Quality of Cochrane reviews: assessment of sample from 1998BMJ 2001; 323 doi: https://doi.org/10.1136/bmj.323.7317.829 (Published 13 October 2001) Cite this as: BMJ 2001;323:829
w1 Kirchner V, Kelly CA, Harvey RJ. A systematic review of the evidence for the safety and efficacy of thioridazine in dementia. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w2 Lauzon L, Hodnett E. Antenatal education for self-diagnosis of the onset of active labour in term pregnancy. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w3 Gillespie WJ, Walenkamp G. Antibiotic prophylaxis in patients undergoing surgery for proximal femoral and other closed long bone fractures. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w4 Arroll B, Kenealy T. Antibiotics versus placebo in the common cold. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w5 Everard ML, Matthew K. Anti-cholinergic therapy for treatment of wheeze in children under the age of two years. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w6 Roos YBWEM, Rinkel GJE, Vermeulen M, Algra A, van Gijn J. Antifibrinolytic treatment in aneurysmal subarachnoid haemorrhage. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w7 Roe B, Williams K, Palmer M. Bladder training for the treatment of urinary urge incontinence. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w8 Kellner JD, Ohlsson A, Gadomski AM, Wang EEL. Bronchodilator therapy in bronchiolitis. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w9 Lauzon L, Hodnett E. Caregivers’ use of strict criteria for the diagnosis of active labour in term pregnancy. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w10 Price JR, Couper J. Cognitive behaviour therapy for adults with chronic fatigue syndrome. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w11 Jones C, Cormac I, Mota J, Campbell C. Cognitive behaviour therapy for schizophrenia. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w12 Daya S. Comparison of gonadotropin releasing hormone agonist (GnRHa) protocols for pituitary desensitization in in vitro fertilization (IVF) and gamete intrafallopian transfer (GIFT) cycles. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w13 Steinhart AH, Ewe K, Griffiths AM, Modigliani R, Thomsen OO. Corticosteroid therapy for maintenance of remission in Crohn’s disease. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w14 Jepson RG, Mihaljevic L, Craig J. Cranberries for the prevention of urinary tract infections. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w15 Jepson RG, Mihaljevic L, Craig J. Cranberries for the treatment of urinary tract infections. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w16 Joy CB, Adams CE, Rice K. Crisis intervention for severe mental illnesses. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w17 Couchoud C. Cytomegalovirus prophylaxis with antiviral agents in solid organ transplantation. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w18 Kearney CE, Wallis CE . Deoxyribonuclease (DNase) therapy in cystic fibrosis. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w19 Fontaine O, Gore SM, Pierce NF. Diarrhoea treatment: rice-based oral rehydration solution. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w20 Wilkinson EAJ, Hawke CI. Does oral zinc aid the healing of chronic leg ulcers? In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w21 Lethaby A, Irvine G, Cameron I. Effectiveness of cyclical progestagen therapy in reducing heavy menstrual bleeding. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w22 Engels EA, Lau J. Efficacy and toxicity of typhoid fever vaccines. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w23 Parker MJ, Handoll HHG, Chinoy MA. Extracapsular hip fracture fixation: comparison of different extramedullary fixation implants (fixed nail plates, RAB_plate, Pugh nail, Medoff plate, sliding hip screw). In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w24 Parker MJ, Handoll HHG, Bhonsle S, Gillespie WJ. Extracapsular proximal femoral fractures: condylocephalic nails (Ender or Harris nails) versus extramedullary implants (fixed nail plates or sliding hip screws). In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w25 Cates CJ, Jefferson TO, Bara AI. Influenza vaccination in asthma: efficacy and side-effects. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w26 Ohlsson A, Lacy JB. Intravenous immunoglobulin (IVIG) in suspected or subsequently proved neonatal infection. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w27 Simmer K. Longchain polyunsaturated fatty acid supplementation of term infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w28 Sowden AJ, Arblaster L. Mass media interventions for preventing smoking among young people. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w29 Kuschel CA, Harding JE. Multicomponent fortification of human milk for premature infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w30 Tuunainen A, Gilbody S. Newer ‘atypical’ antipsychotic medication versus clozapine for schizophrenia. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w31 Pinelli J, Symington A. Non-nutritive sucking in premature infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w32 Harrison JE, Ashby D. Orthodontic treatment for posterior crossbites. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w33 Lumley J, Watson L, Watson M, Bower C. Periconceptional supplementation with folate and/or multivitamins to prevent neural tube defects. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w34 Lethaby A, Vollenhoven B, Sowter M. Pre-operative GnRH analogue therapy before hysterectomy or myomectomy for uterine fibroids. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w35 Subramaniam P, Henderson-Smart DJ, Davis PG. Prophylactic nasal CPAP in very preterm infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w36 Evans DJ, Levene MI. Prophylactic neonatal anticonvulsant therapy following perinatal asphyxia in full term newborns. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w37 Kennedy KA, Tyson JE. Rapid vs. slow rate of advancement of feedings in parenterally fed low-birth weight infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w38 Bell EF, Acarregui MJ. Restricted vs liberal water intake in premature infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w39 Van den Ende CHM, Vliet Vlieland TPM, Munneke M, Hazes JMW. Rheumatoid arthritis (RA): Dynamic exercise therapy in RA. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w40 Lancaster T, Stead LF. Self-help interventions for smoking cessation. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w41 Linde K, Mulrow CD. St John’s wort for depression. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w42 Watson A, Vandekerckhove P, Lilford R. Subfertility: pelvic surgery: pharmacological and liquid adjuncts to prevent adhesions. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w43 Martin-Hirsch PL, Paraskevaidis E, Kitchener H. Surgical treatment of cervical intraepithelial neoplasia (CIN). In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w44 Poole PJ, Black PN. The effect of mucolytic agents on exacerbation frequency in chronic bronchitis. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w45 Birks JS, Melzer D. The efficacy of donepezil for mild and moderate Alzheimer’s disease. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w46 Brocklehurst P, Hannah M, McDonald H. The management of bacterial vaginosis in pregnancy. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w47 Wood-Baker R, Walters EH. The role of corticosteroids in acute exacerbations of chronic obstructive pulmonary disease. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w48 O’Brien P, Vandekerckhove P. The technique of insemination with donor sperm: a systematic review of randomised controlled trials comparing intra-uterine and cervical insemination. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w49 Crockett AJ, Cranston JM, Latimer, KM, Alpers JH. The use of mucolytics in bronchiectasis. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w50 Liu M, Wardlaw J. Thrombolysis in acute ischaemic stroke: direct randomised comparisons of different doses, routes of administration and agents. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w51 Hajenius PJ, Mol BWJ, Bossuyt PMM, Ankum WM, Van der Veen F. Treatment of tubal ectopic pregnancy. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w52 Elbourne D, Wiseman RA. Types of intra-muscular opioids for maternal pain relief in labour. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
w53 Darlow BA, Graham PJ. Vitamin A supplementation in very low birthweight infants. In: Cochrane Library. Issue 4. Oxford: Update Software, 1998.
