Results of the search

We conducted searches up to August 2020. We screened a total of 1278 records from the following databases: Cochrane Bone, Joint and Muscle Trauma Group Specialised Register (26 records), CENTRAL (208 records), MEDLINE (462 records), Embase (227 records), CINAHL Plus (63 records), AMED (75 records), WHO ICTRP (138 records), and ClinicalTrials.gov (79 records) (Table 1).

Among all searches, we identified a total of 47 articles for potential inclusion, for which we obtained full reports where possible. After linking any references pertaining to the same study under a single study ID, we identified 40 studies. Upon further analysis, we included 17 studies (Abdel Sabour 2018; Adolfsson 1996; Farzad 2014; Geetha 2014; Gelberman 1991; Gulke 2018; Hagberg 2000; Kneafsey 1994; Ozkan 2004; Poorpezeshk 2018; Rigo 2017; Scavenius 2000; Silva 2003; Stenekes 2009; Trumble 2010; Uday Raj 2018; Vialaneix 2003). We excluded 12 studies (Bainbridge 1994; Baktir 1996; Horsfall 2016; ISRCTN80184286; Kingston 2014; NCT01939808; Peck 1998; Peck 2014; Percival 1989; Stegink Jansen 1990; Xiao 2018; Yildirim 2010). Four studies are awaiting classification (Kitis 2009; Liu 2004; Naude 2019; Yavari 2009). We found seven ongoing studies from searching the WHO ICTRP (CTRI/2019/01/016821; IRCT201310138177N8; IRCT20150721023277N7; NCT03812978; NCT03850210; NCT04237415; NCT04385485). A flow diagram summarising the study selection process is shown in Figure 1.

Figure 1

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Diagram showing the flow of studies through the study selection process

Translation from German to English was obtained for one included study (Gulke 2018).

Included studies

Full descriptions of each of 17 included trials is provided in the Characteristics of included studies table. A summary of the each study's characteristics and participant details is included in Table 2.

Excluded studies

We excluded 12 studies after review of the full‐text publication (Bainbridge 1994; Baktir 1996; Horsfall 2016; ISRCTN80184286; Kingston 2014; NCT01939808; Peck 1998; Peck 2014; Percival 1989; Stegink Jansen 1990; Xiao 2018; Yildirim 2010). Two studies (Kingston 2014; Xiao 2018) were excluded as they included participants who may have had a flexor tendon injury; however, separate data were not available for only the participants with flexor tendon injuries. Two studies found through a trial registry were abandoned before recruitment started (ISRCTN80184286; NCT01939808). The main reason for excluding the other eight studies was because a non‐randomised study design was used.

Allocation

We rated generation of the randomisation sequence to be at low risk of bias in 10 trials (Abdel Sabour 2018; Adolfsson 1996; Farzad 2014; Geetha 2014; Gulke 2018; Ozkan 2004; Poorpezeshk 2018; Rigo 2017; Trumble 2010; Uday Raj 2018). Three of these trials used a random envelope draw of cards created for the study (Adolfsson 1996; Rigo 2017; Trumble 2010). One trial used a computerised random number generator (Farzad 2014); two studies used stratified block randomisation (Gulke 2018; Poorpezeshk 2018); one used random card selection (Geetha 2014); one used a random number table (Ozkan 2004); and one study used a lottery system (Uday Raj 2018). One study used a quasi‐randomisation sequence by allocating participants to groups based on whether they were born in an even or odd number month (Gelberman 1991). Six studies did not clearly report the randomisation process used (Hagberg 2000, Kneafsey 1994, Scavenius 2000; Silva 2003; Stenekes 2009; Vialaneix 2003), and attempts to obtain this information from trial authors were unsuccessful.

Allocation concealment was rated to be at low risk of bias in five trials (Abdel Sabour 2018; Adolfsson 1996; Geetha 2014; Rigo 2017; Trumble 2010). Allocation concealment was rated to be at high risk of bias in Gelberman 1991, where participants were placed in one of two study groups depending upon the month in which they were born. The remaining 11 studies were rated as having unclear risk of bias, as they did not report a clear method for concealing the allocation sequence (Farzad 2014; Gulke 2018; Hagberg 2000; Kneafsey 1994; Ozkan 2004; Poorpezeshk 2018; Scavenius 2000; Silva 2003; Stenekes 2009; Uday Raj 2018; Vialaneix 2003). Attempts to clarify this with trial authors were unsuccessful.

