Forum:How to improve a bioinformatics study and paper so that it is not considered "too preliminary" by publishers and journals?
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10 weeks ago
egascon ▴ 60

Hello to all,

I am writing to ask for your opinion.

I have done a study between sick and healthy people from a GEO microarray dataset. I have done a DEG analysis, GO analysis, KEGG, PIP, Hub genes and miRNAs related. In short, I have tried to do a very comprehensive transcriptomics study using bioinformatics techniques. I have presented all this in a paper.

But I was told by one of the publishers:

"Your manuscript has been reviewed by our editorial team. We feel that the overall content appears to be rather preliminary, which gives your manuscript a relatively low priority for publication".

Which leads me to think: How can I improve such studies to make them more complete? I specialise in bioinformatics and not in laboratory experimentation. Any advice?

Thank you for your help.

DEG journal • 1.1k views
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It is just an opinion about your work, and apparently without commissioning the reviews. I have read the dreaded words It is not clear in many reviews, enough so to learn that it only sometimes means something is wrong with my work. Instead, it often means that reviewers are not excited about the work, and the easiest way to express that lack of enthusiasm is to say that it isn't clear on its motivation, execution, or interpretation. Then I re-submit to a different journal or a different agency and get strong reviews.

Even though I am an experimental biologist, you will not hear it from me that you need to add wet-lab experiments to your work. Of course it wouldn't hurt if you did, but people publish purely bioinformatics papers all the time. I think you need to make your presentation of results more exciting. That could mean: 1) highlighting your main finding; 2) finding a better selling point; 3) and yes, adding experiments.

My general advice is not to overthink the generic and unhelpful feedback such as the one you received, and certainly not to be brought down by it. Repackage the product and try again.

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By doing the laboratory work.

Bioinformatics as the name implies is about understanding biology.

Computational methods we use are predictions about the system we're working on.

You have to show your predictions are what you say they're in vitro or in vivo.

If you're not experienced with the lab work try finding collaborators who have the labs and infrastructure.

I suggest that you don't restrict yourself to only data analysis and learn wet lab and biology.

Knowing the biology of what you're studying and how these data are generated would give you a better understanding and insight into your analyses and results.

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Hard disagree.

I don't need to do a clinical trial or get preclinical patient-derived xenograft models for the GWAS+eQTL study that took me years to complete.

A lot of novel biology can be discovered and validated from computational methods performed on the wealth of existing datasets out there. The "laboratory work" has already been done; it has generated those datasets.

Computational analysis of data is not "predictions". In my sequencing reads, if I reliably see a transcript being detected; that's not a prediction. That's my data.

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I agree with this comment. To generate such data, a previous experiment has already been done. Perhaps it could be reinforced with a quantitative analysis such as qPCR. But I think also, as colleagues say, if we want to highlight a "finding x" and we can validate it with other databases (generated from other experiments) in a coherent way, that is no reason not to consider it a complete study. Right?

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Validation is always good, but it's typically a supplementary figure to support the finding. It does not really add to the story other than showing that it's robust. The critical part is to work out what the differential genes mean in terms of explaining the phenotype.

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Hi everyone!

Thank you for all comments. You have helped me a lot and broadened my perspective. I am currently starting my thesis and I am learning something new every day, so all your suggestions and experience are welcome. I have noted down all your tips to apply them.

The disease of the study is Alzheimer's disease. My group specialises in ALS and AD.

It's a funny thing about magazines because I've had one publisher really like the type of study and others consider it to be preliminary. That makes me doubt, if some of them are only looking to publish massively, maybe they are not as interested in the quality of the study as others. It's a bit subjective and we depend on luck, isn't it?

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10 weeks ago

A few comments seem to advocate an unrealistic path - one can't just "learn and do labwork". We don't know the OPs background and access to experimental platforms - many people have no access to such infrastructure.

And, of course, numerous computational-only approaches are published every day. It is a widely acceptable approach.

However, if someone pursues a solely computational approach, the bar is higher, and the results that they present need to be more informative than if they also generate new and original data.

When an editor says that some results are too "preliminary," they most likely mean that the results seem to be one or more of the following:

  • derivative, simplistic, appear incorrect, insufficiently informative, speculative, lack novelty, naive, etc.

So, work on addressing this type of criticism.

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10 weeks ago
dsull ★ 6.9k

Comprehensiveness is an important aspect, but it alone is likely not what's going to get you into the journal. What you are describing is an example of a "descriptive" study -- you're just analyzing the crap out of datasets (a single dataset/cohort in this case).

Do you have any real biological conclusions?

You are looking at genes that change between sick and healthy people. I'll get bored if you just shove a bunch of GO terms+networks in my face. Cancer tissue upregulating cell proliferation pathways (duh!) isn't interesting to me. It's no better than the dozens of retrospective medical studies that do the: Hypertension ~ Increased odds of adverse outcomes after surgery (p < 0.05).

