THE JOURNAL OF ALTERNATIVE AND COMPLEMENTARY MEDICINE
Volume 11, Number 2, 2005, pp. 333–342
© Mary Ann Liebert, Inc.
Bias Control in Trials of Bodywork: A Review of
WOLF E. MEHLING, M.D., ZELDA DIBLASI, Ph.D., and FREDERICK HECHT, M.D.
Objective: To review and summarize the methodological challenges in clinical trials of bodywork or hands-
on mind–body therapies such as Feldenkraïs Method, Alexander Technique, Trager Work, Eutony, Body Aware-
ness Therapy, Breath Therapy, and Rolfing, and to discuss ways these challenges can be addressed.
Design: Review and commentary.
Methods: Search of databases PubMed and EMBASE and screening of bibliographies. Published clinical
studies were included if they used individual hands-on approaches and a focus on body awareness, and were
not based on technical devices.
Results: Of the 53 studies identified, 20 fulfilled inclusion criteria. No studies blinded subject to the treat-
ment being given, but 5 used an alternative treatment and blinded participants to differential investigator ex-
pectations of efficacy. No study used a credible placebo intervention. No studies reported measures of patient
expectations. Patient expectations have been measured in studies of other modalities but not of hands-on
mind–body therapies. Options are presented for minimizing investigator and therapist bias and bias from dif-
ferential patient expectations, and for maintaining some control for nonspecific treatment effects. Practical is-
sues with recruitment and attrition resulting from volunteer bias are addressed.
Conclusions: Rigorous clinical trials of hands-on complementary and alternative therapy interventions are
scarce, needed, and feasible. Difficulties with blinding, placebo, and recruitment can be systematically addressed
by various methods that minimize the respective biases. The methods suggested here may enhance the rigor of
further explanatory trials.
Work, Eutony, Body Awareness Therapy, Breath Therapy,
and Rolfing are used with a wide spectrum of diagnoses
(Anonymous, 2003; Mehling, 2001). These therapies aim to
enhance body awareness using touch, movement, and a
mind–body approach. Fuller integration of these therapies
into medical care (Frenkel and Borkan, 2003) will depend
on better evidence demonstrating that they are effective. De-
odywork or hands-on mind–body therapies such as
Feldenkraïs Method, Alexander Technique, Trager
spite many anecdotal reports of their utility, two systematic
reviews of trials of Feldenkrais and Alexander Technique
revealed insufficient research data for supporting “strong
conclusions” for the efficacy of these therapies (Ernst and
Canter, 2003; Ives and Sosnoff, 2000).
While quasiexperimental outcomes research (Riley and
Berman, 2002; Walach et al., 2002) and other study designs,
such as qualitative research, are also needed (Lewith et al.,
2002), randomized controlled trials (RCT) remain the gold
standard for evaluating the efficacy of complementary ther-
apies (Berman and Straus, 2004; Harlan, 2001; Levin et al.,
Osher Center for Integrative Medicine, University of California San Francisco, San Francisco, CA.
1997; Long, 2002; Miller et al., 2004; Vickers et al., 1997).
Randomized, controlled trials of these treatments, however,
face particular challenges similar to those encountered in tri-
als of spinal manipulation, physical therapy (PT), and mas-
sage (Breen, 2002; Field, 2002). These challenges markedly
differ from those of conventional drug therapies and have
been previously summarized (Berman and Straus, 2004;
Carter, 2003; Cawley, 1997; Ernst, 2003; Hart, 2003; Long,
2002; Mason et al., 2002; Redwood, 2002; Richardson,
2000; Smith, 2004). However, with rare exceptions (Field,
2002), little guidance is available for researchers in this field
about how to address these methodological challenges.
The history of trial methodology is the history of con-
trolling bias (Chalmers, 2001; Smith, 2004). Patients’ ex-
pectations and preferences for complementary methods have
a major influence on the benefits of these therapies and can
introduce bias into outcome measures (Kalauokalani et al.,
2001). If we cannot blind the patient, we lose our ability to
equalize patients’ expectations across study treatment arms.
