What Makes a Research Paper Publishable?

[dimensionless]

What exactly is the criteria for a research paper to get published? It seems that few papers contain major breakthroughs like the cloning of a sheep. A lot of papers seem to be contain incomplete ideas, and a lot of times papers seem to discuss ideas that were developed by someone other than the author.

Do people just get published by being super nerdy? I get the impression that original ideas are both unnecessary and by themselves insufficient.

 

[guguma]

you are absolutely right my friend,

Actually science would not progress if everyone just tried to make breakthroughs, but nowadays there is a certain paper publishing madness, physicists are credited according to their citation and paper quantity criteria, rather than original ideas and breakthroughs.

As I always say, publishing papers means money, and physics is being industrialized physicists being walking computer algebra programs and constantly and blindly calculating. Someone publishes a paper, another person makes a first order something expansion to their result and they publish it another one makes a second order correction... goes on like that, or like the Monte Carlo madness going on, "Dude who needs experiment, I just Monte Carlo it and it is true"

I am sure that there are physicists out there just doing physics as an academic endeavor and not participating in this madness. One I know of is Lee Smolin. Also I always had this strong feeling that the people at the theoretical particle physics department in Boston University (including Sheldon Glashow) have similar inclinations.

Nowadays physicists do not want to be like Einstein, or Feynmann, or Dirac. Whom I have a great respect for their character and their approach to physics. They want to be like Van Paradijs or Brian Greene. I find it sad, but it is true.

 

[Choppy]

This is an interesting question.

In general, the reviewers are asked to ensure that what's presented in a paper is original, unpublished work. This does not mean that everything in the the paper needs to be an original idea, or that the authors need to be presenting a cure for cancer.

What I look for when I review a paper is that the work has scientific merit that will neccessarily be of interest to the journal's audience. That means that it must contain some original information or ideas, those must be clearly explained, and any conclusions must be correctly derived and presented. It also means that the work must hold some value with respect to the discipline in which the journal reports. "Value" has a pretty subjective definition, but that's why we submit to the process of peer review. In order for a paper to be accepted, mulitple independent referees and an associate editor (and ultimately the journal's chief editor) must concur that such value is sufficient.

Science, for the most part, is not a process of leaps and bounds. It's an incremental process that builds on the ideas of others.

 

[Asphodel]

What's required to be a published novelist? Well, first you write a good story...

Research papers are a consequence of doing research. The point is to share your results with the wider community, so first you need to do some research. As to what's appropriate, it can be just about anything that would be interesting or useful to others.

 

[turbo]

Having recently gone through this process, may I offer some insights? First off, your research project should have a well-defined and easily identified goal, even if that goal is to clarify or constrain prior research. The research and data reduction must be consistent and well-motivated with selection criteria that are designed to produce a data-set that is as objective as possible. Then, the data-set must be evaluated with a keen eye to potential contamination, and the results should be presented with error-bars or (at a minimum) disclaimers regarding the possible sources of error in your evaluation.

If you don't do these things, expect a lot of friction with referees, unless you have some heavy hitters on board as co-authors. Sometimes, relatively innocuous papers can lead to some pretty significant findings, so please read papers carefully and try to consider the impact of the findings. Papers that seem to be incremental career-extending output may lead to some pretty hot stuff.

 

[ZapperZ]

Some of the comments here are quite off-topic as delving into the "motivation" for publishing. That really isn't want the OP is asking, so please restrict your response to what is being asked.

Since I am a referee for several journals, I think I can give a first hand opinion on what I think is "publishable".

1. It depends very much on the journal's criteria. Journals such as Science, Nature, and Phys. Rev. Lett. have quite a high criteria for acceptance. Science and Nature require that the paper not only be important in that particular field of study, but also be of interest to someone in another field of study. You can look for yourself at the criteria set up by these journals at their webpages. Phys. Rev. Lett. also requires that, but tends to be more forgiving if the paper has a very narrow target, but still of high degree of importance.

2. What all 3 journals look for are either results, discoveries, or ideas that new, revolutionary, unexpected, or results that add significantly to the body of knowledge. These journals will typically send the submitted manuscript to at least 3 different referees, and they all must agree that it is publishable before it is accepted. The referees are also reminded of the journal's criteria for acceptance, so one can already see why it is usually quite difficult to get published in those prestigious journals since the level of scrutiny is quite high.

