Note 1 response concerning statements of primary and ...€¦ · IDMC amendment) and SAP. If there is further evidence required please get in touch. ... why patients with appendicitis

Note 1 – response concerning statements of primary and secondary outcome. We appreciate the BMJs concern of ensuring that we are fully reporting the outcomes as predetermined for the trial. We can confirm that this is the case, but acknowledge that the initial trial documentation we provided did not clearly specified the primary and secondary outcomes because the time points for assessment were not stated in the secondary outcomes section of the protocol. However, as we explain below, this information was included in the Schedule of Assessments for outcome data that was in the original protocol and is most clearly stated in the Statistical Analysis Plan (SAP), and has been adhered to throughout the trial. There is one exception to this, where a secondary outcome was added in a protocol revision partway through the trial. We have reviewed the statements concerning primary and secondary outcomes in the protocol, protocol amendments, SAP and trial registrations, and below provide an explanation on the details that are given. The trial manuscript reports 8 secondary outcomes (counting the targeted adverse events as a single outcome). The original protocol (29/10/2010) also included 8 secondary outcomes, 7 of these 8 outcomes are reported in this paper – the secondary outcome missing from our manuscript is the cost-effectiveness analysis which we are considering reporting separately. The additional secondary outcome in the paper but not in the protocol is the one added partway through the trial - vomiting episodes at 72 hrs and 120 hrs (recall the primary outcome is vomiting episodes at 24 hours). The original protocol did not clearly state the time points when these outcomes would be assessed at the point in the protocol where the secondary outcomes are listed, but it did indicate these time points clearly in the Assessment Schedule a few pages later. The data we report on are all outcomes at all time points stated. Thus there is no selective reporting of outcomes. The protocol also did not include a statistical analysis plan. This was developed separately before the first DMC and before any data analysis (the first draft of which was produced on 7/9/2012). We attach this document to our submission for your information. You will note that this document clearly describes assessment of the secondary outcomes and the time points when they will be analysed, as we present in the paper. Data for the additional secondary outcome of vomiting episodes at 72 hours and 120 hours that we report in the manuscript (but which was not listed in the initial protocol) are based on data that were always planned to be collected (see Assessment Schedule in original protocol) but were overlooked as being listed as a secondary outcome. This oversight was explicitly addressed as the secondary outcome was added to Version 3.0 of the protocol when the DMEC refined the definition of the primary outcome as mentioned on lines 165-7 of the previous version of the text. We are revising the text in our manuscript to fully inform the reader of the situation with this variable. Protocol version 3.0 thus lists nine secondary outcomes, all 8 we report in the paper plus cost-effectiveness. This protocol revision also includes the increased sample size, and received ethical approval before implementation. On our review, we note that both trial registration entries are inadequate. We have noted errors in the ISCRTN trial registration entry as it omitted health related quality of life, cost-effectiveness (not reported in this paper) and risk of infection outcomes. It also mis-specified that all secondary outcomes would be measured at 1 month. We are investigating how this entry was submitted and not checked. The earlier EudraCT entry does match the original protocol

and includes all eight original outcomes but did not state time points, and the EudraCT system truncated the text describing the final targeted adverse events. We believe that it is clear from these documents that the time points for the secondary outcome were pre-specified (although specified late for the 48hr and 120hr vomiting outcomes) and nothing in the paper is based on selective reporting (indeed we are reporting all data we collected). We are embarrassed that the initial protocol and the trial registration do not stand up to the scrutiny that the peer reviewers and editors expect. As we have described, the trial was undertaken by enthusiastic trainee surgeons through the West Midlands Research Collaborative, who are an enthusiastic but inpatient group, and we all have learned during the process of this trial of the importance of double and triple checking these documents, and are raising these issues with the trials we work across. We hope that you can assess that despite these inconsistencies in the trial registration entry, that the trial report is compliant with the protocol (and the IDMC amendment) and SAP. If there is further evidence required please get in touch. Note 2 – revision of the primary outcome by the IDMC The issue concerning the primary outcome was whether it was based on data reported by clinicians, patients or both. Patient reported and clinician reported episodes of vomiting were recorded throughout the trial. We were not aware when we started the trial as to how frequently vomiting episodes would be recorded by clinicians, patients or both. The IDMC reviewed the outcome on the 6th February 2013 where they advised clinician based values, and again at their second meeting on 6th September 2013 when they advised the modification to combine clinician and patient based values. This was based on the observation that patients recorded many episodes of vomiting which were not noted in clinical records and vice versa. Initially after surgery, the patient may not be full aware and only the clinician recorded the events. Later after surgery the patient may be mobile and go to the bathroom, so the carers may not record it. We quote from their notes “The DMEC advised that the current definition of the primary outcome (as decided at the last DMEC meeting) does not capture all possible vomiting events and that the trial team should consider a combined measure using data from both the patient completed forms and the staff completed forms”. The IDMC had reviewed data from 365 patients at the Feb meeting, and 700 patients at the Sep meeting. We are now including data on the number of patients in the analysis that the IDMC saw.