Comment on the Cochrane review ‘Antibiotics for the common cold’
Comment by Heather McIntosh
METHODS and METHODOLOGICAL QUALITIES OF INCLUDED STUDIES
The reviewers use a scoring system for methodological quality, whereby each trial is given a numerical score on a scale of 1 to 12 points, which they say is described in the Cochrane Handbook. The Handbook in fact advises against composite scores as they are not transparent. In the Methodological quality of included studies section, the reviewer’s then say that they do not think that these scores are an accurate measure of study quality. Furthermore, trial quality is not incorporated into interpretation of the results. It is therefore difficult for the reader to assess how systematic bias in the included studies might have affected the findings reported in the review.
It is not clear how concealment of allocation in each trial was assessed. Have the reviewers erroneously used reporting of double blinding in the trials to assess concealment of the allocation sequence? The trials Howie 1970, Kaiser 1996 and Taylor 1977 are reported as having adequate concealment of allocation (A) yet there is no description of how this was achieved. In the trials Hoaglund 1950 and Lexomboom 1971, allocation concealment is reported as unclear (B) yet, according to the Table of characteristics of included studies, in the latter only the pharmacist knew of allocation. Also, why have the reviewers use the option (D) not to assign a score for allocation concealment to the trial Sutrisna 1991? The reader can not find any information in the review about adequacy of allocation concealment for the trial Gordon 1974. he statement, in Methodological quality of included studies, that "Loss to follow-up was an issue for a number of studies..." needs to be expanded and loss to follow-up in each trial should be documented in the table of characteristics of included studies. Presumably the denominators used in the analyses are patients who were evaluable? How might loss to follow-up have affected the findings in the review (worst case and best case scenario)?
In the meta-analysis of General improvement, it would be better to present the Hoaglund study separately if, as the reviewer’s say, there is good biological reason why measuring this outcome at 24 hours does not make sense.
It is questionable to calculate numbers needed to treat and numbers needed to harm from pooled data without qualification of the conditions to which they apply, and they should not be reported without confidence intervals.
There are several small inconsistencies in the numerical data reported in the text compared with the graphs.
The statement, in Implications for practice, that "many patients will get adverse effects" from antibiotics is not supported by evidence presented in the review. The principle of using a random effect model of analysis where there is significant heterogeneity, without going on to explore possible reasons to explain it, is questionable.
The references should be listed in the appropriate reference sections rather than included as text at the end of the conclusions.
Comment on the Cochrane review ‘Anti-cholinergic therapy for wheezy infants’
Comment by Jeanette Ezzo and Phil Alderson
We believe including the following additional information would strengthen this review:
Under the types of outcomes, it would be helpful to the reader to have the primary and secondary outcomes enumerated. For example, the duration of hospital stay may be a secondary, but the symptoms scores may be primary. Along these same lines, it seems important the symptoms scores were measured by blinded assessors and it would be interesting to see a sensitivity analysis of the blinded vs unblinded assessments of symptoms scores. We would also appreciate a more detailed description of the process of data extraction (who did it and how?), and the approach to heterogeneity. Finally, the summary statement which says *the results present do not support the uncritical use of anticholinergics for the treatment of wheeze* could be clarified as to whether this means evidence of no effects or insufficient evidence.
Comment on the Cochrane review ‘Cognitive behaviour therapy for schizophrenia’
Comment by Victoria Hadhazy and Jos Kleijnen
The reviewers found that most of the steps in the review process were sufficiently executed and reported. However, the title of this review is precise for a diagnosis of schizophrenia, and some of the patients in the included studies had diagnoses of manic-depression, delusional disorder, schizoaffective disorder, and unknown diagnosis. Also, the authors report in Implications for Practice, "CBT is associated with a substantially reduced risk of relapse." This may be too strong a finding as the confidence interval crossed 1 on this outcome.
Comment on the Cochrane review ‘Corticosteroids for remission maintenance in CD’
Comment by Phil Alderson and Jos Kleijnen
The restriction to specific languages may introduce bias. It might be better to simply report studies that were found but remain to be translated in the ‘studies awaiting assessment’ section.
Although the trials did not report much information on the side effects of steroids in this setting, it might be useful to have a short discussion of their side effects in general.
Comment on the Cochrane review ‘Corticosteroids in COPD’
Comment by Peter C Gotzsche
It is certainly useful to know that there is only one large trial addressing this important question. This trial dominates the review and contributes more than 80% of the weight in many of the statistical analyses. In this situation, one would have expected a more comprehensive assessment of the internal and external validity of this trial which seems to suffer from major weaknesses. I feel there are a number of other major and minor problems with the review and that its conclusion is misleading. I therefore suggest it be subjected to peer review again.
There are many linguistic and typographical errors, e.g.: "COPD" should not be used in a title. "Outcome measures include: 1. Lung function measurements, pre- and post-bronchodilator. 2 Arterial Blood Gas measurements. " (capital letters to be avoided for consistency)
"Authors of identified trial were contacted" (trials should be plural) "using simple agreement, kappa and weighted kappa statistics In addition" (full stop is lacking)
"Subjects ³45 years" (many similar supscripts appear in the table)
" Smoking history >10 pack years" (what does this mean?)
