Protocol and registration

This review was conducted and is reported following the Preferred Reporting Items for Systematic Reviews (PRISMA) guidelines [22, 23] with a pre-defined protocol registered on the PROSPERO database (CRD42021297383). Deviations from original protocol included a slight delay in completion of literature searching, with completion in February 2022 as opposed to January 2022. The search was updated and reviewed once more up until September 2023. Independent secondary reviewer completion of data extraction and risk of bias assessment was adjusted and independently completed by one reviewer (DO) and then independently ratified by a second reviewer (FJ). The second reviewer was changed (to FJ) due to availability. These deviations from protocol were made due to reviewer availability and review timeframe. Changes of the secondary reviewer were made prior to the commencement of the review, thus reducing the risk of bias and inconsistency in the review process.

Selection criteria

The eligibility criteria for this review were developed in line with PICOS (Population, Intervention, Comparator, Outcome, Study Design) to ensure appropriate consideration was applied for important domains [24, 25] with scoping searches and consultation of previous studies with similarities in methodology [15, 16, 18, 21, 26] and Cochrane Back and Neck Group Guidelines [27] to help develop eligibility criteria. Development of eligibility criteria was also assisted by two reviewers with expertise in the field and in systematic review methodology (DF/FJ). Trials not written in English and animal studies were excluded from this review.

Population

Criteria included individuals aged ≥18 years old with chronic (≥3 months) neck pain, including chronic non-specific neck pain, and pain experienced as a result of a whiplash injury [27]. Exclusion criteria included any individuals with specific pathology, such as cervical radiculopathy, disc herniation, infection, inflammatory arthropathies, previous spinal surgery, spinal stenosis and primary headaches such as migraine or tension type headache, due to somatosensory profile variances experienced by some patient populations with specific pathology when assessed by QST [28].

Intervention

Any form of neck-specific exercise, such as motor control, strengthening or stretching exercise, performed for a minimum of two weeks with no additional treatment other than advice and education (including but not limited to, educational literature and clinician advice) was considered for inclusion in this review. Any study comparing two or more types of neck-specific exercise interventions was also considered with the effects of each exercise intervention assessed through separate groupings.

Comparator

Any study including no intervention or passive interventions (e.g., advice and education or manual therapy) as the comparator was considered for inclusion, to ensure that the effects of exercise could be appropriately assessed without the risk of cofounding variables, resulting from active training modalities, affecting the results of comparator groups [29]. Manual therapy refers to any passively applied movement technique by a practitioner such as spinal mobilisation or manipulation.

Outcome measures

As per previous studies assessing QST on different anatomical locations to this study [21, 18], outcome measures of interest included any QST modalities. Examples of these modalities include, but are not limited to, thermal, electrical, chemical and/or mechanical stimuli applied to the joint, muscle or skin and/or studies describing stimulus site, pain intensity and modality. Examples of these modalities include, but are not limited to, PPTs, thermal pain thresholds, conditioned pain modulation and temporal summation. With the focus of this review towards neck pain, QST sites local to the cervical spine were considered, with studies only assessing remote QST sites excluded.

Study design and setting

Any randomised-controlled trial and/or non-randomised study (including but not limited to quasi-experimental studies, cohort studies, controlled before-and-after studies) of a neck-specific exercise intervention was considered for inclusion in this review. Any setting, such as primary or secondary care, or laboratory-based was considered. Studies were not restricted by geographical location.

Information sources

The following databases were searched: AMED, CINAHL, Embase, Medline, PEDro, PubMed, Scopus, SPORTDiscus, and Science Citation Index and Social Science Citation Index from Web of Science Core Collection. Additionally, Google Scholar was searched. Electronic databases were searched from inception through February 2022 and updated in September 2023. Unpublished literature, ongoing trials and other grey literature were searched using the following databases and trial registries: clinicaltrials.gov, OpenGrey (up until 1^st December 2020 as it was discontinued after this time) and ISRCTN registry. Citation searching was performed by reviewing reference lists from eligible studies to identify any further articles that may not have been identified from database searching.

Search strategy

The search strategy was developed with guidance from the author team with expertise in the methodology of systematic reviews (DF, FJ). Searches were completed independently by a single reviewer (DO). All data relating to the search were imported into and stored, with duplicates removed, using EndNote Version 20 software [30]. The search strategy for all databases and search engines is presented in S1 File.

