Subacromial decompression versus diagnostic arthroscopy for shoulder impingement: randomised, placebo surgery controlled clinical trial

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2018;362:k2860 | doi: 10.1136/bmj.k2860 1

RESEARCH

Subacromial decompression versus diagnostic arthroscopy for

shoulder impingement: randomised, placebo surgery controlled

clinical trial

Mika Paavola,

Antti Malmivaara,

Simo Taimela,

1,3

Kari Kanto,

Jari Inkinen,

Juha Kalske,

Ilkka Sinisaari,

Vesa Savolainen,

Jonas Ranstam,

Teppo L N Järvinen

1,3

for the Finnish

Shoulder Impingement Arthroscopy Controlled Trial (FIMPACT) Investigators

ABSTRACT

OBJECTIVE

To assess the ecacy of arthroscopic subacromial

decompression (ASD) by comparing it with diagnostic

arthroscopy, a placebo surgical intervention, and with

a non-operative alternative, exercise therapy, in a

more pragmatic setting.

DESIGN

Multicentre, three group, randomised, double blind,

sham controlled trial.

SETTING

Orthopaedic departments at three public hospitals in

Finland.

PARTICIPANTS

210 patients with symptoms consistent with shoulder

impingement syndrome, enrolled from 1 February

2005 with two year follow-up completed by 25 June

2015.

INTERVENTIONS

ASD, diagnostic arthroscopy (placebo control), and

exercise therapy.

MAIN OUTCOME MEASURES

Shoulder pain at rest and on arm activity (visual

analogue scale (VAS) from 0 to 100, with 0 denoting

no pain), at 24 months. The threshold for minimal

clinically important dierence was set at 15.

RESULTS

In the primary intention to treat analysis (ASD versus

diagnostic arthroscopy), no clinically relevant between

group dierences were seen in the two primary

outcomes at 24 months (mean change for ASD 36.0 at

rest and 55.4 on activity; for diagnostic arthroscopy

31.4 at rest and 47.5 on activity). The observed mean

dierence between groups (ASD minus diagnostic

arthroscopy) in pain VAS were −4.6 (95% condence

interval −11.3 to 2.1) points (P=0.18) at rest and

−9.0 (−18.1 to 0.2) points (P=0.054) on arm activity.

No between group dierences were seen between

the ASD and diagnostic arthroscopy groups in the

secondary outcomes or adverse events. In the

secondary comparison (ASD versus exercise therapy),

statistically signicant dierences were found in

favour of ASD in the two primary outcomes at 24

months in both VAS at rest (−7.5, −14.0 to −1.0,

points; P=0.023) and VAS on arm activity (−12.0,

−20.9 to −3.2, points; P=0.008), but the mean

dierences between groups did not exceed the pre-

specied minimal clinically important dierence. Of

note, this ASD versus exercise therapy comparison is

not only confounded by lack of blinding but also likely

to be biased in favour of ASD owing to the selective

removal of patients with likely poor outcome from the

ASD group, without comparable exclusions from the

exercise therapy group.

CONCLUSIONS

In this controlled trial involving patients with a

shoulder impingement syndrome, arthroscopic

subacromial decompression provided no benet over

diagnostic arthroscopy at 24 months.

TRIAL REGISTRATION

Clinicaltrials.gov NCT00428870.

Introduction

Management of shoulder pain has been estimated to

account for 4.5 million visits to physicians and $3bn

(£2.3bn; €2.6bn) ﬁnancial burden each year in the

US alone.

1 2

As 44-70% of patients with shoulder pain

are diagnosed as having a shoulder impingement

syndrome, annual direct medical costs of this

complaint are estimated at more than $1bn in the

US.

3-5

The pathognomonic clinical sign of shoulder

impingement syndrome, subacromial shoulder pain

while lifting the arm, is commonly attributed to

“impingement” of the rotator cu tendons between the

humeral head and the overlying acromion. Premised

on this rationale, the undersurface of the acromion

is smoothened to decompress the passage of the

rotator cu tendon through the subacromial space in a

surgical procedure called subacromial decompression.

For numbered aliations see

end of article.

Correspondence to: M Paavola

mika.paavola@hus.

Additional material is published

online only. To view please visit

the journal online.

Cite this as: BMJ ;:k

http://dx.doi.org/10.1136/bmj.k2860

Accepted: 8 June 2018

WHAT IS ALREADY KNOWN ON THIS TOPIC

Arthroscopic subacromial decompression, the most commonly performed

shoulder surgery, is carried out to treat patients with shoulder impingement

syndrome

Three recent systematic reviews indicate that subacromial decompression is not

superior to exercise therapy in patients with shoulder impingement syndrome

Without a placebo surgical comparator (proper blinding), the ecacy of

arthroscopic subacromial decompression cannot be assessed

WHAT THIS STUDY ADDS

This FIMPACT trial and the recently published (highly similar) CSAW trial are

the rst two placebo surgery controlled trials on the ecacy of arthroscopic

subacromial decompression

Both arthroscopic subacromial decompression and diagnostic arthroscopy

(placebo surgery) resulted in signicant improvements in pain and functional

outcomes with no dierence in the incidence of adverse events

However, the patients assigned to arthroscopic subacromial decompression had

no superior improvement over those assigned to diagnostic arthroscopy

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Although various non-operative treatment modalities

are recommended as initial treatment for patients

with shoulder impingement symptoms,

6 7

subacromial

decompression has become one of the most frequently

performed orthopaedic procedures in the world.

With

the advent of arthroscopy, the number of subacromial

decompression procedures has increased many times

between the 1980s and the 2010s.

9 10

We conducted

a multicentre, randomised, double blind, placebo

surgery controlled trial to assess the ecacy of

arthroscopic subacromial decompression (ASD) in

patients with shoulder symptoms consistent with

shoulder impingement syndrome.

Methods

Trial design

We conducted this superiority trial at three orthopaedic

clinics in Finland from 1 February 2005 to 25 June

2015. Details of the trial design and conduct have

been published elsewhere.