"Analysis of these showed a significant difference treatment benefit." (in is lacking)
"Selection criteria: Randomised controlled trials comparing corticosteroids, administered either parenterally or orally, with appropriate placebo and other interventions standardised. " (What exactly does this mean?)
"Main results: We have identified 5 studies that show treatment with corticosteroids is beneficial when assessed as the FEV1 between 6 - 72 hours after treatment. " (This wording gives the reader the impression that there were some additional studies which had found no effect, and, indeed, there were 7 included studies. How many studies were included and what was the overall result?)
"Conclusions: Treatment with oral or parenteral corticosteroids significantly increases the FEV1 up to 72 hours when compared to placebo in subjects with acute exacerbations of COPD. " (This conclusion in the abstract is unwarranted, see below.)
"Types of intervention. Corticosteroids, administered either parenterally or orally, with placebo injections or tablets as appropriate. " and "All randomised controlled trials comparing oral or parenteral corticosteroids with appropriate control" (This is confusing and inconsistent wording, "placebo" and "appropriate control" is not the same. Should specify that the experimental treatment is a corticosteroid and that the control is a placebo, if that is what it is.)
"the reliability of the diagnosis of COPD using the criteria...3. Previous physician diagnosis of asthma." (is it not an exclusion criterion?
Otherwise, the review might concern asthma).
Methodological qualities of included studies: "There was agreement between observers on the quality of the studies (kappa = 1)." This contrasts with the description under results that: "There was only 50% agreement between reviewers, but 100% agreement after resolution by a third assessor in assessment of the quality of the studies." Further, if the third person has decisive power, it is not strange that the agreement goes up to 100%?
"It was not possible to verify the diagnosis of COPD as complete data was available for only one study." This means that asthma cannot be excluded. This weakness seems to be detrimental to the whole review. In particular, the study by Bullard, which has 96% weight in the meta-analysis of early FEV1, included patients with "suspected chronic airflow limitation" which does not exclude asthma. This needs to be made explicit in the discussion, implications and abstract.
Health status has been measured on different scales, e.g. -85, SD 11 and -3.40, SD 1.50, but it is not clear whether the authors have used the standardised mean difference to analyse it as no numerical results are shown. This deficit needs correction. Further, there is large heterogeneity for treatment failures and duration of hospitalisation. How were these analysed and what were the results? The authors should try to explain the heterogeneity.
Total numbers of patients in the studies reviewed should be added to the results and abstract sections. The presentation of results in the table and figures are confusing (no units given).
The results of the quality assessment (Jadad scale) are not given.
Implications for practice:
"There is evidence to support the early use of oral or parenteral corticosteroids in exacerbations of chronic obstructive pulmonary disease."
I strongly object to this conclusion, which is unwarranted and misleading, see above and the results and discussion sections. The authors write themselves that "the numbers were small, with few studies reporting complete data. The mortality rate was higher in the treatment group and thus the improved early FEV1 outcome and shortened hospital stay may come at a price." Actually, as the total numbers of deaths were 5/100 vs 3/85, it seems unwarranted to say anything about increased mortality with steroid treatment (it could also be lower, for example, since the 95% CI for the relative risk is 0.38 to 4.11). And the review might have addressed asthma, rather than exacerbations of chronic obstructive pulmonary disease.
Comment on the Cochrane review ‘Diagnosis of active labour in term pregnancy ‘
Comment by Peter C Gotzsche and Philippa Middleton
The stated objective is to assess strict diagnostic criteria, but the actual intervention is labour assessment (plus advice, support and encouragement) vs direct admission to the labour and delivery unit.
"Randomised controlled trials comparing caregivers’ application of strict diagnostic criteria for active labour versus routine practice; violations of allocated management not sufficient to materially affect outcomes; missing data insufficient to materially affect the comparison. "
This restricts the RCTs which qualify and the decision which studies to exclude appears to be too subjective. You should preferably include all studies and discuss such problems within the review rather than exclude studies beforehand.
Outcomes duplicated; mentioned under Objectives and again, under Types of outcome measures.
"A manual search of the Group’s identified resources were conducted for the year"
It seems to have been electronic, not manual. Was, not were.
"The reviewers independently selected and assessed the single trial resulting from the search."
This is very surprising, and the abstract should mention that there was only one trial, and its size and effects. The Results section does not mention trial size either.
"There is some performance bias noted as some controls (16.3%) were assessed and discharged undelivered following direct admission, in comparison to 18.6% of the experimental group. This, however, may be attributable to the routine care to which the control group was randomised."
Why should this be performance bias? Only when reading the table, does it become clear that all control patients should have been in hospital. But then it is a poor study, as it does not reflect real life. Further, it does not test the hypothesis: "strict diagnostic criteria for active labour versus routine practice". It is not routine practice to keep all women in hospital, some of them are at least always sent home to wait a bit more.
The statistics in the abstract and text are different from Metaview (Metaview appears to be correct). Intrapartum oxytocics is 0.45, 0.25 to 0.80 in Metaview but 0.44, 0.24 to 0.80 in the text; analgesia is 0.36, 0.16 to 0.78 in Metaview, but 0.31, 1.26 to 7.13 in the text.
"analgesia (OR = 0.31; CI. 1.26, 7.13)"
The odds ratio is not included in the CI, so there must be an error.
Outcomes are missing in the table.
This review is not testing the diagnostic criteria, but something a lot broader. How can we tell if the criteria are making a difference or whether the other support is just as important, perhaps even more important? The review needs to be completely re-oriented to reflect this or alternatively it should state that no eligible studies were found.
Comment on the Cochrane review ‘Diarrhoea and rice based ORS ‘
Comment by Jeanette Ezzo and Jos Kleijnen
Thank you for an informative review on an important topic. We have some minor suggestions to help make the review clearer in some sections.
Background/types of outcomes
Ther rate of stool loss is mentioned in the background but not selected as an outcome. An explanation of why this is so would be helpful.
Methods of the review
It would be helpful to have a description of how the data were synthsized and whether heterogeneity was tested.
Under methodological quality of included studies, the reviers state that intention to treat analysis was not performed in some of the trials and that some dropouts were treatment failures. We would like to see a subgroup analysis including only trials which reported on all randomized participants, to see if the overall results were different.
