Technical notes

First-Principles Investigation of ABO₃ Perovskites Using Density Functional Theory (DFT) with CASTEP

Your suggested topic needs more focus and scientific direction to work well for this course. Even though DFT studies of perovskites are certainly valuable, your current plan seems more like a methods tutorial than a research proposal with clear objectives. The main issue is that you're proposing to calculate various properties of SrTiO₃ without explaining what specific questions you're trying to answer. DFT calculations of standard perovskite properties have been done extensively. What new angles can your work offer? What aspects of the behavior of SrTiO₃ are you curious about? The list of properties you mention (structural, mechanical, optical, dynamical) is very vague, which suggests that you haven't yet decided what particular phenomena you plan to investigate. It would be better to focus on one or two properties and explain what you want to learn about them. For example, you could investigate how different exchange-correlation functionals affect predicted properties, study the effects of strain or defects, compare multiple perovskite compositions to identify trends, or focus on a particular property like ferroelectric behavior. Make sure that you also include a background section explaining the physics behind your simulations. The computational workflow you describe is standard DFT procedure, which is fine, but your project needs a scientific hypothesis or question to motivate it. What do you expect to find, and why would those results be interesting or useful? Once you have the results, ask whether they align well with your previous ideas and also with experimental results.

The 2D Ising model is a very common topic choice, but it can still work well if you investigate various aspects thoroughly. However, this description is very short and barely scratches the surface - I have doubts about how much thinking went into this. You need to go beyond just "finding the phase transition." Compare your simulation results with analytical ones, especially the well-known exact critical temperature. Make sure to measure critical exponents (β, γ, ν) and compare them with scaling law predictions. Investigate finite-size scaling by studying how critical behavior changes across different lattice sizes. For the external field work, study hysteresis loops and how they depend on temperature and field strength. Additionally, discuss the computational challenges involved in making accurate measurements near the critical temperature. Address issues like critical slowing down, autocorrelation times, and the statistical analysis needed to extract reliable results from Monte Carlo data.

This is a very ambitious topic choice, that complements your interests in quantum physics. The key phenomena (tunneling ionization, HHG three-step model, resonant transitions) you plan to simulate and the numerical methods are appropriate. My only concern is feasibility, i.e. simulations like this are generally computationally demanding, and getting meaningful results might require very fine time steps and long propagation times. Make sure to discuss these aspects in your report. Maybe also consider adding some quantitative checks, e.g. compare your ground state energy with known hydrogen results, or validate your ionization rates against established strong-field theories. It might be also important to think about how you'll distinguish true physical effects from numerical artifacts and how you'll handle numerical errors throughout the project. Otherwise, a very exciting choice, I'm looking forward to reading your report!

This project has potential but needs more focus and technical depth for a semester-long work. While N-body simulations are truly central to modern cosmology, your current plan reads more like implementing a basic gravitational simulator rather than exploring some interesting astrophysical question. At this point, you're proposing to start with simple Euler integration, but that will severely limit the physics you can study. Real galaxy clustering emerges from simulations with millions of particles, not the hundreds you are likely to manage with this method. The Barnes-Hut optimization you mention as a possible extension should really be core to your project plan. Your description also lacks specifics about what you'll measure beyond creating visualizations. Galaxy clustering studies typically involve correlation functions, power spectra, or halo mass functions, i.e. concrete quantities you can compare with theory or observations. What will you actually analyze from your simulations? Think about comparing different integration schemes (leapfrog performs much better than Euler), studying how clustering depends on initial conditions, and validating against analytical predictions.

Building 2D Resistive Magneto Hydrodynamics Solver for the Studying of Magnetic Reconnection using Python (GUI)

Truth be told, your short description reads as something written by an AI chatbot, who somehow misunderstood your prompt to write a research plan instead of a finalized research report. The "workflow" seems like a generic software development checklist rather than a physics research plan. I have serious doubts about how much of the physics you actually understand. You need to explain what particular aspects of magnetic reconnection you want to investigate and why. What specific questions about the Harris current sheet are you trying to answer? What do you expect to learn from it? What will you compare your results with (e.g. previous expectations based on theory or experiments), how will you validate them? The GUI component, while potentially useful for visualization, shouldn't be your main focus, the core physics should drive the project.