Blinding

Five studies were rated as having low risk of performance bias (Farzad 2014; Geetha 2014; Gelberman 1991; Ozkan 2004; Scavenius 2000). Three studies achieved blinding of both participants and study personnel for self reported outcomes and were rated as having low risk of bias as these studies did not include any patient self reported outcomes (Farzad 2014; Geetha 2014; Gelberman 1991). One study (Ozkan 2004) achieved blinding of the participants, but it is unlikely that the personnel were blinded due to the nature of the intervention. Scavenius 2000 was rated as having low risk of bias as none of the outcomes were self‐reported or measured by the treatment provider. Eight included studies were not able to achieve participant blinding due to the nature of interventions and were rated as having a high risk of bias (Abdel Sabour 2018; Adolfsson 1996; Gulke 2018; Rigo 2017; Silva 2003; Stenekes 2009; Trumble 2010; Vialaneix 2003). Four studies (Hagberg 2000; Kneafsey 1994; Poorpezeshk 2018; Uday Raj 2018) were classified as having an unclear risk of bias regarding blinding of participants and personnel. One study (Uday Raj 2018) reported that participants were blinded from which group they were in, but were aware they were receiving one of the interventions. Due to the nature of the intervention, care providers could not be blinded to the intervention. It is not known how successful the blinding of the participants was considering the care providers could not be blinded. It was classified as unclear risk as attempts to clarify this with trial authors were unsuccessful. Another study with an unclear rating was Poorpezeshk 2018, which stated in the clinical trials registry that the study was "double‐blinded". However it is unclear where this blinding occurred. Due to the nature of the interventions, it is possible that the participants could have been blinded to the interventions, but this was not explicitly stated.

Blinding of outcome assessment (detection bias) was assessed in two categories, for self‐reported measures and measurements recorded by observers. For self‐reported measures, where these were available, blinding was considered to be low risk for Ozkan 2004 only. It was unclear whether blinding was achieved in two studies that did have self‐reported outcomes (Abdel Sabour 2018; Poorpezeshk 2018). In these instances, an explicit statement regarding assessor blinding was not included in the trial description, and attempts to clarify this issue with trial authors were unsuccessful. The risk was considered to be high for five studies (Adolfsson 1996; Gulke 2018; Rigo 2017; Stenekes 2009; Trumble 2010). The other nine studies did not include any self‐reported outcomes.

Blinding of outcome assessment (detection bias) for objective outcomes was deemed to be low risk of bias in four included studies (Farzad 2014; Geetha 2014; Ozkan 2004; Poorpezeshk 2018). It was unclear whether blinding of outcome assessors was achieved in nine studies (Abdel Sabour 2018; Gulke 2018; Hagberg 2000; Kneafsey 1994; Scavenius 2000; Silva 2003; Stenekes 2009; Uday Raj 2018; Vialaneix 2003). In these instances, an explicit statement regarding assessor blinding was not included in the trial description, and attempts to clarify this issue with trial authors were unsuccessful. The risk of bias from unblinded outcome assessors was considered to be high for four studies (Adolfsson 1996; Gelberman 1991; Rigo 2017; Trumble 2010). Adolfsson 1996 only blinded the assessors for the final outcome assessment at 24 weeks, but not at the earlier time points of assessment. Blinding of outcome assessors was not undertaken in the other three studies, which clearly reported that measurement of outcomes was performed by the treating therapists (Gelberman 1991; Rigo 2017; Trumble 2010).

Incomplete outcome data

Seven studies did not clearly report if any of the participants were lost to follow‐up (Gelberman 1991; Hagberg 2000; Kneafsey 1994; Ozkan 2004; Scavenius 2000; Silva 2003; Vialaneix 2003). Of the 10 studies that reported the loss to follow‐up of the participants, three included trials achieved complete follow‐up of the data set (Farzad 2014; Stenekes 2009; Uday Raj 2018). Only five studies reported number of participants lost to follow‐up for each group (Abdel Sabour 2018; Geetha 2014; Poorpezeshk 2018; Rigo 2017; Trumble 2010). Two studies (Adolfsson 1996; Gulke 2018) reported the total number of participants in the study lost to follow‐up (i.e. no specific reporting of the number lost in each group). The time interval when the loss to follow‐up occurred was not clearly reported. The biggest loss to follow‐up was noted by Poorpezeshk 2018, in which 20 participants were lost to follow‐up, all from the control group. Studies were examined for attrition bias at three time intervals: less than three months, three to six months, and greater than six months.