3. There are other journals that may not require as tough of a scrutiny, but it varies from journal to journal and also field to field. That is why if one has a new result and one doesn't think that it is THAT Earth'shattering but still could be useful to some people, one will tend to look for a lower-tier journals. It doesn't mean that the quality isn't good, it just means that the level of impact and importance may not be as high as those required by Nature, Science, and PRL. I can give you a concrete example here. Papers that come out of, say, the field of Accelerator Physics tends to not have the same high degree of impact. So you seldom see such papers published in those journals, mainly because it is a smaller field of study than many other areas in physics. You do get to see some getting their just publication and publicity in major journals (see Science's coverage of the "Dream Beam" from a few years ago), but most of the time, many of the accelerator and beam physics article appears in either PRST-AB, Nucl. Inst. Method, or J. Appl. Phys. The results being published here are still important, but they don't have the same "impact" and wide-coverage as that required by those top 3 journals.

4. One of the surest way of not getting accepted is to present a confusing paper AND to ignore relevant citation. If you claim something, and it is contradictory to a previously published paper, you MUST address the contradiction. Are you claiming you are right and the other is wrong, or is there another way to explain the discrepancy. Science works this way by evaluating things that appear to contradict each other, and that is how we sort things out over time to figure out which one is valid and which isn't. Contrary to popular belief, we disagree with each other all the time on research front issues, because the picture of what truly is a valid idea is still cloudy. That's why we publish our work so that others in the community can evaluate, study, scrutinize etc. This is the only way to add to our understanding of something, and eventually the true picture emerges. It always does.

I've written more about this in Chap 13 of "http://www.chicagotribune.com/news/local/chicago/chi-fermilab-code-both-11jul11,0,1755934.story" ".

Zz.

 

[Asphodel]

Re: 4, sometimes you will see sequences of papers that go back and forth for years to the effect of:

A: "Hey look, something cool!"
B: "Nope, I can't get it to do that. Are you sure your results are valid?"
A: "Of course I'm sure, you're doing it wrong."
B: "Nope, still can't get it."

Et cetera. It's kind of weird to watch, but often enough the end result is that the methodology is refined to the point that other labs can replicate the results and everything moves forward a bit. And there are plenty of papers that largely confirm another paper's results...one of the principles is that you need this sort of confirmation, and articles form the written history and show the connections and ancestry of a theory or result.Preprints seem to be an interesting factor these days, but I'm not sure I understand the intricacies of that well enough to be the one explaining it. Anyone?

 

[ZapperZ]

Re: 4, sometimes you will see sequences of papers that go back and forth for years to the effect of:

A: "Hey look, something cool!"
B: "Nope, I can't get it to do that. Are you sure your results are valid?"
A: "Of course I'm sure, you're doing it wrong."
B: "Nope, still can't get it."

Et cetera. It's kind of weird to watch, but often enough the end result is that the methodology is refined to the point that other labs can replicate the results and everything moves forward a bit. And there are plenty of papers that largely confirm another paper's results...one of the principles is that you need this sort of confirmation, and articles form the written history and show the connections and ancestry of a theory or result.

There's a very clear example of that that I know of rather well - the battle between the spin fluctuation picture versus the phonon picture as the bosonic mode coupling in high-Tc superconductors. Each side keeps coming up with new results that seem to be supporting their argument.

Zz.

 

[Andy Resnick]

I'd like to add a small detail to ZapperZ's excellent post: the selection of what Journal to submit to. Personally, I didn't appreciate this until recently.

Often, how a paper is reviewed depends not only on the quality of the referee, but also what the journal thinks is interesting. Just to pick a topic at random, let's say you did an experiment to address the high-Tc superconductor debate.

It is highly unlikely that Science, PNAS, Phys Rev Lett, etc. will be interested- the subject matter is too specific. Furthermore, unless the Journal you submit to specifically caters to some aspect of your paper, they are not likely to want it, either- regardless of whether or not the paper is 'correct'.

What I've written may not make sense, but that's because there are not too many high-quality Physics journals, so choosing which one to submit to is fairly obvious. Less so obvious is the biomedical field, where the number of high-quality journals is immense. Finally, consider multi-disiplinary research: research that cuts across Departments will produce papers that don't fall into a simple category, meaning that Journals willing to publish the paper, and editors that can locate referees that are capable of producing a useful review are difficult to find. Choosing which Journal to submit to can be the difference between a yawn and excitement.