We acknowledge the short follow-up period of 24 hours reported in most trials, and suggest that the reviewers might recommend a longer floow up in the implications for research or explain why longer follow up is not clinically important.
Comment on the Cochrane review 'DNase therapy in cystic fibrosis
Comments by Andrew Herxheimer & Ole Olsen
Much effort has gone into this difficult and potentially very useful review; however, we have the following comments.
1. In the abstract the results section states ‘No reduction in mortality for treated patients was identified (Relative Risk at six month 1.01, 95%CI 0.09, 11.11).’ However the meta-view graph reports only a subgroup analysis and the estimate reported in the abstract is based on only one study reporting three deaths at six months follow-up. But additional deaths are reported in other studies with one or three months of follow-up; in total the numbers of deaths are 13 vs. 7 with the excess mortality in the experimental group.
The statement in the conclusion: ‘Studies are of insufficient duration to identify a reduction in mortality’ is misleading. It would be more correct to say ‘The studies are small and inconclusive, but suggest an increased mortality.’
2. The results section seems to be an unfinished draft:
a. The first statement under item 1 is a repetition of a subset of what follows (item 1.c).
b. The first result reported under item 1.a. (8.08) does not appear in Meta-view.
c. The last statement under item 1.a. belongs under 1.b.
d. The trial mentioned under 1.c does not appear in Meta-view.
We have not checked the other outcome measures.
3. In the first subgraph (FVC) in meta-view there seems to be an error in the most influential trial (weight=66.9%) as the s.d. is 0.15 in the expt group and 3.47 in the ctrl group.
We suggest (i) that the data are re-entered into Revman and checked, (ii) that the subgroup analyses (1, 3, and 6 months) may be maintained but that an overall analysis is carried out as well - otherwise power may be lost in the statistical tests (iii) that the results section is rewritten.
4. Metaview includes 19 tables, but only 6 of these contain any numbers. The fact that so many tables are empty is already mentioned in the text, but this point could be discussed more explicitly under Results, and perhaps re-emphasised under ‘Implications for research’. Furthermore, the summary graph would be more informative, if overall analyses were carried out as one could immediately read off the graph whether there were any data at the subgraphs.
5. The objectives include consideration of the dose of DNase if an effect was found. An effect was found [see next point, #6] but the review does not consider dose, although in the largest study (Fuchs) some patients received DNase once and others twice daily
6. a. Voice alteration emerges clearly as an adverse effect, but is not described or discussed. What is the alteration, how was it detected in the studies that report it, was it looked for in the others, is it reversible, what did the patients feel about it? b. It may be worth combining the data for pharyngitis, laryngitis and voice alteration, in addition to considering them separately, since they are closely related forms of local toxicity, very likely produced in the same way.
7. Mucociliary clearance and sputum viscosity were examined in some excluded studies. The possible relevance of these deserves brief discussion. Should their measurement in future trials be encouraged or not, and on what grounds?
8.a. The Table of trial characteristics should include the number of patients in each treatment group for each trial.
b. That DNase was nebulised is explicitly stated only for the studies by Laube and Ramasinha. Presumably it was nebulised in all the studies.
c. The source of the DNase is not stated. The acknowledgement to Genentech suggests that this company produced some or all of it, but this needs to be stated. It is possible that different preparations were used in different trials [even if all were made by the same manufacturer].
9. Three references to excluded studies are incomplete [Hemming, Hubbard, Majaesic].
10. The abbreviation rhDNAse is cumbersome and not explicitly explained. The review would be more comfortable to read if DNAse [or possibly rDNAse] were used throughout.
Comment on the Cochrane review ‘Ectopic pregnancy: All treatments’
Comment by Phil Alderson and Peter C Gotzsche
This thorough review addresses an important question and covers many
comparisons. This has the unfortunate effect of making it a very long review to read. As it stands the abstract is very long and could contain more numerical results instead of text. We presume that the abstract will be rewritten during 1999 to conform to the recently agreed structure and word length.
TYPES OF STUDIES
The authors state that only published studies were included but, for example, the Dias Pereira study is listed as ‘unpublished data only’.
TYPES OF INTERVENTION
Although the types of interventions are put into three categories, this is not clearly laid out and looks confusing in the Cochrane Library. Perhaps a blank line could be put between the categories.
METHODOLOGICAL QUALITIES OF INCLUDED STUDIES
"Meta-analysis was only possible for one comparison, ie. laparoscopy versus open surgery [Vermesh 1989, Koninckx 1991, Lundorff 1991a, Murphy 1992].
"The study by Koninckx is excluded as it was quasi randomised so was not used in the metaanalysis. It should not be mentioned in this sentence.
Under medical treatment, the rate of exclusions after randomisation is very high (29 to 43% where reported). This is worrying and should be given prominence where the results are reported.
"The assessment of patients’ preference for systemic methotrexate relative to laparoscopic salpingostomy in a case-control study showed"
This should be moved to the discussion section rather than reported in the results of a review of RCTs.
Under comparison 7, the result for tubal preservation is quoted as "RR 1.0, 95%CI 1.0, 1.0". This confidence interval must be wrong.
DISCUSSION AND IMPLICATIONS FOR RESEARCH
These two paragraphs seem to conflict with each other:
"In the evaluation of the surgical treatment of tubal pregnancy, based on the available evidence, laparoscopic surgery appears to be the treatment of choice.
Although laparoscopic conservative surgery was less successful than the open surgical approach in the elimination of the tubal pregnancy, due to the higher persistent trophoblast rate of laparoscopic surgery, this technique seemed feasible in virtually all patients, and has proven to be safe and less costly in three randomised controlled trials. Short term treatment success will continue to improve with accumulating experience of the surgeons."
"With laparoscopic conservative surgery the risk of persistent trophoblast will always remain present. Experts in laparoscopic surgery have reported low incidences of persistent trophoblast. However, their results are not generalisable to the situation in training settings. "
The first paragraph should probably be brought into line with the more cautious
second paragraph, as none of us knows what will happen when this technology is used by less experienced surgeons.
IMPLICATIONS FOR PRACTICE
"In the treatment of tubal pregnancy, laparoscopic surgery is the cornerstone of treatment. This technique is feasible in virtually all patients, has proven to be safe, and is less costly compared to the open surgical approach."