The patients, the people

who collected and analysed the data, and those who

interpreted the principal ﬁndings for the ASD versus

diagnostic arthroscopy comparison (see below,

“Blinded data interpretation”) were unaware of the

study group assignments. On entering the study,

patients were unequivocally informed that they might

undergo diagnostic arthroscopy and that they would

be allowed to consider crossing over to ASD if they did

not have adequate relief of symptoms, preferably no

sooner than six months after randomisation.

Participants

We enrolled patients aged 35-65 years who had

subacromial pain (for more than three months)

that was unresponsive to conventional conservative

treatment and had clinical ﬁndings consistent with

shoulder impingement syndrome. All patients had

magnetic resonance imaging with intra-articular

contrast to exclude a rotator cu tear. Detailed

inclusion and exclusion criteria are provided in table

S1 in appendix 2.

Randomisation and blinding

In an attempt to obtain three balanced study groups

of similar size, we planned a twofold, sequential

randomisation as follows. Firstly, during the baseline

appointment, patients were randomised to surgical

or conservative treatment (exercise therapy) in a 2:1

ratio. Patients randomised to exercise therapy started

standardised physiotherapy within two weeks of the

baseline appointment, whereas those allocated to

surgery were scheduled for surgery with the aim of

carrying out the procedure within 12 weeks of this

ﬁrst randomisation. In patients allocated to surgery,

we did a diagnostic arthroscopy to rule out a rotator

cu tendon tear and other obvious intra-articular

pathology needing surgical treatment. If we found

a full or a partial thickness rotator cu tear large

enough to need repair (grade III) according to clinical

practice guidelines,

we excluded the patient and

repaired the tear. Patients with a partial tear that did

not need repair (grade I and II) were included in the

study. If the eligibility of the patient was conﬁrmed in

diagnostic arthroscopy, the surgeon asked a research

nurse to carry out the second randomisation by

opening an envelope containing the study group

assignment (ASD or diagnostic arthroscopy; ratio 1:1).

Only the orthopaedic surgeon and other sta in the

operating room were made aware of the surgical group

assignment, and they did not participate in further

treatment or follow-up of the patient.

Randomisation was carried out using sequentially

numbered sealed opaque envelopes. Separate

randomisation lists for each of the three centres, with

blocks varying randomly in size, were prepared by a

statistician with no involvement in the clinical care of

participants in the trial.

Study interventions

Exercise therapy

Supervised, progressive, individually designed

physiotherapy was started within two weeks of

randomisation, using a standardised protocol that

relied primarily on daily home exercises as well as 15

visits to an independent physiotherapist (the detailed

exercise therapy protocol is available in appendix 1).

Diagnostic arthroscopy

We carried out arthroscopic examination of the

glenohumeral joint and subacromial space with

the use of standard posterior and lateral portals

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and a 4 mm arthroscope with the patient under

general anaesthesia, usually supplemented with an

interscalene brachial plexus block. We did an intra-

articular and subacromial assessment of the rotator

cu integrity. If the rotator cu insertion could not be

otherwise visualised, subacromial bursal tissue was

bluntly stretched with a trochar or resected, keeping the

resection to a minimum. If arthroscopic examination

showed any pathology needing intervention other than

ASD, we excluded the patient from the trial (ﬁg 1).

Once the eligibility was conﬁrmed, the participants

were randomly assigned to either ASD or diagnostic

arthroscopy. For those allocated to the diagnostic

arthroscopy group, the operation was terminated. To

ensure concealment of the allocation from participants

and the sta other than those in the operating theatre,

the diagnostic arthroscopy participants were kept in

the operating theatre for the time needed to perform

subacromial decompression.

Arthroscopic subacromial decompression

After arthroscopic examination of the shoulder (that

is, diagnostic arthroscopy), the ASD procedure, which

involved the debridement of the entire subacromial

bursa (bursectomy) and resection of the bony spurs

and the projecting anterolateral undersurface of the

acromion, was carried out with a shaver, burr, and/or

electrocoagulation.

Postoperative care

The postoperative rehabilitation was identical in the

ASD and diagnostic arthroscopy groups, consisting of

one visit to an independent physiotherapist, blind to

the group assignment, for guidance and instructions

for home exercises.

Outcome measures

Given that the pathognomonic clinical sign of shoulder

impingement syndrome is subacromial shoulder pain,

especially at night and while lifting the arm, our two

primary outcome measures were shoulder pain at rest

and shoulder pain on arm activity at 24 months. We used

a 0-100 visual analogue scale (VAS) ranging from 0 (no

pain) to 100 (extreme pain) to assess the shoulder pain.

At the time of our trial’s launch no direct evidence on

the appropriate minimal clinically important dierence

for VAS in patients with shoulder impingement

syndrome was available, so we considered 15 points

to be the minimal clinically important dierence.

We based this estimate on an extensive review of the

existing literature on minimal clinically important

dierences for the VAS scale in a wide range of dierent

musculoskeletal conditions. The appropriateness of

the chosen minimal clinically important dierence has

subsequently been validated.

Secondary outcomes included two shoulder function

assessment instruments, the Constant-Murley score

and the simple shoulder test, as well as the 15D,

generic health related quality of life instrument made

up of 15 dimensions and scored on a scale of 0 (death)

to 1 (full health). Patients’ global assessment of

satisfaction with the treatment was assessed on a VAS

ranging from 0 (completely dissatisﬁed) to 100 (very

satisﬁed), and satisfaction with the treatment outcome

was assessed using a ﬁve item scale (from very satisﬁed

to very dissatisﬁed). We used the responses from the

latter question to carry out a responder analysis

(appendix 1).

Questionnaires were administered at baseline and

three, six, 12, and 24 months after randomisation.

The follow-up questionnaires also included a separate

section on adverse events. We deﬁned adverse events as

untoward medical occurrences that did not necessarily

have a causal relation with the treatment administered.

Serious adverse events were those having the potential

to result in signiﬁcant disability/incapacity, need

inpatient hospital care, prolong the hospital care, be

life threatening, or result in death. At the three month

follow-up, the surgically treated patients were asked

which procedure (ASD or diagnostic arthroscopy) they

thought they had had.