Randomization and allocation concealment attempt to equal-
ize patient characteristics across study arms. However, it
cannot control for bias from differences in expectations to-
ward two different unblinded interventions.
This report identifies the best quantitative studies in the
field of bodywork and reviews, illustrates, and discusses
three challenging topics: blinding, choice of control group,
and recruitment. Within each topic, we briefly reflect on the
goals for which the current research guidelines were estab-
lished, review whether and how these were applied, and dis-
cuss possible solutions.
We searched the PubMed and EMBASE databases up to
September 2004 using the following search terms:
Feldenkrais, Alexander technique, Trager, Eutony, Breath
Therapy, Breathing Exercises, Rolfing. Bibliographies and
the Feldenkrais Research Archive (Psychology Department
of the University of Utah, 2004) were screened for addi-
tional studies. Because RCTs are scarce, we included stud-
ies that met the following criteria for methodological qual-
ity and study characteristics:
1. Clinical study on patients with established medical diag-
2. Quantitative data preintervention and postintervention
3. Intervention included individual hands-on approach (i.e.,
not based on technical devices or verbal guidance only)
and focused awareness (going beyond plain massage or
4. Outcome measures had to be understandable within the
frame of conventional medical science;
5. Publication in peer-reviewed journals.
Studies of Reiki, qigong, or other energy manipulations
were not included in this review because these therapies are
conceptually different, do not require direct touch, or are
done in groups only.
We identified 40 studies in PubMed and EMBASE and
13 additional studies from bibliographies. Of those 53 stud-
ies, a total of 20 fulfilled our criteria. Table 1 presents an
overview of the methods used in these studies.
In controlled trials, the purpose of blinding is to reduce
ascertainment or observer biases by keeping the various par-
ties involved in the study blind to the participants’ group as-
signment (Schulz et al., 2002). This bias is present when the
assessment of outcomes is systematically influenced by
knowledge of which intervention a participant receives. This
knowledge is associated with expectations that might differ
for the allocated treatments (Crow et al., 1999). Blinding ap-
plies to one or several of the following: study participant,
therapist, outcome evaluator, investigator, and data analyst.
Blinding the patient. The purpose of blinding the patient
is to control for differential patient expectations and bias in
self-report outcome rating (Pocock, 1983). Patient blinding
can occur to different degrees with rather different effects:
1. Masking the interventions the participants undergo will
equalize bias from patient expectations.
2. Blinding the participant to which intervention the inves-
tigator expects to work better may reduce bias introduced
by investigator’s influence on patient expectations, but
may not equalize participant expectations between un-
The first type of blinding probably is impossible in stud-
ies of bodywork because of their sensory nature (Deyo,
1988) and was never attempted in the reviewed studies.
The second type of blinding depends in part on the way
information about the study interventions is framed during
informed consent, when participants’ knowledge and ex-
pectations around the interventions are largely shaped
(Bergmann, et al., 1994). An example of this is consenting
to behavioral therapy versus Feldenkrais for premenstrual
syndrome without revealing that Feldenkrais is not expected
to help this condition (Kirkby, 1994). If patients can suc-
cessfully be blinded to which treatment the investigator sees
as potentially effective, allocation concealment has the pur-
pose of equalizing patient expectations without deceiving
the participants. This is not possible in hands-on studies with
a no-intervention control arm or a control intervention that
MEHLING ET AL.