This description is much too brief and at this point lacks the depth needed for a project you can work on the whole semester. I'm also not seeing why this is an important/useful/interesting task. You mention wanting to "explore this topic in depth" but don't explain what specific questions you're trying to answer or what new understanding you hope to gain about cellular light scattering. What biological or medical insights are you pursuing? Your plan to simply use an existing software package (scattnlay) to calculate some cross sections is more like running a few calculations than conducting original research. You're proposing to approximate cells as multilayered spheres and compute their scattering properties, but you don't justify why this approximation is meaningful or realistic. Real cells have complex internal structures, non-spherical shapes, and heterogeneous optical properties. How will you validate that your spherical models actually represent real cells? Where will you get the optical parameters for different cell types? How will you determine appropriate layer structures for the multilayered approximation? You could expand the project to include validation against experimental scattering data, investigate how cellular morphology affects scattering signatures, study methods to distinguish different cell types from scattering patterns, or explore applications to flow cytometry or medical diagnostics. Your proposal would be much stronger if you connected this computational work to actual biological questions. What can light scattering tell us about cellular health, structure, or function? How might this relate to medical applications or basic cell biology?

Numerical Modeling of Pulse Wave Propagation and blood rheology in arteries

I love this topic choice and I love your (very relatable) personal motivation. (It won't help much though, I work in cancer research, I know. ;)) The project seems very ambitious and I'm really looking forward to seeing your results. However, I would strongly suggest approaching it in a stepwise manner from simpler, to more complex cases. E.g. you should start with a few validation cases, like implementing the Womersley profile for pulsatile flow in a rigid circular pipe first, which will give you a solid analytical benchmark. Next, add a simple elastic wall model with uniform properties and compare your pulse wave velocity calculations against well-established relationships (like the Moens-Korteweg equation). For geometry, begin with an idealized stenosis (smooth narrowing) rather than complex plaque shapes. You can find experimental data for flow through stenotic models in the literature for comparison. Only once these steps work reliably should you add non-Newtonian rheology and more complex geometries. For boundary conditions, consider using measured pressure waveforms from the literature rather than trying to model the entire cardiovascular system. The wall shear stress patterns you want to analyze are well-studied experimentally, particularly around stenoses, so you'll have good reference data for validation.

Your proposed project seems somewhat limited in scope and lacks the depth needed for a full semester of work. While comparing analytical and numerical solutions for decay chains is a valid exercise, it feels more like a computational methods assignment than a research project. Radioactive decay chain solutions are well-established (both the analytical and numerical solutions), and you're essentially proposing to verify that two standard methods give the same answer, which they should by construction. To strengthen this project, consider focusing on more complex scenarios: decay chains with neutron capture or other nuclear reactions, equilibrium conditions in natural decay series, or applications to specific problems like radon dating or nuclear waste decay heat calculations. You could also investigate numerical stability issues when dealing with vastly different decay constants, or develop efficient algorithms for very long chains.

I really like your topic choice, as it's both unique and seems worth to investigate for a full semester. I also like that you clearly build on previous work, which makes your plans credible, and the description is well-structured and thorough. Maybe you could extend your goals to compare your quantum reservoir performance to classical reservoir computing to demonstrate, how considering quantum effects might provide an advantage. Also it might be interesting to characterize which features of the Lorenz dynamics are easiest/hardest to learn and why. I'm also looking forward to reading your discussion on how numerical errors influence your results and how you can manage this issue. All in all, a really interesting topic, good look with the report!

While this is a solid topic choice with good physics content, it remains unclear how much of the simulation will actually require your own coding versus just running PYTHIA8 with standard settings. Will you simply press a button and get results, or will you need to implement custom analysis algorithms? The description suggests you'll find a peak at 125 GeV, but what deeper analysis will you perform beyond confirming this known result? Real experimental analyses involve complex selection criteria, background estimation methods, and systematic uncertainty studies. How will you implement realistic detector effects to mimic actual experimental conditions? Varying simulation parameters could significantly strengthen this work. How will you change simulation conditions like different collision energies, luminosities, or detector configurations? There should be a clear distinction in your project between using existing tools out of the box and developing your own analysis methods. Additionally, make sure you validate your reconstruction methods against known experimental results beyond just finding the right mass peak.