As a post hoc sensitivity analysis we have included in the manuscript analysis of the primary outcome restricted to clinician reported episodes and patient reported episodes, which indicates that the effect is robust remaining statistically significant, and of a similar relative magnitude. Note 3 - blinding We believe that it is reasonable to describe the trial as blind, as patients and outcome assessors were blind to allocation, together with the hospital staff other than the anaesthetist. The reviewer correctly raises the point that the anaesthetist may visit the patient post surgery. In practice this would only happen in the immediate post-operative period. The data shows there is a continued effect from Dexamethasone out to 72hrs. This indicates that anaesthetist induced bias (which would be theoretically possible in the first few hours) was not substantially impacting on this effect. The bias would also have acted to reduce the difference as we point out in the discussion (i.e. assuming the anaesthetist might give an additional antiemetic to patients who they were aware had not had the dexamethasone). We have expanded the discussion of blinding in both the methods and discussion in response to the points raised.

We believe that seeking to undertake a fully blinded placebo controlled trial would have been detrimental to the success of this study. Although it would

have scientifically strengthened the validity of the study, in this circumstance we do not think the risk of bias is high enough to compromise our finding. We

have used of an efficient pragmatic design:

1. The trial reduced cost substantially by engaging trainees and avoiding a placebo. The total cost of this trial was less than half that would be expected (400k instead of 1M)

2. The lack of a placebo encouraged anaesthetists who had never entered a patient into a trial to participate. 3. The recruitment was rapid and a placebo would have certainly hindered this. 4. Despite the difficult study population, high recruitment levels were obtained and exclusions were low (for the setting).

We have delivered a randomised intervention in a complex setting and provided results that are relevant not just within teaching hospitals but across general hospitals. We have engaged researchers who would have never envisaged undertaking a trial and designed a process that utilised both the attributes of the anaesthetic and surgical teams. We would contend that to introduce restrictions that may have standardised procedures would have lessened the value of the trial (and substantially increased its costs).

Editorial comments Comment Our response and changes

The outcomes in the text and in the registration don’t match exactly.

See Note 1 above

What was standard care exactly?

Our priority was to perform a pragmatic trial with minimal exclusions, to maximise the generalisability of the study results. We therefor accepted routine clinical practice within the control arm. The key specified standard of care was that a single dose of an antiemetic would be given before the start of surgery. This excluded any anaesthetist who routinely provided 2 different agents at the start of these procedures, in practice there were only a couple of anaesthetists for whom this was routine practice.

Change made in Paragraph 4 of Methods. Insertion of “The key specified standard of care was that a single dose of an antiemetic would be given before the start of surgery.”

There's already a lot of literature out there on the positive effects of dexamethasone on PONV particularly in upper abdominal surgeries and pelvic surgery, but little on bowel surgery.

No response needed No change proposed

Isn’t PONV is largely related to the emetic effects of anaesthetic drugs?

We hoped this point was clearer in the text. It is the unique nature of bowel surgery that makes study of these patients so important.