This conclusion can be debated, e.g. the comparisons with open surgery and systemic methotrexate are not that convincing, see graphs. It is true that many side effects occurred with the chosen dose of the drug, but on the positive side persistent trophoblast was noted significantly less often with systemic methotrexate. This should be mentioned to make the conclusion more balanced.
IMPLICATIONS FOR RESEARCH
There is a lot of discussion in this section which obscures the clear messages about future research.
"Study : Lund 1955 was the first randomized controlled trial in the treatment of ectopic pregnancy comparing expectant management versus operative management in 204 subacute women with a ‘typical course of ectopic pregnancy’ and a positive pregnancy test, who had no demonstrable hemoperitoneum on admission to the hospital, and were not acutely ill. The trial was carried out at the Genofte County hospital in Copenhagen, Denmark between 1930 and 1946.
Randomization was done by surgical department. In two departments eligible women were confined to bed until the pregnancy test became negative and pain ceased, whereas in one other department women were treated surgically.
Reason for exclusion:
The diagnosis ectopic pregnancy does not meet the inclusion criteria as defined for this review, ie. by the transvaginal sonographical finding of an ectopic gestational sac with an empty uterus, by a serum hCG discriminatory zone principle with an empty uterus, and/or by laparoscopy or by open surgery. "
Is the most important reason for exclusion, the randomisation by departments, rather than of patients? However, in light of the paucity of data on expectant management, it would be interesting to know the results of this study, which could be added to the discussion section. Genofte should be corrected to:
Comment on the Cochrane review ‘Fortification of human milk: Multi-component’
Comment by Jeanette Ezzo and Peter C Gotzsche
We are writing in regards to the review *Fortification of human milk: multi component.*
We believe including the following additional information would strengthen this
In the abstract: A summary using numerical data e.g., number of trials, total number of patients and results of most important outcomes, with confidence intervals.
In the methods: A description of what the methods of the Neonatal review group are, and need to specify the method for dichotomous and continuous outcomes. Also, in the graph of weight gain, the authors have used a fixed effects model despite large heterogeneity. It would be helpful to also see the data on this outcome presented in a random effects model and the presence of statistical heterogeneity needs to be mentioned in the text.
The term *blinding of randomization* in the table should be changed to concealment of allocation in order to be consistent with terminology used in other reviews and to not confuse the blinding with clinicians, parents and assessors.
In the excluded studies section: Three studies were excluded. Two of these were eligible but data could not be extracted. The third, by Lucas, "was strongly considered for inclusion in this review, particularly as this study was included in a previous systematic review of infant feeding". It would be interesting to know the sample size and results of the three excluded studies. If the studies are large and the results negative, it would weaken the conclusions of the review. It is particularly problematic not to mention anything about the study by Lucas, since a later study by this author was the largest and had negative results. We do not accept the reviewers’ rationale for excluding this study, which was also large, as it seems to be subjective: "This was not felt to represent "fortification" as
The studies which were included seem to have been of rather poor quality.
For example, the infants who developed significant illness were frequently not enrolled or not included in results. This is of concern because some of the included studies have dropout rates of nearly 50%. In only five studies are the outcomes reported for all the infants enrolled. We are not convinced by these results that fortification does any good, and, given these limitations of the included studies we would recommend that the conclusions be modified to be more cautious. Also, perhaps the abstract should mention the serious weaknesses of the sample of studies.
Comment on the Cochrane review ‘LCPUFA term ‘
Comment by Peter C Gotzsche
Few readers would be able to guess what LCPUFA is.
Is not really an abstract since it contains too detailed information, e.g.
"Visual acuity was assessed by Teller acuity cards in the study of Carlson et al (1996), Clausen et al (1996) and Austed et al (1997)" and "The Adelaide studies showed no effect of supplementation on DQ at one year (Bayley Scales of Infant Development (BSID), Makrides et al 1995 &1996)."
(the reader has not heard of any Adelaide studies before). The results section in the abstract should be very brief, in particular since there was no evidence of an effect and there were few, and very small, studies.
"Abbreviations used in this review include: LCPUFA longchain polyunsaturated fatty acids, n- omega, LA linoleic" (something is missing about omega).
"One study... was excluded because the supplements were not commenced until 3-4 weeks of age" (this is hardly warranted. The inclusion criteria for this review do not specify anything about this, and the primary authors seem simply to have suggested this fact as an explanation for their negative finding, i.e. a post-hoc rationalisation. This is not sufficient reason to exlude the study).
"For this review, visual acuity data are analysed with mean+/-SD as log values. The use of log values and differences between trials preclude the use of meta-analysis" (this is not correct. Use of log values do not preclude a meta-analysis, see, for example, the review "House dust mites and asthma". Further, the results seem to be rather homogeneous, see, for example, visual acuity at 12 months, which could easily be meta-analysed.)
Large parts of the results section describe methods and should therefore be moved to the methods section.
The review found no effect and it should therefore describe the sample sizes of the included trials, or at least the total number of patients, so that the reader can get a feeling for whether an effect may have been overlooked. Only the table of studies gives the sample sizes.
It seems superfluous to show the outcomes at many points in time in these very small studies, e.g. visual acuity after 2, 3, 4, 6 and 12 months. It would be preferable to select one point in time for each study, e.g. the longest observation period.
There are a few typographical errors:
"to have better acuity at 2 months but not at 4, 6, 9 or 12 m"
"end point" or "endpoint"?
Comment on the Cochrane review ‘Non-nutritive sucking in premature infants’
Comment by Ole Olsen and Philippa Middleton
We have encountered some major and minor problems in your very relevant review "Non-nutritive sucking in preterm infants".
The two major problems are that a) the inclusion and exclusion criteria are not very well defined and seem to have been applied inconsistently b) the conclusion seems not to be supported by good evidence. The details are explained below.
There is repetition in the results and conclusions section of the abstract (which is not how the main text of the review is structured).