Statistical analysis and sample size calculation

We powered the study to detect a dierence of at

least the minimal clinically important dierence

(15 points

) in the two primary outcomes between

the ASD and diagnostic arthroscopy groups. For

the study to have 90% power to show a minimal

clinically important advantage of ASD over diagnostic

arthroscopy, under the assumption of a two sided type

1 error rate of 5%, we planned to recruit 70 patients

per group.

The trial was primarily designed to ascertain

whether ASD is superior to diagnostic arthroscopy, at

24 months after the procedure, with the two primary

outcomes (the primary conﬁrmatory comparison). We

also included a pragmatic comparison of the relative

beneﬁts of ASD versus exercise therapy (the secondary

exploratory comparison). An independent statistician

unaware of the group assignments did all the analyses

according to the previously published statistical

analysis plan. The statistical analysis plan, outlining

our statistical methods in more detail, is provided in

appendix 1.

We quantiﬁed the treatment eect on an intention to

treat (ASD versus diagnostic arthroscopy comparison)

or full analysis set (ASD versus exercise therapy

comparison) basis, as the dierence between the

groups in pain scores (VAS), Constant-Murley score,

simple shoulder test score, and 15D score with the

associated 95% conﬁdence intervals and P values at

24 months after the primary randomisation. In the

intention to treat and full analysis set analyses, the

participants were included as randomised. We used

a mixed model repeated measurements analysis of

variance with patient as a random factor (repeated

measurements at three, six, 12, and 24 months),

the baseline value as a covariate, and assuming a

covariance structure with compound symmetry. As

the mixed model repeated measurements analysis of

variance allows for analysis of unbalanced datasets

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without imputation, we analysed all available data,

the full analysis set. The missingness of the outcome

data at dierent time points is shown in table S12

in appendix 2. We ﬁtted the mixed model repeated

measurements model by using the mixed procedure in

Stata and used Satterthwaite’s method to calculate the

degrees of freedom.

We used generalised estimating equation logistic

regression analysis to analyse categorical variables.

We compared the frequencies of patients who

reported satisfaction or subjective improvement and

the proportions of responders and non-responders,

those with a change exceeding the minimal clinically

important improvement in the primary outcomes, and

reoperations/treatment conversions between the two

groups at 24 months.

To safeguard against potential multiplicity eects in

the primary comparison,

we required a statistically

signiﬁcant treatment eect on both of our primary

outcome variables. All secondary analyses are

supportive, exploratory, and/or hypothesis generating.

We did two sensitivity analyses (per protocol and as

treated) and four subgroup analyses (potential eect

modifying of the duration and severity of symptoms,

the acromial anatomy, and the presence/absence

of bursal resection) with the same principles as the

intention to treat and full analysis set analyses. We

considered a P value of 0.05 to indicate statistical

signiﬁcance. We used Stata v14.1 for all statistical

analyses.

Blinded data interpretation

We interpreted the results of the trial according to

a blinded data interpretation scheme.

In brief,

an independent statistician provided the Writing

Committee of the FIMPACT trial with blinded results from

Allocated to surgery (ASD or DA) (n=139)

Underwent shoulder arthroscopy (n=134)

Allocated to exercise therapy (ET) (n=71)

Assessed for eligibility (n=281)

Underwent 1st randomisation (n=210)

Received exercise therapy (n=71)

Analysis at 24 months (n=59)

Allocated to DA (n=63)

Received no further surgery, DA (n=63)

Allocated to ASD (n=59)

Received subacromial

decompression, ASD (n=59)

Withdrew from study (n=0)

Lost to follow-up (n=0)

Excluded before arthroscopy (n=5):

Had symptomatic osteoarthritis of acromioclavicular

joint (n=2)

Declined to participate (n=2)

Did not meet anesthesiological outpatient criteria (n=1)

Underwent second randomisation (n=122)

Excluded because of ndings at diagnostic arthroscopy

(n=12):

Had a full thickness tear of the RC tendons (n=6)

Had a SLAP lesion or pathology of long head of

biceps tendon (n=5)

Had marked instability of shoulder joint (n=1)

Excluded before randomisation (n=71):

Had a full thickness tear of rotator cu tendons (n=47)

Had osteoarthritis of acromioclavicular joint (n=2)

Had substantial calcic deposits in rotator cu tendons (n=2)

Became asymptomatic while waiting for MRA (n=7)

MRA could not be obtained (n=4)

Declined to participate (n=3)

Had other intra-articular pathology (n=6)

Analysis at 24 months (n=68) Analysis at 24 months (n=59)

Withdrew from study (n=2):

Personal reasons (n=1)

Medical reasons unrelated to study (n=1)

Lost to follow-up (n=2):

Dead (n=1)

Data missing (n=1)

Withdrew from study (n=3):

Personal reasons (n=2)

Medical reasons unrelated to study (n=1)

Lost to follow-up (n=0)

Fig | Study flowchart. ASD=arthroscopic subacromial decompression; DA=diagnostic arthroscopy; MRA=magnetic

resonance arthrography; SLAP=superior labrum anterior-posterior. Full details of unblinding, treatment conversions,

and reoperations are provided in table S in appendix 

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the analyses, with the groups labelled group A, group

B, and group C. The Writing Committee then considered

the interpretation of the results until a consensus

was reached and agreed in writing on all alternative

interpretations of the ﬁndings. Once a consensus was

reached, we recorded the minutes of this meeting in a

document coined statement of interpretation, which

was signed by all members of the Writing Committee.

After this common agreement was reached, the data

manager and the independent statistician broke the

randomisation code and the correct interpretation was

chosen. The draft of the manuscript was then ﬁnalised.

Detailed minutes of blinded data interpretation

meetings are provided in appendix 1.

Patient involvement

No patients were involved in designing the study, nor

were they involved in developing plans for recruitment,

design, or implementation of the study. No patients

were asked to advise on interpretation or writing

up of results. When the results of this randomised

controlled trial are published, a lay information ﬂyer

with ﬁnal results will be sent to the recruiting centres

for dissemination to the trial participants.