I often review papers that aren't wrong, but aren't particularly interesting either. My goal as a reviewer, then, is to suggest additional work to bring the paper up to a level that will make it relevant to more people.

 

[Andy Resnick]

What exactly is the criteria for a research paper to get published? It seems that few papers contain major breakthroughs like the cloning of a sheep. A lot of papers seem to be contain incomplete ideas, and a lot of times papers seem to discuss ideas that were developed by someone other than the author.

Do people just get published by being super nerdy? I get the impression that original ideas are both unnecessary and by themselves insufficient.

Just to second what ZapperZ has written, every single Journal has, on its website, what criteria it requires to be considered for publication. The criteria vary greatly from Journal to Journal, but the criteria are all spelled out in detail.

 

[G01]

All of us undergrads in my lab group are encouraged to be a part of the lab journal club, and after reading a good number of articles, I have a question on publications as well. Maybe, Zz, or another member will know the answer.

I have noticed that their are articles published in Nature and then other articles that are published in Nature- Physics. Is their a change in criteria for Nature- Physics? For instance, does the material not have to be as wide reaching to be published in Nature- Physics, as opposed to Nature? Or is there no real difference?

 

[Abraham]

I have a related question: What makes a master's thesis a thesis? And what makes a PhD dissertation a dissertation and not just a thesis? Simply more material written or more research than a paper?

 

[Andy Resnick]

All of us undergrads in my lab group are encouraged to be a part of the lab journal club, and after reading a good number of articles, I have a question on publications as well. Maybe, Zz, or another member will know the answer.

I have noticed that their are articles published in Nature and then other articles that are published in Nature- Physics. Is their a change in criteria for Nature- Physics? For instance, does the material not have to be as wide reaching to be published in Nature- Physics, as opposed to Nature? Or is there no real difference?

I'm a cynic, so my answer is that Nature is cashing in on their reputation by spinning off a whole bunch of 'related' journals: Nature Methods, Nature Physics, etc. as part of the "Nature Publishing Group". It can be spun a variety of ways, but the bottom line is that Journals are a way for some publishers to acquire and maintain a revenue stream, and by branching out or franchising their brand, publishers attempt to increase their revenues.

 

[Andy Resnick]

I have a related question: What makes a master's thesis a thesis? And what makes a PhD dissertation a dissertation and not just a thesis? Simply more material written or more research than a paper?

This is a discussion you need to have with your department chair or academic advisor. Every department has different requirements.

 

[Abraham]

This is a discussion you need to have with your department chair or academic advisor. Every department has different requirements.

Sorry, I'm still in high school.

 

[will.c]

Nowadays physicists do not want to be like Einstein, or Feynmann, or Dirac. Whom I have a great respect for their character and their approach to physics. They want to be like Van Paradijs or Brian Greene. I find it sad, but it is true.

This isn't fair. In the heyday of Einstein, Feynman, and Dirac... there were also thousands of other scientists who weren't Einstein, Feynman, or Dirac. Everyone wants to make a major breakthrough, but quite frankly being a genius and working hard isn't enough. Those things are necessary, of course, but you also have to be a little bit lucky. It's naive to think that you can choose to work only on projects of profound, fundamental importance, and likely to lead to a breakthrough. Also, as others have said, sometimes it's a little tiny bit of new knowledge that sets a certain research direction ablaze. It's not that physicists have no desire to be like the greats, but we do desire to be employable so that we can do our research. Sorry.

 

[guguma]

Nowadays physicists do not want to be like Einstein, or Feynmann, or Dirac. Whom I have a great respect for their character and their approach to physics. They want to be like Van Paradijs or Brian Greene. I find it sad, but it is true.

This isn't fair. In the heyday of Einstein, Feynman, and Dirac... there were also thousands of other scientists who weren't Einstein, Feynman, or Dirac. Everyone wants to make a major breakthrough, but quite frankly being a genius and working hard isn't enough. Those things are necessary, of course, but you also have to be a little bit lucky. It's naive to think that you can choose to work only on projects of profound, fundamental importance, and likely to lead to a breakthrough. Also, as others have said, sometimes it's a little tiny bit of new knowledge that sets a certain research direction ablaze. It's not that physicists have no desire to be like the greats, but we do desire to be employable so that we can do our research. Sorry.