The topic choice seems interesting and justified, as the Vicsek model is indeed a fundamental model in collective behavior with broad applications from biological swarms to active matter physics. However, your description is very short and not specific enough for a project you can work on for the full semester. The main problem is the lack of clear scientific objectives. You mention implementing the model and studying "different variations" but don't specify what research questions you're trying to answer. What aspects of collective motion do you want to understand better, what physical quantities are you planning to measure? Will you measure order parameters like polarization or velocity correlation functions? How will you characterize the order-disorder phase transition? Will you study critical exponents, finite-size scaling, or correlation lengths? It would be interesting to see how specific modifications to the model change collective behaviour. E.g. you could model heterogeneous populations with different speeds or interaction radii, obstacles or boundaries that break symmetry, attractive/repulsive interactions beyond alignment, or time-varying external fields. Make sure you compare your results with experimental or observational data whenever possible. Can you reproduce quantitative features from studies of bacterial swarms, fish schools, or bird flocks? How do your modified models compare with specific biological observations?

OK. Pretty classic, but a solid project choice. You present interesting extensions (carrying capacity, multi-species) to the base model, and the plan to simulate with Runge–Kutta is appropriate. Your report, however, will need stronger context: explain why Kolmogorov models are important in modern ecology. Figures that illustrate predator-prey cycles and their phase portraits will be essential, please put such plots in your report. Finally, compare the model under various input parameters and try to identify parameter-dependent equilibria, their stability, and possible transient effects.

OK. This is a well-chosen project with strong references and clearly presented equations. The link between a system that is relatively simple to characterize and its real-world (safety) applications is clearly motivating. Your problem statement and methods are well described, and the plan to test the panic parameter is concrete. In your report, clarify in more detail how you will validate your results against the Nature article on which you are basing your work. If there are any transients or edge cases in this system (I have no idea), make sure you at least discuss them (and ideally test them as well). Obviously, if you talk about something that has real-world safety applications, then testing edge-cases is paramount. With such small additions, this will be a perfectly compelling project.

OK. Your proposed plan progresses logically from simple to more complex cases, and you acknowledge sensible approximations (neglecting convection and radiation, working in 2D). The motivation is strong, but your report could better connect to prior literature beyond the textbook and should include references to real-world applications. Heat conduction is one of the foundational problems in the history of physics and mathematics, so its broader context deserves explicit mention in your introduction. You have outlined expected results, but you should also propose a validation strategy, e.g., checking energy conservation in the system or benchmarking against the sensible analytical expectations (or concrete solutions if possible), so that your results can be meaningfully assessed.

OK. This is a classic, well-researched chaotic system, and imho it is a strong and well-rounded choice for exploring strange attractors. The problem is simple yet rich, and you have stated it clearly, with equations and physical interpretation. The plan to visualize attractors is concrete, though in your report the expected results and validation (e.g. reproducing published attractor figures you already mentioned) should be spelled out explicitly. One important point to keep in mind is that chaotic systems like Chua’s circuit can show long transients and sensitivity to initial conditions. You may want to check whether your simulations converge to the attractor or if they are still in a transient regime, and discuss how parameter choices or numerical accuracy affect this (these are actually the most common metrics you should check in case of all chaotic systems in general). Overall, this is a well-scoped and promising project!

OK. This proposal is nicely detailed, with a correct derivation leading to the Lane–Emden equation. The background and motivation are well explained, and imho the proposed solution method (adaptive RK45) is appropriate. In your report, please include references to some standard stellar structure text by showing the expected profiles of the stellar parameters you intend to study. Also clarify how you will test your implementation (e.g. by comparing to tabulated Lane–Emden solutions such as Horedt (1986) or something else). It would further strengthen your report to comment on the physical interpretation of different polytropic indices (the n values) and how they relate to real stellar types. Overall, this is a very strong proposal.

OK. This is quite an ambitious and original project. The problem statement is clear, with the path integral formulation well explained and linked to the Green’s function. Your plan to start with the harmonic oscillator is appropriate, since it provides the clearest benchmark for the project you have outlined. Your awareness of numerical challenges (lattice spacing, convergence in imaginary time, noise in higher states) is welcomed. In your report, make sure to include references beyond Landau’s textbook to situate your work in the broader literature. It would be really nice to also see measurable quantities extracted from your simulations (what you also mentioned, e.g., energy eigenvalues, ground-state wavefunction) and explicitly describe how you will validate them against analytic results. Finally, figures illustrating the lattice discretization or imaginary-time evolution would greatly improve clarity. I may not yet have a complete picture of the entire project in my head, but this already sounds like a challenging yet promising proposal, well suited for a semester-long deep exploration.

