First off, I would have expected the authors to have made some comments about this imbalance somewhere in the paper. Secondly, the imbalance itself should have little impact on power with such a large sample size. From your Chi-squared test, there is a 4 percent chance that the imbalance is random - which is entirely feasible. I would therefore simply query it with the authors.

There is generally an increase in power as one increases the size of a study even if the groups are asymmetric in size.  This is usually an issue in design of matched case-control studies where sometimes the number of cases is limited but there are lots of potential controls.  The increase in power is not as large with asymmetric groups (say 2:1 or 3:1 matches of controls per case) as if one could have the same total number in the study but in equal size groups.  As I recall, since the power increase levels off, there is little advantage to having more than a 4:1 match.  I assume that the situation is similar with an intervention study in which one might have intended to end up with equal groups but by chance ended up with the situation you describe - i.e., having more people is better; and there is more power to the study than if both groups had had only 145 persons.  

Thank you both for you very sensible answers. My feeling was that it wasn't a major concern, but a comment or explanation by the author would be appropriate. I can pass that on.

Thanks again!

I guess the author may have presented a sample size calculation based on planned primary end point. This could allow to evaluate the theoretical statistical power based on the smallest of the two study groups. Anyway this could be irrelevant if the results are statistically significant as the power express the probability to find a statistically significant result and not the validity of the significance once it has been found.

The mild imbalance per sè has a minimal influence on the power itself if one consider that a 2:1 randomization decrease statistical power by only 5%.

One possible important point is that such imbalance in the two groupd may reflect either a non balanced randomization (e.g by block of 4) and/or a selection bias leading to more exclusions in one group vs the other. This may be reflected in baseline demographics differencies or more details about patients screened but not rendomized may be informative.

Another possibility I guess is that if the study was not double-blinded there may have been a selection bias for one of the two treatments.

In the end the imbalance should not have a major impact on the results unless it is a result of a methodological bias in treatment allocation..

Thank you- you raise a good point about exclusions and baseline dempgraphics. The author did demonstrate group comparability for all relevant demographic and prognostic factors- which was why I was reassured that the different group sizes were a minor issue.

Hopefully it is random fluctuation due to whatever was the author(s)' method of allocating to conditions. Did they explicitly state how randomisation was carried out? (That's one of the things you could evaluate according to jadad criteria). Presumably they also commented about what effect size they hoped for or would be meaningful. IF so, you could put the figures into a programme such as G*power and see how well powered was their study.

Although David Schmidt has told us at the outset the degree to which the size imbalance is significant and later added that several characteristics of the unequal groups were similar despite the imbalance, I do not believe we know if the study has been completed and if it has been completed whether the results were statistically significant.  So, some of us are speculating about the power of the study to show a difference and others are not.  One respondent assumed that the study has been completed and the results are statistically significant.  This may be the case - or not.  Dr. Schmidt can you clear up this point?  Thanks.

Thank you Stephen- to clarify:

The study is indeed complete and found significant results. Apologies for not stating this earlier.

In terms of the pwer of the study- the authors provided detailed notes on their sample sizes calculations, which they completed using G*Power. The author reports that a sample size of 274 would provide 90% power assuming an alpha of 0.05 and a correlation coefficient of 0.8 for measures taken within each individual. They ended up recruiting an additional 54 patients to allow for a 20% buffer for withdrawal of patients who be come ineligible, thus arriving at the total sample size of 328 patients.

So the power of the study was ample.

I just wish all the papers I review were of the same quality!

@ Esterman, a 4% chance to get such an imbalance by chance is not zero, yet it also is not 'huge'. If we stringently work with an acceptable error of 5% (Type I = alpha = p), we also should take such a 'small' chance seriously (why to reject a result if the uncertainty is larger then 5%, but discuss to accept an allocation imbalance by chance smaller then 5%?). 

I assume the authors calculated their a priori power analysis with a 1:1 allocation model, else the discussion has to change focus. 

@ Sardina, your answer corresponds best to my thoughts while reading the question. Together with the information that the study found significant results, the only concern I am really worried about is the question whether or not there was selection- or exclusion-bias between randomisation and definitive inclusion, or pure fraud.

Assuming the study is one out of the field of medicine, the authors should have submitted it to a clinical trial database (else reject it without further comment). If they did submit it to www.clinicaltrials.gov, you have the possibility to use the 'archive' link. Screen it, and read what they declared at the beginning, at the time when enrolment started (the firm date when nothing should be changed in the study design anymore, and the design should be declared answering ALL 20 topics – see http://www.icmje.org), or at the end of the study (also amazing what additional information is provided once the data has been harvested) Sometimes it is amazing or even alarming what study designers/authors change during an ongoing study. For 'fun', two years ago I checked this source to analyse all original articles published in the NEJM during the first halve year of 2012. One study even changed the primary endpoint in the midst of the enrolment phase...

Thanks Bruno. I have actually been in contact with the authors and they were happy to share their original randomisation data with me and I have been through it- there is certainly no fraud! However it does point to the value in perhaps using a large-block randomisation (e.g. groups of 100) where this kind of imbalance is likely to be evened out, rather than randomising all 328 in one go.

In this study their was blinded allocation via means of sealed envelopes which were opened by clinical staff (not the researchers).

I do want to pick up a point you raised around the original power calculations and the assumption of a 1:1 allocation model. The power calcs called for 274, which would lead to equal group sizes of 137. The group sizes as allocated were 145 and 183. How does that affect the power calculation? Surely they have met and exceeded the group sizes for the 90% power they were after?

Yes, they have.

Dear David, stringently, to use group sizes larger then power calculation bears the fraud to 'test' more patients then needed to fix the study. Basically, you have more patients 'at risk', being it in the treatment arm or the placebo one then needed. The patients in the less favourable arm are at 'risk' (money, ineffective treatment, adverse events) needlessly. Yet, the power itself doesn't suffer. 

While we have type I error (p) that defines significance, and  type II error that defines MINIMAL power, a type III error is not established. As I have an interest in math, I am working on a model defining such an error, let's call it type III, that defines an upper limit in numbers where numbers and effect, even significant efects, becomes useless due to missing clinical relevance. The crucial number to say 'skip the study' will be around n = 1'000 or more, therefore your study won't be affected.

Back to the topic, using sealed envelopes is out-dated. A friend of mine told me confidentially, that they could assume the allocation by holding the envelop against the sun. As their study was conduced during soccer world championship, the true randomisation was soccer: no soccer = treatment, soccer = shame procedure... Yet, if you have group sizes 100-200, what would block-randomisation in packages of 100 change? It would even it out because every package would be 'forced' to be 50:50. Yet if the base-line characteristics are even, as Dr Sardine said, the imbalance is neglect-able in concern of the studies findings, yet in the case under discussion it can be considered 'over-treatment' as fewer patients would have been enough to answer the question.