Results

Characteristics of patients

Of the 281 eligible patients, we excluded 71 (ﬁg 1).

A total of 210 patients were included in the ﬁrst

randomisation; 71 were assigned to exercise therapy

and 139 to surgery. Of those allocated to surgery

(n=139), another 17 were excluded before the second

randomisation (ﬁg 1), leaving 59 patients to receive

ASD and 63 to receive diagnostic arthroscopy. Over

the course of the 24 month follow-up, three patients

in the exercise therapy group and two patients in

the diagnostic arthroscopy group withdrew from the

study, and one patient in the diagnostic arthroscopy

group died. The study groups were well balanced on

all baseline characteristics (table 1). The patients who

withdrew from the study (n=5) were similar to those

who were randomised with respect to primary outcome

measures at baseline.

Primary comparison: ASD versus diagnostic

arthroscopy

Primary outcomes

We saw marked improvement from baseline to 24

months in both primary outcomes in both the ASD

and diagnostic arthroscopy groups (mean change for

ASD 36.0 at rest and 55.4 on activity; for diagnostic

arthroscopy 31.4 at rest and 47.5 on activity) (ﬁg 2 and

table 2), but no signiﬁcant between group dierences

existed at 24 months in either VAS pain at rest (mean

dierence, ASD minus diagnostic arthroscopy, −4.6,

95% conﬁdence interval −11.3 to 2.1; P=0.18) or VAS

pain on arm activity (−9.0, −18.1 to 0.2; P=0.054) (ﬁg

2, table 2, and table S3 in appendix 2). These results

remained unaltered in the pre-speciﬁed sensitivity

analyses (as treated and per protocol) and subgroup

analyses (tables S2, S5, and S6 in appendix 2).

Secondary and other outcomes

We found no signiﬁcant between group dierences in

any of the secondary outcomes (table 2 and table S4

in appendix 2). Patients in the diagnostic arthroscopy

group were no more likely than those in the ASD group

to guess that they had had a placebo procedure (22/53

(42%) and 2154 (39%), respectively; P=0.85).

Unblinding of treatment allocation and crossovers

Six of 59 patients in the ASD group and nine of

63 patients in the diagnostic arthroscopy group

(P=0.49) reported persistent symptoms after surgery

suciently severe to lead to unblinding of the study

group assignment (at an average of 10 months after

the index operation) (table S7 in appendix 2). Two

participants in the ASD group underwent a consequent

reoperation—one had manipulation under anaesthesia

and the other ﬁrst had acromioclavicular resection

and then later manipulation under anaesthesia. In

the diagnostic arthroscopy group, eight patients had

a reoperation (seven ASDs and one ASD coupled with

subscapularis tendon repair). Details of unblindings,

treatment conversions, and reoperations are shown in

table S7 in appendix 2.

Complications and adverse events

One patient in the diagnostic arthroscopy group had

temporary swelling in the brachial area related to

a brachial plexus block. Three patients in the ASD

group and one patient in the diagnostic arthroscopy

group developed symptoms consistent with a frozen

shoulder over the course of the 24 month follow-up

(table 2). No other complications directly related to the

interventions were registered.

Secondary comparison: ASD versus exercise

therapy

Primary outcomes

Marked improvement from baseline to 24 months

was seen in both primary outcomes in both the ASD

and exercise therapy groups (ﬁg 3, table 3, and table

S8 in appendix 2). We found statistically signiﬁcant

dierences in favour of ASD at 24 months in both VAS

at rest (−7.5, −14.0 to −1.0; P=0.023) and VAS on arm

activity (−12.0, −20.9 to −3.2; P=0.008), but the mean

dierence between the groups did not exceed the pre-

speciﬁed minimal clinically important dierence

of 15. These results remained essentially unaltered

in the pre-speciﬁed sensitivity analyses (table S10

in appendix 2). We found no signiﬁcant dierences

between the groups in the proportion of patients

with pain reduction exceeding the minimal clinically

important improvement threshold of 15 in VAS pain at

rest and VAS pain on activity (table S11 in appendix2).

The proportion of patients with VAS pain on activity

below the threshold of 30 at 24 months was lower in

the exercise therapy group than in the ASD group (table

S11 in appendix 2). Of note, this ASD versus exercise

therapy comparison is confounded by lack of blinding

and the fact that 17/139 (12%) patients were excluded

from the two surgical groups before the second

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randomisation without any comparable exclusions

from the exercise therapy group. As a result, this ASD

versus exercise therapy comparison is likely to be

biased in favour of ASD. Also, the progressive exercise

therapy regimen carried out in the exercise therapy

group is dierent from the overall postoperative care

carried out for patients in the ASD group.

Secondary and other outcomes

The only statistically signiﬁcant between group

dierence in the secondary outcomes was in the

Constant-Murley score in favour of ASD (7.7, 1.6 to

13.9; P=0.013) (table 3), but the mean dierence

between the groups did not exceed the pre-speciﬁed

threshold of 17 for minimal clinically important

dierence. Furthermore, the group dierences in the

Constant-Murley score were not statistically signiﬁcant

in the pre-speciﬁed sensitivity analyses (table S10 in

appendix 2).

Unblinding of treatment allocation and crossovers

Fifteen patients who were initially assigned to exercise

therapy reported persistent symptoms suciently

severe to require unblinding; 14 of them subsequently

underwent ASD and one underwent acromioclavicular

resection. Three consequent reoperations were

performed (table S7 in appendix 2).

Complications and adverse events

Two patients in the exercise therapy group developed

symptoms consistent with a frozen shoulder, and one

patient reported aggravation of low back pain over the

course of exercise therapy regimen (table 3). No other

adverse events directly related to the exercise therapy

were registered.

Discussion

This multicentre, randomised, placebo controlled

trial involving patients with shoulder impingement

syndrome showed that arthroscopic subacromial

decompression was not superior to diagnostic

arthroscopy, with regard to outcomes assessed at the

end of a 24 month follow-up period. Although both

groups had signiﬁcant improvement in both primary

outcomes, the patients assigned to ASD had no

clinically relevant improvement over those assigned to

diagnostic arthroscopy.