Change made in paragraph 1 of introduction. Insertion of

PONV is related to anaesthetic agent use in many operations, but in bowel surgery, the bowel handling, resection and associated intra-abdominal contamination promote an ileus of variable duration. It is difficult to apportion effect size in such a diverse population, but in cases with significant intra-abdominal contamination (with bowel contents) this is the major effect, not the anaesthetic agent. In fact this is why patients with appendicitis classically lose their appetite (before they are submitted to any anaesthetic).

“PONV is related to anaesthetic agent use in many operations, but in bowel surgery, the bowel handling, resection and associated intra-abdominal contamination promote an ileus of variable duration, having a major effect on PONV. “

Great that you have a patient co-author, and you could state that in the PI box; if she influenced write-up of the results, that should be stated. If she did not, she doesn't fulfil the requirements of a co-author. We also need information about dissemination.

She does fulfil the criteria. We are not able to report the results of the study directly to patients, as we do not hold their contact details centrally. As occurs with many UK multicentre RCTs, the identities if the individuals who participate in the trial are known only by the recruiting hospital trusts, with the central trials office only identifying individuals by trial id numbers. This means that each site has to disseminate the results to the study participants. We are providing sites with a summary and requested that they distribute it to the patients who were recruited to the trial dependent

No change proposed regards patient co-author. Have added the following concerning dissemination of trial results. “A patient summary of the findings of the trial has been provided to the recruiting centres for dissemination to the trial participants”.

on their vital status.

Table 2 lists quite a few secondary outcomes at each time point, and we are not entirely clear whether all these were pre-specified, e.g., clinically important PONV, number of types of anti-emetics, number of doses of emetics. No mention of 3 time points is made in the registry and the protocols (both the unpublished or published version) are equally vague on this. Some clarification needed here.

See note 1 above Clarified that the additional vomiting time points were added as a secondary outcome as a protocol modification part way through the trial.

The protocols are rather vague documents – no mention of planned statistical analyses.

See note 1 above Added “The Statistical Analysis Plan is also available from the study website”.

Sample size is clear, the re-estimation of the sample size with increased power is clear. Subgroup analyses all planned and all reported.

No response needed No change made

The primary outcome was changed during the trial from episodes of vomiting recorded on the trial care charts to those reported by the patient or clinician – which was approved by the IDMC – at what point in the recruitment was this made?

See note 2 above. We have edited this information into the first paragraph of the statistical analysis section: “The independent data monitoring committee (IDMC) met three times and reviewed interim analyses at three time points when 365, 700 and 1170 participants had been recruited. Due to faster than expected recruitment, at their second meeting the IDMC advised increasing power to 90% raising the final target sample size to 1320 participants. At the same time, the IDMC also clarified that the primary outcome should include both patient and clinician reported episodes of vomiting recorded in patient notes to ensure that all vomiting episodes were captured.”

Table 2 (secondary outcomes): P-values are given for all the comparisons, but no effect sizes or CIs are reported. Some secondary outcomes EQ-5D and Facit-F are in the appendix and not in the main report. Preference if it was a pre-specified outcome then it should not be tucked away in supplementary material.

The effect sizes and confidence intervals for the outcomes in Table 2 were reported in the text. We have added these to the table. WE have computed both relative (risk ratio) and absolute (risk difference) estimates for all binary outcomes as requested by CONSORT.

Effects sizes and confidence intervals have been added to Table 2. Table 3 has been created from the supplementary table for EQ5D and Facit-F (and CIs added too)

Results in the Abstract are reported as NNTs…no explicit reporting of risk differences. You were looking for a 9% absolute difference – you got a marginally lower difference than you thought clinically relevant.

The sample size was based on a relative difference of 24% which had been previously seen in a systematic review. We did not actually state (either in the protocol or the manuscript) what we thought would be a clinically relevant difference We would anticipate that smaller differences are actually clinically important, but there is no consensus on the minimally clinically important difference. CONSORT for abstract requires statement of the estimated effect size and its precision – it does not specify what measure to use. We thought that the NNT would provide the most easily understood absolute metric to present and have used it in the abstract. All the data to compute a risk difference and confidence interval is stated in the abstract for somebody who wants to know this. We additionally present relative risks in the main text

We would be willing to present absolute risk differences in the abstract and text instead of the NNT, if the editors judge that this is a better way to present the results. However, this is not our preference as we believe that the NNT is a more easily understood statistic.