Selection process

Two reviewers (DO/FJ) independently retrieved and assessed articles following the implementation and completion of the search strategy. To ensure that the most recent articles are included in the review, this procedure was repeated after the original search strategy. Articles were screened by title, abstract and full text in order to apply the eligibility criteria. Whilst EndNote Version 20 software [30] was used to remove duplicate articles, no automated software was used throughout the selection process. Consensus was reached between the two reviewers regarding articles meeting the eligibility criteria and subsequent inclusion within this review. A third reviewer with subject and methodological expertise (DF) was available for consultation if needed. No corresponding author contact was required to obtain full-text reports or clarify uncertainty during the selection process.

Data collection process

Data were independently extracted by one reviewer (DO) using pre-defined data extraction tables. Data extraction was independently ratified by a second reviewer (FJ). Data were extracted for the following items: study design, location and setting; participant age, gender, ethnicity and additional characteristics presented in primary articles; sample size, length of follow-up, outcomes of interest (primarily QST modalities), intervention and comparator type; and items related to risk of bias, methods and results of statistical analysis. Follow-up durations were termed as short-term (<3 months), intermediate-term (3 months to <12 months) and long-term (≥12 months) [26]. All data were extracted manually, with no requirement to utilise software tools. There were no missing data from any of the included studies. However, some studies did not report all raw data. It was not possible to retrieve raw data from the authors of the studies included within this review; effort was made to contact authors at least twice by email. Completed data extraction forms for all studies included within this review are presented in S2 File.

Risk of bias

The Cochrane Risk of Bias 2 (RoB-2) tool [31] was used to assess internal validity and bias across the studies included in this systematic review. RoB-2 is a tool that assesses the risk of bias in a study from five domains relating to the ‘randomisation process’, ‘deviation from intended intervention’, ‘missing outcome data’, ‘measurement of the outcome’ and ‘selection of the reported result’. Bias in each domain is rated as either ‘low risk’, ‘some concerns’ (moderate risk) or ‘high risk’.

Whilst there is currently a lack of available data regarding the validity and reliability of the RoB-2 tool for assessing randomised-controlled trials, the tool was selected due to its ability to thoroughly assess internal validity through consideration of multiple sources of bias across the five domains [32]. Further, as opposed to similar tools, the RoB-2 tool provides an overall estimation of risk of bias, as well as individual domain consideration, allowing for a transparent understanding of all sources of potential bias and its overall effect on a study [33].

As difficulty has been noted in the interpretation of different domains and the application of the tool to primary research, especially for non-experts in subject matter [34], following independent risk of bias assessment by a single reviewer (DO), a second reviewer (FJ) independently ratified the results of the RoB-2 assessment to ensure accuracy and consistency of application. A third reviewer (DF) was available should any disagreements have occurred but was not required. Inter-rater reliability between assessors was not statistically assessed. The RoB-2 Cribsheet and Microsoft Excel assessment tool [31] were utilised to assess each individual domain and provide an overall estimation of risk of bias. The full report for the RoB-2 assessment is presented in S3 File.

Certainty of evidence

The quality of evidence for each study was assessed using the Grading of Recommendations, Assessment, Development and Evaluation (GRADE) assessment tool and GRADEpro software [35–38]. GRADE is a commonly used tool for the assessment and quality rating of evidence [39] that enables reviewers to make transparent, evidence-based decisions regarding the quality of evidence of healthcare-based research [40] and is recommended for use by the Cochrane Handbook for Systematic Reviews of Interventions [41]. Decisions are formulated through the assessment of five domains: ‘risk of bias’, ‘inconsistency’, ‘indirectness’, ‘imprecision’ and ‘publication bias’, with each domain rated as either ‘very low’, ‘low’, ‘moderate’ or ‘high’ quality evidence and a total rating calculated to suggest an overall quality rating for a particular study [38].

One reviewer (DO) independently assessed all articles to attribute a quality of evidence rating to each. All studies were assessed independently as it was not possible to pool data due to heterogeneity across the three included studies. A second reviewer (FJ) independently ratified the results of the assessment and provided suggestions for the presentation of results. A third reviewer (DF) was available to settle any disagreement.