BODYWORK AND BIAS CONTROL
TABLE 1. DESIGN DETAILS OF CLINICAL TRIALSaOF HANDS-ON BODYWORK THERAPY
Number of studies
conditions treatedControl groups
Laumer et al. (1997)
Joynson et al. (1999)
Lundblad et al. (1999)
Smith et al. (2001)
Stephens et al. (2001)
Loewe et al. (2002)
Malmgren-Olsson et al.b
1) CBT, 2) NT (waitlist)
same multimodal program, but no FM
sham bodywork, same provider in both groups
1) PT, 2) NT (waitlist)
audiotape narrataive (‘story’)
1) progressive muscle relaxation, 2) NT
1) BAT, 2) PT
Stallibrass et al. (2002)
Elkayam et al. (1996) 
1) massage, 2) NT
none (limited historic control)
Loew et al. (1996a)
1) placebo relaxation, 2) MDI: patients are
their own controls on 2 following days.
MDI: patients are their own control on the
same exercise training, but no BT
Loew et al. (1996b) Asthma
van Dixhoorn et al.
Loew et al. (2000)
Loew et al. (2001)
1) placebo relaxation, 2) MDI: patients are
their own controls on 2 following days.
relaxation technique including auto-
suggestions, visualization, progressive
relaxation, and group discussions
Manocha et al. (2002)Asthma
Body Awareness Therapy
Engel et al. (2000)
Grahn et al. (2000)
primary care, standard care as outpatients
Haugli et al. (2001)
standard care only
1) FM, 2) PT
aIf a single trial generated multiple reports, only one report is quoted.
bThis study fits into two fields as one method is control for the other.
cWe know of at least one unpublished 3-arm randomized controlled trial (RCT) on low-back pain patients (Little, Great Britain).
dThe term “breath therapy” or “breath exercises” is relatively broad and includes a wide variety of Western and Eastern approaches
from diverse conceptual backgrounds. We found numerous studies assessing the health implications of influencing breathing patterns
by using technical devices (biofeedback, video instructions, music, mouthpiece) thus providing well standardized interventions and valu-
able data on the clinical importance of various breathing patterns and their manipulation by physiologic elements of breath therapy.
However, for the purpose of this review, these did not add to the discussion of methodological issues in hands-on bodywork research
and did not meet our inclusion criteria.
eWe found 2 RCTs on healthy volunteers only.
FM, Feldenkrais; BAT, Body Awareness Therapy; BT, Breath Therapy; PT, physical therapy; CBT, cognitive–behavioral therapy;
NT, no-treatment; MDI, metered-dose inhaler; LBP, low-back pain; MI, myocardial infarction.
was explained as being not effective during informed con-
Four studies reported single blinding for study partici-
pants. In these studies, at least one control group received
an intervention that was presented as being an alternative
effective method providing comparable benefits, although it
was clearly seen as placebo by the investigator: placebo–re-
laxation versus Breath Therapy for asthma (Loew et al.,
1996a, 2001), true relaxation versus Breath Therapy for
asthma (Manocha et al., 2002), and Feldenkrais versus cog-
nitive–behavioral therapy for premenstrual syndrome
(Kirkby et al., 1994). Participants were kept uninformed
about the other interventions and the investigators’ hy-
potheses were not disclosed.
In a fifth study (Loew et al., 1996b) reporting patient
blinding, participants received two different relaxation in-
structions, Breath Therapy or a placebo relaxation instruc-
tion, crossing over on consecutive days. Again, participants
expected two active interventions and were deceived about
one intervention that was used as sham. However, in this
study each participant experienced both interventions and
could reach conclusions rendering blinding ineffective.
Although the sensory characteristics of hands-on inter-
ventions likely invalidate blinding in a crossover design
(Deyo, 1988), this was used in four studies (Loew et al.,
1996a, 1996b, 2001; Johnson et al., 1999). No data were
provided as to whether participants or therapists had simi-
lar expectations of the two treatments.