The fact that the review solely focuses on pacifier sucking is neither mentioned in the title, in the background section or in the objective. Furthermore one of the trials excluded (Narayanan, 1991) is described as excluded due to ‘no intervention’, even though the abstract on PubMed states: ‘the ‘intervention’ group ...infants were allowed to suckle at the breast’. We therefore suggest that it is either clarified earlier in the text that ‘non-nutritive sucking’ refers to sucking a pacifier or that the review is enlarged to include non-nutritive breast sucking as well.
Needs to include last date when Medline and CINAHL and CCTR were searched. There is no mention of the Neonatal trials register - was this searched?
"All trials utilizing experimental or quasi-experimental designs" Is this too broad? Does it really mean randomised or quasi-randomised which would be more in line with Cochrane methodology? [The scope of the Neonatal Group is "all randomised controlled trials of interventions involving the baby during the first month after birth"].
Would any difference be hypothesised a priori about difference in length or duration of NNS or proximity to feeding?
Methods of the review:
There is some repetition in this section.
"Blindness of randomization" Does this mean concealment of allocation?
Does not state how the crossover studies will be analysed.
Description of studies:
States that eleven studies were excluded on grounds on not being relevant. However four of these eleven have only that they were experimental or quasi-experimental as the reason for exclusion in the Excluded studies list. This inconsistency is important to address since five (or six) non-randomised studies have been included and it is not clear why these should have been included and why Burroughs, Daniels, Paludetto 84 and 86 should have been excluded.
Furthermore, the only statistically significant effect is based on one small study by Bernbaum and, as far as we can see, the study is not a randomised trial (‘Infants were pair-matched for ... and were subsequently assigned to either a study or control group’).
There are 20, not 19, studies in the Included studies table. States that there were 13 randomised studies, which implies that there must be 7 non-randomised (or 14 randomised and 6 non-randomised, depending on whether the `missing’ study is randomised or not). This is important because randomised and non-randomised data is stated as being treated separately in this review. In the Included studies table: Burroughs is listed as pre-test, post-test Measel is alternate sequential series and matching Pickler 92 as uncertain Seghal as uncertain Woodson (a) as non-randomised Woodson (b) as non-randomised
All the other studies are listed either as randomised or randomised crossover. So we have presumed that there were 14 randomised studies and 6 non-randomised studies. The reviewers state that only randomised data is included in the meta-analysis. However Pickler 92 (uncertain) is included in Metaview, while Seghal (also listed as uncertain) is not included in Metaview even though it appears to have outcomes of interest (presumably weight gain). Either both Pickler 92 and Seghal need to be treated as randomised (16 randomised studies and 4 non-randomised studies) or non-randomised (14 randomised studies and 6 non-randomised studies) - or additional information given to show why the distinction between Pickler and Seghal has been made).
The results section needs to be consistent in how randomised and non-randomised material is treated both statistically and narratively. The results section begins by delineating for each outcome which studies are randomised and which are not. However this blurs towards the end and non-randomised studies are not differentiated from randomised studies, even though the results are inconsistent in some cases (eg. DiPietro (randomised) shows no effect of NNS on oxygen saturation but Burroughs (non-randomised) shows a significant improvement in TcPO2 readings. On the other hand although Woodson (a) and Woodson (b) are shown in the Included studies table, there is no mention of them in the Results section (or anywhere else in the text) although they both report heart rate outcomes.
None of the 6 (4?) nonrandomised studies can be classed as quasi-experimental - they are all experimental since they all involve some form of intervention (and a comparison). However they cannot all be classified as quasi-randomised as it is stated that Woodson (a) and Woodson (b) are non-randomised.
Some of the interventions may not be comparable eg. length of hospital stay. Two trials have been pooled, but one (Field) only controls the use of pacifier during feeds and both the experimental and control groups are offered pacifiers between feeds. Also the SDs in these two trials are very different.
The review includes many very small trials (10-59 participants) with many different outcome variables (more than 20) implying a high risk of reporting bias. Considering this, we think the conclusion in the abstract is too optimistic when it is stated:
‘This review found a significant decrease in length of stay in preterm infants receiving a NNS intervention ... The review identified other positive clinical outcomes of NNS: ... Based on the available evidence, NNS in preterm infants would appear to have some clinical benefit. It does not appear to have any short-term negative effects.’
The wording in the main text discussion is slightly more balanced: ‘NNS demonstrated a benefit in only one of the major outcomes measured. There were also a number of short-term positive results for several of the secondary outcomes. No negative effects of NNS were studied, however.’
Given the quality of the individual trials (only assessor blinding in one study, no data on a multitude of outcomes, very small trials, etc.) we think the conclusion should put much more emphasis on the methodological problems and not mention a lot of positive outcomes, when no possible negative effects have been studied. Also a clearer sorting out of the randomised and non-randomised studies may help in figuring out any patterns or trends.
Comment on the Cochrane review ‘Subfertility:Pelvic surgery: Pharmacological agents’
Comment by Philippa Middleton and Jos Kleijnen
While we found the technical quality of the review to be high, we suggest that it be edited to be more readable and comprehensible. Some technical terms (eg. hydrotubation) should be explained for non-expert audiences.
The results in the text could be better arranged, perhaps with more subheadings and could also be aligned with the results in Metaview more closely and clearly.
last para: redundant to mention that meta-analysis was used.
"Generic" search strategies do not give the reader enough information.
Would like to some more discussion of the pros and cons of the different ways of measuring pregnancy and how this might affect the interpretation of results.
Outcome assessment, subsection A) Pregnancy
The second sentence of the first paragraph is repeated in the third paragraph, which is confusing.
This section (particularly the ‘embedded’ tables) is confusing . The tables are unclear because of formatting limitations (eg. headings don’t line up with results).
The outcome of change in adhesion score % is shown in Metaview, but no trials or data are included. In the summary screen, it states that there is a "subgroup analysis" but under the detail of the outcome there is just an empty screen, which is confusing. Can this be linked to a table of the percentage changes, which is in a separate section of the review and can be formatted more clearly (as has been done in some other Cochrane reviews for reporting observational data or data that cannot be used in Metaview?
In Metaview, two outcomes are labelled identically in some comparisons, namely "Adhesions at followup (per patient)." Going to the next level of detail in Metaview, it becomes clear that the first one is a subgroup analysis of presence or absence of adhesions and the next is a subgroup group analysis of change in adhesion status. Can this be labelled at summary level?