Data analysis and synthesis methods

Due to a high level of heterogeneity between the included studies (e.g., gender of participants, baseline duration of pain, intervention characteristics and dosage and timing of primary outcome assessment), lack of reported data required and variability between the effect estimates utilised by the three included studies, a meta-analysis was not possible to pool overall effect estimates. It was also not possible to conduct statistical assessment for heterogeneity due to lack of required data. Because of this, narrative synthesis was undertaken and reported in line with synthesis without meta-analysis (SWiM) guidelines [42] and PRISMA guidelines [22, 23]. It is acknowledged that the absence of a meta-analysis may reduce the precision of direction of effect estimates and thus the accuracy and generalisability of results.

Effect measures

As per SWiM guidance, p-values (where p<0.05 is considered statistically significant) were selected as the standardised metric for the primary outcome measure (for QST) as all studies consistently reported these data. It was not possible to combine p-values across studies, therefore, this standardised metric is reported individually for each study. Where reported, effect size was also presented in the narrative synthesis of results. Study characteristics and summaries of intervention are presented in tables within the results section of this report.

Grouping of studies for synthesis

For the narrative synthesis of evidence, studies were grouped by exercise type. Although this review protocol initially planned for studies to be grouped by primary outcome measure, all studies utilised the same primary outcome measure, PPT, which would have resulted in only one grouping for all studies. Because of this, and due to variance between studies in exercise intervention protocol, it was deemed more appropriate to group studies by exercise intervention type to explore whether exercise type affected the primary outcome. Exercise types were progressive resistance training (PRT), PRT combined with graded physical training and fixed resistance training (FRT).

The direction of effect was calculated for all studies based on final follow-up assessment of PPTs and visually presented in a direction of effect plot. Calculation was guided by procedure presented by Boon and Thomson [43]. Vote counting was utilised to assess whether there was a positive impact of exercise intervention at intermediate-term follow-up, which is considered an appropriate method to be used in narrative synthesis [44]. Direction of effect was not calculated and vote counting not used at short-term assessments across studies due to variability in assessment timings and available data for each study resulting in inability to apply this technique. The findings for these time-points are presented individually as p-values and discussed.

Study selection

The systematic literature search for this study produced 1661 overall potentially relevant results from all databases searched, as presented in the PRISMA Flow Diagram [23], presented in Fig 1. Of the identified studies, 899 records were removed as duplicates, resulting in the screening of 762 records. 731 records were removed following title and abstract assessment in comparison to the eligibility criteria and 31 full-text records were sought for retrieval. Following full-text assessment in comparison to the eligibility criteria, three randomised-controlled trials met the eligibility criteria and were included for final synthesis of results. Citation screening also identified a further eight potential studies, all of which were excluded due to the lack of use of QST as an outcome measure for the assessment of pain sensitivity in each of the identified studies. A flow diagram of the study selection process is presented in Fig 1.

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Fig 1. PRISMA flow diagram.

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Study characteristics

Data from each identified study were extracted using bespoke data extraction forms. A summary of characteristics for the three studies [45–47] is presented in Table 1. Studies included in this review were published between 2016 and 2020 in three separate countries; one in Spain [45], one in China [46], and one in Denmark [47]. One study adopted a multi-centre design [47], one single-centre [45] and one recruited from multiple places of employment [46]. Two studies utilised intention-to-treat analysis [46, 47] and one did not [45], with one study also using per-protocol analysis for the assessment of adherence [47].

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Table 1. Summary of study characteristics.

https://doi.org/10.1371/journal.pone.0303166.t001

Only one study [47] reported a difference between groups regarding baseline demographic data, which related to a greater percentage (80.8%) of female participants present in the control group.

Regarding population characteristics, all studies reported participant age and gender. Two studies [45, 46] reported height, weight, and BMI data. Two studies [46, 47] reported duration of symptoms and employment data. One study [46] reported job experience and computer usage. One study [47] reported educational level and sleep quality data. Data pertaining to population characteristics are presented in Table 1.

Population

Excluding the second intervention group (manual therapy) from one study [45] as this was not an outcome of interest, a total of 355 participants enrolled at recruitment across all studies. Due to dropout across all three studies, the total number of participants analysed was 352, as intention-to-treat analysis was utilised in two studies [46, 47]. It was not possible to calculate gender distribution at baseline recruitment, as participants in one study dropped out prior to demographic data collection [45]. However, of the 352 participants included in analysis across all studies, 17.3% were male and 82.7% were female, with a higher proportion of females notably present across all studies, especially in the study by Li et al [46], which was restricted to female participants only.