Blinding the therapist. None of the reviewed studies
blinded the therapists. The purpose of blinding the therapist
is to control for conscious or unconscious influences on the
participant, which could modify the intervention’s effect
(Schulz et al., 2002). It is obvious that in interventions that
are hands-on and provide guidance for awareness or move-
ment exercises the therapists cannot be blind to the treat-
ment they are delivering. Therapist blinding has been at-
tempted in massage research by providing massage with
versus without pressure. Presumably, the therapists were not
informed that pressure-free massage was a sham (Diego et
al., 2004; Field, 2002). Apart from this being a questionable
assumption (Cassileth and Vickers, 2004), therapists apply-
ing pressure-free massage are almost certain to believe they
are delivering suboptimal treatment. Even this limited de-
gree of blinding is not possible in studies involving a guided
Blinding of outcome assessment. The purpose of blind-
ing study personnel who are evaluating outcome measures
is to avoid conscious or unconscious biasing of the out-
comes’ assessment. This is particularly important if the out-
come measures are vulnerable to unconscious manipulation
by unblinded assessors (Schulz et al., 2002). An indepen-
dent person whose only role is to perform outcome mea-
sures can be kept blinded to the group assignment. Thirteen
(13) of the reviewed studies used outcome measures, that
might be vulnerable to bias when assessed by unblinded ob-
servers, such as assessment of physical function, range of
movement, flexibility (Elkayam et al., 1996; Grahn et al.,
1998; Johnson et al., 1999; Lundblad et al., 1999; Stephens,
2001), or pulmonary function (Loew et al., 1996a, 1996b,
2001; Manocha et al., 2002). Only three of these studies re-
ported an independent outcome assessment (Johnson et al.,
1999; Stallibrass et al., 2002; van Dixhoorn and Duivenvo-
orden, 1999). Blinding research personnel entering ques-
tionnaires’ data was reported in one study (Stallibrass et al.,
Blinding: conclusions and recommendations.Unlike drug
trials with identical placebo pills, in studies involving touch
and verbal guidance it is difficult to blind either therapist or
patient. Our review did not yield any convincing methods
of blinding patients or therapists. Ernst and Canter (2003),
researchers who strongly advocate for blinding and RCTs,
concede in their systematic review of studies of Alexander
Technique that “patient blinding seems impossible.” How-
ever, double blinding is not a sine qua non of RCTs (Schulz
et al., 2002), and there are several approaches that future re-
search might use to diminish bias that may result from lack
1. Objective outcome measures: Along with subjective out-
come measures, it may be important to assess objective
outcome measures such as changes in laboratory tests.
Many researchers regard these as less susceptible to bias
from expectations. Objective measures of physical func-
tioning may be appropriate endpoints for studies of body-
work. It is relatively easy to blind an observer making
these assessments. The internal validity of future studies
may benefit from including objective outcome measures
and blinding study staff that makes the assessments.
2. Assessing the success of blinding: If blinding is at-
tempted, patients can be queried about whether or not
they believe they received the study intervention (Schulz
et al., 2002). The results of the patient query can be used
as a control variable in data analysis, but this was not at-
tempted in any of the reviewed studies. Observers mak-
ing outcome assessments can be queried as well.
3. Assessing patient expectations: Patient expectations can
be assessed for therapies that cannot be blinded. In a study
comparing acupuncture to massage or an education book-
let in patients with low-back pain, questions on expecta-
tions for each treatment were included in the outcome in-
struments (Kalauokalani et al., 2001). Overall results
showed a moderate advantage of massage over acupunc-
ture, which was similar to placebo. However, outcome in
any therapy was superior to the other according to ex-
pectations. The analysis of study outcome data can in-
corporate a measure of expectations as a covariate in a
regression analysis or compare data stratified according
MEHLING ET AL.
to expectations. This allows an unblinded study to main-
tain some ability to control for patient expectations.
4. Choice of control group: How much patient expectations
differ between groups depends in part on the control
group. In an open study, a no-intervention control (i.e.,
waitlist) creates negligible patient expectations. Placebo
or active controls create expectations that can be mea-
sured and compared with those for the study interven-
tion, thus improving control over bias. This issue is dis-
cussed in more detail in the section on control group.