I always make people misunderstand me, by not being able to state what I mean in the most clear way possible. I am sorry about that and it is totally my fault I accept it. Maybe though it is because my native language is not English.

will.c I agree with you on your point. But what I meant was not the thing you understood.

I did not blame anybody for not wanting to make a major breakthrough, you work on what is desirable, and you make your research on what draws your attention. Actually this is how it should be.

I also said that in my original post "Actually science would not progress if everyone just tried to make breakthroughs" and I am aware that tiny little bits of knowledge leads to breakthroughs, otherwise some genius would come along and explain everything and it would be over.

What I am actually ranting about is the circumstances that does not let people peacefully work on what they desire. You should agree with me that there is a certain paper publishing madness going on. What I advocate is that you do not need to publish a paper to make a discovery or an idea come to light, the act of publishing should not be the central aim in natural sciences it should be the intellectual curiosity. Whether you progress very slowly, or extremely fast, whether you are a genius or not.

But according to what you have stated and what other people says here makes it clear that it does not work that way. Whatever you see or think or work out you have to present it in a "publishable" way as in ZapperZ's critera, and you MUST do that to survive. If you did work on something and think that it did reach a nice conclusion then of course you will want to publish it, and present it in the most formal way, that is fine and it should be. But you are not given the choice to put your work aside, or present your work in an incomplete way because than you would not be publishing and you would not be surviving.

I do not think that this paper publishing madness speeds up or eases the progress of science, on the contrary it clogs it, everything gets unnecessarily fancy. It kills the simplistic beauty of the scientific method,

from this

1.Curious about something? 2.-> Read on it, tinker with it, think on it 3.-> Does your tinkering and thinking confirm each other 4(yes).-> great you learned something and share it with everybody including the joy of your work

or

4(no) -> return to step 2 -> always getting 4(no) and bored -> return to step 1

to this

1.Curious about something? 2.-> Read on it, tinker with it, think on it 3.-> Will it lead to a publishable paper 4(yes).-> great you learned something and share it with everybody including the joy of your work but most importantly you published it

or

4(no).-> forget about it return to step 1 -> getting 4(no) all the time-> forget about step 1 and find something that you may publish ->...-> 4(yes) -> great you published something.

It is the way I see it. If anybody thinks that I am extremely wrong, please tell me on which points I am wrong at, and I am extremely sincere about that, I like discussing, my tone may seem harsh but that is really because of my English knowledge, I cannot form wonderful sentences, and I am always open to reasonable explanations and I accept them regularly. I would much prefer to abandon this thought rather than live through my academic career with the stress this thought gives to me.

Thanks

 

[tmc]

The entire purpose of publications in science is that, once you have discovered something, you publish it. A paper is publishable if other people will gain something from it. Publishing everything that you do ensures that other people won't be wasting time redoing your work.

If everyone always published everything they did (including less-than-complete work on something like Arxiv), then research would probably work better, as it would bring a much larger collaboration among people.

Without a publishing frenzy, you might have 100 people working toward the same problem, each separately. With this frenzy, you suddenly have these 100 people working together toward this problem, improving the chances that it will be solved.

Of course, this has to include partial-publishing in Arxiv; journals are much too slow and require work that is much too polished to bring in such collaboration. However, the rush to publish-publish-publish nowadays tends to include Arxiv as a very valid place to publish: the whole reason universities want you to publish is that it can be used to see how much work you've been doing. It doesn't really matter where it's published (this is an obvious overstatement, but you get my point), as long as they can count it.

 

[Choppy]

I have a related question: What makes a master's thesis a thesis? And what makes a PhD dissertation a dissertation and not just a thesis? Simply more material written or more research than a paper?

Generally speaking, "thesis" and "dissertation" are interchangable terms, although different schools may apply specific, technical definitions to each. For the M.Sc. the candidate needs to demonstrate competance in performing research in a given field. For a Ph.D. the candidate is expected to demonstrate the ability to conduct independent research in a chosen field. Again specifics will vary from school to school, but the Ph.D. should generally be more involved and more about the student properly exporing his or her own own ideas, whereas at the M.Sc. level you can have a little more guidance.

 

[guguma]

The entire purpose of publications in science is that, once you have discovered something, you publish it. A paper is publishable if other people will gain something from it. Publishing everything that you do ensures that other people won't be wasting time redoing your work.