Reviewer 1 (patient) – Emma Jones

This paper is very relevant to me as a patient. Post-operative nausea and vomiting is one of the things that sticks in my mind about what was unpleasant about my recovery. Unfortunately the quicker return to oral diet was not pleasant because the food was not appetising at all – I can remember having awful lumpy custard with a film over the top of it served to me!

We appreciate the comment, but unfortunately the quality of hospital custard is beyond the scope of this study and influence of the investigators.

No change made

I’m not sure whether this is possible or helpful, but I wonder whether some involvement of kitchen-staff in a ‘add-on’ study could be helpful. It would be good to look at the variance in food quality from hospital to hospital, and how the organisational culture or systems within the hospital help or hinder the delivery of good food. Would better food (or better systems which could then deliver better food) effect the speed and attitude with which patients improve their post op oral diet, and would knowing that be a useful addition to a study like this? Reducing nausea is no good if the patient takes one look at the food and doesn’t want to eat it.

We will ponder this for future research ideas.

No change made

I can’t see any reason why this would not work in practice, nor any reason why the addition of this treatment would be challenging for patients.

No response needed No change made

Yes – patient reported vomiting at 24 and 72 hours, antiemetic use, patient reported nausea, fatigue and quality of life, diet, hospital stay and adverse events are all important to me. I can’t think of any others that should be added.

No response needed No change made

I wasn’t sure why in the results section length of stay is documented to be similar (with the same median value) in both arms, but in the abstract this is not made clear – the opening paragraph of the abstract states that reducing length of stay is a main objective, so shouldn’t the results section of the abstract state that little difference in LOS was observed? Also – being able to achieve a

The space restrictions on abstracts make it impossible to report findings for all secondary outcomes. LOS is a multifactorial event influenced by hospital and social factors as well as

No change made

quicker return to oral diet was one of the first things I read (opening sentence of the abstract), but it’s not clear whether this was actually achieved in the results section of the abstract.

recovery. For this reason it is a less valuable measure for groups of patients, although important as an outcome for individual patients. Hence we state its importance in the text, but include it as a secondary outcome only

Some work was conducted prior to designing the trial (six major units in the West Midlands were surveyed), and there was an internal pilot study - Could the authors document whether they involved patients at this stage as well as the main RCT? I am really pleased to see that a patient advocate was part of the management team. I wonder if Lindy would consider writing up something about her experiences of PPI during DREAMS (perhaps as part of another more qualitative paper about learning during the trial, barriers encountered, and the process of actually conducting the trial) - I would be interested to read how PPI was managed in terms of resources, funding, time commitment, support and what she got out of it in return.

Beyond the scope of this manuscript No changes made.

Reviewer 2 - : Andrea Cortegiani : Anaesthesiologist, Intensivist

Line 7: I would not insert "blinded" in the description of the trial (see below)

See note 3 above We have removed the one instance where the trial in error was described as double blind and been clearer as to who was blind and how.

Line 94: Specify here the number of involved study

We did not include the number recruited in the method, as we usually think that this is a result to report, and thus belongs in the results section, but have no problems in adding it.

Inserted in first paragraph of methods “of 1350 participants”

Line 94-98: I suggest to clearly describe here that the intervention is open and the anaesthesist was not blind to the intervention since there was no masking/placebo, even though this information is partly inserted in Lines 140-141

Agree that greater clarification is given on this issue

Inserted the following in the first paragraph of the methods “Whilst the treatment allocation was known by the anaesthetist, patients and clinical staff involved in post-operative care and data collection were blinded to treatment allocation.”

Line 100: Please specify the eligible age of "adult patients"

Agree We have added “aged 18 and over” in the second paragraph of the methods. The actual ages recruited to the study are already reported in Table 1.

Lines 121-123 stated: "All antiemetics were administered before knife to skin and no further antiemetics were administered during the operation." It is not clear to me: 1) If this sentence concerns dexamethasone group only or both group. I would revise it 2) what if the standard care of the anesthesiologist in charge is to administered antiemetics during the intervention or briefly before the end of surgery? In those cases, standard care would not be allowed. It is not clear to me if standard care of the control group was allowed only before knife to skin or for the whole surgery before starting the assessment. I suggest to revise to improve clarity.