5. Preconsent randomization: Participants may be disap-
pointed when assigned to what might be perceived as an
inferior treatment. By randomizing participants before
consent and describing only the treatment (or observa-
tion procedures) to which they are randomized, patients
can be blinded to the study’s purpose and disappointment
or negative expectations can be reduced. However, treat-
ment expectations may still differ between groups with
this approach. Preconsent randomization was performed
in studies by Cherkin et al. (1996) and Williams et al.
(2003), where participants in the control group (placebo
or usual care) were not informed about the main study
intervention to avoid disappointment. An independent
ethical review board needs to decide whether the bene-
fits of conducting a more rigorous study and of avoiding
disappointment for the participants outweigh the ethical
concerns of a design that does not fully inform partici-
Control group options are placebo, active control, or
no intervention. The purpose of using a placebo control
group is to control for numerous nonspecific or placebo
effects of the intervention on outcome measures (Ernst,
2001; Gotzsche, 1994). Difficulties in identifying a suitable
placebo intervention as the control in a RCT are related to
the blinding issue, as an unmasked placebo will not control
for patient expectations (Crow et al., 1999). Ideally, placebo
controls mimic the study intervention as closely as possible
(i.e., function as a “sham” intervention) in order to blind at
least the patient. Unfortunately, the provider who cannot be
blinded might bring a very different degree of passion and
intention to heal to a sham intervention as compared to the
real intervention, thus producing nonspecific or placebo ef-
fects of rather different degrees between groups (Ernst,
2001; Freund et al., 1972; Gracely et al., 1985; Gryll and
Katahn, 1978; Smith, 1989). Hands-on interventions are par-
ticularly difficult to convert to a sham intervention because
nonverbal human touch communicates motivation, empathy,
and mental presence (Latey, 2001). They cannot effectively
control for bias from nonspecific effects from differential
provider engagement, as the therapist’s intention and pas-
sion to heal (here viewed as nonspecific components, al-
though the discussion is not settled whether these might be
key components) would not be included in the nonspecific
effect of the control intervention. Ernst and Canter (2003)
summarize this issue in their review cited earlier by stating,
“There is no credible placebo.”
Only two of the studies we reviewed used placebo in the
control groups: In these studies (by the same author), a
placebo relaxation instruction was developed for patients
with asthma (Loew et al., 1996a, 2001): A 10-minute stan-
dardized but substantially shortened version of the investi-
gated Breath Therapy was compared to an equally timed
placebo method that lacked the focus on body awareness.
The same therapist performed both the placebo and the study
intervention, thus controlling for therapist personality but
not for differential provider engagement or intention to heal.
In summary, our review of studies including touch and
verbal guidance did not discover any credible placebo in-
tervention to control for nonspecific treatment factors.
In two studies, a waitlist–control study design was used
in which the waitlisted controls received no treatment
(Kirkby, 1994; Lundblad et al., 1999): Feldenkrais for
neck–shoulder problems or for premenstrual syndrome. This
design clearly does not blind participants, does not control
for expectations or biased self-report outcome ratings, does
not control for nonspecific treatment effects, and may even
introduce a disillusionment effect (Hart, 2003) or resentful
demoralization (Torgenson and Sibbald, 1998) in the pa-
tients who have “drawn the short straw,” thus weakening in-
ternal and external validity. However, a delayed interven-
tion might be less demoralizing than no intervention,
although this is not known.