Eligibility criteria varied across all studies. Minimum duration of neck pain required for participant inclusion varied from ≥12 weeks to >1 year. Two studies required neck pain to be confirmed by official medical diagnosis [46, 47], one study required minimum level of disability on the Neck Disability Index of 10 [47] and one a minimum self-reported pain intensity of 2/10 on a numerical scale of 0–10 [46].

Two studies [45, 46] reported age as mean years (+/- SD). The mean age for participants per group in the study by Bernal-Utrera et al [45] was: control = 36.9 (SD± 2.9) years; TE = 36.8 (SD± 2.9) years. For participants in the study by Li et al: [46] control = 34.1 (SD± 8.2) years; PRT group = 35.6 (SD± 7.9) years; FRT group = 33.7 (SD± 9.0) years. One study [47] reported age data as mean years (95% CI): control = 45.2 (42.9; 47.5) years; TE = 45.1 (42.8; 47.3).

Intervention

All three studies included active exercise of the neck in the intervention group for their respective trials [45–47]. Reporting of interventions was inconsistent across studies, with one study providing limited detail of intervention protocol [47]. Although the frequency of exercise was consistently reported across the reviewed studies, only one study provided details on the number of sessions provided. A summary of interventions is reported in S4 File.

The duration of intervention ranged from 3 weeks to 4 months, with a frequency of training ranging from twice per day to ≥3 times per week. Exercise intensity was inconsistently reported across the included studies. Two studies included a PRT protocol, one progressed by exercise type [45] and one progressed by an increase in resistance percentage [46], one a PRT protocol combined with graded physical training [47] and one an FRT protocol [46]. One study performed the intervention at the location of participant recruitment [47], with two studies completing the intervention in a home-based environment [45, 46].

Supervision of participants when completing intervention protocols varied across studies, with one providing no supervision [46], one providing 8 x 30-minute sessions of instruction interspersed with the intervention protocol [47] and one providing three sessions (one per week) of individual physiotherapy to ensure correct technique and teach progressions of exercise [45]. Assessors remained blinded in the two studies that included supervision [45, 47], with supervision provided by separate physiotherapists, which mitigated the risk of concealment bias.

Various equipment was utilised across studies, such as Theraband and a handheld dynamometer [46]. Two of the three studies [46, 47] additionally provided advice and education to participants in the intervention group.

Adherence was monitored in two studies [46, 47] and was reported as good in both. One study [45] included a second intervention group that received MT. However, this is not an outcome of interest for this review and, therefore, is not included in the synthesis of results.

Comparator

Control groups were allocated for all three studies [45–47]. As per the eligibility criteria for this review, no study provided active intervention for comparator groups. One study provided sham manual therapy [45] and two provided advice and education [46, 47].

Outcome measures

All studies utilised PPTs as the chosen QST modality for the assessment of pain sensitivity. Three assessments are deemed necessary to obtain an accurate estimate of pain sensitivity [48]. One study [45] obtained PPT measurements at the level of the C2 vertebrae spinous process of the cervical spine, calculating a mean value from three measurements for statistical analysis. One study [46] obtained PPT measurements at the painful region of the cervical spine, again calculating a mean value from three measures for statistical analysis. The final study [47] assessed PPT bilaterally at the level of C5/6 vertebrae but did not provide information on the number of measures assessed for statistical analysis.

The length of follow-up varied across studies, with assessment completed at 2 weeks [45, 46], 4 weeks [45, 46], 6 weeks [46], 12 weeks/3 months [45, 46] and 4-months [47].

Although not the primary focus of this study, secondary outcomes (Visual Analogue Scale, Neck Disability Index and Pain Bothersomeness Scale) that may be of interest are briefly reported. These data are presented in S5 File but are not included in the synthesis of results.

Risk of bias

Agreement was achieved between both primary reviewers (DO/FJ) across all domains of the Cochrane RoB-2 tool [31] for all studies. An overall summary of risk of bias for each study is presented in Fig 2.

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Fig 2. Risk of bias assessment.

Key: Classification of risk of bias for each included study, as determined by the Cochrane RoB-2 tool. Risk of bias is separated into five different domains that are rated separately, with an overall judgement of risk of bias also provided. All studies were rated as having either low risk of bias, or moderate risk of bias in all domains, with no study rated at a high risk of bias in any domain.

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All three studies were rated at an overall moderate risk of bias with concerns stemming from different domains. The two domains that demonstrated the highest risk of bias across all studies were ‘deviations from intended interventions’ and ‘selection of the reported result’.