We can revise to improve clarity We have added “in both arms” to make the sentence: "In both arms, all antiemetics were administered before knife to skin and no further antiemetics were administered during the operation."

Line 131: What type of randomization did the system create? Fixed block? Permuted Block? Please explain

We explain that the method is minimisation and identify the stratifying variables and their levels, we don’t see what else we can say.

No change made

Line 135: Please spell PCA

Patient controlled analgesia Inserted in paragraph 6 of methods

Line 140: In Line 137 the authors stated that intra-operative form was not inserted in medical notes to maintain blindness of outcome assessors. However, anesthetic form is an important part of medical

The intraoperative form mentioned is a specific trial form to record treatment administration. This is separate from

We have revised the text to make this clear as follows: “The record of administration of

records in perioperative medicine. The authors should clarify if the involved anesthesiologists completed specific intraoperative form for the porpuse of the study or they used the usual anaesthesiological record. In the second case, they should explain how centres deal with the lack of anaesthesiological records in the medical chart (specific Ethics Committee waiver?).

the anaesthetic form recorded within the medical notes. The administration of dexamethasone was thus not included in the anaesthetic form. For safety reasons, guidance was provided to contact the trials unit if emergency unblinding was required. This happened on two occasions out of the 1,350 patients in the trial.

dexamethasone was coded only on the trial-specific intra-operative form by the anaesthetist and not in the routine anaesthetic record within the medical notes to ensure staff involved in post-operative care remained blinded to the treatment allocation. Each trial intra-operative reporting form was placed in a sealed envelope and sent to the Trials Unit. The study participants and all clinical staff other than the anaesthetist administering the allocated treatment were thus blinded to treatment allocation. ”

In Lines 165-167 it can be seen that IDMC suggested that the primary outcome should include both patient and clinician reported episodes of vomiting recorded in patient notes. It could mean that there was a phase in the trial when the primary outcome was only based only on reported episodes of vomiting or vomiting recorded. If yes, how many patients have been already enrolled at the moment of changing the primary outcome?

See note 2 above. We have edited this information into the first paragraph of the statistical analysis section: “The independent data monitoring committee (IDMC) met three times and reviewed interim analyses at three time points when 365, 700 and 1170 participants had been recruited. Due to faster than expected recruitment, at their second meeting the IDMC advised increasing power to 90% raising the final target sample size to 1320 participants. At the same time, the IDMC also clarified that the primary outcome should include both patient and clinician reported episodes of vomiting recorded in patient notes to ensure that all vomiting episodes were captured.”

Line 184: Authors should state at which point the p-value was We agree Included “and P<0.05 was considered

considered as significant (p= 0.05?)

statistically significant” in the statistics section

Line 212: It is a huge number of protocol violations for a randomized trial. Authors should give their explanations for this number (low centres' protocol knowledge? Or...? See below)

This study included patients undergoing major surgery, often whist acutely unwell and on occasion sadly succumbed to their illness. In such circumstances, when monitoring complex interventions being undertaken by multidisciplinary teams of clinicians, decisions to change practice during the procedure are common. In practice the number of such events to some extent reflects the major nature of the intervention and demonstrates that we have reached the target population we wished to test.

We have added the following to the discussion of the protocol non-compliance (paragraph 6 of discussion). “This may reflect that the patients recruited to this trial were undergoing major surgery undertaken by multidisciplinary teams of clinicians, where decisions to change practice during procedures are common.”

Line 223-226 The authors should describe the results for their primary outcome without taking the overall number into account and without discriminate between "recorded by clinicians or patients". To improve clarity, they should described proportions of primary outcome in each group at first, followed by the statistical measure of comparison.

We have reordered this section of results. We retain the clinician and patient only reported outcome measures as the sensitivity analysis to investigate the impact of the IDMC decision.