For outcomes measures under three months, we rated five studies as having low risk of bias (Abdel Sabour 2018; Farzad 2014; Geetha 2014; Rigo 2017; Uday Raj 2018). Seven studies were rated as unclear risk either due to insufficient data being provided in the study publications and no further data being received from the trial authors upon request (Gulke 2018; Hagberg 2000; Kneafsey 1994; Ozkan 2004; Stenekes 2009; Trumble 2010; Vialaneix 2003). Two studies did not collect data at this time point (Gelberman 1991; Silva 2003). We rated two studies at high risk of bias (Adolfsson 1996; Poorpezeshk 2018). In Adolfsson 1996, the number of participants and digits contributed to the study was provided via correspondence from the study authors. The 82 participants who were included in the analysis did not include 14 drop‐outs, eight of whom were lost to follow‐up. It is unclear from which group the 14 drop‐outs were excluded from or the reasons for lost to follow‐up. In Poorpezeshk 2018, the loss to follow‐up was 34% in the control group (with no dropouts in the intervention group), which may have influenced the effect size.

For outcomes measured between three and six months, we rated two studies as having low risk of bias (Geetha 2014; Rigo 2017). We rated six as having unclear risk of bias due to insufficient data being provided in the study publications and no further data being received from the trial authors upon request (Abdel Sabour 2018; Gulke 2018; Hagberg 2000; Kneafsey 1994; Trumble 2010; Vialaneix 2003). One study, Adolfsson 1996, was rated as having high risk of bias, as it is not clear how the dropouts were accounted for in the analysis or which groups they were in.

Only six studies measured outcomes beyond six months (Gelberman 1991; Hagberg 2000; Rigo 2017; Scavenius 2000; Silva 2003; Trumble 2010). Of these, two were rated to be at low risk of bias for completeness of outcome data (Rigo 2017; Trumble 2010). Three studies rated as having an unclear risk of bias did not provide sufficient information in their publications and attempts to obtain this were unsuccessful (Hagberg 2000; Scavenius 2000; Silva 2003). Gelberman 1991 was rated to be at high risk of bias as it was not clear how many participants dropped out of the study, and only those who were a minimum of six months following surgery were included.

Selective reporting

We rated two studies as having a low risk of bias for selective reporting (Abdel Sabour 2018; Poorpezeshk 2018). We rated seven studies as having an unclear risk of bias for selective reporting due to insufficient information being provided in the publications for the studies, and attempts to obtain this information from the trial authors were unsuccessful (Farzad 2014; Gelberman 1991; Gulke 2018; Ozkan 2004; Rigo 2017; Scavenius 2000; Trumble 2010). We assessed eight studies as having a high risk of bias for selective outcome reporting, as they did not specify results for some of the outcomes listed in the methods section of the publication, or in a published protocol (Adolfsson 1996; Geetha 2014; Hagberg 2000; Kneafsey 1994; Silva 2003; Stenekes 2009; Uday Raj 2018; Vialaneix 2003).

We compared the outcomes reported to their study design as reported on the clinical trial register where available. We were only able to retrieve trial registration documents for three studies (Abdel Sabour 2018; Geetha 2014; Poorpezeshk 2018).

Other potential sources of bias

We rated six studies to be at high risk of other bias (Abdel Sabour 2018; Geetha 2014; Rigo 2017; Scavenius 2000; Stenekes 2009; Uday Raj 2018), mainly because of unit of analysis errors. However, the unit of analysis was not always clearly stated when reporting outcomes in some of the included studies. Some measurements like grip and pinch strength are recorded per hand, whereas other outcomes may be reported per digit or per tendon repair (that is, one or more tendons can be repaired in the same digit). This means that it is very easy for a unit of analysis error to occur and can lead to errors in analysis and misleading interpretation of the study's findings. Five studies clearly reported the unit of analysis for their outcome measures and four were assessed as being at low risk of bias (Adolfsson 1996; Farzad 2014; Gelberman 1991; Trumble 2010). The other study, Rigo 2017, was rated at high risk of other bias, as strength was analysed as a finger level outcome, rather than hand/participant level outcome; hence, a unit of analysis error occurred. Eight studies were rated as having an unclear risk of bias, due to insufficient information being provided to make a judgement (Gulke 2018; Hagberg 2000; Kneafsey 1994; Ozkan 2004; Poorpezeshk 2018; Silva 2003; Uday Raj 2018; Vialaneix 2003). Four other studies were identified as being at high risk of bias and it appears as if an unit of analysis error was likely (Abdel Sabour 2018; Geetha 2014; Hagberg 2000; Stenekes 2009). Like Rigo 2017, Geetha 2014 analysed grip strength for each of the digits included in the study; however, grip strength is calculated per hand/participant and this likely to have resulted in an unit of analysis error. Similarly, it is unclear whether the number of ruptures that occurred were per person, digit or tendon in Hagberg 2000. In Stenekes 2009, pinch strength was measured for each affected digit; however, the unit of analysis appears to be affected tendons. In Abdel Sabour 2018, the unit of analysis is tendons not fingers; however, measurements such as range of motion, scar adhesion and DASH are measured at the finger or person level. A unit of analysis error appears to have occurred for these outcomes as analyses appear to have been conducted per tendon.