Comparison with other studies

We are aware of only one other randomised, placebo

surgery controlled trial on the ecacy of ASD in the

treatment of shoulder impingement syndrome.

The

ﬁndings of this recently published “Can Shoulder

Arthroscopy Work?” (CSAW) trial showed that at both

Table | Baseline characteristics of participants according to study group

Characteristics

Arthroscopic subacromial

decompression (n=)

Diagnostic

arthroscopy (n=)

Exercise

therapy (n=)

Mean (SD) age, years 50.5 (7.3) 50.8 (7.6) 50.4 (6.6)

No (%) female 42 (71) 46 (73) 47 (66)

No (%) dominant hand aected 35 (59) 36 (57) 46 (65)

Mean (SD) duration of symptoms, months 18 (14) 18 (19) 22 (23)

No (%) able to work normally regardless of shoulder symptoms 27 (46) 31 (49) 35 (49)

Mean (SD) visual analogue scale score, at rest* 41.3 (25.8) 41.6 (25.5) 41.7 (27.5)

Mean (SD) visual analogue scale score, on arm activity* 71.2 (23.6) 72.3 (21.7) 72.4 (20.8)

Mean (SD) Constant-Murley score† 32.2 (15.8) 31.7 (14.0) 35.2 (16.2)

Mean (SD) simple shoulder test score‡ 4.9 (2.9) 4.9 (2.9) 4.8 (2.7)

Mean (SD) 15D score§ 0.89 (0.06) 0.89 (0.07) 0.88 (0.08)

*Shoulder pain at rest and on activity was assessed on a 100 mm visual analogue scale of 0 to 100, with 0 denoting no pain and 100 denoting extreme

pain.

†Scoring system for evaluation of various shoulder disorders consisting of both objective (range of motion and strength) and subjective measurements

(pain assessment, work load, and leisure time activities), summarised in a score between 0 and 100; higher score indicates better shoulder function.

‡Based on 12 questions with yes (1) or no (0) response options; maximum score is 12, indicating normal shoulder function; minimum score of 0 points

indicates severely diminished shoulder function.

§Generic health related quality of life instrument comprising 15 dimensions; maximum score is 1 (full health), and minimum score is 0 (death).

VAS at rest

100

Months

VAS on arm activity

Baseline 36 12 24

100

Arthroscopic subacromial decompression

Diagnostic arthroscopy

Fig | Primary outcomes of primary comparison at

baseline and at , , , and  month follow-up. Visual

analogue scale (VAS) shoulder pain scores at rest and on

arm activity over  month follow-up period are shown.

VAS scales range from  to , with higher values

indicating more severe pain. Data are mean (% CI)

shown at follow-up time points

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the primary six month follow-up and the secondary

12 month follow-up, arthroscopic subacromial

decompression seemed to oer no extra beneﬁt

over arthroscopy alone (placebo comparator).

The

ﬁndings are in full agreement with the short term (six

and 12 month) ﬁndings of our trial (ﬁg 2 and table

S3 in appendix 2) with respect to ecacy of ASD

over diagnostic arthroscopy. Our trial further shows

no clinically relevant beneﬁt of ASD over diagnostic

arthroscopy at our primary, 24 month, follow-up time

point.

Strengths and limitations of study

The placebo surgery controlled design represents the

primary dierence between our trial and the CSAW

trial

and the rest of the existing literature on this

topic. Acknowledging that the act of surgery in itself

produces a profound placebo response,

21-23

the actual

treatment eect is impossible to distinguish from the

nonspeciﬁc (and placebo) eects—such as the patients’

or researchers’ expectations of beneﬁt—without a

placebo comparison group.

Such bias is particularly

important in trials with subjective endpoints.

Given

that the proportions of patients who guessed whether

they had undergone a placebo procedure was similar

in the two surgical groups, we argue that the risk

of performance bias is low in our trial. Diagnostic

arthroscopy controlled trials in the knee and shoulder

with a very similar design to our study have prompted

assertions that diagnostic arthroscopy cannot be

considered a true placebo comparator because of the

alleged therapeutic eects of joint lavage.

26-29

The

existing high quality evidence disputes such assertions,

as tidal irrigation and arthroscopic lavage have both

failed to provide a beneﬁt over placebo procedures

(placebo irrigation or skin incisions, respectively).

22 30

Moreover, no concerns were expressed regarding the

validity of using diagnostic arthroscopy as a control in

a previous placebo surgery controlled trial on surgery

after shoulder dislocation.

One obvious advantage

of appropriate blinding became readily apparent in

our trial. In the previous (unblinded) trials comparing

ASD with conservative treatment alternatives,

13 32-34

the observed higher frequency of crossovers in the

conservatively treated patients has been interpreted as

evidence for the superiority of ASD over conservative

Table | Primary comparison of arthroscopic subacromial decompression versus diagnostic arthroscopy: outcomes of

trial at  month follow-up*. Values are mean (% CI) unless stated otherwise

Arthroscopic subacromial

decompression (ASD; n=)

Diagnostic arthroscopy

(DA; n=)

Between group

dierence (ASD v DA)† P value

Primary outcomes

Visual analogue scale score, at rest 5.3 (0.8 to 9.7) 9.9 (5.4 to 14.3) −4.6 (−11.3 to 2.1) 0.18

Visual analogue scale score, on arm activity 15.8 (9.4 to 22.2) 24.8 (18.4 to 31.2) −9.0 (−18.1 to 0.2) 0.054

Secondary outcomes

Constant-Murley score 77.9 (73.7 to 82.3) 73.7 (69.5 to 78.0) 4.3 (−2.0 to 10.5) 0.18

Simple shoulder test score 10.3 (9.7 to 10.9) 9.9 (9.3 to 10.5) 0.5 (−0.4 to 1.3) 0.29

15D score 0.92 (0.91 to 0.93) 0.92 (0.91 to 0.93) 0.00 (−0.02 to 0.02) 1.00

Proportion of participants able to return to

previous leisure activities‡

0.82 (0.72 to 0.92) 0.77 (0.66 to 0.88) 0.06 (−0.10 to 0.22) 0.45

Proportion of responders§ 0.95 (0.89 to 1.0) 0.91 (0.84 to 0.99) 0.04 (−0.06 to 0.14) 0.42

Patients’ satisfaction with treatment¶ 88.1 (82.9 to 93.3) 87.1 (81.9 to 92.3) 0.9 (−6.6 to 8.3) 0.82

No (%) complications and adverse eects** 3 (5) 2 (3) – –

*Higher score indicates desired (better) treatment outcome for all outcomes other than pain visual analogue scale score and complications, for which lower

score indicates better outcomes.