Simulating Thermodynamics of Spin Systems Using Different Algorithms

OK. This is an excellent project with clear motivation. Your description is detailed, with correct Hamiltonians, algorithms, and observables. The decision to compare Metropolis–Hastings with Wang–Landau is very strong, and you already identify realistic challenges. In your report, however, make sure to narrow the scope: do not attempt too many generalizations at once, but prioritize one (mixed spins, anisotropy, or long-range interactions), as the full set could easily become overwhelming (you can always revisit extensions later in the semester). Concerning the obstacle of computational cost in higher dimensions, be sure to vectorize as many calculations as possible (e.g. using NumPy, JAX, or PyTorch). This can improve runtime dramatically, sometimes by orders of magnitude.

OK. This is a perfectly sound proposal. I appreciate the clear validation checks (symmetry restoration, norm conservation) and that there is a defined measurable output such as the drift velocity, these are vital to examine in detail in a project like this. Additionally, the already proposed heatmaps, but also plots of the validation checks would be appreciated. An animation of the wavepacket drifting across the lattice would be even more nice. Additionally, I would advise you to check the numerical stability of the split-operator FFT. Increase your Δt, while keeping everything else fixed and compare the norm conservation and the drift velocity. Explain what breaks first and why; this would be a really important validation step to your entire implementation.

Time Scale Separation in Ecological Models: Individual-Based Simulations and Numerical ODE Approaches

OK. This is a very strong and well-structured proposal. It seems closely related to your ongoing research, which is perfectly acceptable for this course, provided the report is self-contained and emphasizes the computational work you carried out during this semester. Please make sure your report is not just a resubmission of earlier material, but highlights what you implemented, tested, or explored here. (Sorry if that is not the case, the project itself is fully appropriate either way.) In your report, please discuss concretely how you will judge the validity of your solvers (e.g., by comparing fixed points and bifurcation diagrams between full and reduced models).Then gradually reduce the timescale separation or r and d to show when and how the approximation breaks down. It would also be helpful to define a metric for when reduced models fail (e.g., relative error in trajectories, stability boundaries, shifts in bifurcation points, etc.). A particularly clean validation would be to explore cases where the resource dynamics are made much faster than the consumer dynamics (r >> d): here, QSSA should be very accurate. These are just tips, but you can check practically anything that you think is a robust and strong validation metric. For visualization, heatmaps showing parameter regions where various models/solvers hold vs fail would be really valuable!

Simulating the Sun’s Lower Atmosphere by Numerically Solving Maxwell’s Equations

OK. The derivation of the force-free equations is sound, but the scope is too large for one semester; please narrow early to a small 2D (or 2.5D) test geometry and define boundary conditions precisely. That would already make for a perfectly solid project. Your mention of the Crank–Nicolson stencil is fine if you just mean a centered finite-difference discretization in space. This is appropriate for the elliptic equation you intend to solve. But keep in mind that the stencil is only the discretization; it still leads to a large linear system that must be solved efficiently. The real challenge will be choosing and implementing a suitable solver (e.g. conjugate gradient or multigrid), not the stencil itself. Overall, this is an interesting and relevant project. I would be glad to see cool visualizations if you get there, but please focus first on defining the scope clearly and solving the core problem.

OK. This is a strong proposal with a clear problem statement and well-chosen topic. Your plan to study oscillations and bistability is a probably the best way to study such a simple, yet rich model such as the Wilson–Cowan model. For your report, please be more specific about the numerical approach you plan to use (e.g. Euler, Runge–Kutta, etc.), and state which parameters or regimes you intend to explore. A schematic figure of the excitatory–inhibitory network would also help make the model more self-contained. Also, any figure in general will greatly help; and with coupled differential equations you always have the luxury of producing virtually an infinite amount of different plots. Usually, at this point, I ask people to validate their results, as that is one of the most important steps of any simulation project. In this case, I only ask this with a big "IF": if there is any way to give prior expectations based on any literature in this topic, then please do. Overall, this is a feasible and interesting project. Sneak-peek for later as I can't wait until the first report: later in the semester, you may also find it interesting that models like Wilson–Cowan have close conceptual similarities to other dynamical systems studied in physics, such as Hopfield networks (which received the Nobel prize in physics in 2024) or spin glasses and other attractor networks. This could provide a really nice multidisciplinary perspective for your final report if you choose to include it.