Two studies [45, 47] were rated at a moderate risk of bias regarding deviations from intended interventions; one study [45] due to possible knowledge of allocation for participants and failure to assess participant adherence or implement processes to account for this; the other study [47] due to potential awareness of allocation for participants in both groups with subsequent potential deviations from the intended intervention due to significant dropout in the control group. Furthermore, two studies [45, 46] were rated at a moderate risk of bias regarding selection of the reported result due to failure to report a pre-defined study protocol and analysis plan. Although one study [46] reported a registration number for a trial protocol, this protocol number was linked to a different study by different authors, and we were unable to identify a pre-defined protocol for this study. The other study [45] did not report a protocol.

Certainty of evidence

Based on GRADE recommendations [36], all groupings were initially rated as high-quality evidence due to their respective studies utilising randomised-controlled trial designs, as this is recognised as the gold standard approach [49]. All groupings were downgraded due to risk of bias. As with the RoB-2 analysis, concerns stemmed from possible knowledge of assigned intervention or poor blinding of participants in two studies [45, 47], leading to possible performance bias. Furthermore, high participant dropout potentially consequential to this may have resulted in attrition bias in one study [47]. There were also concerns regarding unidentifiable trial protocol in two studies [45, 46] and the potential introduction of reporting bias because of this.

The total participant attrition rate reported across all studies was 47. One study [45] reported an attrition rate of 4 participants at follow up, one study [46] reported an attrition rate of 7 participants at follow up and one study [47] reported an attrition rate of 36 participants at follow up.

Two groupings were further downgraded due to indirectness resulting from failure to report participant adherence to intervention in one study [45] and stringent eligibility criteria potentially reducing external validity and generalisability of results to the general population in another [46]. Whilst, one study [45] demonstrated a large effect size associated with outcomes of interest for this review, the grouping could not be upgraded as the other study reported no such data. Therefore, one grouping (PRT Combined with Graded Physical Training) was assigned an overall rating of ‘moderate’ quality evidence, and two groupings (PRT and FRT) were ascribed an overall ‘low’ quality of evidence. The overall GRADE rating of each grouping is presented in Table 2.

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Table 2. GRADE rating for certainty of evidence per study.

https://doi.org/10.1371/journal.pone.0303166.t002

Publication bias

Due to the low number of studies included within this review, it was not possible to perform statistical analysis for publication bias. Because of this, publication bias could not be assumed and is, therefore, rated as undetected for all studies. It is, therefore, acknowledged that there is a possibility of existence of publication bias and subsequent potential for data within this review to result in reduced precision of conclusions drawn.

Direction of effect

The direction of effect for all groupings and studies is presented in Table 3. Data in the direction of effect table is calculated based upon intermediate-term follow-up assessment as this was consistently assessed across all studies. The direction of effect assessment demonstrates a positive direction of effect for all studies and groupings. A sign test was not conducted due to the small number of studies included in this review, which would have resulted in an underpowered test [43].

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Table 3. Direction of effect plot with RoB-2 and GRADE rating.

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Results of individual studies

The results of the individual studies could not be combined because of wide variation between study and reported effect measures. One study [45] reported R² values to demonstrate the size of effect; the other two [46, 47] did not. All studies [45–47] reported p-values to determine statistical significance between groups at follow-up (three and four months). Only one study [45] reported effect sizes for between-groups differences at any stage.

High clinical heterogeneity, primarily regarding duration of neck pain for inclusion, participant gender, study setting, intervention type and duration of intervention, was present across the included studies. Variations in participant demographics, such as gender distribution or age range, as well as clinical characteristics such as the duration of their pain, may impact on the response to treatment. Furthermore, variations in intervention protocols, including different exercise types or dosages, can introduce significant heterogeneity. These differences can lead to disparate outcomes and make it challenging to compare or combine results. Because of this, meta-analysis was not possible. Therefore, a narrative synthesis of results is reported. Although results were planned to be grouped according to outcome measure, as per the published protocol, all studies utilised the same outcome measure for QST (PPTs). Therefore, this method of grouping may have limited the analysis and would have resulted in only a single grouping. Thus, results were instead grouped by exercise type.