†Between group dierences may not exactly equal dierence in changes in score between ASD and DA groups because of adjustment for baseline

imbalance in mixed eects model.

‡Ability to return to previous leisure activities was assessed with question “Have you been able to return to your previous leisure activities?” (“yes” or “no”).

§Participants’ satisfaction with treatment outcome was elicited with question “How satised are you with the outcome of your treatment?” on a ve item

scale; participants who reported being very satised or satised were categorised as “responders.”

¶Participants’ global assessment of satisfaction with treatment was elicited with question “Are you satised with the treatment you have received?” on visual

analogue scale ranging from 0 (completely disappointed) to 100 (very satised).

**Complications directly related to interventions were registered.

VAS at rest

100

Months

VAS on arm activity

Baseline 36 12 24

100

Arthroscopic subacromial decompression

Exercise therapy

Fig | Primary outcomes of secondary comparison at

baseline and at , , , and  month follow-up. Visual

analogue scale (VAS) shoulder pain scores at rest and on

arm activity over  month follow-up period are shown.

VAS scales range from  to , with higher values

indicating more severe pain. Data are mean (% CI)

shown at follow-up time points

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treatment. However, we note that the decision to (re)

operate was made after unblinding of the treatment

group allocation, whereas the decision to unblind the

treatment group is made without awareness of the

treatment given to the patient. We thus consider the

frequency of “unblindings” a less biased measure of the

severity of participants’ symptoms than the frequency

crossovers.

In our trial, we found no statistically

signiﬁcant dierence in the frequency of unblindings

between the ASD and diagnostic arthroscopy groups

(6/59 in the ASD group versus 9/63 in the diagnostic

arthroscopy group; P=0.49).

Besides the placebo control, another obvious

strength of the ASD versus diagnostic arthroscopy

comparison was the ecacy or mechanistic design.

We used highly experienced surgeons and therapists

and isolated the critical therapeutic element of the

ASD procedure—the subacromial decompression—as

the only dierence between the two surgical groups

while carefully maintaining all other care as close

to identical as possible. In particular, we used very

stringent eligibility criteria to enrol—according to best

available evidence—only patients most likely to beneﬁt

from ASD. Classically, stringent eligibility criteria are

considered to decrease the external validity of a study.

Although our patient population was indeed highly

selected, as showcased by the lengthy recruitment

period needed despite three high volume centres,

we think that the use of stringent eligibility criteria

paradoxically increases the generalisability of our

ﬁndings. When ASD was proven futile under this best

case scenario, there is no reason to assume that it

would work better under less optimal circumstances

or in a more heterogeneous population. We also note

that our primary ﬁndings are robust, as the sensitivity

and subgroup analyses did not materially change the

ﬁndings of our primary analyses (tables S5 and S6 in

appendix 2). In essence, the duration or severity of

symptoms or the acromial anatomy—factors previously

asserted as potential modiﬁers of the eect of ASD—

did not have a hypothesised eect on the primary

outcomes (table S6 in appendix 2). Obviously, all our

subgroup analyses are at higher risk of bias and should

be considered only supportive, explanatory, and/or

hypothesis generating.

Some limitations warrant discussion. The number

of participants completing the entire two year follow-

up was 59 in both the ASD group and the diagnostic

arthroscopy group, below the pre-speciﬁed target of 68.

The high number of exclusions among the participants

allocated to surgery was primarily attributable to

unexpectedly poor sensitivity of magnetic resonance

arthrography in detecting rotator cu tears and

other pathology needing intervention other than

ASD. Although our sample size being below the pre-

speciﬁed target might prompt assertions that the study

is underpowered, we note that our point estimates

exclude clinically signiﬁcant treatment eects. In

essence, our ﬁndings are not based on absence of

evidence, as in an underpowered study, but rather on

evidence of absence of a clinically signiﬁcant treatment

beneﬁt. One may also criticise the validity of the chosen

minimal clinically important dierence threshold. At

the time of designing the trial, no evidence existed on

the appropriate minimal clinically important dierence

for patients with shoulder impingement syndrome, so

instead of being based on empirical data our estimate

for the minimal clinically important dierence (15

VAS points) was based on extensive review of the

literature in a wide range of dierent musculoskeletal

conditions. Reassuringly, some years after the launch

of our trial, a study exploring the minimal clinically

important dierence for the pain VAS in rotator cu

disease reported a point estimate of 14 VAS points.