What I'd find interesting is something like: You can use those genes on external cohorts and find that you can classify healthy vs. sick with extremely high accuracy and the expression levels of those genes actually have very high prognostic value, but this only happens in disease subtype 1 but never in disease subtypes 2 or 3. Your findings should be useful to me in some way.

Exploratory data analysis is 100% ok but you have to find some sort of recurring pattern that is interesting. More external data is always helpful (I worked in cancer and I've had to dig into TCGA, CCLE, DepMap, other GEO data, etc. in order to get papers published; and that's WHEN I HAD experimental evidence).

Take a look at this study (not mine, but my classmates) in a high-impact cancer journal: https://www.cell.com/cancer-cell/fulltext/S1535-6108(19)30296-X -- it's all computational analysis of public datasets but it's easy to see why this study is interesting.

I know I'm probably echoing what a lot of others are saying and I'm probably just rambling, but I hope you find my rambling helpful in some way!

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I think this, and Istavan's answer are probably closest to the truth. My guess is you could significantly improve the impact of your publication by narrowing the scope to a specific biological hypothesis, and framing it as a bioinformatic approach to testing that hypothesis. For a re-analysis study, this is key. Because you haven't told us anything about the underlying disease, it's hard to give specific suggestions, but you can take on hypotheses about specific cell types, gene families, or transcription factors.

Without that kind of framing, your results are indeed "preliminary" - it is up to the reader to look through the top gene tables and enrichments to figure out what the take-away is.

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10 weeks ago

All (good) journal judge work on its scientific correctness. Does the data presented conclusively support the claims made.

Some journals will also judge work on its impact. How novel are the conclusions drawn, and now exciting are they if they are novel.

You havn't told us the conclusions you draw from your analysis, only which analyses you have done, so I'm going to go out on a limb here, and assume that you didn't pitch your paper as having one single stand-out finding that contributes to the answer some important open question in your field, nor raise important new questions.

So you have two options:

  1. Rework your manuscript so that it is asking or answering a single focused important question in the field of your disease. It can be hard to conclusively answer questions using bioinformatics alone. Noteably techniques such as geneset/pathway analysis are generally hypothesis generating, rather than hypothesis testing approaches. It is not, however, impossible, and there are plenty of good papers out there that answer hypotheses using bioinformatic analysis of functional genomics data.
  2. Pitch your papers as a descriptive paper - you have done a compreshensive analysis of many datasets, and the results of those analyses may be useful to others studying the field. This will mean pitching your paper at a journal that judges papers on their scientific correctness, rather than their impact. Examples of such journals are PLoS One, F1000 Research, PeerJ and Biology Open.
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10 weeks ago

Unfortunately, the scientific community is also not immune to hypes and buzzwords. About 10 years ago, enhancers and cis-regulatory elements were the talk of the town, so many transcriptomic studies were published that looked at those particularly. Then it was all about alternative splicing and long non-coding RNAs and polymerase pausing etc. After that, everyone tried to include some, often far-fetched, relevance to SARS-Cov-2 in their papers and in recent years, of course, anything with AI, whether for classification/detection/segmentation etc., is sexy.

A reanalysis of published microarray data per se is not really intriguing for editors in terms of methodology - it is basically a 20-year-old technology. NGS-based results overshadow microarrays nowadays, unless you really need large sample numbers, also because the selection of probes already limits what you will be able to find.

If you have not generated the data yourself, you are also not the first to analyze it. So either your scope and hypothesis must be significantly different from the existing published results or your bioinformatic methodology must be novel. Without knowing any details about your manuscript, it to me does seem that you applied mostly existing methods. This probably makes the editors doubt that your study is sufficiently informative for the readers to be of interest.

Of utmost importance are of course the conclusions that you reached. If you discovered a truly novel disease mechanism, that may be really exciting, but would presumably need underpinning by wet lab experiments to get accepted. If you confirm existing knowledge and find those pathways enriched that are already known to be implicated in that disease, your study lacks novelty.

So start with the question: "What is the exciting finding that I do want to tell the other researchers about?" and then start rewriting your manuscript in a way that everything that underpins that finding is nicely presented, but also point out, where further research is needed. Add additional datasets to explore your finding further, e.g. in related diseases. Discuss how that finding adds to the existing knowledge and whether it is something that is potentially "druggable" and could help with treatment in the future. But also if it simplifies diagnosis or the management of the disease, it could already represent a significant contribution worth a publication. Good luck!

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10 weeks ago
John ▴ 10

I understand how disappointing it must be to have your paper given such a comment. Based on the feedback from the editor, it might be beneficial to consider submitting your paper to a journal with a slightly lower impact factor. This can often increase the likelihood of acceptance and still provide valuable visibility for your work.

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