Progressive resistance training

Progressive resistance training was investigated in two trials [45, 46] (117 participants between intervention and control groups at analysis). Progressive resistance training entailed any resistance training programme that was systematically progressed in difficulty by frequency, intensity, duration or type of exercise. One study [45] implemented PRT through increasing exercise load and type on a weekly basis. One study [46] implemented PRT by progressing a percentage of one repetition maximum every two weeks. Across the two trials [45, 46], PRT showed a moderate association. Both studies [45, 46] reported statistically significant improvements (p = 0.001 and p<0.001 respectively) demonstrating PRT was effective at reducing pain sensitivity in comparison to control at intermediate-term follow-up (12-weeks/3-months respectively), with one study [45] also reporting a large effect size in support of this (R² = 0.328), where R²>0.14 is considered as a large effect size. The other study did not report the effect size. Both studies indicated a positive direction of effect at intermediate-term follow-up.

One study [46] reported statistically significant short-term improvements in comparison to control at weeks 2 (p = 0.017), 4 (p<0.001) and 6 (p<0.001), whereas the other study [45] did not (week 2: p = 0.991; week 4: p = 0.415), although a medium effect size (R² = 0.082) was noted at week 4 assessment for increased PPTs by this study [45]. One study [45] also reported a significant intragroup difference for PRT at week 12 (p = 0.001), but not at weeks 2 (p = 0.729) or 4 (p = 0.061). Both studies demonstrated an overall moderate risk of bias, with issues primarily stemming from concerns regarding deviations from intended intervention and possible performance bias [45] and risk of bias in selection of the reported result [45, 46]. This exercise grouping demonstrated low-quality evidence based on GRADE assessment due to risk of bias issues in both studies, and indirectness issues, including poor generalisability [46] and lack of reporting regarding adherence to the intervention [45].

Based on low to moderate quality of evidence (GRADE), PRT is effective at increasing PPTs at intermediate-term follow-up.

Progressive resistance training combined with graded physical training

Progressive resistance training combined with graded physical training was investigated in one study [47] (200 participants between intervention and control groups at analysis), which demonstrated a statistically significant improvement (left cervical spine: p = 0.001; right cervical spine: p = 0.004) in comparison to control at 4-month follow-up for PPTs. A positive direction of effect was indicated. No effect size was reported. The study demonstrated a moderate risk of bias due to some concerns regarding performance and attrition bias. This grouping was rated as moderate quality of evidence based on GRADE assessment due to concerns regarding risk of bias.

Based on moderate-quality evidence (GRADE), PRT combined with graded physical training is effective at increasing PPTs at intermediate-term follow-up.

Fixed resistance training

Fixed resistance training was investigated in one study [46] (71 participants between intervention and control groups at analysis). The findings demonstrated a statistically significant improvement for FRT in comparison to control at weeks 4 (p = 0.001), week 6 (p<0.001) and at 3-month follow-up (p<0.001), but not at week 2 (p = 0.075). A positive direction of effect was indicated at intermediate-term follow-up. No effect size was reported. The study was rated at an overall moderate risk of bias due to concerns regarding selection of the reported result. This grouping was rated as low quality of evidence based on GRADE assessment due to concerns regarding risk of bias and potentially poor generalisability of results.

Based on low-quality evidence (GRADE), FRT is effective for increasing PPTs at short-term (from week 4) and intermediate-term follow-up.

Risk of bias and certainty of evidence

The overall risk of bias for all three included studies was rated at moderate. Common issues related to poor reporting of pre-defined study protocols, participant attrition rates and blinding processes, whereby participants were likely aware of their assigned intervention. Although this may have been caused by difficulty disguising interventions due to their nature (e.g., exercise vs inactive control), there are concerns regarding the potential impacts on the internal validity of the studies, especially when potential knowledge of intervention was not accounted for, and the subsequent findings of the effects of exercise; something that has also been noted in prior reviews [18].

Further to risk of bias assessment, the certainty of evidence was rated at either low or moderate for all groupings. Shortcomings related to the aforementioned risks of bias and indirectness. Only one study reported an effect size for the primary outcome. Reporting of this, or presentation of data pertaining to calculation of the effect size may have been beneficial for the two studies and may have resulted in an improved certainty of evidence rating within the exercise groupings which would have assisted the synthesis of our findings.

Strengths and limitations

This systematic review has various strengths. Firstly, the study and intended methods were prospectively registered as a publicly accessible protocol on the PROSPERO database. The reporting of this study also followed both PRISMA and SWiM reporting guidelines to improve reporting quality and transparency. Although some deviations from protocol occurred, these were transparently reported. Data selection was independently performed by two reviewers, whilst data extraction, risk of bias and certainty of evidence assessment were performed by one reviewer and then independently ratified by a second reviewer, with discussion between the reviewers if required.