Geetha 2014 additionally reported outcomes of movement and strength in non‐standardised categories. These ranges for movement and strength were not uniform between the groups and not recorded at the same time interval. This made it difficult to compare the outcomes between the groups. Further, Rigo 2017 recorded grip and pinch strength as a percentage of the contralateral side, with no consideration made in the analysis for hand dominance.

Scavenius 2000 was rated as high risk as the intervention groups also received different surgical treatments which may have influenced the results.

Suitability of trials for meta‐analysis

Most comparisons were tested by single trials only. Of the two comparisons tested by two and three trials respectively, we considered it appropriate to pool only one outcome (tendon rupture).

In addition, 11 (of 17) trials reported data that could not be included in the statistical analysis, for several reasons:

• omission of measures (or errors) of variability (e.g. SDs) in reports of continuous outcomes (Adolfsson 1996; Hagberg 2000; Poorpezeshk 2018; Scavenius 2000; Trumble 2010; Vialaneix 2003);

• conclusions stated without support for point estimates, or frequency counts of outcomes (Hagberg 2000; Stenekes 2009);

• lack of reporting of the time point of measurement (Stenekes 2009);

• conclusion stated with no point estimate, or data for either group (Adolfsson 1996; Hagberg 2000; Kneafsey 1994; Scavenius 2000; Trumble 2010; Uday Raj 2018; Vialaneix 2003); and,

• data were skewed and reported in a format not able to be entered into RevMan 5 (Abdel Sabour 2018); and,

• comparison of data between groups were measured at different time points or used different outcome definitions (Geetha 2014).

Early active flexion plus controlled passive exercise regimen versus early controlled passive exercise regimen alone

One trial (Rigo 2017), which randomised 53 participants with 73 zone I to III FDP tendon repairs, evaluated the addition of active flexion exercises to a controlled passive exercise regimen comprising a modified Kleinert regimen, which was used in both intervention groups. Both active and passive only groups commenced the exercise regiments at one day post‐surgery.
Outcomes were assessed post‐surgically at one and two months (for ROM only) and at 3, 6 and 12 months (for all outcome measures). The outcomes assessed included functional assessment using a patient reported outcome measure (injured finger use in activities of daily living (ADL) using a visual analogue scale); active finger range of motion (Strickland‐Glogovac and Tang classifications); adverse events (number of participants with tendon ruptures, complex regional pain syndrome, wound dehiscence, finger oedema) and strength (grip and pinch strength).

The main outcomes for this comparison, for which there is only very low‐certainty evidence, are presented in summary of findings Table 1. For all outcomes, the evidence was downgraded two levels due to very serious risk of bias and one level due to serious imprecision, reflecting wide confidence intervals, confidence intervals crossing the line of no effect, or both. The evidence was also downgraded one level for serious indirectness for the functional assessment outcome used in this trial; there is also no information on the minimally important difference for this outcome. Unit of analysis problems resulting from the reporting by digit instead of participant means that the confidence intervals are narrower than they should be. Additionally, although the trial authors provided us with mean and SD data for continuous outcomes, it should be noted these were reported as median (Med) and interquartile range (IQR) data in the trial report. We also present the latter for the ADL results because there were greater disparities between these and the mean and SD data for this outcome.

Early active flexion plus passive exercise regimen (Strickland and Small protocol) versus controlled passive exercise regimen (Kleinert protocol)

One trial, Vialaneix 2003, randomised 35 participants who had a primary flexor tendon repair in zone II into two intervention groups listed in the heading. At the third post‐operative day, 16 participants randomised to the active group commenced early passive flexion, active flexion and active extension within the orthosis using the Strickland exercise regimen (Strickland 2000; Small 1989) and 19 participants commenced early controlled passive mobilisation using rubber band traction, according to the Kleinert regimen (Kleinert 1967).

Outcomes were measured at an average of 18 months following the surgery, but also reported at 8, 12 and 24 weeks. Outcomes measured included active finger range of motion (Strickland classification); fingertip to palm distance (not an outcome of interest for this review); adverse events (subsequent surgical procedures) and return to previous activity (total duration of time off work after the surgery for a subgroup of 15 manual workers).

This trial was reported as a conference abstract only and provided very limited and incomplete data. The certainly of the available evidence for this comparison is very low, reflecting downgrading two levels for very serious risk of bias and two levels for very serious imprecision.