Overall, 395 (29.3%) participants experienced the primary outcome of post-operative vomiting within 24 hours of surgery significantly fewer in the dexamethasone arm (N=172; 25.5%) than on standard care (N=223; 33.0%); (RR 0.77, 95% CI 0.65 – 0.92; p=0.003) (Figure 2). Thirteen (95% CI: 5 to 22) patients need to be given dexamethasone pre-operatively to avoid one patient suffering vomiting in the first 24 hours. Two-hundred and fifty-one (63.5%) of the patients experiencing the primary outcome had vomiting episodes noted by both clinicians and patients, 119 (30.1%) by patients only, and 25 (6.3%) by clinicians only. The treatment effect was

of very similar magnitude in episodes recorded by clinicians (RR 0.77, 95% CI 0.62 – 0.95; p=0.02) or reported by patients (RR 0.75. 95% CI 0.63 to 0.89; P=0.001).

In Line 228 Please report numbers and proportions before describing with words the comparison of the effect.

Addressed with previous point Addressed with previous point

In the paragraph "Adverse events" why the authors decided not to report statical measure of comparison between proportions?

The adverse events presented were numbers of events not numbers of patients experiencing events. We have revised the presentation of this data to facilitate statistical comparison. We also noted that in error we had included a very small number of individuals whose adverse events were beyond the 30 day time period.

We have added in comparisons, reporting both numbers of patients experiencing each target event and the statistical comparisons.

Line 287 Please be careful to use the term "blinded" to describe the trial. Authors should avoid to use this term in this way. To have blinded assessors (with the potential bias of one member of the perioperative team who is not blind to the intervention) does not mean to have a "blinded" trial. In Line 289 the authors should describe again that the 8 mg of dexamethasone was added to standard care. This is very important to interpret the effect.

See above for our justification of retaining the use of blinded.

No change made

Line 318 The avoidance of a placebo/masking was the main point of weakness of the study. I suggest the authors to delete from Line 316 to 321 since this paragraph may be not of interests for the readers.

Respectfully we disagree. We think it is important the highlight these aspects of the study given the challenges of completing pragmatic trials in surgery. The importance of efficiency in research is of critical importance to trial funders.

No change made

To successfully complete a >1000 patient trial of an IMP using the model we have used should be more widely considered.

Line 323 I regret to say that I do not agree with the authors. Blinding to the intervention and blinding of outcome assessment are not interchangeable. They are two fundamental part of a trial design. The absence of the blinding to the intervention is a bias if the treatment is prone to masking (as in this case). In my opinion, authors should say that they "tried to reduce the effect of the lack of blinding to the intervention with blinding of outcome assessors". Moreover, according to the authors, anaesthesiologists were the only physicians aware of the treatment allocations. However, anaesthesiologists are perioperative physicians who usually take part of their patients’ management. It is hard to believe that involved anaesthesiologists did not take part in post-operative management of their patients so it is not possible to exclude influence. Moreover, it is very hard for the anaesthesiologists to hide to everyone in the operating rooms (surgeons, nurses....), after randomization, the administration of dexamethasone. In my opinion, investigators should clearly stated that the lack of placebo/masking is a bias and that they tried to reduce the influence of this bias with some measures that cannot reliably exclude the possibility of bias in blinding of outcome assessment. In my opinion, the authors should delete the sentence in Line 328-329.

Whilst the reviewer correctly raises the point that the anaesthetist may sometimes visit the patient after surgery, however, in practice this would only happen in the immediate post-operative period. It is exceptionally unlikely that the care of patients once they have left the recovery ward will be influenced by the same anaesthetist. The data shows there is a continued effect from Dexamethasone out to 72hrs. This indicates that anaesthetist induced bias (which would be theoretically possible in the first few hours) was not substantially impacting on this effect We believe that we have fully and honestly described the way in which the allocation was made and concealed, and that readers of the trial report will be able to judge the risk of bias from the pragmatic approach we adopted.