Limitations were present within this review. Due to a high degree of clinical heterogeneity (e.g., duration of neck pain for inclusion, participant gender, study setting, intervention type and duration of intervention) and differing effect measures across studies, meta-analysis and estimation of effect, which would have been a superior method for combining results [53], was not possible, consequently limiting the strength of answer to the review question. Additionally, although a thorough literature search was conducted, the stringent eligibility criteria, including restriction to articles published in the English language, may have caused exclusion of appropriate articles. Only three studies were included in the review, resulting in conclusions being drawn from a limited sample of data. It was also not possible to assess publication bias, which may have influenced conclusions [54].

Regarding the dataset from which conclusions of this review are drawn, additional limitations are present. It was not possible to assess long-term effects as none of the included studies investigated this timeframe for follow-up. The small sample sizes across the included studies, combined with strict eligibility criteria of some studies, somewhat limits the external validity and generalisability of findings to the wider population. Gender distribution favoured females across the three studies, again potentially limiting generalisability. Furthermore, the average age of participants only fell within the age range in which CNSNP is most prevalent [2] in one study. Thus, the results may not directly relate to the greatest proportion of the population for which CNSNP is prevalent. Considering such limitations, it is difficult to generalise the results of this study to a single population and to understand whether TE is beneficial for long-term improvement.

Furthermore, limitation is present when comparing this review to previous systematic reviews due to heterogeneity between populations and outcome measures. Therefore, comparison with previous research should be considered with caution. Our systematic review also has limitations that may affect the generalisability of the results. Firstly, the sample sizes varied across the included studies, with some having smaller cohorts, potentially impacting the robustness of the findings. Future research with larger, more representative samples is needed to enhance the reliability and generalizability of our findings. Secondly, the gender distribution within the study populations was not consistently reported or balanced across all studies, raising concerns about the extrapolation of findings to populations with different gender compositions. Future studies should ensure adequate representation of both males and females to enhance the applicability of the results. Lastly, the age range of participants included in the studies varied, potentially impacting the generalisability of the findings to populations with distinct age demographics. Future research should aim to elucidate how findings extrapolate to specific age cohorts to better inform clinical practice across the lifespan.

From a physiotherapist’s perspective, exercise adjustments such as modifying resistance, duration, and intensity can customise these exercises to suit individual needs, abilities, and conditions. Additionally, a thorough assessment and personalised exercise plan that takes into account factors such as age, fitness level, and any other health issues ensures that the exercises are applied safely and effectively across various populations, promoting therapeutic benefits while minimising the risk of injury or worsening of symptoms.

Implications

Exercise is currently commonly utilised in standardised care for chronic neck pain as part of a multi-modal management approach [6]. The current findings build on previous evidence [15, 16] and support its use. Our results do not provide clear conclusions as to the most effective exercise type, especially for intermediate-term improvements, which does not help to develop evidence of current clinical guidelines [6]. Moreover, certain protocols utilised equipment that may not be typically available to care providers or patients (e.g. dynamometers) and may require baseline standards of fitness (e.g. for graded physical training). Thus, it may be prudent for clinicians to select exercise type based on patient requirements, capability and equipment availability until firm conclusions can be drawn regarding size of effect. Consideration of the natural covariate factors that may limit generalisability, such as participant gender and age, should also be considered by practitioners when using findings of this review to inform practice.

The use of QST in this study provides an initial understanding of pain response in relation to exercise measured using a more objective method. Furthermore, if more robust future research can develop current understanding of the benefits of exercise, the utilisation of QST may provide a more in depth understanding of pain mechanisms that are not identifiable alone using patient reported measures, which may allow for understanding of subgroups of patient who may benefit from certain types of exercise over another. This may then implicate whether the use of QST in clinical practice would be beneficial for greater individualisation of pain management and treatment selection.

Based upon these clinical implications, future research should include larger samples with a balanced gender distribution. Long-term follow-up would also help provide an understanding of the long-term effects of neck-specific exercise and further inform clinical practice. Additionally, comprehensive data should be openly reported to enable calculation of more meaningful statistics, such as size of effect, allowing future reviews to develop an understanding of which exercise modality demonstrates the most benefit.