Active flexion plus active extension exercise regimen (plus modified Kessler suture surgical technique) versus passive flexion plus active extension exercise regimen (plus grasping suture and external pull‐out know surgical technique)

Scavenius 2000 randomised 39 participants with zone I and II flexor tendon repairs into either an active flexion plus active extension exercise regimen group (active group) or passive flexion plus active extension exercise regimen group (passive group). Each group also received a different surgical technique with the active group having a Modified Kessler suture (Ti‐cron 4.0) repair, and the passive group receiving a grasping suture (Prolene 2.0) and external pull‐out knot technique. Participants had flexor tendon repairs to the thumb (n = 6) or digits (n = 33) in flexor tendon zone I or II. The active group (n = 20) also performed active extension exercises but performed active flexion exercises (instead of passive) which was described as a Mantero protocol. The passive group (n = 19) performed active extension and controlled passive flexion exercises (using a protocol reported by study authors to have been developed "by May E. et al").

The outcomes assessed at one year following surgery included active finger range of motion (TAM and Strickland classification for the FDP repairs of the digits only; that is, this outcome was not calculated for the thumb tendon repairs) and adverse events (tendon ruptures, scar adhesions requiring tenolysis surgery).

This trial was reported as a conference abstract only and provided very limited and incomplete data. Data were missing for the number of participants in each group in the analyses and no measures of variability were provided for range of motion. The certainly of the available evidence for this comparison is very low, reflecting downgrading two levels for very serious risk of bias, two levels for very serious imprecision and one level for serious indirectness (as the groups received different surgical techniques).

Active flexion exercise regimen versus controlled passive exercise regimen

One trial, Hagberg 2000, which was reported in a published abstract only, randomised 100 participants who had direct tendon repair for zone II lacerations in 108 digits. They compared an early active mobilisation group (active group) with an early controlled passive mobilisation using rubber band traction group (controlled passive group). The exercise regimen and orthosis were continued for three weeks following the tendon repair, after which participants were allowed to commence active mobilisation. No further details on the trial participants, including the numbers in each group, were provided.

The outcomes reported in the abstract were limited to active finger range of motion (TAM and DIP joint flexion) and adverse events (tendon ruptures; extension deficit) at one year. The data were incomplete and unusable and it is unclear whether the results applied to participants or digits. The certainly of the available evidence for this comparison is very low, reflecting downgrading two levels for very serious risk of bias and two levels for very serious imprecision.

Active exercise regimen versus immobilisation regimen

One study, Silva 2003, compared an early active exercise regimen (active group) with an immobilisation regimen (immobilisation group) following a zone II flexor tendon repairs in 84 people (152 tendons). Both groups received a dorsal blocking orthosis to protect the flexor tendon repair for three weeks following surgery. The active group commenced an exercise programme 12 hours after surgery. The program consisted of 10 hourly motions of active flexion‐extension during a 16 hour waking day. The immobilisation group did not perform any exercises in the orthosis. After three weeks, the orthosis was discarded by both groups.

Outcomes were evaluated at a mean of 22 months post surgery (range 12 to 36 months). Outcomes assessed included finger range of motion (to calculate outcomes as per the IFSSH and Strickland classifications (described in Table 4) and adverse events (indication for tenolysis surgery; tendon ruptures and repair of these).

The main outcomes for this comparison, for which only very low certainty evidence is available, are presented in summary of findings Table 2.

Early place and hold progressed to tendon gliding exercise regimen versus early passive progressed to active exercise regimen

One randomised study of 30 participants with zone V flexor tendon repairs evaluated the benefits between two types of multiple treatment exercise regimens (Uday Raj 2018). One group received of early mobilisation with place and hold exercises commenced in the first week which progressed to a graduated tendon gliding exercise program at four weeks (place and hold group). The second intervention group received a passive exercise regimen which was progressed to full active exercises of all finger joints at four weeks (passive group). Both groups received the same standard hand therapy treatments and both were placed in dorsal blocking splints (although at different positions for the wrist‐ place and hold at 20 to 30 degrees and passive at 45 to 50 degrees).

Outcomes were evaluated at 4 and 12 weeks for range of motion; and at 12 weeks for grip strength. Outcomes included active finger range of motion (TAM); active finger tip to distal palmar crease distance (not an outcome of interest for this review); wrist active range of motion (not an outcome of interest for this review); adverse events (tendon ruptures) and strength (grip strength measured using a Jamar Dynamometer). The certainly of the available evidence for this comparison is very low, reflecting downgrading by two levels for very serious risk of bias, two levels for very serious imprecision for tendon rupture and one level for serious indirectness, reflecting the inadequate description of outcome assessment.

Place and hold exercise regimen versus controlled passive exercise regimen

Three heterogeneous trials compared place and hold exercise (place and hold group) versus controlled passive exercise (controlled passive group) (Abdel Sabour 2018; Farzad 2014; Trumble 2010).