Some evidence also suggests that bursectomy

alone (complete resection of the subacromial

Table | Secondary comparison of arthroscopic subacromial decompression versus diagnostic arthroscopy: outcomes

of trial at  month follow-up*. Values are mean (% CI)

Arthroscopic subacromial

decompression (ASD; n=)

Exercise therapy

(ET; n=)

Between group

dierence (ASD v ET)† P value

Primary outcomes

Visual analogue scale score, at rest 5.3 (0.6 to 10.0) 12.8 (8.4 to 17.3) −7.5 (−14.0 to −1.0) 0.023

Visual analogue scale score, on arm activity 16.0 (9.6 to 22.5) 28.1 (22.1 to 34.1) −12.0 (−20.9 to −3.2) 0.008

Secondary outcomes

Constant-Murley score 79.1 (74.7 to 83.4) 71.2 (67.0 to 75.3) 7.7 (1.6 to 13.9) 0.013

Simple shoulder test score 10.3 (9.7 to 10.9) 9.7 (9.1 to 10.2) 0.7 (−0.2 to 1.5) 0.12

15D score 0.91 (0.90 to 0.93) 0.91 (0.90 to 0.92) 0.00 (−0.02 to 0.02) 1.00

Proportion of participants able to return to

previous leisure activities‡

0.82 (0.72 to 0.92) 0.76 (0.65 to 0.86) 0.07 (−0.07 to 0.21) 0.31

Proportion of responders§ 0.95 (0.90 to 1.01) 0.90 (0.81 to 0.98) 0.06 (−0.04 to 0.16) 0.23

Patients’ satisfaction with treatment¶ 88.2 (82.8 to 93.5) 84.9 (79.9 to 89.8) 3.3 (−3.9 to 10.5) 0.36

No (%) complications and adverse eects** 3 (5) 3 (4) – –

*Higher score indicates desired (better) treatment outcome for all outcomes other than pain visual analogue scale score and complications, for which lower

score indicates better outcomes.

†Between group dierences may not exactly equal dierence in changes in score between ASD and DA groups because of adjustment for baseline

imbalance in mixed eects model.

‡Ability to return to previous leisure activities was assessed with question “Have you been able to return to your previous leisure activities?” (“yes” or “no”).

§Participants’ satisfaction with treatment outcome was elicited with question “How satised are you with the outcome of your treatment?” on a ve item

scale; participants who reported being very satised or satised were categorised as “responders.”

¶Participants’ global assessment of satisfaction with treatment was elicited with question “Are you satised with the treatment you have received?” on visual

analogue scale ranging from 0 (completely disappointed) to 100 (very satised).

**Complications directly related to interventions were registered.

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bursa) provides similar outcomes to subacromial

decompression (bursectomy accompanied by

resection of acromial bone) in patients with shoulder

impingement syndrome.

37-39

Acknowledging this,

while also appreciating that a rotator cu tendon tear

is considered a dierent clinical entity from shoulder

impingement and a potentially strong prognostic factor

for poor outcome, we were faced with a methodological

dilemma between the elimination of the presence of

a clinically relevant rotator cu tear versus possible

confounding caused by a need to carry minimal

resection of the subacromial bursal tissue to properly

visualise rotator cu tendon insertion. We chose to

prioritise the rotator cu tears; accordingly, bursa

was either bluntly stretched with trochar or resected

if adequate visualisation of the rotator cu insertion

could not be achieved otherwise. Bursal resection was

carried out in 18 (30%) of the 63 participants in the

diagnostic arthroscopy group; in all but three cases,

the resection was minimal. To assess the possible eect

of this bursal tissue resection on our ﬁndings, we did a

pre-speciﬁed post hoc analysis (table S2 in appendix

2). Although underpowered, the analysis did not show

any statistically signiﬁcant dierences in the primary

outcomes between patients who had resection carried

out and those who did not. If anything, the observed

marginal dierences favoured no resection.

Furthermore, on the decision to carry out bursal

resection, despite our thorough preoperative screening

that included both careful clinical examination and

magnetic resonance imaging with contrast, roughly

4% (6/134) of patients having shoulder arthroscopy

had to be excluded owing to a rotator cu tear found

at arthroscopic examination. Conventional wisdom

dictates that the preferred treatment for rotator cu

tears is to repair partial thickness tears that involve

more than 50% of the tendon thickness (grade III),

whereas those that involve less than 50% of the

tendon thickness (grades I and II) can be treated

with debridement, with or without accompanying

subacromial decompression.

In this trial, we chose

to adhere to this treatment strategy, although its

veracity—the need to repair grade III/full thickness

rotator cu tears of degenerative origin—can be

questioned according to the most recent high quality

evidence.

Finally, a frozen shoulder is considered

a potential complication of the treatment of patients

with shoulder impingement syndrome, particularly of

shoulder arthroscopy.

However, at the early stages

of the disease, the clinical presentation of a slowly

developing frozen shoulder can mimic subacromial

impingement, so a legitimate concern exists that some

of the participants we labelled as having developed a

frozen shoulder as a complication of treatment might

actually initially have been misdiagnosed as having

shoulder impingement syndrome while actually

having a frozen shoulder in the ﬁrst place. In the end,

the number of patients labelled having developed a

frozen shoulder was small in all groups (two, three,

and one in the exercise therapy, ASD, and diagnostic

arthroscopy groups, respectively).

In addition to our primary sham surgery controlled

ecacy comparison between ASD and diagnostic

arthroscopy, our study also included a pragmatic,

exploratory secondary comparison between surgical

and non-operative care (ASD versus exercise therapy).

In apparent contrast to four previous, similar

randomised trials that found no beneﬁt of ASD over

various exercise therapy regimens,

13 32-34

we observed

a statistically signiﬁcant beneﬁt of ASD over exercise

therapy in both our primary outcomes. Although

the beneﬁt did not exceed the pre-speciﬁed minimal

clinically important dierence (15 point change in

VAS) in either of the two primary outcomes (table

3), a potential beneﬁcial eect of ASD over exercise

therapy cannot be completely ruled out, as the

conﬁdence intervals for the mean dierence in pain

VAS on arm activity include the minimal clinically

important dierence. In interpreting the ﬁndings for

ASD versus exercise therapy, one needs to appreciate

several concerns related to this comparison. Firstly,

this is not a blinded comparison as the participants

are naturally aware of the treatments given and thus

the results are inevitably confounded by potentially

dierent placebo eects related to the surgical and

nonoperative care. Secondly, a clear prognostic

imbalance exists between the two interventions

owing to the exclusions carried out before the second

randomisation in the group primarily allocated to

surgery: 17 (12%) of the 139 participants allocated

to the two surgical groups were excluded without

any comparable exclusions from the exercise

therapy group. Thus, the ASD versus exercise

therapy comparison is likely to be biased in favour

of ASD owing to the systematic removal of patients

with likely poorer prognosis. Finally, the ASD and

exercise therapy groups cannot be considered fully

comparable owing to dierences in the treatment

given. The progressive exercise therapy regimen

carried out in the exercise therapy group is dierent

from the postoperative rehabilitation carried out

by patients in the ASD group, as surgically treated

patients need time to recover from the initial surgical

trauma while also being subject to some degree of

postoperative immobilisation, extended sick leave,

and modiﬁcations in pain medication and activities.