Nonspecific treatment effects or context effects are those
that are not specific to the treatment given, but influenced
by patient expectations, patient–provider interaction, treat-
ment appearance, and the healing environment (Di Blasi and
Kleijnen, 2003; Gotzsche, 1994). From the perspective of
patient outcomes, both specific and nonspecific effects could
be viewed as important, and nonspecific effects could be
viewed less as a trial nuisance than as potentially meaning-
ful mediators and moderators of therapeutic outcomes in
clinical trials (Di Blasi and Reilly, 2004). When trying to
answer questions around the efficacy of a treatment, how-
ever, the distinction between specific and nonspecific effects
becomes important. Out review found several ways to main-
tain systematic control over some nonspecific factors:
1. Control for time, setting, and practitioner: Time spent
with therapist and different settings in complementary
and alternative medicine (CAM) therapy are individual
components of a nonspecific treatment effect that can be
equalized between study arms. Seven reviewed studies
made great efforts to equalize duration and provider char-
acteristics (Johnson et al., 1999; Kirkby, 1994; Loew et
al., 2000; Lowe et al., 2002; Manocha et al., 2002; Smith
et al., 2001; Stallibrass et al., 2002) and three studies of
Feldenkrais and Alexander Techniques reported on
BODYWORK AND BIAS CONTROL
equalized room settings (Lowe et al., 2002; Stallibrass et
al., 2002; Stephens, 2001).
2. Control for attention: Empathic attention can be con-
trolled for by using an active and equally credible con-
trol intervention that is similar but lacks the specific el-
ement that characterizes the study intervention. In this
study design, the control group receives similar personal
attention, empathy, intention to heal, listening, and some
explanations, but not the therapeutic ingredient(s) seen
as specific for the studied modality (i.e., guided aware-
ness of physical sensations and breath movement, evok-
ing a state of alert and relaxed presence). This approach
would test the effect of the specific components and con-
trol for some nonspecific effects. It was used in 9 of the
20 reviewed trials (Kirkby, 1994; Loew et al., 1996a,
2000, 2001; Lowe et al., 2002; Lundblad et al., 1999;
Manocha et al., 2002; Smith et al., 2001) of which six
were randomized: Breath Therapy was compared to re-
laxation technique (Manocha et al., 2002), cognitive-be-
havioral therapy to Feldenkrais (Kirkby, 1994), a short-
ened version of Breath Therapy to placebo-relaxation
(Loew et al., 2000), and partially audiotaped Feldenkrais
to audiotaped narrative (Smith et al., 2001); in two stud-
ies participants served as their own crossover controls,
comparing a shortened version of Breath Therapy to
placebo-relaxation (Loew et al., 1996a, 2000). The more
nonspecific elements of a therapy are controlled for, the
more explanatory a study becomes. There appear to be
different degrees of rigor for explanatory trials. The most
rigorous has been called fastidious trial, which does not
permit individualized therapy (Schwartz and Lellouch,
1967). Although it has been repeatedly put into question
whether this level of rigor is desirable and appropriate
for CAM and other therapies (Hyland, 2003; Lewith et
al., 2002; Walach et al., 2002), explanatory trials appear
to be feasible when the study protocol allows for some
individualized variations around a core of standardized
treatment guidelines. This design would be a compro-
mise between explanatory trials assessing treatment ef-
ficacy above and beyond nonspecific treatment effects
in the control group and pragmatic trials assessing ef-
fectiveness of a real-life treatment. Pragmatic trials use
flexible, individualized protocols, in which the nonspe-
cific components of extra attention and empathy are al-
lowed to add to and freely interact with the specific ef-
fects of the test intervention thus maximizing outcome.
Rather than being mutually exclusive and contradicting
each other, both approaches complement each other (Le-
with et al., 2002), and may be the poles of a continuum
with both explanatory and pragmatic value to varying
3. A third no-treatment arm: If a credible placebo inter-
vention as control can still be conjured up and patients
can be blinded to group allocation and the investigator’s
intentions, that placebo’s nonspecific effect can be esti-
mated by comparison with a third no-treatment arm. A
three-arm design was used in several studies (Kirkby,
1994; Lowe et al., 2002; Lundblad et al., 1999; Stalli-
brass et al., 2002). Interestingly, one of these studies used
Feldenkrais as the active, supposedly ineffective placebo
for a condition (premenstrual syndrome), for which it was
not expected to help, and included a third no-treatment
arm thus providing us with valid data of the nonspecific
effect of Feldenkrais in that condition (Kirkby, 1994).