Abdel Sabour 2018 recruited 33 participants (45 tendons) following a 2‐strand flexor tendon repair; this study included zones I, II and II flexor tendon injuries. Both groups were placed in a dorsal blocking orthosis with the wrist positioned in 20 degrees flexion and MCP joints in 70 degrees flexion. Exercises commenced three days following the repair. The place and hold exercise regimen consisted of passive flexion of the affected finger and then the participant tried to maintain the flexed posture through contraction of the involved muscle for five seconds. Controlled passive exercise regimen consisted of passive finger flexion achieved by the modified Kleinert rubber band traction system. Both groups performed additional active extension plus passive range of motion of each digit. The place and hold group were allowed to progress to active wrist tenodesis glides but the time interval has not been specified. They performed 25 repetitions of each exercise every waking hour for the first six weeks post‐surgery. At six weeks, the orthosis was discarded. Outcomes, which were assessed from six weeks up to six months, included functional assessment using a patient reported outcome measure (DASH score); adverse events (tendon rupture; scar adherence; flexion contracture; extension lag) and satisfaction with the result of the surgery.

Farzad 2014 randomised 54 participants (64 digits; 108 tendons) with zone II flexor tendon injuries into the two exercise regimen groups. Participants in both groups were placed in a dorsal blocking orthosis with their wrist positioned at 0 to 30 degrees of flexion and their MCP joints in 70 to 90 degrees flexion. Exercises were commenced three days following a 2‐strand flexor tendon repair. Participants of the place and hold group were advised to passively flex their fingers using the other hand with their wrist in 30 degrees of extension (out of the orthosis), and then hold the finger position actively for 3 to 5 seconds, performing 10 repetitions four times a day. In the controlled passive group, flexion was caused by rubber band traction within the dorsal blocking orthosis. Patients performed active finger extension within the dorsal blocking orthosis, performing 10 repetitions every waking hour. At three weeks, both groups progressed to active exercises. Outcomes, which were assessed at eight weeks by an independent blinded assessor, included active finger range of motion (TAM) of PIP and DIP joints combined, Strickland classification (described in Table 4) and adverse events (tendon ruptures).

Trumble 2010 randomised 103 participants (119 digits) who had undergone 4‐strand zone II flexor tendon repair to a place and hold regimen using a tenodesis orthosis or to a passive exercise regimen using an orthosis with rubber band traction. Participants of the place and hold group were placed in a dorsal blocking orthosis for six weeks and were also provided with a tenodesis orthosis (using a wrist hinge) to perform exercises during the first four weeks post‐operation. Place and hold finger exercises were initiated on day three, active flexor tendon gliding exercises at week four, and composite wrist and finger flexion exercises were introduced at week five post‐surgery. Participants of the controlled passive group performed a combination of Kleinert and Duran protocols. This included being placed in a rubber band traction orthosis and coming out of the orthosis to perform passive flexion‐extension and active interphalangeal extension during the first three weeks post‐operation. Place and hold exercises were introduced at three weeks post‐operation and active finger flexion commenced at six weeks. Range of motion and flexion contracture were evaluated at 6, 12, 26 and 52 weeks. All other outcomes were assessed at one year post‐surgery. These included functional assessment using a patient‐reported outcome measure (DASH score); active finger range of motion (PIP and DIP joints); adverse events (tendon ruptures, flexion contracture); return to previous activity (total days from injury to return to work on full duties); functional assessment using an objective measure (Jebsen‐Taylor hand function score, Perdue Pegboard test); satisfaction with the result of the surgery (numerical analogue scale from 1 (dissatisfied) to 10 (completely satisfied).

The main outcomes for this comparison, for which only very low certainty evidence is available, are presented in summary of findings Table 3.

Early passive flexion exercise regimen (modified Duran protocol) versus early controlled passive exercise regimen (modified Kleinert protocol)

Kneafsey 1994 compared controlled passive flexion exercise regimen using a modified Duran, Strickland and Glogovac protocol (passive group) with a controlled passive flexion plus active extension using a modified Kleinert protocol exercise regimen (controlled passive group) in 112 participants with either zones I, II or III tendon lacerations. Participants in the passive group performed isolated and composite flexion in the orthosis without the rubber band traction, and both active and passive extension within the orthosis. Participants in the controlled passive group performed active extension exercises, and fingers were maintained in passive flexion using rubber band traction orthosis between exercises. The sole report of this trial was a published conference abstract reporting an interim analysis of the first 80 participants.

Outcomes measured, up to a possible six months, included active finger range of motion and strength (power grip, pinch grip and maximum finger pressure) measured using a Jamar dynamometer. No data were provided and the timing of the follow‐up to which statistical significance testing applied is unclear.

