstract
and may confuse the elderly patient. Verbal category
scales of pain intensity suffer from neither of these
problems, but may contain too few categories to
detect a modest but clinically meaningful level of
pain reduction.
Mechanism based pain assessment
Pain may comprise a number of components
with different mechanisms. Clinical practice and
scientific understanding may be improved if the
relevant components of pain are measured in
isolation, in addition to the measure of pain relief.
For example, there may be a mixture of neuropathic
and nociceptive pain in a chronic pain condition
that requires different pain measurement scales.
One may also include the assessment of different
pain components with different evoking stimuli,
qualities or temporal profiles [40].
Health-related quality of life measures
Another concern in pain medicine research is that
a change in pain may only be one component of
the overall quality of life. Symptomatic reports
of pain may be surrogate markers for changes in
the broader outcome of quality of life. Conversely,
assessing changes in quality of life may be
insufficient because they cannot specifically mean
changes in pain. Investigators need to measure
both the level of pain and the overall quality of life
if they wish to know an intervention’s overall effect.
For example, if an analgesic agent relieves pain but
produces substantial side effects, the patient may
not consider its use to be advantageous from the
perspective of their quality of life.
Conclusion
In this chapter, several fundamental considerations in
evidence-based medicine and clinical trials have been
covered. Randomised controlled trials and systematic
reviews remain the best available means of evaluating
and summarising pain interventions. However,
readers should be mindful of the many difficulties in
extrapolating the results obtained in a trial setting to
actual interventions in clinical practice.
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Biostatistics in Pain Medicine 79
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