The others used Feldenkrais versus PT versus no-treat-
ment for shoulder-neck problems (Lundblad et al., 1999),
Alexander Technique versus massage versus no-treat-
ment for Parkinson’s disease (Stallibrass et al., 2002), or
Feldenkrais versus muscle relaxation versus no-treatment
for acute myocardial infarction (Lowe et al., 2002). These
studies, however, either did not test for statistical differ-
ences across groups (Stallibrass et al., 2002) or tested
across all three groups together (Lowe et al., 2002; Lund-
blad et al., 1999), thus missing the opportunity to test dis-
criminatively for a specific efficacy beyond nonspecific
effects or the nonspecific effect compared to no-treat-
ment. Nevertheless, these studies provide data on the
amount of specific and nonspecific effects, even if they
were not analyzed or presented that way. Using a third
no-treatment arm can help to differentiate between spe-
cific and measurable nonspecific effects of a therapy
(Ernst, 2001). Furthermore, it can help control for other
elements that frequently contribute to nonspecific or
placebo effects: regression to the mean, spontaneous re-
covery, use of concurrent therapies, and the Hawthorne
effect (Ernst, 2001).
4. A couched study intervention: Using a large multimodal
control intervention package identical to the treatment
package except for the study intervention may make it
possible to couch the study intervention in a bundle of
cointerventions. This was done in a nonrandomized con-
trolled study of inpatients with eating disorder treated
over 5 weeks primarily with intensive individual and
group psychotherapy and optional additional movement
therapy (including Feldenkrais and dance) (Laumer et al.,
1997). In another study (Elkayam et al., 1996), Alexan-
der Technique was one of seven modalities in an uncon-
trolled comprehensive outpatient treatment plan for
chronic low-back pain (including back schooling, inten-
sive psychologic interventions, muscle relaxation train-
ing, acupuncture, chiropractic, Alexander Technique, diet
counseling, and a pain specialist). Theoretically, this
treatment could have been compared to an almost iden-
tical control group without Alexander technique, thus
possibly blinding the patients to some (measurable) de-
gree and reduce bias from differential patient expecta-
tions. However, such design has not yet been employed
in a randomized trial and would not provide definitive
data as, theoretically, treatment interactions might mod-
ify the effect of the treatment of interest.
MEHLING ET AL.
Volunteer bias in recruitment and attrition
Expectations and preferences for CAM therapies often
are highly emotional and, as a result, “patients may not want
to take a chance with randomization . . . in an environment,
where patients’ enthusiasm is often in favor of CAM and
against receiving a control treatment” (Ernst, 2003;
Kalauokalani et al., 2001) or no treatment. This volunteer
bias generates difficulties with obtaining informed consent
and recruitment (Ernst, 2003) and with preventing differen-
tial postrandomization attrition, thus weakening subsequent
interpretation of the results.
There may be a wide variance in patient expectations fol-
lowing different recruitment modes. Self-referral (i.e., in re-
sponse to radio or newspaper advertisements or from CAM
practitioners) likely introduces a higher degree of volunteer
bias compared to sequential referral from physicians. Con-
sequently, recruitment sources should be reported. Only one
of the reviewed studies did not report any recruitment de-
tails (Engel and Andersen, 2000).
Only one study with dropout rates that differed between
groups discussed causes and conclusions (Manocha et al.,
2002), four reported clearly different rates without further
analysis or comment (Kirkby, 1994; Loew et al., 2000;
Lundblad et al., 1999; Malmgren-Olsson and Branholm,
2002). No study reported attempts in assessing or reducing
differences in volunteer bias. We recommend reducing this
bias and the subsequent difficulties with consent and attri-
tion by the following measures:
1. Offering an attractive, high-quality control intervention.
2. Recruitment from university-based clinics or other set-
tings, where patients are often glad to contribute to re-
search and not already committed to using a particular
3. Recruitment through physician referral: This recruitment
mode was used in 10 of the reviewed studies, whereas
the remaining studies used multiple sources (e.g., flyers,
newspaper advertisement). Data from 10 studies report-
ing dropout rates and recruitment mode suggest that re-
cruitment via physician referral may decrease differen-
tial drop-out rates. Recruitment through direct physician
referral, however, can be cumbersome particularly from
university primary care clinics, as one of the authors
learned during a recently completed study of Breath Ther-
apy for chronic low-back pain (Mehling, 2004). He ob-
tained independent review board (IRB) approval to use
a different mode of recruitment that accelerated enroll-
ment: The university’s IRB waived the prior patient au-
thorization for accessing the electronic medical center
database to obtain lists of potentially eligible patients
sorted by primary care providers and allowed mass mail-
ings of provider-signed information letters to these pa-
tients. It took 3 months to recruit a total of 8 participants
by individual direct primary care provider referral and it
took 2 weeks after mailing to recruit another 25 from the
same clinics. Similarly, the electronic database of an in-
tegrated health care system could be used.
Even these three measures combined might not be able
to overcome volunteer bias and differential dropout rates: In
the study of Breath Therapy by one of the authors (Mehling,
2004), an attractive, free, high-quality, individualized PT
from highly motivated and qualified providers was offered
as control intervention. Nevertheless, several patients were
disappointed with their allocation to the control interven-
tion, confirming the disillusionment effect cited above. This
was reflected in higher drop-out rates in the control arm (7
of 18 in control versus 3 of 18 in Breath Therapy group).
Therefore, another recently tried measure might be consid-
4. Partial randomization or patient-preference trials,
whereby patients are given a choice according to their
treatment preferences, and only patients without strong
preferences get randomized (i.e., standard of care versus
CAM method versus randomization to one of the two)
(Carter, 2003; Zelen, 1979). In a similar design, patients
get randomized to usual care or a choice between usual
care and a CAM method (Eisenberg, 2002). Both types
of studies in patients with low-back pain are underway
(Eisenberg, 2002; North American Spine Society Board
of Directors, 2003). To our knowledge, this method has
not been used yet in this field.
Rigorous clinical trials of hands-on complementary and
alternative therapy interventions are scarce and clearly
needed. They face a series of particular challenges that can
be strategically and systematically addressed in order to min-
imize bias. Among methodological difficulties, issues with
blinding, choice of control intervention, and volunteer bias
When therapist blinding is not possible, control for ther-
apist or investigator bias can be partially maintained by
blinding an independent outcome assessor. When patient
blinding is not possible, control for patient expectations can
be partially maintained by assessing the success of attempted
blinding, assessing patient expectations, using a large multi-
modal intervention package in the main arm with an iden-
tical treatment package minus the study intervention for the
control, and preconsent randomization. When a placebo con-
trol is not feasible, control for nonspecific treatment effects
can be partially maintained by carefully and systematically
controlling for their individual elements, such as time spent
with therapist, therapist engagement and attention, settings,
and room environment, use of a similar active control in-
BODYWORK AND BIAS CONTROL
tervention lacking the specific ingredient that characterizes
the study intervention, and by collecting data on nonspecific
effects by a third no-intervention study arm. While an ab-
solute bias control is not realistic, these methods may help
to minimize various key biases encountered in trials of body-
Variations in expectations of treatment outcomes emerge
as the central theme connecting the challenges in the three
discussed areas of blinding, choice of controls, and volun-
teer bias. Although the assessment of expectations appears
to be an important response to the reviewed methodologi-
cal challenges, it has been subject of only limited research
(Di Blasi et al., 2001). That such a measure can be included
was demonstrated in a study by Kalauokalani et al. (2001).
More research on the complex theme of expectations and
their assessment is needed.
We would like to thank Susan Folkman, Ph.D., Dan
Cherkin, Ph.D., and Karen Sherman, Ph.D., M.P.H., for their
constructive criticism during the preparation of this manu-
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