Unrestricted activity at 8 weeks post‐surgery versus unrestricted activity at 10 weeks post‐surgery

Adolfsson 1996 randomised 96 participants (106 digits) with zone II flexor tendon lacerations to either unrestricted hand activity commenced at eight versus ten weeks following surgery. Results were reported for 82 participants (91 digits). All participants received standardised interventions for the first six weeks, which included a forearm based orthosis extending to the PIP joint; initial four weeks of passive flexion with rubber band traction and active extension exercises within the orthosis; followed by two weeks of active exercises within the orthosis. The participants were then randomised at six weeks into the two different programmes that advised a gradual increase in loading to unrestricted activities to be commenced at either eight weeks (8‐week group) or ten weeks (10‐week group).

In Adolfsson 1996, active range of motion data and distance from the fingertip and middle of the pulp to the distal palmar crease data were used to calculate the Buck‐Gramcko (Buck‐Gramcko 1976), Louisville (Lister 1977) and Tsuge (Tsuge 1977) classification systems for the fingers; and the Buck‐Gramcko score for FPL repairs (Buck‐Gramcko 1976). None of these results were relevant to this review. Other outcome measures recorded at 16 weeks included subjectively rated functional assessment of hand function using a visual analogue scale; strength (grip strength using a Jamar dynamometer) and return to previous activity (whether they were absent from work or not). The authors did not provide measures of variability for continuous outcomes.

The certainty of the available evidence for this comparison is very low, reflecting downgrading by two levels for very serious risk of bias and two levels for very serious imprecision.

Exoskeleton versus physiotherapy

One randomised study (Gulke 2018) evaluated the benefit of applying an exoskeleton (exoskeleton group) compared with physiotherapy (physiotherapy group) following zone II flexor tendon repairs of both the FDP and FDS tendons in the index, middle or ring fingers in 62 participants. All participants were placed in a modified Kleinert orthosis with rubber band traction on the second day post surgery and commenced active and passive (as required) extension of the fingers within the orthosis (10 repetitions/hour). From the second week post‐surgery, patients were randomised to the exoskeleton group or the physiotherapy group. The exoskeleton group had the device applied by the physiotherapist for 30 minutes three times a week. No other treatments were provided. The physiotherapy group received physiotherapy treatment but the type of treatment and dose was not specified. It is assumed that the physiotherapy intervention was likely to be multi‐modal, consisting of various treatments. Both groups received treatment three times a week until function was deemed by the doctor to be satisfactory.

Outcomes were evaluated at 6, 12 and 18 weeks post‐surgery. Outcomes evaluated included functional assessment using a patient reported outcome measure (DASH score); active finger range of motion (isolated PIP and DIP joint ROM; TAM of the MCP, PIP and DIP joint; Strickland classification); adverse events (extension deficit; tendon ruptures; complex regional pain syndrome); strength (grip and pinch strength); satisfaction with the rehabilitation intervention (not an outcome of interest for this review). Please refer to Table 4 for a description of how the categories for the Strickland Classification (Strickland 2005) were defined in this study.

This article was published in German, and a translation of the article was obtained.

The certainty of the evidence is very low, being downgraded by two levels for very serious risk of bias and one or two levels for serious or very serious imprecision.

Continuous passive motion device versus controlled passive progressed to active exercise regimen (Modified Kleinert)

Gelberman 1991, a quasi‐randomised trial of 51 participants (60 digits) with zone II flexor tendon repairs, compared continuous passive motion (CPM) device (CPM group) with controlled passive exercise regimen using rubber band traction (controlled passive group). Participants began therapy on the first postoperative day. Digits were protected in dorsal‐blocking orthosis for a minimum of six weeks. The CPM group had the device attached to the protective orthosis on the first day following surgery to allow 60 degrees arc of PIP joint and a 30 to 40 degree arc of DIP joint motion. The CPM group used the device in isolation for 8 to 12 hours a day in the first four weeks. Active movements were introduced at four weeks to be performed in addition to the motion provided by the CPM device. The controlled passive group was placed in a similar dorsal blocking orthosis but with rubber band traction was applied. Patients performed active extension and passive flexion to the palmar crease for the first four weeks, when active flexion was introduced. Gelberman 1991 noted frequent problems with power failures and mechanical breakages of the CPM devices early on as well as issues with adherence; these were alleviated by increased time in patient education, both initially and at intervals throughout the rehabilitation period.

Outcomes were assessed by treating therapists at a minimum of six months post surgery (mean 10.8 months, range: 6 to 38 months). Outcomes included active finger range of motion (TAM and Strickland‐Glogovac classification (Strickland 1980)) and adverse events (infection; tendon rupture).

The evidence for all reported outcomes was of very low certainty, downgraded by two levels for very serious risk of bias and two levels for very serious imprecision.