If everyone always published everything they did (including less-than-complete work on something like Arxiv), then research would probably work better, as it would bring a much larger collaboration among people.

Without a publishing frenzy, you might have 100 people working toward the same problem, each separately. With this frenzy, you suddenly have these 100 people working together toward this problem, improving the chances that it will be solved.

Of course, this has to include partial-publishing in Arxiv; journals are much too slow and require work that is much too polished to bring in such collaboration. However, the rush to publish-publish-publish nowadays tends to include Arxiv as a very valid place to publish

I totally agree with this.

the whole reason universities want you to publish is that it can be used to see how much work you've been doing. It doesn't really matter where it's published (this is an obvious overstatement, but you get my point), as long as they can count it.

If universities really give you credit over your incomplete work, then it is fine. But it is still an ugly method of proving that you are working. The university is the department, and the people in the department do know with a certain extend on what their coworkers work on and how much they work. I think that all this crediting thing could be done in a more humane manner.

 

[mathwonk]

a word of advice. since universities do measure activity by publications, it is important not to censure too much your own papers. a paper is publishable precisely if it is accepted by a journal. hence nothing said here should be interpreted as a reason not to submit your work in most cases. when in doubt, submit it and let the journal decide if it is publishable. i.e. if you are a working scientist and hope to survive, basically everything you do should be published somewhere. this is also a service to your fellow scientists as has been said. hopefully if it is not published the referee will tell you how to raise it to publishable standards, or where else to submit it. i have had referees simultaneously turn down my paper for one journal but accept it for another.

 

[mathwonk]

to keep it simple, a paper can be published if it has 2 qualities:

1) it contains information of interest or importance to other people;
2) it is written well enough that those people can have access to that information.

in fact if even one of the two criteria is very exceptionally met, it can compensate partly for the other.

 

[Andy Resnick]

I always make people misunderstand me, by not being able to state what I mean in the most clear way possible. I am sorry about that and it is totally my fault I accept it. Maybe though it is because my native language is not English.

<snip>

What I am actually ranting about is the circumstances that does not let people peacefully work on what they desire. You should agree with me that there is a certain paper publishing madness going on. What I advocate is that you do not need to publish a paper to make a discovery or an idea come to light, the act of publishing should not be the central aim in natural sciences it should be the intellectual curiosity. Whether you progress very slowly, or extremely fast, whether you are a genius or not.

<snip>

I do not think that this paper publishing madness speeds up or eases the progress of science, on the contrary it clogs it, everything gets unnecessarily fancy. It kills the simplistic beauty of the scientific method,

from this

1.Curious about something? 2.-> Read on it, tinker with it, think on it 3.-> Does your tinkering and thinking confirm each other 4(yes).-> great you learned something and share it with everybody including the joy of your work

<snip>
It is the way I see it. If anybody thinks that I am extremely wrong, please tell me on which points I am wrong at, and I am extremely sincere about that, I like discussing, my tone may seem harsh but that is really because of my English knowledge, I cannot form wonderful sentences, and I am always open to reasonable explanations and I accept them regularly. I would much prefer to abandon this thought rather than live through my academic career with the stress this thought gives to me.

Thanks

The way you describe science is indeed the way it was practiced up until about 60 years ago. In fact, extensive reliance on peer-review only came into existence in the 1980s. However, that is the past. One may look back for fun and nostalgia, but one must always face forward.

Publishing papers (and obtaining grant funding) has become a more important part of the tenure-track process for the simple reason that administrators require an objective metric in order to evaluate a candidate. That science has exploded means that no-one can possibly be considered an expert in more than a vanishingly small number of topics, and so for me to evaluate you when you apply for a position or tenure means I need some way to tell if your research is indeed top-quality. I can read your papers, but I won't understand them since I am not an expert. So, what options do I have at my disposal?

Having a paper accepted for publication means that someone else thinks your work is worthwhile. Having obtained external funding for your research means someone is willing to give you money. Both imply that your research is worthwhile. A track history of papers published in top-quality Journals, with you as senior author, in addition to consistently obtaining funding means that you are productive. Again, how can you convince me that I should give you a job? Because you are a nice person, and are generally liked by others? I've heard that the cost to an institution for a full-time tenure track faculty member doing experimental biomedical research is >$600k per year. You had better be REALLY liked by others.