OK. This is a creative and well-motivated project. The Dzhanibekov effect is a classic example of rigid-body dynamics, and your plan to solve Euler’s equations numerically is a solid starting point. As unstable axis rotations are notorious for amplifying numerical errors, your goal for the project is perfectly appropriate and valid area of research in this topic. In your report you should describe how you will validate your results; for example, by reproducing the known stable and unstable axes of rotation or by comparing with analytical solutions in symmetric cases or whatever you seem fit. It is up to you, but comparing your results to theoretical expectations are really important. A nice schematic figure of the rotating body and axes early on in your report would also improve clarity. The proposed extensions (3D rendering, external potentials) are interesting, but make sure the core implementation is robust first. P.s. In your report, please include authoritative references beyond Wikipedia about the topic.

I am convinced of your genuine interest in the topic, which is a very good starting point. It is good that you want to explore many types of potentials. However, don't forget to take the time to thoroughly understand and interpret the results. You should also check the numerical convergence and stability of the finite difference algorithms. Boundary conditions play an important role in such simulations; it may be worth examining the effect. A crucial step in every project is to compare your results with known results to validate your work. Don't forget to do that!.

It seems from your description that you have already worked with GEANT4 and even on a similar problem, but you didn't state any motivations. I found that you already did a very similar, if not the same, project at your previous university. First, it is not completely fair to reuse the same project to fulfill the requirements of this course. Because you didn't mention and cite your previous work, this could even count as self-plagiarism. Secondly, the aim of this course is to familiarize oneself with new topics and learn new numerical techniques. In light of this, I would encourage you to choose a different topic that differs more significantly from this one. If you stick to your original choice, it is a very strict requirement to extend the project substantially and very clearly describe how the new project is different from your old one.

I like your personal motivation, keeping the topic close to your research interest, and very different at the same time. The project you described is fairly standard and closely follows the textbook. It would be good if you could make it unique in some way. As an extension, you could consider analysing the convergence of the numerical methods as the resolution is changed. I did the same project many years ago, and the biggest challenge for me was to define the boundary conditions correctly. You should also compare your results to literature values and make sanity checks.

This is a relatively common choice. I would have liked some personal motivation for choosing this topic, and also more details about your plans. There are some inconsistencies in your plans. You define the Hamiltonian in 1D, but in 1D no phase transition is observable, hence no Curie temperature exists. Anyway, you should extend the model at least to two dimensions. You also mention quantum state vectors, but the Ising model doesn't have any quantum features. Even if you define it with spin operators, the same spin operator in all the terms makes it equivalent to the classical formulation. If you are interested in quantum mechanical simulations, you should consider the transverse field Ising model as the simplest example, but you will not be able to use Metropolis and Wang Landau sampling algorithms. For the classical Ising model, as extensions, it could be interesting to consider different types of interactions beyond nearest neighbor. And don't forget to check you results against the literature.

I really like that your motivation is to gain a deeper understanding of the underlying physical background of your research. I am not too concerned that your report will be difficult to understand because you don't write about your research, but please ensure that you don't skip any explanations so that an outsider can understand it well. It clearly seems like a very strong project idea. Put emphasis on the validation against the literature and explain the results thoroughly; otherwise, I won't be able to assess the correctness of your results. I noticed a lot of grammatical and spelling mistakes in your text. Avoiding these is quite easy these days, use a spell checker and some AI tool to check your text.

This seems like a highly involved and technical project. Your motivation is not completely clear to me. Did you conduct experiments in your thesis, and now would you like to simulate the same systems numerically? If so, this is a good idea. However, make sure that this project is distinct from your thesis, describe what you have done before, and how the two connect. Also, pay attention that your project is not too hard to understand for someone who is not involved in similar research. Explain your results thoroughly!

This is an extremely short description. Even though you describe your goals for the project clearly, these will be insufficient as a whole semester's work. However, the Ising model is a very popular topic, it won't be difficult to find interesting ideas. But don't forget to make it unique: if you can't come up with something beforehand, you may encounter something during the work. The validation of your results is a good idea and almost always necessary.