We have added the following to the methods “We aimed to minimise the impact of the anaesthetist being aware of the allocation by dictating the timing of randomisation to be after administration of the standard antiemetic, ensuring that no paperwork existed in the patient notes and that anaesthetists were clearly informed that they should not reveal the allocation to patients or clinical staff. The same anaesthetist would only exceptionally be involved in post-operative care, and the possibility that they could influence post-operative antiemetic prescribing was judged minimal.” And we have added the following to the discussion “Whilst we cannot completely exclude the possibility that the lack of blinding of anaesthetics could influence post-operative prescribing, this is highly unlikely to have occurred as it the exception that patients in the study would have been managed post-operatively on hospital wards by the same anaesthetist.”

The authors should give their interpretation of the high number of Discussed in very similar point 7 points This is addressed in the discussion. As

protocol violation (administration of antiemetics). Notably, the protocol violations were done by people who were aware of allocation group. In my opinion authors should delete the sentence in line 328-329.

above. stated above we have expanded this.

Authors should add as first limitation the absence of placebo/masking and the very hard work of anaesthesiologists to be the only physicians/perioperative team members to be aware of the treatment allocation.

A paragraph already exists in the discussion describing these limitations, but it is currently positioned prior to the word “limitations”. A simple reordering of text will meet this concern.

The sentence “There are limitations to this pragmatic trial” has been moved to be before the previous paragraph.

In my opinion, conclusions should be rewritten describing that the intervention were tested in association with specific standard practice.

We believe that this is already clear No change made.

Reviewer 3 Peter Buhl Hjortrup, MD

1. Statistical analysis plan (SAP). I have not been able to see any reference to a SAP. Was a SAP performed? If so, I would recommend adding a dated version as an online supplement to the manuscript. The 25-72 hour and 73-120 hour post-operative observation periods for the PONV outcomes do not appear in the protocol or the ISRCTN registration. If any outcome measures/analyses were not pre-defined, I would suggest designating them as such in the manuscript.

See note 1

See response to note 1.

2. Outcome discrepancies The manuscript described analysing 7 outcomes, but the ISRCTN registration only mentioned 5 secondary outcome measures and the trial protocol mentioned 8. The 8th outcome measure in the protocol (‘Risk of infection as measured up to 30 days (wound infections/dehiscence, anastomotic

See note 1 We have added more detail about adverse events to results

See response to note 1. We have added the following about adverse events “No patient in either arm developed new

leaks, intraabdominal collections, urinary/chest infections and new onset diabetes’(page 10)) was reported as adverse events. I would suggest reporting the infections as secondary outcome measures as outlined in the protocol. Also, were there any SAEs/SARs (as defined by the remaining on the list in the protocol (page 17)) or SUSARs during the trial?

onset diabetes. There were no suspected unexpected serious adverse reactions reported, and no serious adverse events were judged as definitely related to trial treatment. There were two cases of sepsis and two gastrointestinal bleeds judged as probably or possibly related to trial treatment, which were split evenly across study arms. ”

3. Blinding Page 7 L94 stated ‘double-blinded’ whereas other mentions of the design stated ‘blinded’. I would suggest using blinded consistently. Also, were investigators collecting data for the CRF and the statistician blinded to the intervention? If, so I would suggest mentioning this in the manuscript. Also, although I understand the pragmatic rationale for having the anaesthetist administering the intervention unblinded, I think the lack of complete blinding with placebo merits mentioning in the limitations paragraph.

Agree. See note 3 above.

The single mention of “Double blind” was an error which has been removed. We have been clearer about who was blind in the first and sixth paragraphs of the methods, and made the lack of complete blinding the first item in study limitations

4. References Page 5 L41 and page 9 L162 refer to the IMPACT trial as a systematic review (ref 5). In my opinion, a factorial trial is a better term. Page 5 L43-46. I have not been able to locate the recent study that the authors refer to and the reference at the end of the sentence (ref 6) was a systematic review where I could not find the 34.8% requiring antiemetics?

Thank you pointing out the error with reference 5.

We have changed “systematic review” to “factorial trial” at these two points, and have indicated that the 34.8% figure came from reference 5 not reference 6.

5. Stratification variables The authors commendably chose to stratify for known risk factors for the primary outcome. However, in a pragmatic multicentre RCT, I would have expected trial site to have been added as a stratification variable. This would mitigate some of the – presumably – substantial variation in clinical practice across trial

When using minimisation randomisation methods, stratifying by trial site increases the risk of the next allocation becoming predictable, and was not implemented for this reason.