In summary, the results of our secondary comparison

(ASD versus exercise therapy) should be interpreted

with caution, as we do not know whether exercise

therapy is poorer because of the lack of comparability

of the groups, because exercise therapy is truly a less

eective treatment, or a mixture of both.

Conclusions and policy implications

The results of this randomised, placebo surgery

controlled trial show that arthroscopic subacromial

decompression provides no clinically relevant beneﬁt

over diagnostic arthroscopy in patients with shoulder

impingement syndrome. The ﬁndings do not support

the current practice of performing subacromial

decompression in patients with shoulder impingement

syndrome.

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AUTHOR AFFILIATIONS

Department of Orthopedics and Traumatology, Helsinki University

Hospital, Töölö hospital, Helsinki, Finland

National Institute for Health and Welfare, Centre for Health and

Social Economics, Helsinki, Finland

Finnish Centre for Evidence-Based Orthopedics (FICEBO),

Department of Orthopedics and Traumatology, University of

Helsinki, Helsinki, Finland

Department of Orthopedics and Traumatology, Tampere University

Hospital, TAYS Hatanpää, Tampere, Finland

Fysios Finlayson, Physiotherapy Centre Kunnon Klinikka Oy,

Tampere, Finland

Department of Orthopedics and Traumatology, Helsinki University

Hospital, Jorvi Hospital, Espoo, Finland

Terveystalo, Helsinki, Finland

Pohjola Hospital, Helsinki, Finland

Department of Clinical Sciences Lund, Orthopedics, Lund

University, Lund, Sweden

The FIMPACT investigators thank Pekka Paavolainen and Markku

Järvinen for their pivotal contributions and support in the early phases

of the planning and execution of the trial, and Ian Harris and Alan

Cassels for their critical comments and linguistic expertise.

Contributors: The corresponding author attests that all listed authors

meet authorship criteria and that no others meeting the criteria have

been omitted. MP and TJ were co-principal investigators. MP, AM, ST,

and TJ conceived and designed the study, and JI also contributed to

the design. KK, JK, IS, and VS recruited most of the patients, FIMPACT

Investigators followed up the patients. MP, AM, ST, KK, and TJ collected

the data. ST designed the database and cleaned the data. ST, TJ, and

JR contributed to the study analysis plan and data analysis. MP, ST,

KK, AM, JR, and TJ participated in the analysis and interpretation of

the data, JR led the blinded data analysis process. TJ, ST, KK, MP, JR,

and AM draed the manuscript. All authors contributed to nal data

interpretation and contributed to and approved the nal dra of the

manuscript. TJ obtained funding. MP is the guarantor.

Steering Committee: MP, TJ, AM, and ST.

Writing Committee: TJ, ST, MP, KK, and AM.

Participating investigators (FIMPACT Investigators): Mika Paavola,

Teppo Järvinen, Simo Taimela, Antti Malmivaara, Kari Kanto.

Participating clinical sites: Helsinki University Hospital, Jorvi

Hospital: Kalevi Hietaniemi, Juha Kalske, Vesa Lepola, Jyrki Salmenkivi,

Sikri Tukiainen; Helsinki University Hospital, Herttoniemi Hospital:

Jarkko Pajarinen, Mikko Salmela, Vesa Savolainen, Ilkka Sinisaari;

Hatanpää City Hospital, Tampere: Timo Järvelä, Kari Kanto, Janne

Lehtinen, Mikael Salmela.

FIMPACT Methods Centre: Leena Caravitis, Sari Karesvuori, Pirjo

Toivonen (project management), Mathias Bäck (data management),

Ville Haapamäki (imaging), Jari Inkinen (physiotherapy), Esa Läärä

(randomisation), Harri Sintonen (health related quality of life

outcomes).

Funding: The FIMPACT trial was supported by the Sigrid Juselius

Foundation, the state funding for university level health research

(Tampere and Helsinki University Hospitals), the Academy of Finland,

and the Jane and Aatos Erkko Foundation. The funders of the study

had no role in study design, data collection, data analysis, data

interpretation, or writing of the report. Sponsors had no access to the

data and did not perform any of the study analysis. The corresponding

authors had full access to all the data in the study and had nal

responsibility for the decision to submit for publication.

Competing interests: All authors have completed the ICMJE uniform

disclosure form at www.icmje.org/coi_disclosure.pdf (available on

request from the corresponding author) and declare: no support from

any organisation for the submitted work other than those described

above; ST reports personal fees from Evalua group of companies,

personal fees from DBC group of companies, and personal fees from

insurance companies, outside the submitted work; KK reports an

honorarium for a lecture from Linvatec, outside the submitted work;

TLNJ reports an honorarium for a lecture on osteoporosis from AMGEN

(donated to AllTrials campaign); no other relationships or activities

that could appear to have influenced the submitted work.

Ethical approval: This study was approved by the Institutional Review

Board of the Pirkanmaa Hospital District (R04200; 28 December

2004), and informed consent was obtained from all patients.

Data sharing: FIMPACT data are not publicly available owing to data

privacy issues, but access to the anonymised dataset can be obtained

from the corresponding author on reasonable request.

Transparency: The lead author arms that this manuscript is

an honest, accurate, and transparent account of the study being

reported; that no important aspects of the study have been omitted;

and that any discrepancies from the study as planned (and, if relevant,

registered) have been explained.

This is an Open Access article distributed in accordance with the

terms of the Creative Commons Attribution (CC BY 4.0) license, which

permits others to distribute, remix, adapt and build upon this work,

for commercial use, provided the original work is properly cited. See:

http://creativecommons.org/licenses/by/4.0/.

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Appendix 1

Appendix 2

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