It's easy to complain that the system is not a meritocracy, that the key to getting papers published is suggesting the correct reviewers, or that getting funded means "the right people" review and actively lobby your application, and I won't deny that there is truth to that. However, no-one has yet to suggest a better alternative. The bottom line is that you should feel free to pursue whatever captures your fancy, but don't demand that others pay for you to sit around and think all day.

 

[guguma]

This is the problem:

Publishing papers (and obtaining grant funding) has become a more important part of the tenure-track process for the simple reason that administrators require an objective metric in order to evaluate a candidate. That science has exploded means that no-one can possibly be considered an expert in more than a vanishingly small number of topics, and so for me to evaluate you when you apply for a position or tenure means I need some way to tell if your research is indeed top-quality. I can read your papers, but I won't understand them since I am not an expert. So, what options do I have at my disposal?

And this is the solution:

Having a paper accepted for publication means that someone else thinks your work is worthwhile. Having obtained external funding for your research means someone is willing to give you money. Both imply that your research is worthwhile. A track history of papers published in top-quality Journals, with you as senior author, in addition to consistently obtaining funding means that you are productive.

I totally agree with you. I never thought about it this way, although it is still disturbing, it does seem that this is the most efficient and applicable process.

I still find it sad, but really fits in considering the circumstances at hand and is reasonable.

Thank you so much for your explanation.

 

[turbo]

Having a paper accepted for publication means that someone else thinks your work is worthwhile.

Very important. Anyone can submit to ArXiv for electronic publication. It's best to wait until the paper has been accepted by a well-respected journal and then electronically publish in the final (journal-accepted) form. Given the volume of papers being published, peer-review is a a way to stand out.

 

[mathwonk]

things have changed a lot in 20 years or more. 25 years ago we interviewed a top algebraist for department head, and the dean asked him if he had any grant support, since he did not list it on his vita. he replied indignantly, "no self respecting scientist would list his GRANT support on his VITA!"

this is considered rather quaint today. I for one lament the passing of the day when the criterion for prestige was the good opinion of ones scientific peers, not the pay of federal granting agencies with their own criteria for their largess, which can, and often does, include race, gender, age, citizenship, and field of specialization.

for example my university just received a multimillion dollar grant targeted specifically at US citizens among our students. this has forced us to target citizenship as a prime criterion for grad candidates, above scientific strength. I have also known many people to apply for funding from the defense department when the NSF turned them down. The idea is that the desire to track down Bin Laden may add to your chances of funding your computation of conjugacy classes of esoteric group elements. (Even the great classic Commutative Algebra, by Zariski and Samuel, was funded by the Office of Ordnance Research [i.e. the design, testing, manufacture, arming, controlling, maintenance and disposal of weapons and munitions], US Army!.) To mention this seems quaint by todays standards. i.e. "so what's your point?"

in the old days i naively thought summer funding was to support me to do my research, and when i no longer needed it i stopped applying. then i found out it was more for bragging rights within my university. the idea is that you can say, well i may be stupid and uncreative, but i do have more grant money than others, so you have to respect me!

realistically, you need to serve both masters. publish freely and apply for grants to satisfy your job requirements, but be aware your real reputation rests on the scientific quality of your best work, published or not. But if you do not publish it, awareness of your role will be very brief and temporary, limited to the memories of those you tell about it.

 

[lamcf]

This is a very interesting conversation: I'm a grad student in a business school (content of work differs but the nature of work is similar). One thing that I learn (and am learning) so far from my grad school experience here is that a paper is publishable for two reasons:

1) It is theoretically interesting (i.e., 'aha!' moment: See Murray S. Davis (1971) paper on "that's interesting! Towards a phenomenology of sociology and a sociology of phenomenology).

2) It is theoretically impactful (i.e., how is it that your paper adds to what we already know?)

Some mentions that a well-written paper is important. I agree, but only to certain extent: writing well is very important, but you can write an idea (and research report) very well without being impactful or interesting. That, at least as I know in my field, is not enough.

It doesn't need to be ground-breaking either: The key is: Is it interesting enough that offers organizations (or physicians for the Physics community) a different perspective previously not understood AND is important?

As I said, I'm still a grad student and I'm still learning. It's very difficult because doing something not obvious is just a pure challenge. But hang on there and keep persisting is the way to go...

I'm glad to have joined this conversation, especially with most of you who come from a different field from me.J