In later comparisons when there is no data for this outcome, it is still listed as a subgroup analysis, when it should be labelled "not estimable" (or is this a ‘quirk’ of Revman?)
Metaview: Comparison labels (eg. "Intraperitoneal dextran" and Intraperitoneal heparin solution") appear to be incomplete, ie. end at versus. The review title is also truncated in Metaview.
"Although a small beneficial effect of steroids remains possible, the meta-analysis (including 481 patients) had sufficient power (more than 80% with alpha set at 5%) to exclude effects of 10% or more". My understanding is that power calculations of this type are not statistically valid for meta-analyses.
The first paragraph of the discussion section would fit better in the background. The second last paragraph of the discussion is repetition and should be deleted.
References to studies awaiting assessment
It would be helpful to provide reasons for 2 of the 3 studies that have not yet been assessed.
Comment on the Cochrane review ‘Thrombolysis in acute stroke: Different regimens’
Comment by Philippa Middleton and Victoria Hadhazy
Comment on conclusions of the review - inadequate coverage of possible harm
The reviewers found a five-fold increase in intracranial haemorrhage comparing high dose thrombolysis with low dose thrombolysis. This is discussed in the review and while the finding is not methodolologically robust enough to make definitive statements, this potential adverse effect is so important that it should be mentioned in the conclusions of the review. There also should be more discussion of the Wardlaw et al Cochrane review (and Lancet 1997) which indicated a significant (nearly five-fold) increase in intracranial haemorrhage with thrombolysis.
Comment on the Cochrane review ‘Types of IM opioids for pain relief in labour ‘
Comment by Heather McIntosh and Phil Alderson
TYPES OF OUTCOME MEASURES
There are 23 outcome measures included in this review. It is of some concern that multiple outcomes increase the probability that one will reach statistical significance by chance alone. The Table of comparisons is a daunting 4-pages long, and one of the two primary outcomes is 18th in the list.
METHODOLOGICAL QUALITIES OF INCLUDED STUDIES
The reviewers’ interpretation of the methodological quality of the trials is unclear. Perhaps reporting of double blinding has been used by mistake to assess concealment of the allocation sequence. All trials have a quality score of ‘A’ in the graphs, presumably representing adequate allocation concealment. However the reader is not given any information to see how this judgement has been made.
The section on methodological quality of included studies makes no mention of allocation concealment, and the table of included studies just contains terms such as ‘randomised’ with no more detail on allocation concealment.
The reviewer’s say that information on post-randomisation exclusions is to be found in the Table of characteristics of included studies, and in the Discussion go on to say that "post-randomisation exclusions were very common". In the table, however, it is only mentioned for two studies, Borglin 1971 in the Participants column, and Levy 1971 in the Notes column. The Methods column of this table should in general give more information on the methodology of each trial.
In the Methods of the review section, it says that analysis was by intention to treat. For pentazocine versus pethidine, the 10 women not evaluated in the trial Levy 1971 (according to the table of included studies) are not included in the analysis, neither are the 17 women who did not receive the full dose in the trial Mowat 1970.
For tramadol (100mg) versus pethidine (50-100mg) and the outcome
Mother not satisfied with pain relief 1-2h after administration,
Husslein 1987 has a total denominator n=39, implying that one participant has been excluded.
With regard to pooling the data from 7 trials in the comparison of meptazinol versus pethidine, the reviewers say "There was no evidence of significant heterogeneity between these trials". How was this concluded, as no outcome has data presented from all 7 trials? Where it is reported that "there was no convincing evidence of a difference between the two drugs (pentazocine and pethidine) in any of the substantive outcomes considered", it needs to be pointed out that all six eligible trials did not provide data for all outcomes, and it would be helpful to know what these `"substantive outcomes" are.
In the Implications for research, what would be the characteristics of a "well-designed and suitably sized trial", as recommended by the reviewers?
CHARACTERISTICS OF EXCLUDED STUDIES
The study Fairlie 1992 should be moved to the section Studies awaiting assessment?
Comment on the Cochrane review ‘Vitamin A supplementation in VLBW infants’
Comment by Peter C Gotzsche and Jos Kleijnen
Very relevant review and generally well done.
There are many linguistic and typographical errors, e.g. "caretenoids"
"Does the route, dose and timing of supplementation influence the outcome". (question mark lacking)
"Death, neonatal chronic lung disease defined as a) oxygen use at 28 days,
b) oxygen use at 36 weeks corrected age, retinopathy of prematurity, vitamin A concentrations. " (does not make sense, at least two words must be missing)
"Only randomized and quasi-randomised studies" (z or s?)
"data published in abstract form Bental 1990." (brackets lacking)
"The study by Koo 1993) " (bracket lacking)
"The major outcome measure for all studies bar Werkman 1994" (bar?)
"reduction in the incidence death or chronic lung disease"
Unnecessary to write "in the supplemented and control groups" after each outcome.
"blinding of randomization" should be changed to concealment of allocation, to minimise the risk of confusion with blinding of clinicians, parents and assessors.
"data in the study by Rush 1994 are only reported graphically." (this is not a relevant reason to exclude a study)
"All studies analysed plasma vitamin A concentrations at various times but Papagaroufalis 1988 reports no data; Bental 1994, Pearson 1992 and Shenai 1987 only report data as points on a graph, and Werkman 1994 has reported data grouped according to pulmonary status. Hence these outcomes have not been analysed in this version of the review." (again, why exclude these data? The reviewers have not done a meta-analysis of vitamin A levels.
Hence, SD are not necessary, and it makes no sense not to report these data).
Only one study had blinded outcome assessment. This could have biased the decisions whether or not to use oxygen, and the significant effect in the combined outcome reported in the conclusion should therefore be interpreted very cautiously. The lack of blinding is a serious weakness in this sample of studies and it should therefore be noted in the abstract, discussion and in "Implications for research". It does not seem to be a particularly good idea to combine the endpoints death and oxygen requirement and the authors should at least give a motivation for it.
It would be interesting to look at studies with follow-up exceeding 31 days. This deserves a comment in the discussion and potentially in the implications for research.