This is a quite straightforward project idea that can have many interesting extensions. I missed some personal motivation for this project. I hope you are interested in this topic. I did the same project several years ago, I extended the basic 2D version to 3D, and it was simple to do. Other extensions could be to try different lattices, or maybe a continuous DLA. You could also try anisotropic or biased diffusion. Measuring the fractal dimension is a good idea, which is also necessary for this kind of project. However, these DLA aggregates have a multi-gractal property, examining these could really add depth to your report and make it unique.

I like your project idea. You made your motivations and goals clear. I think the proposed investigations are all interesting. To ensure your simulation is accurate, you should compare your results to the literature, both qualitatively and quantitatively. Don't forget to perform quantitative analysis of the results: one of the most interesting could be the fire size distribution, but you could also investigate the fractal properties or the percolation threshold. I think these simulations can be done in Python easily; there are high-performance computing libraries in Python, too. You should vectorize the simulation where you can, to make it faster, and even parallelizable.

Fractals always make for nice projects, with some beautiful visuals. Try and see which generation method is more efficient for getting the correct fractal dimension. For some more ideas, I can recommend the following book, which is quite technical, but also has some examples for different fractal types, which you might use in your project: https://hal.elte.hu/~vicsek/downloads/Fractal_Growth_Phenomena/Fractal%20Growth%20Phenomena-Part%20I-Chapter%202-1.pdf

A nice project idea, though molecular dynamics can be difficult. Try and see which parts of the simulation work, and don't be afraid to simplify the project if you run into some major obstacles. Focusing on the thermodynamical variables is a nice goal, they will provide good observable measures for your simulated system and it's stability.

DLA is a really interesting case of fractal growth, which is not difficult to simulate. However, what you describe could be quite short for a full project. I would recommend reading the following chapter from a book about DLA, and maybe you can get a few interesting ideas: https://hal.elte.hu/~vicsek/downloads/Fractal_Growth_Phenomena/Fractal%20Growth%20Phenomena-Part%20II-Chapter%206.pdf

General relativity always makes for a fascinating project. When solving the ODEs, try and see which of the solvers work best, and don't just start with the most complex one. Also don't forget to give meaningful interpretations of your results, will the dynamics of the universe change the way you would expect or not.

A really unique project idea, for which I'm interested to see the results. Though it does appear quite complicated, and computationally intensive, especially for more complex shapes, such as a F1 car. However, if implementations are successful, there is a lot of potential. Instead of trying to make the racecar design better, you can also try and make it worse, like what if it had two rear wings or more.

Collective motion is an excellent project idea. Your description is quite short, but the ideas you discuss in it look promising. Once the basic simulation is completed and works well with varying panic parameters, you can try and expand it. For example, an interesting topic could be the analysis of the forces present in such a panicking crowd. A well known problem is the so called crowd crush, where the pressure on some people in the crowd can even become fatal. While this may not be a direct goal, if you have the time, it could provide really interesting results: https://en.wikipedia.org/wiki/Crowd_collapses_and_crushes

A very interesting project idea, with a good concrete problem and plans. I would also recommend that you mention the computational parts of the analysis, eg. how long you have to run the simulation until you get converging results. In simulations, it's important to consider not just the accuracy, but the computational capacity as well, a slightly more inaccurate model which can be run much faster can sometimes provide better insight.

A unique ide, which combines a well known physical system with some game theory. I'm interested to see the results, how the strategies of the agents change. I think you will get some very interesting visualizations as well. The Ising model exhibits a fractal-like structure in it's critical state, maybe this will also be reproduced here.

Hydrodinamical simulations can be challenging, but the results are always interesting. In your project, make sure to also include those results which might not be perfect, for some unphysical results. These can still give important information about how the simulation works.

Solving differential equations always makes for an interesting project, and the two equations look promising for this case. As always, try and experiment with all the solvers, and show even those results which run into problems for the simpler ones, these can also be interesting. Your idea of expanding it into the GPU space is also quite novel, I'm interested to see the performance analysis of it compared to a CPU version.

Interesting idea. I think you've set yourself some realistic goals. For limited programming experience, I can recommend some AI tools, just be careful and only ask it to write short, specific functions, and always validate it's results. If you can compare your results to ones from literature, it's always a good idea to do this along the way, even if your simulation is not a perfect match. These can show you whether you're on the right track, or your simulation still needs to be modified.