No change made.

sites. The ICH-GCP guideline E9 states (p26)1: ’If one or more factors are used to stratify the design, it is appropriate to account for those factors in the analysis’. And later same page: ’Special attention should be paid to centre effects…’ Did the authors omit this for a specific reason? Also, it is recommended to adjust the analyses for stratification variables, but the authors chose restrict the stratification variables to predefined subgroup analyses. The CONSORT statement encourages that the trial design is reflected in the analysis including adjustment for stratification variables (item 12b) and not doing so has been criticized in the statistical literature (Kahan et al Stat Med 20122). This is only a minor point, but the authors may consider doing so – especially if the conduction of analyses was not predefined.

The variables we have stratified the analysis on are those that were used in the minimisation algorithm. The SAP stated that the primary outcome would be analysed as a simple comparison of proportions, not with adjustment, and thus we have followed our pre-stated analysis plan. Whilst we agree that adjustment for study design variables is now preferred, and would use this in new trials, the different it makes in reality is very small, and does not affect the conclusion of this study.

6. Choice of maintenance agent Almost 90% of the patients received a volatile agent as maintenance; thus, a maximum of 13.6% received propofol – do the authors have data on how many patients receiving propofol? The IMPACT factorial trial (ref 5 of the manuscript) found that use of propofol as maintenance reduced the occurrence of PONV as compared to volatile agents. Since the vast majority of patients received volatile agents, the generalizability to patients receiving propofol as maintenance may be limited. I would suggest discussing this as a limitation in the manuscript.

93 patients received propofol (7.0%). We can add a comment to the discussion to highlight this issue.

WE have added the following sentence to the discussion “Whist maintenance with propofol is known to reduce PONV, only 93 patients (7.0%) in the trial received propofol.”

7. Prior PONV data Do the authors have data on the incidence of prior PONV in the trial cohort? Page 13 L303-305 reads as if it was equally distributed between the two groups. It would be much interesting to assess the intervention effect on

No we did not collect PONV history at baseline (see Appendix form E for data collection at baseline).

No change made

patients having higher (i.e. multiple risk factors) vs. lower a priori risk of PONV in addition to the subgroup analyses of individual risk factors presented in the manuscript. This could in my opinion strengthen the conclusions of the trial (i.e. if there were no interaction between the intervention and a priori high vs. low risk of PONV).

8. The independent data monitoring committee (IDMC) The trial experienced an infrequent occurrence in conduction of large-scale trials with recruitment substantially faster than expected. The decision to let the IDMC decide whether to increase the sample size or not was a clear strength. Was approval from an Ethics Committee needed for expansion of sample sizes in the UK? The protocol stated that the IDMC would perform interim analyses annually, but the manuscript and CONSORT checklist (7b) do not mention any interim analyses being conducted?

Yes, the increase is sample size required a major amendment to the protocol which was approved by the ethics committee. See response to the editors comments (this was Version 3.0 of the protocol).

No change made

9. Allocation As I read it, the computerized minimization procedure ensured allocation concealment. If so, I would suggest adding a sentence stating that allocation was concealed, because lack of allocation concealment is associated with high risk of bias

Agree

We have added the following in the description of how interventions were allocated “, thus ensuring allocations were concealed until standard care had been delivered.”

10. Figure 2 For clarity, I would suggest adding a mention that the blue/red comparison from 0-24 hours was the primary outcome measure of the trial.

Agree

We have added the following footnote to Figure 2. “The primary outcome is the comparison of vomiting in 0-24 hours (comparison of the first red and blue bars)”.

Full references: 1. ICH Steering Committee. International conference on

harmonisation of technical requirements for registration of pharmaceuticals for human use. ICH Harmonised Tripartite Guideline for Statistical Principles for Clinical Trials, Third ed. 1998. Brookwood Medical Publications Ltd.Moher D, Hopewell S, Schulz KF 2. Kahan BC, Morris TP. Improper analysis of trials randomised using stratified blocks or minimisation. Stat Med 2012;31(4):328-40.