"Supplementing very low birthweight infants with vitamin A is associated with a reduction in death or oxygen requirement at one month of age" (it should be made explicit, both in the abstract’s conclusion and in implications for practice, where the same wording is used, that a significant reduction was only seen for the combined outcome, not for death or reduction in oxygen requirement separately, which most readers would think when reading this conclusion. The two outcomes should be mentioned separately).
Comment on the Cochrane review ‘Zink and chronic leg ulcers’
Comment by Heather McIntosh and Peter C Gotzsche
The review contains many spelling and grammatical errors. It needs to be copyedited.
CRITERIA FOR CONSIDERING STUDIES FOR THIS REVIEW
Types of outcome measures: Adverse effects are not mentioned, yet they are reported in the Results section.
SEARCH STRATEGY FOR IDENTIFICATION OF STUDIES
The dates of the latest search should be included as well as the sources searched.
DESCRIPTION OF STUDIES
The text is duplicated.
When studies are quoted the full study identifier, including date, should be used.
"The trial in arterial ulcers..."; since this trial has not been mentioned before the description of it should begin: "One trial was in patients with arterial ulcers"
Ten studies were identified. After, "only six were randomised controlled trials", it is redundant to add, "The remaining four were not randomised controlled trials".
METHODOLOGICAL QUALITIES OF INCLUDED STUDIES
The reviewers appear to have scored quality of allocation concealment according to what the trial investigators reported about double blinding. In order to see the quality scores for concealment of allocation the reader has to display `Quality’ in MetaView. The reviewers report that the method of random allocation was not described in any of the included trials. We would, therefore, expect all the trials to score "B" (Unclear) for quality of allocation concealment. However, trials reported as double blind have been scored "A", and the one trial reported as not blinded has been assigned category "D" (which means that a quality score was not used). The Cochrane Handbook Section 6.3, and Schulz KF et al. JAMA 1995; 273(5):408-12 and 274(18):1456-8, explain the difference between allocation concealment and treatment blinding. The guide to using Review Manager software advises on the use of the category "D".
Odds ratios are misleading when event rates are high. The relative risk should be used instead. For example, in the study Hallbrook (1972), 9/13 versus 8/14 for `number healed at 18 weeks’, which intuitively are rather similar rates, is reported by the reviewers as Peto odds ratio 1.95, but the relative risk is only 1.25.
The overall picture tends to get lost in detailed description of results from each individual study. For example: "Haegar (1974) found all but two of the 30 ulcers healed within one year OR 8.73 (0.49, 156.29), the two that did not heal were both in the control group and had a low serum zinc. The two ulcers that failed to heal were both much larger than the average...". Overall, the event rate was 16/16 versus 12/14. The reported Peto odds ratio is 8.73, but the more appropriate relative risk is only 1.40.
The reviewers should do a pooled analysis of the trials in venousulcer, regardless of the fact that the length of follow-up varied between trials. This is permissible, since the results are so consistent across the four trials. The total number of healed ulcers is 33/65 versus 33/76, which corresponds to a relative risk of 1.22 (95% CI 0.88 to 1.68). Over all trials, therefore, there is no evidence of effect.
"There is some evidence to suggest that zinc might promote healing in individuals who have low serum zinc. This needs further evaluation". This statement seems to be unwarranted. The reviewers correctly point out that the study that suggested this (Hallbrook 1972) may be flawed in design, conduct and analysis. Hallbrook found no difference overall (9/13 versus 8/14 ulcers healed), the investigators then did a subgroup analysis, probably post hoc, of patients with low serum zinc which showed 5/7 versus 1/7 ulcers healed. Subgroup analyses must always be interpreted with caution, but they are particularly inappropriate when there is no overall effect. IMPLICATIONS FOR PRACTICE
"There is limited evidence that zinc may be beneficial in the treatment of venous leg ulcers when there is a low serum zinc, but recommendations for the dose and duration of treatment cannot be made on the available information." The reviewers should not accept this implication, which is based only on the study by Hallbrook.
IMPLICATIONS FOR RESEARCH
The reviewers state that "Future trials need to be of an adequate size and duration of follow up". What might an adequate trial size and duration of follow up be, to answer the outstanding clinical questions?
- Editor's Choice Published: 13 October 2001; BMJ 323 doi:10.1136/bmj.323.7317.0
- This Week In The BMJ Published: 13 October 2001; BMJ 323 doi:10.1136/bmj.323.7317.0/b
- Editor's Choice Published: 13 October 2001; BMJ 323 doi:10.1136/bmj.323.7317.0/a
- Editorial Published: 13 October 2001; BMJ 323 doi:10.1136/bmj.323.7317.821
- ResearchCochrane reviews compared with industry supported meta-analyses and other meta-analyses of the same drugs: systematic reviewPublished: 12 October 2006; BMJ 333 doi:10.1136/bmj.38973.444699.0B
- RESEARCHCochrane reviews compared with industry supported meta-analyses and other meta-analyses of the same drugs: systematic reviewPublished: 06 October 2006; BMJ doi:10.1136/bmj.38973.444699.0B
- Letter Published: 02 March 2002; BMJ 324 doi:10.1136/bmj.324.7336.545/a
- Research Methods & ReportingThe PRISMA statement for reporting systematic reviews and meta-analyses of studies that evaluate healthcare interventions: explanation and elaborationPublished: 21 July 2009; BMJ 339 doi:10.1136/bmj.b2700
- Feature Published: 03 January 2019; BMJ 364 doi:10.1136/bmj.k5302
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- Has Cochrane lost its way?
- Published review of closed-system drug-transfer devices: Limitations and implications
- Characteristics of the Cochrane Oral Health Group Systematic Reviews
- The PRISMA statement for reporting systematic reviews and meta-analyses of studies that evaluate healthcare interventions: explanation and elaboration
- Cochrane reviews compared with industry supported meta-analyses and other meta-analyses of the same drugs: systematic review
- Evaluating the effectiveness of public health interventions: the role and activities of the Cochrane Collaboration.
- SOCRATES 3 (synopsis of Cochrane reviews applicable to emergency services)
- Quality of Cochrane reviews
- Article from Clinical Evidence
- Cochrane Reviews: Good, but Could Be Better