Ultrasound therapy versus control

One study of 106 participants (139 digits with zone II flexor tendon injuries), Geetha 2014, compared the effect of daily ultrasound therapy lasting five minutes on the repair site in the initial three weeks of rehabilitation versus a control group. Both groups were immobilised a dorsal plaster of Paris cast for three weeks with wrist in neutral and MCP joints in 70 degrees flexion and commenced the same mobilisation from three weeks. Over the five‐year duration of the trial, three different ultrasound regimens with different frequencies, intensities and timing were tested in turn. Details of these are provided in Characteristics of included studies. These three groups were neither randomised nor concurrent and we have pooled the data from the three ultrasound groups in the analyses.

Outcomes assessed included change in active finger ROM (combined measurement summing PIP and DIP joint ROM between 3 to 12 weeks, measured in degrees; Strickland Classification (Strickland 1980) at 3 months); grip strength (measured at 12 weeks); and adverse events (wound dehiscence, tendon ruptures, extension lag). Grip strength was inappropriately reported for digits, not participants. The results for ROM were reported for involved fingers instead of participants and thus resulted in unit of analysis errors.

The evidence for all outcomes reported for this comparison was of very low certainty, reflecting downgrading by two levels for very serious risk of bias, one level for serious indirectness and at least one level for serious imprecision, given the low numbers of events and participants.

Low level laser therapy versus control (placebo)

Two heterogeneous trials compared low level laser therapy with a placebo control (Ozkan 2004; Poorpezeshk 2018).

Ozkan 2004 randomised 25 participants (41 digits) with flexor tendon injuries in zones I to V to either GaAs laser therapy (laser group) or a placebo control group. All participants received the Washington rehabilitation program for 12 weeks after surgery. In the laser group, whirlpool and infrared GaAs diode laser of 100 Hz frequency was applied from day 8 to 21 post surgery in 21 digits (13 participants). The control group, 20 digits (12 participants) received the same intervention with the machine switched off (i.e. placebo). Review‐relevant outcomes, which were measured at 12 weeks post surgery, include: active finger range of motion (total active motion, Strickland classification (Strickland 1980)); adverse events (tendon ruptures); and grip strength.

Poorpezeshk 2018, which included 97 participants (114 fingers) with flexor tendon injuries in zones I to III, randomised between red and infrared low level laser therapy (laser group) and a placebo control group, to examine the adjuvant effect of low‐level laser therapy on recovery of tendon injury in patients. Post‐operative care appeared to have consisted of four weeks of immobilisation in a plaster brace. Ten sessions of laser or sham therapy were provided from the second post‐operative day, two to three times a week. The probe was placed over the repair site using contact method. Outcomes were assessed by two independent blinded assessors. Review‐relevant outcomes include adverse events (infection; tendon rupture) and weekly measurement of passive range of motion of the PIP and DIP joints. Final assessments were recorded at four weeks post‐surgery.

We rated the available evidence as very low certainty, downgraded one level for serious risk of bias and two levels for very serious imprecision.

Motor imagery intervention versus control

Stenekes 2009, which included any zone of flexor tendon injury, compared kinaesthetic motor imagery of finger flexion movements (motor imagery group) with a control group in 25 participants. Standard care provided to both groups included six weeks using a Kleinert dorsal blocking orthosis; with only passive finger flexion allowed for the first four weeks and then 'place and hold' flexion exercises from four to six weeks. During these six weeks, the motor imagery intervention comprised eight sessions of motor imagery (10 repetitions of mental active flexion, held for three seconds followed by imagined finger extension and stretch) on a daily basis.

Outcomes included functional assessment using a patient‐reported outcome measure (MHQ; a single item question on hand skills using VAS); active finger range of motion (TAM); and strength (grip and pinch strength). Stenekes 2009 also measured preparation time of finger flexion and kinematic analysis including drawing accuracy and speed (which were not outcomes of interest of this review). Final follow‐up was at 12 weeks. The authors did not provide data for functional assessment or ROM outcomes.

The evidence for all outcomes reported for this comparison was of very low certainty, reflecting downgrading by two levels for very serious risk of bias, and at least one level for serious imprecision, given the low numbers of participants.

Subgroup and sensitivity analyses, and assessment of publication bias

We could not perform any subgroup analyses in this review. Clinical heterogeneity of interventions and outcomes, or paucity of specified subgroups, meant that these analyses were not possible. Furthermore, sensitivity analyses were not performed as no meta‐analyses were conducted. Also, we were unable to generate funnel plots to assess small study effects. We consider the risk of publication bias to be low as many of the published studies reported statistically non‐significant results. However, whilst it is possible that some unpublished studies with non‐significant results exist, their inclusion in the review would be unlikely to change our conclusions.